Citation
Quasi-Experimental Studies in Health Economics

Material Information

Title:
Quasi-Experimental Studies in Health Economics
Creator:
Woodworth, Lindsey J
Place of Publication:
[Gainesville, Fla.]
Publisher:
University of Florida
Publication Date:
Language:
english
Physical Description:
1 online resource (145 p.)

Thesis/Dissertation Information

Degree:
Doctorate ( Ph.D.)
Degree Grantor:
University of Florida
Degree Disciplines:
Economics
Committee Chair:
HAMERSMA,SARAH ELLEN
Committee Co-Chair:
HAMILTON,JONATHAN H
Committee Members:
KNAPP,CAPRICE ANGANETTE
BROWN,DAVID T
Graduation Date:
5/3/2014

Subjects

Subjects / Keywords:
Bandwidth ( jstor )
College diplomas ( jstor )
Health care industry ( jstor )
High school diplomas ( jstor )
Hospitals ( jstor )
Insurance ( jstor )
Managed care ( jstor )
Medicaid ( jstor )
Receipts ( jstor )
Triage ( jstor )
Economics -- Dissertations, Academic -- UF
dissertation
Duval County ( local )
Genre:
Electronic Thesis or Dissertation
bibliography ( marcgt )
theses ( marcgt )
Economics thesis, Ph.D.

Notes

Abstract:
This dissertation addresses three questions in health economics using quasi-experiments. Such identification procedures allow me to overcome the inherent endogeneity concerns that frequently plague many health-related studies. In doing so, the estimates generated by this body of research can be interpreted as causal effects. In chapter one, instrumental variable estimation is used to measure hospital compliance with the Emergency Medical Treatment and Active Labor Act. Chapter two estimates predictors of physical wellness using regression discontinuity and considers possible mechanisms which might contribute to these relationships. Finally, chapter three uses triple difference estimation to examine the financial effects of Florida's Medicaid Reform Pilot Program. Each of these issues are timely concerns for U.S. policymakers, making unbiased estimates particularly important for crafting legislation. ( en )
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.
Thesis:
Thesis (Ph.D.)--University of Florida, 2014.
Local:
Adviser: HAMERSMA,SARAH ELLEN.
Local:
Co-adviser: HAMILTON,JONATHAN H.
Statement of Responsibility:
by Lindsey J Woodworth.

Record Information

Source Institution:
University of Florida
Holding Location:
University of Florida
Rights Management:
Copyright by J Woodworth. Permission granted to University of Florida to digitize and display this item for non-profit research and educational purposes. Any reuse of this item in excess of fair use or other copyright exemptions requires permission of the copyright holder.
Embargo Date:
12/31/2016
Classification:
LD1780 2014 ( lcc )

Downloads

This item has the following downloads:


Full Text

PAGE 1

QUASI EXPERIMENTAL STUDIES IN HEALTH ECONOMICS By LINDSEY WOODWORTH 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 2014

PAGE 2

2014 Lindsey Woodworth

PAGE 3

To everyone that has patiently read my papers and shared the sentiments of a friend, who (half

PAGE 4

4 ACKNOWLEDGMENTS The first two people that deserve an enormous amount of acknowledgement are my parents. I am credibly grateful to have a mom and dad that encouraged me when school was rough, prayed for me daily, and told me that I could always, just come home if the P uh h uh D uh d id I also could not have asked for a better group of economics faculty to work with. I am so, so grateful for the help, encouragement, and patience of my advisor, Sarah Hamersma. Her example, inside and outside of the classroom, h as been a beautiful picture to me of what it looks like to faithfully live out life in academia. I would also like to sincerely thank my professor, Jonathan Hamilton. Graduate school is so much easier (and enjoyable ) having a kind hearted genius across the hall. Caprice Knapp also deserves much recognition for all of her invaluable help and advice. Outside of the economics department, I would like to express my sincere gratitude to Professor Jed Keesling in the mathematics department. It is rare that a professor on the other side of campus will invite a graduate student (who he should otherwise have no interest in) over to his office to talk about research during spring break. It is rarer yet when, out of that conversation, there comes a concerted ef fort to make real life changes in real life hospitals so that real live people are actually helped. It is has been more challenging than I can say to watch someone whose enthusiasm and love for his discipline is matched only by his enthusiasm and love for the One who made his discipline and the people in his path. I am blessed to be one of those people. Finally, there is a dear couple in Gainesville that deserves much more than a pithy little dissertation acknowledgement. But, nevertheless, here I go. I am deeply thankful for Paul and Donna Miller. Between their chickens which I now know by name, their unselfish schedule,

PAGE 5

5 and their ever open chair at the table, they have made Gainesville feel like home. I hope my time is half as generously, and my he art half as big, as theirs has been to me. Most of all, I know that all of these people, all of these opportunities, and all of life itself, has been given to me as an undeserved gift. For all of this, I am most thankful to God. Psalm 34:3

PAGE 6

6 TABLE OF CONTENTS page ACKNOWLEDGMENTS ................................ ................................ ................................ ............... 4 LIST OF TABLES ................................ ................................ ................................ ........................... 8 LIST OF FIGURE S ................................ ................................ ................................ ....................... 10 LIST OF ABBREVIATIONS ................................ ................................ ................................ ........ 11 A BSTRACT ................................ ................................ ................................ ................................ ... 12 CHAPTER 1 THE DOCTOR THE EFFECT OF INSURANCE COVERAGE ON ED WAIT TIME ................................ ............................... 13 1.1 Introduction ................................ ................................ ................................ ....................... 13 1.2 Timeliness of Care and Government Regulation ................................ .............................. 15 1.3 Existing Literature on Health Insurance and Timeliness of Care ................................ ..... 17 1.4 The National Hospital Ambulatory Medical Care Survey and Sample Selection ............ 20 1.5 Estimation ................................ ................................ ................................ ......................... 22 1.5.1 The Direct Effect of Payer Source on Wait Time ................................ .................. 22 1.5.2 The Effect of Payer Source on Triage Assignment ................................ ................ 26 1.6 The Net Effect of Under Insurance on Wait Ti me ................................ ........................... 37 1.7 Conclusion ................................ ................................ ................................ ........................ 38 2 SMART AS A WHIP AND FIT AS A FIDDLE: THE CAUSAL EFFECT OF A DIPLOMA ON HEALTH ................................ ................................ ................................ ...... 52 2.1 Introduction ................................ ................................ ................................ ....................... 52 2.2 Literature Review ................................ ................................ ................................ ............. 54 2.3 Background ................................ ................................ ................................ ....................... 56 2.3.1 Conscrip tion in WWII ................................ ................................ ............................ 57 ................................ ................................ ................................ ... 58 2.4 Data ................................ ................................ ................................ ................................ ... 60 2.5 Estimation ................................ ................................ ................................ ......................... 62 2.5.1 Identification Procedure ................................ ................................ ......................... 62 2.5.2 Specification ................................ ................................ ................................ ........... 64 2.6 Results ................................ ................................ ................................ ............................... 68 2.6.1 First Stage Results ................................ ................................ ................................ .. 68 2.6.2 Wald Estimates ................................ ................................ ................................ ....... 71 2.7 Disc ussion ................................ ................................ ................................ ......................... 74 2.7.1 Educational Opportunities for Returning WWII Veterans ................................ ..... 75 2.7.2 Veteran Status Effects ................................ ................................ ............................ 77 2.7.3 Local Average Treatment Effects ................................ ................................ ........... 78

PAGE 7

7 2.8 Conclusion ................................ ................................ ................................ ........................ 79 3 RAISING THE BOTTOM LINE: THE EFFECT OF MEDICAID MANAGED CARE ON SAFETY NET HOSPITALS ................................ ................................ ........................... 96 3.1 Introduction ................................ ................................ ................................ ....................... 96 3.2 Background ................................ ................................ ................................ ....................... 99 3.2.1 The Affordable Care Act and Safety Net Hospitals ................................ ............... 99 ................................ ........................... 101 3.2.3 The Link Between Medicaid Managed Care and Safety Net Hospitals ............... 102 3.3 Data ................................ ................................ ................................ ................................ 104 3.4 Identification Procedure ................................ ................................ ................................ .. 105 3.5 Estimation ................................ ................................ ................................ ....................... 109 3.6 Results ................................ ................................ ................................ ............................. 112 3.7 Discussion ................................ ................................ ................................ ....................... 115 3.8 Conclusion ................................ ................................ ................................ ...................... 119 APPENDIX : ADDITIONAL TABLES AND FIGURES ................................ .......................... 131 LIST OF REFERENCES ................................ ................................ ................................ ............. 139 BIOGRAPHICAL SKETCH ................................ ................................ ................................ ....... 145

PAGE 8

8 LIST OF TABLES Table page 1.1 Variables l ist ................................ ................................ ................................ ...................... 41 1 2 R easons for v isit ................................ ................................ ................................ ................. 42 1 3 Wait t ime (in minutes) Tobit ................................ ................................ ........................... 43 1 4 First s tage: e ffect of o ffice h ours on b eing u nder i nsured. ................................ ................ 44 1 5 Fraction of i ndividuals who a ppear at the ED who are u nder i nsured, by o ffice h ours .... 45 1 6 Distribution of t riage s cores and s elf a ssessment m easures, by i nsurance s tatus and o ffice r ours ................................ ................................ ................................ ......................... 45 1 7 IV i nterval r egression: Effect of b eing u nder i nsured on t riage m inute a ssignment ......... 46 1 8 IV o rdered p robit: Effect of b eing u nder i nsured on t riage c ategory. ............................... 47 1 9 2SLS: Effect of b eing u nder i nsured on t riage m inute a pproximation. ............................. 48 1 10 2SLS: Effect of b eing u nder i nsured on t riage c ategory. ................................ .................. 49 1 11 2SLS: Probability of b eing a ssigned a h igher t riage c ategory ................................ ........... 50 1 12 Approximate n et e ffect of b eing u nder i nsured on w ait t ime ................................ ............ 51 2 1 WWII d raft r egistrations ................................ ................................ ................................ .... 88 2 2 Descriptive s tatistics ................................ ................................ ................................ .......... 89 2 3. Hypothesized o utcomes ................................ ................................ ................................ ..... 90 2 4 First s tage e stimates ................................ ................................ ................................ ........... 91 2 5 Wald e stimates: High s chool d iploma ................................ ................................ ............... 93 2 6 Wald e stimates: College d iploma ................................ ................................ ...................... 94 2 7 OLS e stimates ................................ ................................ ................................ .................... 95 3 1 Pre r eform N, a mong r eform c ounty r esidents ................................ ............................... 122 3 2 Post r eform N, a mong r eform c ounty r esidents ................................ .............................. 122 3 3 Means ................................ ................................ ................................ ............................... 123 3 4 DDD ( u nadjusted) e stimate for the r e ffect on u ninsured ................................ ... 124

PAGE 9

9 3 5 DDD ( u nadjusted) e stimate for the r e ffect on Medicaid ................................ .... 125 3 6 DDD ( u nadjusted) e stimate for the r e ffect on p rivately i nsured ........................ 126 3 7 DDD ( u nadjusted) e stimate for the r e ffect on t otal g ross c harges ..................... 127 3 8 DDD ( u nadjusted) e stimate for the r e ffect on m oney r eceived .......................... 128 3 9 DDD ( u nadjusted) e stimates for the e ffects of the r eform ................................ ............... 129 3 10 DDD ( a djusted) e stimates for the e ffects of the r eform ................................ ................... 130 A 1 Non i nstrumented e ffect of b eing u nder i nsured on t riage ................................ .............. 131 A 2 (Analogous to Table 1 4, but with restricted sample) ................................ ...................... 132 A 3 (Analogous to Table 1 7, but with restricted sample) ................................ ...................... 133 A 4 (Analogous to Table 1 8, but with restricted sample) ................................ ...................... 134 A 5 Wald e stimates for h ealth o utcomes : College d iploma ( i ndividual t hresholds) .............. 135 A 6 Wald e stimates for h ealthcare u sage: College d iploma ( i ndividual t hresholds) .............. 137

PAGE 10

10 LIST OF FIGURES Figure page 2 1 Registration a ge, by d ate of b irth ................................ ................................ ....................... 83 2 2 Running v ariable and t reatment a ssignment, by i nstrument ................................ .............. 84 2 3 Regression a djusted MOB m eans for t otal y ears of e ducation ................................ .......... 85 2 4 s e ffects on r egression a djusted MOB m eans ................................ ................. 85 2 5 r e ffects on r egression a djusted MOB m eans: H igh s chool d iploma ....... 86 2 6 r ef fects on r egression a djusted MOB m eans: C ollege Diploma ............. 87 3 1 Map of r eform c ounties ................................ ................................ ................................ .... 121 3 2 Possible e ffects of Medicaid m anaged c are r eform on h ospital p atrons ........................ 121 A 1 Wait t ime d istributions, by t riage a ssignment ................................ ................................ .. 131

PAGE 11

11 LIST OF ABBREVIATIONS 2SLS Two stage least squares ACA Affordable Care Act CDC Centers for Disease Control and Prevention COBRA Consolidated Omnibus Budget Reconciliation Act DD Difference in differences DDD Difference in difference in differences DSH Disproportionate share hospital. ED Emergency department EMTALA Emergency Medical Treatment and Active Labor Act GED General Education Development IOM Institute of Medicine IV Instrumental variable NHAMCS National Hospital Ambulatory Medical Care Survey NHIS National Health Interview Survey OLS Ordinary least squares PCP Primary care physician PSU Primary sampling unit RD Regression discontinuity WWII World War II

PAGE 12

12 Abstract of Dissertation Presented to the Graduate School of the University of Florida in Partial Fulfillment of the Requirements for the Degree of Philosophy QUASI EXPERIMENTAL STUDIES IN HEALTH ECONOMICS By Lindsey Woodworth May 2014 Chair: Sarah E. Hamersma Major: Economics This dissertation addresses three questions in health economics using quasi experiments. Such identification procedures allow me to overcome the inherent endogeneity concerns that frequently plague many health related studies. In doing so, the estimates generated by this body of research can be interpreted as causal effects. In chapter one, instrumental variable estimation is used to measure hospital compliance with the Emergency Medical Treatment and Active Labor Act. Chapter two estim ates predictors of physical wellness using regression discontinuity and considers possible mechanisms which might contribute to these relationships. Finally, chapter three uses triple difference estimation to icaid Reform Pilot Program. Each of these issues are timely concerns for U.S. policymakers, making unbiased estimates particularly important for crafting legislation.

PAGE 13

13 CHAPTER 1 E EFFECT OF INSURANCE COVERAGE ON ED WAIT TIME The Emergency Medical Treatment and Active Labor Act (EMTALA) requires that Medicare participating hospitals screen and stabilize all individuals appearing in their emergency departments, regardless of expecte d compensation. To counter the incentive to prioritize revenue generating patients, the law also prohibits facilities from delaying care to under insured individuals. I estimate whether timeliness of emergency care is, in fact, unaffected by payer source as mandated. Using the National Hospital Ambulatory Medical Care Survey, I first examine the direct effect of under insurance and find that under insurance is associated with an approximately 6 10% increase in emergency department wait time. Because o f concerns that the effects of under insurance may be mediated by triage assignment, I subsequently estimate the relationship between under insurance and triage assignment, using the office hours of general practitioners as an exogenous source of variation in payer source. Instrumental variable results suggest that under insured patients are inexplicably assigned higher triage scores which are known to lengthen waits. Contrary to the stipulations of EMTALA, discrepancies in timeliness of care do exist. Y et, this noncompliance is not readily apparent; roughly 80% of the increase in under insured individuals' wait times are masked by adjustments to triage scores. 1. 1 Introduction In 1986, the U.S. federal government passed the Emergency Medical Treatment an d Active Labor Act (EMTALA) which required emergency departments (EDs) to provide care to individuals regardless of their ability to pay. Specifically, the mandate required Medicare participating hospitals to indiscriminately screen and stabilize all indiv iduals appearing at

PAGE 14

14 individuals not covered by health insurance. The direct effects of EMTALA were three fold. First, as was intended, the composition of ED pat rons changed to include a greater proportion of uninsured individuals. Second, overall ED patient loads increased due to the influx of uninsured individuals. Third, many facilities were forced out of business as a result of the striking shift in reimbursem ent patterns. That is, because EMTALA essentially forced emergency facilities to provide uncompensated care to many uninsured patients, not all hospitals were able to absorb the ensuing losses coming from their EDs. As might be expected, the enactment of E MTALA resulted in gross overcrowding within emergency departments. In a 2001 Report to Congressional Committees assessing the perhaps nowhere have overcrowding concerns been more substantiated than in long delays. As of 2010, the average ED wait time in the U.S. exceeds four hours. The reality of overcrowding in EDs has dealt emergency medical staff the challenge of sorting patients so as to expedite the care given to those with the most pressing needs. If done efficiently, this should result in a direct correlation between individu acuteness of their conditions. However, a troubling prospect is that wait times are systematically hospitals from delaying care to make payer source inquires, there remains a conflict between

PAGE 15

15 discrepancies in wait times exist between under insured populations and their counterparts, which cannot be accounted for by medical factors. To estimate the causal effect of payer source on ED wait time, this study exploits the fact that the EMTALA mandate was directed exclusively at emergency facilities. Because non emergency healthcare providers are allowe d to deny treatment to individuals with certain types (or lack of) health insurances, well insured patients are often filtered out of EDs during the times when non emergency physicians are available. This paper, therefore, uses the office hours of general assessment (as measured by acuity of pain and reason(s) for visit). The results are striking. While the direct effect of under insurance is found to be an approximately 6 10% increase in wait time, this direct effect accounts for roughly one fifth of the total increase in under insured indirectly prolong waits. These findings suggest that, contrary to the stipulations of EMTALA, timeliness of emergency care is affected by compensation patterns, and the full effect of payer source is being masked by discriminatory triage assignments. 1. 2 Timeliness of Care and Government Regulation In 2001, the Institute of Medicine (IOM) identified timeliness of care as one of their six aims for improvement in the 21st century. Additionally, the Institute suggested that if these aims were to be realized, it would be necessary to have a care system build on the foundation of a Yet, timeliness of care is by no means a hallmark of emergency departments. In 2011, year old girl wi th a failing liver who waited for nearly five hours before being seen by an ER physician.

PAGE 16

16 Unfortunately, this is not an isolated occurrence. In 2009, the Government Accountability Office released a report indicating that patients in EDs often wait twice as long as recommended by triage nurses. The following year, Press Ganey released a state by state analysis of average ED wait times. Utah topped the list with an average wait time of 8 hours and 17 minutes, while the national average came in at a distu rbing 4 hours and 7 minutes. As suggested by the Institute of Medicine, if timeliness of care is to be improved then it is important to recognize that many underlying factors influence how readily care is delivered. R edesigning the health care delivery system also will require changing the structures and processes of the environment in which health professionals and organizations func tion. This includes: Aligning payment policies with quality improvement: Although paym ent is not the only factor that influences provider and patient behavior, it is an important one. f all types Here, it is interesting to note that while emergency department s are distinct because of their notoriously long waits, they are also unique within the medical world due to the especially disparate returns they generate. This is largely attributable to the stipulations of EMTALA. EMTALA, an amendment to the Consolid ated Omnibus Budget Reconciliation Act (COBRA), was passed in 1986 in an attempt to protect low income individuals. This law created strict guidelines for hospitals participating in the Medicare program. First, the law required emergency departments to p rovide medical screenings to every individual appearing at an emergency facility: In the case of a hospital that has a hospital emergency department, if any individual behalf for e xamination or treatment for a medical condition, the hospital must provide for an appropriate medical screening examination within the capability of

PAGE 17

17 available to the emergency depa rtment, to determine whether or not an emerg ency medical condition exists. provide stabilizing examinations and treatment. Furthermore: A participating hospi tal may not delay provision of an appropriate medical of payment or insurance status. Although the law placed obvious financial restrictions on hospitals, EMTALA was an unfunded ma compliance. Surprisingly, a number of hospitals found compliance unaffordable and subsequently closed. The American Hospital Association reports that between 1991 and 201 0, the number of U.S. emergency departments in operation fell by 11% (from 5,108 to 4,564). During this same time, the number of ED visits rose from 88.5M to 127.2M (an increase of 61 ED visits per 1,000 individuals). This led to a 61% increase in the numb er of patients per emergency facility. 1. 3 Existing Literature on Health Insurance and Timeliness of Care Given the link drawn by the IOM between timeliness of care and provider compensation, it is surprising that, although wait times are disproportionatel y long in EDs and compensation patterns are particularly varied, no formal inquiries have been made as to whether differences in payer source directly translate to differences in ED wait times. There have, however, been a number of studies which motivate this analysis. Outside of the ED, various researchers highlight differences in wait time across payer source. Roll et al. (2012) use German data to estimate the effect of insurance type on outpatient wait time. Their study finds that private insurance si gnificantly reduces wait time in general

PAGE 18

18 Medicare and Medicaid on access to dermatological care, finding that individuals covered by Medicaid experience signif icantly longer wait times, as measured by days until appointment. However, wait times for individuals covered by private insurance are found to be comparable to those covered by Medicare. Within the ED, considerable attention has also been paid to the e ffects of payer source on the quality and quantity of health care provided. This vein of research has uncovered significant discrepancies in the care provided to the uninsured. For example, a number of studies find insurance to adversely affect hospital admission from the ED. Among these are Ruger et al. (2003), Sox et al. (1998) and White et al. (2007). White et al. additionally find that insurance affects the number of radiology tests ordered for ED patients. This research followed the Institute of M widespread inconsistencies in the health of, and care given to, the uninsured relative to the insured. In terms of the study at hand, there are two papers which bear consid erable importance. Wilper et al. (2008) and James et al. (2005) use the same data as the present study to model ED wait time. While James et al. use pediatric observations to focus on the effect of race and ethnicity on wait time, they control for payer source. This yields insurance coefficients which can be roughly interpreted as the correlation between insurance and ED wait time. These estimates cannot, however, be interpreted as causal effects due to the set up of the model. Nonetheless, James et al find that, compared to the privately insured, government sources of payment are associated with 10% increases in wait time, self payment with 12% increases in wait time, and other non private sources of payment with 29% increases in wait time.

PAGE 19

19 Furthermo re, the paper finds unadjusted differences in triage assignment by race. This suggests that triage may be a less than impartial measure of severity, which I address. Wilper et al. measure the effect of several factors, including payer source, on ED wai t time. They find that being black, Hispanic, female, and appearing at an urban hospital result in longer ED wait time. They additionally find that individuals who are not charged for emergency care wait 51.6% longer than those covered by Medicare. Howe ver, they find no differences in wait time between self pay and insured individuals. Although these insurance results are stated, they are not thoroughly explored. Wilper et al. also test for the possibility that triage is an intermediate variable throug h which race/ethnicity and sex affect wait time. They find no evidence of discriminatory triage among minorities or women. They do not, however, test whether triage is an intermediate variable in the relationship between insurance and wait time. Finally, disparate treatment, Brillman et al. (1996) is relevant due to the insight it provides regarding the subjectivity of triage. By comparing inter observer agreeability between nur ses, physicians and computer guided programs, they uncover great variability in triage assignments. They also compare post examination data to original triage assignments and find that all parties perform poorly in predicting hospital admission. Whether p ayer source affects wait time in emergency departments is an important question for medical, economic and legal reasons. The lack of attention to this issue may be because (i) it is illegal for emergency facilities to discriminate on the basis of payer so urce, thereby making it an improbable occurrence, or (ii) because insured and uninsured populations are innately different, thereby making it difficult to decipher the true causal effect of payer source due to selection bias. Therefore, in the spirit of investigation, I seek to determine the

PAGE 20

20 impact of payer source on wait time through two avenues. First, the effect of being under insured is estimated directly using a tobit model where the lower limit is set at zero. Next, instrumental variable estimatio n is used to estimate whether being under insured influences triage assignment, thereby indirectly affecting wait time. 1. 4 The National Hospital Ambulatory Medical Care Survey and Sample Selection The data used in this paper come from 1997 2000 and 2003 2 004 responses to the National Hospital Ambulatory Medical Care Survey (NHAMCS). 1 This dataset comprises a cross section of patient level observations. The survey is administered to U.S. emergency and outpatient departments and includes questions related services received, medications prescribed and dispositions, among other things. Only data from the ED surveys are used in this paper. The process by which NHAMCS data is collected by the Centers for Disease Control and Prevention (CDC) involves four stages of probability sampling. First, 112 geographic regions are sampled. These are referred to as the primary sampling units (PSUs). Next, a probability sample of practicing physicians within each PSU is gene rated. This is done by selecting a sample of hospitals within each PSU, followed by a sample of service areas within each hospital. Finally, the selected physicians are divided into 52 groups, and each group is randomly assigned one week within the surve y year. Physicians then systematically select a random sample of patient visits occurring during their assigned week. Patient record forms are completed by hospital staff for each of these visits. In order to ensure that the patient record forms are fil led out correctly, field representatives are sent to each participating site. These individuals provide training to hospital 1 Data from 2001 and 2002 is not used because wait times were not measured in those years.

PAGE 21

21 staff on form completion. Once submitted, field staff check for survey completeness and make clerical edits. Inconsistencies an d errors in code ranges are also checked electronically. The sample used in this study to analyze wait times consists of individuals with known wait time and triage score, who did not leave the ED before being seen by a physician, and whose primary source of payment was either private insurance, Medicare, Medicaid, self payment or who were not charged. Individuals without recorded triage scores are not included because triage plays an enormously important role in determining timeliness of care. However, it is not clear why some individuals either did not receive a triage assessment or why their triage ranking was not recorded. As such, it seems unwise to group these individuals together and treat them as a unique triage category. The remaining sample co nsists of 92,587 observations. 2 The sample used to analyze triage assignments consists of all previous observations in addition to those with unknown wait times and/or who left the ED before being seeing by a physician. This sample consists of 118,414 o bservations. There are two possible limitations to the wait time findings which should be addressed at this point. First, although the CDC provides no formal censoring disclosure, it seems peculiar that wait times in this dataset do not exceed 10 hours. This could be because respondents were hesitant to provide evidence of excessively long wait times in their facilities, thereby giving them an incentive to compromise their reporting. However, because wait times are derived (via responses for time of arri val and time seen by a physician) rather than directly reported, this seems less likely. Therefore, if hospitals correctly reported arrival and receipt of service times, then there may be no need for concern. Also, while unavoidable, it is unfortunate th at 2 To verify that the omission of unknown triage obse rvations does not bias wait time results, independent sample t wait time predictors used in this paper, I find that the difference between the average adjusted wait time of individuals in my sample (with known triage) and the average wait time of the omitted sample (with unknown triage) is only 36 seconds.

PAGE 22

22 individuals who left the ED before being seen by a physician are not represented in the sample. This is because of the possibility that those who left early were incited to do so because of long waits, which would cause the distribution of the dependen t variable to be skewed. However, because individuals who left early account for only 0.12% of the sample, this omission does not appear to be a major concern. insuran Individuals whose primary source of payment is private insurance comprise one type of insurance category and are never treated as under insured. Individuals whose primary source of payment is either self and are always treated as under insured. 3 as either Medicaid or Medicare, then the under insured where noted. 1. 5 Estimation 1. 5.1 The Direct Effect of Payer Source on Wait Time In order to estimate treatment effects in a non experimental setting, it is necessary that all confoun ding determinants of the outcome be accounted for. This ensures comparability between the treatment and control groups so that estimates can be interpreted as causal effects. Failure to control for relevant variables, conversely, will result in biased e stimates. In the case of emergency departments, timeliness of care is generally influenced by two is a facility level factor measuring volume, 3 According to the NHAMCS instructions, the self Includes visits for which the patient is expected to

PAGE 23

23 level factor of payer source on ED wait time, it is important to recognize that treatment is not randomized insurance status. This is problematic if these characteristics also affect wait time. Therefore, in an effort to avoid selection bias, it is important to also control for individual level variables which might influence the category in which an individual falls. As such, the effect of being under insured on ED wait time is estimated usi ng the following model: 0 1 Under 2 3 4 (1 1 ) fixed effect controls. Because of existing evidence of discrimination (e.g., James et al., 2005), interactions between race/ethnicity and triage are also included in the urgency vector. Column I of Table 1 1 provides a comprehensive list of these control s. Importantly, the dependent variable in equation ( 1 1) is defined as the number of minutes measure timeliness of care from various standpoints, this specific de finition of wait time is of particular interest due to its medical impact. That is, assuming that the most valuable service provided by EDs is immediate care from a physician, then it seems reasonable that the time it takes to receive this care is the mos t consequential measure of wait. Specifically, timeliness in this sense is more imperative than timeliness of an intermediate step (e.g., time to triage). Because the dependent variable in equation ( 1 1) is inherently non negative, results are estimated using a tobit model. As a test of robustness, alternative specifications use different

PAGE 24

24 classifications of under uninsured relative to privately and/or publicly insured, or if publicly insu red relative to privately insured. 1. 5.1.1 Tobit r esults The results from equation ( 1 1) provide strong evidence that being under insured has a small but statistically significant effect on wait time (Table 1 3). Yet, the varying results across treatment classification are both interesting and surprising. Specifically, wait times are found to be less sensitive to being insured as to being privately insured. First, consider the effects of being without any insurance. Compared to the privately insured, t hose who are uninsured face wait times that are, on average, 4.2 minutes longer. This is an approximately 10% increase from the mean wait time of 44.0 minutes. However, compared to the publicly insured, the effect of being uninsured is not statistically different than zero. This is an interesting result because although individuals covered by Medicaid or Medicare technically have insurance, they are not distinguishable from those without any insurance (in terms of ED wait time). To corroborate these res ults, the publicly insured are compared to the privately insured (Column V) and it is found that individuals with public insurance do, in fact, face statistically significantly longer wait times (2.7 minutes). However, this effect is smaller than between the privately insured and the uninsured. This suggests that, in terms of ED wait time, public insurance might be a sort of intermediary between private insurance and no insurance. Column II of Table 1 3 estimates the effect of being uninsured relative to having any insurance (i.e., public or private). Here, being under insured results in a 3.1 minute delay in care. Similarly, Column IV considers the same set of individuals, but treats those with public insurance as under insured. This classification of under insured also results in a 3.1 minute

PAGE 25

25 increase in wait time. Both of these estimates are statistically significant at the 99% confidence level. It is worth noting that the variables for urgency and volume are statistically significant and of the e xpected sign. Across all specifications, a triage assignment of 15 60 minutes is associated with an approximately 16 minute increase in wait time, relative to individuals who received a triage assignment of <15 minutes. An assignment of >1 2 hours increa ses wait time by approximately 30 minutes, and an assignment of >2 24 hours increases wait time by approximately 34 minutes. 4 Additionally, arrival via an ambulance is associated with a reduction in wait time, and hospitals that are located in MSAs experi ence longer wait times. Though not surprising, these results give credence to the model. It is interesting, however, that the race/ethnicity variables are far less predictive of wait time on their own than when interacted with triage. For both blacks an d Hispanics, higher levels of triage are associated with disproportionately longer waits, with the unadjusted differences increasing with triage assignment. Although it is arguable that a 2.7 4.2 minute longer wait time in the ED for the under insured (depending on the comparison group) is a small effect, the finding is consistent: Under insured populations face longer ED wait times. Given the nature of emergency medicine, 2.7 4.2 minutes could be economically significant, but the repercussions of t his delay are certain to vary from case to case. This gives rise to the question of how these discrepancies in wait time might be explained. One possible explanation is financial inquiries. According to a 1998 news hile emergency room staff consult with health plans to 4 T he distribution of wait times across triage assignments are shown in Figure A 1 of the Appendix This distribution uses the smal ler (n=92,587) sample where observations with unknown waits and/or who left the ED before being seen by a physician are omitted.

PAGE 26

26 the insured, then it would seem plausible that the uninsured might face slightly longer wait times. Simil arly, if the uninsured are screened for Medicaid/Medicare eligibility, then this might also prolong wait times. However, such actions would be in direct contradiction to EMTALA which prohibits delaying examinations to inquire about insurance coverage. A s econd possibility, however, is that the tobit model is only picking up traces of the true effect of under insurance. A number of studies, conducted by both the Institute of Medicine as well as independent researchers, have identified discrepancies in vari ous facets of medical care based on insurance status. This raises suspicion as to whether payer source is affecting other variables rightly belonging in the wait time regression. If so, then the previously specified wait time model will not yield a net c ausal effect since the mechanism through which payer source operates has been treated independently. When considering what variables in the wait time regression might be affected by insurance status, the statistical significance of the race/ethnicity and triage interactions provides the first clue. That is, the fact that triage is not a uniform determinant of ED wait time raises a red flag. Therefore, the following section tests the hypothesis that triage assignments are systematically affected by payer source. 1. 5.2 The Effect of Payer Source on Triage Assignment tri age, is quite subjective. It is, therefore, relevant to ask whether the causal effect of payer source on wait time is being mediated by triage. If it is, then the effect of being under insured may be masked in equation ( 1 1) since the tobit model assumes that all discrepancies in triage physical conditions. If, however, the mechanism which determines urgency (i.e., triage) is

PAGE 27

27 affected by insurance status, then the effect of being under insured will have not been fully captured in the previous model. When determining triage assignments, nurses take both the type and severity of an both of these factors vary by insurance status. According to one line of reasoning, because the under insured have a greater incentive to free ride, the types of conditions that they go to the ED for are less serious and the severity of their conditions are less extreme. However, it can alternatively be argued that because the under insured know that it will be difficult for them to afford medical care, they are more likely to stay at home and worsen until medical care is absolutely necessary. In this c ase, we might expect the types of conditions for which the under insured go to the ED to be more serious and the severity of their conditions to be more extreme. To test whether triage is affected by insurance status, it would be ideal to run a regression condition. However, this is infeasible given the content of observational data. While these do include various qualitative measures which provide inform ation related to the kind of problem an individual has, they do not include a full set of biological variables needed to account for the That is, if we were to e stimate the parameters of equation ( 1 is highly probable that the under insured variable would be correlated with 0 1 Under 2 3 ( 1 2) To account for this, one alternative identification strategy is instrumental variable (IV) estimation. This allows us to identify the causal effect of being under insured by isolating the

PAGE 28

28 exogenous portion o f payer source (via the variation generated by the instrument). This avoids the problem of omitted variables bias. 5 In order for an instrumental variable model to yield a consistent estimate, two conditions must be satisfied. First, the instrument must be correlated with the endogenous variable. This is verified in the first stage. Second, conditional on the controls the instrument must be uncorrelated with the error term in the structural equation. In this case, the instrument can only be related to triage through its relationship with payer source. This requires that the instrument itself be unrelated to the seve propose as an instrument for under insurance is an indicator for whether an individual arrives at an ED during regular office hours (i.e., between 8:00am and 5:00pm, Monday through Frid ay). 1. 5.2.1 Assumption #1: The f irst s tage It has been well documented that access to primary care is highly dependent on payer source. That is, individuals with private insurance generally have a greater degree of access than do those with public insur ance, and greater yet than those who are uninsured. This is made possible by the fact that primary care physicians can refuse to provide treatment to individuals who are unable to provide compensation. The same is not true for EDs; they cannot deny care to individuals who cannot pay. Hence, the degree of substitution between primary care and emergency care should be unique for each payer source category, but this substitutability is only available during a specific window of time namely, the office hou rs of general practitioners. To understand how this instrument might affect payer source, it should first be reiterated that both emergency and primary care facilities are open during regular office hours. However, while emergency care is available to e veryone during this time period, primary care is not. 5 The non instrumented triage results from equation (3 2) are presented in the appendix (Table A 1 ) only for comparison to the results obtained using IV estimation.

PAGE 29

29 Although primary care physicians (PCPs) widely accept private insurance, not all PCPs accept Medicare/Medicaid, and PCPs typically do not see uninsured patients unless they are able to cover their own medical expenses. Therefore, barring self payment (which is an option for everyone), the pool of PCPs available to individuals is largest for the privately insured, followed by the publicly insured, and is empty for the uninsured. Because of this, we mi ght expect the number of people filtered out of the ED during office hours to be highest among the privately insured, followed by the publicly insured, and lastly by the uninsured. Hence, a time of presentation in the ED during office hours should be pred ictive of being under insured. This relationship is tested using the following first stage equation ( 1 3): Under 0 1 2 3 ( 1 3) where office hours is an indicator for a time of presentation at the ED between 8:00am and he presenting level of pain, whether the individual arrived via ambulance, the number of diagnostic or screening services ordered/provided (including a squared term), and the reasons the individual cited for appearing at the ED 6 ). These variables are furt her defined in Column II of Table 1 1 and in Table 1 2. It should also be noted that the fixed effect controls in equation ( 1 3) are slightly different from those in equation ( 1 1). For example, hospital location, ownership, month and day hour interaction s are excluded from the triage model since they are not thought to affect 6 These include 44 dummy variables which represent different reasons for visiting the ED. Each variable takes the value of one if the individual cited that item as either the 1 st 2 nd or 3 rd reason for visiting the E D, and zero if the individual did not cite that item as a reason for visiting the ED.

PAGE 30

30 As shown in Table 1 4, the expected relationship between time of arrival and being under insured holds. For all specifications, the under insured are more likely to seek emergency care during office hours. Moreover, the magnitudes of these relationships are consistent with the hypothesis that the privately insured are least likely to seek emergency care during office hours. As a further test of in strument strength, Table 1 5 shows the fraction of individuals who appear at the ED during office hours who are under insured as opposed the fraction who appear outside of office hours that are under insured. For all under insurance classifications, other than uninsured compared to publicly insured, under insured individuals comprise a greater proportion of total ED patrons during the hours of 8:00am 5:00pm, Monday through Friday, than outside of this time. Additionally the differences in these fractions across arrival times are statistically significant at the 99% confidence level. 1. 5.2.2 Assumption #2: The e xclusion r estriction The second assumption of IV estimation is the exclusion restriction. Unlike the first assumption, the exogeneity of the instru ment cannot be formally tested. However, it is important to intuitively consider the likelihood of exogeneity, for without it the new estimates fail to correct the original problem. As stated before, the original concern in estimating the effect of payer shown in equation ( 1 2). For example, while the model can control for whether an individual visits the ED for chest pains (i.e., the type of ailment), it canno t control for the severity of the ailment. This is problematic because if payer source is also correlated with severity, then the error will not be random. The necessary assumption for IV estimation is, therefore, that the office hours of general practit ioners be uncorrelated with severity. This means that, between 8:00am and 5:00pm, Monday through Friday, the severity of the individuals that appear at EDs should be, on average, no different than the severity of those appearing during off hours.

PAGE 31

31 There is one possible threat to this assumption that should be addressed. The concern is that if an insured individual appears at the ED during office hours, then it may not be because of an access to care problem, but because their condition is truly deserving of emergency care. In this case, their severity is likely more extreme. Phrased alternatively, among the treatment group (i.e., those with limited access to non emergency care), we would not expect a relationship between office hours and severity. Howe ver, for those in the control group (i.e., those with high access to non emergency care), the instrument may be indicative of severity. If, in fact, the insured that appear at the ED during office hours have higher severity than the insured who present du ring off hours, then this would contradict the exclusion restriction. This is because the instrument would be uniquely related to the omitted variable within the control group. To test whether there is any evidence of the above concern, I compare the av erage triage score of the privately insured who appear during office hours (2.284) to the average triage score of the privately insured who appear outside of office hours (2.294), and find that there is not a statistically significant difference in these m ean assignments. To further dispel any concerns of is going to be dependent on how severe they think their condition is. This is worth noting because they are the one choosing whether to go to the ED. While subtle, this is an important point. That is, the same logic/judgment/attitudes that a person uses to asse ss their condition are also the same logic/judgment/attitudes they use when choosing to go to the ED or a PCP. While it is unlikely that an individual will measure his blood pressure, record his heart rate or do lab work to precisely measure the true seve rity of his condition before weighing the PCP versus ED decision, his choice of where to seek care will certainly be influenced by how bad he feels and

PAGE 32

32 presen ting level of pain, and up to the first three reasons an individual gives for visiting the ED. Additionally, the number of diagnostic or screening services ordered/provided is included (independently and as a squared term) as a proxy for the complexity of condition. These controls attempt to rectify the possible incomparability between the insured people who visit the ED during office hours and the insured people who visit during off hours. As a cursory check of exogeneity, Table 1 6 pr esents the distributions of triage assignment, self reported pain, ambulance arrival and number of diagnostic/screening services provided, by treatment classification and time of arrival. While these figures cannot rule in/out the existence of an excluded instrument (since any prevailing differences in these variables are controlled for), comparable means should lessen the concern of endogeneity. In other words, if the observed variables which are thought to be related to severity appear stable across ti me of arrival, then there is less reason to believe that the unobserved variables related to severity (which remain in the error term of the triage model) are correlated with the instrument. As shown, each of these measures is fairly constant across time of arrival and insurance status. The only striking difference is a higher rate of ambulance arrival among the under insured compared to the well insured. However, within insurance classification, the rates of ambulance arrive are fairly steady across ins trument classification. This is reassuring as it demonstrates that this particular predictor of triage (which systematically differs by treatment status) is relatively unaffected by the instrument. Additionally, because it is possible that differences in ambulance arrival rates across insurance classification are driven by access to transportation differences, it could be that these differences are completely unrelated to severity.

PAGE 33

33 In summary, the necessary assumption for exogeneity is that office hours (i.e., the how bad an individual feels and what he believes the proble m to be, should a time of presentation during office hours be related to severity (which is in the error term of the triage model) among either the treatment or control groups? I would argue that it should not, based on f assessment will ultimately determine whether he/she decides to go to the ED when a PCP is available, and because triage scores among the privately insured (relative the publicly insured and uninsured) are not statistically different during versus outside of office hours. With this established, I proceed to the second stage of the estimation. 1. 5.2.3 Instrumental v ariable r esults In the dataset, the dependent variable, triage is defined as follows: 1 if immediacy with which patient should be seen i s assigned as <15 minutes Triage = 2 if immediacy with which patient should be seen is assigned as 15 60 minutes 3 if immediacy with which patient should be seen is assigned as >1 hr 2 hrs 4 if immediacy with which patient should be seen is assigned as >2 hrs 24 hrs Because triage is a categorical variable, IV interval regression and IV ordered probit methods are used to estimate the effect of under insurance. Interval regression is a specific version of an ordered probit model that is appropriate when the ordered categories (e.g., triage assignments) represent some underlying interval of values (e.g., minutes). These results are particularly insightful because, by using the known cut off points between triage categories, interval regression coeff icients represent effects on unobserved minute classifications, which can also be used to determine the effects on observed triage category assignments. Additionally, these results can be extrapolated to understand the effects of under insurance among hos pitals with

PAGE 34

34 different triage structures. Although standard IV ordered probit estimates do not yield interpretable results for hospitals with more than four triage categories and/or different triage category divisions, the results using this procedure are also presented as they are internally consistent with the triage structure used in the NHAMCS dataset. As noted previously, the triage regressions use a larger sample than the wait time regressions. This is because individuals with unknown waits and/or who left the ED before being seen by a physician are included in the triage model since missing values in these categories will not compromise the estimates. However, it may also be of interest to see the triage results using the restrictions from the wai t time regressions (i.e., omitting those with unknown wait time and/or who left the ED early). The primary benefit of employing these further restrictions is consistency between the models. However, the drawback of using these smaller samples is that man y valid observations are omitted which could potentially generate a selection problem. Interestingly, when the results from both samples are compared, the magnitudes of the estimates remain roughly unchanged. There is, however, a slight loss of precision using the wait time samples, which is probably due to the fact that nearly one quarter of the sample is dropped. While the results from the larger triage samples are cited in the text, the triage results using the smaller wait time samples are provided i n the Appendix. Triage IV interval regression results (where office hours are used as an instrument for under insurance) are presented in Table 1 7. Compared to individuals with either public or private insurance, the uninsured, on average, face a 83.6 minute higher triage assignment (Column II). Additionally, compared to the privately insured, individuals with either public insurance or no insurance face a 44.9 minute higher triage assignment (Column IV). These estimates are both statistically signifi cant at the 99% confidence level. The estimates comparing

PAGE 35

35 the uninsured to the privately insured (Column I) and the publicly insured to the privately insured (Column V) are statistically significant at the 95% confidence level. These suggest that, compar ed to the privately insured, the uninsured experience a 39.3 minute increase in triage assignment, and the publicly insured face a 35.2 minute increase in triage assignment. Though comparisons between the publicly insured and the uninsured are omitted due to the lack of a first stage relationship at the 95% confidence level, all other estimates consistently point towards less immediate care for the under insured. Triage IV ordered probit results are presented in Table 1 8I. Similar to before, each classif ication of under insurance predicts an increase in triage category assignment. Moreover, the relative magnitudes of the under insurance coefficients (across columns) are roughly consistent between Tables 1 7 and 1 8. According to the IV ordered probit results, the effects on triage are largest among the uninsured relative to those with any insurance (Column II), followed by the non privately insured relative to the privately insured (Column IV). 1. 5.2.4 Robustness c hecks As checks of robustness, three a lternative two stage least squares (2SLS) procedures are used to estimate the effects of under insurance on triage. First, the variation in triage category width is addressed by transforming each triage category into a rough approximation of an individual level immediacy assignment. A triage ranking of 1 is replaced with 10 minutes, a ranking of 2 is replaced with 40 minutes, a ranking of 3 with 90 minutes, and a ranking of 4 with 180 minutes. While these minute assignments are imperfect, they d o provide a plausible and interpretable representation of underlying triage minute assignments which are comparable to IV interval regression results. Next, triage is treated as a linear running variable (as coded in the dataset) in the second stage of th e estimation. Although, in actuality, triage is not a continuous variable, these estimates provide an additional check of robustness against the

PAGE 36

36 IV ordered probit results. Finally, under insurance is regressed on indicators for being assigned (i) triage= 2+ as opposed to triage=1, (ii) triage=3+ as opposed to triage=2, and (iii) triage=4 as opposed to triage=3. While these tests require the stronger assumption that under insurance only move triage assignments upward, they are useful for determining the pr obability of being assigned a higher triage category. Similar to before, each of these sets of 2SLS regressions use office hours as the instrument for under insurance. Table 1 9 presents the triage results when each triage category is transformed into a minute level approximation and 2SLS estimation is used. As with the initial triage results, all insurance coefficients are statistically significant. Here, it is estimated that the effect of being under insured is a 40.2 to 97.2 minute increase in an ind These results are comparable to the slightly more conservative 35.2 to 83.6 minute estimates obtained using IV interval regression. Table 1 10 presents the triage results when triage category assignments are treated as a continuous running variable and 2SLS estimation is used. Here, being under insured results in a 0.8 to 1.7 increase in triage category. Consistent with the IV ordered probit results, the effects on triage are largest when comparing the uninsured to the privately/publicly insured, and smallest when comparing the uninsured to the privately insured and the publicly insured to the privately insured. These estimates are also consistent with the IV interval regression results which suggest a 35.2 to 83.6 minute increase in triage minute assignment. This is because a 35.2 minute increase in triage would result in a jump of between 0 and 1 triage categories, and 0.8 [0, 1], and because a 83.6 minute increase in triage would result in a jump of between 0 and 2 triage categories, and 1.7 [0, 2].

PAGE 37

37 Finally, Table 1 11 presents the estimates for the effects of under insurance on the probability of being assigned a higher triage category. Similar to previous estimates, these 2SLS results indicate that under insured populations face a higher probability of being assigned a less immediate triage score. The effect of being under insured is estimated to be a 26.9 to 64.9 percentage point increase in the probability of being assigned a triage score of 2+ (as oppo sed to 1), and a 38.8 to 63.5 percentage point increase in the probability of being assigned a triage score of 4 (as opposed to 3). Although the second stage effects of being assigned a triage score of 3+ (as opposed to 2) are not precisely estimated, th e direction of the coefficients are consistent with the existing evidence of discriminatory assignments. 1.6 The Net Effect of Under Insurance on Wait Time The results of this study suggest that under insurance affects triage, and triage affects wait time, but what is the net effect of under insurance on wait time? This is a difficult question to answer because there are both direct and indirect effects of payer source on wait time, and the mechanism through which payer source operates does so in a no n linear fashion. Although calculating a precise point estimate for the net effect of under insurance on wait time is beyond the scope of this paper due to the complexity of causal mechanisms, it is possible to gain a general understanding of the overall magnitude of the effect. 7 To do this, we will consider a hypothetical visitor to the ED. Suppose that our hypothetical visitor is uninsured and we are interested in how much longer she will have to wait due to her insurance status. According to Column I I of Table 1 3, the direct effect of being uninsured (as opposed to having any type of insurance) is a 3.1 minute 7 Flores and Flores mechanisms. However, the use of instrumental variables has y et to be fully developed. Existing IV methods are not yet at a stage where they can be straightforwardly applied in this context.

PAGE 38

38 increase in wait time. What about the indirect effect? According to the instrumental variables results presented in Table 1 7, the uninsured (relative to the privately/publicly insured) are structure, this is consistent with a move from triage category 1 to 3, 2 to 3, 2 to 4, 3 to 4, or 4 to a jump of between zero to two categories. If we first assume that our hypothetical individual is acutely ill and should receive a triage ranking of 1, but is instead bumped up two triage categories as a result of being uninsured, then, according to Tab le 1 3, the total effect of under insurance could be as much as a 3.1+30.1=33.2 minute increase in wait time (assuming she is a non Hispanic white). This is equal to 76% of her average wait time, with 91% of the total effect of under insurance being maske and deserving of a triage score of 2, a conservative one category nudge in triage (due to being uninsured) would result in a 3.1+(30.1 16.2)=17.0 minute increase i n wait time. Here, 82% of the net effect of under insurance is hidden by triage. Similar calculations for other severity levels and under insured classifications are presented in Table 1 12. In each case, it is assumed that the prevailing triage assig nment is one unit higher than would otherwise be assigned if not under insured. According to these calculations, no less than 41% of the total effect of under insurance on wait time is hidden by adjustments to triage. 1. 7 Conclusion Beyond the frustr ation caused, excessive wait times pose a clear and considerable cause for public concern. If waits are further prolonged due to unfair sorting procedures, then this is an even more concerning outcome.

PAGE 39

39 It has been suggested by the Institute of Medicine that timeliness of care may be improved if payment procedures are made more supportive. This paper examines the issue by exploring the micro level relationship between financing and wait times. Specifically, this paper asks whether discrepancies in payer source directly translate to discrepancies in wait time. The analysis is restricted to emergency departments because it is in these settings that timeliness of care is particularly poor and reimbursement patterns are particularly varied. My initial res ults indicate that being under insured results in a 2.7 4.2 minute (or ~6 10%) increase in wait time, and while relatively small, these results are precisely estimated. Next, because of suspicions that the wait time model has not generated a net causa l effect, I test for the possibility of a mediating variable. Here, instrumental variable estimation is used to determine whether payer source is a predictor of triage assignment. The office hours of general practitioners are used as an exogenous source of variation in payer source, and a strong first stage relationship is established. IV interval regression results suggest that being under insured results in a 35.2 to 83.6 minute increase in triage assignment, and various robustness checks support this finding. The results of this paper are significant due to the implications of delayed emergency care. Although there exists little literature on the direct effects of extended time spent in waiting rooms, research on the effects of ED crowding does pro vide some insight as to how prolonged waits might impact other medical outcomes. A 2008 systematic review by Hoot and Aronsky cites six general effects of ED crowding. Among these are two which might be traced directly back to time spent in the waiting r oom. These are increased rates of patient elopement and increased rates of patient mortality. The findings of the present study, then, would suggest that under insured populations face even greater likelihoods of leaving the ED before being seen, and

PAGE 40

40 mor e significantly, dying. Clearly, each of these outcomes is cause for concern for both policymakers and healthcare providers. In short, this paper finds that although naive estimates for the impact of payer source on ED wait time indicate only modest effe cts, there is alternative evidence suggesting that the effect of being under insured may actually be much larger than originally estimated. Using instrumental variable estimation, it is shown that under insured populations are systematically assigned inex plicably higher triage rankings, all else equal, and these higher triage rankings are shown to translate into longer wait times. Contrary to the stipulations of EMTALA, timeliness of emergency care does appear to be affected by insurance coverage, and the majority of this effect is concealed by adjustments to triage.

PAGE 41

41 Table 1 1. Variables l ist Tobit m odel Instrumental v ariable m odel Dependent Variable Dependent Variable Wait The number of minutes between Triage =1 if <15 minute assignment =2 if 15 60 minute assignment by physician =3 if >1 hour to 2 hour assignment =4 if >2 hour to 24 hour assignment Variable of Interest Under Insured Indicator for whether individual is Variable of Interest uninsured relative to publicly and/or Under Insured Indicator for whether individual is privately insured, or publicly insured uninsured relative to publicly and/or relative to privately insured privately insured, or publicly insured relative to privately insured Controls Gender Indicator for male Instrument for Variable of Interest Office Hours Indicator for time of arrival between Race/ethnicity Indicators for black and other race (white referent), and Hispanic (not Hispanic/unknown ethnicity referent) 8:00am and 5:00pm, Monday through Friday Controls Age Indicators for 1 100 Gender Indicator for male Triage triage assignment is 15 60 minutes, >1 hour to 2 hours, or >2 hours to 24 hours (less than 15 minutes referent) Race/ethnicity Indicators for black and other race (white referent), and Hispanic (not Hispanic/unknown ethnicity referent) Age Indicators for 1 100 Triage*Race/ Indicators for interactions between ethnicity triage assignment and race/ethnicity Pain Indicators for whether presenting level of pain was unknown, mild, moderate Ambulance Indicator for whether mode of arrival or severe (no pain referent) was ambulance (not ambulance/ unknown mode of arrival referent) Ambulance Indicator for whether mode of arrival was ambulance (not ambulance/ MSA Indicator for whether hospital located in a MSA unknown mode of arrival referent) Year Indicators Geographic Indicators for whether hospital located Region in the Northeast, Midwest, or Number of Running variable 0 19 (and squared South (West referent) Diagnostic or term) Screening Hospital Indicators for whether hospital is Services Ownership voluntary non profit or government, Ordered/ non federal (proprietary referent) Provided Day*Hour Indicators for interactions between Reason(s) for 44 indicators for whether each item each day of the week and hour of the Visit (listed in Table 1 2) was cited as either the day 1 st 2 nd or 3 rd reason for visiting the ED Month Indicators Year Indicators

PAGE 42

42 Table 1 2. Reasons for v isit SYMPTOMS General Symptoms Symptoms Referable to Psychological and Mental Disorders Symptoms Referable to the Nervous System (Excluding Sense Organs) Symptoms Referable to the Cardiovascular and Lymphatic Systems Symptoms Referable to the Eyes and Ears Symptoms Referable to the Respiratory System Symptoms Referable to the Digestive System Symptoms Referable to the Genitourinary System Symptoms Referable to the Skin, Nails, and Hair Symptoms Referable to the Musculoskeletal System DISEASES Infective and Parasitic Diseases Neoplasms Endocrin e, Nutritional, and Metabolic Diseases Diseases of the Blood and Blood forming Organs Mental Disorders Diseases of the Nervous System Diseases of the Eye Diseases of the Ear Diseases of the Circulatory System Diseases of the Respiratory System Dise ases of the Digestive System Diseases of the Genitourinary System Diseases of the Skin and Subcutaneous Tissue Diseases of the Musculoskeletal System and Connective Tissue Congenital Anomalies Perinatal Morbidity and Mortality Conditions DIAGNOSTIC, SCREENING AND PREVENTIVE SERVICES General Examinations Special Examinations Diagnostic Tests Other Screening and Preventive Procedures Family Planning TREATMENT Medications Preoperative and Postoperative Care Specific Types of Thera py Specific Therapeutic Procedures Medical Counseling Social Problem Counseling Progress Visit, NEC INJURIES AND ADVERSE EFFECTS Injury by Type and/or Location Injury, NOS Poisoning and Adverse Effects TEST RESULTS ADMINISTRATIVE UNCODABLE ENTRIES Each of the 44 reason for visit variables is indicated by a bullet point

PAGE 43

43 Table 1 3. Wait t ime (in minutes) Tobit (I) (II) (III) (IV) (V) Uninsured vs. Privately Insured Uninsured vs. All Insured Uninsured vs. Publicly Insured Non Privately Insured vs. Privately Insured Publicly Insured vs. Privately Insured Mean Wait Time 43.966 min. 43.466 min. 44.842 min. 43.466 min. 42.127 min. Under Insured 4.203 *** 3.132 *** 0.562 3.094 *** 2.696 *** (0.676) (0.651) (0.779) (0.469) (0.538) Male 2.102 *** 1.808 *** 1.768 *** 1.626 *** 1.233 *** (0.553) (0.438) (0.614) (0.437) (0.469) Black a 1.674 0.293 0.555 0.033 0.717 (1.445) (1.204) (1.645) (1.201) (1.308) Other Race a 7.588 ** 6.497 *** 4.960 6.694 *** 7.390 *** (3.329) (2.221) (3.075) (2.225) (2.085) Hispanic b 0.439 0.685 3.253 0.581 0.912 (1.890) (1.447) (1.904) (1.449) (1.560) Triage = <15 minutes -----Triage = 15 60 minutes 15.187 *** 16.228 *** 16.946 *** 16.245 *** 16.438 *** (0.800) (0.613) (0.860) (0.613) (0.641) Black 4.922 *** 3.586 ** 3.508 3.530 ** 2.790 (1.747) (1.424) (1.935) (1.423) (1.549) Other Race 6.136 6.054 ** 4.201 6.260 ** 7.919 *** (3.943) (2.814) (3.855) (2.815) (2.845) Hispanic 8.231 *** 7.380 *** 4.619 ** 7.224 *** 8.534 *** (2.311) (1.761) (2.279) (1.761) (1.918) Triage = >1 2 hours 28.728 *** 30.097 *** 31.372 *** 30.137 *** 30.221 *** (1.004) (0.802) (1.158) (0.802) (0.844) Black 12.349 *** 10.563 *** 9.962 *** 10.468 *** 9.552 *** (2.137) (1.726) (2.319) (1.726) (1.893) Other Race 7.968 8.128 ** 6.055 8.381 ** 10.544 *** (4.489) (3.580) (5.426) (3.581) (3.739) Hispanic 9.454 *** 10.333 *** 9.228 *** 10.135 *** 11.257 *** (2.817) (2.242) (2.901) (2.239) (2.516) Triage = >2 24 hours 32.070 *** 33.599 *** 37.493 *** 33.610 *** 32.070 *** (1.286) (1.066) (1.570) (1.065) (1.134) Black 21.898 *** 17.365 *** 15.811 *** 17.289 *** 13.876 *** (2.879) (2.243) (2.892) (2.244) (2.506) Other Race 11.555 8.836 1.407 9.056 13.223 ** (5.974) (4.673) (5.952) (4.689) (5.414) Hispanic 16.239 *** 14.390 *** 10.256 *** 14.195 *** 15.499 *** (3.512) (2.780) (3.562) (2.779) (3.156) MSA 17.524 *** 17.581 *** 19.139 *** 17.822 *** 16.616 *** (0.683) (0.522) (0.707) (0.524) (0.558) Ambulance c 10.540 *** 9.999 *** 9.831 *** 10.174 *** 10.208 *** (1.129) (0.766) (0.956) (0.766) (0.803) Fixed Effects: Age Y Y Y Y Y Day*Hour Interactions Y Y Y Y Y Year Y Y Y Y Y Month Y Y Y Y Y Geographic Region Y Y Y Y Y Hospital Ownership Y Y Y Y Y Number of Observations 55,137 92,587 54,388 92,587 75,649 Pseudo R Squared 0.0125 0.0125 0.0136 0.0125 0.0126 Values in parentheses are robust a Referent: White; b Referent: Not Hispanic/unknown ethnicity; c Referent: Not ambulance/unknown mode of arrival

PAGE 44

44 Table 1 4. First s tage: Effect of o ffice h ours on b eing u nder i nsured (I) (II) (III) (IV) (V) Uninsured vs. Privately Insured Uninsured vs. All Insured Uninsured vs. Publicly Insured Non Privately Insured vs. Privately Insured Publicly Insured vs. Privately Insured M F 8 5 0.032 *** 0.016 *** 0.008 0.029 *** 0.025 *** (0.005) (0.003) (0.004) (0.004) (0.004) Male 0.040 *** 0.046 *** 0.082 *** 0.007 0.045 *** (0.004) (0.003) (0.004) (0.004) (0.004) Black a 0.139 *** 0.049 *** 0.023 *** 0.160 *** 0.165 *** (0.006) (0.004) (0.005) (0.004) (0.005) Other Race a 0.017 0.012 0.014 0.011 0.006 (0.013) (0.009) (0.014) (0.011) (0.012) Hispanic b 0.173 *** 0.086 *** 0.037 *** 0.153 *** 0.133 *** (0.007) (0.005) (0.006) (0.005) (0.006) Unknown Pain 0.022 *** 0.012 *** 0.005 0.019 *** 0.015 *** (0.007) (0.004) (0.006) (0.005) (0.006) No Pain -----Mild Pain 0.020 *** 0.011 ** 0.006 0.014 ** 0.010 (0.007) (0.005) (0.007) (0.006) (0.006) Moderate Pain 0.025 *** 0.011 ** 0.002 0.031 *** 0.029 *** (0.008) (0.005) (0.007) (0.006) (0.006) Severe Pain 0.002 0.001 0.001 0.007 0.007 (0.009) (0.006) (0.009) (0.007) (0.008) Ambulance c 0.066 *** 0.020 *** 0.010 0.070 *** 0.067 *** (0.008) (0.004) (0.006) (0.006) (0.006) No. Diagnostic/Screening 0.024 *** 0.014 *** 0.014 *** 0.013 *** 0.007 *** Services Provided (0.002) (0.002) (0.002) (0.002) (0.002) No. Diagnostic/Screening 0.001 *** 0.001 *** 0.001 *** 0.001 *** 0.000 *** Services Provided Squared (0.000) (0.000) (0.000) (0.000) (0.000) Fixed Effects: Age Y Y Y Y Y Year Y Y Y Y Y Reason(s) for Visit Y Y Y Y Y Number of Observations 70,732 118,414 70,045 118,414 96,051 R Squared 0.0923 0.0958 0.2359 0.1210 0.2118 a Referent: White; b Referent: Not Hispanic/unknown ethnicity; c Referent: Not ambulance/unknown mode of arrival

PAGE 45

45 Table 1 5. Fraction of i ndividuals who a ppear at the ED who are u nder i nsured, by o ffice h ours (I) (II) (III) (IV) (V) Fraction Uninsured as Opposed to Privately Insured Fraction Uninsured as Opposed to Privately/ Publicly Insured Fraction Uninsured as Opposed to Publicly Insured Fraction Uninsured/ Publicly Insured as Opposed to Privately Insured Fraction Publicly Insured as Opposed to Privately Insured During Office Hours 33.46% 19.69% 32.35% 60.85% 51.25% Outside of Office Hours 30.15% 18.72% 33.04% 56.64% 46.65% Statistically significant difference in fraction of patients who are under insured during office hours versus outside of office hours Yes (p=0.00) Yes (p=0.00) No (p=0.16) Yes (p=0.00) Yes (p=0.00) These fractions are among the triage sample (i.e., only individuals with missing triage scores are omitted). Table 1 6. Distributions of t riage s cores and s elf a ssessment m easures, by i nsurance s tatus and o ffice h ours During Office Hours : Outside of Office Hours : Under Insured=0 Under Insured=1 Under Insured=0 Under Insured=1 Triage =1 if <15 min =2 if 15 60 min =3 if >1 hr to 2 hr =4 if >2 hr to 24 hr Mean: 2.284 Std. Dev: 0.934 Mean: 2.296 Std. Dev: 0.968 Mean: 2.294 Std. Dev.: 0.937 Mean: 2.279 Std. Dev.: 0.960 Self Reported Pain =1 if no pain =2 if mild pain =3 if moderate pain =4 if severe pain Mean: 2.371 Std. Dev: 0.971 Mean: 2.264 Std.Dev.: 1.017 Mean: 2.389 Std. Dev.: 0.971 Mean: 2.288 Std. Dev.: 1.008 Ambulance Arrival =0 if no =1 if yes Mean: 0.079 Std. Dev.: 0.269 Mean: 0.136 Std. Dev.: 0.343 Mean: 0.073 Std. Dev.: 0.260 Mean: 0.126 Std. Dev.: 0.331 No. Diagnostic/ Screening Services Provided (from 0 19) Mean: 3.123 Std. Dev.: 2.750 Mean: 3.396 Std. Dev.: 2.986 Mean: 2.811 Std. Dev.: 2.547 Mean: 3.138 Std. Dev.: 2.861 These numbers are among the triage sample (i.e., only individuals with missing triage scores are omitted) where NOTE: There is not a statistically significant difference in the average triage score of the well insured during office hours versus outside of office hours (i.e., 2.284 vs. 2.294).

PAGE 46

46 Table 1 7. IV i nterval r egression: Effect of b eing u nder i nsured on t riage m inute a ssignment (I) (II) (III) (IV) (V) Uninsured vs. Privately Insured Uninsured vs. All Insured Uninsured vs. Publicly Insured^ Non Privately Insured vs. Privately Insured Publicly Insured vs. Privately Insured Under Insured # 39.331 ** 83.554 *** 44.912 *** 35.167 ** (15.384) (27.088) (13.228) (16.114) Male 2.551 *** 5.012 *** 0.897 ** 0.235 (0.773) (1.299) (0.385) (0.823) Black a 0.861 1.587 1.509 1.086 (2.217) (1.419) (2.166) (2.712) Other Race a 2.262 3.623 *** 3.112 *** 2.765 ** (1.388) (1.306) (1.149) (1.208) Hispanic b 3.804 3.944 3.669 1.860 (2.767) (2.406) (2.103) (2.236) Unknown Pain 6.286 *** 7.331 *** 7.198 *** 7.146 *** (0.815) (0.682) (0.610) (0.633) No Pain ----Mild Pain 4.136 *** 5.137 *** 5.394 *** 5.253 *** (0.876) (0.755) (0.665) (0.686) Moderate Pain 10.823 *** 11.219 *** 10.690 *** 10.604 *** (0.894) (0.749) (0.755) (0.811) Severe Pain 15.598 *** 14.666 *** 14.308 *** 13.560 *** (0.944) (0.831) (0.749) (0.790) Ambulance c 18.070 *** 15.909 *** 17.389 *** 15.898 *** (1.284) (0.818) (1.080) (1.230) No. Diagnostic/Screening 2.259 *** 2.526 *** 3.103 *** 3.201 *** Services Provided (0.437) (0.435) (0.259) (0.227) No. Diagnostic/Screening 0.001 0.032 0.066 *** 0.077 *** Services Provided Squared (0.031) (0.029) (0.019) (0.017) Fixed Effects: Age Y Y Y Y Year Y Y Y Y Reason(s) for Visit Y Y Y Y Number of Observations 70,732 118,414 118,414 96,051 # The instrument for being under insured is appearing at the ED during office hours; a Referent: White; b Referent: Not Hispanic/unknown ethnicity; c Referent: Not ambulance/unknown mode of arrival; ^ Results not presented due to the lack of a first stage relationship at the 95% confidence level

PAGE 47

47 Table 1 8. IV o rdered p robit: Effect of b eing u nder i nsured on t riage c ategory (I) (II) (III) (IV) (V) Uninsured vs. Privately Insured Uninsured vs. All Insured Uninsured vs. Publicly Insured^ Non Privately Insured vs. Privately Insured Publicly Insured vs. Privately Insured Under Insured # 0.907 *** 1.717 *** 1.036 *** 0.923 *** (0.297) (0.328) (0.229) (0.317) Male 0.066 *** 0.110 *** 0.028 *** 0.001 (0.015) (0.014) (0.009) (0.019) Black a 0.016 0.027 0.042 0.040 (0.051) (0.031) (0.046) (0.061) Other Race a 0.048 0.072 *** 0.069 *** 0.060 ** (0.032) (0.026) (0.026) (0.029) Hispanic b 0.086 0.077 ** 0.081 0.046 (0.058) (0.039) (0.042) (0.050) Unknown Pain 0.153 *** 0.158 *** 0.174 *** 0.183 *** (0.017) (0.018) (0.014) (0.015) No Pain ----Mild Pain 0.081 *** 0.094 *** 0.112 *** 0.116 *** (0.021) (0.022) (0.018) (0. 019) Moderate Pain 0.237 *** 0.220 *** 0.234 *** 0.245 *** (0.028) (0.036) (0.028) (0.032) Severe Pain 0.391 *** 0.325 *** 0.356 *** 0.357 *** (0.030) (0.043) (0.030) (0.033) Ambulance c 0.479 *** 0.368 *** 0.446 *** 0.436 *** (0.021) (0.037) (0.016) (0.016) No. Diagnostic/Screening 0.047 *** 0.047 *** 0.065 *** 0.072 *** Services Provided (0.021) (0.014) (0.009) (0.009) No. Diagnostic/Screening 0.000 0.000 0.001 0.001 ** Services Provided Squared (0.001) (0.001) (0.000) (0.000) Fixed Effects: Age Y Y Y Y Year Y Y Y Y Reason(s) for Visit Y Y Y Y Number of Observations 70,732 118,414 118,414 96,051 # The instrument for being under insured is appearing at the ED during office hours a Referent: White; b Referent: Not Hispanic/unknown ethnicity; c Referent: Not ambulance/unknown mode of arrival ^ Results not presented due to the lack of a first stage relationship at the 95% confidence level

PAGE 48

48 Table 1 9. 2SLS: Effect of b eing u nder i nsured on t riage m inute a pproximation (I) (II) (III) (IV) (V) Uninsured vs. Privately Insured Uninsured vs. All Insured Uninsure d vs. Publicly Insured^ Non Privately Insured vs. Privately Insured Publicly Insured vs. Privately Insured Under Insured # 46.334 *** 97.174 *** 52.289 *** 40.173 ** (17.840) (31.468) (15.347) (18.672) Male 2.925 *** 5.676 *** 0.889 ** 0.438 (0.896) (1.508) (0.447) (0.955) Black a 0.373 1.439 2.168 1.530 (2.571) (1.648) (2.513) (3.142) Other Race a 2.943 4.292 *** 3.697 *** 3.414 ** (1.597) (1.510) (1.320) (1.384) Hispanic b 4.745 4.874 4.564 2.424 (3.209) (2.795) (2.440) (2.591) Unknown Pain 6.708 *** 7.895 *** 7.740 *** 7.663 *** (0.942) (0.792) (0.707) (0.733) No Pain ----Mild Pain 4.936 *** 5.943 *** 6.241 *** 6.042 *** (1.012) (0.876) (0.769) (0.793) Moderate Pain 12.101 *** 12.557 *** 11.942 *** 11.886 *** (1.033) (0.868) (0.874) (0.937) Severe Pain 16.762 *** 15.725 *** 15.313 *** 14.478 *** (1.093) (0.964) (0.868) (0.915) Ambulance c 19.594 *** 17.195 *** 18.919 *** 17.159 *** (1.487) (0.947) (1.250) (1.423) No. Diagnostic/Screening 2.636 *** 2.929 *** 3.600 *** 3.695 *** Services Provided (0.505) (0.504) (0.299) (0.261) No. Diagnostic/Screening 0.009 0.043 0.083 *** 0.094 *** Services Provided Squared (0.036) (0.034) (0.022) (0.020) Fixed Effects: Age Y Y Y Y Year Y Y Y Y Reason(s) for Visit Y Y Y Y Number of Observations 70,732 118,414 118,414 96,051 # The instrument for being under insured is appearing at the ED during office hours a Referent: White; b Referent: Not Hispanic/unknown ethnicity; c Referent: Not ambulance/unknown mode of arrival ^ 2SLS results not presented due to the lack of a first stage relationship at the 95% confidence level

PAGE 49

49 Table 1 10. 2SLS: Effect of b eing u nder i nsured on t riage c a tegory (I) (II) (III) (IV) (V) Uninsured vs. Privately Insured Uninsured vs. All Insured Uninsured vs. Publicly Insured^ Non Privately Insured vs. Privately Insured Publicly Insured vs. Privately Insured Under Insured # 0.783 ** 1.727 *** 0.929 *** 0.770 ** (0.307) (0.554) (0.270) (0.335) Male 0.055 *** 0.108 *** 0.023 *** 0.002 (0.015) (0.027) (0.008) (0.017) Black a 0.019 0.032 0.032 0.027 (0.044) (0.029) (0.044) (0.056) Other Race a 0.043 0.074 *** 0.064 *** 0.055 ** (0.028) (0.027) (0.024) (0.025) Hispanic b 0.073 0.078 0.072 0.038 (0.055) (0.049) (0.043) (0.046) Unknown Pain 0.132 *** 0.157 *** 0.155 *** 0.156 *** (0.016) (0.014) (0.012) (0.013) No Pain ----Mild Pain 0.075 *** 0.100 *** 0.105 *** 0.105 *** (0.017) (0.015) (0.013) (0.014) Moderate Pain 0.215 *** 0.229 *** 0.218 *** 0.220 *** (0.018) (0.015) (0.015) (0.017) Severe Pain 0.335 *** 0.322 *** 0.315 *** 0.303 *** (0.019) (0.017) (0.015) (0.017) Ambulance c 0.400 *** 0.358 *** 0.389 *** 0.363 *** (0.026) (0.017) (0.022) (0.026) No. Diagnostic/Screening 0.044 *** 0.051 *** 0.063 *** 0.066 *** Services Provided (0.009) (0.009) (0.005) (0.005) No. Diagnostic/Screening 0.000 0.000 0.001 *** 0.001 *** Services Provided Squared (0.001) (0.001) (0.000) (0.000) Fixed Effects: Age Y Y Y Y Year Y Y Y Y Reason(s) for Visit Y Y Y Y Number of Observations 70,732 118,414 118,414 96,051 # The instrument for being under insured is appearing at the ED during office hours a Referent: White; b Referent: Not Hispanic/unknown ethnicity; c Referent: Not ambulance/unknown mode of arrival ^ 2SLS results not presented due to the lack of a first stage relationship at the 95% confidence level

PAGE 50

50 Table 1 11. 2SLS: Probability of b eing a ssigned a h igher t riage c ategory (I) (II) (III) (IV) (V) Uninsured vs. Privately Insured Uninsured vs. All Insured Uninsured vs. Publicly Insured Non Privately Insured vs. Privately Insured Publicly Insured vs. Privately Insured Probability of Being Assigned Triage 2, 3 or 4 (as opposed to 1) : First Stage Effect of Office Hours 0.032 *** 0.016 *** 0.008 0.029 *** 0.025 *** (0.005) (0.003) (0.004) (0.004) (0.004) Second Stage Effect of 0.269 ** 0.649 *** -0.349 *** 0.374 ** Under Insurance (0.126) (0.232) (0.115) (0.153) Full Set of Controls Y Y Y Y Y Number of Observations 70,732 118,414 70,045 118,414 96,051 Probability of Being Assigned Triage 3 or 4 (as opposed to 2) : First Stage Effect of Office Hours 0.036 *** 0.019 *** 0.012 ** 0.032 *** 0.026 *** (0.005) (0.004) (0.005) (0.004) (0.004) Second Stage Effect f 0.074 0.217 0.861 0.130 0.026 Under Insurance (0.154) (0.232) (0.606) (0.138) (0.183) Full Set of Controls Y Y Y Y Y Number of Observations 57,233 93,885 55,192 93,885 75,345 Probability of Being Assigned Triage 4 (as opposed to 3) : First Stage Effect of Office Hours 0.045 *** 0.025 *** 0.014 0.041 *** 0.035 *** (0.008) (0.005) (0.008) (0.006) (0.007) Second Stage Effect of 0.411 ** 0.635 ** -0.388 ** 0.275 Under Insurance (0.190) (0.285) (0.164) (0.213) Full Set of Controls Y Y Y Y Y Number of Observations 26,964 43,007 25,572 43,007 33,478 Values in parentheses are robust standard errors; Second stage results are not presented when the first stage is not significant at the 95% confidence level

PAGE 51

51 Table 1 12. Approximate n et e ffect of b eing u nder i nsured on w ait t ime Direct Effect Indirect Effect Total Effect Percent of Total Effect Hidden by Triage Approximate effect of being uninsured as opposed to privately insured on ED wait time Triage = 2 4.203 min. 15.187 min. 19.390 min. 78% Triage = 3 4.203 min. 13.541 min. 17.744 min. 76% Triage = 4 4.203 min. 3.342 min. 7.545 min. 44% Approximate effect of being uninsured as opposed to publicly/privately insured on ED wait time Triage = 2 3.132 min. 16.228 min. 19.360 min. 84% Triage = 3 3.132 min. 13.869 min. 17.001 min. 82% Triage = 4 3.132 min. 3.502 min. 6.634 min. 53% Approximate effect of being uninsured/publicly insured as opposed to privately insured on ED wait time Triage = 2 3.094 min. 16.245 min. 19.339 min. 84% Triage = 3 3.094 min. 13.892 min. 16.986 min. 82% Triage = 4 3.094 min. 3.473 min. 6.567 min. 53% Approximate effect of being publicly insured as opposed to privately insured on ED wait time Triage = 2 2.696 min. 16.438 min. 19.134 min. 86% Triage = 3 2.696 min. 13.783 min. 16.479 min. 84% Triage = 4 2.696 min. 1.849 min. 4.545 min. 41% These calculations are for individuals belonging to the race/ethnicity referent categories (i.e., non Hispanic whites). Wait time effects for those who are uninsured as opposed to publicly insured (i.e., Column III of most tables) are not presented as the indirect effect cannot be precisely estimated

PAGE 52

52 CHAPTER 2 SMART AS A WHIP AND FIT AS A FIDDLE: THE CAUSAL EFFECT OF A DIPLOMA ON HEALTH This study examines the causal effect of a diploma on health using a regression discontinuity approach. During WWII, cohorts of men in the U.S. whose birthdays fell within particular intervals of time were required to register for the dr aft on specific dates. These policies created discontinuities in registration age, which subsequently resulted in discontinuities in graduation rates. Because mandatory registration ages fell as the war progressed, the independent variable, diploma recei pt, can be measured in terms of both a high school and college diploma. The results indicate that both forms of credentialing directly improve physical wellness, and there is some evidence that these effects operate through a healthcare usage mechanism. These findings stand in contrast to ordinary least squares estimates which (i) underestimate the effect of a diploma on physical wellness, and (ii) predict strictly negative effects of a diploma on healthcare usage. 2. 1 Introduction Economies benefit from healthy people. Fewer sick days lead to greater productivity, stronger bodies lead to greater efficiency, and less need for treatment allows for resources to be directed elsewhere. As a result, public health has become a priority f or many governments. Yet, the processes by which a government might affect physical wellness remain largely unclear. Of interest to policymakers is the observation that more educated people tend to be healthier. As a result, there is an intriguing poss ibility of addressing public health via educational initiatives. The problem, however, is that education often overlaps with other health improving characteristics. This makes it difficult to isolate the effects of just education in order to determine i f such initiatives might be worthwhile. For econometricians, evaluating the merit of such initiatives is further complicated by the fact that many predictors of health go

PAGE 53

53 unobserved. Consequently, even after controlling for known health determinants, est imates for the effect of education are susceptible to omitted variables bias. This study attempts to parse out the effects of education by exploiting a discontinuous predictor of school completion. Using a regression discontinuity (RD) design, I show th at men born after various military registration thresholds are randomly assigned different probabilities of education generated differences in health status among post threshold men can be interpreted as the causal effect of a diploma. This local randomization in education allows for an unbiased assessment of health targeting proposals. The thresholds used in this study are birthday cut offs between WWII dr aft registration dates. These cut offs required men who were born as little as one day apart to become draft eligible as many as 8.5 months apart. The result was that some men were exogenously pulled out of school before receiving their diploma. A uniqu e strength of this study is that school completion can be measured in terms of both high school and college graduation. This is because the minimum WWII registration age was gradually lowered from 21 to 18 years of age. As such, the early draft registrat ions (which affected older men) provide a strong instrument for college diploma receipt, and the later registrations (which affected 18 year olds) provide a useful instrument for high school diploma receipt. Estimates from this quasi experimental study sug gest that the receipt of a diploma does affect health. The results indicate that a high school diploma improves self reported health, BMI, and number of health conditions. A college diploma is also shown to improve each of these measures, in addition t o number of acute incidence conditions. These effects are, at a minimum, 225% larger than those estimated using ordinary least squares (OLS).

PAGE 54

54 There is some evidence that the improvements in health brought about by a diploma may, in part, be attributed t o greater usage of healthcare. To measure the effect of a diploma on healthcare usage, diploma receipt is regressed on bed days, doctor visits, short stay hospital episodes, and short stay hospital episode days. Each of these variables are thought to be positively affected by resources and negatively affected by improved physical condition. Although OLS results indicate that a diploma decreases each of these variables, RD estimates suggest that a high school diploma increases doctor visits and short stay hospital episodes; a college diploma is estimated to increase short stay hospital episodes and episode days. These findings suggest that previous results may have overlooked what appears to be a strong candidate for the missing link in the long observed health/education correlation. 2. 2 Literature Review While the literature exploring the relationship between education and health is extensive, the results have been inconclusive. Particularly, the question of causality remains unanswered. To address t he inherent endogeneity which has confounded this line of research, a number of studies have proposed instruments for schooling. Most recently, changes in compulsory schooling laws have been used as a source of random variation in education. Among the s tudies which have exploited changes in compulsory schooling laws are Lleras Muney (2005), Kippersluis et al. (2011), Clark and Royer (2013), and Albouy and Lequien (2009). These each estimated the effect of education on the most fundamental measure of hea lth, mortality, and similar to the present study used regression discontinuity. To do so, changes in U.S., Dutch, British, and French laws were considered, respectively. Though Lleras Muney (2005) and Kippersluis et al. (2011) concluded that educatio n has a significant effect on adult mortality, the latter two papers found little evidence of a causal relationship between schooling and mortality.

PAGE 55

55 Aside from mortality, changes in compulsory schooling laws have also been used to identify the effects of education on various other specific health outcomes. A study by Fonseca and Zheng (2011) used data from 13 OECD countries to instrument for education using cross country differences in the timing of educational reforms. Their study concluded that educat ion improves only some measures of health, including diabetes and hypertension, while there is no statistically significant relationship between education and many other chronic conditions. Surprisingly, however, their study found that education actually increases the rate of cancer. Two studies by Arendt (2005 and 2008) considered the effects of education on specific health outcomes using Danish school reforms. These reported inconclusive effects on self reported health and BMI, but significant effects on hospitalizations among women and among men with particular diagnoses. Mazumder (2008) used U.S. school reforms to instrument for education and found that education only affects a small number of health outcomes (including the peculiar outcomes of visi on, hearing, and the ability to speak). Using school reforms in the United Kingdom, Silles (2009) found that education does affect self reported health, the absence of long term illness, activity limitation and work prevention. Finally, Spasojevic (2010) used BMI. In addition to the large body of literature that has utilized changes in compulsory schooling, other studies have attempted to address the endogene ity of education by using more creative predictors of schooling. These include intra state differences in unemployment rates (Arkes, 2003), Vietnam draft dodging (de Walque, 2007), and quarter of birth (Adams, 2002). These studies have generally pointed towards the existence of a causal effect. My study builds on this body of literature by utilizing another unique (and yet untested) source of variation in

PAGE 56

56 education: the timing of WWII draft eligibility. Importantly, my study contributes to the existing literature by measuring education in terms of both a high school and a college diploma, as opposed to just an additional year of schooling. Such milestone markers of educational attainment are already of concern to policymakers wishing to improve graduati on rates. Additionally, by measuring health in terms of both health outcomes and healthcare usage, I am able to consider one distinct avenue through which education might shift physical wellness. If found to exist, a causal effect of a diploma on health would provide evidence that resourcefully targeting public health and education in single pieces of legislation may be a good idea. Additionally, if the mechanism driving these effects is uncovered, then this would provide useful guidance in constructing such policies. Finally, because the results of this paper are representative of the effects among a cohort of American males, these findings are particularly relevant to policymakers in the United States. 2. 3 Background In order for any study considerin g the effect of a diploma on health to be interpreted as causal, it is necessary that treatment be essentially random. Education, however, is far from randomly assigned. To address this, I utilize discontinuous changes in WWII draft registration ages. T he rationale is that registration age should affect the probability of completing school, but the timing of registration should not otherwise affect health. To further motivate and justify the use of this instrument, the following sections provide a more thorough explanation of (i) the practices surrounding conscription in WWII, and (ii) how WWII draft registration policies might be expected to affect the receipt of a diploma.

PAGE 57

57 2. 3.1 Conscription in WWII On September 1 st of 1939, Germany invaded Poland and World War II began. Two days later, on September 3 rd Britain and France declared war on Germany. Two days after this, on September 5 th the United States declared neutrality. first peacetime draft was initiated on September 16, 1940. Only months earlier, France had fallen to the Nazis, President Roosevelt requiring men ages 21 35 to register for draft lotteries. If selected for service, these men were initially required to serve in the armed forces for one year. Additionally, men currently enrolled in college were granted a deferment u ntil July 1, 1941, the date set for the next registration. In August of 1941, however were extended. Long before any of the draftees were due to return home, the American home front was course of the war and the mentality of the nation. No longer eag er to maintain their distant stances, the attack on Pearl Harbor ignited the furies of Americans. Thirty three minutes after On February 16, 1942, the third draft registration was he ld. This time, however, the age requirements were extended to include men 20 44 years of age. Two months later, a fourth 64 to register. Two months after this, a fifth registration l owered the mandatory registration age, yet again, to 18. Finally, beginning December 11, 1942, a series of registrations throughout the month picked up off.

PAGE 58

58 The next year, 1943, marked a decided departure from the previously staggered form of registration that had been in effect. Because previous conscription policies had required men whose birthdays fell within particular intervals of time to register on specific dat es, many similar aged men were able to narrowly avert registering on particular registration dates if their birthdays fell beyond given cut off points. This generated unnecessary delays in the rate of able bodied men entering the draft pool. As a result, beginning January 1, 1943, registration became mandatory for all men (born after December 31, 1924) upon the arrival of their 18 th birthday. 8 Throughout the course of the war, 16M individuals served in the United States military. Of these, 6M voluntari ly enlisted. The remaining 10M were inducted. 2. The practices surrounding conscription in WWII nicely lend themselves to a quasi experimental study of the effects of a diploma on health for two reasons. First, the hard birthday cut offs between registration dates essentially randomized the likelihood of completing school across otherwise similar men. Such exogeneity allows me to measure causal effects. Second, because age requirements were lowered throughout the various registrati ons, I am able to estimate the effect of receiving a high school diploma as well as receiving a college diploma. The correspondence between birthday intervals and registration dates is shown in Table 2 1. The resulting discontinuous relationship between date of birth and registration age is shown in Figure 2 1. Here, the thresholds separating registration cohorts serve as randomization mechanisms. That is, although men born in a narrow window around each threshold were, on average, identical, the thres holds indiscriminately divided them into two groups which were 8 However, as stated in the law: 1, 1925 shall be registered on the day they attain the eighteenth anniversary of the day of their birth; provided, that if such anniversary falls on a Sunday or a legal hol iday, their registration shall take place on the day following which

PAGE 59

59 effectively assigned different probabilities of obtaining a diploma. Right of threshold men were assigned higher probabilities of obtaining a diploma, and left of threshold men were assigned l ower probabilities. This is due to the 4.5 8.5 month jumps in registration ages at the thresholds. These essentially granted right of threshold individuals an additional 4.5 8.5 s towards their diploma (relative to left of threshold men who were made draft eligible immediately). As such, right of of threshold men are considered had no control over their date of birth, this treatment is random. In addition to the differences in ages between threshold straddlers, the actual ages of men at the thresholds are significant. As stated before, registration requirements broadened as the war progressed. During the first three registrations, the men entering the draft pool were no younger than 21 and 20 years old. This would have plausibly placed registrants well into their college years. As a result, treated individuals (i.e., those with a right of threshold birthday) would have Because of this, the treatment status of men born in successive registration cohorts 1 and 2, 2 and 3, and 3 and 5 are used as discontinuous instruments for having received a college diploma. 9 For similar reasons, the treatment of individuals subject to registration 5 versus 6 is used as a discontinuous instrument for having received a high school diploma. This is becau se these men were made liable to the draft at as young as 18 years of age, allowing them to potentially be pulled out of high school before graduating. 9 The individuals that registered at the 4 th registration were born between 1877 and 1897, so their birthdays do not fall between those of cohorts 3 an d 5.

PAGE 60

60 In summary, the above reasoning suggests that dates of birth spanning consecutive registration cohorts might represent a discontinuous source of variation in the receipt of a diploma. Therefore, the treatment status of individuals between each set of successive registrations is subsequently used as an exogenous predictor of either high school or college c ompletion. If this first stage relationship is found to exist, then I am able to interpret any ensuing jumps in health status among the born around the registration thresholds as the causal effect of a diploma on health. 2. 4 Data The data used in this study come from the National Health Interview Survey (NHIS) which is administered by the U.S. Census Bureau. This annual cross sectional survey measures a variety of health related factors in addition to occupational variables, demographics (including mon th of birth), and importantly, years of completed education. Person level records from survey years 1982 1995 are used in the analysis, and observations are weighted to generate nationally representative estimates. In all, the full sample includes 1,526, 906 observations. Although the full NHIS sample is quite large, only a subset is useful for the analysis in this paper. Because the identification strategy used here hinges on the comparability of individuals who were narrowly affected by WWII draft regis tration thresholds (in all ways other than their likelihood of completing school), individuals who were not affected by the thresholds are irrelevant. Consequently, females are omitted from the analysis, as they were not subject to the draft, and individu al regressions do not include observations that fall beyond neighboring threshold boundaries. 10 The maximum window of months around each individual threshold that 10 One might think of using of using women as a falsification test. However, in order for these estimates to be meaningful, the substitutability of male vs. female labor supply during WWII must be thoroughly understood. Modeling this type of joint la bor supply is beyond the scope of this paper.

PAGE 61

61 as suming equal length windows on either side of threshold i) are listed below: Threshold 1 October 17, 1919: 7 months Threshold 2 July 2, 1920: 7 months Threshold 3 January 1, 1922: 17 months Threshold 4 July 1, 1924: 5 months 11 It is important to note that although birthday thresholds, at times, fall mid month, the Since the dates of birth dividing registration cohorts also fall between months, it i s feasible to precisely assign treatment statuses using only month of birth. This is not completely true, however, for thresholds 1 and 2. To address this problem, treatment status for everyone born in October 1919 and July 1920 is assigned based on whet her any one birthday within that month is more likely to be treated or untreated. Therefore, because the majority of dates in the month of October fall before the 17 th (i.e., within the untreated region), all men born during October of 1919 are classified as untreated relative to the first threshold. 12 Similarly, since the majority of dates in this month fall after the 2 nd of the month (i.e., within the treated region), all men born during July of 1920 are classified as treated relative to the second threshold. Using these monthly treatment classifications, four unique running variables are constructed, each centered at 11 Although there are technically 29 months between thresholds 3 and 4, the bandwidth around the fourth threshold is further constrained by the fact that i ndividuals born five months after th is point became subj ect to the new conscription policy which required men to register on their 18 th birthday. Consequently, registration age past this point is no longer a linear decli ning function of month of birth, resulting in a kink in the MOB/registration age relationsh ip. 12 As a check of robustness, all men born in October of 1919 were alternatively classified as treated. This classification led to negative first stage coefficients for each bandwidth. Excluding October birthdays altogether similarly led to negative fi rst stage effects at each bandwidth.

PAGE 62

62 z ero at their relevant threshold. These running variable and treatment classifications are shown in Figure 2 2, along with the useable windows of data around each threshold. 13 2. 5 Estimation 2. 5.1 Identification Procedure To address the reality that i ndividuals who receive a diploma can be inherently different than those who do not, this study compares a subset of individuals who were made randomly more susceptible to being pulled out of school before they could receive their diploma (i.e., those with pre threshold birthdays) to those who were not (i.e., those with post threshold birthdays). Because each of these groups of men should, on average, have similar drive/work ethics/behavior patterns/etc., differences in health outcomes can be reasonably attr ibuted to education differences. The identification strategy used in this study is fuzzy regression discontinuity. Here, the predict the receipt of a dipl register for a WWII draft is an imperfect predictor of being drafted (i.e., potentially pulled out of school early). Men who were not required to register may have dropped out of scho ol, and the men who were required to register may have not been drafted before graduating. Consequently, the instrument in this study predicts the likelihood of receiving a diploma, not the receipt of a diploma itself. Two sets of results are presented. First, high school diploma effects are estimated by computing standard Wald estimates. These divide the jump in health (at the fourth threshold) by 13 T he p roblems that arise when quarter of birth is used as an instrument ( e.g., Buckles & Hungerman (2008)) are not an issue here since month of birth allow s for tighter comparisons.

PAGE 63

63 the jump in high school diploma receipt (at the fourth threshold). 14 Next, to measure the effects of a co llege diploma, a single instrument is constructed which aggregates the effects of thresholds 1 through 3. This is done by stacking the birthdays which are positioned (in the three month windows) around each of the first three thresholds, and then re cente ring each window of time so that thresholds 1, 2, and 3 are simultaneously centered at zero. This allows me to one fell swoop, so as to generate a strong er first stage prediction. Wald estimates for the effect of a college diploma are then computed by dividing the jump in health (at the stacked threshold) by the jump in college diploma receipt (at the stacked threshold). Due to window width constraint s, and to prevent overlapping birthdays in the stacked running variable, a local linear specification is used as opposed to a global polynomial specification. 15 The underlying assumption here is that within a narrow window, birthdays on either side of the threshold are linearly related to both the endogenous variable (i.e., diploma receipt) and the dependent variable (i.e., health). Importantly, because RD estimates represent local average treatment effects, this implies that the estimates generated apply specifically to the men who were born within the windows of time considered in the analysis and whose education Prior to defining the model, it is also important to disclose the assumptions underlying regression discontinuity. First, it is assumed that a first stage relationship exists. In this case, 14 Similar procedures can also be used at the first, second and third thresholds to measure the effects of a college diploma. However, because the first stages at these individual thresholds are sometimes noisy, this paper focuses on the stacked threshold a s the primary predictor of college diploma receipt. 15 As discussed in Imbens and Lemieux (2008), 2SLS is numerically identical to using a local linear regression with a uniform kernel where the same bandwidth is used to estimate the discontinuity in the de pendent variable and in the endogenous treatment variable. This implies that so too are Wald estimates (where the same specification is used in the first stage and reduced form) since these produce the same estimates as 2SLS.

PAGE 64

64 month of birth relative to a threshold must be related to the receipt of a diploma. This is verified below. Second, monotonicity must be sa tisfied. This implies that being born before/after a threshold, in and of itself, does not incite/discourage individuals from graduating. In other a thresh old must be randomly assigned. This means that men cannot have control over their month of birth. While this assumption is not explicitly testable, logic would suggest that it is clearly satisfied. A check for smoothness in observable characteristics ac ross the thresholds also supports this claim. 16 2. 5.2 Specification Due to the fuzzy nature of this identification procedure, two stages of estimation are required. In the first stage, I estimate the effect of being born after a registration threshold on the likelihood of receiving a diploma. Then, using a reduced form equation, I estimate the effect of being born after a registration threshold on health. The ratio of these estimates yields the effect of a diploma on health. To estimate the effects of a high school diploma, equation ( 2 1) is used for the first stage, and equations ( 2 2) and ( 2 form specifications. In each equation, the running variable, MOB (month of birth), serves as a discontinuous predictor o f diploma The magnitude of the discontinuity is captured by the coefficient on the binary variable, exempt which is equal to one among the individuals with birthdays to the right of the registration exempt threshold. The interaction term, exempt*MOB 16 Using a 2 month bandwidth around each individual threshold, there is generally not a statistically significant pre versus post threshold difference in the average likelihood of being married, of a particular race, of Hispanic ethnicity, living in a MSA region, living in a particul ar geographic region, or being a veteran (at the 95% confidence level). The only exceptions are a lower probability of living in the Midwest among the men born after the 2 nd threshold, a lower probability of living in the Northeast among the men born afte r the 4 th threshold, and a higher probability of being married among the men born after the 4 th threshold.

PAGE 65

65 month of birth to affect the dependent variable differently on either side of the threshold, and the and survey year. De scriptive statistics are presented in Table 2 2. diploma i 0 1 exempt i 2 MOB i 3 ( exempt*MOB ) i 4 X i i ( 2 1) health i 0 1 exempt i 2 MOB i 3 ( exempt*MOB ) i 4 X i i ( 2 2) health i 0 1 exempt i 2 MOB i 3 X i i ( 2 The outcome variable, health in equations ( 2 2) and ( 2 reported health 17 BMI, number of acute incidence conditions, number of conditions, bed days in the past 12 months, doctor visits in the past 12 months, short stay hospital episode days in the past 12 months, or number of short stay hospital episodes in the past 12 months. While the first four measures represent health outcomes, the last four measures represent healthcare usage variables. These are defined as those which are expected to decline with improved health but rise with increased resources. The hypothesized effects of a diploma on each of the health variables are presented in Table 2 3. Because lower values of self reported health, BMI, number of acute incidence conditions, and number of conditions correspond with improved physical wellnes s, the predicted that because acute incidence conditions consist of temporary physical conditions (including broken bones, influenza, and headaches), a positive sign need not necessarily imply that overall health is worsened. A diploma is not, however, expected to consistently move healthcare usage in the same direction. Apart from resource effects, a diploma is expected to reduce healthcare usage (as healthier people have less of an incentive to spend time in the hospital, for example). 17 Self reported health =1 if excellent, =2 if very good, =3 if good, =4 if fair, and =5 if poor.

PAGE 66

66 However, if a diploma also improves resources, then the hypothesized effect on each of the healthcare usage variables becomes indeterminate. This is because any health gains b rought about by a diploma (which, on their own, should result in less healthcare usage) may be offset by increased access to healthcare. Taken together, the combined effects of a diploma on health outcomes and healthcare usage might shed light on the clai m that (i) resources serve as a mechanism in the diploma/healthcare usage relationship, and (ii) healthcare usage is a mediating variable in the diploma/health outcomes relationship. Importantly, the reduced form effects on health are estimated using two different specifications. In equation ( 2 2), the discontinuity in health is estimated in the same way as the first stage discontinuity in diploma In equation ( 2 3), the interaction term exempt*MOB is omitted. The justification for the latter spe cification is that, unlike the first stage the time when the thresholds were imposed) the reduced form predicts a more continuous variable which was measured years after the thresholds were imposed. As such, it is not clear whether month of birth should affect health differently on either side of threshold. Therefore, complementary Wald estimates are computed using both reduced form specifications as a check of ro 1 1 1 1 respectively. To estimate the effects of a college diploma, equations ( 2 3), ( 2 4) and ( 2 18 Here, the reference point used to assign treatment is the stacked threshold, positioned at MOB st =0 and the indicator variable, exempt st serves as the instrument for college diploma month window) after either the first, second, or third threshold. Since the running variable in the 18 The individual effects of thresholds 1, 2, and 3 are also computed to estimate preliminary, unaggregated, effects of a college diploma. These use equations ( 2 1), ( 2 2) and ( 2

PAGE 67

67 stacked model ( i.e., MOB st ) no longer controls for time trends, fixed effect controls are included to indicate the window of time (i.e., around the first, second or third threshold) in which educed form equation are used in the analysis. These yield two Wald estimates for the effects of a college diploma on 1 1 1 1 diploma i 0 1 exempt i st 2 MOB i st 3 ( exempt st *MOB st ) i 4 FE i 5 X i i ( 2 3) health i 0 1 exempt i st 2 MOB i st 3 ( exempt st *MOB st ) i 4 FE i 5 X i i ( 2 4) health i 0 1 exempt i st 2 MOB i st 4 FE i 3 X i i ( 2 All regressions are clustered by the running variable (i.e., MOB in equations ( 2 1), ( 2 2) and ( 2 MOB st in equations ( 2 3), ( 2 4) and ( 2 equations ( 2 1), ( 2 2) and ( 2 around the fourth threshold. For equations ( 2 3), ( 2 4) and ( 2 analysis is conducted using the 1, 2 and 3 month windows around the stacked threshold. Because a cross validation procedure suggests that a two month bandwidth is optimal (at both the fourth and stacked thresholds), the results using this bandwidth are th e focus of this paper. 19 19 The literature provides a variety of suggestions for bandwidth selection via cross validation for fuzzy RD designs. In so me cases, researchers use cross validation only on the reduced form equation to select the bandwidth and then use this for both the first stage and the reduced form regressions, or generate separate cross validated bandwidths for the first stage and reduce d form equations but then choose the narrower of the two to generate the RD estimates (see discussion in Imbens and Lemieux (2008) ). Both of these approaches have the benefit of simplicity and some sense of symmetry, but they work best when one can expect a strong first stage relationship regardless of bandwidth. Because the statistical significance of the first stage relationship is sensitive to bandwidth in my application, I choose cross validated bandwidths based on the first stage (to guarantee the choi ce of a bandwidth that represents a strong first stage relationship) and apply them to both equations in the RD. Additionally, these optimal first stage bandwidths (at the fourth and stacked thresholds) differ by no more than one month from the optimal re duced form the use of weights): http://faculty gsb.stanford.edu/ imbens/RegressionDiscontinuity.html

PAGE 68

68 2. 6 Results 2. 6.1 First Stage Results The first stage effects of registration exemption on diploma receipt are presented in Table 2 4. Because of less than 100% response rates across each health measure, first stage results are presented by dependent variable to ensure sample size consistency between the associate first stage and reduced form equations. Additionally, as a check of robustness, the results in the full sample are presented with and without controls. A graphical r schooling (which might roughly correspond to the registration rule depicted in Figure 2 1) is given by Figure 2 3. As shown, there is a general upward trend in schooling over ti me. This suggests that it is necessary to control for time trends, which is done using the month of birth running variable, to distinguish overall trends from the effects of registration rules. Additionally, the relationship between years of education an d month of birth is relatively noisy around the early thresholds. This provides further support for the use of a stacked threshold to instrument for college diploma receipt. 2. 6.1.1 First s tage e ffect on h igh s chool d iploma r eceipt The first stage effec ts of registration exemption on high school diploma receipt are shown in the top panel of Table 2 4, along with a graphical depiction of the discontinuity in high school diploma receipt in Figure 2 4. Surprisingly, each of these indicate a negative relati onship. Using a 2 month bandwidth, the effect of a post threshold birthday is precisely estimated to be an approximately 7 percentage point decrease in the probability of receiving a high school diploma. This would suggest that being required to register at age 18 5.5 / 12 as opposed to at age 18, reduces might account for this result.

PAGE 69

69 Unlike the other thresholds, the instrument used to predict high school diplom a receipt is unique in that the men affected by the fourth threshold were on the heels of the upcoming changes to conscription policies which would require 18 year olds to register on their birthday. The men affected by the fourth threshold would have bee n aware of these upcoming changes, as while the men born on either side of the fourth threshold would have been similarly capable of contributing to the war effort ( in terms of maturity), according to Uncle Sam, only those born to the left of the threshold were old enough. Right of a stigma. If so, then the men who were born after the fourth threshold may have had an increased incentive to voluntarily enlist in order to fulfill a sense of participation in the war effort. Importantly, however, premature participation for right of t hreshold men would have required voluntary enlistment necessarily sending them off to war (and out of school) as opposed to their non eligibility, and not necessarily service. Compounding this effect was the fact that President Roosevelt signed an executive order on December 5, 1942, stating that voluntary enlistments would no longer be allowed the bor intensive implications for the men born around the fourth threshold. For those who barely missed the June 30, 1942, registration (i.e., were born after t he fourth threshold), voluntary enlistment would only remain an option for the next 5 months (in July, August, September, October and November of 1942). In December of 1942, these men would then be required to register themselves, and, at

PAGE 70

70 that point, the y would only be able to enter the military if/when drafted. According to Rottman e expected first stage relationship between registration exemption and high school diploma receipt. Given the above scenario, it is important to reassess the monotonicity assumption required of regression discontinuity. According to this assumption, men h ave no control over their treatment assignment (which is determined by month of birth) so that the effect of treatment generated by the instrument represent those instrument to manipulate their probability of diploma receipt). The problem here is that, by voluntarily enlisting, right of threshold men essentially defied the mechanism by assigning themselves a lowe those who always select into a lower probability of diploma receipt, regardless of treatment) or hen treated, and into a higher probability of diploma receipt when untreated). Significantly, the existence of men who It is important to note that being a quires that an individual who assigns himself a lower probability of completing high school when exempt from registering, would also assign himself a higher probability of diploma receipt if non exempt. I argue, however, that non compliers of the fourth t WWII were generally eager to defend their country. So much so, in fact, that it was not uncommon for under aged men to lie about their age in order to try to prematurely enlist. Becaus e of this, it seems unlikely that the men who voluntarily enlisted (because they were not

PAGE 71

71 draft eligible) would have averted the draft had they had been required to register. Moreover, ly forbidden. As such, I hold that, although the direction of the first stage effect on high school diploma receipt is unexpected, the monotonicity assumption required for validity remains uncompromised. 2. 6.1.2 First s tage e ffect on c ollege d iploma r eceipt The first stage effects of registration exemption on college diploma receipt are presented in the lower panels of Table 2 4. These show the effects at the individual thresholds, as well as at the stacked threshold. It should be noted that the regi stration cut offs were far less predictive of college diploma receipt in the early years of the war than later on, specifically than at the third negated the eff ects of the registration cut offs. In other words, because voluntary enlisters were increasingly filtered out of the civilian population as the war progressed (leaving behind nologically more meaningful. Due to the relative noisiness of the individual college diploma instruments, the stacked threshold is used in the remainder of this paper to instrument for college diploma receipt. At the stacked threshold, which aggregates the predictive power of the first three thresholds, the effect of being granted temporary registration exemption is a 3.6 percentage point increase in the likelihood of completing college (using a 2 month bandwidth). The direction of this estimate conform s with previous predictions. A graphical representation of this discontinuity is shown in Figure 2 4. 2. 6.2 Wald Estimates The effects of a high school diploma on health are presented in Table 2 5. The effects of a college diploma on health are presented in Table 2 6. These estimates are computed by

PAGE 72

72 manually dividing the first stage effect of registration exemption by the reduced form effect of 5 and 2 6. Wh ile it was not clear, theoretically, whether an interaction term was needed in the reduced form equation, this term does appear to be empirically important. Not only are the interaction terms generally statistically significant, but their inclusion adds p recision to diploma coefficients. Because of this, I consider the Wald estimates that allow for different health effects on either side of the thresholds to be my preferred results. The Wald estimates that omit the interaction term in the reduced form ar e presented in the tables; however, they are not discussed in the text. Standard errors for these are calculated using the delta method. Given the serious problems generated by the use of weak instruments (Bound, Jaeger & Baker (1995)), only estimates that utilize a strong first stage are presented in Tables 2 5 and 2 6. Similarly, only the 2 month bandwidth results are cited in the text (as cross validation suggests these are optimal); however, the results across all bandwidths are presented in the ta bles. 2. 6.2.1 The e ffect of h igh s chool d iploma r eceipt on h ealth As shown in Table 2 5, the receipt of a high school diploma is predicted to improve all aspects of health other than the number of acute incidence conditions. It is estimated that the causa l effect of a high school diploma is a 1.2 point improvement in self reported health (which is a 45% improvement, on average), a 4.6 point reduction in BMI (which is a 18% reduction, on average), and a 4.0 reduction in number of health conditions (which is a 288% reduction, on average). The results indicate that a high school diploma increases number of acute incidence conditions by 0.2, but, again, this does not necessarily imply that overall health is worsened since these include short lived conditions s uch as having the flu.

PAGE 73

73 results indicate that a high school diploma increases doctor visits by 16 visits per year and number of short stay hospital episodes by 0.7. However, there is no statistically significant effect on number of short stay hospital episode days in the past 12 months, and bed days are predicted to fall by 65 per year. Though the effect of a diploma on bed days is negative, it should be noted that days spent in bed do not necessarily correspond to days spent with care. As such, it is possible that bed days are representative of wellness more than healthcare usage. If this is the case, then the negative coefficient on bed days is consistent with t he previously estimated health improvements brought about by a diploma. While the mixed effects of a high school diploma on healthcare usage may appear somewhat uninformative on the outset, these results are insightful nonetheless. Recall, it is assumed that healthcare usage decreases with improved health and increases with heightened resources. Estimating the net effect of a diploma on healthcare usage is, therefore, useful for determining which of these factors is most pronounced. Given that a diploma is shown to improve health, one of three scenarios must be true: either (i) a diploma affects health only (in effect on health dominates its effect on resource s (in which case negative coefficients for health (in which case positive coefficients for healthcare usage are sufficient). Though the data is unable to di sentangle (ii) and (iii), option (i) can be immediately ruled out thanks to the positive and negative coefficients on diploma receipt. This suggests that resources do act as a mechanism in the diploma/healthcare usage relationship, and the possibility tha t healthcare usage is a mediating variable in the diploma/health outcomes relationship is not excluded.

PAGE 74

74 2. 6.2.2 The e ffect of c ollege d iploma r eceipt on h ealth Similar to the effects of a high school diploma, there is strong evidence that a college diploma improves physical health. As shown in Table 2 6, the effect of a college diploma on self reported health is estimated to be a 2.0 point improvement (which is a 75% improvement, on average), and the effect of a college diploma on BMI is estimated to be a 3.2 point reduction (which is a 12% decline, on average). Number of health conditions are predicted to fall by 3.8, and number of acute incidence conditions are predicted to fall by 0.3. The results from the stacked model provide additional evidence th at the effect of a diploma on physical wellness may, in part, be explained by increased usage of healthcare. According to Table 2 6, the effect of a college diploma on healthcare usage is non negative. Though the effects on bed days and doctor visits are not predicted to be statistically different than zero, the effects on number of short stage hospital episodes and number of short stay hospital episode days are both predicted to be positive. For those with a college diploma, it is estimated that an addi tional 0.7 short stay hospital episodes occur each year, and short stay hospital episode days are predicted to rise by 21.3 per year. Positive effects, such as these, suggest that resource improvements (brought about by diploma receipt) outweigh health im provements in determining the demand for healthcare. 2. 7 Discussion The results of this study suggest that a diploma does, in fact, improve physical health. Moreover, there is evidence that this relationship may be explained, in part, by some increase d usage of healthcare. There are, however, other factors that should be considered when interpreting these results. First, the increased educational opportunities afforded to WWII veterans inflated their net years of schooling beyond their pre war levels This affects first stage estimates. Second, the military nature of the instrument deserves some scrutiny as various

PAGE 75

75 studies have drawn attention to veteran status effects. Lastly, the generalizability of these findings should be considered. Each of t hese items are discussed, in turn, below. 2. 7.1 Educational Opportunities for Returning WWII Veterans A number of factors uniquely influenced the net educational attainment of the men considered in this analysis. Not only did many WWII veterans experi ence disruptions in their education prior to their service, but post war schooling opportunities were also non standard. During the war, the U.S Office of Education War Time Commission encouraged school districts to offer fast track versions of high scho ol education to high school students wishing to enlist. However, such recommendations were not broadly mandated; as of October 1943 nearly a year after 18 year olds were first required to register on their birthday and voluntary enlistments had been sus pended only a handful of states were granting early diplomas to high school juniors and seniors. The result was that nearly 10M individuals entered WWII without a high school diploma. For other men, war cut short their college studies. It seemed only fair, therefore, that action should be taken to prevent the penalization of men who had prematurely ended their academic careers to fight for their country. The result of such sentiments was the initiation of both the GED program and the GI Bill. Within academic circles, the idea of awarding high school equivalent certificates to non graduates had been floating around for some time before the war. WWII, however, provided a very opportune chance to leverage the idea on a national scale. For one, the Amer ican Council on Education ardently discouraged high schools from awarding honorary diplomas to returning veterans as such practices had proved to ultimately disadvantage recipients during WWI. Additionally, the Council opposed the idea of automatically aw arding veterans educational credits for the military classes and skills they had acquired throughout their service. Instead, the

PAGE 76

76 encouraged as a means of awarding high school equivalent certification to non graduates. The majority of the states complied with the recommendation, and, by late 1946, only four states were not utilizing the GED as a means of providing certification for WWII veterans. Within approximat GED. Roughly 90% passed the exam, though there is evidence that standards were initially set low so as to be generous to the veterans taking the exam. For many, these scores had broad im plications. In addition to potentially making individuals work eligible, a 1948 survey by the American Council on Education indicated that 66% of the college registrars sampled used 20 In terms of acc provisions for $20 a week in unemployment pay, loan guaranty for homes, and, most notably, substan tial assistance with college tuition. As explained by Roosevelt: It gives servicemen and women the opportunity of resuming their education or technical training after discharge, or of taking a refresher or retrainer course, not only without tuition charge up to $500 per school year, but with the right to receive a monthly living allowance while pursuing their studies. these individuals, the bel ief that they performed better in college because of their experience, and because of the funding they brought with them, veterans were readily admitted to colleges and universities. In all, over 2M WWII veterans were able to enroll in higher level instit utions using These educational opportunities awarded to returning veterans have obvious implications for the present study. In terms of GEDs, the ability of non high school graduates to recover an 20 Much of the information on the GED program during WWII comes from Quinn (2002).

PAGE 77

77 equivalent certificate (to repla ce the one they were unable to obtain due to the draft) could result in weak first stage estimates at the fourth threshold. In spite of this, however, the first stage estimates at the fourth threshold remain statistically significant. Similarly, the post war financial incentives given to men, via GI Bill benefits, could also weaken the first stage effects at the stacked threshold. Again, however, these estimates remain statistically significant. 2. 7.2 Veteran Status Effects Several papers (e.g., Angris t and Krueger (1994) and Angrist (1990)) have suggested that veteran status affects particular individual level outcomes. If any of these outcomes subsequently influence either diploma receipt and/or health, then this will bias the estimates of this paper I contend, however, that any existing veteran effects do not threaten this analysis. This is because the instrument used here predicts the timing of military service, not military service itself. In this way, veteran status should be randomized across the thresholds. To verify this is the case, I test for differences in the probability of military service between men born to the right versus left of each threshold. Among the men who were born between April of 1919 and December of 1924 (i.e., seven m onths prior to the first threshold to five months after the last threshold), 74% served in the military and 66% were veterans of WWII specifically. Veterans in this sample have higher rates of diploma receipt than non veterans, and independent sample t te sts confirm statistically significant differences in these likelihoods. 21 However, this is only concerning if the instrument used in the analysis predicts military service. As stated previously, the thresholds I use to 21 The average likelihood of having a high school diploma is 20 percentage points higher among all veterans (as opposed to non veterans), and 1 1 percentage points higher among WWII veterans (as opposed to non WWII veterans). The average likelihood of having a college diploma is 7 percentage points higher among all veterans, and 3 percentage points higher among WWII veterans. Other studies such as Stanley (2003) estimate that the GI Bill increased postsecondary education by 15 20% among men born between 1921 and 1933. Bound and Turner (2002) and Angrist and Chen (2011) similarly find large increases in schooling due to GI Bill benefits.

PAGE 78

78 instrument for education are relevant because they predict when an individual enters the military, not if an individual enters the military. I therefore test for the exogeneity of veteran status using independent sample t tests in the 7 month windows around each of the first three thresholds, and in the 5 month window around the fourth threshold. These tell me whether men born to the right of each threshold, who have different probabilities of obtaining a diploma, are more likely to be veterans. The results indicate that, within a 95% confidence interval, there is not a statistically significant difference in the average likelihood of being a veteran between the men born on the right versus left of each threshold. This supports the claim that the cut offs I use do randomize the receipt of a diploma across all individuals (including veterans) so that I am no t inadvertently estimating the effects of military service on health. Finally, it should be noted that although veteran status appears to be randomized across the thresholds, this may not be the case for time spent in the military. This bears mentioning as it is at least plausible that longer periods of service could result in poorer health. Unfortunately, this caveat of the model is unavoidable as I do not have data on length of service. Consequently, if individuals on the left side of a threshold are systematically made more unhealthy (due to longer periods of war exposure, for example), then an upward bias on the estimated effect of a diploma on health would exist. 2. 7.3 Local Average Treatment Effects When considering the generalizability of these findings, it should be reiterated that the assignment mechanism. In this study, this includes men who were born in the narrow windows around each WWII draft registra tion threshold, and whose diploma receipt was subsequently manipulated by their position relative to these thresholds. It should also be noted that the results obtained here are conditional on survival to the age of approximately 57 to 86 (depending on th e

PAGE 79

79 health conditions are underrepresented in the sample. Men killed during the war are completely unrepresented. Finally, in order to put these results in perspective, OLS estimates are presented in Table 2 7. For consistency, these are only among men who were born between the seventh month preceding the first threshold to the fifth month following the last threshol d. Compared to the local average treatment effects estimated using RD, the OLS effects on health outcomes are relatively small. Additionally, while OLS results suggest that a diploma reduces all measures of healthcare usage, quasi experimental results su ggest that a diploma actually increases some measures of healthcare usage. This finding is particularly noteworthy as it suggests that OLS estimates will likely overlook what appears to be a mechanism in the diploma/health relationship (i.e., increased he althcare usage brought about by a diploma). As it were, comparison between OLS and RD results indicate that omitted variables bias does pose a significant threat to non experimental studies. 2. 8 Conclusion National governments devote large amounts of res ources to the improvement of public health and education. While these aims are generally targeted separately, the possibility of simultaneously improving one via the other opens the door for large efficiency gains. The merit of such initiatives, however, is dependent on the existence of a causal effect. relationship, th

PAGE 80

80 By comparing men who were narrowly allowed vs. not allowed to complete the 12th grade (due to WWII draft registration policies) this study suggests that a high school diploma results in 4 fewer health conditions, an 18% lower BMI and a 45% improvement in self reported health, on average. Acute incidence conditions are predicted to rise by 0.2 conditions, but this result does not necessarily contradict the overall finding that a high school diploma improves health; having a broken bone, for example, is an imperfect measure of healthiness. Large health effects are also predicted to emerge due to the receipt of a college diploma. Among the men who were exogenously allowed to complete college, self reported health ratings are 75% higher and BMI scores are 12% points lower, on average. Acute incidence conditions fall by 0.3, and health condi tions fall by 3.8. To determine whether greater usage of healthcare is to be credited for these gains, the net effect of a diploma on various healthcare usage variables is estimated. Healthcare usage variables are defined here as those which decline with improved physical condition and rise with increased resources. While it is possible to independently estimate the effect of education on resources (as is done with health), regressing diploma receipt on income is only helpful insofar as it demonstrates th at resource effects exist; it says nothing about whether increased resources are allocated towards health improving activities. Therefore, estimating the net effect of a diploma on healthcare usage is helpful for assessing the presumption that high school /college graduates consume more medical care. While OLS results indicate that both high school and college diplomas have strictly negative effects on healthcare usage, RD results indicate otherwise. Rather than curbing usage, this study suggests that a hi gh school diploma results in an additional 16.3 doctor visits per year and 0.7 more short stay hospital episodes per year. A high school diploma is estimated to have

PAGE 81

81 no statistically significant effect on number of short stay hospital episode days and a n egative effect on bed days. A college diploma is shown to increase short stay hospital episode days by 21.3 per year and short stay hospital episodes by 0.7 per year. Though neither bed days nor doctor visits are predicted to be affected by college diplo ma receipt, the consistently non negative effects of a college diploma on healthcare usage variables stand in stark contrast to previous estimates. This study provides several contributions to the existing literature on the relationship between education and health. First, this paper measures education in terms of a diploma not an additional year of school. This measure should be of interest to policymakers who can (and do) offer incentives for students to graduate. The effect of a diploma should als o be of interest to educators. Because institutional success is often measured in terms of graduation rates, using a Additionally, because sheepskin effects are likely t o influence various health predictors in ways that intermediary academic advances are not, this study provides evidence on what is perhaps a marginally more effective way of addressing public health. Second, this study measures the effects of treatment at both the high school and college level. In doing so, an additional layer of information, which is often infeasible to estimate using natural experiments, is provided. Third, because many of the existing studies that measure the effects of education expl oit changes in compulsory schooling laws, the results of those studies are inherently specific to individuals who wish to exit school but are required to stay. This study measures the effects among individuals who wish to remain in school but are prevente d from doing so. Estimating schooling effects among this innately different population allows for a broader understanding of the relationship between education and health. Finally, this study offers one possible explanation as for why

PAGE 82

82 better health is en joyed by those who hold a diploma namely, increased healthcare usage. This finding is significant because an understanding of the mechanisms that influence health is necessary to effectively craft legislation.

PAGE 83

83 22 years 21 years 20 years 19 years 18 years 1919 1920 1921 1922 1923 1924 1925 REGISTRATION 1: REGISTRATION 2: REGISTRATION 3: REGISTRATION 5: REGISTRATION 6: Oct 16, 1940 July 1, 1941 Feb 16, 1942 June 30, 1942 Dec 11+, 1942* *Men born July 1, 1924 through August 31, 1924 registered December 11 17, 1942. Those born September 1, 1924 through October 31, 1924 registered December 18 24, 1924. Those born November 1, 1924 through December 31, 1924 registered December 26 31, 1942, and those born on or after January 1, 1942 were to register on their eigh teenth birthday. Figure 2 1. Registration a ge, by d ate of b irth October 17, 1919 July 2, 1920 January 1, 1922 July 1, 1924

PAGE 84

84 *Shaded region indicates period when 18 year olds were required to register on their birthday (i.e., registration age no long er a declining function of month of birth). Figure 2 2. Running v ariable and t reatment a ssignment, by i nstrument

PAGE 85

85 Figure 2 3. Regression a djusted MOB m eans for t otal y ears of e ducation Figure 2 s e ffects on r egression a djusted MOB m eans

PAGE 86

86 Figure 2 f e ffects on r egression a djusted MOB m eans: High s chool d iploma HEALTHCARE USAGE HEALTH OUTCOMES

PAGE 87

87 Figure 2 f e ffects on r egression a djusted MOB m eans: College d iploma HEALTHCARE USAGE HEALTH OUTCOMES

PAGE 88

88 Table 2 1. WWII d raft r egistrations Registration Date of Registration Dates of Birth of Registrants Registration 1* October 16, 1940 Oct 17, 1904 Oct 16, 1919 21 35 years Registration 2 July 1, 1941 Oct 17, 1919 July 1, 1920 21 years Registration 3 Feb 16, 1942 July 2, 1920 Dec 31, 1921 Feb 17, 1897 Oct 16, 1904 20 21 years 37 44 years Registration 4** April 27, 1942 April 28, 1877 Feb 16, 1897 45 64 years Registration 5 June 30, 1942 Jan 1, 1922 June 30, 1924 18 20 years Registration 6 Dec 11 17, 1942 Dec 18 24, 1942 Dec 26 31, 1942 July 1, 1924 Aug 31, 1924 Sept 1, 1924 Oct 31, 1924 Nov 1, 1924 Dec 31, 1924 (Required to register on 18 th birthday if born on or after Jan 1, 1925) 18 years 18 years 18 years 18 years (The seventh registration was only for men living abroad.) *These individuals received a deferment until July 1, 1941 if enrolled in college. **These men were not liable for service.

PAGE 89

89 Table 2 2. Descriptive s tatistics Variable Mean Standard Deviation Minimum Maximum Health Variables : Self Reported Health 1 2.73 1.22 1 5 BMI 2 26.03 3.82 8.99 120.68 Number of Acute Incidence Conditions 0.03 0.18 0 5 Number of Conditions 1.40 1.65 0 18 Bed Days in Past 12 Months 9.46 40.45 0 365 Doctor Visits in Past 12 Months 5.06 13.47 0 997 Short Stay Hospital Episode Days in Past 12 Months 1.79 8.14 0 243 Number of Short Stay Hospital Episodes in Past 12 Months 0.22 0.64 0 16 Education Variables : High School Diploma 0.64 0.48 0 1 College Diploma 0.17 0.38 0 1 Years of Education 11.56 3.64 0 18 Demographic Variables : Married 0.83 0.37 0 1 White 3 0.89 0.31 0 1 Black 3 0.09 0.28 0 1 Hispanic 0.04 0.19 0 1 MSA 0.73 0.44 0 1 Northeast 4 0.23 0.42 0 1 Midwest 4 0.25 0.43 0 1 South 4 0.33 0.47 0 1 Veteran 0.74 0.44 0 1 1 Where =1 if excellent, =2 if very good, =3 if good, =4 if fair, and =5 if poor. 2 Where <18.5 if underweight, 18.5 24.9 if normal, 25.0 29.9 if overweight, and 30.0+ if obese. 3 The referent race category is 'other'. 4 The referent geographic region is 'West'.

PAGE 90

90 Table 2 3. Hypothesized o utcomes Dependent Variable: Expected Sign: Health Outcomes : Self Reported Health 1 Negative BMI 2 Negative Number of Acute Incidence Conditions Negative Number of Conditions Negative Healthcare Usage 3 : Bed Days in Past 12 Months If diploma only affects health If diploma only affects resources If diploma affects health & resources Negative Positive Indeterminate Doctor Visits in Past 12 Months If diploma only affects health If diploma only affects resources If diploma affects health & resources Negative Positive Indeterminate Short Stay Hospital Episode Days in Past 12 Months If diploma only affects health If diploma only affects resources If diploma affects health & resources Negative Positive Indeterminate Number of Short Stay Hospital Episodes in Past 12 Months If diploma only affects health If diploma only affects resources If diploma affects health & resources Negative Positive Indeterminate 1 Where =1 if excellent, =2 if very good, =3 if good, =4 if fair, and =5 if poor. 2 Where <18.5 if underweight, 18.5 24.9 if normal, 25.0 29.9 if overweight, and 30.0+ if obese. 3 Usage variables are defines as those which are negatively affected by improved health (assuming better health necessitates less ne ed for care), but positively affected by increased resources (assuming greater accessibility encourages higher usage. regardless of health). Therefore, if a diploma simultaneously improves health and increases resources, then the expected signs are indete rminate.

PAGE 91

91 Table 2 4. First s tage e stimates Full Sample: Self Reported Health BMI Bed Days in Past 12 Months Doctor Visits in Past 12 Months HIGH SCHOOL DIPLOMA: 4th Threshold (i.e., exempt = post July 1, 1924 birthday) 5 month bandwidth 0.024 0.036 ** 0.036 ** 0.036 0.039 ** 0.034 ** (N =5,422) (0.023) (0.015) (0.014) (0.017) (0.014) (0.015) 4 month bandwidth 0.022 0.038 0.038 0.038 0.041 0.038 (N =4,451) (0.029) (0.020) (0.019) (0.024) (0.019) (0.019) 3 month bandwidth 0.038 0.057 *** 0.057 *** 0.061 *** 0.059 *** 0.057 *** (N =3,511) (0.021) (0.009) (0.008) (0.011) (0.010) (0.008) 2 month bandwidth 0.074 *** 0.070 *** 0.068 *** 0.077 *** 0.072 *** 0.066 *** (N =2,585) (0.001) (0.004) (0.005) (0.005) (0.007) (0.004) 1 month bandwith 1 0.005 *** 0.039 0.040 0.033 0.048 0.033 (N =1,615) (0.000) (0.012) (0.013) (0.012) (0.013) (0.012) COLLEGE DIPLOMA: 3rd Threshold (i.e., exempt = post January 1, 1922 birthday) 7 month bandwidth 0.050 *** 0.051 *** 0.052 *** 0.051 *** 0.051 *** 0.052 *** (N =7,002) (0.010) (0.011) (0.011) (0.011) (0.011) (0.011) 6 month bandwidth 0.040 *** 0.043 *** 0.043 *** 0.043 *** 0.043 *** 0.044 *** (N=6,046) (0.010) (0.011) (0.011) (0.010) (0.011) (0.011) 5 month bandwidth 0.049 *** 0.050 *** 0.051 *** 0.049 *** 0.050 *** 0.052 *** (N=5,140) (0.009) (0.010) (0.010) (0.010) (0.011) (0.010) 4 month bandwidth 0.041 *** 0.044 *** 0.043 *** 0.041 *** 0.043 *** 0.044 *** (N=4,155) (0.008) (0.009) (0.008) (0.008) (0.010) (0.009) 3 month bandwidth 0.038 *** 0.036 *** 0.037 *** 0.035 *** 0.033 *** 0.037 *** (N=3,236) (0.007) (0.006) (0.006) (0.006) (0.006) (0.006) 2 month bandwidth 0.055 *** 0.041 *** 0.042 *** 0.039 *** 0.035 *** 0.041 *** (N=2,350) (0.009) (0.004) (0.004) (0.004) (0.005) (0.004) 1 month bandwith 1 0.035 *** 0.033 0.035 0.032 0.026 0.034 (N=1,460) (0.000) (0.010) (0.010) (0.010) (0.010) (0.010) 2nd Threshold (i.e., exempt = post July 2, 1920 birthday) 7 month bandwidth 0.016 0.014 0.014 0.014 0.016 0.012 (N =6,536) (0.019) (0.020) (0.020) (0.020) (0.020) (0.020) 6 month bandwidth 0.003 0.006 0.007 0.008 0.005 0.008 (N=5,673) (0.012) (0.013) (0.013) (0.012) (0.012) (0.012) 5 month bandwidth 0.003 0.002 0.003 0.002 0.000 0.004 (N=4,779) (0.011) (0.011) (0.011) (0.011) (0.011) (0.011) 4 month bandwidth 0.000 0.004 0.005 0.004 0.002 0.004 (N=3,951) (0.011) (0.010) (0.010) (0.010) (0.010) (0.011) 3 month bandwidth 0.003 0.007 0.007 0.005 0.005 0.007 (N=3,107) (0.011) (0.009) (0.009) (0.010) (0.010) (0.009)

PAGE 92

92 Table 2 4. First stage estimates (continued) Full Sample: Self Reported Health BMI Bed Days in Past 12 Months Doctor Visits in Past 12 Months 2 month bandwith 0.015 ** 0.013 ** 0.014 ** 0.016 ** 0.016 ** 0.013 ** (N=2,276) (0.003) (0.004) (0.004) (0.004) (0.004) (0.004) 1 month bandwith 1 0.044 *** 0.039 ** 0.039 ** 0.042 ** 0.042 *** 0.039 ** (N=1,410) (0.000) (0.004) (0.004) (0.004) (0.004) (0.004) 1st Threshold (i.e., exempt = post October 17, 1919 birthday) 7 month bandwidth 0.030 0.027 0.027 0.030 0.026 0.025 (N=6,199) (0.020) (0.021) (0.022) (0.022) (0.021) (0.021) 6 month bandwidth 0.033 0.029 0.030 0.033 0.031 0.028 (N=5,373) (0.023) (0.023) (0.024) (0.025) (0.023) (0.023) 5 month bandwidth 0.017 0.014 0.015 0.017 0.015 0.013 (N=4,530) (0.022) (0.023) (0.024) (0.024) (0.023) (0.023) 4 month bandwidth 0.012 0.012 0.012 0.014 0.012 0.008 (N=3,785) (0.022) (0.024) (0.025) (0.026) (0.024) (0.023) 3 month bandwidth 0.007 0.003 0.005 0.004 0.002 0.000 (N=3,006) (0.025) (0.028) (0.029) (0.029) (0.027) (0.027) 2 month bandwidth 0.039 0.048 0.049 0.051 0.046 0.049 (N=2,120) (0.020) (0.022) (0.022) (0.024) (0.023) (0.023) 1 month bandwith 1 0.049 *** 0.039 ** 0.040 ** 0.041 ** 0.043 ** 0.037 ** (N=1,278) (0.000) (0.005) (0.005) (0.005) (0.005) (0.005) Stacked Threshold (i.e., exempt st = post January 1, '22; or July 2, '20; or October 17, '19 birthday) 3 month bandwidth 0.012 0.011 0.010 0.010 0.011 0.012 (N=9,349) (0.012) (0.012) (0.012) (0.012) (0.012) (0.012) 2 month bandwidth 0.038 ** 0.036 ** 0.037 ** 0.037 ** 0.034 ** 0.037 ** (N=6,746) (0.008) (0.010) (0.010) (0.010) (0.010) (0.010) 1 month bandwith 1 0.013 *** 0.014 *** 0.014 *** 0.014 ** 0.012 *** 0.016 *** (N=4,148) (0.001) (0.001) (0.001) (0.001) (0.001) (0.001) Controls 2 N Y Y Y Y Y For sample size consistency, first stage estimates are presented by health measure so that observations omitted in the reduced form models (because of missing health values) are not included in the associated first stage. The health measures with no missing values (full sample) are short stay hospital episode days in past 12 months, number of short stay hospital episodes in past 12 months, number of acu te incidence conditions, and number of conditions. parentheses are robust standard errors clustered by MOB. The stacked model is clustered by the stacked MOB running variable. 1 The regressions using a 1 month bandwidth do not include interaction between 'exempt' and MOB due to collinearity. 2 The controls include marital status, race, ethnicity, MSA, geographic region, veteran status, and survey year. Individual threshold fixed effects are also included in the stacked model.

PAGE 93

93 Table 2 5. Wald e stimates: High s chool d iploma E FFECTS ON HEALTH OUTCOMES : Self Reported Health BMI Number of Acute Incidence Conditions Number of Conditions 5 month bandwidth 4.154 5.266 0.167 2.496 0.475 0.442 5.701 ** 6.784 ** (N=5,422) (2.157) (3.052) (7.893) (6.484) (0.375) (0.389) (2.178) (2.623) 4 month bandwidth 4.159 4.733 NS NS 0.369 0.382 7.005 7.865 (N=4,451) (2.537) (3.295) (0.363) (0.428) (3.313) (4.075) 3 month bandwidth 1.599 1.997 ** 6.159 5.317 0.092 0.143 3.269 *** 4.400 *** (N=3,511) (0.748) (0.767) (4.346) (2.963) (0.094) (0.175) (0.734) (0.868) 2 month bandwidth 1.513 1.217 6.399 4.648 ** 0.001 0.170 *** 2.627 ** 4.038 *** (N=2,585) (0.716) (0.493) (3.461) (1.672) (0.095) (0.024) (0.741) (0.734) 1 month bandwith 1 5.099 5.099 NS NS 0.047 0.047 8.097 8.097 (N=1,615) (1.546) (1.546) (0.061) (0.061) (2.745) (2.745) E FFECTS ON HEALTHCARE USAGE : Bed Days in Past 12 Months Doctor Visits in Past 12 Months Short Stay Hospital Episode Days in Past 12 Months Number of Short Stay Hospital Episodes in Past 12 Months 5 month bandwidth 74.488 64.417 17.670 13.024 23.785 31.723 1.000 1.512 (N=5,422) (45.570) (43.456) (14.244) (7.420) (17.218) (24.419) (1.084) (1.630) 4 month bandwidth 79.480 75.607 1.390 1.000 20.219 20.982 1.124 1.087 (N=4,451) (45.150) (37.648) (10.525) (9.522) (16.204) (17.848) (1.190) (1.368) 3 month bandwidth 27.852 45.351 11.940 6.330 9.281 13.504 0.749 0.710 (N=3,511) (37.420) (28.889) (6.038) (8.038) (6.581) (9.697) (0.553) (0.740) 2 month bandwidth 20.345 65.279 7.982 16.274 *** 2.853 1.581 0.403 0.651 *** (N=2,585) (47.369) (27.248) (7.322) (2.786) (7.302) (4.018) (0.582) (0.106) 1 month bandwith 1 55.082 ** 55.082 ** NS NS 24.724 24.724 0.416 ** 0.416 ** (N=1,615) (11.992) (11.992) (9.488) (9.488) (0.095) (0.095) Interaction Term N Y N Y N Y N Y Controls 2 Y Y Y Y Y Y Y Y statistically significant first confidence level. Values in parentheses are robust standard errors clustered by MOB. The reported N's are for the full samp le (i.e., health measures with no and highlighted estimates are for the optimal bandwidth according to cross validation. 1 The regressions using a 1 month bandwidth do not include interaction between 'exempt' and MOB due to collinearity. 2 The controls include marital status, race, ethn icity, MSA, geographic region, veteran status, and survey year

PAGE 94

94 Table 2 6. Wald e stimates: c ollege d iploma E FFECTS ON HEALTH OUTCOMES : Self Reported Health BMI Number of Acute Incidence Conditions Number of Conditions 3 month bandwidth NS NS NS NS NS NS NS NS (N=9,349) 2 month bandwidth 1.995 2.044 ** 0.351 3.230 *** 0.192 0.256 *** 0.654 3.768 *** (N=6,746) (0.783) (0.682) (2.601) (0.277) (0.342) (0.048) (2.200) (0.442) 1 month bandwith 1 7.102 *** 7.102 *** 3.716 3.716 0.985 *** 0.985 *** 2.977 2.977 (N=4,148) (0.389) (0.389) (3.222) (3.222) (0.068) (0.068) (0.924) (0.924) E FFECTS ON HEALTHCARE USAGE : Bed Days in Past 12 Months Doctor Visits in Past 12 Months Short Stay Hospital Episode Days in Past 12 Months Number of Short Stay Hospital Episodes in Past 12 Months 3 month bandwidth NS NS NS NS NS NS NS NS (N=9,349) 2 month bandwidth 17.717 45.502 8.380 4.817 14.269 21.280 1.273 0.704 ** (N=6,746) (24.304) (29.085) (8.975) (6.223) (8.371) (9.765) (0.502) (0.197) 1 month bandwith 1 164.890 *** 164.890 *** 21.910 ** 21.910 ** 61.877 *** 61.877 *** 2.892 *** 2.892 *** (N=4,148) (10.618) (10.618) (5.113) (5.113) (3.809) (3.809) (0.148) (0.148) Interaction Term N Y N Y N Y N Y Controls 2 Y Y Y Y Y Y Y Y statistically significant first confidence level. Values in parentheses are robust standard errors clustered by the stacked MOB running variable. The repor ted N's are for the full sample (i.e., health measures with no missing values); however, sample sizes in th optimal bandwidth according to cross validation. 1 The regressions using a 1 month bandwidth do not include interaction between 'exempt' and MOB due to collinearit y. 2 The controls include individual threshold fixed effects, marital status, race, ethnicity, MSA, geographic region, veteran sta tus, and survey year.

PAGE 95

95 Table 2 7. OLS e stimates Effects on Health Outcomes Effects on Healthcare Usage Self Reported Health BMI Number of Acute Incidence Conditions Number of Conditions Bed Days in Past 12 Months Doctor Visits in Past 12 Months Short Stay Hospital Episode Days in Past 12 Months Number of Short Stay Hospital Episodes in Past 12 Months HIGH SCHOOL DIPLOMA 0.541 *** 0.378 *** 0.003 0.323 *** 6.244 *** 0.811 *** 0.688 *** 0.040 *** (N=31,500) (0.014) (0.052) (0.002) (0.022) (0.544) (0.149) (0.102) (0.008) COLLGE DIPLOMA 0.563 *** 0.614 *** 0.003 0.231 *** 4.612 *** 0.553 *** 0.521 *** 0.038 *** (N=31,500) (0.019) (0.059) (0.003) (0.028) (0.454) (0.152) (0.108) (0.010) Controls 1 Y Y Y Y Y Y Y Y OLS estimates are among the males born between April 1919 (7 months prior to the first threshold) and December 1924 (5 months after the last threshold). Stars parentheses are robust standard errors clustered by MOB. 1 These include the same controls used in the regression discontinuity model (i.e., marital status, race, ethnicity, MSA, geogr aphic region, veteran status, and survey year).

PAGE 96

96 CHAPTER 3 RAISING THE BOTTOM LINE: THE EFFECT OF MEDICAID MANAGED CARE ON SAFETY NET HOSPITALS This study examines the effect of mandated Medicaid managed care on safety net are Act, Disproportionate Share Hospital (DSH) payments (from which safety nets directly benefit) have been reduced while nearly one half of U.S. states have decided not to expand Medicaid, affecting d by safety nets). Meanwhile, there has been an increasing trend towards the use of managed care in Medicaid. To estimate the effect of this type of Medicaid provision on safety net hospitals, I take advantage of a Medicaid Reform Pilot Program, first la unched in two Florida counties in 2006, which required Medicaid in differences in compensation net vs. non safety net hospitals, and (iii) among patients who resided inside vs. outside of reform counties. In doing so, I gain an estimate for the effect of mandated Medicaid man aged care which is not biased by state selection into a reform program. The results suggest that, in Florida, mandated Medicaid managed care widened the gap between safety caring for the uninsured by any addition al 0.9 percentage point, and reinforced safety relatively lower probability of caring for the privately insured by 3.5 percentage points. This, in turn, caused safety nets to fall behind other facilities, in terms of expected compensation, by an add itional $1,769 per patient, on average. 3. 1 Introduction In a Washington Post blog discussing the effects of the Affordable Care Act (ACA) on

PAGE 97

97 officials say that the Affordable Care Act could now be the worst thing to happen to the hospital an 121 year punch blow, the facility (which serves a disproportionately large s hare of uninsured patients) will reductions to Disproportionate Share Hospital (DSH) payments, which provide additional funds to facilities that care for large numbers of non paying patrons. (Blau, 2013) In short, Grady will be left with no fewer uninsured patients at their doorstep and less money to care for them. Similar to Georgia, 20 other states have chosen not to expand Medicaid under ACA. Consequently, these stat net hospitals are also expected to be financially constrained by the law. Alongside this decision, many states are moving towards a Medicaid structure based on managed care. It is, therefore, worth considering whether such a qualitative reform to Medicaid might at all alleviate the effects of ACA on safety net hospitals, and particularly among those which are located in states that have chosen not to expand their Medicaid program. To determine the effects of Medicaid managed care on safety net one could easily compare compensation patterns across states with different levels of Medicaid managed care participation. The endogeneity concern which arises, however, is that states do not at random decide to provide managed care. That is, when a state selects into Medicaid managed care provision, the decision is almost certainly correlated with other state level factors which, on their own, affect Y. 22 Because of this, it is difficult to determine whether managed care, itse lf, causes Y, or whether observed effects on Y are actually due to other state level factors unique to the region(s) choosing to reform. To account for this concern, this study takes advantage of a Medicaid Reform Pilot Program which was implemented in fi ve counties within a 22 Possible examples include Medicaid eligibility thresholds (which vary widely from state to state), the level of

PAGE 98

98 single state. In this way, all state level factors (which affect Medicaid provision, among other things) remain constant across reformed and non exogenous. The specific experiment this study m which was first launched in 2006 in two counties, and then expanded by three counties in 2007. Rather than offering Medicaid enrollees a traditional public insurance plan (in which the state, itself, reimburs es providers), enrollees living in the pilot counties were required to choose from a set of private insurance plans, managed by HMOs and Provider Service Networks (PSNs) 23 Because the Pilot Program began prior to any reductions in DSH payments or (potenti al) expansions in Medicaid, I can use pre versus post launch differences in safety compensation patterns to estimate the effects of the reform. I can further control for any differences in the reform counties, themselves, by conditioning m y findings on the outcomes non safety net hospitals. 24 And, to account for any trends which were unique to safety net hospitals, but independent of the reform, I can condi tion my findings on the outcomes of individuals who visited safety net hospitals, but who lived outside I am left with a triple difference estimate. The data used to conduct this analysis consists of individ ual level observations on every hospital discharge in the state of Florida between the years of 2000 and 2012. Because this 23 According to the Florida Agency for Health Care Administration network established or organized and operated by a health care provider or group of affiliated health care providers, including minority physician networks and emergency room diversion programs th at meet the requirements of 24 Not only does this particular comparison s may have been systematically different but it also allows me to estimate nets, compared to the effect it had on other hospitals.

PAGE 99

99 dataset identifies the specific hospitals from which patients were discharged, as well as their year and quarter of discharge, I am able to precisely assign treatment classification (i.e., safety net vs. non safety net hospital, residency inside vs. outside of a reform county, and pre versus post ent and total gross charges, I am able to construct a variety of dependent variables to determine from whom, and how much, safety net hospitals were expected to be compensated. The results of this study suggest that safety net hospitals were adversely a ffected by the mandated shift to Medicaid managed care. Though the reform did result in an increased likelihood of any one safety net patient being covered by Medicaid, the reform also resulted in a disproportionate increase in the likelihood of any one s afety net patient being covered by no insurance; as a result of the reform, the rift between safety safety propensities to care for the uninsured grew by 0.9 percentage point. Although, relative to their pre reform pricing spread, safet y nets responded by charging an average of $313 more than their non safety net counterparts, per visit, this adjustment was not enough to fully offset the shift they i mplementation of mandated Medicaid manage care caused the relative weight of uncompensated care borne by safety nets to grow by $1,769 per patient. 3. 2 Background 3. 2.1 The Affordable Care Act and Safety Net Hospitals On March 23, 2010, the Affordable C are Act (ACA) was signed into law by President Barack Obama. One of the hallmark features of the original bill was its mandated expansion of Medicaid to cover all individuals with incomes up to 133% of the federal poverty line. Among other things, it was thought that this provision would alleviate some of the financial burden felt

PAGE 100

100 by safety nets as many of their (non paying) uninsured patients would be nudged under the umbrella of public insurance. Given the presumed expansion of Medicaid, it was logi cal (at the time) to assume that once ACA was fully implemented, safety net hospitals would have less need for DHS payments (which give additional funds to facilities that incur high rates of uncompensated care). As a result, ACA also prescribed significa then safety nets would merely have to deal with a three month lag before the DSH cuts, set to Jan uary 1, 2014. The problem, however, was that for 25 states, the balance did not tilt. Immediately following the passage of ACA, over half of the U.S. states filed lawsuits against the federal government challenging the constitutionality of the law, and, in 2012, ACA mandated expansion of Medicaid. Instead, it was determined that every state could choose whether to expand its Medicaid program to cover individual s with incomes up to 133% of the federal poverty line. If expansion was chosen, then the federal government would match 100% gradually decline. On October 1, 2013 as scheduled DSH cuts were implemented in all 50 states. On January 1, 2014 the deadline initially set for mandatory Medicaid expansion only 25 states were on track to expand. Four states remained undecided as to their expansion decision, and the remaining 21 states had decided against expansion. (Where, 2014) For safety net hospitals in these 21 states, the expected net financial effects of ACA were grim. One such state facing this conern was Florida.

PAGE 101

101 3. ilot Program Five years prior to the enactment of ACA, on Oct 19, 2005, the state of Florida was granted permission by the Centers for Medicare and Medicaid Services to launch a comprehensive Medicaid Reform Pilot Program. The aim of the Pilot Program was to encourage patient flexibility by allowing Medicaid enrollees to receive their health insurance coverage through either a Medicaid HMO or through a PSN. The PSNs differed from the commercially licensed HMOs contracted by the state in that the PSNs were directly controlled and operated by Florida physicians. Additionally, unlike the HMOs (which were only reimbursed using a capitated rate), the state allowed PSNs to be reimbursed using either a fee for service or capitated rate. (Pilot) Beginning on Jul y 1, 2006, the Pilot Program took effect in Broward and Duval counties. The following year, on July 1, 2007, the Pilot Program expanded to include Baker, Clay and Nassau counties. (Florida) The location of these reform counties is shown in Figure 3 1. Consistent with the federal standard for managed care, each of the reform counties offered their Medicaid enrollees at least two insurance plans to choose between. At the time of Pilot Program launch, Medicaid enrollees in Broward county (population ~1.75 M) were allowed to choose between a set of ten HMOs and five PSNs, enrollees in Duval county (population ~0.85M) were allowed to choose between a set of four HMOs and three PSNs, and enrollees in Baker, Clay, and Nassau counties (the rural counties surroun ding Duval) could each choose between one HMO and one PSN. 25 If an individual failed to select a plan, then he/she was 25 Over time, the list of Medicaid HMOs and PSNs available to Medic aid enrollees in particular counties fluctuated program was made available to Medicaid enrollees so that qualified individuals could use (what would ha ve been) the dollar value of their Medicaid benefits to enroll in employer provided coverage. However, there was little participation in this program.

PAGE 102

102 2011, Final Bill Analysis) For families with i beneficiaries receiving Supplemental Security Income, participation was mandatory. Participation was optional fo r other populations. 26 (Medicaid, 2008 ) touted a success. Given the lower state expenditures that have come as a result of the reform (estimated to be $118M per year, FGA Letter), along with higher rates of enrollee satisfaction, the reform is now in the process of being enacted state wide. Meanwhile, across the country, the Government Accountability Office reports that: As Medicaid enrollment and spending have increased significantly over the past beneficiaries, and nearly all states enroll some Medicaid beneficia ries in a form of managed care. (Medicaid, 2012) to expand the size of its Medicaid program, might a qualitative change in the structure of a any of the burden felt by safety nets in terms of caring for the uninsured? 3. 2.3 The Link Between Medicaid Managed Care and Safety Net Hospitals Before turning our attention to the question of whether Medicaid managed care affects safety nets, it is first worth considering why Medicaid managed care might affect safety nets. There are at least two possible reasons to believe that such an effect might exis t. These are: (i) the possibility of a vertical shift in insurance tiers among the Medicaid eligible, and (ii) the possibility of a horizontal shift in facility selection among those actively enrolled in Medicaid. 26 arged from Florida hospitals (between the ages of 18 and 64) were already enrolled in some type of Medicaid managed care plan. Among Broward county Medicaid enrollees, this rate was 37%; in Duval county, 32%; in Baker county, 16%; in Clay county, 8%; and in Nassau county, 17%.

PAGE 103

103 First, it is possible that a qualitative change in Medicaid may incite/discourage participation in the program. Consequently, we might expect a systematic change in the average rate of reimbursement movement between tiers could affect safety compensation. Second, among those in the Medicaid tier, it is plausible to think that assignment to managed care might cause individuals to visit different facilities. If this is the case, then the i ntroduction of a Medicaid managed care program might result in a horizontal shift into or out of safety nets (among the publicly insured). Again, because the Medicaid tier represents some average rate of reimbursement, this could also affect safety net compensation. A graphical depiction of each of these possibilities is presented in Figure 3 2. To help determine whether there is any anecdotal evidence supporting these possibilities (and, consequently, whether there is any reason to believe that Med icaid managed care might have any effect on safety nets), Tables 3 1 and 3 2 present the frequencies of hospital discharges in Florida, before and after the reform, stratified by insurance tier and facility type (among the 18 64 year olds who lived in Flor privately insured before the reform, only 53% was privately insured after the reform. Before the reform, 22% and 14% were covered by Medicaid and no insurance, respectively. After the reform, thes e figures rose to 29% and 18%, respectively. However, among Medicaid enrollees, 53% chose to visit a safety net both before and after the reform. Together, these figures would suggest that the introduction of mandatory Medicaid managed care led to a vertical shift in insurance coverage among the Medicaid eligible but no horizontal shift into/out of safety nets among Medicaid enrollees.

PAGE 104

104 Given that there exists some evidence pointing towards a possible relation ship between Medicaid reform and safety itself. To answer the question of whether Medicaid managed care affects safety line, this study considering three retrospective outcomes Program. These are: (i) whether the net composition of safety of insurance coverage) by the reform, (ii) whether safety net hospitals responded to the reform by adjusting their total g ross charges at the patient level, and (iii) whether, post reform, there was any change in the amount of money safety net hospitals were reimbursed. 3. 3 Data The data used in this study comes from the Agency for Health Care Administration, Florida Center for Health Information and Policy Analysis, and consists of patient level observations for every hospital discharge in the state of Florida between the years of 2000 and f discharge, demographic information (including county of residency). Because safety net status is not explicitly defined in the dataset, safety net treatment is manually assigned by matching discharging facilities to the list of hospitals which are members of the Safety Net Hospital Alliance of Florida. 27 The entire sample consists of 32,705,130 observations. To facilitate estimation, two restrictions are made to the full sample. First, individuals 28 Second, only individuals between the ages of 18 and 64 are retained to avoid the possible 27 http://safetynetsflorida.org/ (Accessed February 2014) 28 Included in the omitted category are individuals with other sources of state/federal funding (e.g., TRICARE/CHAMPUS and VA).

PAGE 105

105 confounding effects of enrollment in M sample consists of 11,620,077 observations. 3. 4 Identification Procedure net hospitals, what I would like to estimate is: (A) (B) E(y it | Treated =1) E(y it | Treated =0) ( 3 1) where Treated is equal to one when the discharging hospital is a safety net and the discharged cannot simultaneously exist. That is, for a treated individual who meets bot h criteria of (i) living in a reform county at time t, and (ii) visiting a safety net at time t, the counterfactual of either not living in a reform county at time t and/or not visiting a safety net at time t will never materialize. To overcome this obstac le, difference in differences (DD) estimation is one alternative identification procedure which can be used to approximate the above effect. A DD estimate allows the econometrician to estimate what is close to the true effect of treatment by using another to one comparison, it then subtracts out any differences between the treated and untreat ed groups which existed at a time when neither group was eligible for treatment. In the case of the present study, one might do this by first narrowing the sample to include only safety net observations and then using, as the baseline comparison group, in dividuals who lived outside of the reform counties. In a simple two period model (where residence in a reform county is denoted R and the post reform period is denoted P ) this can be expressed as:

PAGE 106

106 Residence in Reformed vs. Non Reformed County Residence in Reformed vs. Non Reform County Difference, Post Reform Difference, Pre Reform (C) (D) [E(y it | R =1, P =1) E(y it | R =0, P =1)] [E(y it) | R =1, P =0) E(y it) | R =0, P =0)] ( 3 2) or, alternatively: Pre vs. Post Reform Difference, Pre vs. Post Reform Difference, Given Residence Within a Reform County Given Residence Outside of a Reform County (E) (F) [E(y it | R =1, P =1) E(y it | R =1, P =0)] [E(y it | R =0, P =1) E(y it) | R= 0, P =0)] ( 3 3) where the difference is interpreted as the effect of the reform among safety nets serving patients from reform counties, less the effect which emerged among the safety nets serving patients from non reform counties. While an improvement compared to equation ( 3 counterfactual effect of treatment, this procedure relies on a number of assumptions. First, it is assumed that the observed gap (in y) between the treated safety nets (se rving patients from reform counties) and control safety nets (serving patients from outside of the reform counties) at time P =0 is the same gap which would have emerged at time P =1, had the reform not occurred y requires (C) to equal (D) in the absence of reform so that the difference in differences remains unbiased. Alternatively, it is assumed that the observed jump (in y) among the control safety nets at the time of the reform is the same jump which would ha ve occurred among the treated safety nets at the time of the reform, had the reform not taken place That is, were it not for the Pilot Program, (E) would be equal to (F).

PAGE 107

107 While it is relatively easy to use time trends to graphically verify that the out comes among treated vs. untreated safety net hospitals parallel each other, it is less easy to verify that reform counties were randomly selected so that the residents of reform counties are not relatively more or less sensitive to manipulation. If so, the n the jump in (E) will be relatively inflated/deflated so that the difference between (E) and (F) will not align with the difference between (A) and (B). To account for the possibility that the reform county residents were innately more or less sensitive to the reform than the average individual, an additional outcome which we can condition on is the effect of the reform among individuals who lived inside of the reform counties, after the reform, but were yet untreated. Given the lack of evidence suggest ing that Medicaid recipients appeared at different hospitals after the reform (see Tables 3 1 and 3 2), individuals that visited non safety nets (but who were residents of the reform counties and were discharged after the reform), provide just such a compa rison group. By observing the effects of can be subtracted out. This leaves us with a differences in differences in differences (DDD) estimate for the ef fect of the reform. However, it should be noted that this strategy estimates a slightly different effect than the impact of the reform on safety nets directly. That is, this estimate tells us the impact of the reform on the dissimilarity between safety nets and other facilities. While using a DDD strategy as opposed to a DD strategy subtly alters the interpretation out the effects of the reform which were common to hospitals at large), it does provide a relatively more useful (and hol istic) picture of the effects of the reform on safety nets for two reasons. First, in the DDD framework, the model accounts for

PAGE 108

108 the fact that there may have been an existing spread in y between safety nets and non safety nets prior to the reform. Because of this, the DDD estimate allows us to measure the change in the spread, not just the isolated effect. From a policy standpoint, this estimate for the disproportional impact of the reform on safety nets is insightful because, under ACA, safety nets are e xpected to be disproportionately impacted by the federal reform. Second, the isolated effects of the reform on safety nets can still be obtained. That is, this strategy allows us to calculate the effects of the reform on safety nets directly and on thei should always be interpreted as the effect on their dissimilarity). By selectively differencing only the expected values in the DDD equation that are conditioned on SN =1, the independent effect of the r eform on safety nets is obtained (i.e., the effect which is not relative to other hospitals). In a simple two period model, where P denotes the post reform period, R denotes residency in a reform county, and SN denotes admittance to a safety net, this DDD estimate can be written as: Pre vs. Post Reform Difference, Less Any Changes in Non Safety Net Facilities, Given Residence Within a Reform County (G) {[E(y it | R =1, P =1, SN =1) E(y it | R =1, P =1, SN =0)] [E(y it | R =1, P =0, SN =1) E(y it | R =1, P =0, SN =0)]} ( 3 4) {[E(y it | R =0, P =1, SN =1) E(y it | R =0, P =1, SN =0)] [E(y it | R =0, P =0, SN =1) E(y it | R =0, P =0, SN =0]} (H) Pre vs. Post Reform Difference, Less Any Changes in Non Safety Net Facilities, Given Residence Outside of a Reform County Or, alternatively:

PAGE 109

109 Pre vs. Post Reform Difference, Less Any Changes Among Residents of Non Reformed Counties, Given Admittance to a Safety Net (I) {[E(y it | R =1, P =1, SN =1) E(y it | R =0, P =1, SN =1)] [E(y it | R =1, P =0, SN =1) E(y it | R =0, P =0, SN =1)]} ( 3 5) {[ E(y it | R =1, P =1, SN =0) E(y it | R =0, P =1, SN =0)] [E(y it | R =1, P =0, SN =0) E(y it | R =0, P =0, SN =0]} (J) Pre vs. Post Reform Difference, Less Any Changes Among Residents of Non Reform Counties, Given Admittance to a Non Safety Net Again, for clarity, in total, this equation tells us the extent to which safety nets were disproportionately affected by the implementation of mandated Medicaid managed care relative to non safety net hospitals. 3. 5 Estimation The DDD estimate given by equations ( 3 4) and ( 3 5) can be empirically estimated as follow s: Y it 0 1 R it 2 P it 3 SN it 4 (R*P) it 5 (R*SN) it 6 (P*SN) it 7 (R*P*SN) it it ( 3 6) 7 is analogous to the triple difference. However, in terms of the present study, the multi period implementation of the Medicaid Reform Pilot Program, along with the availability of 13 years of quarterly data, complicates the definition of P in equation ( 3 6). This is because, first, across a period of 13 years there are likely time trends which deserve consideration (unlike in the two period model), and, more importantly, because since P switches on at different times for different people, it will necessarily be indeterminate any time R is undefined. As an example, for a discharge in July of 2006, it is impossible to assign P =1 or P =0 status without first knowing whether R =1 or R =0 (i. e., whether the discharged individual lived in a reform county at the time). To address this, this paper first defines P =0 to be all

PAGE 110

110 discharges which occurred prior to July 1, 2006 (that is, prior to the implementation of the reform in any of the Florida counties) and defines P =1 to be all discharges which occurred on/after July 1, 2007 (that is, after all five reform counties were eventually reformed). Although this simple two period structure has obvious limitations, it does provide a way of cleanly ver ifying that the regression results align with the conditional expectations given by equations ( 3 4) and ( 3 5). Next, as the primary focus of this paper, equation ( 3 6) is amended so that P is replaced by a vector of quarter of discharge dummy variables ( Q independent of R Additionally, patient level demographic variables are added so that the model is specified as follows: Y it 0 1 R it 2 it 3 SN it 4 ( R*P) it 5 (R*SN) it 6 it 7 (R*P*SN) it 7 X it it ( 3 7) where: R=1 if discharged individual was a resident of a county that was reformed in either 2006 or 2007 ; R =0 if discharged individual was a resident of a county that was never reformed : Set of d ummies for quarter of discharge SN = 1 if individual discharged from a safety net ; SN =0 if individual discharged from a non safety net (R*P)=1 if individual discharged on/after July 1, 2006 AND resident of Broward or Duval or if individual dischar ged on/after July 1, 2007 AND resident of Broward, Duval, Baker, Clay or Nassau ; (R*P) =0 otherwise (R*SN)=1 if individual was a resident of a county that was reformed on either July 1, 2006 or July 1, 2007 AND discharged from a safety net ; (R*SN) =0 otherwi se = (Set of dummies for quarter of discharge, where any value among a non safety net facility is replaced with a zero) (R*P*SN)=1 if individual discharged on/after July 1, 2006 from a safety net AND resident of Broward or Duval or if individual dis charged on/after July 1, 2007 from a safety net AND resident of Broward, Duval, Baker, Clay or Nassau ; (R*P*SN) =0 otherwise

PAGE 111

111 : Controls for age, race, ethn icity and gender 7 is the coefficient of interest representing the tripe difference estima te for the effect of the reform on safety 7 coefficient outlined in equation ( 3 5). To answer the three questions of interest in this study, namely: (i) how Floridians, appearing at safety nets, responded to the reform in terms of their choice of insurance coverage, (ii) how Florida safety nets responded to the reform in terms of the amou nt of money they charged their patients, and (iii) the net effect of the reform on the amount of money safety nets were reimbursed, the dependent variable is allowed to take on one of five values. First, to determine how safety net patients responded to the reform, in terms of their choice of insurance coverage, y it is defined as: Uninsured=1 if uninsured ; Uninsured =0 if privately insured or enrolled in Medicaid Medicaid=1 if enrolled in Medicaid ; Medicaid =0 if privately insured or uninsured Privately In sured= 1 if privately insured ; Privately Insured =0 if enrolled in Medicaid or uninsured To determine how safety net hospitals responded in their pricing, y it is defined as: Total Gross Charges : Total dollar amount of undiscounted charges, excluding profes sional fees Finally, to determine the net effect of the reform on safety amount of money received from individual i, discharged at time t, is constructed. Here, y it is defined as: ; Money Received = ; Money Received

PAGE 112

112 The values of these approximations come from aggregated data on average reimbursement rates acros s insurance tiers. According to a 2009 Medicare Payment Advisory Commission report, "Medicare payment rates continue to be about 80 percent of private insurance payment rates as they have for the past decade," and, according to the Kaiser Foundation, Flor to Medicare Fee Index is 0.57. 29 (Medicare Payment, 2009; Medicaid to Medicare) Together, these to figures yield the 0.80*0.57=45.6% approximation for realized reimbursement from Medicaid enrollees. The approximation for uninsured patien on average afford to pay the full bills for only about 12% of the hospitalizations they might experience." 30 (The Value, 2011) Though this assertion does not necessarily imply that the average per patient reimbursement rate is 12%, if the uninsured families who cannot afford to pay the full bill provide close to zero compensation, then, among the uninsured, the average per patient reimbursement rate will be close to 12%. 3. 6 Results Presented in Table 3 3 are the mean values for each of the dependent variables. Compared to non Reform Pilot Program had relatively higher rates of safety net visits, both pre and post reform. The majority of hospital discharges in the state of Florida were among privately insured individuals, and average total gross charge to an individual was in the range of approximatel y 29 This figure is based on the 2012 Medicaid to Medicare Fee Index. 30 Note, these imputations hinge on the assumption that hospitals receive 100% compensation from the privately insured. While this does not require that private insurance companies cover 100 % of charges, it does assume that hospitals are able to squeeze any excess (uncovered) charges out of privately insured individuals, themselves. If so, then they will be fully reimbursed.

PAGE 113

113 $20,000 to $36,000, per hospital stay, depending on the time period. 31 The average amount of money hospitals received per visit ranged from approximately $16,000 to $26,000, depending on the time period, corresponding to roughly three quarters of their charges. Tables 3 4 through 3 8 present the unadjusted conditional expec tations for each term outlined in equations ( 3 4) and ( 3 5). As shown, these means can be manually subtracted to of equation ( 3 Non Safety equation ( 3 5). The results of the associated regression form of the two period DDD analysis (given by equation ( 3 6)), are presented in Table 3 9. For ease of comparison, Tables 3 4 through 3 8 also list th e associated regression coefficients (from Table 3 9) which can be used to obtain the same values. The DDD estimates that include quarter of discharge fixed effects, to account for time trends and the staggered implementation of the reform, are given in Table 3 10. These results correspond to equation ( 3 7). Because this specification is believed to provide the most robust nets, the results from this model are used for the remainder of the discussio n. To answer the question of whether mandated Medicaid managed care caused the composition of safety Table 3 10 present the effects of the Pilot Program on the relative likelihoo d of a safety net serving an uninsured individual, a Medicaid enrollee, and a privately insured individual. statistically significant 0.9 percentage point increase i n the gap between safety 31 These figures are not adjusted for inflation.

PAGE 114

114 originally felt by safety nets namely, their disproportionate load of uninsured patients was exacerbated by the refo rm. The reform also led to a widened gap in the likelihood of a safety net serving a Medicaid patient, with these facilities pulling ahead of others by an additional 2.6 percentage points. Given these relatively heavier weights of patients at lower insur ance tiers, safety Program, safety declined by 3.5 percentage points. This is a concerning outcome as private insurance plans typically provide the highest rates of reimbursements. In short, these results suggest that Pilot Program resulted in a unique downward shift in the insurance coverage of safety net patrons. The next qu estion of interest in this study is: What did the reform cause safety nets to do, in terms of pricing? According to the fourth column of Table 3 10, safety nets responded by increasing their prices, relative to what they were charging, compared to other h ospitals, before the reform. This is perhaps not surprising given that these facilities also experienced a unique dual (that is, an individual from a pilot county) would have been charged at a safety net vs. a non safety net before the reform, after the reform, the price charged at safety nets became $313 higher, on average. This is not to say that safety nets necess arily raised their prices, but that the disparity in the pricing spread between safety nets and other facilities was altered as a direct result of the reform. To give an illustration, if we think of this as a race between safety nets and other hospitals, start from different positions, then, by the end of the race, safety nets will have traveled forward $313 more steps than their opponent.

PAGE 115

115 The final question this paper seeks to answer is: What was the net effect of the ref orm on safety net patients appear to have responded by moving to lower tiers of insurance coverage, one might assume that the reform had a relatively negative effect on safety nets. However, there is also evidence tha t safety nets responded to the reform by becoming relatively more aggressive in the amount of money they were charging their patients. It is plausible, then, that this latter response may have off set the relatively lower rates of realized reimbursement. As shown in the final column of Table 3 10, this does not appear to be the case. Instead, it appears as though the change in charges was insufficient to counter the lower rates of reimbursement. It is estimated that the net effect of the reform was an a dditional $1,769 reduction the amount of money each safety net hospital was expected to receive, per patient, relative other facilities. That is, starting from the initial imbalance in between safety move to mandated Medicaid managed care reinforced the imbalance, with safety nets, once again, falling short. 3. 7 Discussion Given the findings of this study which suggest that Medicaid managed care intensified the relative weight of uncompensated care ca rried by safety nets in Florida, there are two issues which merit discussion. First, it is important to consider the isolated impact of the reform on safety nets, which is independent of other facilities. If the reform resulted in a systematic reduction in uncompensated care across all Florida hospitals, than an increase in the disparity between safety nets and other facilities may not have necessarily hurt safety nets, relative to their pre reform position. Second, in order to gauge the generalizability of these findings specific implementations of Medicaid managed care, are considered.

PAGE 116

116 As discussed previously, a simple DD estimate comparing the pre vs. post re form difference in safety nets caring for patients who lived inside vs. outside of reform counties (as given by equations ( 3 2) and ( 3 3)) would yield the isolated effect of the Pilot Program on safety nets. Upon observation, one will note that this DD es timate is identical to portion (I) of the two period DDD model outlined in equation ( 3 5). Moreover, as shown by the top panels of Tables 3 4 through 3 8, this estimate is also identical to the two period regression coefficient 4 7 That is, the estima te for the effect of the reform on safety nets, independent of other facilities, is numerically equivalent to the summation of the coefficients on the interaction terms ( R*P ) and ( R*P*SN ). In the DDD model that accounts for time trends and the multi perio d implementation of the reform, this corresponds to 4 7 32 Using the coefficients in Table 3 10, the results suggest that the isolated effect of the Pilot Program on safety net hospitals was a 1.8 percentage point increase in their likelihood of caring for an uninsured individual. Given that the reform also increased their likelihood of caring for Medicaid enrollees (by 2.2 percentage points), this left safety nets a whole 4.0 percentage points less likely to have a visit covered by private insurance. Comparing these DD estimates to the DDD estimates, we see that not only did the reform cause the initial gap between safety the end of the day, it also left safety nets further behind their own initial starting point. In terms of the direct effect of the reform on the amount of money safety nets charged, an interesting result emerges. Although the reform caused safety nets to increase their prices, relative to what they were charging, compared to other hospitals, before the reform, it did succeed in bringing down charges overall. Ultimately, it is estimated that the implementation of 32 Using a similar r ationale, we can also obtain the effects of the reform on only non safety net facilities, which is equivalent to the coefficients on ( R*P ), or 4

PAGE 117

117 nets to charge $1,051 less, per patient, tha n they did prior to the reform. To put this in context with the DDD estimate, this indicates that the reform caused all Florida hospitals to decrease their prices (on average), but it caused safety nets to decrease their prices by slightly ($313) less tha n other facilities. Finally, perhaps of greatest significance, it is estimated that the isolated effect of money safety nets were expected to be compensated, on average. That is, while other facilities received ($561, per patient) less compensation after the reform, safety nets received ($1,769, per patient) even less compensation after the reform. What this meant was that, withstanding the effect of the refo rm on the spread between safety reimbursement, safety nets were made strictly worse off. Although the above results paint a grim picture of the effects of Medicaid managed care on safety nets, it should be reiterated that these results do not necessarily support or refute the overall merit of Medicaid managed care. They say nothing as to whether this Medicaid structure saves the state money, increases enrollee satisfaction, or affects public health. They also do not speak to the effects of the reform on healthcare providers that work in outpatient settings. They only evaluate the effects of the reform on hospitals, and, specifically, on the compensation that hospitals receive from the portion of their patients that a re admitted. Lastly, so that these results may be put in perspective, it is important to note that the will not perfectly align with other

PAGE 118

118 managed care program are h ighlighted. The first factor is related to the marginal impact of Florida. First, when Medicaid managed care was mandated in Florida, the pilot counties did not s tart from a point of 0% participation in Medicaid managed care and then move to a rate of 100% participation. Prior to the reform, the option of managed care was available to Medicaid enrollees (state wide), and, even after the reform, particular individu als living in the reform were Government Accountability of the Florida Legislature reported post implementation participation rates: A little more than a year an d a half after implementing Reform in Broward and Duval counties, 187,264 Medicaid beneficiaries were enrolled in a Reform health In the expansion counties, (Baker, Clay, a nd Nassau) where enrollment began in September 2007, AHCA had enrolled 13,419 Medicaid beneficiaries in Reform health plans as of May 2008, representing slightly over half (55%) of the 24,374 Medicaid beneficiaries in these counties. (Medicaid, 2008) Give n that roughly 35% of Medicaid enrollees in Broward and Duval counties, and 15% of Medicaid enrollees in Baker, Clay and Nassau counties, were already voluntarily participating in Medicaid managed care prior to the reform (see footnote 26 ), this suggests that, on the margin, approximately one third of the Medicaid participants living in the pilot counties. Therefore, the results of this study should be interpreted as the marginal effect of mandating Medicaid managed care, when the margin is roughly one third. Second, as opposed to only allowing HMOs to participate in their Medicaid managed care program, Florida also allowed Provider Service Networks to participate. Becaus e Florida also gave Medicaid enrollees the ability to replace their HMO/PSN plans when more attractive

PAGE 119

119 plans became available, this allowed the better performing networks to gain market share. Recently, there is evidence that, in Florida, PSNs (which were not forcefully tied to capitated reimbursement rates) fare better than Medicaid HMOs. According to one University of Florida study, PSNs save approximately $7 more, per member, per month than do Medicaid HMOs. Additionally, enrollees covered by PSNs rep ort slightly higher levels of satisfaction than those to PSN coverage (among pilot county enrollees) was 73% to 27%, by August 2011, this ratio had fallen to 53% to 47%. (Bragdon, 2011) Therefore, the results of this study should be interpreted as the effects of a Medicaid managed care system that is highly comprised on non HMOs. 3. 8 Conclusion ordable Care Act, in conjunction with DSH cuts, alternative methods of alleviating safety financial burden have become pressing concerns. One potential alternative method is to qualitatively reform Medicaid so that eligible, but yet unenrolled, individuals are incited to sign up for coverage. In 2006, the state of Florida launched their Medicaid Reform Pilot Program which had the potential of doing just this. In order to determine whether Medicaid managed care (as mandated in Flo Medicaid Reform Pilot Program) had any disproportionate effect on the financial burden felt by safety net hospitals, relative to non safety net hospitals, triple difference estimation is employed. Using 13 years of individual level hospital dischar ge data, I compare pre versus post reform differences in safety inside versus outside of reform counties, and individuals who appeared at safety net versus non safety net facilities. In similar populations which were left untreated.

PAGE 120

120 The results of this paper suggest a three Program on safety net facilities. First, relati ve to non safety net facilities, the reform resulted in a heavier weight of uninsured patients. Second, in response to the reform, safety net hospitals lowered the amount of money they were charging their patients, but by less than the amount that non saf ety nets became relatively more aggressive as a result of the reform. Finally, using a proxy for monetary compensation, triple difference estimation suggests that the reform had a sta tistically significant negative effect on the level of compensation safety nets received. Relative to non safety net facilities, it is estimated that the implementation of mandatory Medicaid managed care directly resulted in a $1,769 reduction in safety n

PAGE 121

121 Figure 3 1. Map of r eform c ounties Figure 3 2 Possible effects of Medicaid managed care reform on hospital patrons

PAGE 122

122 Table 3 1. Pre r eform N, a mong r eform c ounty r esidents Non SN SN Private 407,320 201,323 64% Medicaid 95,671 107,430 22% Uninsured 60,389 72,317 14% 60% 40% Sample consists of (18 64 year old) individuals living in Broward and Duval before 2006 Q3, and Baker, Clay or Nassau before 2007 Q3. Table 3 2. Post r eform N, a mong r eform c ounty r esidents Non SN SN Private 351,053 170,151 53% Medicaid 132,167 151,595 29% Uninsured 82,949 92,715 18% 58% 42% Sample consists of (18 64 year old) individuals living in Broward and Duval on/after 2006 Q3, and Baker, Clay or Nassau on/after 2007 Q3.

PAGE 123

123 Table 3 3. Means NON REFORM COUNTIES REFORMED COUNTIES Before Reform After Reform Before Reform After Reform Visits that were to SNs 25% 26% 41% 42% Visits that were covered by private insurance 62% 52% 64% 52% Visits that were covered by Medicaid 26% 33% 22% 30% Visits that were no covered by insurance 12% 15% 14% 18% SN visits that were covered by private insurance 56% 48% 53% 40% SN visits that were covered by Medicaid 32% 38% 28% 38% SN visits that were not covered by insurance 12% 13% 19% 22% Total charges, per patient $20,950.57 $36,140.40 $21,656.63 $35,575.54 Money received, per patient $16,295.86 $25,941.64 $16,671.98 $24,924.23 N: 4,638,637 4,284,788 931,259 840,229 "(Non) reformed county" is defined as residency in a (non) reformed county. "Before Reform" is defined as 2000 Q1 through 2006 Q2, and "After Reform" is defined as 2007 Q3 through 2012 Q4. 2006 Q3 through 2007 Q2 data is excluded so that the pre vs. post reform cut point can be cleanly drawn for the non reformed counties. For SN visits, N=1,174,356 in column 1, N=1,109,130 in column 2, N=379,543 in column 3, and N=350,597 in column 4. For to tal charges, dollar values are as reported (i.e., not adjusted for inflation).

PAGE 124

124 Table 3 4. DDD ( u nadjusted) e stimate for the r e ffect on u ninsured Before Reform ('00 Q1 through '06 Q2) After Reform ('07 Q3 through '12 Q4) Time Difference, by Facility Type AMONG SAFETY NETS Reform Counties 0 1 3 5 0 7 2 4 6 7 0.190 0.222 0.032 (0.001) (0.001) (0.001) n=379,543 n=350,597 Non Reform Counties 0 3 0 2 3 6 2 6 0.117 0.134 0.017 (0.000) (0.000) (0.000) n=1,174,356 n=1,109,130 Facility Type 1 5 1 4 5 7 Difference, by Time 0.073 0.089 (0.001) (0.001) DD 4 7 0.016 (0.001) AMONG NON SAFETY NETS Reform Counties 0 1 0 1 2 4 2 4 0.107 0.149 0.042 (0.000) (0.001) (0.001) n=551,716 n=489,632 Non Reform Counties 0 0 2 2 0.121 0.155 0.035 (0.000) (0.000) (0.000) n=3,464,281 n =3,175,658 Facility Type 1 1 4 Difference, by Time 0.014 0.007 (0.000) (0.001) DD 4 0.007 (0.001) DDD 7 0.009 (0.001) Values in parentheses are standard errors. "(Non) reformed county" is defined as residency in a (non) reformed county. "Before Reform" is defined as 2000 Q1 through 2006 Q2, and "After Reform" is defined as 2007 Q3 through 2012 Q4. 2006 Q3 through 2007 Q2 data is excluded so that the pre vs. post reform cut point can be cleanly drawn for the non reformed counties.

PAGE 125

125 Table 3 5. DDD ( u nadjusted) e stimate for the r e ffect on Medicaid Before Reform ('00 Q1 through '06 Q2) After Reform ('07 Q3 through '12 Q4) Time Difference, by Facility Type AMONG SAFETY NETS Reform Counties 0 1 3 5 0 7 2 4 6 7 0. 282 0. 380 0.0 99 (0.001) (0.001) (0.001) n=379,543 n=350,597 Non Reform Counties 0 3 0 2 3 6 2 6 0. 324 0. 383 0.0 59 (0.000) (0.000) (0.00 1 ) n=1,174,356 n=1,109,130 Facility Type 1 5 1 4 5 7 Difference, by Time 0.0 42 0.0 03 (0.001) (0.001) DD 4 7 0.0 40 (0.001) AMONG NON SAFETY NETS Reform Counties 0 1 0 1 2 4 2 4 0.1 69 0. 239 0.0 70 (0.00 1 ) (0.001) (0.001) n=551,716 n=489,632 Non Reform Counties 0 0 2 2 0. 242 0. 314 0.0 73 (0.000) (0.000) (0.000) n=3,464,281 n =3,175,658 Facility Type 1 1 4 Difference, by Time 0.0 72 0.0 75 (0.000) (0.001) DD 4 0.00 3 (0.001) DDD 7 0.0 43 (0.00 2 ) Values in parentheses are standard errors. "(Non) reformed county" is defined as residency in a (non) reformed county. "Before Reform" is defined as 2000 Q1 through 2006 Q2, and "After Reform" is defined as 2007 Q3 through 2012 Q4. 2006 Q3 through 2007 Q2 data is excluded so that the pre vs. post reform cut point can be cleanly drawn for the no n reformed counties.

PAGE 126

126 Table 3 6. DDD ( u nadjusted) e stimate for the r e ffect on p rivately i nsured Before Reform ('00 Q1 through '06 Q2) After Reform ('07 Q3 through '12 Q4) Time Difference, by Facility Type AMONG SAFETY NETS Reform Counties 0 1 3 5 0 7 2 4 6 7 0. 529 0. 397 0. 131 (0.001) (0.001) (0.001) n=379,543 n=350,597 Non Reform Counties 0 3 0 2 3 6 2 6 0. 560 0. 483 0.0 76 (0.000) (0.000) (0.00 1 ) n=1,174,356 n=1,109,130 Facility Type 1 5 1 4 5 7 Difference, by Time 0.0 31 0.0 86 (0.001) (0.001) DD 4 7 0.0 55 (0.001) AMONG NON SAFETY NETS Reform Counties 0 1 0 1 2 4 2 4 0. 724 0. 612 0. 111 (0.00 1 ) (0.001) (0.001) n=551,716 n=489,632 Non Reform Counties 0 0 2 2 0. 638 0. 530 0. 107 (0.000) (0.000) (0.000) n=3,464,281 n =3,175,658 Facility Type 1 1 4 Difference, by Time 0.0 86 0.0 82 (0.00 1 ) (0.001) DD 4 0.00 4 (0.001) DDD 7 0.0 51 (0.00 2 ) Values in parentheses are standard errors. "(Non) reformed county" is defined as residency in a (non) reformed county. "Before Reform" is defined as 2000 Q1 through 2006 Q2, and "After Reform" is defined as 2007 Q3 through 2012 Q4. 2006 Q3 through 2007 Q2 data is excluded so that the pre vs. post reform cut point can be cleanly drawn for the non reformed counties.

PAGE 127

127 Table 3 7. DDD ( u nadjusted) e stimate for the r e ffect on t otal g ross c harges Before Reform ('00 Q1 through '06 Q2) After Reform ('07 Q3 through '12 Q4) Time Difference, by Facility Type AMONG SAFETY NETS Reform Counties 0 1 3 5 0 7 2 4 6 7 $22,125.16 $35,327.71 $13,202.55 ( 81.70 ) ( 121.84 ) ( 146.70 ) n=379,543 n=350,597 Non Reform Counties 0 3 0 2 3 6 2 6 $22,836.47 $36,720.22 $13,883.76 ( 44.36 ) ( 67.88 ) ( 81.09 ) n=1,174,356 n=1,109,130 Facility Type 1 5 1 4 5 7 Difference, by Time $711.30 $1,392.51 ( 92.96 ) ( 139.47 ) DD 4 7 $681.21 ( 167.62 ) AMONG NON SAFETY NETS Reform Counties 0 1 0 1 2 4 2 4 $21,334.32 $35,752.99 $14,418.68 ( 46.84 ) ( 76.51 ) ( 89.71 ) n=551,716 n=489,632 Non Reform Counties 0 0 2 2 $20,311.28 $35,937.89 $15,626.61 ( 17.84 ) ( 31.64 ) ( 36.62 ) n=3,464,281 n =3,175,658 Facility Type 1 1 4 Difference, by Time $1,023.04 $184.89 ( 50.12 ) ( 82.80 ) DD 4 $1,207.94 ( 96.78 ) DDD 7 $526.72 ( 193.55 ) Values in parentheses are standard errors. "(Non) reformed county" is defined as residency in a (non) reformed county. "Before Reform" is defined as 2000 Q1 through 2006 Q2, and "After Reform" is defined as 2007 Q3 through 2012 Q4. 2006 Q3 through 2007 Q2 data is excluded so that the pre vs. post reform cut point can be cleanly drawn for the non reformed counties.

PAGE 128

128 Table 3 8. DDD ( u nadjusted) e stimate for the r e ffect on m oney r eceived Before Reform ('00 Q1 through '06 Q2) After Reform ('07 Q3 through '12 Q4) Time Difference, by Facility Type AMONG SAFETY NETS Reform Counties 0 1 3 5 0 7 2 4 6 7 $ 15,472.86 $ 21,892.56 $ 6,419.70 ( 65.38 ) ( 88.12 ) ( 109.72 ) n=379,543 n=350,597 Non Reform Counties 0 3 0 2 3 6 2 6 $ 17,200.16 $ 25,948.29 $ 8,748.13 ( 35.68 ) ( 53.12 ) ( 63.99 ) n=1,174,356 n=1,109,130 Facility Type 1 5 1 4 5 7 Difference, by Time $ 1,727.30 $4,055.73 ( 74.48 ) ( 102.89 ) DD 4 7 $ 2,328.43 ( 127.01 ) AMONG NON SAFETY NETS Reform Counties 0 1 0 1 2 4 2 4 $ 17,496.89 $ 27,095.03 $ 9,598.14 ( 40.42 ) ( 63.84 ) ( 75.57 ) n=551,716 n=489,632 Non Reform Counties 0 0 2 2 $ 15,989.32 $ 25,939.32 $ 9,950.00 ( 15.42 ) ( 25.36 ) ( 29.68 ) n=3,464,281 n =3,175,658 Facility Type 1 1 4 Difference, by Time $1, 507.57 $ 1,155.71 ( 43.26 ) ( 68.70 ) DD 4 $ 351.86 ( 81.19 ) DDD 7 $ 1,976.57 ( 150.74 ) Values in parentheses are standard errors. "(Non) reformed county" is defined as residency in a (non) reformed county. "Before Reform" is defined as 2000 Q1 through 2006 Q2, and "After Reform" is defined as 2007 Q3 through 2012 Q4. 2006 Q3 through 2007 Q2 data is excluded so that the pre vs. post reform cut point can be cleanly drawn for the non reformed counties.

PAGE 129

129 Table 3 9. DDD ( u nadjusted) e stimates for the e ffects of the r eform Patient Uninsured Patient Enrolled in Medicaid Patient Privately Insured Total Gross Charges, Per Patient Money Received, Per Patient Reform County (R) 1 = 0.014 *** 0.072 *** 0.086 *** $1023.04 *** $1,507.57 *** (0.000) (0.001) (0.001) (50.12) (43.26) Post Reform (P) 2 = 0.035 *** 0.073 *** 0.107 *** $15,626.61 *** $9,950.01 *** (0.003) (0.000) (0.000) (36.32) (29.68) Safety Net (SN) 3 = 0.004 *** 0.082 *** 0.078 *** $2,525.19 *** $1,210.84 *** (0.000) (0.000) (0.001) (47.81) (38.87) (R*P) 4 = 0.007 *** 0.003 *** 0.004 *** $1,207.94 *** $351.86 *** (0.001) (0.001) (0.001) (96.78) (81.19) (R*SN) 5 = 0.087 *** 0.030 *** 0.117 *** $1,734.35 *** $3,234.87 *** (0.001) (0.001) (0.001) (105.61) (86.13) (P*SN) 6 = 0.018 *** 0.013 *** 0.031 *** $1,742.86 *** $1,201.88 *** (0.001) (0.001) (0.001) (88.85) (70.54) (R*P*SN) 7 = 0.009 *** 0.043 *** 0.051 *** $526.73 *** $1,976.57 *** (0.001) (0.002) (0.002) (193.55) (150.74) Constant 0 = 0.121 *** 0.242 *** 0.638 *** $20,311.28 *** $15,989.32 *** (0.000) (0.000) (0.000) (17.84) (15.42) R Squared 0.005 0.015 0.021 0.022 0.014 Observations 10,694,913 10,694,913 10,694,913 10,694,913 10,694,913 nt with Tables 3 4 through 3 8. Values in parentheses are robust standard errors. Stars indicate s.

PAGE 130

130 Table 3 10. DDD ( a djusted) e stimates for the e ffects of the r eform Patient Uninsured Patient Enrolled in Medicaid Patient P rivately Insured Total Gross Charges, Per Patient Money Received, Per Patient Reform County (R) 1 = 0.014 *** 0.078 *** 0.092 *** $1,640.16 *** $2,114.63 *** (0.000) (0.001) (0.001) (49.02) (41.93) Quarter Dummies (Q') 2 = Yes Yes Yes Yes Yes Satey Net (SN) 3 = 0.025 *** 0.051 *** 0.025 *** $490.54 $213.37 (0.002) (0.002) (0.002) (336.77) (258.22) (R*P) 4 = 0.009 *** 0.004 *** 0.005 *** $1,363.57 *** $560.55 *** (0.001) (0.001) (0.001) (87.97) (73.71) (R*SN) 5 = 0.083 *** 0.030 *** 0.113 *** $2,227.33 *** $3,455.88 *** (0.001) (0.001) (0.001) (103.80) (84.56) (Q'*SN) 6 = Yes Yes Yes Yes Yes (R*P*SN) 7 = 0.009 *** 0.026 *** 0.035 *** $312.58 $1,769.28 *** (0.001) (0.001) (0.002) (177.68) (138.99) Controls: Male 0.117 *** 0.075 *** 0.042 *** $7,656.43 *** $4,197.67 *** (0.000) (0.000) (0.000) (36.81) (29.22) White 0.022 *** 0.034 *** 0.056 *** $2,208.51 *** $17.69 (0.000) (0.001) (0.001) (70.01) (54.30) Black 0.014 *** 0.170 *** 0.156 *** $1,229.87 *** $2,802.19 *** (0.000) (0.001) (0.001) (76.40) (58.30) Hispanic 0.022 *** 0.149 *** 0.171 *** $686.28 *** $2,393.02 *** (0.000) (0.000) (0.000) (41.33) (31.18) Age Dummies Yes Yes Yes Yes Yes Constant 0 = 0.055 *** 0.463 *** 0.482 *** $4,538.07 *** $2,648.79 *** (0.001) (0.001) (0.002) (143.69) (113.33) R Squared 0.036 0.135 0.121 0.061 0.059 Observations 11,620,077 11,620,077 11,620,077 11,620,077 11,620,077 Values in parentheses are robust standard errors. parentheses are robust standard errors. Race categories are White, Black, and Other (referent). Ethnicity categories are Hispanic and Non Hispanic (referent).

PAGE 131

131 APPENDIX ADDITIONAL TABLES AND FIGURES Triage Whisker ends denote the 5 th and 95 th percentiles, outer box edges denote the 25 th and 75 th percentiles, and center lines mark the median. Figure A 1. Wait t ime d istributions, by t riage a ssignment Table A 1 Non instrumented effect of being under insured on triage (I) (II) (III) (IV) (V) Uninsured vs. Privately Insured Uninsured vs. All Insured Uninsured vs. Publicly Insured Non Privately Insured vs. Privately Insured Publicly Insured vs. Privately Insured Under Insured 4.742 *** 4.370 *** 4.062 *** 2.195 *** 0.851 ** (Interval Regression) (0.505) (0.469) (0.553) (0.360) (0.408) Under Insured 0.108 *** 0.101 *** 0.095 *** 0.046 *** 0.012 (Ordered Probit) (0.012) (0.011) (0.013) (0.009) (0.010) Full Set of Controls Y Y Y Y Y Number of Observations 70,732 118,414 70,045 118,414 96,051 Values in parentheses (n=19,464) (n=41,467) (n=20,627) (n=11,029)

PAGE 132

132 Table A 2 (Analogous to Table 1 4, but with restricted sample) (I) (II) (III) (IV) (V) Uninsured vs. Privately Insured Uninsured vs. All Insured Uninsured vs. Publicly Insured Non Privately Insured vs. Privately Insured Publicly Insured vs. Privately Insured M F 8 5 0.032 *** 0.015 *** 0.007 0.029 *** 0.025 *** (0.005) (0.003) (0.005) (0.004) (0.004) Male 0.037 *** 0.043 *** 0.079 *** 0.009 ** 0.045 *** (0.005) (0.003) (0.005) (0.004) (0.004) Black a 0.127 *** 0.044 *** 0.023 *** 0.151 *** 0.156 *** (0.006) (0.004) (0.006) (0.005) (0.005) Other Race a 0.014 0.011 0.011 0.011 0.007 (0.015) (0.010) (0.015) (0.012) (0.013) Hispanic b 0.164 *** 0.081 *** 0.037 *** 0.146 *** 0.125 *** (0.008) (0.006) (0.007) (0.006) (0.007) Unknown Pain 0.019 ** 0.008 0.000 0.019 *** 0.017 *** (0.008) (0.005) (0.007) (0.006) (0.006) No Pain -----Mild Pain 0.017 ** 0.009 0.005 0.010 0.005 (0.008) (0.005) (0.007) (0.007) (0.007) Moderate Pain 0.024 *** 0.010 0.003 0.030 *** 0.029 *** (0.008) (0.005) (0.008) (0.007) (0.007) Severe Pain 0.003 0.003 0.006 0.009 0.013 (0.010) (0.007) (0.010) (0.008) (0.009) Ambulance c 0.070 *** 0.020 *** 0.011 0.075 *** 0.072 *** (0.009) (0.005) (0.006) (0.006) (0.007) No. Diagnostic/Screening 0.020 *** 0.012 *** 0.014 *** 0.010 *** 0.004 Services Provided (0.003) (0.002) (0.002) (0.002) (0.002) No. Diagnostic/Screening 0.001 *** 0.001 *** 0.001 *** 0.001 *** 0.000 Services Provided Squared (0.000) (0.000) (0.000) (0.000) (0.000) Fixed Effects: Age Y Y Y Y Y Year Y Y Y Y Y Reason(s) for Visit Y Y Y Y Y Number of Observations 54,967 92,319 54,248 92,319 75,423 R Squared 0.0871 0.0934 0.2384 0.1217 0.2141 Values in parentheses are robust standard a Referent: White; b Referent: Not Hispanic/unknown ethnicity; c Referent: Not ambulance/unknown mode of arrival

PAGE 133

133 Table A 3 (Analogous to Table 1 7, but with restricted sample) (I) (II) (III) (IV) (V) Uninsured vs. Privately Insured Uninsured vs. All Insured Uninsured vs. Publicly Insured^ Non Privately Insured vs. Privately Insured Publicly Insured vs. Privately Insured Under Insured # 31.948 74.420 ** 38.614 *** 27.627 (16.851 ) (29.836) (14.267) (17.469 ) Male 2.029 ** 4.301 *** 0.782 0.056 (0.806) (1.350) (0.427) (0.906) Black a 0.681 1.484 1.078 0.435 (2.224) (1.426) (2.217) (2.784) Other Race a 0.682 2.670 ** 2.306 2.478 (1.495) (1.361) (1.249) (1.305) Hispanic b 2.425 2.258 1.835 0.225 (2.877) (2.520) (2.169) (2.287) Unknown Pain 5.319 *** 6.570 *** 6.679 *** 6.616 *** (0.875) (0.700) (0.668) (0.707) No Pain ----Mild Pain 3.857 *** 5.067 *** 5.342 *** 5.281 *** (0.927) (0.782) (0.699) (0.723) Moderate Pain 10.727 *** 10.821 *** 10.371 *** 10.365 *** (0.945) (0.781) (0.795) (0.862) Severe Pain 14.265 *** 13.604 *** 13.013 *** 12.355 *** (1.011) (0.883) (0.810) (0. 872) Ambulance c 17.464 *** 15.440 *** 16.809 *** 15.020 *** (1.436) (0.884) (1.215) (1.406) No. Diagnostic/Screening 2.003 *** 2.210 *** 2.737 *** 2.866 *** Services Provided (0.420) (0.426) (0.249) (0.226) No. Diagnostic/Screening 0.011 0.021 0.052 *** 0.066 *** Services Provided Squared (0.030) (0.028) (0.018) (0.017) Fixed Effects: Age Y Y Y Y Year Y Y Y Y Reason(s) for Visit Y Y Y Y Number of Observations 54,967 92,319 92,319 75,423 # The instrument for being under insured is appearing at the ED during office hours a Referent: White; b Referent: Not Hispanic/unknown ethnicity; c Referent: Not ambulance/unknown mode of arrival ^ Results not presented due to the lack of a first stage relationship at the 95% confidence level

PAGE 134

134 Table A 4 (Analogous to Table 1 8, but with restricted sample) (I) (II) (III) (IV) (V) Uninsured vs. Privately Insured Uninsured vs. All Insured Uninsured vs. Publicly Insured^ Non Privately Insured vs. Privately Insured Publicly Insured vs. Privately Insured Under Insured # 0.803 ** 1.653 *** 0.955 *** 0.805 ** (0.356) (0.408) (0.270) (0.380) Male 0.056 *** 0.102 *** 0.026 ** 0.002 (0.017) (0.016) (0.011) (0.023) Black a 0.009 0.025 0.036 0.028 (0.053) (0.033) (0.049) (0.067) Other Race a 0.004 0.053 0.050 0.051 (0.036) (0.028) (0.029) (0.033) Hispanic b 0.064 0.050 0.045 0.001 (0.065) (0.047) (0.048) (0.056) Unknown Pain 0.139 *** 0.150 *** 0.170 *** 0.179 *** (0.019) (0.021) (0.015) (0.017) No Pain ----Mild Pain 0.080 *** 0.100 *** 0.118 *** 0.125 *** (0.023) (0.025) (0.019) (0.021) Moderate Pain 0.241 *** 0.220 *** 0.234 *** 0.248 *** (0.030) (0.039) (0.030) (0.034) Severe Pain 0.374 *** 0.318 *** 0.340 *** 0.343 *** (0.032) (0.046) (0.032) (0.036) Ambulance c 0.486 *** 0.378 *** 0.454 *** 0.438 *** (0.023) (0.041) (0.017) (0.018) No. Diagnostic/Screening 0.044 *** 0.043 *** 0.061 *** 0.069 *** Services Provided (0.012) (0.014) (0.009) (0.008) No. Diagnostic/Screening 0.001 0.000 0.001 0.001 ** Services Provided Squared (0.001) (0.001) (0.000) (0.000) Fixed Effects: Age Y Y Y Y Year Y Y Y Y Reason(s) for Visit Y Y Y Y Number of Observations 54,967 92,319 92,319 75,423 Values in parentheses # The instrument for being under insured is appearing at the ED during office hours a Referent: White; b Referent: Not Hispanic/unknown ethnicity; c Referent: Not ambulance/unknown mode of arrival ^ Results not presented due to the lack of a first stage relationship at the 95% confidence level

PAGE 135

135 Table A 5 Wald e stimates for h ealth o utcomes: College d iploma ( i ndividual t hresholds) Self Reported Health BMI Number of Acute Incidence Conditions Number of Conditions 1st Threshold (i.e., exempt = post October 17, 1919 birthday): 7 month bandwidth NS NS NS NS NS NS NS NS (N=6,199) 6 month bandwidth NS NS NS NS NS NS NS NS (N=5,373) 5 month bandwidth NS NS NS NS NS NS NS NS (N=4,530) 4 month bandwidth NS NS NS NS NS NS NS NS (N=3,785) 3 month bandwidth NS NS NS NS NS NS NS NS (N=3,006) 2 month bandwidth 0.804 1.299 2.113 3.935 *** 0.474 0.268 6.212 2.627 (N=2,120) (0.716) (0.914) (5.400) (0.819) (0.531) (0.150) (5.137) (2.027) 1 month bandwith 1 2.096 ** 2.096 ** 9.472 ** 9.472 ** 0.588 0.588 11.345 ** 11.345 ** (N=1,278) (0.286) (0.286) (2.213) (2.213) (0.145) (0.145) (1.714) (1.714) 2nd Threshold (i.e., exempt = post July 2, 1920 birthday): 7 month bandwidth NS NS NS NS NS NS NS NS (N=6,536) 6 month bandwidth NS NS NS NS NS NS NS NS (N=5,673) 5 month bandwidth NS NS NS NS NS NS NS NS (N=4,779) 4 month bandwidth NS NS NS NS NS NS NS NS (N=3,951) 3 month bandwidth NS NS NS NS NS NS NS NS (N=3,107) 2 month bandwidth 10.424 6.695 30.262 0.562 1.289 2.638 16.163 19.730 (N=2,276) (3.880) (2.729) (16.242) (7.686) (1.331) (0.962) (16.042) (11.706) 1 month bandwith 1 1.947 ** 1.947 ** 19.792 *** 19.792 *** 0.079 0.079 2.329 ** 2.329 ** (N=1,410) (0.225) (0.225) (1.498) (1.498) (0.042) (0.042) (0.521) (0.521) Interaction Term N Y N Y N Y N Y Controls 2 Y Y Y Y Y Y Y Y

PAGE 136

136 Table A 5 Wald e stimates for h ealth o utcomes: College d iploma ( i ndividual t hresholds) (continued) Self Reported Health BMI Number of Acute Incidence Conditions Number of Conditions 3rd Threshold (i.e., exempt = post January 1, 1922 birthday): 7 month bandwidth 0.793 0.820 1.859 2.021 0.058 0.077 1.030 0.882 (N=7,002) (0.770) (0.764) (2.248) (2.497) (0.145) (0.156) (1.538) (1.493) 6 month bandwidth 0.670 0.641 3.220 2.422 0.200 0.244 2.435 2.000 (N=6,046) (0.998) (1.134) (2.875) (4.230) (0.242) (0.247) (1.965) (2.093) 5 month bandwidth 1.119 1.537 3.781 5.460 *** 0.086 0.030 3.362 3.554 (N=5,140) (1.051) (0.829) (3.004) (1.448) (0.138) (0.154) (1.864) (1.684) 4 month bandwidth 0.003 0.363 4.545 5.457 0.158 0.185 1.749 1.814 (N=4,155) (1.271) (1.239) (3.225) (2.871) (0.137) (0.158) (2.092) (2.156) 3 month bandwidth 0.947 2.382 3.267 9.225 *** 0.376 ** 0.572 ** 3.871 4.617 (N=3,236) (1.546) (1.120) (5.733) (0.705) (0.140) (0.172) (2.069) (2.040) 2 month bandwidth 1.077 1.683 5.753 8.264 *** 0.261 0.432 3.335 5.880 ** (N=2,350) (1.415) (0.919) (2.600) (1.299) (0.108) (0.172) (2.437) (1.817) 1 month bandwith 1 5.265 5.265 3.994 3.994 0.476 ** 0.476 ** 10.986 10.986 (N=1,460) (1.246) (1.246) (2.769) (2.769) (0.087) (0.087) (3.824) (3.824) Interaction Term N Y N Y N Y N Y Controls 2 Y Y Y Y Y Y Y Y statistically significant first stage at the confidence level. Values in parentheses are robust standard errors clustered by MOB. The stacked model is clustered by the stacked MOB running variable. The reported N's are for the full sample (i.e., health measures with no missing values); howeve smaller. 1 The regressions using a 1 month bandwidth do not include interaction between 'exempt' and MOB due to collinearity. 2 The controls include marital status, race, ethnicity, MSA, geographic region, veteran status, and survey year.

PAGE 137

137 Table A 6 Wald e stimates for h ealthcare u sage: College d iploma ( i ndividual t hresholds) Bed Days in Past 12 Months Doctor Visits i n Past 12 Months Short Stay Hospital Episode Days in Past 12 Months Number of Short Stay Hospital Episodes in Past 12 Months 1st Threshold (i.e., exempt = post October 17, 1919 birthday): 7 month bandwidth NS NS NS NS NS NS NS NS (N=6,199) 6 month bandwidth NS NS NS NS NS NS NS NS (N=5,373) 5 month bandwidth NS NS NS NS NS NS NS NS (N=4,530) 4 month bandwidth NS NS NS NS NS NS NS NS (N=3,785) 3 month bandwidth NS NS NS NS NS NS NS NS (N=3,006) 2 month bandwidth NS NS 1.989 4.377 0.840 2.322 0.115 0.438 (N=2,120) (11.052) (11.438) (4.872) (4.587) (0.508) (0.524) 1 month bandwith1 58.419 ** 58.419 ** 33.846 ** 33.846 ** 13.490 *** 13.490 *** 1.167 *** 1.167 *** (N=1,278) (6.211) (6.211) (3.765) (3.765) (1.145) (1.145) (0.108) (0.108) 2nd Threshold (i.e., exempt = post July 2, 1920 birthday): 7 month bandwidth NS NS NS NS NS NS NS NS (N=6,536) 6 month bandwidth NS NS NS NS NS NS NS NS (N=5,673) 5 month bandwidth NS NS NS NS NS NS NS NS (N=4,779) 4 month bandwidth NS NS NS NS NS NS NS NS (N=3,951) 3 month bandwidth NS NS NS NS NS NS NS NS (N=3,107) 2 month bandwidth 9.134 54.733 219.897 7.725 12.039 80.162 5.113 6.531 ** (N=2,276) (167.456) (114.511) (140.373) (74.550) (59.227) (33.794) (2.491) (2.037) 1 month bandwith 1 114.862 ** 114.862 ** 3.961 3.961 42.117 ** 42.117 ** 3.626 ** 3.626 ** (N=1,410) (14.098) (14.098) (1.111) (1.111) (4.815) (4.815) (0.413) (0.413) Interaction Term N Y N Y N Y N Y Controls 2 Y Y Y Y Y Y Y Y

PAGE 138

138 Table A 6 Wald e stimates for h ealthcare u sage: College d iploma ( i ndividual t hresholds) (continued) Bed Days in Past 12 Months Doctor Visits in Past 12 Months Short Stay Hospital Episode Days in Past 12 Months Number of Short Stay Hospital Episodes in Past 12 Months 3rd Threshold (i.e., exempt = post January 1, 1922 birthday): 7 month bandwidth 31.075 39.423 11.501 7.444 0.591 0.273 0.473 0.437 (N=7,002) (47.258) (50.158) (10.505) (7.422) (9.348) (8.796) (0.355) (0.356) 6 month bandwidth 37.740 50.312 17.087 12.881 5.802 4.423 0.692 0.680 (N=6,046) (61.310) (64.857) (12.186) (8.670) (10.601) (9.978) (0.447) (0.544) 5 month bandwidth 40.075 40.905 13.064 10.661 1.153 2.104 0.185 0.031 (N=5,140) (54.754) (57.504) (11.230) (9.023) (10.395) (9.465) (0.541) (0.347) 4 month bandwidth 3.163 0.247 16.440 10.358 2.762 0.867 0.497 0.005 (N=4,155) (51.778) (59.834) (14.624) (9.972) (12.105) (10.758) (0.627) (0.283) 3 month bandwidth 50.509 71.466 30.920 17.791 2.632 9.938 0.658 0.094 (N=3,236) (93.133) (109.628) (19.836) (10.482) (19.917) (18.015) (0.677) (0.292) 2 month bandwidth 118.151 ** 206.944 *** 41.851 5.144 ** 26.397 *** 29.647 *** 1.425 0.294 (N=2,350) (39.268) (33.888) (20.756) (1.795) (4.797) (4.266) (0.704) (0.368) 1 month bandwith 1 NS NS 43.565 43.565 42.406 42.406 0.659 0.659 (N=1,460) (12.885) (12.885) (11.840) (11.840) (0.358) (0.358) Interaction Term N Y N Y N Y N Y Controls 2 Y Y Y Y Y Y Y Y statistically significant first stage at the level. Values in parentheses are robust standard errors clustered by MOB. The stacked model is clustered by the stacked MOB running variable. The reported N's are for the full sample (i.e., health measures with no missing values); howeve 1 The regressions using a 1 month bandwidth do not include interaction between 'exempt' and MOB due to collinearity. 2 The controls include marital status, race, ethnicity, MSA, g eographic region, veteran status, and survey year.

PAGE 139

139 LIST OF REFERENCES 42 U.S.C. § 1395dd (1986). Adams, S. J. (2002). Educational Attainment and Health: Evidence from a Sample of Older Adults. Education Economics, 10 (1). AHCA. (2014). Florida Medicaid Reform Pilot. from http://ahca.myflorida.com/medicaid/medicaid_reform/index.shtml Albouy, V., & Lequien, L. (2009). Does compulsory education lower mortality? Journal of Health Economics, 28 (1), 155 168. doi: http://dx.doi.org/10.1016/j.jhealeco.2008.09.003 Angrist, J., & Krueger, A. B. (1994). Why Do World War II Veterans Earn More than Nonveterans? Journal of Labor Economics, 12 (1), 74 97. doi: 10.2307/2535121 Angrist, J. D. (1990). Lifetime Earnings and the Vietnam Era Draft Lottery: Evidence from Social Security Administrative Reco rds. The American Economic Review, 80 (3), 313 336. doi: 10.2307/2006669 Angrist, J. D. (1991). The Draft Lottery and Voluntary Enlistment in the Vietnam Era. Journal of the American Statistical Association, 86 (415), 584 595. doi: 10.1080/01621459.1991.1047 5083 Angrist, J. D., & Chen, S. H. (2011). Schooling and the Vietnam Era GI Bill: Evidence from the Draft Lottery. American Economic Journal: Applied Economics, 3 (2), 96 118. doi: doi: 10.1257/app.3.2.96 Angrist, J. D., Chen, S. H., & Frandsen, B. R. (2010 ). Did Vietnam veterans get sicker in the 1990s? The complicated effects of military service on self reported health. Journal of Public Economics, 94 (11 12), 824 837. doi: http://dx.doi.org/10 .1016/j.jpubeco.2010.06.001 Arendt, J. N. (2005). Does education cause better health? A panel data analysis using school reforms for identification. Economics of Education Review, 24 (2), 149 160. doi: http://dx.doi.org/10.1016/j.econedurev.2004.04.008 Arendt, J. N. (2008). In sickness and in health Till education do us part: Education effects on hospitalization. Economics of Education Review, 27 (2), 161 172. doi: http://dx.doi.org/10.1016/j.econedurev.2006.08.006 Arkes, J. (2003). Does Schooling Improve Adult Health RAND Working Paper DRU 3051 Auld, C. M., & Sidhu, N. (2005). Schooling, cognitive ability and health. Heal th Economics, 14 (10), 1019 1034. doi: 10.1002/hec.1050

PAGE 140

140 Bauer, T. K., Bender, S., Paloyo, A. R., & Schmidt, C. M. (2012). Evaluating the labor market effects of compulsory military service. European Economic Review, 56 (4), 814 829. doi: http://dx.doi.org/10.1016/j.euroecorev.2012.02.002 Bindman, A. B., Grumbach, K., Keane, D., Rauch, L., & Luce, J. M. (1991). Consequences of queuing for care at a public hospital emergency department. JAMA, 2 66 (8), 1091 1096. The Washington Post: Wonkblog http://www.washingtonpost.com/blogs/wonkblog/wp/2013/06/26/this georgia hospital shows why rejecting medicaid isnt easy/ Bound, J., Jaeger, D. A., & Baker, R. M. (1995). Problems with Instrumental Variables Estimation When the Correlation Betwe en the Instruments and the Endogenous Explanatory Variable is Weak. Journal of the American Statistical Association, 90 (430), 443 450. Bound, J., & Turner, S. (2002). Going to War and Going to College: Did World War II and the G.I. Bill Increase Educational Attainment for Returning Veterans? Journal of Labor Economics, 20 (4), 784 815. prove Health, Increase Satisfaction, and Control Costs. http://www.heritage.org/research/repor ts/2011/11/floridas medicaid reform shows the way to improve health increase satisfaction and control costs Brillman, J. C., Doezema, D., Tandberg, D., Sklar, D. P., Davis, K. D., Simms, S., & Skipper, B. J. (1996). Triage: Limitations in Predicting Need for Emergent Care and Hospital Admission. Annals of Emergency Medicine, 27 (4), 493 500. doi: 10.1016/s0196 0644(96)70240 8 Buckles, K., & Hungerman, D. M. (2008). Season of Birth and Later Outcomes: Old Questions, New Answers NBER working paper series work ing paper 14573 Clark, D., & Royer, H. (2013). The Effect of Education on Adult Health and Mortality: Evidence from Britain. American Economic Review, 103 (6), 2087 2120. doi: http://dx.doi.org/10.125 7/aer.103.6.2087 Cutler, D. M., & Lleras Muney, A. (2006). Education and Health: Evaluating Theories and Evidence NBER working paper series working paper 12352 de Walque, D. (2007). Does education affect smoking behaviors?: Evidence using the Vietnam draft as an instrument for college education. Journal of Health Economics, 26 (5), 877 895. doi: http ://dx.doi.org/10.1016/j.jhealeco.2006.12.005

PAGE 141

141 Derlet, R. W., & Richards, J. R. (2000). Overcrowding in the nation's emergency departments: complex causes and disturbing effects. Ann Emerg Med, 35 (1), 63 68. doi: S0196064400097729 [pii], 42 U.S.C. § 1395dd (1986). Emergency Department: Patient Perspectives on American Health Care. (2010) Pulse Report : Press Ganey. Final Bill Analysis. (2011): Florida State Government. Flores, C. A., & Flores Lagunes, A. Identification and Estimation of Causal Mechanisms and Net Effects of a Treatment Under Unconfoundedness. SSRN eLibrary Florida Medicaid Reform Pilot. Retrieved March 17, 2014, from http://ahca.myflorida.com/Medicaid/medicaid_ref orm/index.shtml University of Florida News website: http://news.ufl.edu/2014/01/29/medicaid refor m pilot/ Fonseca, R., & Zheng, Y. (2011). The Effect of Education on Health: Cross Country Evidence RAND Working Paper WR 864 Retrieved from http://www.rand.org/pubs/working_papers/WR864 The GI Bill's History. (2012). 2013, from http://www.gibill.va.gov/benefits/history_timeline/ Gruber, J. (1994). The Incidence of Mandated Maternity Benefits. The American Economic Review 84 (3), 622 641. doi: 10.2307/2118071 The Home Front Encyclopedia: United States, Britain, and Canada in World Wars I and II. (2006). In J. D. Ciment & T. Russell (Eds.), (1 ed., Vol. I, pp. 1352 1353). Hoot, N. R., & Aronsky, D. (2008). Systematic review of emergency department crowding: causes, effects, and solutions. Annals of emergency medicine 52(2), 126 136. Hospital Emergency Departments: Crowding Continues to Occur, and Some Patients Wait Longer than Recommended Time Frames. (2009) Report to the C hairman, Committee on Finance, U.S. Senate : United States Government Accountability Office. Howard, M. S., Davis, B. A., Anderson, C., Cherry, D., Koller, P., & Shelton, D. (2005). Patients' perspective on choosing the emergency department for nonurgent me dical care: a qualitative study exploring one reason for overcrowding. J Emerg Nurs, 31 (5), 429 435. doi: S0099 1767(05)00328 4 [pii], 10.1016/j.jen.2005.06.023 Imbens, G. (2012). Software: Regression Discontinuity. 2013, from http://faculty gsb.stanford.edu/imbens/RegressionDiscontinuity.html

PAGE 142

142 Imbens, G. W., & Lemieux, T. (2008). Regression discontinuity designs: A guide to practice. Journal of Econometrics, 142 (2), 615 635 doi: http://dx.doi.org/10.1016/j.jeconom.2007.05.001 Induction Statistics. (2007, May 28, 2003). History & Records. 2013, from http://www.sss.gov/induct.htm Institute of Medicine (U.S.). Committee on Quality of Health Care in America. (2001). Crossing the Quality Chasm: A New Health System for the 21st Century : The National Academies Press. Institute of Medicine (U.S.). Committee on the Consequences of Uninsurance. (2002). Care without coverage: too little, too late Washington, D.C.: National Academy Press. James, C. A., Bourgeois, F. T., & Shannon, M. W. (2005). Association of race/ethnicity with emergency department wait times. Pediatrics, 115 (3), e310 315. doi: 115/3/e310 [pii], 10.1542/peds.2004 1541 Kellermann, A. L. (2006). Crisis in the Emergency Department. New England Journal of Medicine, 355 (13), 1300 1303. doi: 10.1056/NEJMp068194 Kennedy, J., Rhodes, K., Walls, C. A., & Asplin, B. R. (2004). Access to emergency care: restricted by long waiting times and cost and coverage concerns. Ann Emerg Med, 43 (5), 567 573. doi: 10.1016/S0196064403010758, S0196064403010758 [pii] Leddy, K. M., Kaldenberg, D. O., & Becker, B. W. (2003 ). Timeliness in ambulatory care treatment. An examination of patient satisfaction and wait times in medical practices and outpatient test and treatment facilities. J Ambul Care Manage, 26 (2), 138 149. Lee, D. S., & Card, D. (2008). Regression discontinuit y inference with specification error. Journal of Econometrics, 142 (2), 655 674. doi: DOI 10.1016/j.jeconom.2007.05.003 Lleras Muney, A. (2005). The relationship between education and adult mortality in the United States. Review of Economic Studies, 72 (1), 189 221. doi: Doi 10.1111/0034 6527.00329 Martorell, P., & Clark, D. (2010). The signaling value of a high school diploma : Industrial Relations Section, Princeton University. Mazumder, B. (2008). Does Education Improve Health? A Reexamination of the Eviden ce from Compulsory Schooling Laws. Economic Perspectives, 32 (2). Medicaid Reform: Two Thirds of the Initial Pilot Counties' Beneficiaries are Enrolled in Reform Plans. (2008): Office of Program Policy Analysis & Government Accountability, office of the Fl orida Legislature. Medicaid: States' Use of Managed Care. (2012): U.S. Government Accountability Office.

PAGE 143

143 Medicaid to Medicare Fee Index. State Health Facts. Retrieved March 19, 2014, from http://kff.org/medicaid/state indicator/medicaid to medicare fee index/ Medicare Payment Policy. (2009) Report to the Congress : Medicare Payment Advisory Commission. Mitchell, T. A., & Remmel, R. J. (1992). Level of uncompensated care delivered by emergency physicians in Florida. Annals of Emergency Medicine, 21 (10), 1208 1214. doi: 10.1016/s0196 0644(05)81748 2 National News Briefs; Hospitals Cannot Delay Care for Insurance O.K. (1998). The New York Times Retrieved from http://www.nytimes.com/1998/11/30/us/national news briefs hospitals cannot delay care for insurance ok.html The National WWII Museum: Timeline. 2013, from http://www.nationalww2museum.org/history/final/interactive_timeline.html O'Shea, J. S. (2007). The Crisis in Hospital E mergency Departments: Overcoming the Burden of Federal Regulation Backgrounder Washington D.C.: Center for Health Policy Studies. Perri, T. J. (1984). Health status and schooling decisions of young men. Economics of Education Review, 3 (3), 207 213. doi: http://dx.doi.org/10.1016/0272 7757(84)90033 5 Provider Service Network (PSN). Retrieved March 17, 2014, from http://ahca.my florida.com/Medicaid/psn/index.shtml Quinn, L. (2002). An Institutional History of the GED Unpublished Manuscript University of Wisconsin Milwaukee Employment and Training Institute Resneck, J., Jr., Pletcher, M. J., & Lozano, N. (2004). Medicare, Medic aid, and access to dermatologists: the effect of patient insurance on appointment access and wait times. J Am Acad Dermatol, 50 (1), 85 92. doi: 10.1016/S0190, S0190962203024630 [pii] Rice, S. (2011). Don't die waiting in the ER, from http://www.cnn.com/2011/HEALTH/01/13/emergency.room.ep/index.html Roll, K., Stargardt, T., & Schreyogg, J. (2012). Effect of Type of Insurance and Income on Waiting Time for Outpatient Care. Gene va Papers on Risk and Insurance Issues and Practice, 37 (4), 609 632. doi: Doi 10.1057/Gpp.2012.6 Rottman, G. L., & Wright, D. (2008). Hell in the Pacific : the battle for Iwo Jima Oxford ; New York: Osprey. Ruger, J. P., Richter, C. J., & Lewis, L. M. (20 03). Association between Insurance Status and Admission Rate for Patients Evaluated in the Emergency Department. Academic Emergency Medicine, 10 (11), 1285 1288. doi: 10.1197/s1069 6563(03)00500 1

PAGE 144

144 Silles, M. A. (2009). The causal effect of education on heal th: Evidence from the United Kingdom. Economics of Education Review, 28 (1), 122 128. doi: http://dx.doi.org/10.1016/j.econedurev.2008.02.003 Spasojevic, J. (2010). Chapter 9 Effects of Edu cation on Adult Health in Sweden: Results from a Natural Experiment Vol. 290. D. Slottje & R. Tchernis (Eds.), Contributions to Economic Analysis (pp. pp. 179 199). Retrieved from http://www.emeraldinsight.com/books.htm?chapterid=1906732&show=abstract admissions through the emergency department: does insurance status matter? The American Journal of Medicine, 105 (6), 506 512. doi: 10.1016/s0002 9343(98)00324 6 Stanley, M. (2003). College Education and the Midcentury GI Bills. The Quarterly Journal of Economics, 118 (2), 671 708. doi: 10.1162/003355303321675482 Trends Affecting H ospitals and Health Systems. (2012). Chapter 3: Utilization and Volume Retrieved from http://www.aha.org/research/reports/tw/chartbook/2012/table3 3.pdf United States General Accounting Office. Report to Congressional Committees. (June 2001). Emergency Care: EMTALA Implementation and Enforcement Issues Washington, D.C. The Value of Health Insurance: Few of the Uninsured Have Adequate Resources to Pay Pote ntial Hospital Bills (2011) ASPE Research Brief : U.S. Department of Health and Human Services. Van Der Klaauw, W. (2002). Estimating the Effect of Financial Aid Offers on College Enrollment: A Regression Discontinuity Approach*. International Economic Revi ew, 43 (4), 1249 1287. doi: 10.1111/1468 2354.t01 1 00055 Run Returns to Education: Does Schooling Lead to an Extended Old Age? Journal of Human Resources, 46 (4), 695 721. Where the state s stand on Medicaid expansion. (2014). Retrieved March 17, 2014, from http://www.advisory.com/daily briefing/resources/primers/medicaidmap White, F. A., French, D., Zwe mer Jr, F. L., & Fairbanks, R. J. (2007). Care without coverage: Is there a relationship between insurance and ED care? The Journal of Emergency Medicine, 32 (2), 159 165. doi: 10.1016/j.jemermed.2006.05.043 Wilper, A. P., Woolhandler, S., Lasser, K. E., Mc Cormick, D., Cutrona, S. L., Bor, D. H., & Himmelstein, D. U. (2008). Waits to see an emergency department physician: U.S. trends and predictors, 1997 2004. Health Aff (Millwood), 27 (2), w84 95. doi: hlthaff.27.2.w84 [pii], 10.1377/hlthaff.27.2.w84

PAGE 145

145 BIOGRAPHICAL SKETCH Lindsey Woodworth, a Kansas native, received her undergraduate degree in economics from Wichita State University in 2009, along with minors in mathematics, finance, and e University of Florida in 2011, and her doctorate in economics from the University of Florida in 2014.


xml version 1.0 encoding UTF-8
REPORT xmlns http:www.fcla.edudlsmddaitss xmlns:xsi http:www.w3.org2001XMLSchema-instance xsi:schemaLocation http:www.fcla.edudlsmddaitssdaitssReport.xsd
INGEST IEID EZGHQBGA2_Z14NA2 INGEST_TIME 2014-10-03T22:03:56Z PACKAGE UFE0046684_00001
AGREEMENT_INFO ACCOUNT UF PROJECT UFDC
FILES