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Essays in Health-Related Public Policy

Permanent Link: http://ufdc.ufl.edu/UFE0021152/00001

Material Information

Title: Essays in Health-Related Public Policy
Physical Description: 1 online resource (158 p.)
Language: english
Creator: Piette, Christine Ann
Publisher: University of Florida
Place of Publication: Gainesville, Fla.
Publication Date: 2007

Subjects

Subjects / Keywords: abortion, after, any, behavior, care, claim, contraception, diseases, drugs, emergency, expenditures, frequency, health, hmo, malpractice, managed, medical, morning, pharmaceutical, pill, prescription, provider, reform, risky, sexually, tort, transmitted, willing
Economics -- Dissertations, Academic -- UF
Genre: Economics thesis, Ph.D.
bibliography   ( marcgt )
theses   ( marcgt )
government publication (state, provincial, terriorial, dependent)   ( marcgt )
born-digital   ( sobekcm )
Electronic Thesis or Dissertation

Notes

Abstract: My research examined three separate studies of health-related public policy. In the first study, I analyzed the effect of non-economic damage caps on the frequency of medical malpractice claims, recognizing that such laws are likely endogenous. I constructed a unique instrument using past and current values of state political composition and other factors. I also exploited exogenous Supreme Court findings of unconstitutionality. In both cases, I found that caps on non-economic damages are not associated with a reduction in medical malpractice claim frequency. This result is robust to alternative specifications and comparison groups. Next, I considered risky behavior. The FDA recently approved a proposal to allow emergency contraception, or Plan B, to be available through pharmacies without a prescription. While this change is only now occurring nationally, several states had previously allowed pharmacy access to emergency contraception. In particular, Washington State was the first state to implement such a program in 1998. Proponents of pharmacy access argued that improved access could decrease the number of abortions. Opponents cited concern that pharmacy access could lead to an increase in risk-taking, especially among teens or young adults, and hence lead to increased rates of sexually transmitted diseases. In my paper, I used county-level data as well as specific timing of pharmacy participation to consider the intended and unintended consequences of pharmacy access to emergency contraception in Washington. My findings support both claims. Pharmacy access is associated with a small decrease in abortions for some age groups. In addition, pharmacy access is associated with an increase in Chlamydia rates for young women. These results are robust to an alternative comparison group as well as alternative definitions of treatment. In the final study, I analyzed any-willing provider (AWP) legislation. In recent years, many states have implemented AWP legislation, which requires a managed care organization (MCO) to accept any provider, who agrees to the managed care organization's reimbursement rates, terms, and conditions, into its network. Proponents argue that AWP laws provide for larger networks, more patient choice, greater competition among providers, and arguably increased quality of care. Opponents cite AWP legislation as prohibiting managed care organizations from selective contracting and obtaining discounts by offering providers a larger volume of patients. Such legislation is therefore argued to prevent MCOs from effectively reducing health care costs. A small literature exists on the effect of these laws on hospital expenditures, physician expenditures, and total health care expenditures. Most studies, however, fail to recognize that the vast majority of the existing laws target pharmacies exclusively, as opposed to more comprehensive laws that also apply to physicians and hospitals. If AWP legislation prevents cost reduction available through selective contracting, then states with such legislation may incur higher health care expenditures. My paper is the first to analyze the impact of pharmacy-specific AWP legislation on state-level prescription drug expenditures.
General Note: In the series University of Florida Digital Collections.
General Note: Includes vita.
Bibliography: Includes bibliographical references.
Source of Description: Description based on online resource; title from PDF title page.
Source of Description: This bibliographic record is available under the Creative Commons CC0 public domain dedication. The University of Florida Libraries, as creator of this bibliographic record, has waived all rights to it worldwide under copyright law, including all related and neighboring rights, to the extent allowed by law.
Statement of Responsibility: by Christine Ann Piette.
Thesis: Thesis (Ph.D.)--University of Florida, 2007.
Local: Adviser: Kenny, Lawrence W.

Record Information

Source Institution: UFRGP
Rights Management: Applicable rights reserved.
Classification: lcc - LD1780 2007
System ID: UFE0021152:00001

Permanent Link: http://ufdc.ufl.edu/UFE0021152/00001

Material Information

Title: Essays in Health-Related Public Policy
Physical Description: 1 online resource (158 p.)
Language: english
Creator: Piette, Christine Ann
Publisher: University of Florida
Place of Publication: Gainesville, Fla.
Publication Date: 2007

Subjects

Subjects / Keywords: abortion, after, any, behavior, care, claim, contraception, diseases, drugs, emergency, expenditures, frequency, health, hmo, malpractice, managed, medical, morning, pharmaceutical, pill, prescription, provider, reform, risky, sexually, tort, transmitted, willing
Economics -- Dissertations, Academic -- UF
Genre: Economics thesis, Ph.D.
bibliography   ( marcgt )
theses   ( marcgt )
government publication (state, provincial, terriorial, dependent)   ( marcgt )
born-digital   ( sobekcm )
Electronic Thesis or Dissertation

Notes

Abstract: My research examined three separate studies of health-related public policy. In the first study, I analyzed the effect of non-economic damage caps on the frequency of medical malpractice claims, recognizing that such laws are likely endogenous. I constructed a unique instrument using past and current values of state political composition and other factors. I also exploited exogenous Supreme Court findings of unconstitutionality. In both cases, I found that caps on non-economic damages are not associated with a reduction in medical malpractice claim frequency. This result is robust to alternative specifications and comparison groups. Next, I considered risky behavior. The FDA recently approved a proposal to allow emergency contraception, or Plan B, to be available through pharmacies without a prescription. While this change is only now occurring nationally, several states had previously allowed pharmacy access to emergency contraception. In particular, Washington State was the first state to implement such a program in 1998. Proponents of pharmacy access argued that improved access could decrease the number of abortions. Opponents cited concern that pharmacy access could lead to an increase in risk-taking, especially among teens or young adults, and hence lead to increased rates of sexually transmitted diseases. In my paper, I used county-level data as well as specific timing of pharmacy participation to consider the intended and unintended consequences of pharmacy access to emergency contraception in Washington. My findings support both claims. Pharmacy access is associated with a small decrease in abortions for some age groups. In addition, pharmacy access is associated with an increase in Chlamydia rates for young women. These results are robust to an alternative comparison group as well as alternative definitions of treatment. In the final study, I analyzed any-willing provider (AWP) legislation. In recent years, many states have implemented AWP legislation, which requires a managed care organization (MCO) to accept any provider, who agrees to the managed care organization's reimbursement rates, terms, and conditions, into its network. Proponents argue that AWP laws provide for larger networks, more patient choice, greater competition among providers, and arguably increased quality of care. Opponents cite AWP legislation as prohibiting managed care organizations from selective contracting and obtaining discounts by offering providers a larger volume of patients. Such legislation is therefore argued to prevent MCOs from effectively reducing health care costs. A small literature exists on the effect of these laws on hospital expenditures, physician expenditures, and total health care expenditures. Most studies, however, fail to recognize that the vast majority of the existing laws target pharmacies exclusively, as opposed to more comprehensive laws that also apply to physicians and hospitals. If AWP legislation prevents cost reduction available through selective contracting, then states with such legislation may incur higher health care expenditures. My paper is the first to analyze the impact of pharmacy-specific AWP legislation on state-level prescription drug expenditures.
General Note: In the series University of Florida Digital Collections.
General Note: Includes vita.
Bibliography: Includes bibliographical references.
Source of Description: Description based on online resource; title from PDF title page.
Source of Description: This bibliographic record is available under the Creative Commons CC0 public domain dedication. The University of Florida Libraries, as creator of this bibliographic record, has waived all rights to it worldwide under copyright law, including all related and neighboring rights, to the extent allowed by law.
Statement of Responsibility: by Christine Ann Piette.
Thesis: Thesis (Ph.D.)--University of Florida, 2007.
Local: Adviser: Kenny, Lawrence W.

Record Information

Source Institution: UFRGP
Rights Management: Applicable rights reserved.
Classification: lcc - LD1780 2007
System ID: UFE0021152:00001


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ESSAYS INT HEALTH-RELATED PUBLIC POLICY


By

CHRISTINE ANN PIETTE













A DISSERTATION PRESENTED TO THE GRADUATE SCHOOL
OF THE UNIVERSITY OF FLORIDA IN PARTIAL FULFILLMENT
OF THE REQUIREMENTS FOR THE DEGREE OF
DOCTOR OF PHILOSOPHY

UNIVERSITY OF FLORIDA

2007






























O 2007 Christine Ann Piette



































To my parents, Michael and Dianne, and to my husband, Joseph









ACKNOWLEDGMENTS

The successful completion of this dissertation was not possible without with guidance and

support of several individuals. I thank my committee: Lawrence Kenny, Roger Blair, David

Figlio, and Bruce Vogel. Each of these individuals has provided endless support, overwhelming

encouragement, invaluable discussions, and thoughtful suggestions. I cannot thank them enough

for their support through this process. I also thank Mark Rush for graciously participating on my

committee, in my defense, and for providing useful suggestions. I also received valuable input

and guidance from other individuals including Sarah Hamersma, Damon Clark, Steven Slutsky,

Jonathan Hamilton, and Jeffrey Harrison. Finally, I thank Michael and Dianne Piette who have

spent a lifetime not only helping me to achieve this goal, but to achieve all my goals.












TABLE OF CONTENTS


page

ACKNOWLEDGMENTS .............. ...............4.....


LIST OF TABLES ........._..... ...............7..____ ......


LIST OF FIGURES .............. ...............9.....


AB S TRAC T ............._. .......... ..............._ 10...


CHAPTER


1 INTRODUCTION ................. ...............12.......... ......


2 NON-ECONOMIC DAMAGE CAPS AND MEDICAL MALPRACTICE CLAIM

FREQUENCY: IS IT TIME FOR A SECOND OPINION ................. .........................15

Introducti on ................. ...............15.................

Empirical Model ............... .... ... ..............1
Model and Dependent Variable ................. ...............19................
Independent Variables ................ ...............20.................
In strmentati on ................. ...............24........... ....
Data................. ...............27.
Identifi cation ................. ...............29................
Policy Endogeneity ................. ...............30.................
Empirical Results ................. ...............32.................
First Stage ................. ...............32.................
Second Stage .............. ...............33....
Lags in Suit Duration ................. ...............34................
Alternative M ethodology ............... ... .......... ... ...............35.....
Robustness Checks and Additional Considerations .............. ...............37....
Severe Damage Caps ................. ...............37........... ....
Additional Considerations ................. ...............38.................
Conclusions............... ..............3


3 THE EFFECTS OF INCREASED ACCESS TO THE MORNNG-AFTER PILL ON
ABORTION AND STD RATES ................. ...............55................


Introducti on ................. ...............55.................
Previous Literature................ ... .................5
The Relative Costs of Sexual Activity............... ...............62
Pharmacy Access to Emergency Contraception ................. ...............63........... ...
History of Emergency Contraception............... .............6
The Washington State Pilot Proj ect. .........._.... ...............63.._.__. ....
Data............... ...............67..
Chl amy di a........._...... ...............67..__._. .....












Abortion Data ................. ...............68.......... .....

Program Participation ................. ...............69.................
Identification ................. ...............71.................

Chl amy di a ................ ...............71................
Abortions .................. ...............73.................

Pharmacy Participation............... .............7
Other Characteristics .............. ...............76....

Empirical Methodology ................. ...............76.......... ......
Re sults................... .......... ...............78.......

Chlamydia Rates............... ...............78.
Abortion Rates ................. ...............79.................

Lag in Treatment ............... ... ...............79..
Alternative Treatment Definitions ................. ...............80........... ....

Chlamydia Rates............... ...............80.
Abortion Rates ................. ...............8.. 1..............
Other Considerations ................. ...............8.. 1..............
Falsification Tests ............. _.. .... ._ ...............82....

Additional Control Group: Oregon ............. ...... ._ ...............83...
Chl am y di a............. ...... ._ ...............83...
Ab orti on ................. ...............85........... ....
Conclusions............... ..............8


4 THE IMPACT OF PHARMACY-SPECIFIC ANY-WILLING-PROVIDER
LEGISLATION ON PRESCRIPTION DRUG EXPENDITURES .............. ...................128


Introducti on .............. .... ....__ .. .. .. .__ ..... ..........2

Managed Care and Any-Willing-Provider Legislation. ...._ ..............._ ................1 29
Managed Care and Health Maintenance Organizations ................. .......................129
Any-Willing-Provider Legislation. ......___ ...... ..._._ ......__ ............13
Previous Literature................ ..............13
D ata............... ..... .. ...........13

Health Care Spending ..........._...._ ......._._ ...............133.....
Health Maintenance Organization Presence ............_._.......... .........._._........13

Empirical Methodology ............_..__........ ...............13 5....
Re sults............_..._ ....... .._...._ .. ..... ...._ ... ..........13

General Any-Willing-Provider Legislation ............_.... ... ....._.._ ......._.. ...........3
Heterogeneous Application of Any-Willing-Provider Legislation ........._..... .............138
Policy Endogeneity & Robustness............... ..............13
Policy Endogeneity.................... .......... ...............139......
Robustness & Sensitivity Analysis............... ...............14
Conclusion ................ ...............142................


LIST OF REFERENCES ................. ...............152................


BIOGRAPHICAL SKETCH ................. ...............158......... ......











LIST OF TABLES

Table page


2-1 Summary statistics of variables .............. ...............40....

2-2 Data sources ............ ....._._._ ...............41....

2-3 States enacting non-economic damage reforms (1991-2001) ........_.._.. .... ....._.._.. ......42

2-4 State limits on damages .............. ...............43....

2-5 Non-economic damage caps held unconstitutional............... ............4

2-6 Description of categories of states ........._.._.. ...._... ...............46..

2-7 Baseline statistics (1991) .............. ...............47....

2-8 Change in suits between year t-2 and t-1; t-1 and t=0 .............. ...............48....

2-9 First stage results............... ...............49

2-10 Ordinary least squares (OLS) and two-stage least squares (2SLS) results .......................50

2-11 2SLS results variants of duration. ........._._. ........... ...............51..

2-12 OLS results using unconstitutionality of caps .............. ...............52....

2-13 Results for severe cap. ............. ...............53.....

3-1 Summary statistics .............. ...............87....

3-2 Baseline statistics ................. ...............88........... ....

3-3 Difference in means t-tests between treatment and control ................ ..................8

3-4 Difference in means t-tests between early and late adopters .............. .....................9

3-5 Difference in means t-tests for county characteristics .................... ...............9

3-6 Chlamydia rates overall, by gender, and by gender/age .............. ....................9

3-7 Three-year pretreatment average, Washington ......___ ..... .._._. ......._...........9

3-8 Chlamydia rates overall, by gender, and by gender/age with covariates ................... ........94

3-9 Abortion rates overall and by age ................. ...............95......... ..

3-10 Chlamydia rates overall, by gender, and by gender/age .............. ....................9











3-11 Abortion rates overall and by age ................ ...............97........... ..

3-12 Falsification tests using county cancer rates ....._ .....___ .........__ ..........9

3-13 Falsification exercise .............. ...............99....

3-14 Difference in means t-test, chlamydia rates ....._ .....___ ........._ ...........0

3-15 Summary statistics, Washington and Oregon ....._ .....___ ............_........10

3-16 Chlamydia rates including Oregon .............. ...............102....

3-17 Three-year pre-treatment average, Washington and Oregon............._ .........._ .....103

3-18 Chlamydia rates including Oregon .............. ...............104....

3-19 Abortion rates including Oregon .............. ...............105....

3-20 Abortion rates including Oregon .............. ...............106....

4-1 Description of state any-willing provider (AWP) legislation ................. ............... ....144

4-2 Summary statistics .............. ...............145....

4-3 Expenditures per capital results .............. ...............146....

4-4 Expenditures per capital results with fractions of government insurance .................. ...... 147

4-5 Expenditures per capital results with heterogeneous applicability of AWP law ..............148

4-6 Spline regression results .............. ...............149....

4-7 Expenditures per capital results with freedom of choice (FOC) indicator ....................... 150

4-8 Expenditures per capital results with heterogeneous applicability of AWP law and
FOC indicator.............. .............151











LIST OF FIGURES


Figure page

2-1 Description of enactment of cap and change in political composition............ ...............54

3-1 Chlamydia rates in the United States, 1992 2003 ......_._. ......._.. ........_......10

3-2 Overall and female Chlamydia rates in Washington state ........._ ...... .._._...........108

3-3 Overall abortion rate (age 15-44) in Washington state ................. .........................109

3-4 Abortion rates in the United States, 1992 2003 ................ .......... .................11

3-5 Abortion rates in Washington state, ages 15-19 and ages 20-24 ................. .................1 11

3-6 Washington state pharmacy access in 1998 ................. ...............112.............

3-7 Washington state pharmacy access in 2002 ................. ...............113........... ..

3-8 Washington state pharmacy access in 2005 ................. ...............114........... ..

3-9 Overall chlamydia rates by treatment and control group ................. .......................115

3-10 Female chlamydia rates by treatment and control group ................ .......................116

3-11 Overall abortion rates (age 15-44) by treatment status ................. .........................117

3-12 Abortion rates (age 15-19) by treatment status ................. ...............118............

3-13 Abortion rates (age 20-24) by treatment status ................. ...............119.............

3-14 Overall chlamydia rates, Washington and Oregon .............. ...............120....

3-15 Overall chlamydia rates by treatment status ................ ...............121........... ..

3-16 Abortion rates, Washington and Oregon .............. ...............122....

3-17 Abortion rates 15-19, Washington and Oregon ................. ...............123............

3-18 Abortion rates 20-24, Washington and Oregon ................. ...............124........... ..

3-19 Abortion rates by treatment status .............. ...............125....

3-20 Abortion rates 15-19 by treatment status ................. ...............126............

3-21 Abortion rates 20-24 by treatment status ................. ...............127........... ..

4-1 Expenditures per capital, 1987-1998. ............. ...............143....









Abstract of Dissertation Presented to the Graduate School
of the University of Florida in Partial Fulfillment of the
Requirements for the Degree of Doctor of Philosophy

ESSAYS INT HEALTH-RELATED PUBLIC POLICY

By

Christine Ann Piette

August 2007

Chair: Lawrence Kenny
Major: Economics

My research examined three separate studies of health-related public policy. In the first

study, I analyzed the effect of non-economic damage caps on the frequency of medical

malpractice claims, recognizing that such laws are likely endogenous. I constructed a unique

instrument using past and current values of state political composition and other factors. I also

exploited exogenous Supreme Court findings of unconstitutionality. In both cases, I found that

caps on non-economic damages are not associated with a reduction in medical malpractice claim

frequency. This result is robust to alternative specifications and comparison groups.

Next, I considered risky behavior. The FDA recently approved a proposal to allow

emergency contraception, or Plan B, to be available through pharmacies without a prescription.

While this change is only now occurring nationally, several states had previously allowed

pharmacy access to emergency contraception. In particular, Washington State was the first state

to implement such a program in 1998. Proponents of pharmacy access argued that improved

access could decrease the number of abortions. Opponents cited concern that pharmacy access

could lead to an increase in risk-taking, especially among teens or young adults, and hence lead

to increased rates of sexually-transmitted diseases. In my paper, I used county-level data as well

as specific timing of pharmacy participation to consider the intended and unintended










consequences of pharmacy access to emergency contraception in Washington. My findings

support both claims. Pharmacy access is associated with a small decrease in abortions for some

age groups. In addition, pharmacy access is associated with an increase in Chlamydia rates for

young women. These results are robust to an alternative comparison group as well as alternative

definitions of treatment.

In the final study, I analyzed any-willing provider (AWP) legislation. In recent years,

many states have implemented AWP legislation, which requires a managed care organization

(MCO) to accept any provider, who agrees to the managed care organization's reimbursement

rates, terms, and conditions, into its network. Proponents argue that AWP laws provide for larger

networks, more patient choice, greater competition among providers, and arguably increased

quality of care. Opponents cite AWP legislation as prohibiting managed care organizations from

selective contracting and obtaining discounts by offering providers a larger volume of patients.

Such legislation is therefore argued to prevent MCOs from effectively reducing health care costs.

A small literature exists on the effect of these laws on hospital expenditures, physician

expenditures, and total health care expenditures. Most studies, however, fail to recognize that the

vast maj ority of the existing laws target pharmacies exclusively, as opposed to more

comprehensive laws that also apply to physicians and hospitals. If AWP legislation prevents cost

reduction available through selective contracting, then states with such legislation may incur

higher health care expenditures. My paper is the first to analyze the impact of pharmacy-specific

AWP legislation on state-level prescription drug expenditures.









CHAPTER 1
INTTRODUCTION

My analysis of public policy issues is comprised of three studies: (1) Non-economic

damage caps and medical malpractice claim frequency: is it time for a second opinion?, (2) The

effects of increased access to the morning-after pill on abortion and sexually-transmitted disease

rates, and (3) The impact of pharmacy-specific any-willing provider legislation on prescription

drug expenditures.

The first study considered the effect of non-economic damage caps, one particular type of

tort reform, on the frequency of medical malpractice claims, while recognizing that such laws are

endogenous. I constructed a unique instrument by calculating the predicted probability that a law

is in place in each of the prior years given state political composition and other factors. I then

used the cumulative probability, based on current and past influences, as an instrument for the

enactment of a cap. This procedure is preferable to using instruments of contemporaneous

political control, an approach typically exploited in the literature. My approach produces strong

first stage statistics. I found that caps on non-economic damages are not associated with a

reduction in claim frequency. This result is robust to alternative specifications and comparison

groups. In addition, I exploited exogenous Supreme Court findings of unconstitutionality. If non-

economic damage caps are effective in reducing claim frequency, then the removal of such caps

will increase claim frequency. Using this alternative approach, I again found no relationship

between non-economic damage caps and claim frequency.

I also considered the effects of increased access to the morning-after pill. A recent FDA

decision allowed emergency contraception, or Plan B, to be available through pharmacies

without a prescription. While this change is only now occurring nationally, several states had

previously allowed pharmacy access to emergency contraception. In particular, Washington State









was the first state to implement such a program in 1998. Proponents of pharmacy access argue

that improved access could decrease the number of abortions. Opponents cite concern that

pharmacy access could lead to an increase in risk taking, especially among teens or young adults,

and hence lead to increased rates of sexually-transmitted diseases. In my paper, I used county-

level data as well as specific timing of pharmacy participation to consider the intended and

unintended consequences of pharmacy access to emergency contraception in Washington. My

findings support both claims. Pharmacy access is associated with a small decrease in abortions

for some age groups. In addition, pharmacy access is associated with an increase in Chlamydia

rates for young women. These results are robust to an alternative comparison group as well as

alternative definitions of treatment.

Finally, my analysis focused on another type of health policy, any-willing provider

(AWP) legislation. In recent years, many states have implemented AWP legislation, which

requires a managed care organization (MCO) to accept any provider, who agrees to the managed

care organization's reimbursement rates, terms, and conditions, into its network. Proponents

argue that AWP laws provide for larger networks, more patient choice, greater competition

among providers, and arguably increased quality of care. Opponents cite AWP legislation as

prohibiting managed care organizations from selective contracting and obtaining discounts by

offering providers a larger volume of patients. Such legislation is therefore argued to prevent

MCOs from effectively reducing health care costs. A small literature exists on the effect of these

laws on hospital expenditures, physician expenditures, and total health care expenditures. Most

studies, however, fail to recognize that the vast majority of the existing laws target pharmacies

exclusively, as opposed to more comprehensive laws that also apply to physicians and hospitals.

If AWP legislation prevents cost reduction available through selective contracting, then states










with such legislation may incur higher health care expenditures. My research is the first to

analyze the impact of pharmacy-specific AWP legislation on state-level prescription drug

expenditures.













CHAPTER 2
NON-ECONOMIC DAMAGE CAPS AND MEDICAL MALPRACTICE CLAIM
FREQUENCY: IS IT TIME FOR A SECOND OPINION

Introduction

Medical malpractice litigation is a source of much concern. Claim frequency is on the rise.

Between 1993 and 2002, claims increased by 18% (National Center for State Courts, 2003). In

addition, median awards jumped from $253,000 in 1992 to $431,000 in 2001, a real increase of

70% (Bureau of Justice Statistics, 2001). As a result, physicians are faced with rising insurance

premiums. In spite of soaring premiums, maj or medical malpractice insurers are exiting the

industry (Freudenheim, 2001). Anecdotal evidence suggests that there may be additional effects

of medical malpractice litigation. For example, physicians are said to be transferring states in

search of lower insurance premiums (Wagner, 2004). Special sts in ob stetrics/gynecology are

reportedly refusing to perform difficult deliveries and changing their procedure usage due to the

fear of malpractice suits (American College of Obstetricians and Gynecologists, 2004). Some

claim that physicians are changing their fields of specialty (American College of Obstetricians

and Gynecologists, 2004)1 or are practicing without insurance (Silverman, 2004).

The public policy response has been tort reform, with particular interest in imposing caps

on non-economic damages. 2Non-economic damages are typically those awarded for pain and





1 Fourteen percent of respondents to an ACOG Survey stopped practicing obstetrics because of
the risk of medical liability claims.

2 Tort reform, with a focus on medical malpractice litigation, has also been proposed at the
national level. The Comprehensive Medical Malpractice Reform Act of 2005 (HR 321) calls for
a cap on non-economic damages of $250,000, adjusted for inflation from 1975.









suffering, loss of consortium or companionship, or emotional distress.3 Proponents of tort reform

argue that non-economic damage caps will decrease claim severity through a reduction in non-

economic damage awards. Additionally, non-economic damage caps alter the expected benefits

of filing a claim by reducing the available non-economic damages. If the expected benefits fail to

exceed the costs of pursuing a medical malpractice action, then some claims may be deterred. Is

this behavioral response to caps on non-economic damages common enough to lead to a

discernable reduction in claim frequency?

An extensive literature exists regarding the effects of tort reform on a number of different

outcomes: claim frequency (Danzon, 1984; Danzon, 1986),4 claim severity (Danzon, 1984;

Danzon, 1986; Yoon, 1991; Browne & Puelz (1999), insurance profitability (Viscusi & Born,

1995; Born, Viscusi, & Carlton, 1998), and premiums (Thorpe, 2004), and physician supply

(Matsa, 2005; Klick & Strattman, 2003). Only one main study specifically targets medical

malpractice claim frequency, as opposed to the frequency of general tort claims. Danzon (1984)

focuses on the determinants of claim frequency as a result of tort reforms enacted during the

1970s.5 Danzon reports that while limits on awards do have an effect on claim severity, such

caps (as well as other tort reforms) do not have an effect on claim frequency.





3 Although most commonly referred to as non-economic damages, these damages are "non-
pecuniary" in the sense that they do not compensate the plaintiff for lost earnings or medical
expenses, but rather for a loss that is difficult to quantify. The "non-economic" characterization
is clearly wrong. These damages may be non-pecuniary, but they are hardly non-economic.

4 Danzon (1984) and Danzon (1986) focus on medical malpractice claim frequency specifically,
Lee, Browne, & Schmidt (1994) and Browne & Puelz (1999) focus on general tort claims and
automobile accident claims, respectively.

SDanzon (1986) presents similar evidence to Danzon (1984), but does not specifically address
the relationship between damage caps and claim frequency.










My study focuses on the effect of non-economic damage cap legislation on the frequency

of medical malpractice claim frequency, as measured by successful medical malpractice

lawsuits. My paper furthers the existing literature in several ways. As noted earlier, this is a

subj ect that has received little attention in the literature. This is the first study to examine the

impact of recent non-economic damage caps legislation on claim frequency and to use

appropriate instrumental variables estimation.

The literature that estimates the effects of various policies, including tort reforms, is

plagued by the fact that economic and political forces partly determine whether a policy is

enacted. The estimated impact of the policy may reflect the factors that played a role in enacting

the policy rather than the true effect of the policy. Others working in the policy area have

recognized this problem and have employed instrumental variables procedures to deal with the

endogeneity bias due to spurious correlation between the policy and the factors that determine

whether the policy is enacted. My study is the first to employ instrumental variable techniques

to study the effect of non-economic damage caps on the frequency of medical malpractice

claims.

My study uses a novel strategy to remedy policy endogeneity.6 The instrumental variable

policy literature assumes that only current factors determine whether a law is in place. But

legislators deal with a small number of issues each year and as a result laws are changed

infrequently. Therefore, the probability that a law is in place not only reflects the current factors

6 Other studies have treated tort reforms as endogenous. Klick & Stratmann (2003), who consider
the effect of tort reform on physician supply, use indicators for whether the state legislature is
controlled by the Democratic party, if corporations can make political contributions, and other
unspecified instruments. Rubin & Shepherd (2005), who study the effect of tort reform on
accidental death rates, use the state population voting Republican in each presidential election as
well as per capital employment in the legal profession. Sharkey (2005) uses contemporaneous
state political control as an instrument for damage caps, but Einds that it is a weak instrument and
proceeds with OLS estimation.









affecting the enactment of the law but also incorporates past influences. The cumulative

probability that a law is in place, based on current and past values of these factors, should best

explain whether the law is currently in place. I compare the fits under various formulations and

demonstrate that it is important to consider prior values in addition to current values of factors

affecting the enactment of a law. A better fit is obtained using prior influences of law enactment

than with contemporaneous influences. The best fit is obtained when the predicted probability

that a law is in place reflects the probability that the law was enacted in each of the prior years

(i.e., the cumulative probability). This unique strategy for instrumentation yields strong first

stage results, making the estimated effects of damage caps more plausible. The novel strategy

used here for taking account of the stickiness of state laws when dealing with policy endogeneity

should be of value in other studies that consider the impact of public policies.

The effects of non-economic damage caps on claim frequency are also estimated using an

alternative methodology. This approach exploits exogenous changes in the law (state court

Endings of unconstitutionality) to consider the effect of removing a cap on claim frequency.

This approach thus avoids having to deal with the endogeneity associated with the enactment of

a law.

Since caps on non-economic damages should decrease the expected return of Eiling a suit,

one would expect to find a negative relationship between claim frequency and the imposition of

damage caps. While ordinary least squares (OLS) results indicate a negative and statistically

significant relationship between non-economic damage caps and claim frequency, two-stage

least squares (2SLS) results yield different findings. When using the instrumental variables

approach, caps do not have a statistically significant effect on claim frequency. This result is

robust to a variety of specifications including different instrument definitions. Similarly,









estimates based on exogenous state Supreme Court rulings indicate that the removal of a damage

cap does not have an identifiable effect on claim frequency.

Empirical Model

Proponents of tort reform argue that caps on non-economic damages will decrease claim

frequency and claim severity, reduce malpractice premiums, and thereby improve access to

health care. It may, therefore, be difficult to argue that imposing a cap is an exogenous policy

change. To assume exogeneity, we must believe that caps on non-economic damages were not

implemented with the underlying factors of the health care industry or medical malpractice in

mind. If we suspect that caps are enacted as a result of underlying factors, then we should be

concerned that non-economic damage caps and the number of suits are simultaneously

determined, and therefore endogenous.

Model and Dependent Variable

A two-stage least squares approach is utilized to account for the potential endogeneity of

non-economic damage caps. A model representing claim frequency is specified in the following

equation:

Mart = a,, + 6S,, + PR,, + EP, + 8, + E,, (2-1)

where i = 1,...I for each state and t = 1,...T for each year. M~,, represents the natural

logarithm of the number of successful medical malpractice suits per 100,000 population in state i

in year t. Since claim frequency reflects the size of the state, the number of successful suits is





SThis logarithmic transformation was made for ease of interpretation. All models were initially
run with the number of successful medical malpractice suits per 100,000 of the population as the
dependent variable rather than the natural logarithm. Estimates obtained from the initial models
are very similar to the estimates presented here.









scaled by the state population.8 S,, is a vector indicating the state-level demographic variables

and RI, indicates a vector of tort reform variables. 9, denotes state fixed effects and 6, indicates

year fixed effects.

Independent Variables

The independent variables used to control for variations in state demographic and health

characteristics are described in this section.9 Dummy variables indicating the existence of non-

economic damage caps are also included. Additionally, state and year fixed effects were utilized

to capture unobserved state and time differences. Summary statistics are included in Table 2-1

and Table 2-2 contains the source information for each of the variables included.

Disposable Income per Capita. In general, higher levels of per capital income are

associated with better health levels. 10 Higher incomes are associated with a greater propensity for

healthy activity, less demand for medical care, and therefore less exposure to medical

malpractice. It is also possible that individuals with higher incomes are less likely to file suit

given the higher opportunity cost of their time. The predicted sign of this variable,

IncomePerCapita, is negative.





STotal suits scaled by the state population provided a better fit than total suits scaled by the
number of physicians.

9 The literature has suggested that lawyers per capital may be a determinant of claim frequency.
This variable was not included for three main reasons. First, the number of lawyers per capital is
likely to be endogenous since lawyers respond to the cost of suing. Second, lawyers per capital
may be multicollinear with the percent of the population living in a metropolitan area. Finally,
this variable was never significant in any model, and the results are therefore omitted.

10 Nominal disposable income per capital was converted to 1991 dollars using the Consumer
Price Index-Urban (CPI).









Percent of Population Living in Metropolitan Areas. The inclusion of an urbanization

variable captures the level of medical complexity and legal specialization. Urban areas are

centers of medical treatment, and are likely to offer more complex medical treatments which

could lead to more occurrences of medical malpractice. 1 Additionally, metropolitan areas may

exhibit less personal doctor-patient relationships than less urban areas. This anonymity may

contribute to a higher rate of litigation. Moreover, metropolitan areas provide greater access to

litigation. Hence, the percent of the population living in metropolitan areas, Metro, is predicted

to have a positive impact on claim frequency.

Personal Health Care Expenditures. Medical care physician visits, prescription

drugs, nursing homes, and the like are a growing portion of our economy. To capture the

importance and size of the medical sector, the level of personal health care expenditures as a

percentage of Gross State Product (GSP) has been included in this model. One would expect that

as the size of the health care industry increases, the greater the interaction between individuals

and the medical community. This increased exposure to many different components of the

medical sector could potentially lead to more medical malpractice exposure and could therefore

result in more suits. 12

Unemployment Rate. The state unemployment rate was included as a general measure

of the economic conditions during the relevant time period. When unemployment rates are high,


11 Danzon (1984) and Lee, Browne, and Schmidt (1994) also used an urbanization variable in
their studies. Each found urbanization to be statistically significant and a strong positive
determinant of claim frequency.

12 Following other studies, specific medical treatment variables had been included in my study
prior to including personal health care expenditures as a percentage of GSP. Initially, percent of
the population over age 65, surgeries per capital, outpatient visits per capital, and births per capital
were included in the model. While some of these variables had an effect on the number of suits
per capital, personal health care expenditures is a more comprehensive measure of health care
utilization and ultimately provided a better fit for the model.










opportunity cost for lawyers and those injured is low and therefore may lead to more suits. An

increase in the unemployment rate, however, could also be associated with a decrease in claim

frequency. If unemployment is high, we may see more individuals without insurance. If this is

the case, individuals without health insurance benefits may be less likely to seek medical care,

and we may see a decrease in claim frequency during economic downturns.

Non-Economic Damage Caps. Caps on non-economic damages are designed to decrease

the non-economic damages available to a plaintiff, which reduces the value of the total award. At

the margin, the expected benefits may no longer exceed the expected costs, and therefore some

medical malpractice cases will not be filed. Thus, it is possible that claim frequency will decline

following the imposition of a cap on non-economic damages. If, however, the driving force of

most suits is due to economic losses, then non-economic damage caps may have little effect on

claim frequency.

States that enacted a damage cap during the relevant data period receive a value of 1 for

the year in which their damage cap was implemented and every year thereafter. For example,

Alaska, which established a cap in 1997, receives a value of 1 for the years 1997 through 2001,

and 0 otherwise. Potential lags in policy effectiveness will be considered in Section IV.

Table 2-3 lists the states and associated years in which non-economic damage caps were

implemented as well as the dollar amount of the cap (in the year in which it was enacted). 13 Only

reforms that were implemented during the 1991-2001 period were used in this analysis. Any

state that enacted a non-economic damage cap before 1991 or that had a cap on total damages

was omitted from this analysis. Any state with a specific medical malpractice non-economic



13 Tables 2-4 and 2-5 contain more detailed documentation of state laws on non-economic
damage caps.










damage cap is included as well as any state with a non-economic damage cap on general tort

claims.

The American Tort Reform Association (ATRA) outlines its "ideal package" regarding

medical malpractice reform. Included in the suggested reforms is a severe non-economic damage

cap of $250,000, collateral source reform, and a sliding scale for attorneys' fees. The collateral

source rule prevents evidence involving payments to the plaintiff from a third party, such as

insurance payments, workers' compensation, or social security benefits, from being admitted at

trial. Collateral source reform typically involves the admissibility of third party payments at trial.

Almost all collateral source reforms took place prior to the time period considered in my study.

The other proposed reform, a sliding scale for attorneys' fees, limits the amount that attorneys

can collect in contingency fees. All states which enacted limits on attorneys' fees did so before

the time period considered in my study. Therefore, any potential effect of these reforms should

be contained in the state fixed effects. Variables indicating the presence of these two reforms are

therefore not included in the model.

While other reforms such as joint and several liability reform and limits on punitive

damages may have an impact on tort filings in general, they are not necessarily relevant when

considering medical malpractice specifically. The ATRA does not consider these reforms as an

essential remedy to the current health care crisis. Joint and several liability affects tort filings

indirectly because the reform does not directly target damages.14 Punitive damages are rarely

awarded in medical malpractice cases."5 Damages of this type are used solely to punish the


14 See Kessler & McClellan (1996) who categorize reforms as direct and indirect.

15 Eisenberg et al (1997, page 623) comment that "juries rarely award punitive damages and
appear to be reluctant to do so in areas of law that have captured most attention, products liability
and medical malpractice. Punitive damages are most frequently awarded in business/contract
cases and intentional tort cases."









defendant, not to compensate the plaintiff.16 As a result, these two reforms are not included as

independent variables in the analysis.

Instrumentation

If indeed non-economic damage caps are endogenous, an instrumental variable is

required in order to proceed. In this case, a proper instrument for the enactment of a non-

economic damage cap must be unrelated to the underlying conditions of the health care industry.

The political composition of state or federal government is often utilized as an instrumental

variable in studies of public policies. 1 In my paper, a unique instrument using state political

composition is devised in order to account for the enactment of non-economic damage caps in a

particular year. I

Tort reform, and caps on non-economic damages in particular, are policies typically

supported by Republicans. As such, we would expect to Eind caps in states with more

conservative representation. Control in this context is defined as one party controlling the State

Senate, the State House, and the Governor' s Office. If in a particular year, Republicans gain





16 It is also possible that juries use non-economic damage awards to punish physicians for
malpractice infractions beyond any compensation for pain and suffering.

17 See, for example, Klick & Stratmann (2003), Rubin & Shepherd (2005), and Sharkey (2005).

Is Several other instruments, TermLimits and M~edSchool, were initially attempted in conjunction
with RepEver, but lacked sufficient power as measured by first stage statistics. Term limits lower
the value of holding onfce and in turn can generate a lower level of contributions from special
interest groups. It is possible that a state with term limits may be less likely to adopt such laws if
special interest groups are less likely to try to influence legislators who have limited tenure.
Additionally, states with reputable medical schools may be more likely to support damage caps
to protect their prosperous physicians from being sued. To capture this idea, the union of the top
50 medical schools by research and the top 50 medical schools by primary care were used. Both
of these potential variables were determined to be weak instruments and were therefore omitted.









control of all three branches, we might expect a non-economic damage cap to be passed in that

state. Contemporaneous control, RepCurrent, equals 1 if Republicans controlled the Senate,

House, and Governor' s Office in state i in year t. If Republicans did not hold control, that state

receives a value of 0 in year t. An alternative form of the instrument involves considering prior

values of control, or when a change in political composition occurred, rather than simply the

state of current control. To capture this idea, the instrumental variable RepEver was created. This

instrument equals 1 in the first year in which the Republicans controlled all three branches of

state government between 1991 and 2001, and every year thereafter. The idea is that once

Republicans take control, a cap will be enacted and will persist every year thereafter. A non-

economic damage cap has never been rescinded, so this particular definition is credible. 19

In order for the first stage to be successful, we must have strong correlation between the

measure of political composition used and the enactment of the cap. Figure 2-1 illustrates the

relationship among the instrument RepCurrent, the instrument RepEver, and the enactment of the

damage cap by state. As shown in Figure 2-1, RepEver performs well for seven of the eight

states that enacted caps between 1991 and 2001: Alaska, Illinois, Montana, North Dakota, Ohio,

South Dakota, and Wisconsin. Illinois, for example, experienced a political shift in 1994 when

Republicans took control of the State House, State Senate, and Governor' s Office. A non-

economic damage cap was enacted in Illinois in 1995. The law adoption almost perfectly

coincides with the change in political composition. Republican control existed in Illinois during

1994 and 1995, as illustrated by RepCurrent.





19 Several non-economic damage caps have been found unconstitutional. This, however, is not a
result of a change in political composition, but rather an inherent problem with the construction
of the law.









Given that the endogenous variable is binary, it may be more appropriate to use an

alternative technique to standard instrumental variables estimation. RepEver assumes that the law

was passed when Republicans gained control of state government. But the probability that a law

is in place in a particular year reflects prior probabilities that the law was passed. In other words,

a state that has had Republican control for four years would be more likely to have a non-

economic damage cap than a state with Republican control for only one year. To take account of

this consideration, a binary choice model is utilized.20 This procedure produces valid standard

errors21 and more precise estimates. First, a logit model is estimated for observations in which a

cap has not yet been passed. The dependent variable equals 1 if the cap was enacted in that year

and 0 if no cap was enacted in that year. Explanatory variables in the logit model include

RepCurrent as well as the four explanatory variables defined previously. Predicted probabilities

obtained from the logit procedure estimate the probability that a cap was adopted in each year

given contemporaneous characteristics. For each state, these predicted probabilities can vary

over time and are higher when the Republicans control of state government. These probabilities

are then used to construct the cumulative probability that a cap was passed in year t, beginning

with 1991. For example, the probability of passing a law in year 0 is po, where po is the

predicted probability. The probability of not passing a law in year 0, therefore, is 1 po -

Similarly, the probability of not passing a law in year 1 is 1 p, To find the probability of a law

at the end of year 1, we must consider both year 0 and year 1. The probability, therefore, of a law

at the end of year 1 is 1 -(1 po )(1 p, ). This expression can be restated as po + (1 po )PI,



20 See Wooldridge (2002) pages 623-625 and Cameron & Trivedi (2005) pages 192-193.

21 Valid standard errors would not be available in the event that the first stage is a binary choice
model and the predicted values were then substituted in the second stage.









meaning that the probability of a law being enacted in year 1 is the probability that it was enacted

in year 0 plus the probability that it was enacted in year 1 times the probability that it was not

enacted in year 0.

If the predicted probabilities of adoption for this state are 0.05 in 1991 (year 0), 0.08 in

1992, and 0. 11 in 1993, then the probability of having a cap in 1991 is simply 0.05, while the

probability of having a cap in 1992 is 0. 13. Using the same method, the probability of having a

law in 1993 is estimated to be 0.22. The probability of having a cap rises over time, reflecting

more years with some prospect of adoption. The probability of having a cap is also greater in

states in which Republican's have controlled state government for multiple years.

This calculation of cumulative probabilities from the predicted probabilities is conducted

for the remaining years. In this way, the cumulative probabilities account for prior influences,

including past political composition. These cumulative probabilities are then used as an

alternative instrument to RepCurrent and RepEver. By construction, the cumulative probabilities

rise over time by state and are constrained between 0 and 1.

Data

Under the requirements of the Health Carve Quality Imp~rovementf Act,22 all medical

malpractice payments must be reported.23 These individual reports are contained in the Na~tional

Practitioner Data Ban2k (NPDB) Public Use F~ile. 24 The malpractice portion of this data set is




22 Title IV of Public Law 99-660, Health Care Quality Improvement Act of 1986.

23 The Health Care Quality Improvement Act of 1986 imposes civil penalties of up to $1 1,000
for a failure to report each medical malpractice payment, per Section 421(c).

24 National Practitioner Data BankBBBBB~~~~~~~BBBBBB Public Use File, (August 30, 2005), U. S. Department of
Health and Human Services, Health Resources and Services Administration, Bureau of Health
Professionals, Division of Practitioner Data Banks.









relatively complete in the sense that it contains all reported medical malpractice payments.25

These data do not contain information on cases Eiled that resulted in no payment, which would

include dismissals, directed verdicts, summary judgments, and verdicts for the defendant. In my

analysis, cases and payments refer to judgments for the plaintiff or settlements. No data set is

able to completely represent the total number of malpractice occurrences; however, this data set

provides a useful subset.

Each record contains information about the practitioner, such as the work state, home state,

license state, license Hield, age group, and year of graduation.26 Specific information regarding

the alleged malpractice incident includes the cause of the malpractice action, year, payment

amount, and whether the case was settled or fully litigated.

While the dataset is not suitable for some research proj ects, it is acceptable for my

purposes.27 I do not need information on physician Hield of specialization. Rather, I require a

measure of aggregate claims by state and by year for my dependent variable, which this dataset







25 Recent controversy exists as to the completeness of the data bank. If the physician named in
the original suit is removed from the Einal settlement papers, the payment is not required to be
reported. Only payments associated with physicians, not hospitals or insurance companies, are
subj ect to mandatory reporting. This loop-hole in the system has been referred to as the corporate
shield, and therefore might indicate undercounting of settlements in the data bank (Hallinan
2004).

26 The state variable required some necessary assumptions. The database reports three state
variables: work state, home state, and license state. However, only the work state or the home
state is required, not both. Additionally, a practitioner can be licensed in more than one state. In
this data set, only the first state of license listed is recorded. Work state has been used as the
primary measure of a practitioner' s state; if no work state was reported, then home state was
used. If neither home state nor work state was provided, then license state was used.

27 Other researchers, e.g., Baicker & Chandra (2004) and Matsa (2005), have used the NPDB.










provides. Although the NPDB was not designed as a research tool, it is perhaps the best

nationally collected data set on medical malpractice suits.28

Ultimately, the units of observation in this analysis are not at the individual claim level, but

rather are a measure of claim frequency per capital. Individual-level data were aggregated to the

number of successful suits in a given state, in a given year. The NPDB began collecting data at

the end of 1990 and, therefore, 1991 is the first complete year of data. Observations from 30

states for a period of 11 years, 1991-2001, were constructed. Eighteen states that had previously

enacted damage caps or total damage caps were removed from the analysis. Ultimately, the

sample was reduced further by removing several years for two specific states. Ohio and Illinois

passed non-economic damage caps between 1991 and 2001 and their courts subsequently found

them unconstitutional during the same time period. The years following the Einding of

unconstitutionality for Illinois (1998 and after) and for Ohio (1999 and after) are omitted from

the analysis. This creates an unbalanced panel dataset with a total of 324 observations.

Identification

This analysis uses a specific set of states over an eleven-year period. In order to identify

the effect of caps on claim frequency, the most appropriate comparison is between states that

enacted caps on non-economic damages between 1991 and 2001 and states that did not have

damage caps during the relevant time period. There are several ways to categorize the states and

therefore, several sets of potential comparison groups. The analysis was conducted with multiple

comparison groups in order to determine whether the results are robust and not conditional on

the specific set of states used.



28 Very few states collect detailed data on closed claims. Those that do include Florida, Illinois,
Missouri, Minnesota, Massachusetts, Nevada, and Texas, of which only Texas and Florida make
their data available for research purposes. See Black (2005).









Table 2-6 describes some specific criteria for considering the remaining potential control

states. As previously listed in Table 2-3, the states with recent non-economic damage caps are

those in Sets 1 and 2 of Table 2-6. The original analysis is estimated using only those states

described in Set 3 of Table 2-6 as comparison states, that is, states that never had non-economic

damage caps. This specification excludes states that had non-economic damage caps that were

later found unconstitutional prior to 1991. A second specification excludes only states that had

caps previously in place, but includes states that may have had caps in the past, but do not have

caps now due to laws being found unconstitutional (includes Set 4).

Since changes in the law occurred in different years for different states, it is difficult to

illustrate pre and post characteristics. In 1991, however, none of the states in the reduced sample

(Sets 1, 2, and 3) had yet adopted a non-economic damage cap. Table 2-7 presents baseline

statistics for capped states and non-capped states. As shown in the table, both sets of states look

very similar in terms of the observed characteristics. We can, therefore, be fairly confident that

the capped and non-capped states are similar prior to any policy change.

Policy Endogeneity

Many studies that consider the effect of tort reforms, and in particular non-economic

damages caps, fail to account for the fact that such policies were put into effect in a nonrandom

fashion. In other words, such policies may have underlying causes that could be correlated with

the policy change. This leads to an endogeneity problem that would bias any coefficient

estimates of the policy. In order to properly identify the effect of the policy, we must correct for

the endogeneity, but in addition, consider first the potential direction of the bias. If policies are

enacted in response to a surge in claim frequency due to omitted factors, then we might expect

the estimate of the policy change to be biased upwards. In other words, if the true effect of a non-










economic damage cap is negative (or zero), such a bias would favor a finding of no effect (or a

positive effect).

At first blush, this explanation may sound reasonable. This does not appear to be the case,

however, based on the available data. For each of the states which enacted a cap between 1991

and 2001, Table 2-8 displays the percentage change in the number of suits per 100,000 capital

between the year in which the cap was enacted (t = 0) and one year prior (t = -1) as well as

between t = -1 and t = -2 Each state is then compared to the average percentage change of the

set of comparison states (see Set 3 of Table 2-6) for the corresponding years. The comparison

group for each state with a cap is comprised of the same states, but differs according to which

years are used, since each capped state has its own specific year zero. The experience of the

comparison states is a baseline, so consider the sign of the difference column. The difference

illustrates that, relative to the comparison set, the level of litigation in most capped states was

declining somewhat, not spiking, in the two years prior to the policy change.

Between t = -2 and t = -1, only three states experienced positive differences. Only

Alaska experienced a large change in suits, which is mainly due to the low level of litigation in

that state. Between t = -1 and t = 0, only two states experienced a positive difference, where

one of the two values is close to zero. Overall, it does not appear that an abnormally high number

of suits occurred in the period before the cap for any of the capped states relative to the

comparison set.

It appears that states which enacted non-economic damage cap legislation did not do so in

response to surges in claims in the years preceding the policy change. An alternative explanation

for the endogeneity of the caps is the presence of factors which are associated with the enactment

of a cap that discourage litigation and therefore would bias claim frequency in the negative









direction. For example, there may be a common perception that medical malpractice cases are

Hiled too often, receive excessive publicized awards, or are often frivolous. There may be more of

a general backlash due to this perception in states enacting caps. This would bias the coefficient

down (i.e., more negative).

Empirical Results

First Stage

The estimates obtained from the first stage are displayed in Table 2-9. This table reports

several different instrumental variables including (1) RepCurrent, (2) RepEver, and (3)

cumulative probabilities derived from predicted probabilities from a logit model using

RepCurrent. In all three cases, the instrument is a positive and significant predictor of Cap. The

important difference among these three specifications is seen in the first stage statistics: partial

R-squared29 and F- statistic.30 Low F-statistic or partial R-squared statistics indicate the presence

of a weak instrument. RepCurrent alone does not appear to be a very strong instrument, with a

low F-statistic and partial R-squared. This contemporaneous version of control is what has

previously appeared in the literature. RepEver provides an improvement over RepCurrent, with

an F-statistic well above 10 and partial R-squared of approximately 13 percent. The statistics

associated with RepEver are consistent with the information provided in Figures 1 -8; RepEver is

a strong predictor of Cap. 31 Using the predicted cumulative probabilities from the logit model



29 A partial R-squared is defined as the variation in the endogenous variable that is explained by
the instrument. In this case, it is the variation in the adoption of non-economic damage caps that
is explained by the instrument choice. This statistic is obtained from the first-stage regression.

30 The standard threshold level for a valid instrument is an F-statistic of greater than 10
(Cameron & Trivedi, 2005).

31 The strength of the instrumental variable RepEver is not conditional on its particular definition
of control. Variations of RepEver were utilized to test the particular definition of control:
RepEver60 and RepEver2. RepEver60 requires a 60 percent maj ority of Republicans in the









with RepCurrent provides even stronger first stage statistics, with an F-statistic over 75 and a

partial R-squared of about 22 percent. Given the strength of the first stage statistics, the predicted

cumulative probabilities will be used as the preferred instrument choice in what follows.

Second Stage

The 2SLS results from estimating Equation (1) are displayed in Table 2-10. OLS results

are presented in column (1) of this table for comparison purposes. Without accounting for

endogeneity, damage caps have a negative and statistically significant effect on claim frequency.

If non-economic damage caps reduce the incentives to fie by reducing the expected benefits of

Ceiling a claim, then we might expect to Eind this result. Using the OLS estimates, one would

conclude that a cap reduces the amount of litigation by about 21 percent. But when the

instrument variables procedure is used, the coefficient is no longer statistically significant.

Columns 2 through 5 in Table 2-10 employ the predicted cumulative probabilities obtained from

the logit model as the instrument of choice. 32 Table 2-10 also displays the confidence interval

around Cap. As seen in column (2), this coefficient is imprecise. The interval ranges from a 25

percent decrease to a 18 percent increase in suits per 100,000 of the population. It is important to

note that the lack of statistical significance on the variable Cap is not a result of substantially

larger 2SLS standard errors.

The remaining coefficients are also presented in column (2). The percent of the population

living in a metropolitan area and the unemployment rate are not statistically significant.

Disposable income per capital also has a statistically significant impact on the amount of


House, in the Senate, and a Republican Governor. RepEver2 defines control according to only
the State House and Senate, but not the Governor. Each of these alternatives provided similar
results to using RepEver.

32 Similar results to those presented in Table 7 are obtained when using the other instrument
variations, RepCurrent and RepEver.










litigation. This negative coefficient fits our hypothesis. The demand for medical care was

controlled for using PersonalHealthExpend. This variable is highly significant and positive. The

coefficient indicates that a one unit increase in PersonalHealthExpend leads to a Hyve percent

increase in claim frequency.

Several other variants of capped and non-capped states were used to estimate equation (1).

The results of these alternatives are presented in columns (3) (5) of Table 2-10. Column (3)

uses the same comparison states as Column (2), however, this specification does not omit states

that had caps prior to 1991 that were found unconstitutional before or during 1991. Originally

omitted from the analysis, observations for Alabama, New Hampshire, and Washington are

included in column (3). The results using this alternative set of comparison states are very similar

to the results presented in column (2). Column (4) employs the same set of comparison states as

column (2) while column (5) uses the comparison group as column (3), but the years following

the findings of unconstitutionality in Ohio and Illinois are not omitted. Again, these results are

consistent with those presented in the original model shown in column (2). In all cases, caps

were not statistically significant. Caps do not reduce claim frequency.

Lags in Suit Duration

The dataset used in my study records claims at their date of completion, whether that date

signifies the time of settlement or the time of judgment. If caps affect the decision to file, it may

be necessary to consider a lag in suits based on several variants in duration. Not only it is

possible that there is a lag in the policy's effectiveness, but there may also be time between the

opening and closing of a claim. The previous analysis is re-estimated according to Equation (2):

M,,t~ = a,, + 6S,, + PR,, + ep, + 8, + E,, (2-2)









where s is the lag time, and is defined as either 1, 2, or 3 years. In other words, given a one year

lag, a suit that is closed in year t+1, will be explained by year t characteristics, including the

status of the state' s non-economic damage cap policy. Similarly, given a two year lag, a suit that

is closed in year t+2 will be explained by year t characteristics. In this way, this specification

accounts for both a lag in policy effectiveness as well as a lag in suit duration. Table 2-11 shows

the results from each of these three additional specifications.33 These results use the same set of

comparison states and instrument choice as column (2) of Table 2-10.

Compare the results in Table 2-1 1 to those in column (2) of Table 2-10. In all three cases,

damage caps do not have a statistically significant effect on claim frequency. The coefficients on

the remaining variables, however, lose precision when we introduce additional lags in suits.

Alternative Methodology


If caps are effective in reducing claim frequency, then the removal of a cap should increase

claim frequency. Thus, an alternative method is to examine claim frequency following the

removal of a cap due to unconstitutionality. In several states, previously enacted damage caps

were held unconstitutional by the court system.34 This approach exploits a purely exogenous

change in the law. A change in the law, implemented by the court system, is not due to the



33 When estimating models with lagged variables, the number of observations is typically
declines. However, in this case, data from the National Practitioner Data Bank is also available
for 2002-2004. Although these years were not used in the original analysis, due to data
availability of other covariates, the number of suits per 100,000 of the population for 2002-2004
are used when considering lags in suit duration. As a result, the number of years of data is not
decreased when estimating Equation (2). In addition, data for the covariates exists for 1990.
When introducing lags in suits, I am able to add one year of data (1990), or 30 observations, to
the original number of observations.

34 See Table 2-5. Those states which are relevant for this portion of the analysis include Illinois,
Ohio, and Oregon. The caps in both Illinois and Ohio were found unconstitutional at the end of
1997 and 1999, and are therefore coded as changing in 1998 and 2000, respectively.









underlying factors of the healthcare industry, but rather is based on some problem with the law' s

construction. It is safe to assume, therefore, that rulings of unconstitutionality are not

endogenous in the same way that the implementation of caps may be endogenous.

As before, we compare two groups of states: states with non-economic damage caps and

states whose caps were found unconstitutional during the relevant time period.35 In this case,

states that had caps in place throughout the time period comprise the comparison group. States

with caps which were found unconstitutional during the relevant time period define the treatment

group.36 Since each state adopted non-economic damage caps in different years, the number of

observations for each state differs. The total number of states in this section of the analysis is 23,

and the number of observations is 218.

If caps are effective in reducing claim frequency, then removing a cap will increase claim

frequency, all else equal. To test this hypothesis, the following equation was estimated:

M,,t = a,, + 3 S,, + /7 un constitutional,, + cp + 8, + E,, (3)

The coefficient on unconstitutional is the parameter of interest and is hypothesized to be

positive. All other variables are as defined in Equation (1).

The results presented in column (1) of Table 2-12 suggest that caps are not effective at

reducing suits. The coefficient is not precisely estimated, and we therefore can not identify an


35 States whose caps were found unconstitutional during the relevant time period include Illinois,
Ohio, and Oregon. The relevant comparison states include Alaska, California, Colorado, Hawaii,
Idaho, Kansas, Louisiana, Maryland, Massachusetts, Michigan, Missouri, Montana, New
Hampshire, New Mexico, North Dakota, South Dakota, Texas, Utah, and Wisconsin.

36 Some of these caps were only in effect for several years, therefore, there is some question as to
how many cases would actually have been affected by the caps during the time period. In
Illinois, for example, it is more likely that the cap (effective from 1995-1997) had a larger impact
on settlements than on suits that received judgments. This is because the cap applied to
malpractice acts committed after the law' s passage. Such suits would need to be resolved (by a
judgment or a settlement) before the law was later relaxed.









effect. As tested in the previous section, there may be some time between when a suit is filed and

when a suit is closed. To account for this, the analysis was conducted with the same three

variations of lag times in suits. The results found in columns (2) (4) of Table 2-12 are robust to

these variations. We are unable to identify an effect of removing such a cap in any of the models.

Using exogenous changes in the law does not provide any evidence that caps are effective at

reducing claim frequency.

Robustness Checks and Additional Considerations

The lack of statistical significance with respect to caps on claim frequency is of crucial

policy significance. Thus, I conducted several robustness checks using the original models

estimated with Equation (1) in this section. All robustness checks provide similar evidence; no

effect can be identified between non-economic damage caps and claim frequency.

Severe Damage Caps

For those states that have non-economic damage caps, the amount of the cap ranges from

approximately $250,000 to $600,000 in nominal terms. Additionally, several states have overall

damage cap reforms in place. Overall damage caps are limits on the total amount a plaintiff can

recover at trial economic and non-economic damages. Caps on overall (total) damages are

severe in the sense that they limit economic and non-economic components. Initially, states

which have caps on overall damages were removed from the dataset. These states, which altered

their total damage caps during the relevant time period, include Indiana, Nebraska, and

Virginia.37 In this section, let SevereCap equal 1 if state i in year t has either a non-economic

damage cap or an overall damage cap in place, and 0 otherwise. Additionally, consider overall

damage caps in conjunction with severe non-economic damage caps only (less than $500,000).

37 Indiana changed their cap in 1993, Nebraska changed their cap in 1992, and Virginia changed
their cap in 1999.










Let this variable be SevereCap2. Using the same instrumental variable procedure described

previously, Equation (1) is re-estimated using these two alternatives of the reform variable. The

results are consistent with those presented in Table 2-10. We are unable to identify an effect of

damage caps on claim frequency. These results are contained in Table 2-13.

Additional Considerations

One may be concerned that these results are affected by serial correlation. Each

observation does not contain entirely new information about each state-level observation.

Bertrand, Duflo, and Mullainathan (2004) discuss the problems of using differences-in-

differences (DD) in the presence of serial correlation. Serial correlation can produce standards

errors that are too small, meaning that we would be more likely to find an effect of a treatment

than not. If indeed serial correlation is a problem in this analysis, it would imply that the standard

errors are even larger than in the previous analysis. It is, therefore, even more likely that there is

no effect of non-economic damage caps in this context.

Conclusions

It is undeniable that the health care industry is currently facing problems that deserve

careful consideration and thoughtful solutions. Among the myriad concerns is the frequency of

medical malpractice claims. A commonly-offered solution is the use of non-economic damage

caps in medical malpractice litigation as part of a tort reform effort. Over the past 30 years,

proponents of tort reform have had some success in persuading state legislatures. Thirty states

have enacted and/or modified tort reforms by incorporating damage caps in an attempt to address

health care concerns. Due to the fact that these reforms are widespread at the state level and that

non-economic damage caps are being proposed at the national level, it is essential that policy

makers understand the true effects of such reforms.









To analyze this issue, I utilize two different approaches. First, I treat caps as endogenous

using a unique instrument of political control. This novel approach should be of value to studies

that consider the impact of public policies. The literature has used contemporaneous political

measures as instrumental variables for the enactment of public policies. My paper, however,

recognizes that laws are sticky and that the probability that a law is in place hinges upon

probabilities that the law was enacted in prior years. I calculate cumulative probabilities using

predicted probabilities of enacting a cap obtained from a logit model. Using the cumulative

probabilities as an instrument for the enactment of a damage cap yields strong first stage results.

In the 2SLS estimates, I find no evidence to suggest that non-economic damage caps are

effective in reducing medical malpractice claim frequency. This finding is robust to a variety of

additional specifications, including different instruments and alternative sets of comparison

groups. Second, I exploit exogenous changes in the law, when state courts find damage cap

legislation to be unconstitutional. Again, I can identify no effect between caps and claim

frequency. Since caps are ostensibly intended to reduce claim frequency, this particular tort

reform strategy may be misguided.










Table 2-1. Summary statistics of variables*
Standard
Variable Mean Deviation Median Minimum Maximum
Ln(Suits) 1.70 0.42 1.69 0.53 2.69
Suitsperl00Capita 6.02 2.67 5.40 1.70 14.8
IncomePerCapita 17,857 2,572 17,610 12,525 26,375
Metro 64.05 22.89 67.83 23.50 100.00
PersonalHealthExpend 12.13 2.00 12.31 6.16 16.64
Unempl 5.17 1.44 5.08 2.24 9.23
Cap 0.142 0.350 0 0 1

*This table contains observations for all states which enacted non-economic damage caps during the
relevant time period and states which never had non-economic damage caps. These statistics include 30
states over 11 years (330 observations).










Table 2-2: Data sources
Data
Disposable Income per Capita (real)
Consumer Price Index
Percent of Population Living in
Metropolitan Areas

Personal Health Care Expenditures
(as a percent of GSP)

Unemployment Rate
Population
Non-economic Damage Caps















Political Control Data


Term Limits
Medical School Rankings


Source Information
Bureau of Economic Analysis (BEA), www.bea.gov
The Economic Report of the President, 2004
Statistical Abstract of the United States,
National Data Book (Note: These data are reported every other
year and required interpolation for the remaining years)
Centers for Medicare and Medicaid Services,
www.cms.hhs.gov

Bureau of Labor Statistics (BLS), www.bls.gov
Census Bureau, www.census.gov
No one source provides accurate data on the status, date of
enactment, date of change, or amount of caps. A number of
sources were used. These include (but are not limited to) the
following :
(1) American Tort Reform Association (ATRA), Medical
Liability Reform, http://www.atra.org/show/7338
(2) ATRA Tort Reform Record, December 31, 2003.
www.atra.org
(3) Center for Justice and Democracy, www.centerjd.org
(4) National Conference of State Legislatures, State Medical
Liability Laws Table,
http://!www.ncsl .org/program s/insur/medliability .pdf
(5) McCullough, Campbell & Lane, Summary of Medical
Malpractice Law, www.mcandl.com
(1) Book of the States
(2) Statistical Abstract of the United States, National Data
Book
Book of the States, 2002
U.S. News & World Reports, America 's Best Graduate
Schools 2006, "Top Medical Schools Primary Care" and
"Top Medical Schools Research










Table 2-3. States enacting non-economic damage reforms (1991-2001)
State Year Nominal Amount ($)
Alaska 1997 $400,000
Illinois 1995 $500,000
Montana 1995 $250,000
New Mexico 1992 $600,000
North Dakota 1995 $500,000
Ohio 1997 $250,000
South Dakota 1997 $500,000
Wisconsin 1995 $350,000
Some state courts found non-economic damage caps unconstitutional. Illinois held the cap
unconstitutional in 1997 while Ohio held the cap unconstitutional in 1999. See Best v. Taylor
M~ach. Works, 689 NE 2d. 1057 (1997) and State ex rel. Ohio Academy of Trial Lawyers v.
\iu, JI,,, 86 Ohio St. 3d 451 (1999), respectively.










Table 2-4. State limits on damages
State Year Amount


Description
Non-economic damage cap; Held
unconstitutional in 1991.
Non-economic damage cap.


Non-economic damage cap.
Non-economic damage cap.


Non-economic damage cap for single
practitioner (($1 million for multiple
practitioners) .
No-- cnmcdaaec
Non-economic damage cap.
Non-economic damage cap.
Overall (total) damage cap.
Non-economic damage cap; Held
unconstitutional in 1997.

Non-economic damage cap.

Cap on all damages, exclusive of
future medical expenses and related
benefits .

Non-economic damage cap.
Increased by $15,000 every year
thereafter.
Non-economic damage cap.
Non-economic damage cap.
Non-economic damage cap (or
$500,000 under extreme
circumstances).
Non-economic damage cap, but does
not apply to pain & suffering damages.
Non-economic damage cap.
Non-economic damage cap.
Non-economic damage cap.
Overall (total) damage cap.
Non-economic damage cap.
Non-economic damage cap; held
unconstitutional in 1991.


Alabama
Alaska
Anizona
Arkansas
California
Colorado
Connecticut
Delaware


Florida
Georgia
Hawa~ii
Idaho

Indiana

[Illinois
Iowa
Kansas
Kentucky


Louisiana
Maine
Maryland


Massachusetts
Michigan*


1987
1997


1975
1988





2003

1986
1987
2003
1993

1995

1988



1975

1986

1994
1986
1986


1993

1986
2003
1986
1995
1992
2002

1986


$400,000
$400,000


$250,000
$250,000





$500,000

$375,000
$400,000
$250,000
$1.25 mil

$500,000

$250,000



$500,000

$350,000

$500,000
$500,000
$225,000


$280,000

$400,000
$500,000
$350,000
$250,000
$1.75 mil
$350,000

$875,000


Minnesota
Mississippi
Missouri*
Montana
Nebraska
Nevada

New Hampshire
New Jersey










Table 2-4. State limits on damages (continued)
State Year Amount


Description
Total damage cap, but does not include
punitive or future medical expenses
and related benefits.


Non-economic damage cap.
Non-economic damage cap.
Non-economic damage cap (or
$500,000 under extreme
circumstances): held unconstitutional
in 1999.
Non-economic damage cap (applies to
pregnancy and emergency care only).
Non-economic damage cap: held
unconstitutional in 1999.



Non-economic damage cap.

Non-economic damage cap: applies
only to wrongful death actions.
Non-economic damage cap.
Non-economic damage cap.

Overall (total) damage cap.

Non-economic damage cap.
Non-economic damage cap.


New Mexico
New York
North Carolina
North Dakota




Ohio

Oklahoma

Oregon
Pennsylvania
Rhode Island
South Carolina
South Dakota
Tennessee

Texas
Utah*


1992


1995
2003



1997

2003

1987



1997


1977
1986
2001


$600,000


$500,000
$350,000



$250,000

$350,000

$500,000



$500,000


$500,000
$250,000
$400,000


Vermont -
Virginia 1999 $1.5 mil
Washington -
West Virginia 1986 $1 mil
Wisconsin* 1995 $350,000
Wyoming -- --
*"Limits on damages are adjusted for inflation.










Table 2-5. Non-economic damage caps held unconstitutional
Year
State Year Enacted Unconstitutional Amount
Alabama 1987 1991 $400,000
[Illinois 1995 1997 $500,000
$500,000
Ohio* 1997 1999 ($250,000 if less severe)
New Hampshire 1976, 1986 1980,1991 $875,000
Minnesota 1986 1990 $400,000
Oregon 1987 1999 $500,000
43% wage *life
Washington 1986 1989 expectancy
*Ohio re-enacted a cap in 2003, however, this does not apply to the data used in this analysis.










Table 2-6. Description of categories of states
Set No. Criteria
States which enacted non-economic damage
caps and they were not found
1 6 unconstitutional.

States which enacted non-economic damage
caps between 1991-2001, but whose caps
were found unconstitutional between 1991-
2 2 2001.



State which never had damage caps during
3 22 the relevant time period.

States which had non-economic damage caps
in place prior to 1991, where these caps were
4 3 found unconstitutional before/during 1991.

States which had non-economic damage caps
in place prior to 1991, where these caps are
5 13 still in effect.

States which had non-economic damage caps
in place prior to 1991, where the cap was
6 1 found unconstitutional between 1991-2001.


7 3 States with caps on total damages.


States



AK, MT, NM, ND,SD, WI





IL,0H

AR, AK, CT, DE, FL, GA, IA, KY,
ME, MN, MS, NV, NJ, NY, NC,
OK, PA, RI, SC, TN, VT, WY


AL, NH, WA


CA, CO, HI, ID, KS, LA, MD, MA,
MI, MO, TX, UT, WV



OR


IN, NE, VA










Table 2-7. Baseline statistics (1991)
States with Caps
(8 states)
Variable Average Standard
Deviation
Ln(Suits) 1.84 0.42
Suitsperl100 6.8 2.54
Metro 54.08 221.6
IncomePerCapita 16,408 2,252
Unempl 6.25 1.71
PersonalHealthExpend 11.63 2.64


States without Caps
(22 states)
Average Standard
Deviation
1.68 0.43
5.90 2.70
67.13 23.5
16,870 2,620
6.58 1.10
11.66 1.96











Table 2-8. Change in suits between year t-2 and t-1; t-1 and t=0


States with
Caps
Percent Change
from t-2 to t-1
70.26%
-14.05%
14.68%

11.87%
1.98%
-3.19%
-11.63%
States with
Caps
Percent Change
from t-1 to t-0
-44.84%
-18.36%
-23.72%
-5.02%
-28.12%
-8.70%
-0.27%
12.30%


States without
Caps
Percent Change
from t-2 to t-1
4.76%
3.58%
3.58%

2.08%
4.76%
4.76%
3.58%
States without
Caps
Percent Change
from t-1 to t-0
-1.49%
-11.72%
-11.72%
6.16%
-11.72%
-1.49%
-1.49%
-11.72%


State
Alaska
[Illinois
Montana
New Mexico
North Dakota
Ohio
South Dakota
Wisconsin




State
Alaska
[Illinois
Montana
New Mexico
North Dakota
Ohio
South Dakota
Wisconsin


Difference
65.49%
-17.63%
11.10%

9.80%
-2.79%
-7.96%
-15.20%




Difference
-43.35%
-6.64%
-12.00%
-11.18%
-16.39%
-7.21%
1.22%
24.03%






































significant at 10%; ** significant at 5%; *** significant at 1%
First stage results were obtained using ordinary least squares (OLS) estimation.


Table 2-9. First stage results
(1)
IV=RepCurrent


(2)
IV=RepEver

Cap
-0.00002
[0.00004]
0.019
[0.0128]
0.0596
[0.0221]***
0.0506
[0.0229]**
0.3341
[0.0507]***
324
30
0.71
Yes
Yes


(3)
IV=Cumulative
Probabilities
Cap
-0.000089
(0.000036)**
-0.0254
(0.0132)*
0.0286
-0.0214
0.0301
-0.0217
1.4359
(0.1637)***
324
30
0.74
Yes
Yes

76.98
0.2162


Variable Name
IncomePerCapita

Metro

Unempl

PersonalHealthExpend

Instrument


Cap
-0.00006
[0.00004]
0.0192
[0.0136]
0.0586
[0.0236]**
0.0356
[0.0242]
0.1133
[0.0485]**


Observations 324
Number of States 30
R-squared 0.67
State Fixed Effects Yes
Year Fixed Effects Yes
First Stage Statistics
F-statistic 5.46
Partial R-squared 0.0192
Standard errors in parentheses


43.50
0.1349










Table 2-10. Ordinary least squares (OLS) and two-stage least squares (2SLS) results


(1)
OLS


(2)
2SLS
IV=Cumulative
Probabilities
Ln(Suits)
-0.00007
[0.00004]*
0.0104
[0.0115]
-0.0315
[0.0236]
0.052
[0.0200]***
-0.0366
[0.1096]
324
30
0.85
Yes
Yes


(3)
2SLS
IV=Cumulative
Probabilities
Ln(Suits)
-0.00007
[0.00003]**
0.0112
[0.0113]
-0.0314
[0.0212]
0.0446
[0.0196]**
-0.0538
[0.1064]
357
33
0.86
Yes
Yes

85.45
0.2166


(4)
2SLS
IV=Cumulative
Probabilities
Ln(Suits)
-0.00007
[0.00004]*
0.0102
[0.0115]
-0.0329
[0.0236]
0.0545
[0.0202]***
-0.0248
[0.1134]
330
30
0.84
Yes
Yes

65.27
0.1863


(5)
2SLS
IV=Cumulative
Probabilities
Ln(Suits)
-0.00007
[0.000033]**
0.0111
[0.0112]
-0.0325
[0.0212]
0.0474
[0.0197]**
-0.0453
[0.1104]
363
33
0.86
Yes
Yes

71.82
0.1857


Variable Name
IncomePerCapita

Metro

Unempl

PersonalHealthExpend

Cap

Observations
Number of States
R-squared
State Fixed Effects
Year Fixed Effects
First Stage Statistics
F-statistic
Partial R-squared
Confidence Intervals


Ln(Suits)
-0.000081
[0.000034]**
0.0166
[0.0117]
-0.0281
[0.0203]
0.0586
[0.0208]***
-0.2106
[0.0506]***
324
30
0.83
Yes
Yes


76.98
0.2162


(-0.2777,
-0.0890)


(-0.2523,
0.1792)


(-0.2631,
0.1555)


(-0.2479,
0.1984)


(-0.2625,
0.1719)


Cap


Robust standard errors in parentheses
*significant at 10%; ** significant at 5%; *** significant at 1%

Columns (1) and (2) present the results of Equation (1) omitting states (20) which had caps before 1991
(and still have caps today), states which had caps before 1991 which were found unconstitutional, and states
which have caps on total damages. The years after the Ohio and Illinois caps were found unconstitutional
are also omitted.
Column (3) omits the same states as in column (2), but includes observations for Alabama, New Hampshire,
and Washington. These are states whose caps were found unconstitutional before or during 1991, and
therefore do not have caps during the relevant time period.
Column (4) contains the same set of states as columns (1) and (2), but does not omit the years following the
findings of unconstitutionality for Ohio and Illinois.
Column (5) contains the same set of states as column (3), but does not omit the years following the findings
of unconstitutionality for Ohio and Illinois.










Table 2-11i. 2SLS results variants of duration*
(1) (2
One Year Lag T
Variable Name Ln(Suits) L
IncomePerCapita -0.00004-
[0.00004] [0
Metro 0.0144 0
[0.0097] [0
Unempl -0.0063 0
[0.0205] [0
PersonalHealthExpend 0.035 0
[0.0197]* [0
Cap -0.0279 0
[0.0990] [0
Observations 354 3.
Number of States 30 31
R-squared 0.83 0
State Fixed Effects Yes Y
Year Fixed Effects Yes Y


wo Year Lag
n(Suits)
0.00002
,.00003]
.0035
).0083]
.0149
).0198]
.0027
).0185]
.0276
).0991]
54
0
.83
es
es


(3)
Three Year Lag
Ln(Suits)
-0.00004
[0.00003]
-0.0094
[0.0102]
-0.0009
[0.0179]
-0.0154
[0.0181]
-0.0375
[0.0927]
354
30
0.83
Yes
Yes


First Stage Statistics
F-statistic
Partial R-squared


76.44
0.1988


76.44
0.1988


76.44
0.1988


Robust standard errors in parentheses
significant at 10%; ** significant at 5%; *** significant at 1%
*The control states in this table correspond to the initial specification of control states
used in column (2) of Table 6.










Table 2-12. OLS results using, unconstitutionality of caps*


(1)
No Lag
Ln(Suits)
-0.00014
(0.000029)**

0.0147
(0.0089)
-0.0187
(0.0218)
0.0662
(0.0446)
-0.0319
(0.0649)
218
0.82
Yes
Yes


(2)
One Year Lag
Ln(Suits)
-0.00006

(0.000035)*
0.0119
(0.0080)
0.0155
(0.0181)
0.0292
(0.0328)
-0.0511
(0.0646)
221
0.83
Yes
Yes


(3)
Two Year Lag
Ln(Suits)
0.00002

-0.000038
0.0043
(0.0069)
0.0118
(0.0145)
0.0883
(0.0340)**
-0.0641
(0.0709)
232
0.83
Yes
Yes


(4)
Three Year Lag
Ln(Suits)
0.00005

-0.000033
-0.0096
(0.0107)
0.0338
(0.0154)**
0.0789
(0.0323)**
0.0131
(0.0660)
232
0.83
Yes
Yes


Variable Name
IncomePerCapita


Metro

Unempl

PersonalHealthExpend

Unconstitutional

Observations
R-squared
State Fixed Effects
Year Fixed Effects


Robust standard errors in parentheses
significant at 10%; ** significant at 5%; *** significant at 1%










Table 2-13. Results for severe cap.
(1)
2SLS
Ln(Suits)
Variable Name SevereCap
RealPCdispos -0.00006
(0.00004)*
Metro 0.0148
(0.0114)
Unempl -0.038
(0.0214)*
PersonalHealthExpend 0.063
(0.0201)***
Cap -0.0482
(0.1072)
Observations 346
Number of States 32
R-squared 0.85
State Fixed Effects Yes
Year Fixed Effects Yes
First Stage Statistics


(2)
2SLS
Ln(Suits)
SevereCap2
-0.00007
(0.00004)*
0.0144
(0.0110)
-0.0398
(0.0210)*
0.0631
(0.0201)***
-0.0919
(0.2013)
346
32
0.85
Yes
Yes


F statistic 76.75 27.84
Partial R-squared 0.2043 0.0852
Robust standard errors in parentheses
significant at 10%; ** significant at 5%; *** significant at 1%














Figure 1 Alaska Figure 2 Illinois Figure 3 Montana







1991 1993 1995 1997 1999 2001 1991 1993 1995 1997 1999 2001 1991 1993 1995 1997 1999 2001
year year year
RepEver RepCurrent -8- RepEver RepCurrent -8- RepEver RepCurrent

Figure 4 New Mexico Figure 5 North Dakota Figure 6 Ohio


1991 1993 1995 1997 1999 2001 1991 1993 1995 1997 1999 2001
year year
RepEver RepCurrent -8- RepEver RepCurrent

Figure 7 South Dakota Figure 8 Wisconsin





uCap

1991 1993 1995 1997 1999 2001 1991 1993 1995 1997 1999 2001
year year
-8- RepEver RepCurrent -8- RepEver RepCurrent


1991 1993 1995 1997 1999 2001
year
-8- RepEver RepCurrent


Figure 2-1. Description of enactment of cap and change in political composition









CHAPTER 3
THE EFFECTS OF INCREASED ACCESS TO THE MORNNG-AFTER PILL ON
ABORTION AND STD RATES

Introduction

Over six million pregnancies occur each year in the United States: three million are

unintended and over one million are terminated by abortion.38 Some of these unintended

pregnancies could be prevented and the corresponding abortions avoided with easier access to

emergency contraception. Emergency contraception, also known as the morning-after pill or Plan

B, is a type of birth control that can be taken up to 72 hours after sexual activity that can prevent

a pregnancy from occurring. On August 24, 2006, the FDA approved sales of emergency

contraception through pharmacists without a prescription for individuals age 18 and older.39 This

approval follows a previous rejection by the FDA of a proposal that would have allowed

emergency contraception to be available over-the-counter without an age restriction.40 In its

earlier rej section, the FDA pointed to potential misuse by teenage girls, who would be able to

purchase the product without a doctor' s supervision. The recent decision restricts access to

women over the age of 18, thereby alleviating this particular concern. Those who oppose easier

access raised concerns that over-the-counter access could lead to increased sexual activity.41

Pharmacy access to emergency contraception was an approach first adopted in the U.S. by

the State of Washington. In 1997, Washington began a pilot program to expand access to

emergency contraception through pharmacies. Enabling pharmacy provision dramatically

changes the accessibility of emergency contraception. Pharmacy access facilitates faster

38 Contraception Counts, March 2006, Alan Guttmacher Institute, www.nuttmacher.orn.

39 Harris (August 25, 2006).

40 CB S News, May 6, 2004.

41 CBS News, June 11, 2006.









provision of the medication because there are no appointment delays with a doctor. Moreover, it

provides evening and weekend access. Since 1997, eight states have followed Washington's

lead, adopting similar initiatives allowing pharmacists to dispense emergency contraception

without a prescription.42 Eight additional state legislatures have introduced similar legislation,

but failed to pass it, while two other bills are still under consideration.43 By studying the effects

of the program in Washington, we can gain an understanding of how pharmacy access may affect

the rest of the country in the future. Focusing on Washington, the first state to change access,

utilizes the most post-implementation years. Additionally, although eight other states have since

implemented similar initiatives, many of these laws were passed quite recently.

Increased accessibility to emergency contraception reduces the expected costs of engaging

in sexual activity. If a pregnancy is possible, whether due to contraceptive failure or unsafe

sexual activity, use of emergency contraception can prevent an unwanted pregnancy.

Additionally, emergency contraception may be more ethically appealing in that it works like oral

contraceptives to prevent a pregnancy from occurring rather than terminating an existing

pregnancy. If emergency contraception is used as a substitute for a subsequent abortion, then

abortion rates could decline. If individuals recognize that the costs associated with engaging in

risky sexual behavior are lower, however, then these individuals may enj oy greater risk taking. If

indeed increased access to emergency contraception increases the amount of sexual behavior, it

is possible that sexually transmitted disease (STD) rates will also increase as a result.




42 These states include Alaska, California, Hawaii, Maine, Massachusetts, New Mexico, New
Hampshire, and Vermont.

43 Proposals failed in Colorado, Kentucky, Illinois, Maryland, Oregon, Texas, Virginia, and West
Virginia. Proposals are still in progress in New Jersey and New York, although similar proposals
in these states have previously failed to pass (http://www.go2ec. org/Legi slation.htm).










In my paper, I consider the intended and unintended consequences of increased access to

emergency contraception. Using county-level data on Chlamydia rates and abortion rates as well

as dates of pharmacy participation, I estimate the treatment effect, if any, of pharmacy access to

emergency contraception on several outcomes. The results indicate that pharmacy access is

associated with an increase in Chlamydia rates, both overall and for females, and is associated

with a decrease in abortion rates for some age groups. This result is robust to the use of an

alternative comparison group as well as alternative definitions of treatment.

My paper contribute s to the exi sting literature by exploiting a difference-in-di fference

methodology to consider the impact of pharmacy access to emergency contraception. Although

difference-in-difference estimates could suffer from selection bias due to individual pharmacist

or pharmacy participation decisions, I show that the treatment and control groups are statistically

indistinguishable in terms of Chlamydia rates. Although the treatment and control groups are

statistically distinguishable in terms of abortion rates, selection would bias the estimates

upwards, i.e., in favor of finding no effect. My estimates, therefore, are conservative estimates of

the relationship between pharmacy access and abortion rates.

Previous Literature

Economic models generally assume that individuals respond to economic and policy-

related factors. Economic models related to risky behavior are no exception. Empirical evidence

suggests, however, that this is often, but not always the case. In contrast, non-economic models

of risky behavior often assert that individuals, and teens especially, make decisions in a more

spontaneous or random fashion. This section provides an overview of the economic literature on

risky sexual behavior and its potential consequences, as well as reviews some related medical

studies.









An extensive literature exists on the effects of various public policies on risky behavior

and the potential consequences. There is much less literature, however, on risky sexual behavior.

For present purposes, the most relevant literature involves those papers which focus on the

increased accessibility and availability of family planning services or emergency contraception

on outcomes such as pregnancy, abortion, and STDs. Paton (2002) considers the impact of the

increased provision of family planning services in England on underage conceptions and

abortions. He Einds no evidence that increased attendance at family planning clinics reduces teen

pregnancy or abortion. Additionally, he considers the impact of a court ruling, which for

approximately one year barred family planning services from being offered to women under the

age of 16 without parental consent.44 A reduction in the accessibility to family planning services

should affect this age group differently than those aged 16-19 (who were unaffected by the

ruling). Paton, however, found no evidence that these two groups experienced different

conception or abortion rates. In another study, Paton (2006) Einds no effect of the provision of

emergency contraception at family planning clinics on abortion rates. The author, however,

identifies a positive effect on STD rates. Finally, Girma and Paton (2006) Eind no effect of free

access to over-the-counter emergency contraception on teen pregnancy rates using a matching

estimator approach. All three of these papers use regional data from England.

Several medical papers exploit randomized control trials to examine the impact of

emergency contraception or family planning services on a variety of outcome measures. The

initial sample selection of women, however, may be problematic in these studies. In Raine et al,

(2005), for example, a randomized control trial was administered in California between July

2001 and June 2003. Their initial sample, however, included women aged 15-24, who had been


44 The ruling was the Gillick ruling in December 1984; it was later overturned in 1985.









sexually active in the last 6 months, who could participate in a follow-up visit 6 months later,

and who were already attending the family planning clinic. Women were randomized into three

groups of emergency contraception access: (1) advanced provision, (2) pharmacy access, and (3)

clinic access. The administrators of the trial, however, eliminated Group (3) in December 2001

because the California legislature passed pharmacy access legislation. The maj ority of the study,

therefore, compared Group (1) to Group (2). Given the high level of access in both groups, we

may not expect to find a difference in abortion or STD incidence between Groups (1) and (2).

Utilizing group (3) gives a baseline of traditional access for comparison purposes. The study

found no evidence that Groups (1) and (2) were different in terms of pregnancy or STD rates.

Several other studies have used similar randomization procedures, but fail to find any difference

in abortion, pregnancy, or STD rates. The evidence, however, is consistent in showing that

advanced provision of emergency contraception does increase its use. 45

A somewhat separate literature examines the effects of various policies on state-level STD

rates. Such policies affect the costs and benefits of engaging in risky behavior and may in turn

affect sexual outcomes. Sen (2003a) and similarly Sen (2003b) consider the effect of restrictions

on Medicaid funding for abortions on risky sexual behavior, measured by state-level gonorrhea

rates.46 Increased restrictions on Medicaid funding for abortions increase the price of abortions to

individuals who would otherwise rely on Medicaid payment. If the price of an abortion increases,

we would expect individuals to engage in less risky sexual behavior because an unintended

pregnancy would be more costly. This should lead to a reduction in sexual activity, which could

45 Glasier and Baird (1998), Falk et al (2001), and Glasier et al (2004).

46 Several studies have considered state-level Medicaid funding restrictions, but have focused on
abortions, pregnancies, and births as the outcome measures. The results are these papers are
consistent; increases in the price of abortion decreases the demand for abortion. See Blank,
George, and London (1996), Hass-Wilson (1996), and Levine, Trainor, and Zimmerman (1996).









be reflected in lower STD rates. In both papers, using slightly different panel data techniques,

Sen is unable to identify an effect of Medicaid funding restrictions on gonorrhea rates.

In contrast to Sen's restriction in abortion access, Klick and Stratmann (2003) analyze the

exogenous change of abortion legalization on risky behavior measured by state-level gonorrhea

and syphilis rates. If abortion lowers the cost of engaging in sexual activity by providing

insurance in the event of a pregnancy, then the legalization of abortion could increase risky

behavior and therefore STD rates. Klick and Stratmann find that STD rates increased as a result

of abortion legalization, confirming this hypothesis.

Many researchers have studied the relationship between alcohol or substance use and

sexual behavior and its potential consequences.47 Although previous literature has positively

linked alcohol consumption to sexual behavior,48 the identification strategies used are

questionable because substance abuse and sexual decisions are dependent upon a common set of

unobservable personal factors.49 Other studies consider public policies targeted at alcohol or

drugs. Restrictive alcohol policies, such as higher taxes on alcohol or stricter drunk driving laws,

have the potential to reduce alcohol consumption which could in turn reduce risky sexual





47 See, for example, Sen (2003) who studies the effect of beer taxes on teen abortion rates,
finding a small but statistically significant negative effect on abortion rates.

48 See, for example, Graves & Leigh (1995).

49 Two specific studies attempt to correct for this omitted variable problem by employing
instrumental variables approaches. Rees et al (2001) find that the link between substance use and
sexual activity is weaker than previously suggested in the literature. In contrast, Sen (2002) finds
that substance use increases the probability of engaging in sexual activity. Rashad and Kaestner
(2004), however, discuss the pitfalls of these identification strategies, suggesting that the
relationship between substance abuse and sexual behavior is still uncertain. As with most
instrumental variables approaches, the success of the identification strategy lies heavily in the
exogeneity and correlation of the instruments; these two criteria are questioned in both papers.









behavior. 5o Chesson et al (2000) use state-level panel data to consider the impact of liquor and

beer taxes on STD rates. The authors find that an increase in either tax is associated with a

reduction in gonorrhea and syphilis rates. Grossman et al (2004) consider the impact of alcohol

taxes as well as drunk driving laws on the incidence of gonorrhea. 51Similar to Chesson et al, the

authors find that more restrictive alcohol policies have a negative effect on gonorrhea rates, but

this result is only statistically significant for males. In a similar paper, Carpenter (2005)

examines the impact of Zero Tolerance Laws on state-level gonorrhea rates. He finds that the

adoption of a Zero Tolerance policy has a negative effect on gonorrhea rates, but this effect is

only significant for males between the ages of 15 and 19.

My paper j oins a small literature focusing on the effects of emergency contraception and

other family planning services on abortion rates and STD rates. The main papers in the economic

literature discussed previously (Paton (2002), Paton (2006), and Girma and Paton (2006)) present

findings from England. However, England experiences much lower rates of teen pregnancy,

abortion, and sexually-transmitted disease than the United States.52 In the economic literature,

this paper is the first to consider the American experience of pharmacy access to emergency

contraception. I utilize a difference-in-difference approach by exploiting the similarities between

the treatment and control groups before the program began. Using the differences across




so More restrictive alcohol policies could also reduce abortions through a decrease in risky
behavior. Sen (2003) finds evidence that higher beer taxes are associated with small but
statistically significant reductions in teen abortion rates.

51 Chesson et al use a panel data framework with a lagged dependent variable and fixed effects.
Estimation in this way is inconsistent because of the endogeneity of the lagged dependent
variable. Grossman et al improve on this specification by accounting for the endogeneity and
implementing FD2SLS with subsequent lagged dependent variables as instruments.

52 Darroch, Singh, & Frost (2001).









participating and nonparticipating counties as well as timing of participation, I estimate a

treatment effect of pharmacy access on several outcome measures.

The Relative Costs of Sexual Activity

We generally assume that individuals behave rationally, taking account of the costs and

benefits of engaging in a particular behavior. There is some debate as to whether individuals,

especially teens, make sexual decisions rationally or make such decisions in a more random

fashion.53 Levine (2000) Einds evidence suggesting that individuals behave rationally with

respect to sexual decisions, that is, they respond to incentives or to changes in costs and benefits.

His results indicate that individuals respond to specific changes in costs and benefits, such as

changes in labor market conditions, abortion access, welfare benefits, and AIDS prevalence.

In particular, my paper focuses on individual responses to changes in costs. If the cost of

an activity (sexual behavior, for example) increases, we would expect the associated behavior to

decrease simply because the costs are higher and may not outweigh the benefits for some

individuals. If, however, individuals make sexual decisions in a random fashion, i.e., fail to

weigh the costs and benefits of a particular decision, then changes in the costs of sexual activity

or its potential consequences may have no effect on sexual behavior.

Increased access and awareness of emergency contraception represents a decrease in the

cost of engaging in sexual behavior. Emergency contraception decreases the potential costs of

engaging in sexual activity, because it can eliminate a potential pregnancy before it actually

occurs. This may forgo possible moral dilemmas that arise with abortion decisions. We would

expect, therefore, that changes in the costs associated with engaging in risky sexual behavior

affect the amount of sexual activity. If the costs associated with engaging in sexual activity, or



53 Paton (2006).









the costs associated with a potential pregnancy, decrease, then we would expect the amount of

this behavior to increase. This could be reflected in an increase in the rate of sexually transmitted

diseases.

Pharmacy Access to Emergency Contraception

History of Emergency Contraception

In 1997, the FDA approved the use of certain oral contraceptive pills for use as

emergency contraception, although they had been used on an off-label basis for years. As

demonstrated by Albert Yuzpe in 1974, use of oral contraceptives in specific dosages after a

sexual encounter can be used as a safe and effective method of preventing pregnancy. This

method, known as the Yuzpe method, is the basis for today's morning-after pill. Preven, the first

emergency contraception on the market, was approved by the FDA in 1998 and is modeled after

the Yuzpe regimen. Two tablets are taken initially and then followed by two additional tablets 12

hours later. Plan B, a progestin-only product, was approved in 1999 and is now the only

emergency contraception on the market. 54

The Washington State Pilot Project

Pharmacists in Washington State have been able to form collaborative agreements with

physicians since 1979.5 A collaborative agreement grants a pharmacist the ability to dispense a

prescription medication, within a specified protocol, without a physician's prescription. Outlined

in the agreement is the particular medication, the criteria for who is eligible to receive the

medication, and the process of review regarding pharmacist decisions by the prescriber.


54 Preven was discontinued by its manufacturer, Barr Laboratories, in 2004.

55RCW 18.64.011. Originally, collaborative agreements were Hiled according to individual
pharmacies, with a primary responsible pharmacist named on the agreement. After the fall of
2003, the Board of Pharmacy began recording collaborative agreements by individual
pharmaci st.









Collaborative agreements have been used successfully in Washington with other medications,

and are also common in other states.56 Currently, eight other states have similar initiatives.

A Washington State report estimated that 53 percent of pregnancies in Washington in 1997

were unintended."' At that time, emergency contraception was available only through a

physician. Not only were many women unfamiliar with emergency contraception, but health care

professionals rarely discussed emergency contraception with their patients. As a result of these

concerns, the Emergency Contraception Collaborative Agreement Pilot Proj ect was initiated in

July of 1997. The program was the first of its kind to enable pharmacists to directly dispense

emergency contraception without a prescription. This is, however, distinctly different from an

over-the-counter designation. The main goal of the program was to reduce unintended

pregnancies in Washington through increased access to and awareness of emergency

contraception. 58Participants included the Washington Board of Pharmacy, Washington State

Pharmacy Association, University of Washington Department of Pharmacy, and an organization

called PATH (Program for Appropriate Technology in Health). Funding was provided by the

David and Lucile Packard Foundation, while media coverage was handled by Eglin DDB Seattle.

The planning phase of the program began in July of 1997, while the maj ority of the

program activities occurred during the 16-month period between February 1998 and June 1999.

The pilot program encouraged Washington pharmacists to form collaborative agreements with

respect to emergency contraception. Pharmacies continued to file for access well after the official



56 COllaborative agreements have been used with respect to other medications such as
immunizations, asthma therapy, diabetes screening, cholesterol screening, and chronic disease
management (Gardner et al).

57County Profiles, Birth and Unintended Pregnancy Statistics: February 2001, Washington State
Department of Social and Health Services.
58Gardner et al. (2001).









program ended. Once a pharmacist forms such an agreement with a physician, the agreement is

submitted to and approved by the State Board of Pharmacy.59 Agreements were initially valid

until 2001 and then required a renewal every two years thereafter.60 IHEOrmation about

emergency contraception was sent to Washington state pharmacists, including a list of willing

physician and nurse practitioner prescribers and a template collaborative agreement.61 In Order to

fie a collaborative agreement with the Board of Pharmacy, each pharmacist must first participate

in a training session. These sessions included training in not only patient care and appropriate

provision of the medication, but also providing referral information, talking with parents if

necessary, and counseling on future contraceptive decisions.

To be effective, emergency contraception must be taken within 72 hours of sexual activity,

and even then, is most effective if taken within the first 24 hours. 62 If taken within 72 hours,

emergency contraception can reduce the chance of pregnancy by 89 percent. 63 Prior to

dispensing emergency contraception, the pharmacist performs a brief consultation with the

patient to rule out potential existing pregnancy.64 If HOCOSsary, the patient is referred to a primary

care physician or other health care professional.





59 The agreements were initially made between pharmacy and physician, rather than between
pharmacist and physician. This recently changed and now the agreements are between
pharmacist and physician.

60 Gardner et al (2001).

61 Downing (2004).

62 CBS News. November 24, 2003.

63 CBS News, November 24, 2003.

64 Pharmacists were reimbursed for consultation time, approximately $13.50 per counseling
se ssi on. htt ://www. no~ec. orn/Proil eWashinnton. htm.









Pharmacies are convenient they are open evenings, weekends, and holidays. No

appointment is required and a patient does not have to see her primary physician. This means no

delay due to scheduling an appointment or fear of discussing such matters with your primary

physician. Washington State law does not prohibit the provision of contraceptive or family

planning services to minors. No parental consent is required. The program, therefore, improved

emergency contraception access to women of all ages. The patient cost of emergency

contraception is between $30 and $40.

Additionally, the pilot program involved a mass consumer awareness campaign using

extensive media coverage. Public service announcements, mainly in the form of TV and radio

advertisements, occurred between July 1997 and March 1998. Additional paid TV, radio, and

newspaper advertisements were publicized between July and August of 1998.65 Both the

existence of emergency contraception and the recent accessibility changes were heavily

publicized in these advertisements. While the campaign targeted females aged 18-34,

participants believed that they were reaching younger females as well. News of Washington' s

program was also recognized by local and national print and TV news stories; some 120 stories

appeared.66 This campaign promoted the use of a new national hotline that allows women to call

and locate their nearest provider of emergency contraception. 1-888-NOT-2-LATE provides

information regarding both pharmacies and clinics where emergency contraception is available.67






65 Trussell (2001).

66 Gardner (2001).

67 A website maintained by Princeton was also established containing the same information:
www.Not-2-Late. com.









Data


Data on Chlamydia rates and abortion rates were obtained from the State of Washington.

These data are described in this section and summary statistics are provided in Table 3-1.

Chlamydia

The State of Washington collects detailed data on sexually transmitted diseases by date of

diagnosis. As such, the reports capture new incidents of the particular disease. These statistics

are reported at the county level by age group and gender.68 Among the most reliable statistics are

disease rates for Chlamydia.69 These data are available for the years 1992 through 2005. Using

occurrences by date of diagnosis, rates are calculated per 100,000 of the relevant population.

In the United States, Chlamydia is the most commonly reported STD. The disease does not

always present with symptoms, but if symptoms arise, they are typically discovered within three

weeks.'0 Women experience a greater risk of contracting Chlamydia (and other STDs) and are

more likely to have symptoms, as well as serious complications, simply because of their physical

design." Because most women have yearly physical or gynecological visits, however, the

disease is also more likely to be diagnosed in women.72 The disease is easily diagnosed, treated,

and cured with antibiotics, but can lead to serious health problems if not treated promptly.




68 Disease & Reproductive Health Assessment Unit, Community & Family Health Division,
Washington State Department of Health. These data were graciously made available by Mark
Stenger at the Washington Department of Health.

69 Data are also collected for Gonorrhea, Herpes, and Syphilis. Gonorrhea incidence is less
common in Washington than Chlamydia. Herpes statistics are largely underreported and Syphilis
is a rare disease in the State of Washington (per Mark Stenger).

7o WebMD, http://www.webmd. com/hw/std/aa293 03.asp.

71 Reproductive Health Technologies Proj ect, http://www.rhtp. org/std/types.asp.

72 Reproductive Health Technologies Proj ect, http://www.rhtp. org/std/types.asp.









The CDC reports that in 2004 over 900,000 incidences were reported in the United

States.73 Figure 3-1 shows Chlamydia rates over time for the United States from 1992 through

2003.74 In the US, Chlamydia rates have been on the rise since the beginning of the data period

in 1992, reaching a high rate of 300 in 2003. While Washington State has experienced increases

as well, the pattern for Chlamydia is not the same as the national pattern. Figure 3-2 shows the

rate of Chlamydia diagnosis in the State of Washington between 1992 and 2005 for all diagnoses

and female diagnoses. Chlamydia rates were relatively stable between 1995 and 1997. In the

years following 1997, Chlamydia rates rose for both groups and have reached all time high levels

relative to the past 14 years. Between 1998 and 2005, overall Chlamydia rates increased by

approximately 47 percent, while female Chlamydia rates increased by approximately 39 percent.

Because of the predominance of the disease in women, overall and female Chlamydia rates are

studied. Age-specific rates are available for females aged 15-19 and 20-24.7

Abortion Data

Washington gathers and reports detailed statistics on induced abortions by year, by county,

and by age group.76 One of the main goals of the pilot program was to reduce the number of

unintended pregnancies in the Washington area. Unintended pregnancies are difficult to measure,

73 Chlamydia CDC Fact Sheet, Centers for Disease Control and Prevention,

http://www.cdc. gov/std/Chlamvdia/STDFact-Chlamvdia. htm.

74 Centers for Disease and Control, http://wonder. cdc.gov/std.html.

75Race and ethnicity information is also collected, but is often missing. STD counts by race may
be incomplete and I have therefore not utilized the data by race.

76 Data are available through the Washington Department of Health, Center for Health Statistics,
http://www.doh.wa. nov/ehsphl/chs/chs-data/ab orti on/vi ewdown.htm. The Center for Health
Statistics does not calculate rates when the number of cases is less than or equal to five. To avoid
large jumps in rates, I have utilized the actual number of abortions by county and calculated rates
for all values of occurrences. Caution should be taken, however, in interpreting rates associated
with a small number of occurrences.









but the effects of the program can be captured by abortion rates. Figure 3-3 shows the overall

abortion rate for females (aged 15-44) in Washington State. Between 1992 and 2004, abortion

rates in Washington decreased by approximately 20 percent. Between 1998 and 2004, overall

abortion rates decreased by approximately 5 percent. Figure 3-4 displays the changes in abortion

rates for the US between 1992 and 2003 for comparison purposes. In the United States, the

abortion rate has fallen from 1992 until 1998, and then remained fairly stable from 1998 to 2003.

Of particular concern are abortion rates for young women, mainly women aged 15-19 and

20-24. Females aged 15-19 are of particular interest because most potential pregnancies in this

age group are unintended and most of these young women are unmarried. At least some of the

women in the 20-24 age band will be unmarried and have unplanned pregnancies. Figure 3-5

illustrates the trend in abortion rates for Washington women aged 15-19 and 20-24. These two

age bands experience the highest abortion rates of all age groups. Similar to the overall rate,

abortion rates for both age bands are somewhat static between 1995 and 1997. Abortion rates for

women aged 15-19 decreased by approximately 19 percent between 1998 and 2004. For women

aged 20-24, abortion rates decreased by 9 percent between 1998 and 2004.

Program Participation

Information on the filing of collaborative agreements was provided by the Board of

Pharmacy, Washington Department of Health. 7 The Board of Pharmacy approves all

collaborative agreement filings and therefore was able to provide a list of pharmacies by location




77I also received similar, but less complete, information from the Office of Population Research
at Princeton University, the organization which manages the Not-Too-Late website and hotline.
They maintain a current list of participating pharmacies in states with pharmacy access
legislation. Their database is designed to provide women seeking emergency contraception with
current provider locations. Although the database was not designed to keep historical
participation records, I have utilized this information for some purposes.









and date of filing. 78 I subsequently used this information to determine when certain areas gained

eligibility to dispense emergency contraception without a prescription. While participation in the

program and the formation of collaborative agreements are at the pharmacist level, I aggregate

access to the county-level. If a pharmacist had an agreement on file in year t in county i, I

designate that county as having pharmacy access for that year and the remaining years in the

dataset. 79 In later specifications, I substitute this definition of treatment with the percent of total

pharmacies with pharmacy access in county i in year t.

Initially, the pilot was intended to focus on counties in the Puget Sound area, mainly King,

Pierce, and Snohomish counties. These counties were chosen because they are located in the

Seattle area and monitoring would be more feasible. Since the law allows any pharmacist across

the state to form a collaborative agreement, when news of the pilot spread, pharmacists in other

areas of the state began to participate. The majority of the pilot program occurred between

February 1998 and June 1999. During this time, 11,976 prescriptions for emergency

contraception were dispensed by pharmacists. soPharmacists in 18 counties were involved during






78In almost all cases, I relied on the dates of collaborative agreement filing provided by the
Department of Health. There were a few circumstances, however, where there was a discrepancy
in dates and I relied on dates compiled by Princeton. These circumstances involved Washington
counties that had little participation over the time period. The Princeton information showed the
same pharmacy as the Washington Department of Health information, but with a much earlier
date of initial participation. In these instances, I adjusted the definition of treatment to reflect the
Princeton information.

79 Some specific pharmacies may have lost approval to dispense emergency contraception, but it
does not appear from the data that any county lost access to emergency contraception. In other
words, there may have been a change in the number of pharmacies dispensing emergency
contraception in each county over time.

so Gardner et al (2001).










the pilot program.8 After the official pilot program activities concluded, additional pharmacies

across the state continued to file collaborative agreements and access to emergency contraception

continued to spread. As of 2006, 294 pharmacies in 3 1 (of 39) counties are eligible to provide

emergency contraception without a prescription.82

Figure 3-6 displays a map of Washington State, shading the counties which had pharmacy

access in 1998, the first full year of the program. In Figure 3-7, the same map is displayed for a

2002, and Figure 3-8 shows pharmacy access for 2005. As shown, pharmacy access has grown

over time between 1998 and 2005. Today, almost all counties in Washington State have some

pharmacies which provide nonprescription access to emergency contraception.

Identification

In this section, I compare the participating and nonparticipating counties before the

program began. A county is defined to be participating or treated if any pharmacy access to

emergency contraception is available in that county. If no pharmacy access is available in a

county, then it is considered a nonparticipating or control area. The program was officially

initiated in 1997, but most of the program activities began in 1998. The pretreatment years, or

years before any pharmacy access was available in Washington, are defined as 1995-1997.

Baseline statistics for these years are presented in Table 3-2.

Chlamydia

To properly identify the effect of pharmacy access on Chlamydia rates, we require the

treatment and control groups to be similar but for the treatment. More specifically, the groups


slThese counties include Benton, Clallam, Clark, Cowlitz, Island, King, Kitsap, Pierce, Skagit,
Skamania, Snohomish, Spokane, Thurston, Wahkiakum, Walla Walla, Whatcom, Whitman, and
Yakima.

82 A national website, www.not-2-late.com, provides a current listing of EC providers in
Washington State.









must be on the same traj ectory prior to the program's implementation. With difference-in-

difference estimation, we do not require the groups to be at the same level necessarily but we do

require the groups to exhibit similar trends. County fixed effects, which are employed in what

follows, control for any time-invariant changes in unobservable characteristics. But Chlamydia

is a communicable disease, and therefore, the level at time t may be determined in part by the

level at time t-1.83 In Other words, the greater the number of individuals infected with the

disease, the more quickly it can spread and cause new infections.

In my paper, however, I use county-level observations and illustrate that pre-treatment,

areas with and without pharmacy access are not only on the same traj ectory, but are statistically

indistinguishable in terms of their levels. Consider Figure 3-9, which plots the overall Chlamydia

rate for the treatment and control groups between 1995 and 2005. As shown, both groups follow

the same traj ectory between 1995 and 1997, while the treatment group is at a slightly higher

level. After the start of the pilot program, indicated by the dotted vertical line at 1998, the two

groups diverge in terms of their overall Chlamydia rates. Similarly, Figure 3-10 illustrates that

female Chlamydia rates exhibit a similar pattern to overall Chlamydia rates.

At first glance, it may appear troublesome that Chlamydia rates are higher in treatment

counties than in control counties. After conducting a difference in means t-test, however, I fail to

rej ect the null hypothesis that the difference in the two groups is zero and conclude that the two


83 Some of the previous empirical literature has indicated the importance of including a lagged
dependent variable as a covariate. Panel OLS estimates with a lagged dependent variable are
inconsistent in the presence of fixed effects. This occurs because the lagged dependent variable
is correlated with the state fixed effects. Alternative methods have been developed to allow
estimation. One option is to take first differences and estimate a 2SLS model using lagged levels
or lagged differences as instruments (1',t- Of Ez,t,-2 Y,t-3). Such instruments are typically highly
correlated with the first lagged difference, but uncorrelated with the transformed error. Arellano
and Bond (1991) and more recently Blundell and Bond (1998) developed a G1VM style approach
to exploit a similar FD2SLS idea, where lagged levels and/or lagged differences serve as
instrumental variables.










groups are statistically indistinguishable at the five percent level. The means test was conducted

for 1995, 1996, and 1997, and these results are presented in Table 3-3. For females in 1997, we

would rej ect the null at the 10 percent level. It is possible, however, that some effects of the

program began occurring as early as 1997. The actual program was initiated in 1997, and

therefore, any effects of the initial activities, prior to start of the official program, could be

observed here. But for the treatment, we conclude that the counties are alike. In 1998, the first

year of the pilot program, Figures 3-9 and 3-10 show the rates begin to slightly diverge between

the treatment and control group. Without expanded access to emergency contraception, and

given no other shocks, we would expect the groups to continue to look and trend similarly.

Given that our treatment and control groups are similar prior to 1998, we assume that

without treatment, the groups would continue to be on the same traj ectory. Other studies which

use the lagged STD rate as a right-hand side regressor may not be able to exploit such an

environment. Many other studies which estimate STD rates utilize state or regional level data,

which may not satisfy these conditions. Since both groups experience the same trend in the years

before the pilot program, and their levels are not statistically different, we do not need to account

for a one-period lag in the Chlamydia rate.

Abortions

The initial treatment and control groups also look similar in terms of their abortion rates.

Figure 3-11 displays the overall abortion rate for the years 1995-2004 by treatment status.

Although the initially treated counties exhibit a slightly higher level, both groups trend similarly

during the pretreatment years. The two groups trend somewhat similarly before 1998, with the

control group experiencing somewhat larger declines in abortion rates. Figures 3-12 and 3-13

illustrate the abortion rate for age 15-19 and 20-24 by treatment status for the years 1995 through









2004.84 Abortion rates for ages 15-19 trend similarly in the treatment and control group. Both

groups experience slight declines during the pretreatment years, with the control group

experiencing a slightly more dramatic decline between 1997 and 1998. For 20-24 abortion rates,

both groups experience slight increases in abortion rates during the pretreatment years, with the

control group experiencing a slightly more dramatic increase between 1996 and 1997.

Table 3 -3 shows the results of the difference in means tests with respect to abortion rates.

For these measures, we conclude that abortion rates in the treatment group are statistically

different from the control group. The areas with pharmacy access exhibit slightly higher levels of

abortion rates. To the extent that this is a time-invariant characteristic, the county fixed effects

used in the analysis deal with the difference in levels. If the true effect of pharmacy access is to

reduce abortions, however, then higher abortion rates in the treatment group would lead

coefficient estimates to be upward biased. Such a bias could lead to a finding of no effect. If an

effect is identified, however, then it is a conservative estimate.

Pharmacy Participation

The decision to form a collaborative agreement and ultimately dispense emergency

contraception is made by the individual pharmacist or pharmacy. Pharmacy participation is based

on a variety of factors. Possible factors include the demand for emergency contraception in the

area, the attitudes and beliefs of the pharmacist or pharmacy management, or a desire to change

the pharmacist-patient relationship. If a given pharmacist forms a collaborative agreement

because of high demand for emergency contraception in the area, which could be correlated with

a high degree of sexual activity in the area, then the coefficient estimates on pharmacy access


84 For ages 15-19 and 20-24, there are two control counties which have virtually zero abortions
in these two age bands. I have dropped these two counties from the control group.









with respect to Chlamydia rates could be biased upwards. Figures 3-9 and 3-10 illustrated the

similarities in the trends of the treatment and control groups before the pilot program began. Not

only did the two groups trend similarly, but Table 3-3 indicated that pretreatment the two groups

are statistically indistinguishable. It does not appear that pharmacies in treatment counties are

different from the control group. Moreover, we should not expect the coefficient estimate on

pharmacy access to be biased upwards.

As discussed above, pharmacy participation could be related to the overall level of sexual

activity or risky behavior in the pharmacy's area. This could be correlated with the level of teen

pregnancy or the level of abortions in the area. Pharmacy access to emergency contraception

may lead to fewer abortions and/or fewer teen pregnancies because some pregnancies may be

prevented and some abortions may not be necessary. If pharmacies that formed collaborative

agreements did so because of these factors, then it is possible that the coefficient estimate on

abortion rates or teen pregnancy rates could be biased upward. If the true effect of treatment is

negative, however, this would upward bias my results in terms of finding no effect or a positive

effect. If I find a negative effect, then the coefficient estimates would be a conservative estimate.

Given that pharmacies choose to file a collaborative agreement at different times

throughout the data period, we must also consider the timing of participation. Because not all

areas of Washington gained pharmacy access to emergency contraception at the same time, the

timing of participation could affect the coefficient estimates. Many counties experienced

pharmacy participation between 1998 and 1999, during the pilot program. Any county with a

participating pharmacy during this time is considered an "early" participant. Any county which

did not have a pharmacy participate until 2000 or after is considered a "late" participant.










To properly identify the effect of pharmacy access, we must ensure that the early

participants look similar to the late participants. Difference in means tests were conducted for

early and late participants and are contained in Table 3-4. These tests confirm that the overall

and female Chlamydia rates between the early and late participants are not statistically

distinguishable. The same conclusion is reached for abortion rates for women aged 15-19. Early

and late participants are not statistically different. When considering the overall abortion rate,

however, the early and late participants are statistically different in 1995 and 1996, but are

statistically indistinguishable in 1997.

Other Characteristics

Difference in means tests were also conducted for other county-level characteristics such

as the county-level unemployment rate, per capital income (real), and divorce rate. We would

expect the counties which had pharmacy access to look similar to counties without pharmacy

access. The unemployment rate and per capital income may suggest something about the

economic conditions of the county, while the divorce rate may suggest something about the

family environment for young people in the area. Table 3-5 reports differences in means tests for

1995, 1996, and 1997 for the three county-level measures. In each and every case, we fail to

rej ect the null hypothesis that there is no difference in these measures between the treatment and

control counties at the five percent level.

Empirical Methodology

My study exploits county-level variation in both Chlamydia and abortion rates to examine

the intended and unintended effects of pharmacy access to and awareness of emergency

contraception. The equations below will be estimated using a fixed effects model:

Chlllllainali = og + P,PharmacyAccessl, + : Et (3-1)









Abortion,, = o, + P,PharmacyAccess,, + S at+, (3 -2)

where Chlumnlia~tl indicates the Chlamydia rate in county i in year t. The rate is defined as the

number of occurrences divided by the relevant population, multiplied by 100,000. Abortion,, is

defined as the number of abortions divided by the relevant population, multiplied by 1,000.

PharmacyAccessl, is a dummy variable for county-level pharmacy access to emergency

contraception. In the initial specifications, a county is defined as having pharmacy access in year

t if at least one pharmacy has a collaborative agreement on file with the Board of Pharmacy. In

later specifications, pharmacy access is defined as the percentage of total county pharmacies with

pharmacy access. Both equations also contain county and year fixed effects. The fixed effects

will capture any time-invariant county characteristics which could bias the estimated effects of

pharmacy access. Equations (3-1) and (3-2) are estimated without other county-level

characteristics. Any covariate must be identified from within county variation over fourteen

years."' Available county-level measures, however, do not vary considerably over time.. For

comparison purposes, however, the results with several covariates are presented in Section VIII.

Unless otherwise specified, data are available for 39 counties in Washington State for 14 years,

1992 through 2005, yielding a total of 546 observations when estimating Equation (3-1). For

estimation of equation (3-2), data are available from 1992 to 2004, yielding 507 observations.









ssLevine (2001), who explains the amount of sexual behavior using various costs of engaging in
sexual behavior, uses labor market conditions, generosity of the welfare system, and abortion
restrictions as independent variables. While these measures vary at the state-level, they do not
vary substantially at the county-level.












Chlamydia Rates

Table 3-6 contains the coefficient estimates for Overall, Female, Female Age 15-19, and

Female Age 20-24 Chlamydia rates.8s6 The coefficient of pharmacy access on total Chlamydia

rates is statistically significant and positive. Counties with pharmacy access experienced an

increase in the total Chlamydia rate, with a coeffieient of 24. Relative to a baseline average of

pre-treatment years (three-year average of 1995-1997), pharmacy access increases the

Chlamydia rate by approximately 18 percent. s7 For females, pharmacy access is also associated

with an increase of 18 percent, relative to the three-year pre-treatment average. Equation (3-1)

was also estimated for males but is not reported here. Pharmacy access does not have a

statistically significant effect on Chlamydia rates for men.

Columns (3) and (4) of Table 3-6 contain regression results by female age group.

Statistically significant results are obtained for those females aged 20-24. Pharmacy access is

associated with a 331 unit (or a 28 percent) increase in the 20-24 Female Chlamydia rate. The

coefficient estimate for PharmacyAccess for females aged 15-19 is not statistically significant.

The results using several covariates are presented in Table 3-8 for comparison purposes.

The additional independent variables employed are county-level per capital income and the

county unemployment rate. In almost all circumstances, the covariates included are statistically

insignificant. In all cases, inclusion of the covariates does not sufficiently change the statistical




86 To determine pharmacy access, I use the Washington Department of Health information
primarily, but in some situation I supplement the dates with information from the Office of
Population Research at Princeton University. The results are fairly consistent with the results
presented in this section if I utilize Washington Department of Health data exclusively.

87Three-year pretreatment averages are contained in Table 3-7.


Results










significance of the treatment effect, although the magnitude of the treatment effect is slightly

different.

Abortion Rates

Table 3-9 reports the results obtained from estimating Equation (3-2) for all women (15-

44), women aged 15-19, and women aged 20-24. Abortion rates also appear to be affected by

pharmacy access to emergency contraception. If women use emergency contraception as a

substitute for abortion, then the number of abortions may decrease. Treatment is associated with

a one unit decrease in the overall abortion rate. Relative to a three-year pre-treatment average,

this decrease corresponds to a 6 percent decrease in abortions. For teens aged 15-19, treatment is

associated with over a two unit (or an 11 percent) decrease in abortion rates. Pharmacy access is

also statistically significant with respect to abortion rates for women aged 20-24. Again relative

to the three-year pre-treatment average, abortion rates for women 20-24 were reduced by 15

percent.

Although the results are not reported here, I also conducted the analysis for women aged

25-29, 30-34, 35-39, and 40-44. Pharmacy access was not statistically significant in the

regressions of any of these four age bands. Pharmacy access to emergency contraception appears

to mainly impact the abortion rate for younger women, particularly those aged 15-24.

Lag in Treatment

The results presented in the previous section use the actual dates of participation based on

the initial collaborative agreement filing when considering the timing of treatment. These results

are fundamentally unchanged if we lag the treatment time by 6 months or by 1 year. The effect

of pharmacy access to emergency contraception is robust to these two alternative treatment

definitions.









Alternative Treatment Definitions

In the previous section, counties were considered treated if any pharmacies in county i had

pharmacy access in year t. In this section, treatment is defined as the number of pharmacies with

pharmacy access divided by the total number of pharmacies in that county in that year. In other

words, treatment is the fraction of county pharmacies with pharmacy access.

I count pharmacies using Washington Department of Health collaborative agreement

information filed with the Board of Pharmacy. I have tried to eliminate some duplicative records

which appear in this information in order to count new collaborative agreements. After counting

the number of collaborative agreements, I divide the number of pharmacies with access by the

total number of pharmacies in that county in that year. ssThe results of this estimation are

contained in what follows.89

Chlamydia Rates

Table 3-10 reproduces the results of Equation (3-1) using this alternative definition of

treatment. The results in Table 3-10 are similar to those in Table 3-7. Pharmacy access is

associated with an increase in both overall and female Chlamydia rates. In this specification,

however, pharmacy access is associated with an increase in the female Chlamydia rates for





ssThe total number of pharmacies by county by year was obtained from County Business
Patterns, U.S. Census Bureau, http://www.census. gov/epcd/cbp/view/cbpyiew.html, relevant
years. These data are only available from 1993 through 2002, so I used the counts for 2002 as
counts for the years 2003, 2004, and 2005. Because pharmacy totals are not available for 1992, I
am unable to use this year of data in what follows.

89 I alternatively use all records provided to me by the Department of Health by county by year.
In this counting mechanism, I do not try to eliminate any potential duplications, but rather use all
the records provided. The results using these counts of pharmacies are consistent with my
corrected counts.










women age 15-19 as well as for women age 20-24. For the female 20-24 Chlamydia rate, a one

percent increase in pharmacy access is associated with a 4.5 percent increase in the disease rate.

Abortion Rates

Table 3-11 shows the results for county abortion rates when estimating Equation (3-2).

Using the percent of county pharmacies with pharmacy access yields much weaker results in this

model. In Table 3-9, pharmacy access was associated with decreases in overall abortion rates,

female abortion rates for women aged 15-19, and female abortion rates for women aged 20-24.

Using this alternative treatment definition, however, pharmacy access is only associated with a

decrease in abortion rates for women aged 15-19.

Other Considerations

My empirical strategy relies on variation in pharmacy access by county as well as outcome

variables that are measured at the county-level. Although to my knowledge these are the best

data available at this time, there are some drawbacks of using county-level data to identify this

treatment effect. First, I define treatment at the county-level first as a binary indicator and then as

the percentage of pharmacies in a county with pharmacy access. Restricting treatment to the

county-level could cause problems if some areas of certain counties are in fact "more" treated

than others. First, some counties in Washington State are very large while some are much

smaller. Other counties in Washington are more densely populated while other counties are more

rural. Furthermore, the population in some counties is concentrated in specific areas of a larger

geographic region. It is possible, therefore, that I could be misclassifying treated and nontreated

counties. In other words, if a county has some pharmacy access but this access is all concentrated

around a border with a nontreated county, then it is possible that the nontreated county could be

just as affected or more affected by pharmacy access. To the extent that any misclassifieation










means that I classify areas without pharmacy access nontreated when in fact they are treated, this

would bias my estimates in favor of Einding no effect.

Falsification Tests

To test that the identification of the treatment effect is not capturing a general trend in

increased disease or in overall risky behavior, a falsifieation exercise is performed and reported

in Table 3-12 and 3-13.

I use Washington State Cancer Registry data on county cancer rates.90 Washington cancer

data are available by county in three-year averages beginning with 1992-1994 and ending with

2002-2004. In order to utilize this data, I use the midpoint of the three-year ranges as

observations for that year. In this way, I am able to use county-level cancer rates for 1993

through 2003. There are some observations which are not reported for some counties in some

years. These missing observations account for number of observations used in each regression.

If the identified effects of pharmacy access on sexually transmitted diseases are capturing

an upward trend in general disease rates in Washington State, then we should Eind a positive

coefficient on pharmacy access with respect to cancer rates. Table 3-12, where each column is a

separate regression, shows the results when regressing pharmacy access, along with county and

year fixed effects, on several cancer rates including total cancer rates, female cancer rates, total

lung cancer rates, female lung cancer rates, and female breast cancer rates. In all cases, I Eind no

evidence that pharmacy access is associated with an increase in cancer rates.

Additionally, I test if the effect of pharmacy access is capturing a general upward trend in

risky behavior. I use measures of risky behavior including alcohol or substance use as well as




90 Washington State Cancer Registry, http://www3.doh.wa. Rov/WSCR/default.htm, relevant
years .









various criminal behaviors.91 To ensure that the participation in emergency contraception by

pharmacies is unrelated to other measures of risky behavior, I regress PharmacyAccess on the

rates contained in Table 3-13. Each column is a separate regression. Alcohol/Drug Related Death

Rate is calculated as the number of alcohol/drug related deaths per 100 total deaths. The

remaining rates are calculated as the number of arrests of the particular crime divided by 1,000

of the respective population. For example, alcohol-related arrests (18+) is defined as the total

number of alcohol related arrests for individuals aged 18 and over divided by 1,000 of the 18 and

over population.

Pharmacy access has no effect on any other measure of risky behavior. Pharmacy access

is not statistically significant in any of the regressions presented in columns (1) through (9).

Pharmacy access to emergency contraception does not appear to have an effect on these

alternative measures of risky behavior.

Additional Control Group: Oregon

Chlamydia

This section utilizes an additional source of data to increase the size of the control group.

This section is used as a supplement to original methodology because the available Washington

data are richer than the available Oregon data. We can, therefore, compare some of the results in

this section with Section VIII, but due to data availability, we cannot compare all measures.

Oregon, which does not have pharmacy access to emergency contraception, looks similar to

Washington in the pre-treatment years and is therefore an appropriate comparison group. As


91 2005 Risk and Protection Profile for Substance Abuse Prevention, Research and Analysis
Division, Washington State Department of Social and Health Services,
http://wwwl.dshs.wa.gov/rda/research/4/47/pae/eal~hm Most measures are available
for 1993 through 2004, except Alcohol and Drug Related Deaths which is available for 1992
through 2003. Some counties did not report certain measures for certain years due to small
sample sizes or missing information. I have coded these observations as missing observations.









illustrated in Figure 3-14, Washington and Oregon exhibit similar trends between 1994 and

1998; the rates are almost identical. After the start of the pilot program and subsequent pharmacy

access, rates for both states increase, but Washington experienced greater increases in Chlamydia

rates. Figure 3-14 confirms that Oregon is suitable as a comparison group in terms of Chlamydia

rates. Additionally, Figure 3-15 presents overall Chlamydia rates for the treatment and control

groups. In this figure, untreated areas of Washington are combined with Oregon counties (also

untreated) to comprise a larger control group. As shown, both groups trend similarly during the

pre-program period. Differences in means tests, shown in Table 3-14, confirm that the treatment

and control groups are statistically indistinguishable. Equation (3-1) is reestimated using the

additional Oregon county-level data. Oregon, however, only publishes overall Chlamydia rates;

county-level rates are not available by gender or by age.92 Chlamydia rates for Oregon are

available from 1994 through 2005. As a result, Equation (3-1) is now estimated for 1994-2005.

Summary statistics for these data, and the abortion data, are contained in Table 3-15. The results

from the estimation are contained in Table 3-16.

The coefficient estimate on PharmacyAccess when including the Oregon data is larger and

more precise than the coefficient presented in Section VIII. Without including the Oregon data,

the treatment effect for overall Chlamydia rates was 28.9. Upon using Oregon county data, the

treatment effect is 38.8. Relative to the three-year pretreatment average, the latter coefficient

represents a 29 percent increase in overall Chlamydia rates. Three-year pretreatment averages are

contained in Table 3-17.

Using the combined Washington and Oregon data, I also re-estimate the model using the

percent of pharmacies with pharmacy access as the treatment. Table 3-18 contains the results of


92 Oregon Department of Human Services, http ://oregon.gov/DHS/ph/std/annrep .shtml.










this estimation. Again, increased pharmacy access is associated with an increase in the overall

Chlamydia rate.

Abortion

A comparable alternative approach can also be conducted for abortion rates. In order to

use Oregon counties as additional control counties, we must confirm that Oregon and

Washington look and trend similarly before introduction of pharmacy access in Washington.

Figures 3-16, 3-17, and 3-18 present graphical evidence that support this requirement. As shown,

Washington and Oregon trend similarly between 1995 and 1997 in terms of the overall abortion

rate, 15-19 abortion rate, and 20-24 abortion rate.

We can further compare the counties which were treated in Washington with the

untreated counties from both Washington and Oregon. Figures 3-19, 3-20, and 3-21 illustrate

these trends graphically. Overall abortion rates declined somewhat for both treatment and control

groups during the time period. Abortion rates for age 15-19 show sharper declines after the

introduction of pharmacy access, while abortion rates for age 20-24 show small declines.

The results of the reestimation of Equation (3-2) are presented in Table 3-19. Using this

alternative approach, we are unable to identify an effect of pharmacy access on the overall

abortion rate for women aged 15-44 or for teens age 15-19. We are, however, able to identify a

negative effect of pharmacy access on abortions by females age 20-24. The coefficient on

pharmacy access accounts for approximately 11 percent of the decrease in abortion rates for

females aged 20-24.

This model was reestimated using the percent of pharmacies with pharmacy access as the

treatment in place of the binary treatment indicator. The results of this estimation are contained

in Table 3-20. In this model, the results for overall abortion rates are much weaker. Using this










definition of treatment, I am unable to identify an effect of pharmacy access on overall abortion

rates, abortion rates for age 15-19, or abortion rates for age 20-24.

Conclusions

The FDA recently approved a proposal to allow emergency contraception to be available

nationwide without a prescription for women over the age of 18. The State of Washington,

however, was the first state to implement a program to increase access to emergency

contraception through pharmacies. In my paper, I employ county-level data from Washington to

consider the impact of such a program. Using a difference-in-difference methodology, and taking

care to ensure that the treatment and control groups are similar pre-treatment, I find evidence of

effects with respect to both STD rates and abortion rates. The results suggest that increased

access is associated with a reduction in the abortion rate, particularly for young women. This

result is stronger when using the binary treatment definition than when using the percentage of

pharmacies with access. A tradeoff, perhaps, is that increased access is also associated with an

increase in the overall and female Chlamydia rates. In particular, the results for suggest increases

in the Chlamydia rate for females aged 20-24. When using the percentage of pharmacies with

access, the results suggest that increased pharmacy access is associated with not only increases in

the female 20-24 Chlamydia rate, but also the female age 15-19 Chlamydia rate.










Table 3-1. Summary statistics
Summary Statistics*
Variable Mean Median Min Max Std. Dev.
Chlamydia Rate 169.3 165.9 0 440.0 82.7
Female Chlamydia Rate 266.4 260.4 0 683.7 127.9
Female Chlamydia Rate, Age 15-19 1,603.1 1,646.7 0 3,605.8 750.9
Female Chlamydia Rate, Age 20-24 1,545.0 1,477.3 0 5,199.3 875.4
Abortion Rate 14.5 14.8 0 29.1 5.1
Abortion Rate, Age 15-19 19.4 19.4 0 42.9 8.4
Abortion Rate, Age 20-24 33.4 34.0 0 70.2 13.9
Unemployment Rate 7.47 7.2 1.6 17.6 2.5
Real income per capital $26,749 $25,470 $18,650 $53,583 $5,085.4
Pharmacy Access (binary) 0.37 0 0 1 0.48
Percent of Pharmacies with Access 12.3 0 0 100 23.2
* STD summary statistics and explanatory variables are calculated for the years 1992 through 2005. Summary
statistics for the abortion variables are calculated for the years 1992 through 2004.










Table 3-2. Baseline statistics
1995 1996 1997
Variable Treat Control Treat Control Treat Control
Chlamydia Rate 141.3 106.8 142.4 108.4 140.2 101.7
Female Chlamvdia Rate 228.7 189.8 231.5 169.8 224.3 164.2
Abortion Rate 15.5 10.3 15.7 9.1 15.7 8.6
Abortion Rate, Age 15-19 23.2 12.1 21.9 11.4 21.9 11.7
Abortion Rate, Age 20-24 34.1 18.7 34.8 18.2 34.8 25.1










Table 3-3. Difference in means t-tests between treatment and control
[Null Hypothesis: difference in means is zero]
Overall Chlamydia Rate
Year Mean Treatment Mean Control P-value
1995 141.3 106.8 0.1163
1996 142.4 108.4 0.1693
1997 140.2 101.7 0.0655
Female Chlamydia Rate
Year Mean Treatment Mean Control P-value
1995 228.7 189.8 0.2773
1996 231.5 169.8 0.1280
1997 224.3 164.2 0.0828
Abortion Rate 15-44
Year Mean Treatment Mean Control P-value
1995 15.5 10.3 0.0025
1996 15.7 9.1 0.0003
1997 15.7 8.6 0.0004
Abortion Rate 15-19
Year Mean Treatment Mean Control P-value
1995 23.2 12.1 0.0002
1996 21.9 11.4 0.0002
1997 21.9 11.7 0.0007
Abortion Rate 20-24
Year Mean Treatment Mean Control P-value
1995 34.1 18.7 0.0013
1996 34.8 18.2 0.0015
1997 34.8 25.1 0.0753










Table 3-4. Difference in means t-tests between early and late adopters
[Null Hypothesis: difference in means is
zero]
Overall Chlamydia Rate
Year Mean Early Mean Late P-value
1995 149.0 131.1 0.3423
1996 142.7 142.2 0.9802
1997 145.5 133.1 0.4874
Female Chlamydia Rate
Year Mean Early Mean Late P-value
1995 243.4 209.3 0.2713
1996 229.1 234.6 0.8714
1997 230.3 216.6 0.6583
Abortion Rate 15-44
Year Mean Early Mean Late P-value
1995 16.4 13.3 0.0457
1996 16.7 13.4 0.0546
1997 16.5 13.8 0.1621
Abortion Rate 15-19
Year Mean Early Mean Late P-value
1995 24.1 21.1 0.2452
1996 22.7 19.9 0.2511
1997 23.3 18.8 0.1144
Abortion Rate 20-24
Year Mean Early Mean Late P-value
1995 36.5 28.4 0.0720
1996 38.7 25.7 0.0079
1997 35.7 32.6 0.5684













Year Mean Treatment Mean Control P-value
1995 7.5 8.8 0.2018
1996 7.3 8.9 0.1409
1997 6.2 7.5 0.1380
Real Per Capita Income


Table 3-5: Difference in means t-tests for county characteristics
Unemployment Rate


Treatment Mean Control
42 $23,401
72 $26,453
26 $24,025
Divorce Rate


Year
1995
1996
1997

Year
1995
1996
1997


Mean
$25,6
$25,0
$26,8


P-value
0.1513
0.3985
0.1020

P-value
0.1894
0.4418
0.2049


Mean Treatment Mean Control
6.42 5.74


6.41
6.27


6.06
5.74










Table 3-6. Chlamydia rates overall, by gender, and by gender/age
(1) (2) (3) (4)
Variable Name All Female Females 15-19 Females 20-24
PharmacyAccess 23.88 38.06 147.64 330.60
[12.36]* [17.62]** [102.95] [155.85]**
R-squared 0.75 0.75 0.55 0.52
Number of Observations 546 546 546 546
County Fixed Effects X X X X
Year Fixed Effects X X X X
Clustered standards errors (at the county-level) in brackets.
Chlamydia Rate = (Number of Cases / Relevant Population) 100,000
* significant at 10%; ** significant at 5%; *** significant at 1%










Table 3-7. Three-year pretreatment average, Washington
Variable Average (1995-1997)
Chlamydia Rate 133.04
Female Chlamydia Rate 215.80
Female Chlamydia Rate 15-19 1,362.4
Female Chlamydia Rate 20-24 1,163.4
Abortion Rate 14.18
Abortion Rate, Age 15-19 19.90
Abortion Rate, Age 20-24 31.34










Table 3-8. Chlamvdia rates overall, by sender, and by sender/age with covariates


(1)
All
19.75
[10.89]*
0.0041
[0.0024]*
-1.41
[3.96]
0.75
546
X
X


(2)
Female
33.86
[16.30]**
0.0045
[0.0039]
-1.06
[5.41]
0.76
546
X
X


(3)
Females 15-19
92.12
[95.56]
0.0471
[0.0267]*
-22.11
[35.34]
0.55
546


(4)
Females 20-24
298.2
[153.33]*
0.0405
[0.0277]
5.08
[45.27]
0.52
546


Variable Name
PharmacyAccess

Per Capita Income

Unemployment Rate

R-squared
Number of Observations
County Fixed Effects
Year Fixed Effects


Clustered standards errors (at the county-level) in brackets.
Chlamydia Rate = (Number of Cases / Relevant Population) 100,000
* significant at 10%; ** significant at 5%; *** significant at 1%










Table 3-9. Abortion rates overall and by age
(1) (2) (3)
Variable Name Age 15-44 Age 15-19 Age 20-24
PharmacyAccess -0.9 -2.14 -5.25
[0.37]** [1.15]* [1.70]***
R-squared 0.85 0.72 0.66
Number of Observations 507 481 481
County Fixed Effects X X X
Year Fixed Effects X X X
Clustered standards errors (at the county-level) in brackets.
Abortion rate = (Number of Abortions / Relevant Population) 1,000
* significant at 10%; ** significant at 5%; *** significant at 1%










Table 3-10. Chlamydia rates overall, by gender, and by gender/age
(1) (2) (3) (4)
Variable Name All Female Females 15-19 Females 20-24
Percent of Total
Pharmacies Participating 0.496 0.651 3.311 4.485
[0.1 75]*** [0.263]** [1.785]* [2.075]**
Number of Observations 507 507 507 507
R-squared 0.77 0.77 0.56 0.55
County Fixed Effects X X X X
Year Fixed Effects X X X X
Clustered standards errors (at the county-level) in brackets.
Chlamydia Rate = (Number of Cases / Relevant Population) 100,000
* significant at 10%; ** significant at 5%; *** significant at 1%
By using the percent of total pharmacies participating, I am only able to utilize data from 1993 through 2005. The
data for total number of pharmacies for 1992 is incomplete, so I drop 1992 observations in these regressions.
Because of using this method, in five cases, the percent of participating pharmacies out of total county pharmacies
exceeds 100. In these five cases, I recode these percentages to 100 until updated data is available.










Table 3-11. Abortion rates overall and by age
(1) (2) (3)
Variable Name Age 15-44 Age 15-19 Age 20-24
Percent of Total
Pharmacies Participating -0.004547 -0.03404 0.002877
[0.005630] [0.019525]* [0.04481 9]
R-squared 490 490 490
Number of Observations 0.86 0.76 0.62
County Fixed Effects X X X
Year Fixed Effects X X X
Clustered standards errors (at the county-level) in brackets.
Abortion rate = (Number of Abortions / Relevant Population) 1,000
* significant at 10%; ** significant at 5%; *** significant at 1%
By using the percent of total pharmacies participating, I am only able to utilize data from 1993 through 2004. The
data for total number of pharmacies for 1992 is incomplete, so I drop 1992 observations in these regressions.
Because of using this method, in one case, the percent of participating pharmacies out of total county pharmacies
exceeds 100. In this case, I recode the percentage to 100 until updated data is available.











(4)
Female
Lung
Cancer
Rate
0.52
[2.658]
395
0.69
X
X


(5)

Female
Breast
Cancer Rate
-7.859
[8.858]
428
0.47
X
X


Table 3-12. Falsification tests using county cancer rates
(1) (2) (3)
Variable Name Total
Total Lung
Cancer Female Caner
Rate Cancer Rate Rate
PharmacyAccess 3.63 4.742 1.343
[9.610] [13.629] [2.999]
No. of Observations 429 429 424
R-squared 0.63 0.66 0.67
County Fixed Effects X X X
Year Fixed Effects X X X





Table 3-13. Falsification exercise
(1)
Variable Name Alcohol &
Drug
Related
Deaths
PharmacyAccess 0.10
[0.28]
R-squared 0.73
No. of Observations 410
County Fixed Effects X
Year Fixed Effects X


(2)
Alcohol
Related
Arrests (Age
18+)
0.84
[1.026]
0.74
453
X
X


(3)
Drug
Related
Arrests
(Age 18+)
-0.12
[0.35]
0.64
453
X
X


(4)
Violence
Related
Arrests
(Age 18+)
0.14
[0.22]
0.58
453
X
X
(9)
Drug
Related
Arrests
(Age 10-17)
0.32
[0.52]
0.67
456
X
X


(5)
Property
Crime
Arrests
(Age 18+)
-0.48
[0.36]
0.78
453
X
X


(6) (7) (8)
Variable Name Property Violence Alcohol
Crime Related Related
Arrests (Age Arrests (Age Arrests
10-17) 10-17) (Age 10-17)
Treatment -1.32 0.27 -1.722
[2.59] [0.47] [1.46]
R-squared 0.69 0.44 0.72
No. of Observations 456 456 456
State Fixed Effects X X X
Year Fixed Effects X X X
Clustered standards errors (at the county-level) in brackets.
Rates = (Number of Occurrences / Relevant Population) 1,000
* significant at 10%; ** significant at 5%; *** significant at 1%










Table 3-14. Difference in means t-test, Chlamydia rates
Overall Chlamydia Rates
[Null Hypothesis: difference in means is zero]
Year Mean Washington Mean Oregon P-value
1995 133.3 134.5 0.9402
1996 134.5 132.6 0.9091
1997 131.3 135.2 0.8090
Overall Chlamydia Rates
Mean Washington Mean Washington or
Year Treated Oregon Untreated P-value
1995 141.3 129.0 0.4455
1996 142.4 127.7 0.4090
1997 140.2 128.5 0.4801










Table 3-15. Summary statistics, Washington and Oregon
STD Summary Statistics, 1994 2005
Variable Mean Median Minimum Maximum
Chlamydia Rate 157.5 147.0 0 642.9
Abortion/Birth Summary Statistics, 1992 2004
Abortion Rate 12.7 12.9 0 30.6
Abortion Rate, Age 15-19 16.6 16.5 0 49.1
Abortion Rate, Age 20-24 28.0 27.6 0 83.5










Table 3-16. Chlamvdia rates including Oregon


(1)
Chlamydia Rate
38.79
[9.11]***
0.77
900


Variable Name
PharmacyAccess

R-squared
Number of Observations
County Fixed Effects
Year Fixed Effects


Clustered standards errors (at the county-level) in brackets.
Chlamydia Rate = (Number of Cases / Relevant Population) 100,000
* significant at 10%; ** significant at 5%; *** significant at 1%










Table 3-17. Three-year pre-treatment average, Washington and Oregon
Variable Average (1995-1997)
Chlamydia Rate 133.54
Abortion Rate 12.92
Abortion Rate, Age 15-19 17.77
Abortion Rate, Age 20-24 26.19










Table 3-18. Chlamydia rates including Oregon
(1)
Variable Name Chlamydia Rate
Percent of Total
Pharmacies Participating 0.81
[0.1 79]***
R-squared 900
Number of Observations 0.77
County Fixed Effects X
Year Fixed Effects X
Clustered standards errors (at the county-level) in brackets.
Chlamydia Rate = (Number of Cases / Relevant Population) 100,000
* significant at 10%; ** significant at 5%; *** significant at 1%

















R-squared 0.87 0.75
No. of Observations 900 900
County Fixed Effects X X
Year Fixed Effects X X
Clustered standards errors (at the county-level) in brackets.
Abortion Rate = (Number of Cases / Relevant Population) 1,000
* significant at 10%; ** significant at 5%; *** significant at 1%


:2)
Abortion Rate
15-19
0.52
0.81]


(3)
Abortion Rate
20-24
-2.76
[1.44]*
0.73
900


Table 3-19. Abortion rates including Oregon
(1) (
Variable Name Abortion Rate r
15-44
PharmacyAccess 0.20-
[0.37][










Table 3-20. Abortion rates including Oregon
(1)
Variable Name Abortion Rate
15-44


(2)
Abortion Rate
15-19


(3)
Abortion Rate
20-24


Percent of Total
Pharmacies Participating 0.007 -0.001
[0.005] [0.010]
R-squared 900 900
No. of Observations 0.87 0.75
County Fixed Effects X X
Year Fixed Effects X X
Clustered standards errors (at the county-level) in brackets.
Abortion Rate = (Number of Cases / Relevant Population) 1,000
* significant at 10%; ** significant at 5%; *** significant at 1%


0.034
[0.027]
900
0.73
X
X





50 -


0
1992 1993 1994 1995 1996 1997 1998 1999 2000 2001 2002 2003


Figure 3-1.Chlamydia rates in the United States, 1992 2003.
















O
CO
-

O

O
-0







Ob
CO


1992 1994 1996 1998 2000 2002 2004
Year








Figure 3-2. Overall and female chlamydia rates in Washington state





O







LO


o-L
1992


19194


19196


1998
year


20100


2002


2004


Figure 3-3. Overall abortion rate (age 15-44) in Washington state




















15



10



5



0
1992 1993 1994 1995 1996 1997 1998 1999 2000 2001 2002 2003


Figure 3-4. Abortion rates in the United States, 1992 2003.





































110





m


O


m


O
O
O

L
a,
n,
a~hl
m
L~m


O


m-


1992 1994 1996


1998
year


2000


2002


2004


I ~Abortion Rates 15-19 Abortion Rates 20-24


Figure 3-5. Abortion rates in Washington state, ages 15-19 and ages 20-24





O No Pharmacy Access
I Pharmacy Access


Figure 3-6. Washington state pharmacy access in 1998





O No Pharmacy Access
I Pharmacy Access


Figure 3-7. Washington state pharmacy access in 2002





Cl No Pharmacy Access
I Pharmacy Access


Figure 3-8. Washington state pharmacy access in 2005















O


00


OO
OO
co
-

-i
CO



CO
O0


1995 1996 1997 1998 1999 2000 2001 2002 2003 2004 2005
Year








Figure 3-9. Overall chlamydia rates by treatment and control group






















O
O
d

O




o
o

o
oo
o~n
r~
o
o

LO
a~r~
n
ao
-c~~n
m


o
o



o




o


1995 1996 1997 1998 1999 2000 2001 2002 2003 2004 2005

Year












Figure 3-10. Female chlamydia rates by treatment and control group


















In -~I ~ __






-z I


2003 2004


O
O
O
L
a,
n
m


1995 1996 1997 1998 1999 2000 2001 2002
year

Treatment Control



Figure 3-11. Overall abortion rates (age 15-44) by treatment status






































117













O











195 19 97 198 19 00 201 20 03 20

yea
Tram nt Coto


Figue 312.Abotionrats (ge 5-1) bytretmet satu























11





















oI


O I

O
O




OI


r-


yea
TrametCoto


Figure 3-13. Abortion rates (age 20-24) by treatment status













O



O
0-
Oi
O
co


OC
1994


19196


19198


20b00
Year


20102


20104


-*- Washngton ~Oregon


Figure 3-14. Overall chlamydia rates, Washington and Oregon














O

On
Oi
-


1994 1996 1998 2000
Year

STreatment -* Not Treate




Figure 3-15. Overall chlamydia rates by treatment status


2002


:d WA or OR


20104
















I ,




tccz~e~c_


In

o
o
o
LO
n
m


1994 1996 1998 20
Year
SWA TreatmentWA



Figure 3-16. Abortion rates, Washington and Oregon


;00


2002


2004


or OR Not Treated



















































I I I I I I


In
hi




o
hi



o
Oln
o

L
a,
n

Bo

rr



In-





o-


1993 1995 1997 1999
Year


2001


2003


SWashington ~ Oregon


Figure 3-17. Abortion rates 15-19, Washington and Oregon









































IWashington ~Oregon


O
d



O
(3
O
O
O
LO
a)hl
a,
iij
[LI
o


~Z ~e--c~t~--r,





2


1993


1995


1997 1999
Year


2001


2003


Figure 3-18. Abortion rates 20-24, Washington and Oregon











O





LO


I -



~-c~cc


1996


1998
Year


2000


2002


2004


SWA Treatment -4 WA or OR Not Treated


Figure 3-19. Abortion rates by treatment status
























SWA Treatment -* WA or OR Not Treated


O


On
ON
O
Oh


o
-


::::::::::::-::1:


1994


1996


19198
Year


2000


2002


2004


Figure 3-20. Abortion rates 15-19 by treatment status





























SWA Treatment -* WA or OR Not Treated


O






In
-


z



*--c-e


1994 1996


19198
Year


2000


2002


2004


Figure 3-21. Abortion rates 20-24 by treatment status









CHAPTER 4
THE IMPACT OF PHARMACY-SPECIFIC ANY-WILLING-PROVIDER LEGISLATION ON
PRESCRIPTION DRUG EXPENDITURES

Introduction

In recent years, many states have implemented Any-Willing-Provider (AWP) legislation.

This form of health care legislation requires a managed care organization (MCO) to accept any

provider who agrees to the MCO's reimbursement rates, terms, and conditions. A provider in this

context could be a physician, hospital, or pharmacy. Proponents argue that AWP laws increase

network size, expand patient choice, and increase competition among providers. Opponents

believe that AWP legislation prevents managed care organizations from selectively contracting

and obtaining discounts by offering providers a larger volume of patients. Additionally,

administrative costs could be affected simply due to the difficulties of dealing with a larger

number of pharmacies, physicians, or hospitals in the network. Such legislation, therefore, may

prevent MCOs from effectively reducing health care costs as much as they might otherwise.

A small literature exists on the effect of AWP laws on several categories of health care

expenditures including total health care expenditures, hospital expenditures, and physician

expenditures. Most studies, however, fail to recognize that the vast maj ority of the existing AWP

laws target pharmacies exclusively, as opposed to more comprehensive laws that apply to some

combination of physicians, hospitals, and pharmacies. If AWP legislation limits cost reductions

available through selective contracting, then states with such legislation may incur higher health

care expenditures. There are additional potential consequences of AWP legislation, which related

mainly to physicians and hospitals. For example, some opponents argue that AWP forces HMOs

to contract with physicians who might be "higher-cost" in that they provide relatively inferior

care or use excessive resources. If MCOs must now contract with physicians who might not

comply with the MCO's treatment philosophy, then health care costs could increase. Arguments









of this type obviously cannot apply to pharmacies since pharmacists do not have prescribing

authority .

Given that most AWP laws focus exclusively on pharmacies, it is relevant to consider the

impact of these specific types of AWP laws. For pharmacies specifically, AWP laws not only

increase patient choice but also allow independent pharmacies to compete with large chain

pharmacies. If AWP laws prevent the MCO from selectively contracting with specific

pharmacies or if AWP laws raise administrative costs in dealing with pharmacies for the MCO,

then it is possible that expenditures on prescription drugs could increase. The effect of pharmacy

AWPs is distinct from the effect of more comprehensive laws. My study is the first to analyze

the impact of pharmacy-specific AWP legislation on state-level prescription drug expenditures

per capital. I find that AWP legislation is associated with increases in pharmaceutical drug

expenditures per capital. This result is robust to several alternative specifications. Additionally, I

find evidence consistent with other studies in terms of the relationship between AWP and health

care expenditures as well as the relationship between HMO market share and health care

expenditures.

Managed Care and Any-Willing-Provider Legislation

Managed Care and Health Maintenance Organizations

In the early 1980s, managed care was a new concept on the health care front. Enrollments

in managed care increased dramatically during the 1980s, and continued to gain popularity

through the 1990s. Today, managed care is the predominant form of health care in the United

States. Managed care is a broad term that encompasses several types of health care plans such as

Health Maintenance Organizations (HMOs) and Preferred Provider Organizations (PPOs).

HMOs, the more restrictive type of plan, usually require that all services be authorized by an in-

network primary care physician, otherwise known as a gatekeeper. In contrast, PPOs offer









enrollees lower cost sharing when using services within some preferred provider list and higher

cost sharing when using services outside the preferred provider network. PPOs do not have

formal gatekeepers. These forms of managed care plans are in contrast to what was traditionally

known as an indemnity plan or a Fee-For-Service (FFS) plan. A FFS plan would permit its

enrollees to purchase medical services from any provider of their choice. The providers submit a

claim to the insurance company and all covered claims would be paid. A FFS plan has no

gatekeepers and no restrictions on medical services or on choice of provider, although FFS

subscribers are subj ect to policy limits.

The conventional belief is that managed care lowers health care spending through various

cost containment strategies. This decrease in spending is dependent mainly upon selective

contracting which allows MCOs to obtain volume discounts. By promising providers a certain

volume of patients, managed care organizations are able to negotiate volume discounts.

Additionally, because MCOs limit their provider networks, they reduce the number of providers

with whom they contract. This can reduce administrative expenses. In these ways, states with

higher HMO enrollments are believed to have lower health care spending.

But HMO presence does not necessarily reduce health care spending in all areas.

Managed care stresses the importance of well patient visits as well as preventive care. One goal

of managed care is to reduce hospital expenditures by substituting less expensive physician visits

and other preventive services for more costly hospital stays. Increased HMO presence is

associated with a shift in expenditures from hospitals to physicians. This substitution is also

found between hospitals and prescription drugs. In a 1998 study, Cutler and Sheiner report that

HMO enrollment is associated with a decrease in hospital spending growth, but increases

spending growth for physicians' services and prescription drug expenditures.










Any-Willing-Provider Legislation

In the 1980s and again in the 1990s, a new form of legislation appeared in the United

States. Many states passed any-willing-provider laws that require managed care organizations to

accept any provider into their network if the provider agrees to the conditions, terms, and

reimbursement rates. Managed care organizations have come under criticism for a variety of

reasons. One consequence of a managed care organization's cost reducing strategies is the

restriction in provider choice. Accordingly, proponents of AWP argue that such legislation will

increase the number of available providers in a network and thereby increase competition among

providers.

The main mechanism through which managed care organizations are able to constrain

costs is through limited provider networks, selective contracting, and volume discounting. As

such, in order for managed care organizations to be effective at cost containment, they must be

able to negotiate volume discounts by committing to a larger volume of patients to each provider.

AWP prevents a managed care organization from being able to offer providers a much larger

patient base and therefore diminishes its ability to selectively contract. Additionally, if managed

care organizations are required to accept any provider who agrees to its terms into its network,

then it will have less control over the quality of care and the types of providers with whom it

collaborates. This could force a managed care organization to contract with providers that use

relatively excessive medical resources or provide relatively inferior care. A final concern

involves administrative or transactions costs, which increase with the number of providers with

whom the managed care organization contracts.

Any-willing-provider legislation varies across states and over time. AWP laws are

heterogeneous in their application. For example, some AWP laws target hospitals, physicians,

pharmacies, or some combination of the three. The focus of my paper centers on AWP










legislation that targets pharmacies specifically. For the remainder of what follows, we will focus

on the AWP laws enacted in states that focus on pharmacy providers specifically, while

controlling for effects of other types of AWP laws.

Many states have enacted some form of any-willing-provider legislation. Most of these

laws were passed in the 1990s, but some were passed earlier. Table 4-1 describes the states that

passed pharmacy-specific any-willing-provider laws as well as those which have other variants

of the legislation. Twenty-six states have AWP laws in place, with 23 states having laws which

apply to pharmacies, and 15 of which apply only to pharmacies.

Previous Literature

A small literature examines the effects of any-willing-provider legislation. In particular, a

study by Vita (2001) considers the impact of AWP legislation on general health care

expenditures. Using state-level per capital expenditures for total health care spending, hospital

care, and physician care, Vita considers the relationship between AWP laws and personal health

care expenditures. He categorizes the laws as ranging from weak to moderate to strong,

depending on their application. He finds that states with AWP legislation have higher per capital

total health care expenditures controlling for demographic factors and state trends. He also finds

some evidence that AWP laws are associated with increases in hospital care spending.

Most AWP laws are applicable to only pharmacies, meaning that HMOs in states with

pharmacy AWPs must admit any pharmacy that agrees to its terms, conditions, and

reimbursement rates into the network. Other states have physician or hospital AWP laws, which

require contracting with those types of providers. Given the overwhelming presence of

pharmacy-specific laws, it is important for us to understand the effects of pharmacy-specific

legislation on health care spending. Prior studies have failed to consider these types of laws

specifically or to consider the effect of AWP laws on pharmaceutical expenditures. To fill in this









gap in the literature, my paper considers the impact of pharmacy-specific AWP legislation on

pharmaceutical health care expenditures.

Data

Health Care Spending

The Centers for Medicare and Medicaid (CMS) publish state-level health expenditures

for specific health accounts and medical products, such as hospital care, physician services,

prescription drug expenditures, nursing home care, dental care, and the like. These data are

available by state for a panel of years and are based on the state of the provider.93 In Other words,

these data are based on the state where the services were received rather than the state where the

health care consumer resides. I use state-level observations on medical expenditures per capital

for the years 1987 through 1998.94 While there are many categories of health care spending, the

main focus in my paper will be on pharmaceutical expenditures. Additionally, I show results for

total health care expenditures, physician services, and hospital care in order to compare my

results with Vita (2001). For the purposes of this analysis, state of provider data are preferred to

the state of residence data.95 State of provider data distinguishes among prescription drug

expenditures, nonprescription drug expenditures, and other nondurable medical expenditures.

State of residence data, however, group these three into one category. We might be concerned,

however, about using state of provider data when analyzing hospital care or physician services


93 Data are also available based on State of Residence, but the panel of data available is shorter,
1991-1998.

94 State of provider data are available as early as 1980, but due to the availability of some other
variables, including HMO enrollment and market share, Medicare enrollment, Medicaid
enrollment, and the number of insured individuals I am able to utilize state of provider data
only as early as 1987.

95 State of residence data exist for 1991 through 1998, but do not distinguish between
prescription drugs and nonprescription drugs and medical sundries.









expenditures. For example, some individuals may cross state lines to receive some forms of

medical treatment like a surgery at a renowned hospital or an office visit with a specialist. But it

is less likely, however, that many individuals cross state lines in order to obtain prescription

drugs. Pharmaceutical expenditures, therefore, are unlikely to be affected significantly by the

state of provider characterization. Additionally, using data based on state of provider makes it

possible to utilize five additional years of data for every state.

Health care expenditures have increased dramatically since 1987. Real total health care

spending per capita96 increased 49 percent between 1987 and 1998. Similarly, hospital care and

physicians' services expenditures per capital have increased 33 percent and 50 percent,

respectively, between 1987 and 1998. Expenditures on prescription drugs per capital more than

doubled between 1987 and 1998, an increase of 119 percent. Figure 4-1 illustrates the pattern of

expenditures per capital over time for three categories: hospital care, physicians' services, and

prescription drugs.

Health Maintenance Organization Presence

One of the essential factors in this analysis is a measure of HMO presence. Relevant data

on HMO enrollments and HMO penetration rates were obtained through Forte Information

Resources.97 Aventis Pharmaceuticals sponsors a yearly survey of HMOs whose results are

summarized in an annual publication called the Managed Calre Digest Series, managed and

published by Forte.98 These publications are available for the years 1986 through 2004. I utilize


96 All dollar figures are adjusted to 1998 dollars.

97 Data published in each digest were collected by SMG Marketing Verzipan LLC, a health
care consulting firm which also conducts market research. Data were gathered mainly by mail
and telephone surveys.

98 Managed Calre Digest Series, HM\~O-PPO/M\~edicare-Medicaida Digest, Aventi s
Pharmaceuticals, relevant years.









HMO data for 1987 through 1998. These publications contain state-level information on the

number of HMOs serving each state, the total HMO enrollment, and HMO penetration. In the

analysis, I use HMO enrollments to calculate HMO market shares as well as HMO penetration

rates. HMO market share is calculated as the total HMO enrollment divided by the number of

covered lives.99 HMO penetration is defined as the total HMO enrollment divided by the state

population.

HMO enrollment has changed dramatically between 1987 and 1998. In 1987, average

HMO market share in the United States was 11.6 percent. By 1994, HMO market share had

increased to 20.2 percent. In 1998, HMO market share reached 33 percent.

Sample

Data for HMO enrollment and market share are only available as early as 1986. Medicare

enrollment, Medicaid enrollment, and the number of covered lives are only available for as early

as 1987. The data used in this analysis, therefore, spans 1987 through 1998. The District of

Columbia is omitted from this analysis. The sample is composed of 50 states over 12 years for a

total of 600 observations.

Empirical Methodology

To consider the effect of any-willing-provider legislation on health care expenditures, I

implement a fixed effects model using ordinary least squares. The estimated model is defined by

equation 4-1:

Expl, = ao + P, A Wig, + AlX,, + 3, + 8, + #2,, (4-1)

where Exp indicates the expenditures of the particular category of health care, A WP indicates

whether the state has an AWP law in place in that year, Xis a vector of state-level demographic


99 Historical Health Insurance Tables, Table HI-4, U.S. Census Bureau.









and health characteristics, 3 is a vector of state indicators, and B is a vector of year indicators.

Included in the vector of X covariates are the following variables: HMO market share, state-level

unemployment rate,'00 real per capital income, 101 percentage of the population over the age of

65, 102 percentage of the population of African American race, 103 and population density. 104 In

some specifications, as noted, I include the percentage of the population insured by Medicare and

the percentage of the population insured by Medicaid. In these specifications, the percentage of

the population over the age of 65 is omitted. I cluster my standard errors at the state-level and

weight each observation according to the state population. Table 4-2 contains summary statistics

for the relevant variables used in this analysis.

To begin, I estimate similar models to Vita (2001) to determine if the estimated effects of

any AWP laws on total health care expenditures, physician services, and hospital care are

comparable. To supplement that analysis and because most AWP laws apply only to pharmacies,

I test the effect of pharmacy-specific AWP legislation on prescription drugs expenditures, while

controlling for the laws affecting other providers. Since the maj ority of these types of legislation

target pharmacies as opposed to doctors and hospitals, it is important to understand the

consequences of these specific types of laws on health care expenditures.







100 Bureau of Labor Statistics, relevant years.

101 Personal income per capital, Bureau of Economic Analysis, relevant years. Nominal dollars
were inflated to 1998 dollars using changes in CPI-U from the Economic Report of the President.

102 U.S. Census Bureau, relevant years.

103 U.S. Census Bureau, relevant years.

104 Statistical Abstract of the United States, relevant years.









Results

General Any-Willing-Provider Legislation

HMOs are said to be effective in reducing health care expenditures. One way this occurs

is through selective contracting. AWP laws prevent an MCO from successfully negotiating

volume discounts and therefore from reducing health care spending effectively. This section

provides empirical evidence to support this claim.

Table 4-3 displays the results of regressions that consider any-willing-provider legislation

in general. In these specifications, AWP identifies states that have either a law applying to

pharmacies, hospitals, physicians, or some combination of the three providers. In this

specification, AWP laws are associated with an increase in total health care expenditures. The

magnitude of this effect is approximately $100 per capital. Relative to an average value of total

health care expenditures over the time period of $3 127, this accounts for a 3 percent increase in

expenditures per capital. AWP laws are also associated with increases in expenditures on

pharmaceutical drugs. The magnitude of this coefficient is approximately $15 per capital.

Relative to average pharmaceutical spending of $220 per capital, this increase accounts for a 7

percent increase in pharmaceutical spending per capital. There is no evidence that physician

services or hospital care expenditures are higher as a result of AWP legislation.

The results with respect to HMO market share are consistent with those of Cutler and

Sheiner (1998). Increased HMO presence is associated with a reduction in hospital expenditures

per capital. Although HMO market share is not statistically significant in the other three models,

the signs of the coefficients are consistent with previous empirical evidence. All models were

also estimated using HMO penetration rates in place of HMO enrollment rates. The results are

consistent across both specifications.









Table 4-4 illustrates the results of a similar specification that includes the percentage of

the population insured by Medicare and the percentage of the population insured by Medicaid,

omitting the percentage of the population over the age of 65. These results are not fundamentally

different from the results presented in Table 4-3. AWP legislation is associated with an increase

in total expenditures and prescription drug expenditures. The magnitudes in Table 4-4 are quite

similar to those in Table 4-3.

Some of the other covariates used in this analysis proved significant in some models. The

state-level unemployment rate and real income per capital are associated with higher levels of

health care spending. The percent of the population of African American race is positive and

significant in some models, as is the Fraction of the population with Medicare. Population

density, however, is not significant in any of the models.

Heterogeneous Application of Any-Willing-Provider Legislation

Any-willing-provider laws may apply to one or more of the following providers:

pharmacies, hospitals, and physicians. Most of the current laws, however, apply only to

pharmacy providers, while very few apply to hospitals or physicians or both. As a result, I

estimate several specifications which take into account whether the state law applies to

pharmacies or has other applications. Since the majority of these types of laws impact only

pharmacies, the most relevant category to consider is expenditures on pharmaceutical drugs. Any

effect on expenditures for hospital care or physician services should be less prominent. Table 4-5

utilizes Pharmacy AWP, which indicates if a particular state has an AWP law which applies to

pharmacies only. Pharmacy Plus indicates states which have an AWP targeting pharmacies as

well as another provider type. Hospital/Physician AWP indicate states which have AWP

applying to hospitals or physicians, but not to pharmacies. These results are consistent with the

results presented in Tables 4-3 and 4-4. Pharmacy-specific AWP laws are associated with an









increase in pharmaceutical drug expenditures per capital. Similarly, laws which target pharmacies

as well as other providers are also associated with an increase in pharmaceutical drug

expenditures per capital. Additionally, laws which apply to hospitals or physicians but not to

pharmacies are associated with an increase in hospital care expenditures per capital, but not with

a rise in physician services expenditures per capital. Reassuringly, these laws have no impact on

pharmacy expenditures.

Policy Endogeneity & Robustness

Policy Endogeneity

I attempted several forms of instrumental variables which had been suggested in the

literature, such as the percentage of firms defined as large, i.e., with more than 500 employees.

Ohsfeldt et al (1998) examines the likelihood of a state to pass an AWP law based on the winners

(providers, hospitals, pharmacies), the losers (MCOs, employers, and employees), and the

political environment. 1os When considering all AWP laws, the only variable that predicts the

enactment of the law is the number of hospital beds per capital. Other variables such as number of

physicians or pharmacists per capital and measures of the political climate were not significant

with respect to any-willing-provider law presence. Because AWP laws vary in their applicability

across states, the authors categorize the laws by what entities they target. Their model works well

for laws that are focused on hospitals, but does not perform well for laws which target

pharmacies and physicians. Only one variable, the percentage of employers defined as "large," is

related to the enactment of a pharmacy-specific any-willing provider law. Additionally, I utilized

a measure of political control, since more conservative states tend to support and enact AWP

legislation. Neither of these potential instrumental variables had any predictive power in the first



los This variable was also explored in an earlier study, McLaughlin (1987).









stage where AWP or pharmacy AWP was the dependent variable. This suggests a lack of valid

instruments for the policy change.

Other variables used in the public choice studies to predict the enactment of AWP

legislation, such as the number of physicianS106 Or hospital beds per capital, 107 would certainly

not be exogenous with respect to health care expenditures per capital. All of these instruments,

therefore, are not suitable as instruments in this analysis. 10s

It is still possible that AWP laws themselves are endogenous with respect to health care

expenditures per capital. If states enact these laws as a reaction to changes in health care

spending, then any estimated effect of AWP legislation will capture not only any change in

spending, but also any trend that was already occurring. If this is true, then any estimated effect

of AWP legislation would be biased upwards. If the likelihood that a state would enact an AWP

law is constant over time, then some of this potential bias is captured within the state fixed

effects.

To consider the possibility that estimated relationships in the previous section are

spurious, I examine state-specific trends before and after the change in legislation. I create a

piece-wise linear function or spline. For each state, I define year ofadoption as the year in which

the state adopted a pharmacy-specific AWP law. The first segment of the piece-wise linear

function captures the beginning of the data period to the year of law' s adoption. The second

segment represents the year of adoption through the end of the data period. If AWP legislation is

associated with a change or shock with respect to health care expenditures, then we would see a



106 Marsteller et al (1997).

107 Ohsfeldt el al (1998).

1os Bound, Jaeger, and Baker (1995); Staiger and Stock (1997).










change in the slope or trend line. To consider this potential change, I estimate separate

regressions for each state enacting pharmacy-specific AWP laws by regressing the two slope

coefficients on pharmaceutical expenditures per capital. I then test the difference between these

two slopes (slopel1 = slope2) to determine if there is a statistically significant difference.

Table 4-6 reports the results of this approach. Each row is a separate regression and

columns (1) and (2) report the estimated slope coefficients. Column (3) reports the F-statistic for

the restriction that the two coefficients are equal. This trend analysis works well for twelve of the

fourteen states with pharmacy-specific AWP legislation. In only two cases are the two slope

coefficients not statistically different. It appears from this component of the analysis that the

relationship between pharmacy-specific AWP legislation and pharmaceutical expenditures per

capital is not spurious. There does appear to be a change in the trend of expenditures with respect

to prescription drugs when AWP laws are adopted.

Robustness & Sensitivity Analysis

Another form of legislation targeted at managed care organizations is freedom of choice

(FOC) legislation. FOC legislation allows managed care subscribers to access providers outside

the managed care network, for a different fee but without having to pay the full price of care.

FOC laws could increase health care costs in a similar manner to AWP laws.

While my paper focuses exclusively on the effect of AWP legislation on health care

expenditures, in what follows I add an indicator for FOC as an additional explanatory variable.

The results presented in Table 4-7 and 4-8 suggest that FOC are not associated with a change in

health care expenditures per capital, for any of the four categories, and the signs and significance

on the AWP coefficients are similar to the results without an FOC indicator.









Conclusion

While the growth in the number and enrollment of health maintenance organizations has

reduced health care spending in some areas, it has done so through cost containment strategies

such as limiting patient choice. One political movement aimed at giving consumers of health

care more choice has resulted in the enactment of any-willing-provider legislation. Because such

state laws require a managed care organization to contract with any provider who is willing to

submit to the plan's terms, conditions, and reimbursement policies, patients by definition will

experience more choice within their managed care network. A potential side effect of such

legislation is an increase in health care spending due to two main factors: (1) inability of

managed care organization to selectively contract and (2) increases in administrative costs

associated with contracting with more providers. Most any-willing-provider laws target

pharmacies specifically, meaning that a managed care organization in a state with such a law

would only be required to contract with any willing pharmacy, not any willing physician or

hospital. As demonstrated through this analysis, pharmacy-specific AWP legislation is associated

with an increase in pharmaceutical drug expenditures per capital. Additionally, any-willing-

provider laws in general are associated with increases in total personal health care expenditures

(as well as pharmaceutical drug expenditures), a result which is consistent with prior Eindings.













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Table 4-1. Description of state any-willing-provider (AWP) legislation
State Year of Law Applicability of Law
Alabama 1988 Pharmacy
Arkansas 1991: 1995 Pharmacy: Physician/Hospital
Connecticut 1982 Pharmacy
Delaware 1994 Pharmacy
Florida 1993 Pharmacy
Georgia 1983 Pharmacy, Physician, Hospital
Idaho 1994 Physicians, Hospital
Illinois 1985 Physician
Indiana 1994 Pharmacy, Physician, Hospital
Kansas 1994 Pharmacy
Kentucky 1994 Physicians, Hospital
Massachusetts 1995 Pharmacy
Minnesota 1994 Pharmacy
Mississippi 1994 Pharmacy
Montana 1991 Pharmacy, Hospital, Physician
New Hampshire 1992 Pharmacy
New Jersey 1994 Pharmacy
New Mexico 1987 Pharmacy, Physician
North Carolina 1993 Pharmacy
North Dakota 1989 Pharmacy
Oklahoma 1994 Pharmacy
South Carolina 1994 Pharmacy
South Dakota 1990 Pharmacy
Texas 1991 Pharmacy, Hospital, Physician
Virginia 1983 Pharmacy, Hospital, Physician
Wyoming 1990 Pharmacy, Hospital, Physician










Table 4-2. Summary statistics
Variable Mean Std. Dev. Min Max
Real Total Health Care per Capita 3127.51 559.35 1800.01 4912.64
Real Hospital Care per Capita 1271.50 215.30 708.48 1992.16
Real Physicians Services per Capita 878.09 188.03 459.11 1520.21
Real Prescription Drugs per Capita 219.87 63.02 105.26 436.85

HMO Market Share 19.06 14.62 0 74.75
HMO penetration 16.50 12.66 0 60.8
Any AWP 0.31 0.46 01
Pharmacy AWP 0.16 0.37 0 1
Pharmacy Plus AWP 0.11 0.31 01
Hospital/Physician AWP 0.04 0.18 0 1
Population Density 168.54 233.18 0.9 1093.8
Percent Over Age 65 12.54 2.09 3.34 18.59
Percent Black 9.83 9.30 0.28 36.41
Real per Capita Income 23,269 3,571 15,322 36,822
Fraction Medicare 12.99 2.22 4.33 19.55
Fraction Medicaid 9.85 3.42 1.90 22.16










Table 4-3. Expenditures per capital results
(1) (2) (3) (4)
Variable Name Total Hospital Physician Drugs
AWP 106.44 36.31 23.51 14.90
[34.98]*** [20.74] [16.28] [6.75]**
HMO Market Share 0.05 -2.89 0.72 0.44
[1.81] [0.89]*** [0.83] [0.38]
Population Density -1.85 -0.93 0.05 -0.01
[1.92] [0.95] [0.28] [0.23]
Percent Black 124.51 46.62 4.34 27.72
[70.99]* [31.96] [14.54] [16.17]*
Real income per capital 0.11 0.05 0.02 0.01
[0.03]*** [0.02]*** [0.01]** [0.01]*
Unemployment Rate 42.85 11.29 22.17 -0.24
[9.97]*** [5.64]* [4.90]*** [2.06]
Population Over 65 63.36 42.84 0.07 6.72
[43.91] [24.33]* [22.64] [9.61]
Observations 600 600 600 600
R-squared 0.98 0.96 0.97 0.96
State Fixed Effects X X X X
Year Fixed Effects X X X X
Clustered standards errors (at the state-level) in brackets; weighed by the state
population.
* significant at 10%; ** significant at 5%; *** significant at 1%










Table 4-4. Expenditures per capital results with fractions of government insurance
(1) (2) (3) (4)
Variable Name Total Hospital Physician Drugs
AWP 103.51 34. 11 23.78 14.67
[35.88]*** [20.72] [16.62] [6.87]**
HMO Market Share 0.22 -2.63 0.62 0.45
[1.73] [0.83]*** [0.74] [0.40]
Population Density -1.67 -0.8 0.03 -0.079
[1.93] [0.96] [0.29] [0.23]
Percent Black 126.17 42.74 8.15 28.45
[71.61]* [33.09] [14.69] [15.93]*
Real income per capital 0.11 0.05 0.02 0.01
[0.03]*** [0.02]*** [0.01]** [0.01]*
Unemployment Rate 41.33 12.11 20.77 -0.59
[10.36]*** [5.62]** [4.77]*** [1.96]
Fraction Medicare 8.98 10.12 -4.49 -0.26
[7.09] [3.88]** [3 .22] [1.25]
Fraction Medicaid 3.84 -0.99 1.96 0.39
[4.79] [1.92] [2.37] [0.73]
Observations 600 600 600 600
R-squared 0.98 0.96 0.98 0.96
State Fixed Effects X X X X
Year Fixed Effects X X X X
Clustered standards errors (at the state-level) in brackets; weighed by the state
population.
* significant at 10%; ** significant at 5%; *** significant at 1%










Table 4-5. Expenditures per capital results with heterogeneous applicability of AWP law
(1) (2) (3) (4)
Variable Name Total Hospital Physician Drugs
Pharmacy AWP 108.5 28.89 27.05 14.65
[40.04]*** [24.22] [20.94] [7.86]*
Pharmacy Plus AWP 10.53 13.67 4.89 12.03
[28.10] [18.11] [7.27] [6.55]*
Hospital/Physician AWP 179.03 80.82 41.65 21.12
[91.33]* [35.85]** [29.70] [11.51]*
HMO Market Share 0.04 -2.66 0.58 0.43
[1.76] [0.85]*** [0.74] [0.40]
Population Density -1.69 -0.404 -0.77 -0.079
[1.95] [0.355] [0.94] [0.23]
Percent Black 124.94 42.342 43.69 28.35
[71.83]* [32.856] [33.07] [16.17]*
Real income per capital 0.11 0.052 0.05 0.01
[0.03]*** [0.017]*** [0.02]*** [0.01]*
Unemployment Rate 41.06 11.254 12.03 -0.64
[10.34]*** [5.503]** [5.55]** [1.97]
Fraction Medicare 9.68 10.642 10.4 -0.2
[7.06] [3.831]*** [3.90]** [1.26]
Fraction Medicaid 3.56 -0.839 -1.03 0.41
[4.73] [1.936] [1.92] [0.72]
Observations 600 600 600 600
R-squared 0.98 0.96 0.98 0.96
State Fixed Effects X X X X
Year Fixed Effects X X X X
Clustered standards errors (at the state-level) in brackets; weighted by the state
population.
* significant at 10%; ** significant at 5%; *** significant at 1%










Table 4-6. Spline regression results*
(1) (2)
State Slope 1 Slope 2


(3)
F-statistic
Slope 1 = Slope 2
1.69
46.51
54.90
36.42
40.71
49.73
23.76
5.57
42.32
42.59
2.69
51.36
172.56
0.15


Alabama -9.01
Delaware 12.05
Florida 13.02
Kansas 10.84
Massachusetts 12.60
Minnesota 9.99
Mississippi 10.96
New Hampshire 10.19
New Jersey 16.88
North Carolina 8.31
North Dakota 7.71
Oklahoma 11.07
South Carolina 10.85
South Dakota 10.98
*Each row is a separate regression.


15.78
39.05
33.11
21.95
30.67
25.57
24.91
19.03
33.81
24.18
14.36
22.22
30.66
12.41










Table 4-7. Expenditures per capital results with freedom of choice (FOC) indicator
(1) (2) (3) (4)
Variable Name Total Hospital Physician Drugs
AWP 97.5 26.1 26.03 16.6
[34.49]*** [19.85] [18.67] [6.69]**
FOC 25.43 33.84 -9.54 -8.17
[27.88] [21.24] [12.42] [5.56]
HMOMarket 0.27 -2.57 0.61 0.44
[1.72] [0.82]*** [0.73] [0.40]
Population Density -1.73 -0.88 0.05 0.02
[1.98] [1.00] [0.28] [0.23]
Percent Black 128.07 45.27 7.43 27.84
[71.64]* [32.18] [14.47] [15.94]*
Real income per capital 0.11 0.05 0.02 0.01
[0.03]*** [0.02]*** [0.01]** [0.00]**
Unemployment Rate 40.91 11.55 20.93 -0.46
[10.12]*** [5.24]** [4.82]*** [1.86]
Fraction Medicare 8.15 9.02 -4.18 0.01
[6.94] [3.84]** [3.01] [1.26]
Fraction Medicaid 3.94 -0.86 1.93 0.36
[4.74] [1.80] [2.35] [0.75]
Observations 600 600 600 600
R-squared 0.98 0.98 0.98 0.96
State Fixed Effects X X X X
Year Fixed Effects X X X X
Clustered standards errors (at the state-level) in brackets; weighed by the state
population.
* significant at 10%; ** significant at 5%; *** significant at 1%










Table 4-8. Expenditures per capital results with heterogeneous applicability of AWP law and
FOC indicator.
(1) (2) (3) (4)
Variable Name Total Hospital Physician Drugs
Pharmacy AWP 100.84 18.19 29.93 16.84
[38.08]** [22.09] [23.98] [7.86]**
Pharmacy Plus AWP 14.33 18.99 3.45 10.95
[29.46] [19.21] [7.95] [6.24]*
Hospital/Physician AWP 179.81 81.91 41.36 20.89
[94.91]* [40.47]** [28.42] [10.73]*
FOC 26.8 37.45 -10.1 -7.65
[28.06] [22.64] [13.65] [5.99]
HMOMarket 0.11 -2.57 0.55 0.41
[1.75] [0.84]*** [0.73] [0.40]
Population Density -1.75 -0.85 0.04 0.01
[2.00] [0.98] [0.29] [0.23]
Percent Black 127.47 47.22 6.73 27.63
[71.96]* [32.01] [13.86] [16.21]*
Real income per capital 0.11 0.05 0.02 0.01
[0.03]*** [0.02]*** [0.01]** [0.00]*
Unemployment Rate 40.66 11.47 20.89 -0.53
[10.07]*** [5.17]** [4.92]*** [1.87]
Fraction Medicare 8.79 9.14 -4.00 0.06
[6.86] [3.89]** [2.96] [1.26]
Fraction Medicaid 3.7 -0.83 1.85 0.37
[4.69] [1.80] [2.36] [0.73]
Observations 600 600 600 600
R-squared 0.98 0.96 0.98 0.96
State Fixed Effects X X X X
Year Fixed Effects X X X X
Clustered standards errors (at the state-level) in brackets; weighted by the
state population.
* significant at 10%; ** significant at 5%; *** significant at 1%









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BIOGRAPHICAL SKETCH

Christine Ann Piette graduated from Emory University with a Bachelor of Arts in

economics. She earned her degree with highest honors after completing and defending a thesis

on the labor market effects of earning a GED versus a high school diploma. After completing her

degree at Emory, Christine worked as a research assistant for a management consulting firm in

Tallahassee, Florida for one year.

In 2003, Christine began the graduate program at the University of Florida in the

Department of Economics. After two years of coursework and successful completion of field

examinations, Christine earned her Master of Arts in economics. Both during her coursework

and in the two years following, Christine was employed by the department as both a research

assistant and a teaching assistant. Additionally, Christine served as a teaching assistant for an

executive level 1VBA course during two consecutive years. In the fall of 2006, Christine was an

instructor for an upper-level elective, government regulation of business, within the economics

department. After successful completion of all requirements for her degree, Christine will eamn

the Doctor of Philosophy degree in August 2007. She has accepted an assistant professor

position at the University of North Carolina at Chapel Hill where she will begin in the fall of

2007.





PAGE 1

1 ESSAYS IN HEALTH-RELATED PUBLIC POLICY By CHRISTINE ANN PIETTE A DISSERTATION PRESENTED TO THE GRADUATE SCHOOL OF THE UNIVERSITY OF FLOR IDA IN PARTIAL FULFILLMENT OF THE REQUIREMENTS FOR THE DEGREE OF DOCTOR OF PHILOSOPHY UNIVERSITY OF FLORIDA 2007

PAGE 2

2 2007 Christine Ann Piette

PAGE 3

3 To my parents, Michael and Di anne, and to my husband, Joseph

PAGE 4

4 ACKNOWLEDGMENTS The successful completion of this dissertati on was not possible without with guidance and support of several individuals. I thank my committee: Lawr ence Kenny, Roger Blair, David Figlio, and Bruce Vogel. Each of these indivi duals has provided endl ess support, overwhelming encouragement, invaluable discussions, and th oughtful suggestions. I cannot thank them enough for their support through this pr ocess. I also thank Mark Rush for graciously participating on my committee, in my defense, and for providing useful suggestions. I also re ceived valuable input and guidance from other indivi duals including Sarah Hamersma Damon Clark, Steven Slutsky, Jonathan Hamilton, and Jeffrey Harrison. Finally, I thank Michael and Dianne Piette who have spent a lifetime not only helping me to achieve this goal, but to ach ieve all my goals.

PAGE 5

5 TABLE OF CONTENTS page ACKNOWLEDGMENTS...............................................................................................................4 LIST OF TABLES................................................................................................................. ..........7 LIST OF FIGURES................................................................................................................ .........9 ABSTRACT....................................................................................................................... ............10 CHAPTER 1 INTRODUCTION..................................................................................................................12 2 NON-ECONOMIC DAMAGE CAPS AND MEDICAL MALPRACTICE CLAIM FREQUENCY: IS IT TIME FOR A SECOND OPINION....................................................15 Introduction................................................................................................................... ..........15 Empirical Model................................................................................................................ .....19 Model and Dependent Variable.......................................................................................19 Independent Variables.....................................................................................................20 Instrumentation................................................................................................................24 Data........................................................................................................................... ..............27 Identification................................................................................................................. ...29 Policy Endogeneity..........................................................................................................30 Empirical Results.............................................................................................................. ......32 First Stage.................................................................................................................... ....32 Second Stage...................................................................................................................33 Lags in Su it Duration.......................................................................................................34 Alternative Methodology........................................................................................................35 Robustness Checks and Add itional Considerations...............................................................37 Severe Damage Caps.......................................................................................................37 Additional Considerations...............................................................................................38 Conclusions.................................................................................................................... .........38 3 THE EFFECTS OF INCREASED ACCESS TO THE MORNNG-AFTER PILL ON ABORTION AND STD RATES............................................................................................55 Introduction................................................................................................................... ..........55 Previous Literature............................................................................................................ ......57 The Relative Costs of Sexual Activity....................................................................................62 Pharmacy Access to Emergency Contraception.....................................................................63 History of Emergency Contraception..............................................................................63 The Washington State Pilot Project.................................................................................63 Data........................................................................................................................... .......67 Chlamydia...................................................................................................................... ..67

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6 Abortion Data..................................................................................................................68 Program Participation......................................................................................................69 Identification................................................................................................................. ..........71 Chlamydia...................................................................................................................... ..71 Abortions...................................................................................................................... ...73 Pharmacy Participation....................................................................................................74 Other Characteristics.......................................................................................................76 Empirical Methodology..........................................................................................................76 Results........................................................................................................................ .............78 Chlamydia Rates..............................................................................................................78 Abortion Rates.................................................................................................................79 Lag in Treatment.............................................................................................................79 Alternative Treatment Definitions...................................................................................80 Chlamydia Rates..............................................................................................................80 Abortion Rates.................................................................................................................81 Other Considerations.......................................................................................................81 Falsification Tests............................................................................................................ .......82 Additional Control Group: Oregon.........................................................................................83 Chlamydia...................................................................................................................... ..83 Abortion....................................................................................................................... ....85 Conclusions.................................................................................................................... .........86 4 THE IMPACT OF PHARMACY-SPE CIFIC ANY-WILLING-PROVIDER LEGISLATION ON PRESCRIPTION DRUG EXPENDITURES.....................................128 Introduction................................................................................................................... ........128 Managed Care and Any-Willing-Provider Legislation.........................................................129 Managed Care and Health Maintenance Organizations................................................129 Any-Willing-Provider Legislation.................................................................................131 Previous Literature............................................................................................................ ....132 Data........................................................................................................................... ............133 Health Care Spending....................................................................................................133 Health Maintenance Organization Presence..................................................................134 Empirical Methodology........................................................................................................135 Results........................................................................................................................ ...........137 General Any-Willing-Provider Legislation...................................................................137 Heterogeneous Application of Any-Willing-Provider Legislation...............................138 Policy Endogeneity & Robustness........................................................................................139 Policy Endogeneity........................................................................................................139 Robustness & Sensitivity Analysis................................................................................141 Conclusion..................................................................................................................... .......142 LIST OF REFERENCES.............................................................................................................152 BIOGRAPHICAL SKETCH.......................................................................................................158

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7 LIST OF TABLES Table page 2-1 Summary statistics of variables.........................................................................................40 2-2 Data sources............................................................................................................... ........41 2-3 States enacting non-economi c damage reforms (1991-2001)............................................42 2-4 State limits on damages.................................................................................................... .43 2-5 Non-economic damage caps held unconstitutional............................................................45 2-6 Description of cat egories of states.....................................................................................46 2-7 Baseline statistics (1991)................................................................................................. ..47 2-8 Change in suits between y ear t-2 and t-1; t-1 and t=0.......................................................48 2-9 First stage results........................................................................................................ ........49 2-10 Ordinary least squares (OLS) and tw o-stage least squares (2SLS) results .......................50 2-11 2SLS results variants of duration.....................................................................................51 2-12 OLS results using unconstitutionality of caps...................................................................52 2-13 Results for severe cap.................................................................................................... ....53 3-1 Summary statistics......................................................................................................... ....87 3-2 Baseline statistics........................................................................................................ .......88 3-3 Difference in means t-tests between treatment and control...............................................89 3-4 Difference in means t-tests be tween early and late adopters.............................................90 3-5 Difference in means t-test s for county characteristics.......................................................91 3-6 Chlamydia rates overall, by gender, and by gender/age....................................................92 3-7 Three-year pretreatme nt average, Washington..................................................................93 3-8 Chlamydia rates overall, by gender, and by gender/age with covariates...........................94 3-9 Abortion rates overall and by age......................................................................................95 3-10 Chlamydia rates overall, by gender, and by gender/age....................................................96

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8 3-11 Abortion rates overall and by age......................................................................................97 3-12 Falsification tests us ing county cancer rates......................................................................98 3-13 Falsification exercise.................................................................................................... .....99 3-14 Difference in means t-test, chlamydia rates.....................................................................100 3-15 Summary statistics, Washington and Oregon..................................................................101 3-16 Chlamydia rates including Oregon..................................................................................102 3-17 Three-year pre-treatment av erage, Washington and Oregon...........................................103 3-18 Chlamydia rates including Oregon..................................................................................104 3-19 Abortion rates including Oregon.....................................................................................105 3-20 Abortion rates including Oregon.....................................................................................106 4-1 Description of state any-willi ng provider (AWP) legislation..........................................144 4-2 Summary statistics......................................................................................................... ..145 4-3 Expenditures per capita results........................................................................................146 4-4 Expenditures per capita results with fractions of government insurance........................147 4-5 Expenditures per capita results with he terogeneous applicability of AWP law..............148 4-6 Spline regression results..................................................................................................149 4-7 Expenditures per capita results with freedom of choice (FOC) indicator.......................150 4-8 Expenditures per capita results with he terogeneous applicability of AWP law and FOC indicator.................................................................................................................. .151

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9 LIST OF FIGURES Figure page 2-1 Description of enactment of cap and change in political composition..............................54 3-1 Chlamydia rates in the United States, 1992 2003.........................................................107 3-2 Overall and female Chlam ydia rates in Washington state...............................................108 3-3 Overall abortion rate (age 15-44) in Washington state....................................................109 3-4 Abortion rates in the United States, 1992 2003............................................................110 3-5 Abortion rates in Washington state, ages 15-19 and ages 20-24.....................................111 3-6 Washington state pharmacy access in 1998.....................................................................112 3-7 Washington state pharmacy access in 2002.....................................................................113 3-8 Washington state pharmacy access in 2005.....................................................................114 3-9 Overall chlamydia rates by treatment and control group.................................................115 3-10 Female chlamydia rates by treatment and control group.................................................116 3-11 Overall abortion rates (age 15-44) by treatment status....................................................117 3-12 Abortion rates (age 15-19) by treatment status................................................................118 3-13 Abortion rates (age 20-24) by treatment status................................................................119 3-14 Overall chlamydia rate s, Washington and Oregon..........................................................120 3-15 Overall chlamydia ra tes by treatment status....................................................................121 3-16 Abortion rates, Washington and Oregon.........................................................................122 3-17 Abortion rates 15-19, Washington and Oregon...............................................................123 3-18 Abortion rates 20-24, Washington and Oregon...............................................................124 3-19 Abortion rates by treatment status...................................................................................125 3-20 Abortion rates 15-19 by treatment status.........................................................................126 3-21 Abortion rates 20-24 by treatment status.........................................................................127 4-1 Expenditures per capita, 1987-1998................................................................................143

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10 Abstract of Dissertation Pres ented to the Graduate School of the University of Florida in Partial Fulfillment of the Requirements for the Degree of Doctor of Philosophy ESSAYS IN HEALTH-RELATED PUBLIC POLICY By Christine Ann Piette August 2007 Chair: Lawrence Kenny Major: Economics My research examined three separate studies of health-related public policy. In the first study, I analyzed the effect of non-economic damage caps on the frequency of medical malpractice claims, recognizing that such laws are likely endogenous. I constructed a unique instrument using past and current values of state political com position and other factors. I also exploited exogenous Supreme Court findings of unconstitutionality. In both cases, I found that caps on non-economic damages are not associated w ith a reduction in medical malpractice claim frequency. This result is robust to alternat ive specifications and comparison groups. Next, I considered risky behavior. The FDA recently approved a proposal to allow emergency contraception, or Plan B, to be av ailable through pharmacies without a prescription. While this change is only now occurring nati onally, several states had previously allowed pharmacy access to emergency contraception. In part icular, Washington Stat e was the first state to implement such a program in 1998. Propone nts of pharmacy access argued that improved access could decrease the number of abortions Opponents cited concern that pharmacy access could lead to an increase in risk-taking, esp ecially among teens or young adults, and hence lead to increased rates of sexually-transmitted diseases. In my paper, I used county-level data as well as specific timing of pharmacy participati on to consider the intended and unintended

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11 consequences of pharmacy access to emergenc y contraception in Washington. My findings support both claims. Pharmacy access is associated with a small decrease in abortions for some age groups. In addition, pharmacy access is associated with an increase in Chlamydia rates for young women. These results are robust to an altern ative comparison group as well as alternative definitions of treatment. In the final study, I analyzed any-willing pr ovider (AWP) legislation. In recent years, many states have implemented AWP legislation, which requires a managed care organization (MCO) to accept any provider, who agrees to the managed care organizations reimbursement rates, terms, and conditions, into its network. Pr oponents argue that AWP laws provide for larger networks, more patient choice, greater comp etition among providers, and arguably increased quality of care. Opponents cite AWP legislation as prohibiting managed care organizations from selective contracting an d obtaining discounts by o ffering providers a larger volume of patients. Such legislation is therefore argued to prevent MCOs from effectively reducing health care costs. A small literature exists on the effect of these laws on hospital expenditures, physician expenditures, and total health care expenditures. Mo st studies, however, fail to recognize that the vast majority of the existing laws target pharmacies exclusively, as opposed to more comprehensive laws that also apply to physicians and hospitals. If AWP legislation prevents cost reduction available through selec tive contracting, then states w ith such legislation may incur higher health care expenditures. My paper is the first to analyze the impact of pharmacy-specific AWP legislation on state-level prescription drug expenditures.

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12 CHAPTER 1 INTRODUCTION My analysis of public policy issues is comprised of thr ee studies: (1) Non-economic damage caps and medical malpractice claim freque ncy: is it time for a second opinion?, (2) The effects of increased access to the morning-after pill on abortion and sexually-transmitted disease rates, and (3) The impact of pharmacy-specific any-willing provider legi slation on prescription drug expenditures. The first study considered the effect of non-ec onomic damage caps, one particular type of tort reform, on the frequency of medical malpracti ce claims, while recognizing that such laws are endogenous. I constructed a unique instrument by calcu lating the predicted probability that a law is in place in each of the prior years given state political composition and other factors. I then used the cumulative probability, based on current a nd past influences, as an instrument for the enactment of a cap. This procedure is preferab le to using instruments of contemporaneous political control, an approach typically exploited in the literature. My approach produces strong first stage statistics. I found that caps on non-economic damages are not associated with a reduction in claim frequency. This result is robus t to alternative specifications and comparison groups. In addition, I exploited exogenous Supr eme Court findings of unconstitutionality. If noneconomic damage caps are effective in reducing cl aim frequency, then the removal of such caps will increase claim frequency. Using this alternative approach, I again found no relationship between non-economic damage caps and claim frequency. I also considered the effects of increased access to the morning-after pill. A recent FDA decision allowed emergency contraception, or Pl an B, to be available through pharmacies without a prescription. While this change is only now occurring nationally, several states had previously allowed pharmacy access to emergency contraception. In particular, Washington State

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13 was the first state to implement such a program in 1998. Proponents of pharmacy access argue that improved access could decrea se the number of abortions. Opponents cite concern that pharmacy access could lead to an increase in risk taking, especially among teens or young adults, and hence lead to increased rates of sexually-transmitted diseases. In my paper, I used countylevel data as well as specific timing of pharmacy participation to consider the intended and unintended consequences of pharmacy access to emergency contraception in Washington. My findings support both claims. Pharmacy access is associated with a small decrease in abortions for some age groups. In addition, pharmacy access is associated with an increase in Chlamydia rates for young women. These results are robust to an alternative comparison group as well as alternative definitions of treatment. Finally, my analysis focused on another type of health policy, any-willing provider (AWP) legislation. In recent years, many stat es have implemented AWP legislation, which requires a managed care organiza tion (MCO) to accept any provider, who agrees to the managed care organizations reimbursement rates, terms, and conditions, into its network. Proponents argue that AWP laws provide for larger netw orks, more patient choice, greater competition among providers, and argua bly increased quality of care. O pponents cite AWP legislation as prohibiting managed care organiza tions from selective contrac ting and obtaining discounts by offering providers a larger volume of patients. Su ch legislation is therefore argued to prevent MCOs from effectively reducing hea lth care costs. A small literature exists on the effect of these laws on hospital expenditures, physician expenditure s, and total health care expenditures. Most studies, however, fail to recognize that the vast majority of the existing laws target pharmacies exclusively, as opposed to more comprehensive laws that also apply to physicians and hospitals. If AWP legislation prevents cost reduction available through select ive contracting, then states

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14 with such legislation may incur higher health car e expenditures. My research is the first to analyze the impact of pharmacy-specific AWP legislation on state-le vel prescription drug expenditures.

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15 CHAPTER 2 NON-ECONOMIC DAMAGE CAPS AND MEDICAL MALPRACTICE CLAIM FREQUENCY: IS IT TIME FOR A SECOND OPINION Introduction Medical malpractice litigation is a source of much concern. Claim frequency is on the rise. Between 1993 and 2002, claims increased by 18% (National Center for State Courts, 2003). In addition, median awards jumped from $253,000 in 1992 to $431,000 in 2001, a real increase of 70% (Bureau of Justi ce Statistics, 2001). As a result, physicians are faced with rising insurance premiums. In spite of soaring premiums, major medical malpractice insurers are exiting the industry (Freudenheim, 2001). Anecdotal evidence suggests that th ere may be additional effects of medical malpractice litigation. For example, phys icians are said to be transferring states in search of lower insurance premiums (Wagner, 2004). Specialists in obst etrics/gynecology are reportedly refusing to perform di fficult deliveries and changing th eir procedure usage due to the fear of malpractice suits (A merican College of Obstetrici ans and Gynecologists, 2004). Some claim that physicians are changi ng their fields of specialty (Ame rican College of Obstetricians and Gynecologists, 2004)1 or are practicing without insurance (Silverman, 2004). The public policy response has been tort reform with particular interest in imposing caps on non-economic damages.2 Non-economic damages are typically those awarded for pain and 1 Fourteen percent of respondent s to an ACOG Survey stopped pr acticing obstetrics because of the risk of medical liability claims. 2 Tort reform, with a focus on medical malpract ice litigation, has also been proposed at the national level. The Comprehens ive Medical Malprac tice Reform Act of 2005 (HR 321) calls for a cap on non-economic damages of $ 250,000, adjusted for inflation from 1975.

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16 suffering, loss of consortium or co mpanionship, or emotional distress.3 Proponents of tort reform argue that non-economic damage caps will decrea se claim severity through a reduction in noneconomic damage awards. Additionally, non-economi c damage caps alter the expected benefits of filing a claim by reducing the av ailable non-economic damages. If the expected benefits fail to exceed the costs of pursuing a medical malpractice action, then some claims may be deterred. Is this behavioral response to caps on non-ec onomic damages common enough to lead to a discernable reduction in claim frequency? An extensive literature exists regarding the e ffects of tort reform on a number of different outcomes: claim frequency (Danzon, 1984; Danzon, 1986),4 claim severity (Danzon, 1984; Danzon, 1986; Yoon, 1991; Browne & Puelz (1999), insurance profitability (Viscusi & Born, 1995; Born, Viscusi, & Carlton, 1998), and premiums (Thorpe, 2004), and physician supply (Matsa, 2005; Klick & Strattman, 2003). Only one main study specifically targets medical malpractice claim frequency, as opposed to the fr equency of general tort claims. Danzon (1984) focuses on the determinants of claim frequency as a result of tort reforms enacted during the 1970s.5 Danzon reports that while limits on awards do have an effect on claim severity, such caps (as well as other tort reforms) do not have an effect on claim frequency. 3 Although most commonly referred to as noneconomic damages, these damages are nonpecuniary in the sense that they do not compensa te the plaintiff for lost earnings or medical expenses, but rather for a loss that is difficu lt to quantify. The non-economic characterization is clearly wrong. These damages may be non-pe cuniary, but they are hardly non-economic. 4 Danzon (1984) and Danzon (1986) focus on medical malpractice claim frequency specifically, Lee, Browne, & Schmidt (1994) and Browne & Pu elz (1999) focus on general tort claims and automobile accident claims, respectively. 5 Danzon (1986) presents similar evidence to Danzon (1984), but does not specifically address the relationship between dama ge caps and claim frequency.

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17 My study focuses on the effect of non-economic damage cap legislation on the frequency of medical malpractice claim frequency, as measured by successful medical malpractice lawsuits. My paper furthers the existing literature in several ways. As noted earlier, this is a subject that has received little at tention in the literature. This is the first study to examine the impact of recent non-economic damage caps le gislation on claim frequency and to use appropriate instrumental variables estimation. The literature that estimates the effects of various policies, includi ng tort reforms, is plagued by the fact that economic and political forces partly determine whether a policy is enacted. The estimated impact of the policy may re flect the factors that played a role in enacting the policy rather than the true effect of the policy. Others working in the policy area have recognized this problem and have employed instrume ntal variables procedur es to deal with the endogeneity bias due to spurious correlation between the pol icy and the factors that determine whether the policy is enacted. My study is the fi rst to employ instrumental variable techniques to study the effect of non-economic damage caps on the frequency of medical malpractice claims. My study uses a novel strategy to remedy policy endogeneity.6 The instrumental variable policy literature assumes that only current fact ors determine whether a law is in place. But legislators deal with a small number of issues each year and as a result laws are changed infrequently. Therefore, the probability that a law is in place not only reflects the current factors 6 Other studies have treated tort reforms as endogenous. Klick & Stratmann (2003), who consider the effect of tort reform on physician supply, us e indicators for whether th e state legislature is controlled by the Democratic party, if corporatio ns can make political contributions, and other unspecified instruments. Rubin & Shepherd (200 5), who study the effect of tort reform on accidental death rates, use the state population vo ting Republican in each presidential election as well as per capita employment in the legal pr ofession. Sharkey (2005) uses contemporaneous state political control as an instrument for damage caps, but finds that it is a weak instrument and proceeds with OLS estimation.

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18 affecting the enactment of the law but also incorporates past influences. The cumulative probability that a law is in place, based on current and past values of these factors, should best explain whether the law is curren tly in place. I compare the fits under various formulations and demonstrate that it is important to consider prior values in addition to cu rrent values of factors affecting the enactment of a law. A better fit is obtained using prior infl uences of law enactment than with contemporaneous influences. The best fit is obtained when th e predicted probability that a law is in place reflects the probability that the law was enacted in each of the prior years (i.e., the cumulative probability). This unique st rategy for instrumentation yields strong first stage results, making the estimated effects of damage caps more plausible. The novel strategy used here for taking account of the stickiness of state laws when deali ng with policy endogeneity should be of value in other studies that consider the impact of public policies. The effects of non-economic damage caps on clai m frequency are also estimated using an alternative methodology. This approach exploits exogenous changes in the law (state court findings of unconstitutionality) to consider the effect of remo ving a cap on claim frequency. This approach thus avoids having to deal with the endogeneity associated with the enactment of a law. Since caps on non-economic damages should decrease the expected return of filing a suit, one would expect to find a negative relations hip between claim frequency and the imposition of damage caps. While ordinary least squares (OLS ) results indicate a negative and statistically significant relationship between non-economic damage caps and claim frequency, two-stage least squares (2SLS) results yield different fi ndings. When using the instrumental variables approach, caps do not have a statistically significa nt effect on claim frequency. This result is robust to a variety of specifications includi ng different instrument definitions. Similarly,

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19 estimates based on exogenous state Supreme Court rulings indicate that th e removal of a damage cap does not have an identifiabl e effect on claim frequency. Empirical Model Proponents of tort reform argue that caps on non-economic damages will decrease claim frequency and claim severity, reduce malpract ice premiums, and thereby improve access to health care. It may, therefore, be difficult to argue that impo sing a cap is an exogenous policy change. To assume exogeneity, we must belie ve that caps on non-economic damages were not implemented with the underlying f actors of the health care industry or medi cal malpractice in mind. If we suspect that caps are enacted as a re sult of underlying factors, then we should be concerned that non-economic damage caps a nd the number of suits are simultaneously determined, and therefore endogenous. Model and Dependent Variable A two-stage least squares approach is utilized to account for the potential endogeneity of non-economic damage caps. A model representing cl aim frequency is specifi ed in the following equation: it t i it it it itR S M (2-1) where I i ,... 1 for each state and T t ,... 1 for each year. itM represents the natural logarithm of the number of successful medical malpractice suits per 100, 000 population in state i in year t. 7 Since claim frequency reflects the size of th e state, the number of successful suits is 7 This logarithmic transformation was made for eas e of interpretation. All models were initially run with the number of successf ul medical malpractice suits pe r 100,000 of the population as the dependent variable rather than the natural logarithm. Estimates obtained from the initial models are very similar to the estimates presented here.

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20 scaled by the state population.8 itS is a vector indicating the st ate-level demographic variables and itR indicates a vector of tort reform variables. i denotes state fixed effects and t indicates year fixed effects. Independent Variables The independent variables used to control for variations in state de mographic and health characteristics are described in this section.9 Dummy variables indicati ng the existence of noneconomic damage caps are also included. Additiona lly, state and year fixed effects were utilized to capture unobserved state and time differences Summary statistics are included in Table 2-1 and Table 2-2 contains the source informa tion for each of the variables included. Disposable Income per Capita. In general, higher levels of per capita income are associated with better health levels.10 Higher incomes are associated with a greater propensity for healthy activity, less demand for medical care and therefore less exposure to medical malpractice. It is also possible that individual s with higher incomes are less likely to file suit given the higher opportunity co st of their time. The predicted sign of this variable, IncomePerCapita, is negative. 8 Total suits scaled by the stat e population provided a better fit than total suits scaled by the number of physicians. 9 The literature has suggested that lawyers per cap ita may be a determinant of claim frequency. This variable was not included for three main re asons. First, the number of lawyers per capita is likely to be endogenous since lawy ers respond to the cost of suing. Second, lawyers per capita may be multicollinear with the pe rcent of the population living in a metropolitan area. Finally, this variable was never significant in any m odel, and the results are therefore omitted. 10 Nominal disposable income per capita was c onverted to 1991 dollars using the Consumer Price Index-Urban (CPI).

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21 Percent of Population Living in Metropolitan Areas. The inclusion of an urbanization variable captures the level of medical complex ity and legal specialization. Urban areas are centers of medical treatment, a nd are likely to offer more co mplex medical treatments which could lead to more occurrenc es of medical malpractice.11 Additionally, metropolitan areas may exhibit less personal doctor-pat ient relationships than less urban areas. This anonymity may contribute to a higher rate of litigation. Moreover, metropolitan areas provide greater access to litigation. Hence, the percent of the population living in metropolit an areas, Metro, is predicted to have a positive impact on claim frequency. Personal Health Care Expenditures. Medical care physicia n visits, prescription drugs, nursing homes, and the like are a grow ing portion of our economy. To capture the importance and size of the medical sector, the level of personal health care expenditures as a percentage of Gross State Product (GSP) has been in cluded in this model. One would expect that as the size of the health care industry increases the greater the interact ion between individuals and the medical community. This increased e xposure to many different components of the medical sector could potentially lead to more medical malprac tice exposure and could therefore result in more suits.12 Unemployment Rate. The state unemployment rate wa s included as a general measure of the economic conditions during the relevant time period. When unemployment rates are high, 11 Danzon (1984) and Lee, Browne, and Schmidt ( 1994) also used an urbanization variable in their studies. Each found urbanization to be statistically significan t and a strong positive determinant of claim frequency. 12 Following other studies, specifi c medical treatment variables had been included in my study prior to including personal health care expenditures as a percentage of GSP. Initially, percent of the population over age 65, surgerie s per capita, outpatient visits pe r capita, and births per capita were included in the model. While some of thes e variables had an effect on the number of suits per capita, personal health care expenditures is a more comprehensive measure of health care utilization and ultimately provided a better fit for the model.

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22 opportunity cost for lawyers and those injured is low and therefore may lead to more suits. An increase in the unemployment rate, however, could also be associated with a decrease in claim frequency. If unemployment is high, we may see mo re individuals without in surance. If this is the case, individuals without heal th insurance benefits may be le ss likely to seek medical care, and we may see a decrease in clai m frequency during economic downturns. Non-Economic Damage Caps. Caps on non-economic damages are designed to decrease the non-economic damages available to a plaintiff, which reduces the value of the total award. At the margin, the expected benefits may no longer exceed the expected cost s, and therefore some medical malpractice cases will not be filed. Thus it is possible that claim frequency will decline following the imposition of a cap on non-economic damages. If, however, the driving force of most suits is due to economic losses, then noneconomic damage caps may have little effect on claim frequency. States that enacted a damage cap during the re levant data period rece ive a value of 1 for the year in which their damage cap was implem ented and every year thereafter. For example, Alaska, which established a cap in 1997, receiv es a value of 1 for the years 1997 through 2001, and 0 otherwise. Potential lags in policy effect iveness will be consid ered in Section IV. Table 2-3 lists the states a nd associated years in which non-economic damage caps were implemented as well as the dollar amount of the cap (in the year in which it was enacted).13 Only reforms that were implemented during the 19912001 period were used in this analysis. Any state that enacted a non-economic damage cap before 1991 or that had a cap on total damages was omitted from this analysis. Any state with a specific medical malpractice non-economic 13 Tables 2-4 and 2-5 contain more detailed documentation of stat e laws on non-economic damage caps.

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23 damage cap is included as well as any state with a non-economic damage cap on general tort claims. The American Tort Reform Association (ATR A) outlines its ideal package regarding medical malpractice reform. Included in the sugg ested reforms is a severe non-economic damage cap of $250,000, collateral source reform, and a sliding scale for attorneys fees. The collateral source rule prevents evidence invol ving payments to the plaintiff from a third party, such as insurance payments, workers compensation, or social security benefits, from being admitted at trial. Collateral source reform typi cally involves the admissibility of third party payments at trial. Almost all collateral source reforms took place prio r to the time period c onsidered in my study. The other proposed reform, a sliding scale for atto rneys fees, limits the amount that attorneys can collect in contingency fees. All states which enacted limits on attorneys fees did so before the time period considered in my study. Therefor e, any potential effect of these reforms should be contained in the state fixed effects. Variables indicating the presence of these two reforms are therefore not included in the model. While other reforms such as joint and several liability reform and limits on punitive damages may have an impact on tort filings in ge neral, they are not necessarily relevant when considering medical malpractice specifically. Th e ATRA does not consider these reforms as an essential remedy to the current health care crisis Joint and several liability affects tort filings indirectly because the reform does not directly target damages.14 Punitive damages are rarely awarded in medical malpractice cases.15 Damages of this type are used solely to punish the 14 See Kessler & McClellan (1996) who categ orize reforms as direct and indirect. 15 Eisenberg et al (1997, page 623) comment that juries rarely award punitive damages and appear to be reluctant to do so in areas of law th at have captured most attention, products liability and medical malpractice. Punitive damages are most frequently awarded in business/contract cases and intentional tort cases.

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24 defendant, not to compensate the plaintiff.16 As a result, these two reforms are not included as independent variables in the analysis. Instrumentation If indeed non-economic damage caps are e ndogenous, an instrumental variable is required in order to proceed. In this case, a proper instrument for the enactment of a noneconomic damage cap must be unrelated to the un derlying conditions of the health care industry. The political composition of state or federal govern ment is often utilized as an instrumental variable in studies of public policies.17 In my paper, a unique inst rument using state political composition is devised in order to account for the enactment of non-economic damage caps in a particular year.18 Tort reform, and caps on non-economic damage s in particular, are policies typically supported by Republicans. As such, we would expect to find caps in states with more conservative representation. Control in this cont ext is defined as one pa rty controlling the State Senate, the State House, and the Governors Office. If in a pa rticular year, Republicans gain 16 It is also possible that juri es use non-economic damage awards to punish physicians for malpractice infractions beyond any co mpensation for pain and suffering. 17 See, for example, Klick & Stratmann (2003) Rubin & Shepherd (2005), and Sharkey (2005). 18 Several other instruments, TermLimits and MedSchool, were initially attempted in conjunction with RepEver but lacked sufficient power as measured by first stage statistics. Term limits lower the value of holding office and in turn can genera te a lower level of contributions from special interest groups. It is possible that a state with term limits may be less likely to adopt such laws if special interest groups are less likely to try to influence legi slators who have limited tenure. Additionally, states with reputable medical schools may be more likely to support damage caps to protect their prosperous physicia ns from being sued. To capture this idea, the un ion of the top 50 medical schools by research and the top 50 medi cal schools by primary care were used. Both of these potential variables were determined to be weak instruments and were therefore omitted.

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25 control of all three branches, we might expect a non-economic damage cap to be passed in that state. Contemporaneous control, RepCurrent equals 1 if Republicans controlled the Senate, House, and Governors Office in state i in year t If Republicans did not hol d control, that state receives a value of 0 in year t An alternative form of the inst rument involves considering prior values of control, or when a change in politic al composition occurred, rather than simply the state of current control. To capture this idea, the instrumental variable RepEver was created. This instrument equals 1 in the first year in which the Republicans controlled all three branches of state government between 1991 and 2001, and ever y year thereafter. The idea is that once Republicans take control, a cap will be enacted and will persist every year thereafter. A noneconomic damage cap has never been rescinded, so this particular de finition is credible.19 In order for the first stage to be successful, we must have strong correlation between the measure of political composition used and the enactment of the cap. Figure 2-1 i llustrates the relationship among the instrument RepCurrent, the instrument RepEver and the enactment of the damage cap by state. As shown in Figure 2-1, RepEver performs well for seven of the eight states that enacted caps between 1991 and 2001: Alaska, Illinois, Montana, North Dakota, Ohio, South Dakota, and Wisconsin. Illinois, for exampl e, experienced a political shift in 1994 when Republicans took control of the State House, State Senate, and Gove rnors Office. A noneconomic damage cap was enacted in Illinois in 1995. The law adoption almost perfectly coincides with the change in political compositi on. Republican control existed in Illinois during 1994 and 1995, as illustrated by RepCurrent. 19 Several non-economic damage caps have been found unconstitutional. This, however, is not a result of a change in political composition, but ra ther an inherent problem with the construction of the law.

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26 Given that the endogenous vari able is binary, it may be mo re appropriate to use an alternative technique to standard instrumental variables estimation. RepEver assumes that the law was passed when Republicans gained control of st ate government. But the pr obability that a law is in place in a particular year reflects prior probabilities that the law was passed. In other words, a state that has had Republican control for four years would be more likely to have a noneconomic damage cap than a state with Republican control for only one year To take account of this consideration, a binary choice model is utilized.20 This procedure produces valid standard errors21 and more precise estimates. First, a logit m odel is estimated for observations in which a cap has not yet been passed. The dependent variable equals 1 if the cap wa s enacted in that year and 0 if no cap was enacted in that year. Expl anatory variables in the logit model include RepCurrent as well as the four explanatory variables defined previously. Pr edicted probabilities obtained from the logit procedure estimate the pr obability that a cap was adopted in each year given contemporaneous characterist ics. For each state, these pr edicted probabilities can vary over time and are higher when the Republicans co ntrol of state government. These probabilities are then used to construct the cumulative probability that a cap was passed in year t beginning with 1991. For example, the probability of passing a law in year 0 is 0p where 0p is the predicted probability. The probability of not passing a law in year 0, therefore, is 01 p Similarly, the probability of not passing a law in year 1 is 11 p To find the probability of a law at the end of year 1, we must c onsider both year 0 and year 1. Th e probability, therefore, of a law at the end of year 1 is ) 1 )( 1 ( 11 0p p This expression can be restated as 1 0 0) 1 ( p p p 20 See Wooldridge (2002) pa ges 623-625 and Cameron & Trivedi (2005) pages 192-193. 21 Valid standard errors would not be available in the event that the first stage is a binary choice model and the predicted values were th en substituted in the second stage.

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27 meaning that the probability of a law being enacted in year 1 is the probability that it was enacted in year 0 plus the probability that it was enacted in year 1 times the probability that it was not enacted in year 0. If the predicted probabilities of adoption for this state are 0.05 in 1991 (year 0), 0.08 in 1992, and 0.11 in 1993, then the probability of having a cap in 1991 is simply 0.05, while the probability of having a cap in 1992 is 0.13. Usin g the same method, the probability of having a law in 1993 is estimated to be 0.22. The probabil ity of having a cap rises over time, reflecting more years with some prospect of adoption. Th e probability of having a cap is also greater in states in which Republicans have controlled state government for multiple years. This calculation of cumulative probabilities from the predicted probabilities is conducted for the remaining years. In this way, the cumula tive probabilities account for prior influences, including past political compos ition. These cumulative probab ilities are then used as an alternative instrument to RepCurrent and RepEver By construction, the cumulative probabilities rise over time by state and are constrained between 0 and 1. Data Under the requirements of the Health Care Quality Improvement Act ,22 all medical malpractice payments must be reported.23 These individual reports are contained in the National Practitioner Data Bank (NPDB) Public Use File.24 The malpractice portion of this data set is 22 Title IV of Public Law 99-660, Health Care Quality Improvement Act of 1986 23 The Health Care Quality Improvement Act of 1986 imposes civil penalties of up to $11,000 for a failure to report each medical ma lpractice payment, per Section 421(c). 24 National Practitioner Data Bank Public Use File (August 30, 2005), U.S. Department of Health and Human Services, Health Resources a nd Services Administration, Bureau of Health Professionals, Division of Practitioner Data Banks.

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28 relatively complete in the sense that it contai ns all reported medical malpractice payments.25 These data do not contain information on cases filed that resulted in no payment, which would include dismissals, directed verdicts, summary judg ments, and verdicts for the defendant. In my analysis, cases and payments refer to judgments for the plainti ff or settlements. No data set is able to completely represent the total number of malpractice occurrences; however, this data set provides a useful subset. Each record contains information about the pract itioner, such as the work state, home state, license state, license field, ag e group, and year of graduation.26 Specific information regarding the alleged malpractice incident includes the ca use of the malpractice action, year, payment amount, and whether the case was settled or fully litigated. While the dataset is not suitable for some research projects, it is acceptable for my purposes.27 I do not need information on physician fiel d of specialization. Rather, I require a measure of aggregate claims by st ate and by year for my dependent variable, which this dataset 25 Recent controversy exists as to the completene ss of the data bank. If the physician named in the original suit is removed from the final settle ment papers, the payment is not required to be reported. Only payments associated with physicians, not hospitals or insurance companies, are subject to mandatory reporting. Th is loop-hole in the system has been referred to as the corporate shield, and therefore might indicate undercounti ng of settlements in the data bank (Hallinan 2004). 26 The state variable required some necessary assumptions. The database reports three state variables: work state, home state, and license state. However, only the work state or the home state is required, not both Additionally, a practitio ner can be licensed in more than one state. In this data set, only the first state of license list ed is recorded. Work state has been used as the primary measure of a practitioners state; if no work state was reported, then home state was used. If neither home state nor work state wa s provided, then license state was used. 27 Other researchers, e.g., Baicker & Chandra ( 2004) and Matsa (2005), ha ve used the NPDB.

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29 provides. Although the NPDB was not designed as a research t ool, it is perhaps the best nationally collected data set on medical malpractice suits.28 Ultimately, the units of observation in this anal ysis are not at the individual claim level, but rather are a measure of claim frequency per capita. Individual-level data were aggregated to the number of successful suits in a given state, in a given year. Th e NPDB began collecting data at the end of 1990 and, therefore, 1991 is the firs t complete year of data. Observations from 30 states for a period of 11 years, 1991-2001, were cons tructed. Eighteen states that had previously enacted damage caps or total damage caps were removed from the analysis. Ultimately, the sample was reduced further by removing several y ears for two specific states. Ohio and Illinois passed non-economic damage caps between 1991 a nd 2001 and their courts subsequently found them unconstitutional during the same time period. The years following the finding of unconstitutionality for Illinois (1998 and after) and for Ohio ( 1999 and after) are omitted from the analysis. This creates an unbalanced pane l dataset with a total of 324 observations. Identification This analysis uses a specific set of states ove r an eleven-year period. In order to identify the effect of caps on claim frequency, the most appropriate comparison is between states that enacted caps on non-economic damages between 1991 and 2001 and states that did not have damage caps during the relevant time period. Ther e are several ways to categorize the states and therefore, several sets of potential comparis on groups. The analysis was conducted with multiple comparison groups in order to determine whethe r the results are robus t and not conditional on the specific set of states used. 28 Very few states collect detailed data on closed claims. Those that do include Florida, Illinois, Missouri, Minnesota, Massachusetts, Nevada, and Texas, of which only Texas and Florida make their data available for resear ch purposes. See Black (2005).

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30 Table 2-6 describes some specifi c criteria for considering th e remaining potential control states. As previously listed in Table 2-3, the states with recent non-economic damage caps are those in Sets 1 and 2 of Table 2-6. The original analysis is estimated using only those states described in Set 3 of Table 2-6 as comparison states, that is, states that never had non-economic damage caps. This specification excludes states that had non-economic damage caps that were later found unconstitutional prior to 1991. A sec ond specification excludes only states that had caps previously in place, but includes states that may have had caps in the past, but do not have caps now due to laws being f ound unconstitutional (includes Set 4). Since changes in the law occurred in different years for different st ates, it is difficult to illustrate pre and post characteristics. In 1991, how ever, none of the states in the reduced sample ( Sets 1, 2, and 3) had yet adopted a non-economic damage cap. Table 2-7 presents baseline statistics for capped states and noncapped states. As shown in the ta ble, both sets of states look very similar in terms of the obser ved characteristics. We can, theref ore, be fairly confident that the capped and non-capped states are si milar prior to any policy change. Policy Endogeneity Many studies that consider the effect of tort reforms, and in particular non-economic damages caps, fail to account for the fact that such policies were put into effect in a nonrandom fashion. In other words, such policies may have underlying causes that could be correlated with the policy change. This leads to an endogeneity problem that would bias any coefficient estimates of the policy. In order to properly identif y the effect of the policy, we must correct for the endogeneity, but in addition, consider first the potential direction of the bias. If policies are enacted in response to a surge in claim frequenc y due to omitted factors, then we might expect the estimate of the policy change to be biased upwa rds. In other words, if the true effect of a non-

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31 economic damage cap is negative (or zero), such a bias would favor a fi nding of no effect (or a positive effect). At first blush, this explanation may sound reason able. This does not appear to be the case, however, based on the available data. For each of the states which enacted a cap between 1991 and 2001, Table 2-8 displays the percentage cha nge in the number of suits per 100,000 capita between the year in whic h the cap was enacted (0 t) and one year prior (1 t) as well as between 1 t and 2 t. Each state is then compared to th e average percentage change of the set of comparison states (see Set 3 of Table 2-6) for the corre sponding years. The comparison group for each state with a cap is comprised of the same states, but differs according to which years are used, since each capped state has its own specific year zero. The experience of the comparison states is a baseline, so consider the sign of the difference column. The difference illustrates that, relative to the comparison set, th e level of litigation in most capped states was declining somewhat, not spiking, in th e two years prior to the policy change. Between 2 t and 1 t, only three states experienced positive differences. Only Alaska experienced a large change in suits, which is mainly due to the low level of litigation in that state. Between 1 t and 0 t, only two states experienced a positive difference, where one of the two values is close to zero. Overall, it does not app ear that an abnormally high number of suits occurred in the period before the cap for any of the capped st ates relative to the comparison set. It appears that states which enacted non-economic damage cap legislation did not do so in response to surges in claims in the years preced ing the policy change. An alternative explanation for the endogeneity of the caps is the presence of factors which are associ ated with the enactment of a cap that discourage litigation and therefor e would bias claim frequency in the negative

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32 direction. For example, there may be a common perception that medical malpractice cases are filed too often, receive excessive publicized awards, or are often fr ivolous. There may be more of a general backlash due to this pe rception in states enacting caps. This would bias the coefficient down (i.e., more negative). Empirical Results First Stage The estimates obtained from the first stage are displayed in Table 2-9. This table reports several different instrument al variables including (1) RepCurrent (2) RepEver and (3) cumulative probabilities derived from predic ted probabilities from a logit model using RepCurrent. In all three cases, the instrument is a positive and significant predictor of Cap. The important difference among these thr ee specifications is seen in th e first stage statistics: partial R-squared29 and Fstatistic.30 Low F-statistic or partial R-squared statistics indicate the presence of a weak instrument. RepCurrent alone does not appear to be a very strong instrument, with a low F-statistic and partial R-squared. This c ontemporaneous version of control is what has previously appeared in the literature. RepEver provides an improvement over RepCurrent with an F-statistic well above 10 and partial R-square d of approximately 13 percent. The statistics associated with RepEver are consistent with the inform ation provided in Figures 1 -8; RepEver is a strong predictor of Cap.31 Using the predicted cumulative probabilities from the logit model 29 A partial R-squared is defined as the variation in the endogenous variable that is explained by the instrument. In this case, it is the variation in the adoption of non-economic damage caps that is explained by the instrument choice. This statis tic is obtained from the first-stage regression. 30 The standard threshold level for a valid instrument is an F-statistic of greater than 10 (Cameron & Trivedi, 2005). 31 The strength of the instrumental variable RepEver is not conditional on its particular definition of control. Variations of RepEver were utilized to test the pa rticular definition of control: RepEver60 and RepEver2 RepEver60 requires a 60 percent major ity of Republicans in the

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33 with RepCurrent provides even stronger first stage statis tics, with an F-statistic over 75 and a partial R-squared of about 22 percen t. Given the strength of the firs t stage statistics, the predicted cumulative probabilities will be used as the preferred instrument choice in what follows. Second Stage The 2SLS results from estimating Equation (1 ) are displayed in Table 2-10. OLS results are presented in column (1) of this table for comparison purposes. Without accounting for endogeneity, damage caps have a negative and sta tistically significant effect on claim frequency. If non-economic damage caps reduce the incentives to file by reducing the expected benefits of filing a claim, then we might expect to find th is result. Using the OLS estimates, one would conclude that a cap reduces the amount of litigation by about 21 percent. But when the instrument variables procedure is used, the coefficient is no l onger statistically significant. Columns 2 through 5 in Table 2-10 employ the pred icted cumulative probabilities obtained from the logit model as the instrument of choice .32 Table 2-10 also displays the confidence interval around Cap. As seen in column (2), this coefficient is imprecise. The interval ranges from a 25 percent decrease to a 18 pe rcent increase in suits per 100,000 of the population. It is important to note that the lack of statistical significance on the variable Cap is not a result of substantially larger 2SLS standard errors. The remaining coefficients are also presented in column (2). The percent of the population living in a metropolitan area and the unemploymen t rate are not statistically significant. Disposable income per capita also has a sta tistically signifi cant impact on the amount of House, in the Senate, an d a Republican Governor. RepEver2 defines control according to only the State House and Senate, but not the Governor Each of these alternatives provided similar results to using RepEver. 32 Similar results to those presented in Table 7 are obtained when usi ng the other instrument variations, RepCurrent and RepEver

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34 litigation. This negative coe fficient fits our hypothesis. Th e demand for medical care was controlled for using PersonalHealthExpend This variable is highly significant and positive. The coefficient indicates that a one unit increase in PersonalHealthExpend leads to a five percent increase in claim frequency. Several other variants of capped and non-capped st ates were used to estimate equation (1). The results of these alte rnatives are presented in columns (3 ) (5) of Table 2-10. Column (3) uses the same comparison states as Column (2), however, this specification does not omit states that had caps prior to 1991 that were found unc onstitutional before or during 1991. Originally omitted from the analysis, observations for Alabama, New Hampshire, and Washington are included in column (3). The results using this alte rnative set of comparison states are very similar to the results presented in column (2). Column (4) employs the same set of comparison states as column (2) while column (5) uses the comparis on group as column (3), but the years following the findings of unconstitutionality in Ohio and Il linois are not omitted. Again, these results are consistent with those presented in the original model shown in column (2). In all cases, caps were not statistically significant. Caps do not reduce claim frequency. Lags in Suit Duration The dataset used in my study records claims at their date of completi on, whether that date signifies the time of settlement or the time of judgm ent. If caps affect the decision to file, it may be necessary to consider a lag in suits based on several variants in duration. Not only it is possible that there is a lag in the policys eff ectiveness, but there may also be time between the opening and closing of a claim. The previous anal ysis is re-estimated according to Equation (2): it t i it it it s itR S M (2-2)

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35 where s is the lag time, and is defined as either 1, 2, or 3 years. In other words, given a one year lag, a suit that is closed in year t +1, will be explained by year t characteristics, including the status of the states non-economic damage cap policy. Similarly, gi ven a two year lag, a suit that is closed in year t +2 will be explained by year t characteri stics. In this way, this specification accounts for both a lag in policy effectiveness as well as a lag in suit duration. Table 2-11 shows the results from each of these three additional specifications.33 These results use the same set of comparison states and instrument c hoice as column (2) of Table 2-10. Compare the results in Table 2-11 to those in column (2) of Ta ble 2-10. In all three cases, damage caps do not have a statisti cally significant effect on claim frequency. The coefficients on the remaining variables, however, lose precisi on when we introduce additional lags in suits. Alternative Methodology If caps are effective in reducing claim frequency, then th e removal of a cap should increase claim frequency. Thus, an alternative method is to examine claim frequency following the removal of a cap due to unconstitutionality. In several states, previously enacted damage caps were held unconstitutional by the court system.34 This approach exploits a purely exogenous change in the law. A change in the law, impl emented by the court system, is not due to the 33 When estimating models with lagged variab les, the number of observations is typically declines. However, in this case, data from the National Practitioner Data Bank is also available for 2002-2004. Although these years were not used in the original analysis, due to data availability of other covariat es, the number of suits per 100,000 of the population for 2002-2004 are used when considering lags in suit duration. As a result, the number of years of data is not decreased when estimating Equation (2). In addi tion, data for the covariates exists for 1990. When introducing lags in suits, I am able to a dd one year of data (1990), or 30 observations, to the original number of observations. 34 See Table 2-5. Those states which are relevant fo r this portion of the an alysis include Illinois, Ohio, and Oregon. The caps in both Illinois a nd Ohio were found unconstitutional at the end of 1997 and 1999, and are therefore coded as changing in 1998 and 2000, respectively.

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36 underlying factors of the healthcare industry, but rather is based on some problem with the laws construction. It is safe to assume, therefor e, that rulings of unconstitutionality are not endogenous in the same way that the im plementation of caps may be endogenous. As before, we compare two groups of states : states with non-economic damage caps and states whose caps were found unconstituti onal during the relevant time period.35 In this case, states that had caps in place throughout the time period comprise the comparison group. States with caps which were found unconstitutional during th e relevant time period define the treatment group.36 Since each state adopted non-economic damage caps in different years, the number of observations for each state differs. The total number of states in this section of the analysis is 23, and the number of observations is 218. If caps are effective in reduc ing claim frequency, then removing a cap will increase claim frequency, all else equal. To test this hypothesis, the following equation was estimated: it t i it it it ittional unconstitu S M (3) The coefficient on unconstitutional is the parameter of interest and is hypothesized to be positive. All other variables are as defined in Equation (1). The results presented in column (1) of Table 2-12 suggest that caps are not effective at reducing suits. The coefficient is not precisely estimated, and we therefore can not identify an 35 States whose caps were found unconstitutional duri ng the relevant time period include Illinois, Ohio, and Oregon. The relevant comparison states include Alaska, California, Colorado, Hawaii, Idaho, Kansas, Louisiana, Maryland, Massac husetts, Michigan, Missouri, Montana, New Hampshire, New Mexico, North Dakota, S outh Dakota, Texas, Utah, and Wisconsin. 36 Some of these caps were only in effect for severa l years, therefore, there is some question as to how many cases would actually have been a ffected by the caps duri ng the time period. In Illinois, for example, it is more likely that th e cap (effective from 1995-1997) had a larger impact on settlements than on suits that received j udgments. This is because the cap applied to malpractice acts committed after the laws passage. Such suits would need to be resolved (by a judgment or a settlement) before the law was later relaxed.

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37 effect. As tested in the previous section, there may be some time between when a suit is filed and when a suit is closed. To account for this, the analysis was conducted with the same three variations of lag times in suits. The results found in columns (2) (4) of Table 2-12 are robust to these variations. We are unable to identify an effect of removing su ch a cap in any of the models. Using exogenous changes in the la w does not provide any evidence that caps are effective at reducing claim frequency. Robustness Checks and Additional Considerations The lack of statistical signifi cance with respect to caps on cl aim frequency is of crucial policy significance. Thus, I conducted several ro bustness checks using the original models estimated with Equation (1) in this section. Al l robustness checks provi de similar evidence; no effect can be identified between non-econom ic damage caps and claim frequency. Severe Damage Caps For those states that have non-economic dama ge caps, the amount of the cap ranges from approximately $250,000 to $600,000 in nominal terms. Additionally, several states have overall damage cap reforms in place. Overall damage cap s are limits on the total amount a plaintiff can recover at trial economic and non-economic da mages. Caps on overall (total) damages are severe in the sense that they limit economic a nd non-economic components. Initially, states which have caps on overall damages were removed fr om the dataset. These states, which altered their total damage caps during the relevant ti me period, include I ndiana, Nebraska, and Virginia.37 In this section, let SevereCap equal 1 if state i in year t has either a non-economic damage cap or an overall damage cap in place, and 0 otherwise. Additi onally, consider overall damage caps in conjunction with severe non-economic damage caps only (less than $500,000). 37 Indiana changed their cap in 1993, Nebraska ch anged their cap in 1992, and Virginia changed their cap in 1999.

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38 Let this variable be SevereCap2 Using the same instrumental variable procedure described previously, Equation (1) is re-est imated using these two alternatives of the reform variable. The results are consistent with those presented in Tabl e 2-10. We are unable to identify an effect of damage caps on claim frequency. These results are contained in Table 2-13. Additional Considerations One may be concerned that these results are affected by serial correlation. Each observation does not contain enti rely new information about e ach state-level observation. Bertrand, Duflo, and Mullainathan (2004) disc uss the problems of using differences-indifferences (DD) in the presence of serial co rrelation. Serial correlation can produce standards errors that are too small meaning that we would be more likel y to find an effect of a treatment than not. If indeed serial correlati on is a problem in this analysis, it would imply that the standard errors are even larger than in the previous analysis It is, therefore, even more likely that there is no effect of non-economic damage caps in this context. Conclusions It is undeniable that the hea lth care industry is currently facing problems that deserve careful consideration and thoughtful solutions. Am ong the myriad concerns is the frequency of medical malpractice claims. A commonly-offered solution is th e use of non-economic damage caps in medical malpractice litigation as part of a tort reform effort. Over the past 30 years, proponents of tort reform have had some success in persuading state legislatures. Thirty states have enacted and/or modified tort reforms by inco rporating damage caps in an attempt to address health care concerns. Due to the fa ct that these reforms are widespr ead at the state level and that non-economic damage caps are being proposed at the national level, it is essential that policy makers understand the true effects of such reforms.

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39 To analyze this issue, I util ize two different approaches. Fi rst, I treat caps as endogenous using a unique instrument of political control. Th is novel approach should be of value to studies that consider the impact of public policies. The literature has used contemporaneous political measures as instrumental variables for the enact ment of public policies. My paper, however, recognizes that laws are sticky and that the probability that a law is in place hinges upon probabilities that the law was enacted in prior ye ars. I calculate cumulative probabilities using predicted probabilities of enac ting a cap obtained from a logit model. Using the cumulative probabilities as an instrument for the enactment of a damage cap yields strong first stage results. In the 2SLS estimates, I find no evidence to suggest that non-economic damage caps are effective in reducing medical malpractice claim fre quency. This finding is robust to a variety of additional specifications, includi ng different instruments and a lternative sets of comparison groups. Second, I exploit exogenous changes in th e law, when state courts find damage cap legislation to be unconstitutional. Again, I can identify no effect between caps and claim frequency. Since caps are ostensib ly intended to reduce claim fre quency, this particular tort reform strategy may be misguided.

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40 Table 2-1. Summary statistics of variables* Variable Mean Standard Deviation Median Minimum Maximum Ln(Suits) 1.70 0.42 1.69 0.53 2.69 Suitsper100Capita 6.02 2.67 5.40 1.70 14.8 IncomePerCapita 17,857 2,572 17,610 12,525 26,375 Metro 64.05 22.89 67.83 23.50 100.00 PersonalHealthExpend 12.13 2.00 12.31 6.16 16.64 Unempl 5.17 1.44 5.08 2.24 9.23 Cap 0.142 0.350 0 0 1 *This table contains observations for all states which enacted non-economic damage caps during the relevant time period and states which never had non -economic damage caps. These statistics include 30 states over 11 years (330 observations).

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41 Table 2-2: Data sources Data Source Information Disposable Income per Capita (real) Bureau of Economic Analysis (BEA), www.bea.gov Consumer Price Index The Econom ic Report of the President, 2004 Percent of Population Living in Metropolitan Areas Statistical Abstract of the United States, National Data Book (Note: These data are reported every other year and required interpolation for the remaining years) Personal Health Care Expenditures (as a percent of GSP) Centers for Medicare and Medicaid Services, www.cms.hhs.gov Unemployment Rate Bureau of Labor Statistics (BLS), www.bls.gov Population Census Bureau, www.census.gov Non-economic Damage Caps No one source provi des accurate data on the status, date of enactment, date of change, or amount of caps. A number of sources were used. These include (but are not limited to) the following: (1) American Tort Reform Association (ATRA), Medical Liability Reform, http://www.atra.org/show/7338 (2) ATRA Tort Reform Record, December 31, 2003. www.atra.org (3) Center for Justice and Democracy, www.centerjd.org (4) National Conference of State Legislatures, State Medical Liability Laws Table, http://www.ncsl.org/programs/insur/medliability.pdf (5) McCullough, Campbell & Lane, Summary of Medical Malpractice Law, www.mcandl.com Political Control Data (1) Book of the States (2) Statistical Abstract of the United States, National Data Book Term Limits Book of the States, 2002 Medical School Rankings U.S. News & World Reports, Americas Best Graduate Schools 2006 Top Medical Schools Primary Care and Top Medical Schools Research

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42 Table 2-3. States enacting non-ec onomic damage reforms (1991-2001) Some state courts found non-economic damage ca ps unconstitutional. Illinois held the cap unconstitutional in 1997 while Ohio he ld the cap unconstitutional in 1999. See Best v. Taylor Mach. Works 689 NE 2d. 1057 (1997) and State ex rel. Ohio Academy of Trial Lawyers v. Sheward, 86 Ohio St. 3d 451 (1999), respectively. State Year Nominal Amount ($) Alaska 1997 $400,000 Illinois 1995 $500,000 Montana 1995 $250,000 New Mexico 1992 $600,000 North Dakota 1995 $500,000 Ohio 1997 $250,000 South Dakota 1997 $500,000 Wisconsin 1995 $350,000

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43 Table 2-4. State limits on damages State Year Amount Description Alabama 1987 $400,000 Non-economic damage cap; Held unconstitutional in 1991. Alaska 1997 $400,000 Non-economic damage cap. Arizona ---Arkansas ---California 1975 $250,000 Noneconomic damage cap. Colorado 1988 $250,000 Noneconomic damage cap. Connecticut ---Delaware ---Florida 2003 $500,000 Non-economic damage cap for single practitioner (($1 million for multiple practitioners). Georgia ---Hawaii 1986 $375,000 Non-ec onomic damage cap. Idaho 1987 $400,000 Non-ec onomic damage cap. 2003 $250,000 Non-economic damage cap. Indiana 1993 $1.25 mil Overall (total) damage cap. Illinois 1995 $500,000 Non-economic damage cap; Held unconstitutional in 1997. Iowa ---Kansas 1988 $250,000 Non-economic damage cap. Kentucky ---Louisiana 1975 $500,000 Cap on all damages, exclusive of future medical expenses and related benefits. Maine ---Maryland 1986 $350,000 Noneconomic damage cap. 1994 $500,000 Increased by $15,000 every year thereafter. Massachusetts 1986 $500,000 Non-economic damage cap. Michigan* 1986 $225,000 Noneconomic damage cap. 1993 $280,000 Non-economic damage cap (or $500,000 under extreme circumstances). Minnesota 1986 $400,000 Non-economic damage cap, but does not apply to pain & suffering damages. Mississippi 2003 $500,000 Non-economic damage cap. Missouri* 1986 $350,000 Noneconomic damage cap. Montana 1995 $250,000 Non-economic damage cap. Nebraska 1992 $1.75 mil Overall (total) damage cap. Nevada 2002 $350,000 Noneconomic damage cap. New Hampshire 1986 $875,000 Non-economic damage cap; held unconstitutional in 1991. New Jersey ----

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44 Table 2-4. State limits on damages (continued) State Year Amount Description New Mexico 1992 $600,000 Total damage cap, but does not include punitive or future medical expenses and related benefits. New York ---North Carolina ---North Dakota 1995 $500,000 Non-economic damage cap. 2003 $350,000 Non-economic damage cap. Ohio 1997 $250,000 Non-economic damage cap (or $500,000 under extreme circumstances); held unconstitutional in 1999. Oklahoma 2003 $350,000 Non-economic damage cap (applies to pregnancy and emergency care only). Oregon 1987 $500,000 Non-economic damage cap; held unconstitutional in 1999. Pennsylvania ---Rhode Island ---South Carolina ---South Dakota 1997 $500,000 N on-economic damage cap. Tennessee ---Texas 1977 $500,000 Non-economic damage cap; applies only to wrongful death actions. Utah* 1986 $250,000 Non-ec onomic damage cap. 2001 $400,000 Non-economic damage cap. Vermont ---Virginia 1999 $1.5 mil Overall (total) damage cap. Washington ---West Virginia 1986 $1 mil Non-economic damage cap. Wisconsin* 1995 $350,000 N on-economic damage cap. Wyoming ---*Limits on damages are adjusted for inflation.

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45 Table 2-5. Non-economic damage caps held unconstitutional State Year Enacted Year Unconstitutional Amount Alabama 1987 1991 $400,000 Illinois 1995 1997 $500,000 Ohio* 1997 1999 $500,000 ($250,000 if less severe) New Hampshire 1976, 1986 1980,1991 $875,000 Minnesota 1986 1990 $400,000 Oregon 1987 1999 $500,000 Washington 1986 1989 43% wage *life expectancy *Ohio re-enacted a cap in 2003, however, this does not apply to the data used in this analysis.

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46 Table 2-6. Description of categories of states Set No. Criteria States 1 6 States which enacted non-economic damage caps and they were not found unconstitutional. AK, MT, NM, ND,SD, WI 2 2 States which enacted non-economic damage caps between 1991-2001, but whose caps were found unconstitutional between 19912001. IL,OH 3 22 State which never had damage caps during the relevant time period. AR, AK, CT, DE, FL, GA, IA, KY, ME, MN, MS, NV, NJ, NY, NC, OK, PA, RI, SC, TN, VT, WY 4 3 States which had non-economic damage caps in place prior to 1991, where these caps were found unconstitutional before/during 1991. AL, NH, WA 5 13 States which had non-economic damage caps in place prior to 1991, where these caps are still in effect. CA, CO, HI, ID, KS, LA, MD, MA, MI, MO, TX, UT, WV 6 1 States which had non-economic damage caps in place prior to 1991, where the cap was found unconstitutional between 1991-2001. OR 7 3 States with caps on total damages. IN, NE, VA

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47 Table 2-7. Baseline statistics (1991) States with Caps States without Caps (8 states) (22 states) Variable Average Standard Deviation Average Standard Deviation Ln(Suits) 1.84 0.42 1.68 0.43 Suitsper100 6.8 2.54 5.90 2.70 Metro 54.08 221.6 67.13 23.5 IncomePerCapita 16,408 2,252 16,870 2,620 Unempl 6.25 1.71 6.58 1.10 PersonalHealthExpend 11.63 2.64 11.66 1.96

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48 Table 2-8. Change in suits between year t-2 and t-1; t-1 and t=0 States with Caps States without Caps State Percent Change from t -2 to t -1 Percent Change from t -2 to t -1 Difference Alaska 70.26% 4.76% 65.49% Illinois -14.05% 3.58% -17.63% Montana 14.68% 3.58% 11.10% New Mexico North Dakota 11.87% 2.08% 9.80% Ohio 1.98% 4.76% -2.79% South Dakota -3.19% 4.76% -7.96% Wisconsin -11.63% 3.58% -15.20% States with Caps States without Caps State Percent Change from t -1 to t =0 Percent Change from t -1 to t =0 Difference Alaska -44.84% -1.49% -43.35% Illinois -18.36% -11.72% -6.64% Montana -23.72% -11.72% -12.00% New Mexico -5.02% 6.16% -11.18% North Dakota -28.12% -11.72% -16.39% Ohio -8.70% -1.49% -7.21% South Dakota -0.27% -1.49% 1.22% Wisconsin 12.30% -11.72% 24.03%

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49 Table 2-9. First stage results (1) (2) (3) IV= RepCurrent IV= RepEver IV= Cumulative Probabilities Variable Name Cap Cap Cap IncomePerCapita -0.00006 -0.00002 -0.000089 [0.00004] [0.00004] (0.000036)** Metro 0.0192 0.019 -0.0254 [0.0136] [0.0128] (0.0132)* Unempl 0.0586 0.0596 0.0286 [0.0236]** [0.0221]*** -0.0214 PersonalHealthExpend 0.0356 0.0506 0.0301 [0.0242] [0.0229]** -0.0217 Instrument 0.1133 0.3341 1.4359 [0.0485]** [0.0507]*** (0.1637)*** Observations 324 324 324 Number of States 30 30 30 R-squared 0.67 0.71 0.74 State Fixed Effects Yes Yes Yes Year Fixed Effects Yes Yes Yes First Stage Statistics F-statistic 5.46 43.50 76.98 Partial R-squared 0.0192 0.1349 0.2162 Standard errors in parentheses significant at 10%; ** significant at 5%; *** significant at 1% First stage results were obtained using ordinary least squares (OLS) estimation.

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50 Table 2-10. Ordinary least squares (OLS) a nd two-stage least squares (2SLS) results (1) (2) (3) (4) (5) OLS 2SLS 2SLS 2SLS 2SLS IV= Cumulative Probabilities IV= Cumulative Probabilities IV= Cumulative Probabilities IV= Cumulative Probabilities Variable Name Ln(Suits) Ln(Suits ) Ln(Suits) Ln(Suits) Ln(Suits) IncomePerCapita -0.000081 -0.00007 -0.00007 -0.00007 -0.00007 [0.000034]** [0.00004]* [0.00003]** [0.00004]* [0.000033]** Metro 0.0166 0.0104 0.0112 0.0102 0.0111 [0.0117] [0.0115] [0.0113] [0.0115] [0.0112] Unempl -0.0281 -0.0315 -0.0314 -0.0329 -0.0325 [0.0203] [0.0236] [0.0212] [0.0236] [0.0212] PersonalHealthExpend 0.0586 0.052 0.0446 0.0545 0.0474 [0.0208]*** [0.0200]*** [0.0196]** [0.0202]*** [0.0197]** Cap -0.2106 -0.0366 -0.0538 -0.0248 -0.0453 [0.0506]*** [0.1096] [0.1064] [0.1134] [0.1104] Observations 324 324 357 330 363 Number of States 30 30 33 30 33 R-squared 0.83 0.85 0.86 0.84 0.86 State Fixed Effects Yes Yes Yes Yes Yes Year Fixed Effects Yes Yes Yes Yes Yes First Stage Statistics F-statistic 76.98 85.45 65.27 71.82 Partial R-squared 0.2162 0.2166 0.1863 0.1857 Confidence Intervals Cap (-0.2777, -0.0890) (-0.2523, 0.1792) (-0.2631, 0.1555) (-0.2479, 0.1984) (-0.2625, 0.1719) Robust standard errors in parentheses *significant at 10%; ** significant at 5%; *** significant at 1% Columns (1) and (2) present the results of Equati on (1) omitting states (20) which had caps before 1991 (and still have caps today), states which had caps befo re 1991 which were found unconstitutional, and states which have caps on total damages. The years after the Ohio and Illinois caps were found unconstitutional are also omitted. Column (3) omits the same states as in column (2), but includes observations for Alabama, New Hampshire, and Washington. These are states whose caps were found unconstitutional before or during 1991, and therefore do not have caps during the relevant time period. Column (4) contains the same set of states as columns (1) and (2), but does not omit the years following the findings of unconstitutionality for Ohio and Illinois. Column (5) contains the same set of states as column (3), but does not omit the years following the findings of unconstitutionality for Ohio and Illinois.

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51 Table 2-11. 2SLS results variants of duration* (1) (2) (3) One Year Lag Two Year Lag Three Year Lag Variable Name Ln(Suits) Ln(Suits) Ln(Suits) IncomePerCapita -0.00004 -0.00002 -0.00004 [0.00004] [0.00003] [0.00003] Metro 0.0144 0.0035 -0.0094 [0.0097] [0.0083] [0.0102] Unempl -0.0063 0.0149 -0.0009 [0.0205] [0.0198] [0.0179] PersonalHealthExpend 0.035 0.0027 -0.0154 [0.0197]* [0.0185] [0.0181] Cap -0.0279 0.0276 -0.0375 [0.0990] [0.0991] [0.0927] Observations 354 354 354 Number of States 30 30 30 R-squared 0.83 0.83 0.83 State Fixed Effects Yes Yes Yes Year Fixed Effects Yes Yes Yes First Stage Statistics F-statistic 76.44 76.44 76.44 Partial R-squared 0.1988 0.1988 0.1988 Robust standard errors in parentheses significant at 10%; ** significant at 5%; *** significant at 1% *The control states in this table correspond to the initial specification of control states used in column (2) of Table 6.

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52 Table 2-12. OLS results using unconstitutionality of caps* (1) (2) (3) (4) No Lag One Year Lag Two Year Lag Three Year Lag Variable Name Ln(Suits) Ln (Suits) Ln(Suits) Ln(Suits) IncomePerCapita -0.00014 -0.00006 0.00002 0.00005 (0.000029)** (0.000035)* -0.000038 -0.000033 Metro 0.0147 0.0119 0.0043 -0.0096 (0.0089) (0.0080) (0.0069) (0.0107) Unempl -0.0187 0.0155 0.0118 0.0338 (0.0218) (0.0181) (0.0145) (0.0154)** PersonalHealthExpend 0.0662 0.0292 0.0883 0.0789 (0.0446) (0.0328) (0.0340)** (0.0323)** Unconstitutional -0.0319 -0.0511 -0.0641 0.0131 (0.0649) (0.0646) (0.0709) (0.0660) Observations 218 221 232 232 R-squared 0.82 0.83 0.83 0.83 State Fixed Effects Yes Yes Yes Yes Year Fixed Effects Yes Yes Yes Yes Robust standard errors in parentheses significant at 10%; ** significant at 5%; *** significant at 1%

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53 Table 2-13. Results for severe cap. (1) (2) 2SLS 2SLS Ln(Suits) Ln(Suits) Variable Name SevereCap SevereCap2 RealPCdispos -0.00006 -0.00007 (0.00004)* (0.00004)* Metro 0.0148 0.0144 (0.0114) (0.0110) Unempl -0.038 -0.0398 (0.0214)* (0.0210)* PersonalHealthExpend 0.063 0.0631 (0.0201)*** (0.0201)*** Cap -0.0482 -0.0919 (0.1072) (0.2013) Observations 346 346 Number of States 32 32 R-squared 0.85 0.85 State Fixed Effects Yes Yes Year Fixed Effects Yes Yes First Stage Statistics F statistic 76.75 27.84 Partial R-squared 0.2043 0.0852 Robust standard errors in parentheses significant at 10%; ** significant at 5%; *** significant at 1%

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54 Cap 0 1 1991 1993 1995 1997 1999 2001 year RepEverRepCurrentFigure 1 Alaska Cap 0 1 1991 1993 1995 1997 1999 2001 year RepEverRepCurrentFigure 2 Illinois Cap 0 1 1991 1993 1995 1997 1999 2001 year RepEverRepCurrentFigure 3 Montana Cap 0 1 1991 1993 1995 1997 1999 2001 year RepEverRepCurrentFigure 4 New Mexico Cap 0 1 1991 1993 1995 1997 1999 2001 year RepEverRepCurrentFigure 5 North Dakota Cap 0 1 1991 1993 1995 1997 1999 2001 year RepEverRepCurrentFigure 6 Ohio Cap 0 1 1991 1993 1995 1997 1999 2001 year RepEverRepCurrentFigure 7 South Dakota Cap 0 1 1991 1993 1995 1997 1999 2001 year RepEverRepCurrentFigure 8 Wisconsin Figure 2-1. Description of enactment of cap and change in political composition

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55 CHAPTER 3 THE EFFECTS OF INCREASED ACCESS TO THE MORNNG-AFTER PILL ON ABORTION AND STD RATES Introduction Over six million pregnancies occur each year in the United States: three million are unintended and over one million are terminated by abortion.38 Some of these unintended pregnancies could be prevented and the corres ponding abortions avoided with easier access to emergency contraception. Emergency contraception, also known as the morning-after pill or Plan B, is a type of birth control th at can be taken up to 72 hours afte r sexual activity th at can prevent a pregnancy from occurring. On August 24, 2006, the FDA approved sales of emergency contraception through pharmacists without a pr escription for individuals age 18 and older.39 This approval follows a previous rejection by the FDA of a proposal that would have allowed emergency contraception to be available ove r-the-counter without an age restriction.40 In its earlier rejection, the FDA pointed to potential misuse by teenage girls, who would be able to purchase the product without a doctors supervis ion. The recent decision restricts access to women over the age of 18, there by alleviating this particular concern. Those who oppose easier access raised concerns that overthe-counter access could lead to increased sexual activity.41 Pharmacy access to emergency contraception was an approach first adopted in the U.S. by the State of Washington. In 1997, Washingt on began a pilot program to expand access to emergency contraception through pharmacies. Enabling pharmacy provision dramatically changes the accessibility of emergency contr aception. Pharmacy access facilitates faster 38 Contraception Counts March 2006, Alan Gu ttmacher Institute, www.guttmacher.org 39 Harris (August 25, 2006). 40 CBS News, May 6, 2004. 41 CBS News, June 11, 2006.

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56 provision of the medication because there are no appointment delays with a doctor. Moreover, it provides evening and weekend access. Since 1997, eight states have followed Washingtons lead, adopting similar initiatives allowing pharm acists to dispense emergency contraception without a prescription.42 Eight additional state legislatures ha ve introduced similar legislation, but failed to pass it, while two othe r bills are still under consideration.43 By studying the effects of the program in Washington, we can gain an understanding of how pharmacy access may affect the rest of the country in the future. Focusing on Washington, the first state to change access, utilizes the most post-implementation years. Ad ditionally, although eight other states have since implemented similar initiatives, many of these laws were passed quite recently. Increased accessibility to emergency contracep tion reduces the expected costs of engaging in sexual activity. If a pregnancy is possible, wh ether due to contracep tive failure or unsafe sexual activity, use of emergency contrace ption can prevent an unwanted pregnancy. Additionally, emergency contracepti on may be more ethically appea ling in that it works like oral contraceptives to prevent a pregnancy from o ccurring rather than terminating an existing pregnancy. If emergency contracepti on is used as a substitute fo r a subsequent abortion, then abortion rates could decline. If individuals recogn ize that the costs associated with engaging in risky sexual behavior ar e lower, however, then these individuals may enjoy greater risk taking. If indeed increased access to emergency contracep tion increases the amount of sexual behavior, it is possible that sexually transmitted disease (STD ) rates will also increase as a result. 42 These states include Alaska, California, Ha waii, Maine, Massachus etts, New Mexico, New Hampshire, and Vermont. 43 Proposals failed in Colorado, Kentucky, Illinois, Maryland, Oregon, Texas, Virginia, and West Virginia. Proposals are still in progress in Ne w Jersey and New York, although similar proposals in these states have prev iously failed to pass ( http://www.go2ec.org/Legislation.htm ).

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57 In my paper, I consider the intended and uni ntended consequences of increased access to emergency contraception. Using county-level data on Chlamydia rates and abortion rates as well as dates of pharmacy participation, I estimate th e treatment effect, if a ny, of pharmacy access to emergency contraception on several outcomes. The results indicate that pharmacy access is associated with an increase in Chlamydia rates, both overall and for females, and is associated with a decrease in abortion rates for some age groups. This result is robu st to the use of an alternative comparison group as well as alternative definitions of treatment. My paper contributes to the existing literature by exploiting a differe nce-in-difference methodology to consider the impact of pharmacy access to emergency contraception. Although difference-in-difference estimates could suffer from selection bias due to individual pharmacist or pharmacy participation decisions I show that the treatment and control groups ar e statistically indistinguishable in terms of Chlamydia rate s. Although the treatment and control groups are statistically distinguishable in terms of abortion rates, sele ction would bias the estimates upwards, i.e., in favor of finding no effect. My esti mates, therefore, are conservative estimates of the relationship between pharmacy access and abortion rates. Previous Literature Economic models generally assume that individuals respond to economic and policyrelated factors. Economic models related to ri sky behavior are no exception. Empirical evidence suggests, however, that this is often, but not always the case. In cont rast, non-economic models of risky behavior often assert that individuals, and teens especially, make decisions in a more spontaneous or random fashion. This section pr ovides an overview of the economic literature on risky sexual behavior and its potential consequences, as well as reviews some related medical studies.

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58 An extensive literature exists on the effects of various publ ic policies on risky behavior and the potential consequences. There is much le ss literature, however, on risky sexual behavior. For present purposes, the most re levant literature involves those papers which focus on the increased accessibility and availability of fam ily planning services or emergency contraception on outcomes such as pregnancy, abortion, and ST Ds. Paton (2002) considers the impact of the increased provision of family planning servic es in England on undera ge conceptions and abortions. He finds no evidence that increased attendance at family planning clinics reduces teen pregnancy or abortion. Additionally, he consid ers the impact of a court ruling, which for approximately one year barred family planning se rvices from being offered to women under the age of 16 without parental consent.44 A reduction in the accessibility to family planning services should affect this age group differently than those aged 16-19 (who were unaffected by the ruling). Paton, however, found no evidence that these two groups experienced different conception or abortion rates. In another study, Paton (2006) finds no effect of the provision of emergency contraception at family planning cl inics on abortion rates. The author, however, identifies a positive effect on STD rates. Finally Girma and Paton (2006) find no effect of free access to over-the-counter emergency contracepti on on teen pregnancy rates using a matching estimator approach. All three of these pa pers use regional data from England. Several medical papers exploit randomized control trials to examine the impact of emergency contraception or family planning se rvices on a variety of outcome measures. The initial sample selection of women, however, may be problematic in these studies. In Raine et al, (2005), for example, a randomized control trial wa s administered in California between July 2001 and June 2003. Their initial sample, however included women aged 15-24, who had been 44 The ruling was the Gillick ruling in Decem ber 1984; it was later overturned in 1985.

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59 sexually active in the last 6 months, who could pa rticipate in a follow-up visit 6 months later, and who were already attending the family pla nning clinic. Women were randomized into three groups of emergency contraception access: (1) a dvanced provision, (2) pharmacy access, and (3) clinic access. The administrators of the tria l, however, eliminated Group (3) in December 2001 because the California legislature passed pharmacy access legislation. The majority of the study, therefore, compared Group (1) to Group (2). Gi ven the high level of access in both groups, we may not expect to find a differe nce in abortion or STD inciden ce between Groups (1) and (2). Utilizing group (3) gives a base line of traditional access fo r comparison purposes. The study found no evidence that Groups (1) and (2) were diffe rent in terms of pregnancy or STD rates. Several other studies have used similar randomi zation procedures, but fa il to find any difference in abortion, pregnancy, or STD rates. The evid ence, however, is consistent in showing that advanced provision of emergency contraception does increase its use. 45 A somewhat separate literature examines the effects of various policies on state-level STD rates. Such policies affect the costs and benefits of engaging in risky behavior and may in turn affect sexual outcomes. Sen (2003a) and similarly Se n (2003b) consider the effect of restrictions on Medicaid funding for abortions on risky sexu al behavior, measured by state-level gonorrhea rates.46 Increased restrictions on Medi caid funding for abortions increa se the price of abortions to individuals who would otherwise re ly on Medicaid payment. If the price of an abortion increases, we would expect individuals to engage in le ss risky sexual behavior because an unintended pregnancy would be more costly. This should lead to a reduction in sexual activity, which could 45 Glasier and Baird (1998), Falk et al (2001), and Glas ier et al (2004). 46 Several studies have considered state-level Medicaid funding re strictions, but have focused on abortions, pregnancies, and birt hs as the outcome measures. Th e results are these papers are consistent; increases in the price of abortion decreases the demand for abortion. See Blank, George, and London (1996), Hass-Wilson (1996), and Levine, Trainor, and Zimmerman (1996).

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60 be reflected in lower STD rates. In both papers using slightly different panel data techniques, Sen is unable to identify an effect of Medicaid funding re strictions on gonorrhea rates. In contrast to Sens restriction in aborti on access, Klick and Stratmann (2003) analyze the exogenous change of abortion le galization on risky behavior m easured by state-level gonorrhea and syphilis rates. If abortion lowers the co st of engaging in sexual activity by providing insurance in the event of a pr egnancy, then the legalization of abortion could increase risky behavior and therefore STD rates. Klick and Stratmann find that STD rates increased as a result of abortion legalization, c onfirming this hypothesis. Many researchers have studied the relations hip between alcohol or substance use and sexual behavior and its potential consequences.47 Although previous lite rature has positively linked alcohol consumption to sexual behavior,48 the identification strategies used are questionable because substance abuse and sexua l decisions are dependent upon a common set of unobservable personal factors.49 Other studies consider public po licies targeted at alcohol or drugs. Restrictive alcohol policies, such as higher taxes on alcohol or stricter drunk driving laws, have the potential to reduce alcohol consumption which coul d in turn reduce risky sexual 47 See, for example, Sen (2003) who studies the effect of beer taxes on teen abortion rates, finding a small but statistically signifi cant negative effect on abortion rates. 48 See, for example, Graves & Leigh (1995). 49 Two specific studies attempt to correct for this omitted variable problem by employing instrumental variables approaches. Rees et al (2 001) find that the link between substance use and sexual activity is weaker than prev iously suggested in the literatur e. In contrast, Sen (2002) finds that substance use increases the probability of engaging in sexual activity. Rashad and Kaestner (2004), however, discuss the pitfalls of these identification strategies suggesting that the relationship between substance abuse and sexual behavior is still uncertain. As with most instrumental variables approaches, the success of the identification strategy lies heavily in the exogeneity and correlation of the instruments; th ese two criteria are que stioned in both papers.

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61 behavior.50 Chesson et al (2000) use stat e-level panel data to consid er the impact of liquor and beer taxes on STD rates. The authors find that an increase in either tax is associated with a reduction in gonorrhea and syphilis rates. Grossman et al (2004) consider the impact of alcohol taxes as well as drunk driving la ws on the incidence of gonorrhea.51 Similar to Chesson et al, the authors find that more restrictiv e alcohol policies have a negativ e effect on gonorrhea rates, but this result is only statistically significant for males. In a similar paper, Carpenter (2005) examines the impact of Zero Tolerance Laws on state-level gonorrhea rates. He finds that the adoption of a Zero Tolerance polic y has a negative effect on gonorrh ea rates, but this effect is only significant for males between the ages of 15 and 19. My paper joins a small literature focusing on the effects of emergency contraception and other family planning services on abortion rates and STD rates. Th e main papers in the economic literature discussed previously (Paton (2002), Pa ton (2006), and Girma and Paton (2006)) present findings from England. However, England experi ences much lower rates of teen pregnancy, abortion, and sexually-transmitted disease than the United States.52 In the economic literature, this paper is the first to consider the Amer ican experience of pharmacy access to emergency contraception. I utilize a differen ce-in-difference approach by e xploiting the similarities between the treatment and control groups before the program began. Using the differences across 50 More restrictive alcohol polic ies could also reduce abortions through a decrease in risky behavior. Sen (2003) finds eviden ce that higher beer taxes ar e associated with small but statistically significant reductions in teen abortion rates. 51 Chesson et al use a panel data framework with a lagged dependent variab le and fixed effects. Estimation in this way is inconsistent because of the endogeneity of the lagged dependent variable. Grossman et al improve on this sp ecification by accounting for the endogeneity and implementing FD2SLS with subs equent lagged dependent va riables as instruments. 52 Darroch, Singh, & Frost (2001).

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62 participating and nonparticipati ng counties as well as timing of participation, I estimate a treatment effect of pharmacy acce ss on several outcome measures. The Relative Costs of Sexual Activity We generally assume that individuals behave rationally, taking account of the costs and benefits of engaging in a particular behavior. Th ere is some debate as to whether individuals, especially teens, make sexual decisions rationa lly or make such decisions in a more random fashion.53 Levine (2000) finds evidence suggesting that individuals beha ve rationally with respect to sexual decisions, that is, they respond to incentives or to change s in costs and benefits. His results indicate that individu als respond to specific changes in costs and benefits, such as changes in labor market conditions, abortion acce ss, welfare benefits, and AIDS prevalence. In particular, my paper focuses on individual responses to change s in costs. If the cost of an activity (sexual behavior, for example) increase s, we would expect the associated behavior to decrease simply because the costs are higher and may not outweigh the benefits for some individuals. If, however, indivi duals make sexual decisions in a random fashion, i.e., fail to weigh the costs and benefits of a particular decisi on, then changes in the costs of sexual activity or its potential consequences may have no effect on sexual behavior. Increased access and awareness of emergency c ontraception represents a decrease in the cost of engaging in sexual behavior. Emergency contraception decreases the potential costs of engaging in sexual activity, because it can elim inate a potential pregnancy before it actually occurs. This may forgo possible moral dilemmas that arise with abortio n decisions. We would expect, therefore, that changes in the costs as sociated with engaging in risky sexual behavior affect the amount of sexual activity. If the cost s associated with engagi ng in sexual activity, or 53 Paton (2006).

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63 the costs associated with a potential pregnancy, decrease, then we woul d expect the amount of this behavior to increase. This could be reflecte d in an increase in the rate of sexually transmitted diseases. Pharmacy Access to Emergency Contraception History of Emergency Contraception In 1997, the FDA approved the use of certain oral contraceptive pills for use as emergency contraception, although they had been used on an off-label basis for years. As demonstrated by Albert Yuzpe in 1974, use of or al contraceptives in sp ecific dosages after a sexual encounter can be used as a safe and e ffective method of preventing pregnancy. This method, known as the Yuzpe method, is the basis for todays morning-after pill. Preven, the first emergency contraception on the market, was appr oved by the FDA in 1998 and is modeled after the Yuzpe regimen. Two tablets are taken initially and then followed by two additional tablets 12 hours later. Plan B, a progestin-only produc t, was approved in 1999 and is now the only emergency contraception on the market. 54 The Washington State Pilot Project Pharmacists in Washington State have been ab le to form collaborative agreements with physicians since 1979.55 A collaborative agreement grants a ph armacist the ability to dispense a prescription medication, within a specified prot ocol, without a physician s prescription. Outlined in the agreement is the particular medication, th e criteria for who is eligible to receive the medication, and the process of review regard ing pharmacist decisions by the prescriber. 54 Preven was discontinued by its manuf acturer, Barr Laboratories, in 2004. 55 RCW 18.64.011. Originally, collaborative agre ements were filed according to individual pharmacies, with a primary responsible pharmacist named on the agreement. After the fall of 2003, the Board of Pharmacy began recordi ng collaborative agreements by individual pharmacist.

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64 Collaborative agreements have been used succe ssfully in Washington with other medications, and are also common in other states.56 Currently, eight other states have similar initiatives. A Washington State report estimated that 53 percent of pregnancie s in Washington in 1997 were unintended.57 At that time, emergency contraception was available only through a physician. Not only were many wo men unfamiliar with emergency c ontraception, but health care professionals rarely discussed emergency contracep tion with their patients. As a result of these concerns, the Emergency Contraception Collaborat ive Agreement Pilot Project was initiated in July of 1997. The program was the first of its ki nd to enable pharmacists to directly dispense emergency contraception without a prescription. Th is is, however, distinctly different from an over-the-counter designation. The main goal of the program was to reduce unintended pregnancies in Washington through increased access to and awareness of emergency contraception.58 Participants included the Washington Board of Pharmacy, Washington State Pharmacy Association, University of Washingt on Department of Pharm acy, and an organization called PATH (Program for Appropriate Techno logy in Health). Funding was provided by the David and Lucile Packard Foundation, while medi a coverage was handled by Eglin DDB Seattle. The planning phase of the program began in July of 1997, while the majority of the program activities occurred dur ing the 16-month period between February 1998 and June 1999. The pilot program encouraged Washington pharmaci sts to form collaborative agreements with respect to emergency contraception. Pharmacies c ontinued to file for access well after the official 56 Collaborative agreements have been used with respect to other medications such as immunizations, asthma therapy, diabetes screeni ng, cholesterol screening, and chronic disease management (Gardner et al). 57 County Profiles, Birth and Unintended Pregnancy Statisti cs: February 2001, Washington State Department of Social and Health Services. 58 Gardner et al. (2001).

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65 program ended. Once a pharmacist forms such an agreement with a physician, the agreement is submitted to and approved by the State Board of Pharmacy.59 Agreements were initially valid until 2001 and then required a rene wal every two years thereafter.60 Information about emergency contraception was sent to Washingt on state pharmacists, including a list of willing physician and nurse practitioner prescribers and a template collaborative agreement.61 In order to file a collaborative agreement with the Board of Pharmacy, each pharmacist must first participate in a training session. These sessi ons included training in not only patient care and appropriate provision of the medication, but also providing referral informati on, talking with parents if necessary, and counseling on futu re contraceptive decisions. To be effective, emergency contraception must be taken within 72 hours of sexual activity, and even then, is most effective if taken within the first 24 hours.62 If taken within 72 hours, emergency contraception can reduce the chance of pregnancy by 89 percent.63 Prior to dispensing emergency contraception, the pharmaci st performs a brief consultation with the patient to rule out poten tial existing pregnancy.64 If necessary, the patient is referred to a primary care physician or other hea lth care professional. 59 The agreements were initially made between pharmacy and physician, rather than between pharmacist and physician. This recently ch anged and now the agreements are between pharmacist and physician. 60 Gardner et al (2001). 61 Downing (2004). 62 CBS News. November 24, 2003. 63 CBS News, November 24, 2003. 64 Pharmacists were reimbursed for consulta tion time, approximately $13.50 per counseling session. http://www.go2ec.org/ProfileWashington.htm

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66 Pharmacies are convenient they are open evenings, weekends, and holidays. No appointment is required and a pa tient does not have to see her primary physician. This means no delay due to scheduling an appoi ntment or fear of discussing such matters with your primary physician. Washington State law does not prohibit the provision of contraceptive or family planning services to minors. No parental consen t is required. The progr am, therefore, improved emergency contraception access to women of all ages. The patient cost of emergency contraception is between $30 and $40. Additionally, the pilot progr am involved a mass consumer awareness campaign using extensive media coverage. Public service announcem ents, mainly in the form of TV and radio advertisements, occurred between July 1997 and March 1998. Additional paid TV, radio, and newspaper advertisements were public ized between July and August of 1998.65 Both the existence of emergency contraception and th e recent accessibility changes were heavily publicized in these advertisements. While the campaign targeted females aged 18-34, participants believed that they were reaching younger females as well. News of Washingtons program was also recognized by local and nationa l print and TV news stories; some 120 stories appeared.66 This campaign promoted the use of a new national hotline that allows women to call and locate their nearest provi der of emergency contraception. 1-888-NOT-2-LATE provides information regarding both pharmacies and clinics where emergency contraception is available.67 65 Trussell (2001). 66 Gardner (2001). 67 A website maintained by Princeton was also established containing the same information: www.Not-2-Late.com

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67Data Data on Chlamydia rates and abortion rates we re obtained from the State of Washington. These data are described in th is section and summary statisti cs are provided in Table 3-1. Chlamydia The State of Washington collects detailed data on sexually transmitted diseases by date of diagnosis. As such, the reports ca pture new incidents of the partic ular disease. These statistics are reported at the county level by age group and gender.68 Among the most reliable statistics are disease rates for Chlamydia.69 These data are available fo r the years 1992 through 2005. Using occurrences by date of diagnosis, rates are ca lculated per 100,000 of the relevant population. In the United States, Chlamydia is the most commonly reported STD. The disease does not always present with symptoms, but if symptoms ar ise, they are typically discovered within three weeks.70 Women experience a greater risk of cont racting Chlamydia (and other STDs) and are more likely to have symptoms, as well as serious complications, simply because of their physical design.71 Because most women have yearly physic als or gynecological visits, however, the disease is also more likely to be diagnosed in women.72 The disease is easily diagnosed, treated, and cured with antibiotics, but can lead to seri ous health problems if not treated promptly. 68 Disease & Reproductive Health Assessment Un it, Community & Family Health Division, Washington State Department of Health. These data were graciously made available by Mark Stenger at the Washington Department of Health. 69 Data are also collected for Gonorrhea, He rpes, and Syphilis. Gonorrhea incidence is less common in Washington than Chlamydia. Herpes st atistics are largely un derreported and Syphilis is a rare disease in the State of Washington (per Mark Stenger). 70 WebMD, http://www.webmd.com/hw/std/aa29303.asp 71 Reproductive Health Technologies Project, http://www.rhtp.org/std/types.asp 72 Reproductive Health Technologies Project, http://www.rhtp.org/std/types.asp

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68 The CDC reports that in 2004 over 900,000 incidences were reported in the United States.73 Figure 3-1 shows Chlamydia rates over tim e for the United States from 1992 through 2003.74 In the US, Chlamydia rates have been on the rise since the beginning of the data period in 1992, reaching a high rate of 300 in 2003. Wh ile Washington State has experienced increases as well, the pattern for Chlamydia is not the sa me as the national patter n. Figure 3-2 shows the rate of Chlamydia diagnosis in the State of Washington between 1992 and 2005 for all diagnoses and female diagnoses. Chlamydia rates were re latively stable between 1995 and 1997. In the years following 1997, Chlamydia rates rose for both groups and have reached all time high levels relative to the past 14 years. Between 1998 and 2005, overall Chlamydia rates increased by approximately 47 percent, while female Chlamydi a rates increased by approximately 39 percent. Because of the predominance of the disease in women, overall a nd female Chlamydia rates are studied. Age-specific rates are availabl e for females aged 15-19 and 20-24.75 Abortion Data Washington gathers and reports de tailed statistics on induced abortions by year, by county, and by age group.76 One of the main goals of the pilo t program was to reduce the number of unintended pregnancies in the Wa shington area. Unintended pregnanc ies are difficult to measure, 73 Chlamydia CDC Fact Sheet, Centers for Disease Control and Prevention, http://www.cdc.gov/std/Chlamydia/STDFact-Chlamydia.htm 74 Centers for Disease and Control, http://wonder.cdc.gov/std.html 75 Race and ethnicity information is also collect ed, but is often missing. STD counts by race may be incomplete and I have therefore not utilized the data by race. 76 Data are available through the Washington Depart ment of Health, Center for Health Statistics, http://www.doh.wa.gov/ehsphl/chs/c hs-data/abortion/viewdown.htm The Center for Health Statistics does not calculate rates when the number of cases is less than or equal to five. To avoid large jumps in rates, I have utilized the actual number of abortions by co unty and calculated rates for all values of occurrences. Caution should be taken, however, in interpreting rates associated with a small number of occurrences.

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69 but the effects of the program can be captured by abortion rates. Figur e 3-3 shows the overall abortion rate for females (aged 15-44) in Wa shington State. Between 1992 and 2004, abortion rates in Washington decreased by approximate ly 20 percent. Between 1998 and 2004, overall abortion rates decreased by approxi mately 5 percent. Figure 3-4 di splays the changes in abortion rates for the US between 1992 and 2003 for comp arison purposes. In the United States, the abortion rate has fallen from 1992 until 1998, and then remained fairly stable from 1998 to 2003. Of particular concern are abortion rates fo r young women, mainly women aged 15-19 and 20-24. Females aged 15-19 are of particular inte rest because most potential pregnancies in this age group are unintended and most of these young women are unmarried. At least some of the women in the 20-24 age band will be unmarried and have unplanned pregnancies. Figure 3-5 illustrates the trend in abortion rates for Wa shington women aged 15-19 and 20-24. These two age bands experience the highest abortion rates of all age groups Similar to the overall rate, abortion rates for both age bands are somewhat static between 1995 and 1997. Abortion rates for women aged 15-19 decreased by approximately 19 percent between 1998 and 2004. For women aged 20-24, abortion rates decrease d by 9 percent between 1998 and 2004. Program Participation Information on the filing of collaborative agreements was provided by the Board of Pharmacy, Washington Department of Health.77 The Board of Pharmacy approves all collaborative agreement filings and therefore was able to provide a list of pharmacies by location 77 I also received similar, but less complete, info rmation from the Office of Population Research at Princeton University, the organization which manages the Not-Too-Late website and hotline. They maintain a current list of participa ting pharmacies in states with pharmacy access legislation. Their database is designed to provide women seek ing emergency contraception with current provider locations. Although the databa se was not designed to keep historical participation records, I have utilized this information for some purposes.

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70 and date of filing.78 I subsequently used this information to determine when certain areas gained eligibility to dispense emergency contraception w ithout a prescription. While participation in the program and the formation of collaborative agreem ents are at the pharmac ist level, I aggregate access to the county-level. If a pharmacist had an agreement on file in year t in county i, I designate that county as having pharmacy access fo r that year and the remaining years in the dataset.79 In later specifications, I substitute this definition of treatment with the percent of total pharmacies with pharmacy access in county i in year t Initially, the pilot was intended to focus on counties in the Puget Sound area, mainly King, Pierce, and Snohomish counties. These counties we re chosen because they are located in the Seattle area and monitoring would be more feasib le. Since the law allows any pharmacist across the state to form a collaborative agreement, when news of the pilot spread, pharmacists in other areas of the state began to participate. The ma jority of the pilot program occurred between February 1998 and June 1999. During this time, 11,976 prescriptions for emergency contraception were dispensed by pharmacists.80 Pharmacists in 18 counties were involved during 78 In almost all cases, I relied on the dates of collaborative agreemen t filing provided by the Department of Health. There were a few circum stances, however, where there was a discrepancy in dates and I relied on dates compiled by Prin ceton. These circumstances involved Washington counties that had little participation over the tim e period. The Princeton information showed the same pharmacy as the Washington Department of Health information, but with a much earlier date of initial participation. In these instances, I adjusted the defi nition of treatment to reflect the Princeton information. 79 Some specific pharmacies may have lost approv al to dispense emergency contraception, but it does not appear from the data that any county lost access to emergency contraception. In other words, there may have been a change in the number of pharmacies dispensing emergency contraception in each county over time. 80 Gardner et al (2001).

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71 the pilot program.81 After the official pilot program activities concluded, additional pharmacies across the state continued to file collaborative agreements and access to emergency contraception continued to spread. As of 2006, 294 pharmacies in 31 (of 39) c ounties are eligible to provide emergency contraception without a prescription.82 Figure 3-6 displays a map of Washington State, shading th e counties which had pharmacy access in 1998, the first full year of the program. In Figure 3-7, the same map is displayed for a 2002, and Figure 3-8 shows pharmacy access for 2005. As shown, pharmacy access has grown over time between 1998 and 2005. Today, almost all counties in Washington State have some pharmacies which provide nonprescription access to emergency contraception. Identification In this section, I compare the participating and nonparticipating counties before the program began. A county is defined to be par ticipating or treated if any pharmacy access to emergency contraception is available in that county. If no pharmacy access is available in a county, then it is considered a nonparticipating or c ontrol area. The program was officially initiated in 1997, but most of the program activ ities began in 1998. The pretreatment years, or years before any pharmacy access was availabl e in Washington, are defined as 1995-1997. Baseline statistics for these year s are presented in Table 3-2. Chlamydia To properly identify the effect of pharmacy access on Chlamydia rates, we require the treatment and control groups to be similar but for the treatment. More specifically, the groups 81 These counties include Benton, Clallam, Clark, Cowlitz, Island, King, Kitsap, Pierce, Skagit, Skamania, Snohomish, Spokane, Thurston, Wahk iakum, Walla Walla, Whatcom, Whitman, and Yakima. 82 A national website, www.not-2-late.com provides a current listing of EC providers in Washington State.

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72 must be on the same trajectory prior to the programs implementation. With difference-indifference estimation, we do not require the groups to be at the same level necessarily but we do require the groups to exhibit similar trends. C ounty fixed effects, which are employed in what follows, control for any time-invariant changes in unobservable characteris tics. But Chlamydia is a communicable disease, and therefore, the le vel at time t may be determined in part by the level at time t-1.83 In other words, the greater the numb er of individuals infected with the disease, the more quickly it can sp read and cause new infections. In my paper, however, I use county-level obser vations and illustrate that pre-treatment, areas with and without pharmacy access are not only on the same trajectory, but are statistically indistinguishable in terms of their levels. Consid er Figure 3-9, which plots the overall Chlamydia rate for the treatment and control groups be tween 1995 and 2005. As shown, both groups follow the same trajectory between 1995 and 1997, while the treatment group is at a slightly higher level. After the start of the pilot program, indicated by the dotted vertical line at 1998, the two groups diverge in terms of their overall Chlamydia rates. Similarly, Figure 3-10 illustrates that female Chlamydia rates exhibit a similar pattern to overall Chlamydia rates. At first glance, it may appear troublesome th at Chlamydia rates are higher in treatment counties than in control counties. After conducting a difference in means t-test, however, I fail to reject the null hypothesis that the difference in the two groups is zero and conclude that the two 83 Some of the previous empirical literature has indicated the importa nce of including a lagged dependent variable as a covari ate. Panel OLS estimates with a lagged dependent variable are inconsistent in the presence of fixed effects. Th is occurs because the lagged dependent variable is correlated with the state fixed effects. Al ternative methods have been developed to allow estimation. One option is to take first differences and estimate a 2SLS m odel using lagged levels or lagged differences as instruments (2 t iY or 3 2 t i t iY Y). Such instruments are typically highly correlated with the first lagged difference, but un correlated with the transformed error. Arellano and Bond (1991) and more recently Blundell and Bond (1998) developed a GMM style approach to exploit a similar FD2SLS idea, where lagge d levels and/or lagged differences serve as instrumental variables.

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73 groups are statistically in distinguishable at the five percent level. The means test was conducted for 1995, 1996, and 1997, and these results are pres ented in Table 3-3. For females in 1997, we would reject the null at the 10 per cent level. It is possible, howe ver, that some effects of the program began occurring as early as 1997. The actual program was initiated in 1997, and therefore, any effects of the ini tial activities, prior to start of the official program, could be observed here. But for the treatment, we conclude that the counties are al ike. In 1998, the first year of the pilot program, Figures 3-9 and 3-10 sh ow the rates begin to s lightly diverge between the treatment and control group. Without expa nded access to emergency contraception, and given no other shocks, we would expect the groups to continue to look and trend similarly. Given that our treatment and control groups are similar prior to 1998, we assume that without treatment, the groups would continue to be on the same trajectory. Other studies which use the lagged STD rate as a ri ght-hand side regressor may not be able to exploit such an environment. Many other studies which estimate STD rates utilize state or regional level data, which may not satisfy these conditions. Since both groups experience the sa me trend in the years before the pilot program, and thei r levels are not statistically di fferent, we do not need to account for a one-period lag in the Chlamydia rate. Abortions The initial treatment and contro l groups also look similar in terms of their abortion rates. Figure 3-11 displays the overall abortion rate for the years 1995-2004 by treatment status. Although the initially treated coun ties exhibit a slightly higher le vel, both groups trend similarly during the pretreatment years. The two groups tr end somewhat similarly before 1998, with the control group experiencing somewh at larger declines in aborti on rates. Figures 3-12 and 3-13 illustrate the abortion rate for age 15-19 and 20-24 by treatment status for the years 1995 through

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74 2004.84 Abortion rates for ages 15-19 trend similarl y in the treatment and control group. Both groups experience slight declines during the pretreatment years, w ith the control group experiencing a slightly more dramatic dec line between 1997 and 1998. For 20-24 abortion rates, both groups experience slight increas es in abortion rates during the pretreatment years, with the control group experiencing a slightly more dramatic in crease between 1996 and 1997. Table 3-3 shows the results of the difference in means tests with respect to abortion rates. For these measures, we conclude that abortion rates in the treatment group are statistically different from the control group. The areas with pharmacy access exhibit sli ghtly higher levels of abortion rates. To the extent that this is a ti me-invariant characteristic the county fixed effects used in the analysis deal with the difference in levels. If the true effect of pharmacy access is to reduce abortions, however, then higher aborti on rates in the treatme nt group would lead coefficient estimates to be upward biased. Such a bi as could lead to a finding of no effect. If an effect is identified, however, then it is a conservative estimate. Pharmacy Participation The decision to form a collaborative agreement and ultimately dispense emergency contraception is made by the individual pharmacist or pharmacy. Pharmacy participation is based on a variety of factors. Possibl e factors include the demand for emergency contraception in the area, the attitudes and beliefs of the pharmacist or pharmacy management, or a desire to change the pharmacist-patient relations hip. If a given pharmacist forms a collaborative agreement because of high demand for emergency contraception in the area, which could be correlated with a high degree of sexual activity in the area, then the coefficient estimates on pharmacy access 84 For ages 15-19 and 20-24, there are two contro l counties which have virtually zero abortions in these two age bands. I have dropped these two counties from the control group.

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75 with respect to Chlamydia rates could be biased upwards. Figures 3-9 and 3-10 illustrated the similarities in the trends of th e treatment and control groups before the pilot program began. Not only did the two groups trend simila rly, but Table 3-3 indicated th at pretreatment the two groups are statistically indistinguishable. It does not appear that pharmacies in treatment counties are different from the control group. Moreover, we should not expect the coefficient estimate on pharmacy access to be biased upwards. As discussed above, pharmacy participation coul d be related to the ove rall level of sexual activity or risky behavior in the pharmacys area. Th is could be correlated with the level of teen pregnancy or the level of abortions in the ar ea. Pharmacy access to emergency contraception may lead to fewer abortions and/or fewer teen pregnancies because some pregnancies may be prevented and some abortions may not be necess ary. If pharmacies that formed collaborative agreements did so because of these factors, th en it is possible that the coefficient estimate on abortion rates or teen pregnancy rates could be bias ed upward. If the true effect of treatment is negative, however, this would upw ard bias my results in terms of finding no effect or a positive effect. If I find a negative effect, then the coe fficient estimates would be a conservative estimate. Given that pharmacies choose to file a co llaborative agreement at different times throughout the data period, we must also consider the timing of particip ation. Because not all areas of Washington gained pharmacy access to em ergency contraception at the same time, the timing of participation could affect the coe fficient estimates. Many counties experienced pharmacy participation between 1998 and 1999, during the pilot program. Any county with a participating pharmacy during this time is consid ered an early participant. Any county which did not have a pharmacy participate until 2000 or after is considered a late participant.

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76 To properly identify the effect of pharmacy access, we must ensure that the early participants look similar to the late participants. Difference in means tests were conducted for early and late participants and are contained in Table 3-4. These tests confirm that the overall and female Chlamydia rates between the early and late participants are not statistically distinguishable. The same conclusion is reache d for abortion rates for women aged 15-19. Early and late participants are not statistically diffe rent. When considering the overall abortion rate, however, the early and late participants are statistically different in 1995 and 1996, but are statistically indisti nguishable in 1997. Other Characteristics Difference in means tests were also conducted for other county-level characteristics such as the county-level unemployment rate, per capita income (real), and di vorce rate. We would expect the counties which had pharmacy access to look similar to counties without pharmacy access. The unemployment rate and per capita income may suggest something about the economic conditions of the county, while the divorce rate may suggest something about the family environment for young people in the area. Ta ble 3-5 reports differences in means tests for 1995, 1996, and 1997 for the three county-level meas ures. In each and every case, we fail to reject the null hypothesis that ther e is no difference in these measures between the treatment and control counties at the five percent level. Empirical Methodology My study exploits county-level variation in both Chlamydia and abortion rates to examine the intended and unintended effects of pharm acy access to and awareness of emergency contraception. The equations below will be estimated using a fixed effects model: it t i it itcess PharmacyAc Chlamydia 1 0 (3-1)

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77it t i it itcess PharmacyAc Abortion 1 0 (3-2) where itChlamydia indicates the Chlamydia rate in county i in year t. The rate is defined as the number of occurrences divided by the relevant population, multiplied by 100,000. itAbortion is defined as the number of abortions divided by the relevant population, multiplied by 1,000. itcess PharmacyAc is a dummy variable for countylevel pharmacy access to emergency contraception. In the initial specifications, a coun ty is defined as having pharmacy access in year t if at least one pharmacy has a collaborative agr eement on file with the Board of Pharmacy. In later specifications, pharmacy access is defined as the percentage of total county pharmacies with pharmacy access. Both equations also contain count y and year fixed effects. The fixed effects will capture any time-invariant county characteris tics which could bias the estimated effects of pharmacy access. Equations (3-1) and (3-2) are estimated without other county-level characteristics. Any covariate must be identifi ed from within county variation over fourteen years.85 Available county-level measures, however do not vary considerably over time.. For comparison purposes, however, the results with seve ral covariates are presented in Section VIII. Unless otherwise specified, data are available fo r 39 counties in Washington State for 14 years, 1992 through 2005, yielding a tota l of 546 observations when estimating Equation (3-1). For estimation of equation (3-2), data are availa ble from 1992 to 2004, yielding 507 observations. 85 Levine (2001), who explains the amount of se xual behavior using various costs of engaging in sexual behavior, uses labor mark et conditions, generosity of the welfare system, and abortion restrictions as independent variables. While thes e measures vary at the state-level, they do not vary substantially at the county-level.

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78Results Chlamydia Rates Table 3-6 contains the coefficient estimates for Overall, Female, Female Age 15-19, and Female Age 20-24 Chlamydia rates.86 The coefficient of pharmacy access on total Chlamydia rates is statistically significant and positive. Counties with pharmacy access experienced an increase in the total Chlamydia rate, with a coe fficient of 24. Relative to a baseline average of pre-treatment years (three-year averag e of 1995-1997), pharmacy access increases the Chlamydia rate by approximately 18 percent. 87 For females, pharmacy access is also associated with an increase of 18 percent, relative to the three-year pre-treatment average. Equation (3-1) was also estimated for males but is not reported here. Pharmacy access does not have a statistically significant effect on Chlamydia rates for men. Columns (3) and (4) of Table 3-6 contain regression results by female age group. Statistically significant results are obtained fo r those females aged 20-24. Pharmacy access is associated with a 331 unit (or a 28 percent) in crease in the 20-24 Female Chlamydia rate. The coefficient estimate for PharmacyAccess for females aged 15-19 is not statistically significant. The results using several cova riates are presented in Table 3-8 for comparison purposes. The additional independent va riables employed are county-leve l per capita income and the county unemployment rate. In almo st all circumstances, the covari ates included ar e statistically insignificant. In all cases, inclusion of the covari ates does not sufficiently change the statistical 86 To determine pharmacy access, I use the Wash ington Department of Health information primarily, but in some situation I supplement the dates with information from the Office of Population Research at Princeton University. The results are fairly consistent with the results presented in this section if I utilize Washingt on Department of Health data exclusively. 87 Three-year pretreatment averag es are contained in Table 3-7.

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79 significance of the treatm ent effect, although the magnitude of the treatment effect is slightly different. Abortion Rates Table 3-9 reports the results obtained from estimating Equa tion (3-2) for all women (1544), women aged 15-19, and women aged 20-24. Abortion rates also appear to be affected by pharmacy access to emergency contraception. If women use emergency contraception as a substitute for abortion, then the number of aborti ons may decrease. Treatment is associated with a one unit decrease in the overall abortion rate. Relative to a thre e-year pre-treatment average, this decrease corresponds to a 6 percent decrease in abortions. For teens aged 15-19, treatment is associated with over a two unit (or an 11 percent) decrease in abortion ra tes. Pharmacy access is also statistically significant with respect to abortion rates for women aged 20-24. Again relative to the three-year pre-treatment average, a bortion rates for women 20-24 were reduced by 15 percent. Although the results are not repor ted here, I also conducted th e analysis for women aged 25-29, 30-34, 35-39, and 40-44. Pharmacy access was not statistically significant in the regressions of any of these four age bands. Ph armacy access to emergency contraception appears to mainly impact the abortion rate for younge r women, particularly those aged 15-24. Lag in Treatment The results presented in the previous section use the actual dates of participation based on the initial collaborative agreement filing when considering the timing of treatment. These results are fundamentally unchanged if we lag the treatm ent time by 6 months or by 1 year. The effect of pharmacy access to emergency contraception is robust to these two alternative treatment definitions.

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80Alternative Treatment Definitions In the previous section, counties were cons idered treated if any pharmacies in county i had pharmacy access in year t. In this section, treatment is defi ned as the number of pharmacies with pharmacy access divided by the total number of pharm acies in that county in that year. In other words, treatment is the fraction of county pharmacies with pharmacy access. I count pharmacies using Washington Depart ment of Health collaborative agreement information filed with the Board of Pharmacy. I have tried to eliminate some duplicative records which appear in this info rmation in order to count new collaborative agreements. After counting the number of collaborative agreements, I divide the number of pharmaci es with access by the total number of pharmacies in that county in that year. 88 The results of this estimation are contained in what follows.89 Chlamydia Rates Table 3-10 reproduces the result s of Equation (3-1) using this alternative definition of treatment. The results in Table 3-10 are simila r to those in Table 3-7. Pharmacy access is associated with an increase in both overall and fe male Chlamydia rates. In this specification, however, pharmacy access is associated with an increase in the female Chlamydia rates for 88 The total number of pharmacies by county by year was obtained from County Business Patterns, U.S. Census Bureau, http://www.census.gov/epcd/cbp/view/cbpview.html relevant years. These data are only available from 1993 through 2002, so I used the counts for 2002 as counts for the years 2003, 2004, and 2005. Because pharmacy totals are no t available for 1992, I am unable to use this year of data in what follows. 89 I alternatively use all records provided to me by the Department of Health by county by year. In this counting mechanism, I do not try to elimin ate any potential duplicati ons, but rather use all the records provided. The result s using these counts of pharmaci es are consistent with my corrected counts.

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81 women age 15-19 as well as for women age 20-24. For the female 20-24 Chlamydia rate, a one percent increase in pharmacy access is associated w ith a 4.5 percent increase in the disease rate. Abortion Rates Table 3-11 shows the results for county abor tion rates when estimating Equation (3-2). Using the percent of county pharmacies with phar macy access yields much weaker results in this model. In Table 3-9, pharmacy access was associat ed with decreases in overall abortion rates, female abortion rates for women aged 15-19, a nd female abortion rates for women aged 20-24. Using this alternative treatment definition, how ever, pharmacy access is only associated with a decrease in abortion rate s for women aged 15-19. Other Considerations My empirical strategy relies on variation in pharmacy access by county as well as outcome variables that are measured at the county-level. Although to my knowledge these are the best data available at this time, there are some drawb acks of using county-level data to identify this treatment effect. First, I define tr eatment at the county-level first as a binary indicator and then as the percentage of pharmacies in a county with pharmacy access. Restrict ing treatment to the county-level could cause problems if some areas of certain counties are in fact more treated than others. First, some counties in Washingt on State are very large while some are much smaller. Other counties in Washington are more densely populated while other counties are more rural. Furthermore, the population in some counties is concentrated in specific areas of a larger geographic region. It is possible, therefore, that I could be misclassifyin g treated and nontreated counties. In other words, if a county has some pharmacy access but th is access is a ll concentrated around a border with a nontreated c ounty, then it is possible that the nontreated county could be just as affected or more affected by pharmacy access. To the extent that any misclassification

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82 means that I classify areas without pharmacy access nont reated when in fact they are treated, this would bias my estimates in favor of finding no effect. Falsification Tests To test that the identificati on of the treatment effect is not capturing a ge neral trend in increased disease or in overall risky behavior, a falsification ex ercise is performed and reported in Table 3-12 and 3-13. I use Washington State Cancer Regi stry data on county cancer rates.90 Washington cancer data are available by county in three-year averages beginning with 1992-1994 and ending with 2002-2004. In order to utilize th is data, I use the midpoint of the three-year ranges as observations for that year. In this way, I am able to use county-level cancer rates for 1993 through 2003. There are some observations which are not reported for some counties in some years. These missing observations account for numbe r of observations used in each regression. If the identified effects of pharmacy access on sexually transmitted diseases are capturing an upward trend in general disease rates in Wa shington State, then we should find a positive coefficient on pharmacy access with respect to cancer rates. Table 3-12, where each column is a separate regression, shows the results when regressing pharmacy access, along with county and year fixed effects, on several cancer rates includin g total cancer rates, female cancer rates, total lung cancer rates, female lung cancer rates, and fe male breast cancer rates. In all cases, I find no evidence that pharmacy access is associated with an increase in cancer rates. Additionally, I test if the eff ect of pharmacy access is capturing a general upward trend in risky behavior. I use measures of risky behavior including alcohol or substance use as well as 90 Washington State Cancer Registry, http://www3.doh.wa.gov/WSCR/default.htm relevant years.

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83 various criminal behaviors.91 To ensure that the participa tion in emergency contraception by pharmacies is unrelated to other meas ures of risky behavior, I regress PharmacyAccess on the rates contained in Table 3-13. Each column is a separate regression. Alcohol/Drug Related Death Rate is calculated as the nu mber of alcohol/drug related deaths per 100 total deaths. The remaining rates are calculated as the number of arrests of the particular crime divided by 1,000 of the respective population. For example, alcohol -related arrests (18+) is defined as the total number of alcohol related arre sts for individuals aged 18 and over divided by 1,000 of the 18 and over population. Pharmacy access has no effect on any other measure of risky behavior. Pharmacy access is not statistically significant in any of the re gressions presented in co lumns (1) through (9). Pharmacy access to emergency contraception does not appear to have an effect on these alternative measures of risky behavior. Additional Control Group: Oregon Chlamydia This section utilizes an additional source of da ta to increase the size of the control group. This section is used as a supplement to orig inal methodology because the available Washington data are richer than the availabl e Oregon data. We can, therefore, compare some of the results in this section with Sectio n VIII, but due to data availabili ty, we cannot compare all measures. Oregon, which does not have pharmacy access to emergency contraception, looks similar to Washington in the pre-treatment years and is therefore an appropriate comparison group. As 91 2005 Risk and Protection Profile for Substan ce Abuse Prevention, Research and Analysis Division, Washington State Department of Social and Health Services, http://www1.dshs.wa.gov/rda/res earch/4/47/updat ed/default.shtm Most measures are available for 1993 through 2004, except Alcohol and Drug Re lated Deaths which is available for 1992 through 2003. Some counties did not report certain measures for certain years due to small sample sizes or missing information. I have coded these observations as missing observations.

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84 illustrated in Figure 3-14, Washington and Or egon exhibit similar trends between 1994 and 1998; the rates are almost identical After the start of the pilot program and subsequent pharmacy access, rates for both states increase, but Washi ngton experienced greater increases in Chlamydia rates. Figure 3-14 confirms that Oregon is suitab le as a comparison group in terms of Chlamydia rates. Additionally, Figure 3-15 presents overall Chlamydia rate s for the treatment and control groups. In this figure, untreated areas of Washington are combined with Oregon counties (also untreated) to comprise a larger control group. As shown, both groups tr end similarly during the pre-program period. Differences in means tests, shown in Table 3-14, confirm that the treatment and control groups are sta tistically indistinguisha ble. Equation (3-1) is reestimated using the additional Oregon county-level data. Oregon, how ever, only publishes over all Chlamydia rates; county-level rates are not av ailable by gender or by age.92 Chlamydia rates for Oregon are available from 1994 through 2005. As a result, E quation (3-1) is now estimated for 1994-2005. Summary statistics for these data, and the abortion data, are contained in Table 3-15. The results from the estimation are contained in Table 3-16. The coefficient estimate on PharmacyAccess when including the Oregon data is larger and more precise than the coefficient presented in Section VIII. Without including the Oregon data, the treatment effect for overall Chlamydia ra tes was 28.9. Upon using Oregon county data, the treatment effect is 38.8. Relative to the three-ye ar pretreatment average, the latter coefficient represents a 29 percent increase in overall Chlamydia rates. Threeyear pretreatment averages are contained in Table 3-17. Using the combined Washington and Oregon data I also re-estimate the model using the percent of pharmacies with pharmacy access as the treatment. Table 3-18 contains the results of 92 Oregon Department of Human Services, http://oregon.gov/DHS/ ph/std/annrep.shtml

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85 this estimation. Again, increased pharmacy access is associated with an increase in the overall Chlamydia rate. Abortion A comparable alternative appro ach can also be conducted for abortion rates. In order to use Oregon counties as additional control c ounties, we must confirm that Oregon and Washington look and trend simila rly before introduction of pharmacy access in Washington. Figures 3-16, 3-17, and 3-18 pres ent graphical evidence that support this requirement. As shown, Washington and Oregon trend sim ilarly between 1995 and 1997 in terms of the overall abortion rate, 15-19 abortion rate, and 20-24 abortion rate. We can further compare the counties whic h were treated in Washington with the untreated counties from both Washington and Ore gon. Figures 3-19, 3-20, and 3-21 illustrate these trends graphically. Overall abortion rates declined somewhat for both treatment and control groups during the time period. Abortion rates fo r age 15-19 show sharpe r declines after the introduction of pharmacy access, while abortion rates for age 20-24 show small declines. The results of the reestimati on of Equation (3-2) are presente d in Table 3-19. Using this alternative approach, we are unable to identify an effect of pharmacy access on the overall abortion rate for women aged 15-44 or for teens age 15-19. We are, however, able to identify a negative effect of pharmacy access on aborti ons by females age 20-24. The coefficient on pharmacy access accounts for approximately 11 per cent of the decrease in abortion rates for females aged 20-24. This model was reestimated using the percent of pharmacies with pharmacy access as the treatment in place of the binary treatment indicator. The results of this estimation are contained in Table 3-20. In this model, the results for overall abortion rates are much weaker. Using this

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86 definition of treatment, I am unable to identify an effect of pharmacy access on overall abortion rates, abortion rates for age 15-19, or abortion rates for age 20-24. Conclusions The FDA recently approved a proposal to allo w emergency contraception to be available nationwide without a prescripti on for women over the age of 18. The State of Washington, however, was the first state to implement a program to increase access to emergency contraception through pharmacies. In my paper, I employ county-level data from Washington to consider the impact of such a program. Using a difference-in-d ifference methodology, and taking care to ensure that the treatment and control gr oups are similar pre-treatment, I find evidence of effects with respect to both STD rates and abor tion rates. The results suggest that increased access is associated with a reduc tion in the abortion rate, particularly for young women. This result is stronger when using the binary treatmen t definition than when using the percentage of pharmacies with access. A tradeoff, perhaps, is th at increased access is also associated with an increase in the overall and female Chlamydia rates. In particular, the results for suggest increases in the Chlamydia rate for females aged 20-24. When using the percentage of pharmacies with access, the results suggest that increased pharmacy access is associated with not only increases in the female 20-24 Chlamydia rate, but also the female age 15-19 Chlamydia rate.

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87 Table 3-1. Summary statistics Summary Statistics* Variable Mean Median Min Max Std. Dev. Chlamydia Rate 169.3 165.9 0 440.0 82.7 Female Chlamydia Rate 266.4 260.4 0 683.7 127.9 Female Chlamydia Rate, Age 15-19 1,603.1 1,646.7 0 3,605.8 750.9 Female Chlamydia Rate, Age 20-24 1,545.0 1,477.3 0 5,199.3 875.4 Abortion Rate 14.5 14.8 0 29.1 5.1 Abortion Rate, Age 15-19 19.4 19.4 0 42.9 8.4 Abortion Rate, Age 20-24 33.4 34.0 0 70.2 13.9 Unemployment Rate 7.47 7.2 1.6 17.6 2.5 Real income per capita $26,749 $25,470 $18,650 $53,583 $5,085.4 Pharmacy Access (binary) 0.37 0 0 1 0.48 Percent of Pharmacies with Access 12.3 0 0 100 23.2 *STD summary statistics and explanatory variables are calculated for the years 1992 through 2005. Summary statistics for the abortion variables are calc ulated for the years 1992 through 2004.

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88 Table 3-2. Baseline statistics 1995 1996 1997 Variable Treat Control Treat Control Treat Control Chlamydia Rate 141.3 106.8 142.4 108.4 140.2 101.7 Female Chlamydia Rate 228.7 189.8 231.5 169.8 224.3 164.2 Abortion Rate 15.5 10.3 15.7 9.1 15.7 8.6 Abortion Rate, Age 15-19 23.2 12.1 21.9 11.4 21.9 11.7 Abortion Rate, Age 20-24 34.1 18.7 34.8 18.2 34.8 25.1

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89 Table 3-3. Difference in means t-te sts between treatment and control [Null Hypothesis: difference in means is zero] Overall Chlamydia Rate Year Mean Treatment Mean Control P-value 1995 141.3 106.8 0.1163 1996 142.4 108.4 0.1693 1997 140.2 101.7 0.0655 Female Chlamydia Rate Year Mean Treatment Mean Control P-value 1995 228.7 189.8 0.2773 1996 231.5 169.8 0.1280 1997 224.3 164.2 0.0828 Abortion Rate 15-44 Year Mean Treatment Mean Control P-value 1995 15.5 10.3 0.0025 1996 15.7 9.1 0.0003 1997 15.7 8.6 0.0004 Abortion Rate 15-19 Year Mean Treatment Mean Control P-value 1995 23.2 12.1 0.0002 1996 21.9 11.4 0.0002 1997 21.9 11.7 0.0007 Abortion Rate 20-24 Year Mean Treatment Mean Control P-value 1995 34.1 18.7 0.0013 1996 34.8 18.2 0.0015 1997 34.8 25.1 0.0753

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90 Table 3-4. Difference in means t-te sts between early and late adopters [Null Hypothesis: difference in means is zero] Overall Chlamydia Rate Year Mean Early Mean Late P-value 1995 149.0 131.1 0.3423 1996 142.7 142.2 0.9802 1997 145.5 133.1 0.4874 Female Chlamydia Rate Year Mean Early Mean Late P-value 1995 243.4 209.3 0.2713 1996 229.1 234.6 0.8714 1997 230.3 216.6 0.6583 Abortion Rate 15-44 Year Mean Early Mean Late P-value 1995 16.4 13.3 0.0457 1996 16.7 13.4 0.0546 1997 16.5 13.8 0.1621 Abortion Rate 15-19 Year Mean Early Mean Late P-value 1995 24.1 21.1 0.2452 1996 22.7 19.9 0.2511 1997 23.3 18.8 0.1144 Abortion Rate 20-24 Year Mean Early Mean Late P-value 1995 36.5 28.4 0.0720 1996 38.7 25.7 0.0079 1997 35.7 32.6 0.5684

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91 Table 3-5: Difference in means ttests for county characteristics Unemployment Rate Year Mean Treatment Mean Control P-value 1995 7.5 8.8 0.2018 1996 7.3 8.9 0.1409 1997 6.2 7.5 0.1380 Real Per Capita Income Year Mean Treatment Mean Control P-value 1995 $25,642 $23,401 0.1513 1996 $25,072 $26,453 0.3985 1997 $26,826 $24,025 0.1020 Divorce Rate Year Mean Treatment Mean Control P-value 1995 6.42 5.74 0.1894 1996 6.41 6.06 0.4418 1997 6.27 5.74 0.2049

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92 Table 3-6. Chlamydia rates overall, by gender, and by gender/age (1) (2) (3) (4) Variable Name All Female Females 15-19 Females 20-24 PharmacyAccess 23.88 38.06 147.64 330.60 [12.36]* [17.62]** [102.95] [155.85]** R-squared 0.75 0.75 0.55 0.52 Number of Observations 546 546 546 546 County Fixed Effects X X X X Year Fixed Effects X X X X Clustered standards errors (at th e county-level) in brackets. Chlamydia Rate = (Number of Cases / Relevant Popula tion) 100,000 significant at 10%; ** significant at 5%; *** significant at 1%

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93 Table 3-7. Three-year pretreatment average, Washington Variable Average (1995-1997) Chlamydia Rate 133.04 Female Chlamydia Rate 215.80 Female Chlamydia Rate 15-19 1,362.4 Female Chlamydia Rate 20-24 1,163.4 Abortion Rate 14.18 Abortion Rate, Age 15-19 19.90 Abortion Rate, Age 20-24 31.34

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94 Table 3-8. Chlamydia rates overall, by gender, and by gender/age with covariates (1) (2) (3) (4) Variable Name All Female Females 15-19 Females 20-24 PharmacyAccess 19.75 33.86 92.12 298.2 [10.89]* [16.30]** [95.56] [153.33]* Per Capita Income 0.0041 0.0045 0.0471 0.0405 [0.0024]* [0.0039] [0.0267]* [0.0277] Unemployment Rate -1.41 -1.06 -22.11 5.08 [3.96] [5.41] [35.34] [45.27] R-squared 0.75 0.76 0.55 0.52 Number of Observations 546 546 546 546 County Fixed Effects X X X X Year Fixed Effects X X X X Clustered standards errors (at th e county-level) in brackets. Chlamydia Rate = (Number of Cases / Relevant Popula tion) 100,000 significant at 10%; ** significant at 5%; *** significant at 1%

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95 Table 3-9. Abortion rate s overall and by age (1) (2) (3) Variable Name Age 15-44 Age 15-19 Age 20-24 PharmacyAccess -0.9 -2.14 -5.25 [0.37]** [1.15]* [1.70]*** R-squared 0.85 0.72 0.66 Number of Observations 507 481 481 County Fixed Effects X X X Year Fixed Effects X X X Clustered standards errors (at th e county-level) in brackets. Abortion rate = (Number of Abortions / Relevant Population) 1,000 significant at 10%; ** significant at 5%; *** significant at 1%

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96 Table 3-10. Chlamydia rates overa ll, by gender, and by gender/age (1) (2) (3) (4) Variable Name All Female Females 15-19 Females 20-24 Percent of Total Pharmacies Participating 0.496 0.651 3.311 4.485 [0.175]*** [0.263]** [1.785]* [2.075]** Number of Observations 507 507 507 507 R-squared 0.77 0.77 0.56 0.55 County Fixed Effects X X X X Year Fixed Effects X X X X Clustered standards errors (at th e county-level) in brackets. Chlamydia Rate = (Number of Cases / Relevant Popula tion) 100,000 significant at 10%; ** significant at 5%; *** significant at 1% By using the percent of total pharmacies participating, I am only able to utilize data from 1993 through 2005. The data for total number of pharmacies for 1992 is incomplete, so I drop 1992 observations in these regressions. Because of using this method, in five cases, the percent of participating pharmacies out of total county pharmacies exceeds 100. In these five cases, I recode these pe rcentages to 100 until updat ed data is available.

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97 Table 3-11. Abortion ra tes overall and by age (1) (2) (3) Variable Name Age 15-44 Age 15-19 Age 20-24 Percent of Total Pharmacies Participating -0.004547 -0.03404 0.002877 [0.005630] [0.019525]* [0.044819] R-squared 490 490 490 Number of Observations 0.86 0.76 0.62 County Fixed Effects X X X Year Fixed Effects X X X Clustered standards errors (at th e county-level) in brackets. Abortion rate = (Number of Abortions / Relevant Population) 1,000 significant at 10%; ** significant at 5%; *** significant at 1% By using the percent of total pharmacies participating, I am only able to utilize data from 1993 through 2004. The data for total number of pharmacies for 1992 is incomplete, so I drop 1992 observations in these regressions. Because of using this method, in one case, the percent of participating pharmacies out of total county pharmacies exceeds 100. In this case, I recode the percen tage to 100 until updated data is available.

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98 Table 3-12. Falsification te sts using county cancer rates (1) (2) (3) (4) (5) Variable Name Total Cancer Rate Female Cancer Rate Total Lung Caner Rate Female Lung Cancer Rate Female Breast Cancer Rate PharmacyAccess 3.63 4.742 1.343 0.52 -7.859 [9.610] [13.629] [2.999] [2.658] [8.858] No. of Observations 429 429 424 395 428 R-squared 0.63 0.66 0.67 0.69 0.47 County Fixed Effects X X X X X Year Fixed Effects X X X X X

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99 Table 3-13. Falsification exercise (1) (2) (3) (4) (5) Variable Name Alcohol & Drug Related Deaths Alcohol Related Arrests (Age 18+) Drug Related Arrests (Age 18+) Violence Related Arrests (Age 18+) Property Crime Arrests (Age 18+) PharmacyAccess 0.10 0.84 -0.12 0.14 -0.48 [0.28] [1.026] [0.35] [0.22] [0.36] R-squared 0.73 0.74 0.64 0.58 0.78 No. of Observations 410 453 453 453 453 County Fixed Effects X X X X X Year Fixed Effects X X X X X (6) (7) (8) (9) Variable Name Property Crime Arrests (Age 10-17) Violence Related Arrests (Age 10-17) Alcohol Related Arrests (Age 10-17) Drug Related Arrests (Age 10-17) Treatment -1.32 0.27 -1.722 0.32 [2.59] [0.47] [1.46] [0.52] R-squared 0.69 0.44 0.72 0.67 No. of Observations 456 456 456 456 State Fixed Effects X X X X Year Fixed Effects X X X X Clustered standards errors (at th e county-level) in brackets. Rates = (Number of Occurrences / Relevant Population) 1,000 significant at 10%; ** significant at 5%; *** significant at 1%

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100 Table 3-14. Difference in m eans t-test, Chlamydia rates Overall Chlamydia Rates [Null Hypothesis: difference in means is zero] Year Mean Washington Mean Oregon P-value 1995 133.3 134.5 0.9402 1996 134.5 132.6 0.9091 1997 131.3 135.2 0.8090 Overall Chlamydia Rates Year Mean Washington Treated Mean Washington or Oregon Untreated P-value 1995 141.3 129.0 0.4455 1996 142.4 127.7 0.4090 1997 140.2 128.5 0.4801

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101 Table 3-15. Summary statis tics, Washington and Oregon STD Summary Statistics, 1994 2005 Variable Mean Median Minimum Maximum Chlamydia Rate 157.5 147.0 0 642.9 Abortion/Birth Summary Statistics, 1992 2004 Abortion Rate 12.7 12.9 0 30.6 Abortion Rate, Age 15-19 16.6 16.5 0 49.1 Abortion Rate, Age 20-24 28.0 27.6 0 83.5

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102 Table 3-16. Chlamydia rates including Oregon (1) Variable Name Chlamydia Rate PharmacyAccess 38.79 [9.11]*** R-squared 0.77 Number of Observations 900 County Fixed Effects X Year Fixed Effects X Clustered standards errors (at th e county-level) in brackets. Chlamydia Rate = (Number of Cases / Relevant Popula tion) 100,000 significant at 10%; ** significant at 5%; *** significant at 1%

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103 Table 3-17. Three-year pre-treatm ent average, Washington and Oregon Variable Average (1995-1997) Chlamydia Rate 133.54 Abortion Rate 12.92 Abortion Rate, Age 15-19 17.77 Abortion Rate, Age 20-24 26.19

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104 Table 3-18. Chlamydia rates including Oregon (1) Variable Name Chlamydia Rate Percent of Total Pharmacies Participating 0.81 [0.179]*** R-squared 900 Number of Observations 0.77 County Fixed Effects X Year Fixed Effects X Clustered standards errors (at th e county-level) in brackets. Chlamydia Rate = (Number of Cases / Relevant Popula tion) 100,000 significant at 10%; ** significant at 5%; *** significant at 1%

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105 Table 3-19. Abortion rates including Oregon (1) (2) (3) Variable Name Abortion Rate 15-44 Abortion Rate 15-19 Abortion Rate 20-24 PharmacyAccess 0.20 -0.52 -2.76 [0.37] [0.81] [1.44]* R-squared 0.87 0.75 0.73 No. of Observations 900 900 900 County Fixed Effects X X X Year Fixed Effects X X X Clustered standards errors (at th e county-level) in brackets. Abortion Rate = (Number of Cases / Relevant Population) 1,000 significant at 10%; ** significant at 5%; *** significant at 1%

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106 Table 3-20. Abortion rates including Oregon (1) (2) (3) Variable Name Abortion Rate 15-44 Abortion Rate 15-19 Abortion Rate 20-24 Percent of Total Pharmacies Participating 0.007 -0.001 0.034 [0.005] [0.010] [0.027] R-squared 900 900 900 No. of Observations 0.87 0.75 0.73 County Fixed Effects X X X Year Fixed Effects X X X Clustered standards errors (at th e county-level) in brackets. Abortion Rate = (Number of Cases / Relevant Population) 1,000 significant at 10%; ** significant at 5%; *** significant at 1%

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107 0 50 100 150 200 250 300 350 199219931994199519961997199819992000200120022003 Figure 3-1.Chlamydia rates in the United States, 1992 2003.

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108 0 60 120 180 240 300 360 Rate per 100,000 1992 1994 1996 1998 2000 2002 2004 Year OverallFemale Figure 3-2. Overall and female ch lamydia rates in Washington state

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109 0 5 10 15 20 Rate per 1,000 1992 1994 1996 1998 2000 2002 2004 year Figure 3-3. Overall abortion rate (age 15-44) in Washington state

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110 0 5 10 15 20 25 199219931994199519961997199819992000200120022003 Figure 3-4. Abortion rates in th e United States, 1992 2003.

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111 0 5 10 15 20 25 30 35 40 45 Rate per 1,000 1992 1994 1996 1998 2000 2002 2004 year Abortion Rates 15-19Abortion Rates 20-24 Figure 3-5. Abortion rates in Washingt on state, ages 15-19 and ages 20-24

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112 No Pharmacy Access Pharmacy Access Figure 3-6. Washington state pharmacy access in 1998 Seattle S p okane Pullman Tacoma Ol y m p ia

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113 No Pharmacy Access Pharmacy Access Figure 3-7. Washington state pharmacy access in 2002 Seattle S p okane Pullman Tacoma Ol y m p ia

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114 No Pharmacy Access Pharmacy Access Figure 3-8. Washington state pharmacy access in 2005 Seattle S p okane Pullman Tacoma Ol y m p ia

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115 0 40 80 120 160 200 240 280 320 Rate per 100,000 1995 1996 1997 1998 1999 2000 2001 2002 2003 2004 2005 Year TreatmentControl Figure 3-9. Overall chlamydia ra tes by treatment and control group

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116 0 50 100 150 200 250 300 350 400 Rate per 100,000 1995 1996 1997 1998 1999 2000 2001 2002 2003 2004 2005 Year TreatmentControl Figure 3-10. Female chlamydia ra tes by treatment and control group

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117 0 5 10 15 20 Rate per 1,000 1995 1996 1997 1998 1999 2000 2001 2002 2003 2004 year TreatmentControl Figure 3-11. Overall abortion rates (age 15-44) by treatment status

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118 0 5 10 15 20 25 30 Rate per 1,000 1995 1996 1997 1998 1999 2000 2001 2002 2003 2004 year TreatmentControl Figure 3-12. Abortion rates (age 15-19) by treatment status

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119 0 5 10 15 20 25 30 35 40 45 Rate per 1,000 1995 1996 1997 1998 1999 2000 2001 2002 2003 2004 year TreatmentControl Figure 3-13. Abortion rates (age 20-24) by treatment status

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120 0 50 100 150 200 250 Rate per 100,000 1994 1996 1998 2000 2002 2004 Year WashingtonOregon Figure 3-14. Overall chlamydia rates, Washington and Oregon

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121 0 50 100 150 200 250 Rate per 100,000 1994 1996 1998 2000 2002 2004 Year TreatmentNot Treated WA or OR Figure 3-15. Overall chlamydi a rates by treatment status

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122 0 5 10 15 20 Rate per 1,000 1994 1996 1998 2000 2002 2004 Year WA TreatmentWA or OR Not Treated Figure 3-16. Abortion rates, Washington and Oregon

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123 0 5 10 15 20 25 Rate per 1,000 1993 1995 1997 1999 2001 2003 Year WashingtonOregon Figure 3-17. Abortion rates 15-19, Washington and Oregon

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124 0 10 20 30 40 Rate per 1,000 1993 1995 1997 1999 2001 2003 Year WashingtonOregon Figure 3-18. Abortion rates 20-24, Washington and Oregon

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125 0 5 10 15 20 Rate per 1,000 1994 1996 1998 2000 2002 2004 Year WA TreatmentWA or OR Not Treated Figure 3-19. Abortion rates by treatment status

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126 0 5 10 15 20 25 30 Rate per 1,000 1994 1996 1998 2000 2002 2004 Year WA TreatmentWA or OR Not Treated Figure 3-20. Abortion rates 15-19 by treatment status

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127 0 10 20 30 40 50 Rate per 1,000 1994 1996 1998 2000 2002 2004 Year WA TreatmentWA or OR Not Treated Figure 3-21. Abortion rates 20-24 by treatment status

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128 CHAPTER 4 THE IMPACT OF PHARMACY-SPECIFIC ANY-WILLING-PROVIDER LEGISLATION ON PRESCRIPTION DRUG EXPENDITURES Introduction In recent years, many states have implemented Any-Willing-Provider (AWP) legislation. This form of health care legislation requires a managed care organization (MCO) to accept any provider who agrees to the MCOs reimbursement ra tes, terms, and conditions. A provider in this context could be a physician, hospital, or pha rmacy. Proponents argue that AWP laws increase network size, expand patient choice, and in crease competition among providers. Opponents believe that AWP legislation prevents managed care organizations from selectively contracting and obtaining discounts by offeri ng providers a larger volume of patients. Additionally, administrative costs could be affected simply due to the difficulties of dealing with a larger number of pharmacies, physicians, or hospitals in the network. Such legisl ation, therefore, may prevent MCOs from effectively reducing health ca re costs as much as they might otherwise. A small literature exists on the effect of AW P laws on several categories of health care expenditures including total he alth care expenditures, hospi tal expenditures, and physician expenditures. Most studies, however, fail to recognize that the vast majority of the existing AWP laws target pharmacies exclusively, as opposed to more comprehensive laws that apply to some combination of physicians, hospita ls, and pharmacies. If AWP legi slation limits cost reductions available through selective contrac ting, then states with such le gislation may incur higher health care expenditures. There are additional potential consequences of AWP legislation, which related mainly to physicians and hospitals. For example, some opponents argue that AWP forces HMOs to contract with physicians who might be higher-cost in that they provide relatively inferior care or use excessive resources. If MCOs must now contract with physicians who might not comply with the MCOs treatmen t philosophy, then health care co sts could increase. Arguments

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129 of this type obviously cannot apply to pharmaci es since pharmacists do not have prescribing authority. Given that most AWP laws focus exclusively on pharmacies, it is relevant to consider the impact of these specific types of AWP laws For pharmacies specifically, AWP laws not only increase patient choice but also allow indepe ndent pharmacies to compete with large chain pharmacies. If AWP laws prevent the MCO from selectively contracting with specific pharmacies or if AWP laws raise administrative costs in dealing with pharmacies for the MCO, then it is possible that expenditures on prescrip tion drugs could increase. The effect of pharmacy AWPs is distinct from the effect of more comp rehensive laws. My study is the first to analyze the impact of pharmacy-specific AWP legislatio n on state-level prescription drug expenditures per capita. I find that AWP legislation is asso ciated with increases in pharmaceutical drug expenditures per capita. This result is robust to several alternative speci fications. Additionally, I find evidence consistent with other studies in terms of the relationship between AWP and health care expenditures as well as the relationship between HMO market share and health care expenditures. Managed Care and Any-Willing-Provider Legislation Managed Care and Health Maintenance Organizations In the early 1980s, managed care was a new c oncept on the health car e front. Enrollments in managed care increased dramatically duri ng the 1980s, and continued to gain popularity through the 1990s. Today, managed care is the pre dominant form of health care in the United States. Managed care is a broad term that encompa sses several types of health care plans such as Health Maintenance Organizations (HMOs) a nd Preferred Provider Organizations (PPOs). HMOs, the more restrictive type of plan, usually re quire that all services be authorized by an innetwork primary care physician, otherwise known as a gatekeeper. In contrast, PPOs offer

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130 enrollees lower cost sharing when using services within some preferred provider list and higher cost sharing when using services outside th e preferred provider network. PPOs do not have formal gatekeepers. These forms of managed care pl ans are in contrast to what was traditionally known as an indemnity plan or a Fee-For-Ser vice (FFS) plan. A FFS plan would permit its enrollees to purchase medical services from any provider of their choice. The providers submit a claim to the insurance company and all cove red claims would be paid. A FFS plan has no gatekeepers and no restrictions on medical se rvices or on choice of provider, although FFS subscribers are subject to policy limits. The conventional belief is that managed care lowers health care spending through various cost containment strategies. This decrease in spending is dependent mainly upon selective contracting which allows MCOs to obtain volume discounts. By promisin g providers a certain volume of patients, managed care organizations are able to negotiate volume discounts. Additionally, because MCOs limit their provider networks, they reduce the number of providers with whom they contract. This can reduce admini strative expenses. In th ese ways, states with higher HMO enrollments are believed to have lower health care spending. But HMO presence does not necessarily re duce health care spending in all areas. Managed care stresses the importa nce of well patient visits as well as preventive care. One goal of managed care is to reduce hos pital expenditures by substituting less expensive physician visits and other preventive services for more costly hospital stays. Increased HMO presence is associated with a shift in expenditures from hos pitals to physicians. This substitution is also found between hospitals and pres cription drugs. In a 1998 study, Cutler and Sheiner report that HMO enrollment is associated with a decrea se in hospital spending growth, but increases spending growth for physicians services and prescription drug expenditures.

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131 Any-Willing-Provider Legislation In the 1980s and again in the 1990s, a new form of legislation appeared in the United States. Many states passed anywilling-provider laws that requir e managed care organizations to accept any provider into their netw ork if the provider agrees to the conditions, terms, and reimbursement rates. Managed ca re organizations have come under criticism for a variety of reasons. One consequence of a managed care orga nizations cost reducin g strategies is the restriction in provider choice. Accordingly, propo nents of AWP argue that such legislation will increase the number of availabl e providers in a network and thereby increase competition among providers. The main mechanism through which managed ca re organizations are able to constrain costs is through limited provider networks, selec tive contracting, and volume discounting. As such, in order for managed care organizations to be effective at cost containment, they must be able to negotiate volume discounts by committing to a larger volume of patie nts to each provider. AWP prevents a managed care organization from be ing able to offer providers a much larger patient base and therefore diminishes its ability to selectively contract. Additionally, if managed care organizations are required to accept any provid er who agrees to its terms into its network, then it will have less control ove r the quality of care and the ty pes of providers with whom it collaborates. This could force a managed care orga nization to contract wi th providers that use relatively excessive medical reso urces or provide relatively in ferior care. A final concern involves administrative or transac tions costs, which in crease with the number of providers with whom the managed care organization contracts. Any-willing-provider legislation varies across states and over time. AWP laws are heterogeneous in their application. For example, some AWP laws target hospitals, physicians, pharmacies, or some combination of the thr ee. The focus of my paper centers on AWP

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132 legislation that targets pharmacies specifically. For the remainder of what follows, we will focus on the AWP laws enacted in states that fo cus on pharmacy providers specifically, while controlling for effects of other types of AWP laws. Many states have enacted some form of anywilling-provider legislation. Most of these laws were passed in the 1990s, but some were passed earlier. Table 4-1 describes the states that passed pharmacy-specific any-willing-provider laws as well as those which have other variants of the legislation. Twenty-six states have AWP laws in place, with 23 states having laws which apply to pharmacies, and 15 of which apply only to pharmacies. Previous Literature A small literature examines the effects of anywilling-provider legisla tion. In particular, a study by Vita (2001) considers the impact of AWP legislation on general health care expenditures. Using state-level pe r capita expenditures for total health care spending, hospital care, and physician care, Vita considers the re lationship between AWP laws and personal health care expenditures. He categorizes the laws as ranging from weak to moderate to strong, depending on their application. He finds that st ates with AWP legislatio n have higher per capita total health care expenditures cont rolling for demographic factors a nd state trends. He also finds some evidence that AWP laws are associated with increases in hospital care spending. Most AWP laws are applicable to only pharmacies, meaning that HMOs in states with pharmacy AWPs must admit any pharmacy th at agrees to its terms, conditions, and reimbursement rates into the network. Other st ates have physician or hospital AWP laws, which require contracting with those types of pr oviders. Given the overwhelming presence of pharmacy-specific laws, it is important for us to understand the effects of pharmacy-specific legislation on health care spendi ng. Prior studies have failed to consider these types of laws specifically or to consider the effect of AWP la ws on pharmaceutical expenditures. To fill in this

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133 gap in the literature, my pape r considers the impact of pharm acy-specific AWP legislation on pharmaceutical health care expenditures. Data Health Care Spending The Centers for Medicare and Medicaid (CMS ) publish state-level health expenditures for specific health accounts and medical products, such as hospital care, physician services, prescription drug expenditures, nur sing home care, dental care, and the like. These data are available by state for a panel of years a nd are based on the state of the provider.93 In other words, these data are based on the state where the services were received rather than the state where the health care consumer resides. I use state-level observations on medical expenditures per capita for the years 1987 through 1998.94 While there are many categories of health care spending, the main focus in my paper will be on pharmaceutical expenditures. Additionally, I show results for total health care expenditures, physician services, and hospital care in order to compare my results with Vita (2001). For the pur poses of this analysis, state of provider data are preferred to the state of residence data.95 State of provider data disti nguishes among prescription drug expenditures, nonprescription drug expenditures, and other nondur able medical expenditures. State of residence data, however group these three into one category. We might be concerned, however, about using state of provider data when analyzing hospital care or physician services 93 Data are also available based on State of Residen ce, but the panel of data available is shorter, 1991-1998. 94 State of provider data are avai lable as early as 1980, but due to the availability of some other variables, including HMO enrollment and market share, Medicare enrollment, Medicaid enrollment, and the number of insu red individuals I am able to utilize state of provider data only as early as 1987. 95 State of residence data exist for 1991 through 1998, but do not distinguish between prescription drugs and nonprescripti on drugs and medical sundries.

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134 expenditures. For example, some individuals ma y cross state lines to receive some forms of medical treatment like a surgery at a renowned hospital or an office visit with a specialist. But it is less likely, however, that many individuals cr oss state lines in orde r to obtain prescription drugs. Pharmaceutical expenditures, therefore, ar e unlikely to be affected significantly by the state of provider characterization. Additionally, using data based on state of provider makes it possible to utilize five additional years of data for every state. Health care expenditures have increased dramatically since 19 87. Real total health care spending per capita96 increased 49 percent between 1987 a nd 1998. Similarly, hospital care and physicians services expenditure s per capita have increased 33 percent and 50 percent, respectively, between 1987 and 1998. Expenditure s on prescription drugs per capita more than doubled between 1987 and 1998, an increase of 119 pe rcent. Figure 4-1 illust rates the pattern of expenditures per capita over time for three categ ories: hospital care, phys icians services, and prescription drugs. Health Maintenance Organization Presence One of the essential factors in this analysis is a measure of HMO presence. Relevant data on HMO enrollments and HMO penetration rate s were obtained through Forte Information Resources.97 Aventis Pharmaceuticals sponsors a yearly survey of HMOs whose results are summarized in an annual publication called the Managed Care Digest Series, managed and published by Forte.98 These publications are available fo r the years 1986 through 2004. I utilize 96 All dollar figures are adjusted to 1998 dollars. 97 Data published in each digest were collected by SMG Marketing Verzipan LLC, a health care consulting firm which also conducts market research. Data were gathered mainly by mail and telephone surveys. 98 Managed Care Digest Series, HM O-PPO/Medicare-Medicaid Digest, Aventis Pharmaceuticals, relevant years.

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135 HMO data for 1987 through 1998. These publications contain state-level information on the number of HMOs serving each state, the total HMO enrollment, and HMO penetration. In the analysis, I use HMO enrollments to calculate HMO market shares as well as HMO penetration rates. HMO market share is calculated as th e total HMO enrollment divided by the number of covered lives.99 HMO penetration is defined as the to tal HMO enrollment divided by the state population. HMO enrollment has changed dramatically between 1987 and 1998. In 1987, average HMO market share in the United States was 11.6 percent. By 1994, HMO market share had increased to 20.2 percent. In 1998, HMO market share reached 33 percent. Sample Data for HMO enrollment and market share ar e only available as early as 1986. Medicare enrollment, Medicaid enrollment, and the number of covered lives are only available for as early as 1987. The data used in this analysis, ther efore, spans 1987 through 199 8. The District of Columbia is omitted from this analysis. The samp le is composed of 50 states over 12 years for a total of 600 observations. Empirical Methodology To consider the effect of a ny-willing-provider legislation on health care expenditures, I implement a fixed effects model using ordinary le ast squares. The estimated model is defined by equation 4-1: it t i it it itX AWP Exp 1 0 (4-1) where Exp indicates the expenditures of the part icular category of health care, AWP indicates whether the state has an AWP law in place in that year, X is a vector of st ate-level demographic 99 Historical Health Insurance Tables Table HI-4, U.S. Census Bureau.

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136 and health characteristics, is a vector of state indicators, and is a vector of year indicators. Included in the vector of X covariates are the fo llowing variables: HMO market share, state-level unemployment rate,100 real per capita income,101 percentage of the popul ation over the age of 65,102 percentage of the population of African American race,103 and population density.104 In some specifications, as noted, I include the perc entage of the population insured by Medicare and the percentage of the population insured by Medicai d. In these specifications, the percentage of the population over the age of 65 is omitted. I cluster my standard errors at the state-level and weight each observation according to the state popul ation. Table 4-2 contains summary statistics for the relevant variables used in this analysis. To begin, I estimate similar models to Vita (2001) to determine if th e estimated effects of any AWP laws on total health care expenditures, physician serv ices, and hosp ital care are comparable. To supplement that analysis and be cause most AWP laws apply only to pharmacies, I test the effect of pharmacy-s pecific AWP legislation on prescr iption drugs expenditures, while controlling for the laws affecting other providers. Since the majority of these types of legislation target pharmacies as opposed to doctors and hospitals, it is important to understand the consequences of these specific types of laws on health care expenditures. 100 Bureau of Labor Statistics, relevant years. 101 Personal income per capita, Bure au of Economic Analysis, rele vant years. Nominal dollars were inflated to 1998 dollars using changes in CP I-U from the Economic Report of the President. 102 U.S. Census Bureau, relevant years. 103 U.S. Census Bureau, relevant years. 104 Statistical Abstract of the United States, relevant years.

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137 Results General Any-Willing-Provider Legislation HMOs are said to be effective in reducing health care expenditures. One way this occurs is through selective contracting. AWP laws prevent an MCO from successfully negotiating volume discounts and therefore from reducing hea lth care spending effectively. This section provides empirical evidence to support this claim. Table 4-3 displays the results of regressions that consider any-willing-provider legislation in general. In these specifications, AWP identifies states that have either a law applying to pharmacies, hospitals, physicians, or some co mbination of the three providers. In this specification, AWP laws are associated with an increase in total health care expenditures. The magnitude of this effect is approximately $100 pe r capita. Relative to an average value of total health care expenditures over the time period of $3127, this account s for a 3 percen t increase in expenditures per capita. AWP laws are also associated with increases in expenditures on pharmaceutical drugs. The magnitude of this co efficient is approximately $15 per capita. Relative to average pharmaceutical spending of $220 per capita, this increase accounts for a 7 percent increase in pharmaceutical spending per capita. There is no evidence that physician services or hospital care expenditures are higher as a result of AWP legislation. The results with respect to HMO market shar e are consistent with those of Cutler and Sheiner (1998). Increased HMO presence is associ ated with a reduction in hospital expenditures per capita. Although HMO market shar e is not statistically significan t in the other three models, the signs of the coefficients are consistent with previous empirical evidence. All models were also estimated using HMO penetration rates in place of HMO enrollment rates. The results are consistent across both specifications.

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138 Table 4-4 illustrates the results of a similar specification that includes the percentage of the population insured by Medicare and the perc entage of the populatio n insured by Medicaid, omitting the percentage of the population over the ag e of 65. These results are not fundamentally different from the results presente d in Table 4-3. AWP legislation is associated with an increase in total expenditures and prescription drug expe nditures. The magnitudes in Table 4-4 are quite similar to those in Table 4-3. Some of the other covariates us ed in this analysis proved significant in some models. The state-level unemployment rate a nd real income per capita are asso ciated with higher levels of health care spending. The per cent of the population of African American race is positive and significant in some models, as is the Fractio n of the population with Medicare. Population density, however, is not signifi cant in any of the models. Heterogeneous Application of An y-Willing-Provider Legislation Any-willing-provider laws may apply to one or more of the following providers: pharmacies, hospitals, and physicians. Most of the current laws, however, apply only to pharmacy providers, while very few apply to hosp itals or physicians or both. As a result, I estimate several specifications which take into account whether the state law applies to pharmacies or has other applications. Since the majority of these type s of laws impact only pharmacies, the most relevant category to cons ider is expenditures on pharmaceutical drugs. Any effect on expenditures for hospital care or physicia n services should be less prominent. Table 4-5 utilizes Pharmacy AWP, which indicates if a pa rticular state has an AWP law which applies to pharmacies only. Pharmacy Plus indicates states whic h have an AWP targeting pharmacies as well as another provider type. Hospital/Phys ician AWP indicate states which have AWP applying to hospitals or physicians but not to pharmacies. These re sults are consis tent with the results presented in Tables 4-3 and 4-4. Pharm acy-specific AWP laws are associated with an

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139 increase in pharmaceutical drug expenditures per cap ita. Similarly, laws which target pharmacies as well as other providers are also associated with an increase in pharmaceutical drug expenditures per capita. Additionally, laws which a pply to hospitals or physicians but not to pharmacies are associated with an increase in ho spital care expenditures per capita, but not with a rise in physician services e xpenditures per capita. Reassuringly these laws have no impact on pharmacy expenditures. Policy Endogeneity & Robustness Policy Endogeneity I attempted several forms of instrumental variables which had been suggested in the literature, such as the percentage of firms defi ned as large, i.e., with more than 500 employees. Ohsfeldt et al (1998) examines the likelihood of a state to pass an AWP law based on the winners (providers, hospitals, pharmacies), the losers (MCOs, employers, and employees), and the political environment. 105 When considering all AWP laws, the only variable that predicts the enactment of the law is the number of hospital beds per capita. Other variables such as number of physicians or pharmacists per capita and measures of the political climate were not significant with respect to any-willing-provide r law presence. Because AWP laws vary in thei r applicability across states, the authors categorize the laws by wh at entities they target. Their model works well for laws that are focused on hospitals, but does not perform well for laws which target pharmacies and physicians. Only one variable, the pe rcentage of employers de fined as large, is related to the enactment of a pharmacy-specific any-willing provider law. Additionally, I utilized a measure of political control, since more c onservative states tend to support and enact AWP legislation. Neither of these potential instrumental variables had any predictive power in the first 105 This variable was also explored in an earlier study, McLaughlin (1987).

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140 stage where AWP or pharmacy AWP was the depende nt variable. This sugge sts a lack of valid instruments for the policy change. Other variables used in the public choice studies to predict the enactment of AWP legislation, such as the number of physicians106 or hospital beds per capita,107 would certainly not be exogenous with respect to health care expenditures per capit a. All of these instruments, therefore, are not suitable as instruments in this analysis.108 It is still possible that AWP laws themselv es are endogenous with re spect to health care expenditures per capita. If states enact these la ws as a reaction to changes in health care spending, then any estimated effect of AWP legislation will capture not only any change in spending, but also any trend that was already occurri ng. If this is true, then any estimated effect of AWP legislation would be bias ed upwards. If the likelihood th at a state would enact an AWP law is constant over time, then some of this potential bias is captured within the state fixed effects. To consider the possibility th at estimated relationships in the previous section are spurious, I examine state-specific trends before and after the change in legislation. I create a piece-wise linear function or splin e. For each state, I define year of adoption as the year in which the state adopted a pharmacy-specific AWP law. The first segment of the piece-wise linear function captures the beginning of the data period to the year of laws adoption. The second segment represents the year of adoption through the end of the data period. If AWP legislation is associated with a change or shock with respect to health care expenditure s, then we would see a 106 Marsteller et al (1997). 107 Ohsfeldt el al (1998). 108 Bound, Jaeger, and Baker (1995); Staiger and Stock (1997).

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141 change in the slope or trend line. To consider this potential change, I estimate separate regressions for each state enacting pharmacy-s pecific AWP laws by regressing the two slope coefficients on pharmaceutical expenditures per capit a. I then test the difference between these two slopes (slope1 = slope2) to determine if th ere is a statistically significant difference. Table 4-6 reports the results of this approach. Each row is a separate regression and columns (1) and (2) report the estimated slope coefficients. Column (3) reports the F-statistic for the restriction that the two coefficients are equal. This trend analysis works well for twelve of the fourteen states with pharmacy-specific AWP legi slation. In only two cases are the two slope coefficients not statistically di fferent. It appears from this com ponent of the analysis that the relationship between pharmacy-sp ecific AWP legislation and pharmaceutical expenditures per capita is not spurious. There does appear to be a change in the trend of expenditures with respect to prescription drugs when AWP laws are adopted. Robustness & Sensitivity Analysis Another form of legislation targeted at managed care organi zations is freedom of choice (FOC) legislation. FOC legislation allows mana ged care subscribers to access providers outside the managed care network, for a different fee but without having to pay the full price of care. FOC laws could increase health care costs in a similar manner to AWP laws. While my paper focuses exclusively on the effect of AWP legislation on health care expenditures, in what follows I add an indicator for FOC as an additional explanatory variable. The results presented in Table 47 and 4-8 suggest that FOC are not associated with a change in health care expenditures per capita for any of the four categorie s, and the signs and significance on the AWP coefficients are similar to the results without an FOC indicator.

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142 Conclusion While the growth in the number and enrollme nt of health maintenance organizations has reduced health care spending in some areas, it has done so thr ough cost containment strategies such as limiting patient choice. One political movement aimed at giving consumers of health care more choice has resulted in the enactment of any-willing-provider legislation. Because such state laws require a managed care organization to contract with any provider who is willing to submit to the plans terms, conditions, and reim bursement policies, patients by definition will experience more choice within their managed ca re network. A potential side effect of such legislation is an increase in h ealth care spending due to two main factors: (1) inability of managed care organization to selectively contra ct and (2) increases in administrative costs associated with contracting with more provi ders. Most any-willing-provider laws target pharmacies specifically, meaning that a managed care organization in a state with such a law would only be required to contract with a ny willing pharmacy, not any willing physician or hospital. As demonstrated through this analysis, pharmacy-specific AWP legislation is associated with an increase in pharmaceutical drug expend itures per capita. Additionally, any-willingprovider laws in general are asso ciated with increases in total personal health care expenditures (as well as pharmaceutical drug expenditures), a re sult which is consistent with prior findings.

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143 0 250 500 750 1000 1250 1500 Expenditures per capita 1987 1988 1989 1990 1991 1992 1993 1994 1995 1996 1997 1998 year avgRDrugspercap avgRPhyspercap avgRHosppercap Figure 4-1. Expenditures per capita, 1987-1998.

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144 Table 4-1. Description of state any-willing-provider (AWP) legislation State Year of Law Applicability of Law Alabama 1988 Pharmacy Arkansas 1991; 1995 Pharmacy; Physician/Hospital Connecticut 1982 Pharmacy Delaware 1994 Pharmacy Florida 1993 Pharmacy Georgia 1983 Pharmacy, Physician, Hospital Idaho 1994 Physicians, Hospital Illinois 1985 Physician Indiana 1994 Pharmacy, Physician, Hospital Kansas 1994 Pharmacy Kentucky 1994 Physicians, Hospital Massachusetts 1995 Pharmacy Minnesota 1994 Pharmacy Mississippi 1994 Pharmacy Montana 1991 Pharmacy, Hospital, Physician New Hampshire 1992 Pharmacy New Jersey 1994 Pharmacy New Mexico 1987 Pharmacy, Physician North Carolina 1993 Pharmacy North Dakota 1989 Pharmacy Oklahoma 1994 Pharmacy South Carolina 1994 Pharmacy South Dakota 1990 Pharmacy Texas 1991 Pharmacy, Hospital, Physician Virginia 1983 Pharmacy, Hospital, Physician Wyoming 1990 Pharmacy, Hospital, Physician

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145 Table 4-2. Summary statistics Variable Mean Std. Dev. Min Max Real Total Health Care per Capita 3127.51 559.35 1800.01 4912.64 Real Hospital Care per Capita 1271.50 215.30 708.48 1992.16 Real Physicians Services pe r Capita 878.09 188.03 459.11 1520.21 Real Prescription Drugs per Capita 219.87 63.02 105.26 436.85 HMO Market Share 19.06 14.62 0 74.75 HMO penetration 16.50 12.66 0 60.8 Any AWP 0.31 0.46 0 1 Pharmacy AWP 0.16 0.37 0 1 Pharmacy Plus AWP 0.11 0.31 0 1 Hospital/Physician AWP 0.04 0.18 0 1 Population Density 168.54 233.18 0.9 1093.8 Percent Over Age 65 12.54 2.09 3.34 18.59 Percent Black 9.83 9.30 0.28 36.41 Real per Capita Income 23,269 3,571 15,322 36,822 Fraction Medicare 12.99 2.22 4.33 19.55 Fraction Medicaid 9.85 3.42 1.90 22.16

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146 Table 4-3. Expenditure s per capita results (1) (2) (3) (4) Variable Name Total Hospital Physician Drugs AWP 106.44 36.31 23.51 14.90 [34.98]*** [20.74] [16.28] [6.75]** HMO Market Share 0.05 -2.89 0.72 0.44 [1.81] [0.89]***[0.83] [0.38] Population Density -1.85 -0.93 0.05 -0.01 [1.92] [0.95] [0.28] [0.23] Percent Black 124.51 46.62 4.34 27.72 [70.99]* [31.96] [14.54] [16.17]* Real income per capita 0.11 0.05 0.02 0.01 [0.03]*** [0.02]***[0.01]** [0.01]* Unemployment Rate 42.85 11.29 22.17 -0.24 [9.97]*** [5.64]* [4.90]*** [2.06] Population Over 65 63.36 42.84 0.07 6.72 [43.91] [24.33]* [22.64] [9.61] Observations 600 600 600 600 R-squared 0.98 0.96 0.97 0.96 State Fixed Effects X X X X Year Fixed Effects X X X X Clustered standards errors (at the state-level) in brackets; weighed by the state population. significant at 10%; ** significant at 5%; *** significant at 1%

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147 Table 4-4. Expenditures per capita results with fractions of government insurance (1) (2) (3) (4) Variable Name Total Hospital Physician Drugs AWP 103.51 34.11 23.78 14.67 [35.88]*** [20.72] [16.62] [6.87]** HMO Market Share 0.22 -2.63 0.62 0.45 [1.73] [0.83]***[0.74] [0.40] Population Density -1.67 -0.8 0.03 -0.079 [1.93] [0.96] [0.29] [0.23] Percent Black 126.17 42.74 8.15 28.45 [71.61]* [33.09] [14.69] [15.93]* Real income per capita 0.11 0.05 0.02 0.01 [0.03]*** [0.02]***[0.01]** [0.01]* Unemployment Rate 41.33 12.11 20.77 -0.59 [10.36]*** [5.62]** [4.77]*** [1.96] Fraction Medicare 8.98 10.12 -4.49 -0.26 [7.09] [3.88]** [3.22] [1.25] Fraction Medicaid 3.84 -0.99 1.96 0.39 [4.79] [1.92] [2.37] [0.73] Observations 600 600 600 600 R-squared 0.98 0.96 0.98 0.96 State Fixed Effects X X X X Year Fixed Effects X X X X Clustered standards errors (at the state-level) in brackets; weighed by the state population. significant at 10%; ** significant at 5%; *** significant at 1%

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148 Table 4-5. Expenditures per cap ita results with heterogeneous applicability of AWP law (1) (2) (3) (4) Variable Name Total Hospital Physician Drugs Pharmacy AWP 108.5 28.89 27.05 14.65 [40.04]*** [24.22] [20.94] [7.86]* Pharmacy Plus AWP 10.53 13.67 4.89 12.03 [28.10] [18.11] [7.27] [6.55]* Hospital/Physician AWP 179.03 80.82 41.65 21.12 [91.33]* [35.85]** [29.70] [11.51]* HMO Market Share 0.04 -2.66 0.58 0.43 [1.76] [0.85]*** [0.74] [0.40] Population Density -1.69 -0.404 -0.77 -0.079 [1.95] [0.355] [0.94] [0.23] Percent Black 124.94 42.342 43.69 28.35 [71.83]* [32.856] [33.07] [16.17]* Real income per capita 0.11 0.052 0.05 0.01 [0.03]*** [0.017]***[0.02]*** [0.01]* Unemployment Rate 41.06 11.254 12.03 -0.64 [10.34]*** [5.503]** [5.55]** [1.97] Fraction Medicare 9.68 10.642 10.4 -0.2 [7.06] [3.831]***[3.90]** [1.26] Fraction Medicaid 3.56 -0.839 -1.03 0.41 [4.73] [1.936] [1.92] [0.72] Observations 600 600 600 600 R-squared 0.98 0.96 0.98 0.96 State Fixed Effects X X X X Year Fixed Effects X X X X Clustered standards errors (at the state-le vel) in brackets; weighted by the state population. significant at 10%; ** significant at 5%; *** significant at 1%

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149 Table 4-6. Spline regression results* (1) (2) (3) State Slope 1 Slope 2 F-statistic Slope 1 = Slope 2 Alabama -9.01 15.78 1.69 Delaware 12.05 39.05 46.51 Florida 13.02 33.11 54.90 Kansas 10.84 21.95 36.42 Massachusetts 12.60 30.67 40.71 Minnesota 9.99 25.57 49.73 Mississippi 10.96 24.91 23.76 New Hampshire 10.19 19.03 5.57 New Jersey 16.88 33.81 42.32 North Carolina 8.31 24.18 42.59 North Dakota 7.71 14.36 2.69 Oklahoma 11.07 22.22 51.36 South Carolina 10.85 30.66 172.56 South Dakota 10.98 12.41 0.15 *Each row is a separate regression.

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150 Table 4-7. Expenditures per capita results with freedom of choice (FOC) indicator (1) (2) (3) (4) Variable Name Total Hospital Physician Drugs AWP 97.5 26.1 26.03 16.6 [34.49]*** [19.85] [18.67] [6.69]** FOC 25.43 33.84 -9.54 -8.17 [27.88] [21.24] [12.42] [5.56] HMOMarket 0.27 -2.57 0.61 0.44 [1.72] [0.82]***[0.73] [0.40] Population Density -1.73 -0.88 0.05 0.02 [1.98] [1.00] [0.28] [0.23] Percent Black 128.07 45.27 7.43 27.84 [71.64]* [32.18] [14.47] [15.94]* Real income per capita 0.11 0.05 0.02 0.01 [0.03]*** [0.02]***[0.01]** [0.00]** Unemployment Rate 40.91 11.55 20.93 -0.46 [10.12]*** [5.24]** [4.82]*** [1.86] Fraction Medicare 8.15 9.02 -4.18 0.01 [6.94] [3.84]** [3.01] [1.26] Fraction Medicaid 3.94 -0.86 1.93 0.36 [4.74] [1.80] [2.35] [0.75] Observations 600 600 600 600 R-squared 0.98 0.98 0.98 0.96 State Fixed Effects X X X X Year Fixed Effects X X X X Clustered standards errors (at the state-level) in brackets; weighed by the state population. significant at 10%; ** significant at 5%; *** significant at 1%

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151 Table 4-8. Expenditures per capita results with heterogeneous applicability of AWP law and FOC indicator. (1) (2) (3) (4) Variable Name Total Hospital Physician Drugs Pharmacy AWP 100.84 18.19 29.93 16.84 [38.08]** [22.09] [23.98] [7.86]** Pharmacy Plus AWP 14.33 18.99 3.45 10.95 [29.46] [19.21] [7.95] [6.24]* Hospital/Physician AWP 179.81 81.91 41.36 20.89 [94.91]* [40.47]** [28.42] [10.73]* FOC 26.8 37.45 -10.1 -7.65 [28.06] [22.64] [13.65] [5.99] HMOMarket 0.11 -2.57 0.55 0.41 [1.75] [0.84]*** [0.73] [0.40] Population Density -1.75 -0.85 0.04 0.01 [2.00] [0.98] [0.29] [0.23] Percent Black 127.47 47.22 6.73 27.63 [71.96]* [32.01] [13.86] [16.21]* Real income per capita 0.11 0.05 0.02 0.01 [0.03]*** [0.02]*** [0.01]** [0.00]* Unemployment Rate 40.66 11.47 20.89 -0.53 [10.07]*** [5.17]** [4.92]*** [1.87] Fraction Medicare 8.79 9.14 -4.00 0.06 [6.86] [3.89]** [2.96] [1.26] Fraction Medicaid 3.7 -0.83 1.85 0.37 [4.69] [1.80] [2.36] [0.73] Observations 600 600 600 600 R-squared 0.98 0.96 0.98 0.96 State Fixed Effects X X X X Year Fixed Effects X X X X Clustered standards errors (at the statelevel) in brackets; weighted by the state population. significant at 10%; ** significant at 5%; *** significant at 1%

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152 LIST OF REFERENCES American College of Obstetricians and Gyn ecologists (ACOG), ACOG Survey (ACOG News Release), July 16, 2004. Baicker, Katherine and Amitabh Chandra. The E ffect of Malpractice Liability on the Delivery of Health Care. NBER Working Paper: 10709, 2005. Bahr, William J. Although Offering More Fr eedom to Choose, Any Willing Provider Legislation is the Wrong Choice. Kansas Law Review, 45(112), 1997, 557-590. Baker, Lawrence C. and Sharmila Shankarkumar. Managed Care and Health Care Expenditures: Evidence from Medicare, 1990-1994. Frontiers in Health Policy Research: National Bureau of Economic Research 1, 1998, 117-152. Bertrand, Marianne, Esther Duflo, and Sendh il Mullainathan. How Much Should We Trust Differences-In-Differences Estimates? Quarterly Journal of Economics, 119(1), 2004, 249 275. Black, Bernard, Charles Silver, David A. Hyman, and William M. Sage. Stability, Not Crisis: Medical Malpractice Claim Outcomes in Texas, 1988-2002, Journal of Empirical Legal Studies 2(2), 2005, 207-259. Blank, Rebecca M., Christine C. George, and Rebecca A. London. State Abortion Rates: The Impact of Policies, Providers, Politics Demographics, and Economic Environment. Journal of Health Economics, 15, 1996, 513-553. Born, Patricia H., W. Kip Viscusi and Dennis W. Carlton. The Distri bution of the Insurance Market Effects of Tort Liability Reforms. Brookings Papers on Economics Activity, Microeconomics, 1998, 55-105. Bound, John, David A. Jaeger, and Regina M. Ba ker. Problems with In strumental Variables Estimation When the Correlation Between the In strument and the Endogenous Variable is Weak. Journal of the American Statistical Association, 90, 1995, 443-450. Browne, Mark J. and Robert Puelz. The Eff ect of Legal Rules on the Value of Economic and Non-Economic Damages and the Decision to File. Journal of Risk and Uncertainty, 18:2, 1999, 189-213. Bureau of Justice Statistics, M edical Malpractice Trials and Ve rdicts in Large Counties, 2001, Civil Justice Survey of State Courts, 2001. Cameron, A Colin and Pravin K. Trivedi. Microeconometrics: Met hods and Applications, Cambridge University Press, 2005. Carpenter, Christopher. Youth Alcohol Us e and Risky Sexual Behavior: Evidence from Underage Drunk Driving Laws. Journal of Health Economics 24, 2005, 613-628.

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153 Carroll, Anne and Jan M. Ambrose. Any-Willing-Provider Laws: Their Financial Effects on HMOs. Journal of Health Politics, Policy and Law, 27(6), 2002, 927-945. CBS News, Easier Morning-After Pill Access, November 24, 2003. CBS News, FDA Rejects OTC Morn ing After Pill, May 6, 2004. CBS News, The Debate Over Plan B, June 11, 2004. Cutler, David M. and Louise Sheiner. Managed Care and the Growth of Medical Expenditures. Frontiers in Health Policy Research: National Bureau of Economic Research, 1, 1998, 77-116. Danzon, Patricia. The Frequency and Seve rity of Medical Malpractice Claims. Journal of Law and Economics, 27(1), 1984, 115-148. Danzon, Patricia M. The Frequency and Seve rity of Medical Malpractice Claims: New Evidence. Law and Contemporary Problems, 49(2), 1986, 57-84. Daroch, Jacqueline E., Susheella Singh, Jennife r Frost, and the Study Team. Differences in Teenage Pregnancy Rates Among Five Developed Countries: The Roles of Sexual Activity and Contraceptive Use. Family Planning Perspectives, 33(6), 2001, 244-250. Downing, Don. Pharmacist Prescribing of Em ergency Contraception: The Washington State Experience. Emergency Contraception: The Pharmacists Role, American Pharmacists Association, 2004. Eisenberg. Theodore, John Goerdt, Brian Ostrom, David Rottman, and Martin T. Wells. The Predictability of Punitive Damages, The Journal of Legal Studies, 26(2), 1997, 623-661. Falk, Gabriella, Lars Falk, Ulf Hanson, and Ian Milson. Young Women Requesting Emergency Contraception Are, Despite Contraceptive Coun seling, a High Risk Group for New Unintended Pregnancies. Conception, 64, 2001, 23-37. Freudenheim, Milt. St. Paul Exits Medical Malpractice Insurance. The New York Times, December 13, 2001: C14. Gardner, Jacqueline S., Jane Hutchings, Timo thy S. Fuller, and Don Downing. Increasing Access to Emergency Contraception Through Community Pharmacies: Lessons from Washington State. Family Planning Perspectives, 33(4), 2001, 172-175. Girma, Sourafel and David Paton. Matching Estimates of the Impact of Over-the-Counter Emergency Birth Control on Teenage Pr egnancy, Working Paper, January 2006. Glasier, Anna and David Baird. The Effects of Self-Adminis tering Emergency Contraception. The New England Journal of Medicine, 339(1), 1998, 1-4.

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154 Glasier, Anna, Karen Fairhurst, Sally Wyke, Sue Ziebland, Pete r Seaman, Jeremy Walker, and Fatim Lakha. Advanced Provision of Emergency Contraception Does Not Reduce Abortion Rates. Conception, 69, 2004, 361-366. Gould, John. The Economics of Legal Conflicts. Journal of Legal Studies, 2(2), 1973, 279300. Graves, Karen L. and Barbara C. Leigh. The Relationship of Substance Use to Sexual Activity Among Young Adults in the United States. Family Planning Perspectives, 27, 1995, 18-22, 33. Grossman, Michael, Robert Kaestner, and Sara Markowitz. An Investigation of the Effects of Alcohol Policies on Youth STDs. NBER Working Paper 10949, 2004. Hallinan, J.T. Doctor Is Out: Attempt to Tr ack Malpractice Cases Is Often Thwarted, The Wall Street Journal, August 27, 2004: A1. Harris, Gardiner. F.D.A Approves Broader Access to Next-Day Pill. The New York Times. August 25, 2006. Hass-Wilson, Deborah. The Impact of State Abortion Restrictions on Minors Demand for Abortion. The Journal of Human Resources, 31(1), 1996, 140-158. Hellinger, Fred J. Any-Willing-Provider and Freedom-of-Choice Laws: An Economic Assessment. Health Affairs, 14, 1995, 297-302. Henshaw, Stanley K. Unintended Pr egnancies in the United States. Family Planning Perspectives, 30(1), 1998, 24-29. HR 321, Common Sense Medical Malpractice Reform Act of 2003 (Introduced in House). Hutchings, Jane, Jennifer L. Wrinkl er, Timothy S. Fuller, Jacqueline S. Gardner, Elisa S. Wells, Don Downing, and Rod Shafer. When the Morning After is Sunday: Pharm acist Prescribing of Emergency Contraceptive Pills. Journal of the American Medical Association, 53(5), 1998, 230-232. Kessler, Daniel and Mark McClellan. D o Doctors Practice Defensive Medicine? The Quarterly Journal of Economics, 111(2), 1996, 353-390. Klick, Jonathan and Thomas Stratmann. Does Me dical Malpractice Reform Help States Retain Physicians and Does it Matter? http://ssrn.com/abstract=453481 2003, accessed November 1, 2006. Klick, Jonathan and Thomas Stratmann. T he Effect of Abortion Legalization on Sexual Behavior: Evidence from Sexually Transmitted Diseases. Journal of Legal Studies, 32, 2003, 407-433.

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155 Lee, Han-Duck, Mark Browne, and Joan T. Schm itt. How Does Joint and Several Tort Reform Affect the Rate of Tort Filling? Evidence from the State Courts. The Journal of Risk and Insurance, Tort Reform Sympos ium, 61(2), 1994, 295-316. Levine, Philip B. The Sexual Activity and Birth-Control Use of American Teenagers. Risky Behavior Among Youths, ed. Jonathan Gruber, 2001, 167-217. Levine, Phillip B. and Douglas Staiger. Abor tion as Insurance. NBER Working Paper 8813, http://www.nber.org/papers/w8813 2002, accessed June 15, 2006. Levine, Phillip B., Amy B. Trainor, and David J. Zimmerman. The Effect of Medicaid Abortion Funding Restrictions on Abortions Pregnancies, and Births. Journal of Health Economics, 15, 1996, 555-578. Landes, William M. An Economic Analysis of the Courts. Journal of Law and Economics, 14(1), 1971, 61-107. Marsteller, Jill A. et al. The Resurgence of Selective Contracting Restrictions. The Journal of Health Politics, Policy, and Law, 22(5), 1997, 1133-1189. Matsa, David. A. Does Malpra ctice Liability Keep the Doct or Away? Evidence from Tort Reform Damage Caps. Working Paper, March 2, 2005. McLaughlin, Catherine G. HMO Growth and Hospital Expenses and Use: A SimultaneousEquation Approach. Health Services Research, 22(2), 1987, 183-205. Miceli, Thomas. The Economic Approach to Law. Stanford: Stanford University Press, 1997. Morrisey, Michael A. and Robert L. Ohsfel dt. Do Any Willing Provider and Freedom of Choice Laws Affect HMO Market Share? Inquiry, 40(4), 2003/2004, 362-374. National Center for State Courts. Exa mining the Work of State Courts, 2003. New, Michael J. The Effect of State Regulatio ns on Health Insurance Premiums: A Preliminary Analysis. The Heritage Foundation, www.heritage.org ., 2005, accessed January 12, 2007. Ohsfeldt, Robert L. et al. The Spr ead of State Any Willing Provider Laws. Health Services Research, 33(5), 1998, 1537-1562. Paton, David. The Economics of Fam ily Planning and Underage Conceptions. Journal of Health Economics, 21, 2002, 207-225. Paton, David. Random Behavior or Rational Choice? Family Pl anning, Teenage Pregnancy and STIs. Sex Education: Sexuality, Society, and Learning 6, 2006, forthcoming. Posner, Richard A. Economic Analysis of Law. New York: Aspen Publishers, 2002.

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156 Raine, Tina R., Cynthia C. Cooper, Corinne H. Rocca, Richard Fischer, Na ncy Padian, Jeffrey D. Klausner, and Philip D. Darney. Direct Access to Emergency Contraception Through Pharmacies and Effect on Unintended Pregnancy and STIs. Journal of the American Medical Association, 293(1), 2005, 54 -62. Rashad, Inas and Robert Kaestner. Teenage Se x, Drugs, and Alcohol Us e: Problems Identifying the Cause of Risky Behaviors. Journal of Health Economics, 23, 2004, 493-503. Rees, Daniel I., Laura M. Argys, and Susan Averett. New Evidence on the Relationship Between Substance Use and Adolescent Sexual Behavior. Journal of Health Economics, 20, 2001, 835-845. Rubin, Paul H. and Shepherd, Joanna, "Tort Reform and Accidental Deaths" Emory Law and Economics Research Paper No. 05-17 at http://ssrn.com/abstract=781424 2005, accessed January 27, 2006. Sen, Bisakha. An indirect test for whether restricting Medicai d funding for abortion increases pregnancy-avoidance behavior. Economic Letters, 81, 2003, 155-163. Sen, Bisakha. A Preliminary Investigation of th e Effects of Restricti ons on Medicaid Funding for Abortions on Female STD Rates. Health Economics, 12, 2003, 453-464. Sen, Bisakha. Can Beer Taxes Affect Teen Pregnancy? Evidence Ba sed On Teen Abortion Rates and Birth Rates. Southern Economic Journal, 70(2), 2003, 328-343. Silverman, Rachel Emma. So Sue Me: Doctor s Without Insurance; As Premiums Rise, Physicans Drop Malpractice Coverage; What it Means for Patients. Wall Street Journal, January 28, 2004: D1. Smith, Cynthia. Retail Prescription Drugs In The National Health Accounts. Health Tracking, 23(1), 2004, 160-167. Staiger, Douglas and James H. Stock. Ins trumental Variables Regression With Weak Instruments. Econometrica, 65(3), 1997, 557-586. Thorpe, Kenneth E. The Medica l Malpractice Crisis: Recent Tr ends and the Impact of State Tort Reforms. Health Tracking, January 21, 2004. Viscusi, W. Kip and Patricia Born. Medical Ma lpractice Insurance in the Wake of Liability Reform. The Journal of Legal Studies, 24(2), 1995, 463-490. Vita, Michael G. Regulatory Restrictions on Sel ective Contracting: An Empirical Analysis of Any-Willing-Provider Regulations. Journal of Health Economics, 20, 2001, 955-966. Wagner, Andrew H. Md. Doctors Hoping for Ma lpractice Relief; High Premiums Have Some Mulling Leaving State. The Washington Post, November 30, 2004: B04.

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157 Wells, Elisa S., Jane Hutchings, Jacqueline S. Gar dner, Jennifer L. Wrinkler, Timothy S. Fuller, Don Downing, and Rod Shafer. Using Pharmacies in Washington State to Expand Access to Emergency Contraception. Family Planning Perspectives, 30(6), 1998, 288-290. Wooldridge, Jeffrey M. Econometric Analysis of Cr oss Section and Panel Data. Cambridge: MIT Press, 2002. Yoon, Albert. Damage Caps and Civil Litigatio n: An Empirical Study of Medical Malpractice Litigation in the South. American Law and Economics Review, 3(2), 2001, 199-227. Zezima, Katie. National Briefing New England: Massachusetts: Contraceptives Must Be Stocked. New York Times, February 15, 2006: A20. Zimmerman, Ann. Wal-Mart to Stoc k Emergency Contraception Pill. The Wall Street Journal, March 4, 2006: A6.

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158 BIOGRAPHICAL SKETCH Christine Ann Piette graduated from Emory University with a Bachelor of Arts in economics. She earned her degree with highest honors after completing and defending a thesis on the labor market effects of earning a GED ve rsus a high school diploma. After completing her degree at Emory, Christine worked as a research assistant for a management consulting firm in Tallahassee, Florida for one year. In 2003, Christine began the graduate program at the University of Florida in the Department of Economics. After two years of coursework and successful completion of field examinations, Christine earned her Master of Ar ts in economics. Both during her coursework and in the two years following, Christine was em ployed by the department as both a research assistant and a teaching assistant. Additionally, Ch ristine served as a teaching assistant for an executive level MBA course during two consecutive years. In the fall of 2006, Christine was an instructor for an upper-level el ective, government regulation of business, within the economics department. After successful completion of all re quirements for her degree, Christine will earn the Doctor of Philosophy degree in August 2007. She has accepted an assistant professor position at the University of Nort h Carolina at Chapel Hill wher e she will begin in the fall of 2007.