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Essays on the Effects of Family and Schooling on Student Outcomes

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ESSAYS ON THE EFFECTS OF FAMILY AND SCHOOLING ON STUDENT OUTCOMES By MARK HOEKSTRA A DISSERTATION PRESENTED TO THE GRADUATE SCHOOL OF THE UNIVERSITY OF FLOR IDA IN PARTIAL FULFILLMENT OF THE REQUIREMENTS FOR THE DEGREE OF DOCTOR OF PHILOSOPHY UNIVERSITY OF FLORIDA 2006

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Copyright 2006 by Mark Hoekstra

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iii ACKNOWLEDGMENTS This work has benefited tremendously from the instruction and encouragement of David Figlio. I would also like to thank Larry Kenny, Rich Romano, Mark Rush, Damon Clark, Francisco Martorell, Steve Slutsky and countless others who provided helpful advice and comments throughout all of th e stages of this research. I would like to thank the School Board of Alachua County for providing school data and the people at the Office of the Cler k of the Circuit Court at the Alachua County Courthouse for help in acquiring the divorce data used in this analysis. I would also like to thank an anonymous state university for sh aring admissions data and a state office for sharing earnings data.

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iv TABLE OF CONTENTS page ACKNOWLEDGMENTS.................................................................................................iii LIST OF TABLES.............................................................................................................vi LIST OF FIGURES.........................................................................................................viii ABSTRACT.....................................................................................................................xi ii CHAPTER 1 “JUST KIDDING, DEAR”: USIN G DISMISSED DIVORCE CASES TO IDENTIFY THE EFFECT OF PARENTAL DIVORCE ON STUDENT PERFORMANCE.........................................................................................................1 1.1 Introduction........................................................................................................1 1.2 Theoretical Considerations, Literature Review, and Identification Strategy.....6 1.2.1 How Divorce Affects Student Achievement..........................................6 1.2.2 A Review of the Literature....................................................................7 1.2.3 Identification Strategy..........................................................................10 1.3 Parental Divorce and Student Test Scores.......................................................13 1.3.1 School Data..........................................................................................13 1.3.2 Divorce Data........................................................................................14 1.3.3 Divorces in Alachua County, Florida..................................................15 1.3.4 Merging the Divorce Data with the School Data.................................16 1.3.5 The Final Data Set Used in the Analysis.............................................20 1.4 The Effects of Divorce on Student Performance.............................................23 1.4.1 Comparing the Test Scores of Children of Divorce to Those of Children in Intact Families...............................................................................23 1.4.2 Do We Observe the Same Correla tion when Comparing Children of Dismissed Divorce to Childre n of Intact Families?.........................................27 1.4.3 How Similar are Families That Experience Divorce to Those That Experienced a Dismissed Divorce?.................................................................29 1.4.4 The Effect of Parental Divorce on Family Income..............................29 1.4.5 The Pre-Divorce Trends of Child ren Whose Parents Later File for Divorce.............................................................................................................31 1.4.6 The Causal Time-Invariant E ffect of Parental Divorce.......................32 1.4.7 The Causal Effects of Pa rental Divorce Over Time............................33 1.4.8 Are the Effects of Parental Divor ce Different for Boys than for Girls? ..............................................................................................................35

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v 1.4.9 Does the Effect of Parental Divorce Depend on the Age of the Student at the Time of Divorce?......................................................................37 1.5 Robustness of Results......................................................................................37 1.6 Conclusions......................................................................................................40 2 THE EFFECT OF ATTENDING THE FLAGSHIP STATE UNIVERSITY ON EARNINGS: A REGRESSION DI SCONTINUITY APPROACH...........................60 2.1 Introduction......................................................................................................60 2.2 Data..................................................................................................................64 2.3 Identification Strategy......................................................................................65 2.4 The Admission Rule........................................................................................67 2.4.1 Estimating the Admission Rule...........................................................67 2.4.2 Does the Admission Cutoff Predict Which Students Are Accepted and Which Are Rejected?................................................................................69 2.4.3 Potential Causes of the ‘Fuzziness’ of the Estimated Admission Discontinuity....................................................................................................70 2.4.4 Do Applicants Who Just Meet the Admission Cutoff Subsequently Attend and Graduate from the Flagship State University?..............................72 2.4.5 Do Admitted Applicants above the Admission Cutoff Enroll and Graduate from the Flagship at Different Rates than Applicants Just Below the Cutoff?.......................................................................................................73 2.5 Attrition from the Earnings Data.....................................................................74 2.5.1 The Attrition of White Males...............................................................75 2.5.2 The Attrition of White Females...........................................................76 2.5.3 The Admission Discontinuity for Those Observed with Positive Earnings...........................................................................................................76 2.6 The Effect of Admission at the Fl agship University on Labor Market Outcomes...............................................................................................................77 2.6.1 The Earnings of White Males..............................................................77 2.6.2 White Females.....................................................................................80 2.6.2.1 The effect of admission on subsequent earnings.....................80 2.6.2.2 The effect of admission on the labor market attachment of white women...........................................................................................81 2.7 The Sensitivity of the Earnings Estimates.......................................................82 2.7.1 White Men...........................................................................................82 2.7.2 White Women......................................................................................83 2.8 Conclusion.......................................................................................................84 LIST OF REFERENCES.................................................................................................130 BIOGRAPHICAL SKETCH...........................................................................................133

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vi LIST OF TABLES Table page 1-1 Matchable Divorces in Alachua County, Florida.....................................................43 1-2 Families Matched to Unique Divorces.....................................................................43 1-3 Families Matched to Unique Divorces.....................................................................44 1-4 Distribution of Observations of Stude nts Matched to a Parental Divorce Case......44 1-5 The Cross-Sectional Effects of Pare ntal Divorce on Reading Test Scores..............45 1-6 The Cross-Sectional Effects of Parent al Divorce on Mathematics Test Scores.......45 1-7 The Cross-Sectional Effects of Parent al Divorce on Days Suspended Per Year.....46 1-8 The Cross-Sectional Effects of Parent al Divorce on Disciplinary Infractions Per Year..........................................................................................................................4 6 1-9 The Cross-Sectional “Effects” of Di smissed Divorce on Reading Test Scores.......47 1-10 The Cross-Sectional “Effects” of Dismissed Divorce on Mathematics Test Scores.......................................................................................................................48 1-11 The Cross-Sectional “Effects” of Di smissed Divorce on Days Suspended Per Year..........................................................................................................................4 9 1-12 The Cross-Sectional “Effects” of Dism issed Divorce on Disciplinary Infractions Per Year....................................................................................................................49 1-13 Descriptive Statistics................................................................................................50 1-14 Estimated Effects of Parental Divorc e on Student Family Income Using Student Fixed Effects............................................................................................................51 1-15 Estimated Pre-Divorce Trends.................................................................................52 1-16 Estimated Time-Invariant Effects of Parental Divorce on Student Test Scores and Behavior............................................................................................................52 1-17 Estimated Effects of Parental Divorc e on Student Test Scores and Behavior.........53

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vii 1-18 Estimated Effects of Parental Divorc e on Student Test Scores and Behavior.........54 1-19 Estimated Effects of Parental Divorc e on Student Test Scores and Behavior.........55 1-20 Estimated Effects of Parental Di vorce on Student Reading Test Scores.................56 1-21 Estimated Effects of Parental Divo rce on Student Mathematics Test Scores..........57 1-22 Estimated Effects of Parental Divorce on Days Suspended per Year......................58 1-23 Estimated Effects of Parental Divorc e on Disciplinary Infractions per Year..........59 2-1 Regression Discontinuity Estimat es for the Admission Rate of White Applicants.................................................................................................................88 2-2 Regression Discontinuity Estimates fo r the Likelihood of Being Observed with Earnings 7 – 15 Years after High School Graduation (a summary of estimates presented in Figures 2-4a-f, 2-5a-f, 2-6a-f, and 2-7a-f).........................................108 2-3 Summary of Regression Discontinuity Estimates for the Earnings of White Men Presented in Figures 10a – 10f and Figures 11a – 11f...........................................119 2-4 Summary of Regression Discontinuity Estimates for the Earnings of White Women Presented in Figures 12a – 12f and Figures 13a – 13f..............................126 2-5 Regression Discontinuity Estimat es after 12 and 15 Years for Various Specifications and Subsamples..............................................................................128 2-6 Regression Discontinuity Estimat es after 12 and 15 Years for Various Specifications and Subsamples for White Women................................................129

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viii LIST OF FIGURES Figure page 2-1 Fraction Admitted to the Flagship State University.................................................87 2-2 Enrollment Rates for Ad mitted White Applicants...................................................89 2-3 Graduation Rates for Enrolling White Applicants...................................................89 2-4a The Likelihood of Being Observed w ith 4 Consecutive Quarters of Positive Earnings 7 Years after High Sc hool Graduation for White Men.............................90 2-4b The Likelihood of Being Observed with 4 Consecutive Quarters of Positive Earnings 8 Years after High Sc hool Graduation for White Men.............................90 2-4c The Likelihood of Being Observed w ith 4 Consecutive Quarters of Positive Earnings 9 Years after High Sc hool Graduation for White Men.............................91 2-4d The Likelihood of Being Observed with 4 Consecutive Quarters of Positive Earnings 10 Years after High Sc hool Graduation for White Men...........................91 2-4e The Likelihood of Being Observed w ith 4 Consecutive Quarters of Positive Earnings 11 Years after High Sc hool Graduation for White Men...........................92 2-4f The Likelihood of Being Observed w ith 4 Consecutive Quarters of Positive Earnings 12 Years after High Sc hool Graduation for White Men...........................92 2-4g The Likelihood of Being Observed with 4 Consecutive Quarters of Positive Earnings 13 Years after High Sc hool Graduation for White Men...........................93 2-4h The Likelihood of Being Observed with 4 Consecutive Quarters of Positive Earnings 14 Years after High Sc hool Graduation for White Men...........................93 2-4i The Likelihood of Being Observed w ith 4 Consecutive Quarters of Positive Earnings 15 Years after High Sc hool Graduation for White Men...........................94 2-5a The Likelihood of Being Observed with Positive Earnings in the 7th Year after High School Graduation for White Men..................................................................94 2-5b The Likelihood of Being Observed with Positive Earnings in the 8th Year after High School Graduation for White Men..................................................................95

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ix 2-5c The Likelihood of Being Observed with Positive Earnings in the 9th Year after High School Graduation for White Men..................................................................95 2-5d The Likelihood of Being Observed with Positive Earnings in the 10th Year after High School Graduation for White Men..................................................................96 2-5e The Likelihood of Being Observed with Positive Earnings in the 11th Year after High School Graduation for White Men..................................................................96 2-5f The Likelihood of Being Observed with Positive Earnings in the 12th Year after High School Graduation for White Men..................................................................97 2-5g The Likelihood of Being Observed with Positive Earnings in the 13th Year after High School Graduation for White Men..................................................................97 2-5h The Likelihood of Being Observed with Positive Earnings in the 14th Year after High School Graduation for White Men..................................................................98 2-5i The Likelihood of Being Observed with Positive Earnings in the 15th Year after High School Graduation for White Men..................................................................98 2-6a The Likelihood of Being Observed w ith 4 Consecutive Quarters of Positive Earnings 7 Years after High School Graduation for White Women........................99 2-6b The Likelihood of Being Observed with 4 Consecutive Quarters of Positive Earnings 8 Years after High School Graduation for White Women........................99 2-6c The Likelihood of Being Observed w ith 4 Consecutive Quarters of Positive Earnings 9 Years after High School Graduation for White Women......................100 2-6d The Likelihood of Being Observed with 4 Consecutive Quarters of Positive Earnings 10 Years after High School Graduation for White Women....................100 2-6e The Likelihood of Being Observed w ith 4 Consecutive Quarters of Positive Earnings 11 Years after High School Graduation for White Women....................101 2-6f The Likelihood of Being Observed w ith 4 Consecutive Quarters of Positive Earnings 12 Years after High School Graduation for White Women....................101 2-6g The Likelihood of Being Observed with 4 Consecutive Quarters of Positive Earnings 13 Years after High School Graduation for White Women....................102 2-6h The Likelihood of Being Observed with 4 Consecutive Quarters of Positive Earnings 14 Years after High School Graduation for White Women....................102 2-6i The Likelihood of Being Observed w ith 4 Consecutive Quarters of Positive Earnings 15 Years after High School Graduation for White Women....................103

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x 2-7a The Likelihood of Being Observed with Positive Earnings in the 7th Year after High School Graduation for White Women...........................................................103 2-7b The Likelihood of Being Observed with Positive Earnings in the 8th Year after High School Graduation for White Women...........................................................104 2-7c The Likelihood of Being Observed with Positive Earnings in the 9th Year after High School Graduation for White Women...........................................................104 2-7d The Likelihood of Being Observed with Positive Earnings in the 10th Year after High School Graduation for White Women...........................................................105 2-7e The Likelihood of Being Observed with Positive Earnings in the 11th Year after High School Graduation for White Women...........................................................105 2-7f The Likelihood of Being Observed with Positive Earnings in the 12th Year after High School Graduation for White Women...........................................................106 2-7g The Likelihood of Being Observed with Positive Earnings in the 13th Year after High School Graduation for White Women...........................................................106 2-7h The Likelihood of Being Observed with Positive Earnings in the 14th Year after High School Graduation for White Women...........................................................107 2-7i The Likelihood of Being Observed with Positive Earnings in the 15th Year after High School Graduation for White Women...........................................................107 2-8a Regression Discontinuity Estimates fo r the Admission Rate of White Applicants Observed with 4 Consecutive Qu arters of Earnings in the 12th Year after High School Graduation..................................................................................................109 2-8b Regression Discontinuity Estimates for the Admission Rate of White Applicants Observed with 4 Consecutive Qu arters of Earnings in the 15th Year after High School Graduation..................................................................................................110 2-9a Regression Discontinuity Estimates fo r the Admission Rate of White Applicants Observed with Positive Earnings in the 12th Year after High School Graduation.111 2-9b Regression Discontinuity Estimates for the Admission Rate of White Applicants Observed with Positive Earnings in the 15th Year after High School Graduation.112 2-10a The Natural Log of 4 Consecutive Qu arters of Earnings for White Males 10 Years after High School Graduation......................................................................113 2-10b The Natural Log of 4 Consecutive Quar ters of Earnings for White Males 11 Years after High School Graduation......................................................................113

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xi 2-10c The Natural Log of 4 Consecutive Qu arters of Earnings for White Males 12 Years after High School Graduation......................................................................114 2-10d The Natural Log of 4 Consecutive Quar ters of Earnings for White Males 13 Years after High School Graduation......................................................................114 2-10e The Natural Log of 4 Consecutive Qu arters of Earnings for White Males 14 Years after High School Graduation......................................................................115 2-10f The Natural Log of 4 Consecutive Qu arters of Earnings for White Males 15 Years after High School Graduation......................................................................115 2-11a The Natural Log of Annualized Earn ings for White Males 10 Years after High School Graduation..................................................................................................116 2-11b The Natural Log of Annualized Earn ings for White Males 11 Years after High School Graduation..................................................................................................116 2-11c The Natural Log of Annualized Earn ings for White Males 12 Years after High School Graduation..................................................................................................117 2-11d The Natural Log of Annualized Earn ings for White Males 13 Years after High School Graduation..................................................................................................117 2-11e The Natural Log of Annualized Earn ings for White Males 14 Years after High School Graduation..................................................................................................118 2-11f The Natural Log of Annualized Earn ings for White Males 15 Years after High School Graduation..................................................................................................118 2-12a The Natural Log of 4 Consecutive Qu arters of Earnings for White Women 10 Years after High School Graduation......................................................................120 2-12b The Natural Log of 4 Consecutive Qu arters of Earnings for White Women 11 Years after High School Graduation......................................................................120 2-12c The Natural Log of 4 Consecutive Qu arters of Earnings for White Women 12 Years after High School Graduation......................................................................121 2-12d The Natural Log of 4 Consecutive Qu arters of Earnings for White Women 13 Years after High School Graduation......................................................................121 2-12e The Natural Log of 4 Consecutive Qu arters of Earnings for White Women 14 Years after High School Graduation......................................................................122 2-12f The Natural Log of 4 Consecutive Qu arters of Earnings for White Women 15 Years after High School Graduation......................................................................122

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xii 2-13a The Natural Log of Annualized Earn ings for White Women 10 Years after High School Graduation..................................................................................................123 2-13b The Natural Log of Annualized Earni ngs for White Women 11 Years after High School Graduation..................................................................................................123 2-13c The Natural Log of Annualized Earn ings for White Women 12 Years after High School Graduation..................................................................................................124 2-13d The Natural Log of Annualized Earni ngs for White Women 13 Years after High School Graduation..................................................................................................124 2-13e The Natural Log of Annualized Earn ings for White Women 14 Years after High School Graduation..................................................................................................125 2-13f The Natural Log of Annualized Earn ings for White Women 15 Years after High School Graduation..................................................................................................125 2-14 The Labor Force Participation of Wh ite Women Age 28 – 33 Observed in the Labor Force at Age 33............................................................................................127

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xiii Abstract of Dissertation Pres ented to the Graduate School of the University of Florida in Partial Fulfillment of the Requirements for the Degree of Doctor of Philosophy ESSAYS ON THE EFFECTS OF FAMILY AND SCHOOLING ON STUDENT OUTCOMES By Mark Hoekstra August 2006 Chair: David Figlio Major Department: Economics This dissertation examines th e effect of changes in fam ily structure a nd university selectivity on the outcomes for students. In the first pape r, I examine the effect of parental divorce. Previous research ha s identified the effects of parental divorce primarily by comparing the outcomes of ch ildren whose parents divorced to those of children in intact families, conditional on obser vable characteristics. In contrast, this paper identifies the effect of parental divorce on educationa l outcomes by comparing the outcomes of children whose parents divorced to those of children whose parents filed for divorce but later had the cases dismissed. Using a panel of child-level administra tive data on reading and mathematics standardized test scores and disciplinary records for a large Florida school district, I find no evidence that parental divorce negatively affects children over all. In contrast, I find that experiencing parental divorce 6 years earl ier causes girls to score over 14 percentile points higher on tests of readi ng achievement, relative to the a lternative. I also find some

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xiv evidence for a positive effect on the mathema tics achievement of girls and a negative effect on the reading achievement of boys, although those results are less precisely estimated and less robust. In the second paper, I estimate the effect of attending a state’s flagship university on earnings from ages 28-33. Doing so is typically difficult because those who are accepted at and choose to attend more selective schools typically would have higher earnings later on due to other factors such as higher ability, motivation, or family support. To solve that problem, I use a regression disc ontinuity design that effectively compares the earnings of students who were barely a ccepted at the flagship to those of students who barely missed the cutoff. I find sugge stive evidence of a pos itive effect on the earnings of white men ranging from 1% to 25%, the magnitude and statistical significance of which depend on the functional form used. I find no consistent evidence of an effect on the earnings of women generally, although I do find that white women with a strong attachment to the labor force have significantly higher earnings as a result of being accepted at the state flagship university.

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1 CHAPTER 1 “JUST KIDDING, DEAR”: USING DISM ISSED DIVORCE CASES TO IDENTIFY THE EFFECT OF PARENTAL DIVORCE ON STUDENT PERFORMANCE 1.1 Introduction The increased incidence of divorce in American families was undoubtedly one of the most significant social trends of th e 20th century. Although divorce rates have declined slightly recently, the number of divorces per 1,000 married women aged 15 and older more than doubled from 9.2 in 1960 to 19.5 in 1996, and demographers project that if current rates of divorce continue, approxima tely 50% of recent first marriages will end in divorce. The impact of this trend on children is clear: over 1 million children are affected annually by divorce. In a rare example of unity between liber als and conservatives, concern regarding the implications of parental divorce for ch ildren’s well-being ha s been expressed by politicians across the political spectrum. Presid ent George W. Bush has stated that “the most effective, direct way to improve the live s of children is to encourage the stability of American families” (2002a). Senator and former First Lady Hillary Rodham Clinton has also shown concern regarding the effect divor ce has on children, saying, “The instability of American households poses great risks to the healthy development of children” (1998, p. 39). These concerns have resulted in several political movements toward divorce reform. Three states have passed “covenan t marriage” laws, which introduce a second tier of marriage that offers more limited grounds for divorce and require pre-divorce counseling. Perhaps more importantly, there ha s also been a political movement toward

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2 legislation that would change no-fault and unilateral divorce laws to make it more difficult to get a divorce when children are invol ved; at least eight st ates have considered such legislation since 1996 (Friedberg, 1998). The common belief underlying nearly all po licy statements on this issue is that divorce causes children to be worse off than they would be if their parents had stayed together. An equally common view in policy circ les is that this belief is not motivated by ideological agenda but is rather a well-docu mented empirical fact. For example, in remarks made to the Chamber of Commerce in Charlotte, North Carolina, President George W. Bush stated Research shows that two-parent families ar e more likely to raise a child that is going to go to high school or colle ge, that a child in a two-pare nt family is less likely to get addicted to drugs. Now, I understand there are some families that just simply aren't meant to be. I know that. I'm not—I’m wise about that. On the other hand, we ought to aim for a goal, a goal that recognizes the power and importance of two-parent families in America.” (2002b) Similarly, in It Takes a Village Hillary Rodham Clinton wrote, “Recent studies demonstrate convincingly that while many adu lts claim to have benefited from divorce and single parenthood, most childre n have not” (1998, p. 39). It seems, however, that this is one more area in which the causal link has been made in the political arena before it has b een convincingly demonstrated in academia. Despite all of the interest in divorce and its effects on ch ildren, serious methodological issues limit the extent to which academic researchers have been able to determine the causal link. While there is clear ly a strong association betwee n family structure and child well-being, the central problem is that it is difficult to determine what child outcomes would result if troubled marriages that might otherwise end in divorce were to continue. Put differently, the challenge at hand is to separate the underlyi ng causes of divorce and

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3 their effects on children from the effects of th e divorce itself. Determ ining the nature of these causal relationships is very importan t for public policy, since the scope of public policy is largely limited to increasing the costs to the parents of getting a divorce and forcing the couple to reconcile rather than solving the unde rlying problems directly. While researchers have made some progre ss toward meeting this challenge, data limitations have continued to impair efforts at determining whether the effects captured are those of the divorce or of some unobserved variable that is in fact causing both the divorce and the child outcomes. Such limita tions have caused McLanahan and Sandefur to lament the fact that because no randomized experiment is feasible, analysts will never be able to agree on the caus al role of family structur e in child outcomes (p. 11, 1994), while Gruber states that the ev idence “has yet to convincingl y address poten tial selection biases associated with the d ecision to divorce” (p. 2, 2000). Clearly such pessimism is not the result of a lack of interest or effort by academics. Indeed, as Gruber (2000) has noted, there ar e vast literatures in economics, sociology, and developmental psychology that examine th e consequences of divorce. Although the early studies were cross-sectional, more re cently the trend has been toward doing event analyses of divorce that control for as many pre-divorce student and family characteristics as possible. These studies essentially identify th e effects of divorce by comparing the outcomes of children who expe rienced parental divorce to those of children in intact families, conditional on pre-divorce observables. However, this identification strategy only works to the extent one is able to control for every conceivable difference between families that divorce and families that do not, which is a difficult if not impossible standard for any data set to meet. This problem is exacerbated

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4 by the fact that the outcome variables used (such as high school graduation, years of education, and earnings) are not observed prio r to the parental divorce, so one cannot even control for the pre-divorce level of th e outcome measure used. Consequently, the conditional outcomes of children of intact families may not represent the correct counterfactual of how well off children of pa rental divorce would have been had their parents stayed together for an exogenous reason. To estimate the true effect of divorce, one must then be able to separate the eff ects of the unobserved process evident prior to the filing of the divorce from the effects of the marriage dissolution itself, something that is difficult to do by comparing children from intact families to children from families that experienced divorce. A better approach would be to utili ze data not only on children whose parents divorce, but also on children whos e parents file for a divorce that is later dismissed, the latter of which would effectivel y form the control group. This is precisely the identification strategy th at I propose. I am able to do this by combining two excep tional data sets. The first consists of an eight-year panel of detailed data on ev ery student in grades 1 through 12 in the Alachua County school dist rict, which is the 194th largest district in terms of enrollment among the more than 16,000 school districts in the United States. The second data set consists of public records on divorces f iled in Alachua County from 1993 2003. I merge these into one data set matching parent names, child names, and child birth dates found in both data sets. By constructing a data set in this way, I can examine the effects of parental divorce on children’ s standardized reading and mathematics test scores as well as discipline problems at the micro level of the children themselves. This is the first research that uses individual-level data for which the educational outcomes of students

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5 are observed prior to parental divorce, which enables me to use student-specific fixed effects. Furthermore, this is the first resear ch that utilizes a data set that identifies the children of parents who file for divorces that are eventually dismissed rather than granted, in addition to children whose parents did divor ce. By comparing children whose parents dismissed divorce cases to the children of parents who actually divorced, I can distinguish the effects of di vorce from those of the underlying causes of divorce, the latter of which are evident in both families. The results lend little support to the idea that parental divor ce negatively affects the academic achievement of students overall. Although I find that students who experienced parental divorce have lower read ing and math scores and more disciplinary problems afterward relative to children from intact families, I find a similar (and stronger) result when comparing the outcomes of children whose parents filed for divorce but later decided against it to those of childre n from intact families. This suggests that the so-called consequences of divorce found by comparing children of divorce to children of intact families are likely c onsequences of the factors that caused the parents to divorce rather than of the divorce itself. Indeed, when comparing the outcomes of children whose parents divorced to children whose parents fi led for and dismissed a divorce case, I find no negative effect of divorce overa ll. In fact, I find that experiencing a parental divorce six years ago causes girls to score 14.68 percentile points hi gher on reading tests than they would have had their parents stayed t ogether, a result that is both statistically significant and robust. I find somewhat weak er and less robust evidence that parental divorce has a positive effect on the mathema tics achievement of girls and a negative effect on the reading achievement of boys. Fi nally, the results suggest that experiencing

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6 parental divorce causes an increase in di sciplinary problems immediately after the divorce, but that there is no eff ect 4 years after the divorce. 1.2 Theoretical Considerations, Literatu re Review, and Identification Strategy 1.2.1 How Divorce Affects Student Achievement There are several mechanisms through wh ich divorce may affect the academic achievement of children. A child whose pa rents divorce may experience less parental attention and assistance with sc hool work at home, thus redu cing child learning. Parental absence may also reduce the average quality of the assistance received at home, further lowering school performance. For example, th e custodial parent may now be the one to assist a child in a subject area in which the ab sent parent would have been more able to help. The child may also experience less parental guidance as a result of divorce, allowing the student to lose focus in school. The overa ll trauma of the divorce and family structure change may also distract a child from school activities, at least temporarily. A divorce may lower the level of economic resources available for the child, leading to a reduction in the quantity and quality of non-school educational inputs purchased for the child, causing the child to be worse off. Finally, a child may have to move as a result of the divorce, forcing th e child to adapt to a new house, neighborhood, and perhaps even school. Some research has suggested that m oving itself negatively affects academic achievement (e.g., Haveman, Wolfe, and Spaulding, 1991). It is important to note, however, that not all of the ways in which divorce can affect children are negative. For exam ple, although the loss of contact with a divorced parent is typically assumed to have negative conseque nces for the child, divorce may be beneficial if the divorced parent is abusive or alcoholic. Furthermore, parental conflict itself may lead to a reduction in the quant ity or quality of parental inpu ts for the child’s education as

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7 well as distract the student fr om focusing on school. To the extent that divorce reduces parental conflict, children may perform better academically. Consequently, while divorce may affect child outcomes though any of several mechanisms, the net effect of divorce is theoretically ambiguous. The effect of divorce need not be permanen t, either. Depending on the extent to which parent and child overcome the trauma from the change in family structure and successfully adapt to the new circumstances, it is quite possible that th e effect of divorce may change over time. 1.2.2 A Review of the Literature The early research on divorce consisted ma inly of cross-sectional studies that compared the outcomes of children from intact families to those of children from divorced families (e.g., Keith and Finlay, 1988). Several researchers have noted, however, that there are significant diffe rences in the pre-divorce observable characteristics of families that experience di vorce relative to those that do not. In an effort to control for pre-divorce characteristics of families, some studies have used retrospective data on variable s such as self-reported pare ntal conflict (e.g., Amato and Booth, 1991). More recently, the trend througho ut the literature is to use longitudinal data to accurately control for some pre-divor ce student and family characteristics such as the student’s cognitive test scores, family income, and parent’s education (e.g., Cherlin, Kiernan, and Chase-Lansdale, 1995; Borge ss, 1998; Lang and Zagorsky, 2000; Painter and Levine, 2000; Ermisch and Francesconi 2001a and 2001b; Fronstin, Hill, Yeung, and Duncan, 2001; Greenberg, and Robins, 2001; Deleire and Kalil, 2002;). With the exception of Lang and Zagorsky (2000), thes e studies have found that divorce has negative consequences for children.

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8 Although this research does illustrate that it is important to control for pre-existing differences in divorced and intact families, significant problems remain. First, several studies rely on self-reported m easures of parental conflict. For such measures to be properly used, it must not only be the case that the measures accurately capture the parental conflict that may impact children’s outcomes, but it must also hold that such measures of conflict are comparable acro ss households. Similar problems exist when using measures of children’s psychological well-being. Second, the primary child outcomes that re searchers have use d, such as marital status, educational attainment, and earnings, ar e observable only when the child reaches adulthood. Consequently, researchers exam ining those outcomes can only control for pre-divorce differences in family characteristi cs and not in child outcomes themselves. Third, and most importantly, th ere is significant reason to believe that controlling for pre-existing levels of family characteristics and child outcomes may be inadequate. For example, it is easy to conceive of an unobserved variable that determines both a child’s outcome and the family structure. Th is unobserved variable may be a process that causes parental relations to wors en to the point that parents se lect into divorce, while at the same time negatively affecting the children. Since this is a process and not merely a level of family or child characteristics (aft er all, by definition the parents had not yet divorced at the time of the pre-divorce observation), control ling for pre-divorce characteristics or outcomes will not adequate ly measure how well off the children would be if the parents did not divorce. Cons equently, even conditional on pre-divorce observables, the outcomes of children of intact families may not be the correct counterfactual for children who experienced pa rental divorce. In contrast, by using the

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9 outcomes of children whose parents file for a divorce that is later dismissed as an estimate of the counterfactual, my identification strategy is able to separate the effect of the divorce from the effects of the processes that caused the divorce. There have been other attempts at overco ming the selection effects associated with parental divorce. Sandefur and Wells (1999) used sibling information to identify the effects of divorce by comparing siblings with varying exposures to single-parent families or changes in family structure to each othe r. Ermisch and Francesconi (2001a) used a similar sibling strategy. However, within-fam ily comparisons will be flawed if siblings are affected differently by divorce, whet her due to age or other reasons. More importantly, sibling strategies will also lead to downward-biased estimated effects of divorce if there is an underly ing family trend over time that determines both family structure and child outc omes. Furstenberg and Kiernan (2 001) used a slightly different strategy and compared the outcomes of child ren who experienced divorce to those of children whose parents divorced after the children had grown up. That approach, however, will fail when there are significan t pre-divorce trends or when there are unobserved differences in the intensities of the underlying problems leading to the two types of divorce, both of which are very plausible possibilities. Gruber (2000) approached the selection problem by e xploiting variation in the unilateral divorce laws across states and ove r time. That approach, however, may not overcome the selection problem if there were underlying trends that led states to pass unilateral divorce laws at different times or if as Gruber noted, those laws had an effect on children in ways other than through divorce. Indeed, the basic problem is that in addition to being concerned with unobserved variables in families that experience

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10 divorce, since the variation used to identify the effects of divorce in Gruber’s approach occurred at the macro (state) level (instead of the individual leve l), one must also be concerned about unobserved charact eristics at the state level that might lead to worse outcomes through means other than an increased propensity for divorce. Other research on the consequences of divorce has focused on examining the effects of separation by parental death (F ronstin, Greenberg, and Robins, 1999; Lang and Zagorsky, 1999; Corak, 2001). This allows re searchers to identify the effects of the complete loss of parental contact and supervision as well as of economic support.1 However, in nearly all cases the underlying pr ocesses that cause divor ce are substantially different from those that cause spousal death.2 Consequently, an examination of the effects of parental separation by death does litt le to shed light on the issue of what would happen to children whose parents divorced if an exogenous force such as increased costs of divorce had prevented them from doing so. 1.2.3 Identification Strategy The identification strategy employed in this paper is most similar in spirit to that used by Bound (1989), who estimated the disi ncentive effects of Social Security Disability Benefits by compari ng the labor outcomes of reject ed disability applicants to those of accepted disability applicants. Bound concluded that disability benefits accounted for substantially less than half of the postwar decline in the labor force participation rates of older men and that previous cross-sectio nal strategies had exaggerated the causal disincentive effects. The purpose of this paper is to determine 1 Unobserved life insurance payouts may compli cate the issue of economic support, however. 2 A notable but rare possible exception is spousal homicide.

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11 whether or not a similar story is true with resp ect to the causal effect s of parental divorce on student outcomes. To do that, I compare the annual standardiz ed test scores and disciplinary records (number of infractions per year and days su spended per year) of children whose parents dismissed divorce cases to those of childre n whose parents divorced. Since I observe outcomes for each student in every year, I am ab le to utilize student-specific fixed effects, allowing for both a time-invariant shock effect of parental divorce as well as an effect that changes over time. By identifying the effects of parental divorce by comparing not the achievement levels but the changes in the test scores of children whose parents divorce to those of children whose parents di smiss divorce cases, I lessen the possibility that the effect I estimate is really an effect of an unobser ved variable co rrelated with divorce and not of the divorce itself Still, my data allow me to test the validity of this identification strategy in two ways: Do the observable characteristics of the tw o groups look similar prior to the parents filing for divorce? To the extent that th ere are differences, one might be concerned that these differences may cause one group to trend differently in the post-divorce period regardless of whether the couples divo rced or not. I address this question in Section 1.4.3 Are there differences in the trends of the outcomes prior to the filing of divorce? Again, to the extent that there are, one might be concerned that these trends may continue in the post-divorce period regard less of whether the marriages ended in divorce or not. I address this question in Section 1.4.5. Although the variation I exploi t in this paper is not e xogenous, there is reason to believe that the selection at work would im ply that the estimated effects of parental divorce on student test sc ores will be biased downward, if at all. For example, those couples who decide to have the divorce case dismissed may do so in part out of concern that the divorce may adversely affect their ch ildren, which for reasons discussed earlier is

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12 a widely held belief. To the extent that th e increased concern for children in this group (the control) might have cause d the post-divorce case scores of their children to trend upward over time relative to the divorce group even had they divorced, my estimates will be downward biased. Second, it could also be the case that the parents who dismiss their divorce cases do so because they experienced a positive shock to their marriage during the divorce process that may cause them to rationally expect their marriage to improve significantly in the future, whereas those couples who divorce do not. Again, to the extent that this would cause the test scores of children w hose parents dismissed divorce cases to trend up relative to those of child ren whose parents divorced, my estimates will be downward biased. Finally, those parents who choose not to divorce may do so simply because their marriages are not as ba d as those of parents who divorce.3 If this implies that the children whose parents dismissed di vorce cases would learn at a faster rate afterward than would the appropriate control group ideally characterized by families that would have experienced divorce if not for so me exogenous force, then this too would cause my estimates of the parental divorce eff ect on test scores to be biased downward. Together, these possibilities suggest that th e selection at work in my identification strategy should, if anything, bias my estimates of the effect on test scores downward, implying that any positive effect would be a lower bound. 3 This would be similar to the problem with the tr aditional identification strategy of comparing children whose parents divorce to children whose parents stay together, although one might reasonably expect that the extent of the bias would be smaller here since both groups of couples filed for divorce.

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13 1.3 Parental Divorce and Student Test Scores 1.3.1 School Data To address the effects of divorce, I us e a confidential student-level data set provided by the School Board of Alachua County in the state of Florida. This data set consists of observations of students in the first through twelfth grades for the academic years of 1993-94 through 2002-2003. The Alach ua County School District is large relative to school di stricts nationwide; in the 2000 -2001 school year, there were on average 2,200 students in each grade, making it the 194th largest school district among the more than 16,000 districts nationwide. The student population was approximately 56% white, 36% African-American, 4% Hispanic and 2% Asian. Forty-four percent of students were eligible for subsidized lunches. For each firstthrough tenth-grader I obser ve norm-referenced standardized test scores in reading and mathematics. The te st scores reflect the percentile ranking on one of two national tests relative to all test-takers nati onwide. Prior to the 1999-2000 academic year, nearly every student in the third through ninth grades took the Iowa Test of Basic Skills (ITBS). In addition, at the discretion of the school principal, many first and second-graders also took these exams. Starting in the 1999-2000 school year all firstthrough tenth-graders were tested using the Stanford 9 test. This change was made because the Stanford 9 test is used for the Florida Comprehensive Assessment Test (FCAT) that was introduced in the 2000-01 school year to enable the st ate of Florida to evaluate schools. Both the ITBS and the Stanford 9 are exams used by schools nationwide to test mathematics and reading. Except for some first and second graders prior to 2000, almost all students took the te sts in a given year. As described later,

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14 however, observations on some students we re dropped in order to ensure a clean comparison. In addition, student records al so contain the names and a ddresses of the parents of each student for each year. This information is gathered primarily during August of each year during registration, alt hough it is updated continually th roughout the year. The data on names are crucial because that is the info rmation used to match divorce information to the student records. Discipline records are also observed for ever y firstthrough twelfthgrader, beginning in 1993 (prior to when the st andardized testing reco rds begin). Finally, I observe information on each student’s race, sex, school lunch status, disability status, and gifted status. In the following analysis, I use four depende nt variables from these school data. The primary outcomes that are used are the mathematics and reading scores on the Iowa Test of Basic Skills or Stanford 9 examinati ons. In addition, I also look at two outcomes from the disciplinary records for each year including the total number of days each student was suspended and the total number of disciplinary infractions each student committed. 1.3.2 Divorce Data The divorce data used in this study were gathered from public records information at the Alachua County Courthouse. This information includes the names of every husband and wife who filed for a divorce at the Alachua County Courthouse between January 1, 1993 and March 12, 2003. For each filing, I retrieved the filing date, the final judgment date, and the final judgment type. In addition, I also obtained child names and birth dates for certain divorce cases by pers onally examining the files at the Alachua County Courthouse, as desc ribed in Section 1.3.4.

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15 1.3.3 Divorces in Alachua County, Florida In order to file for a divor ce in Florida, at least one of the parties in the marriage must have resided in Florida for at least six months. There are then two filing types. If there are no minor or dependent children of the marriage parties and if the marriage parties agree about how to divide property and that the marriage is irretrievably broken, they may file for a Simplified Dissolution. However, if there are children involved, the couple must file for a Dissolution of Marriage All divorce information used in this study is obtained for couples who have filed for the general Dissolution of Marriage.4 In order for the court to grant the dissolu tion of the marriage, the court must either rule that the marriage is irretrievably broken or that one of the marriage parties has been judged mentally incapacitated for a minimum of three years.5 The court may then choose to do any of several things s een as in the best interest s of the marriage parties and dependent children, such as ordering that e ither or both marriage pa rties consult with a person deemed qualified by the court (e.g., a marriage counselor) and found accepby the ordered party or parties, or extending the proceedings no more th an three months to enable the parties themselves to effect a reconciliation. During any period of continuance, the cour t can make orders regarding a limony and support for the parties, child custody and visitation rights, propert y division, and so on. Although there is no mandated pre-divorce waiting period in Flor ida, if there are minor children of the 4 This includes nearly all divorceseeking couples with children. Although having children violates a condition for filing for a Simplified Dissolution, some su ch couples may exist. For example, if a couple files for a divorce and mistakenly claims that the wife is not pregnant when she in fact is, they may file for a Simplified Dissolution. These sorts of exceptions are probably very rare, how ever, and to the extent young children are involved, my data set would not be changed anyway. 5 Not surprisingly, the “irretrievab ly broken” clause is the path most commonly tread by those seeking divorce in Alachua County, Florida.

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16 marriage, then prior to obtaining a final hear ing each parent is required to attend one of seven four-hour parenting edu cation classes approved by the 8t h Judicial Circuit Court. Finally, if after the final heari ng the court finds that the marri age is irretrievably broken, a final order of dissolution of marriage is given. Alternativel y, if the parties work out the problems, the petitioner may have the case vo luntarily dismissed. The judge may also notify the parties of intent to dismiss if th ey have not fulfilled their obligations to the court. Within a month after this intent to dismiss is issued, the judge may order that the case be dismissed. Within days of the re solution, the case is closed. For reasons discussed in the next section and seen in 9, this study uses only those dismissed divorce cases in which the petitioner specifically requested that the case be dismissed. 1.3.4 Merging the Divorce Data with the School Data Since my primary identification strategy depends crucially on correctly matching children in the school data to divorces filed in Alachua County, every effort was made to ensure that those matches that were made were correctly made. Consequently, divorces were matched to students’ pare nts using a created variable: Firstnameparent1Lastnameparent1Firstnameparent2Lastnameparent2. Only unique couple-name combinations we re used. Consequently, if John and Mary Smith were observed to have filed for more than one divorce case from January 1, 1993 through March 12, 2003, those divorce cas es were not matched to students.6 Similarly, if in the school district in a ny given year from 1993 through 2003 there were two or more children who were not siblings but who had parents with identical names, 6 In reality, the uniqueness standard was applied more stri ctly than this. In the divorce data I observe up to nine names for both the husband and the wife, due to the fact than any address or name changes must be disclosed to the court. If any first-last name couple combination for a given divorce was identical to that in another divorce case, that divorce case was not matched.

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17 those children were not matched to any divorce. Siblings were de fined as children who shared the same last name and lived at the same residential address. Divorces were matched to students on a y ear-by-year basis. Since the parental name information from the school district is from fall registration in August of each year, these parental names were matche d to divorces filed from August 1st of that year through July 31st of the following year. This was done to increase the likeli hood that the parent names from the school district used to match to divorces were both present. In contrast, if one were to try to match August names to a divorce filed in January of that same year, the parent names in the school data may not both be present or may have changed since the divorce was filed. Table 1 shows how many divorces have been filed in Alachua County, Florida, from January 1, 1993, through March 12, 2003. The also shows how the number of total divorce cases varies from the number of divorce cases expected to be associated with children in the public school system. For example, in the year 2000 there were 1,123 divorce cases filed, of which 974 were Gene ral Dissolutions (a necessary but not sufficient condition for the case to have chil dren involved.) Of those, 904 had unique parent name combinations. A random ch eck of 100 General Dissolutions from 19932003 indicated that 54% of the marriages had minor children of that marriage, implying that an estimated 488 of those divorce cases ma y be expected to have minor children of the relevant marriage involved. Since I matc h divorces only to children in grades one through twelve and approximately 10% of stude nts in the county atte nd private schools, there were approximately 293 divorces in 2000 th at I could reasonably expect to match. Given that about 10% of the parent name combinations in th e school data were

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18 nonunique, there remained approximately 264 divor ces filed in the year 2000 that I could expect to match. In all, I could reason ably expect to have matched at most 2,512 divorces. While I do not claim that this is the exact number of matchable divorces, it is my best guess as to how many I could expect to match. As shown in Table 2, I matched 724 divor ce cases to names in the school data using the parent name identifier7, for a match rate of 28.8%. Of those 724 divorce cases, 583 were matched to a student for whom I obser ved at least one test score. Of those matches made to children observed with at least one test score, a random check of 100 children matched to divorces suggested that an estimated 97 percent of the matches made were made correctly.8 However, only 66 of those 724 matched di vorce cases had been dismissed. In order to increase the sample size of dismi ssed divorce cases, I went to the Alachua County Courthouse and looked up all dismisse d divorce cases with unique parent name combinations that were filed from Janua ry 1, 1993 – March 12, 2003. I then matched these dismissed divorce cases to children in the school data for which the first and last name of the child matched along with at leas t one of the followi ng two identifiers (and none contradicted significantly9) 7 The matches in Table 2 include only matches made to children whose parents were believed to be the natural or adoptive parents of that child. I defined parents as the natural or adoptive parents of a child when the child shared his or her last name with at least one of the parents listed by the school district in the year before or in the year in which the divorce case was filed. 8 This was done by manually looking up the divorce judgment papers fo r each of 100 randomly selected matches made and comparing the child’s name from my matched data to the names of the children in the divorce papers. All observations matched to the thr ee cases that were incorrectly matched were dropped from the data set. 9 For example, if the date of birth in one file said 8/16/1985 and the date of birth in the other file said 8/16/1986, I made the match provided that the child name and parent names matched.

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19 child’s date of birth parents’ names Furthermore, only dismissed divorce cases in which one spouse was not found to be deceased were matched. At this point, some adjustments were made to the matched set of students matched to a dismissed di vorce case in order to ensure a proper comparison, the impact of which is shown in Table 3. First, all observations matched to a divorce case that had been dismissed by th e judge (as opposed to ones in which the petitioner requested the dismi ssal directly) were dropped from the data set. Although it may not at first seem intuitive why one would want to eliminate those dismissed cases from the data set, it becomes evident from looking at the characteristics of both groups prior to filing for divorce, as shown in columns C and D of Table 9. For example, the average reading score of children whose pa rents later filed for a divorce that was dismissed due to something other than a di rect request by the pe titioner was 33.3, while the average reading score of children whos e parents later filed for and specifically requested the dismissal of a divorce case was 57.3. Similar differences are evident between these two groups with respect to ma th scores, subsidized lunch status, and the percent black. In addition, since I want to ensure that the dismissed divorce cases in the data set were not caused by a threat of violence by one spouse to the other, I acquired data on domestic violence cases filed from 1993-2003. I then matched domestic violence cases to the school data by matching the parent na me combinations in the domestic violence cases to parent name combinations in the sc hool data set. The obs ervations of students who were matched to a domestic violence case were then dropped from the data set.

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20 Finally, all observations matched to st udents for whom only one parent name was listed by the school district in the year prior to that in wh ich the divorce was filed were dropped from the data set, since those childr en could not have been matched to a case that ended in divorce due to the nature of the matching algorithm described above. The absence of a parent in the school record s could reflect unobserved negative family characteristics. In addition, it is unclear exactly what a divorce means for a family for which only one parent name is lis ted by the school district. 1.3.5 The Final Data Set Used in the Analysis Although my primary identifica tion strategy is to compar e the outcomes of children of actual parental divorces to those of dismi ssed parental divorces, in order to replicate the methodology of other papers in the literature, I need to be able to identify children who did not experience parental divo rce from 1993 through March of 2003. Unfortunately, the data do not contain this in formation. Consequentl y, I try to identify these children in two ways. First, in the less restrictiv e method, I define two groups by trying to eliminate those children who a) could not have been matched to a divorce, or b) were likely to be in a single-parent family. Specifically, I removed from the data set all observations of any child who met one of the following conditions: 1. Was observed with at most one parent’s na me for one year and was not matched to a divorce in another year. 2. Was observed with parents whose names were not unique for any year from 19932003 (after accounting for sibl ings) and thus could not have been matched to a divorce case in that year. 3. Was observed with parents whose names were the same as those associated with more than one divorce from 1993-2003.

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21 Although the primary cross-se ctional results excluded st udents only on the basis of the above conditions, as a check I also perfor med the cross-sectional analysis using data in which I also excluded each student that met the following condition as well: 4. Was observed to have a different last name than at least one of the parents listed by the school district. The purpose of these deletions is to ensu re that those students who remained did not experience parental divorce and form the c ounterfactual used in previous researchers’ identification strategies. In addition, I drop all observati ons of students for whom the first and last names of both parents changed over time. The result of leaving out these students based on conditions 1 through 3 is to reduce the overall sample size from 1,500-2 ,000 students/grade/year to 400-700 students/grade/year. In all, the data used to compare ch ildren of divorce to children whose parents did not divorce consist of 60,196 observations on 17,241 children from 1993-2003 (35,055 observations on 9,654 children when conditions 1-4 are used). The descriptive statistics of these students in th e year 2000 can be seen in columns A and B of Table 9. It is clear from these columns that the more restrictive sample (column B) does appear to eliminate students whose parents ar e not married or for whom a grandparent is listed as a parent, even though it may also e liminate children whose parents are in fact married. In the main analysis in which only child ren whose parents filed for divorce are included, there are 6,761 observations on 1,028 ch ildren whose parents filed for one of 716 divorce cases. A total of 93 of those divorce cases were di smissed, affecting 156 children. The first row of Table 4 shows how observations of these two groups of

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22 students are distributed over time. It shows that approximately 75% of the children linked to a divorce case are observed after th e divorce. This proportion of children declines steadily; approximat ely 20-25% of students linked to a divorce are observed at least five years after their pare nts’ divorce case was closed. When only observations linked to at leas t one test score are included, there are 27,102 observations on 9,388 children in the data set that includes children whose parents never filed for divorce and those whose parents did file for divorce. In the data set used in the main analysis in which only child ren whose parents filed for divorce were included, there are 3,525 observations on 801 children, representing 580 divorce cases. There are 111 children linked to 93 dismissed divorce cases. The second row of Table 4 shows how observations on students matched to parental divorce cases were distributed over time. Approximately 75-80% of the st udents matched in each group are observed with a test score after the di vorce case was closed. As shown in Table 4, approximately 35% of students matched to divorce are observe d 3 to 5 years after the case is closed, while approximately 20-30% are observed with a test score more than 5 years after the divorce case was closed.10 Overall, the distribution for the group of children whose parents divorced is quite similar to the distribution for the group of children whose pare nts filed for a divorce that was later dismissed, with the exception that more than 5 years after the divorce or dismissal, I tend to observe relatively more (5 to 10 percentage points) students who 10 For the entire sample of observations (some of which do not have a test score), the time after the divorce is defined as the calendar year of the observation minus the year in which the divorce case was closed. For the subset of observations for which there is at least one test score, the time after the divorce is defined as the number of years between the date the divorce case was closed and the date of the test and thus is not necessarily an integer.

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23 experienced a dismissed divorce than those w ho experienced parental divorce. While this could be due to the fact that childr en whose parents later divorce are on average slightly older (1.6 years) than their peers whose parents file and dismiss a divorce case, later in the paper I nevertheless examine the sensitivity of the results by reestimating the results after excluding all obser vations 5 or more years afte r the closure of the divorce case. However, the overall similarities in th e distributions of the observations in the two groups is important because one might be c oncerned that children who are negatively affected by divorce leave the county and thus the sample. The overall similarities in the distributions indicates, however, that for attr ition to bias the results, it must not only be the case that children whose parents divorced do so at the same ra te as those whose parents dismissed a divorce case (at least for the first five years afterwards) but also that those in the two groups who did leave were affected by the closure of the case in different ways. While not impossible, such a scenario does seem unlikely. 1.4 The Effects of Divorce on Student Performance 1.4.1 Comparing the Test Scores of Child ren of Divorce to Those of Children in Intact Families A common finding in the divor ce literature is that ch ildren of divorced parents experience poorer outcomes than do child ren who are brought up in two-parent households. Even though this approach has seri ous flaws, it is still constructive to test whether my data appear to be qualitatively sim ilar to data used in previous research. To test for the unconditional cross-sectional eff ects of divorce, I estimated a regression using pooled data in which I control only for year a nd grade effects to remove the effect of any trend over time in percentile test scores in th e school district (wheth er caused by a change in the test used or something else.) The general regr ession equation was

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24 testit = b0 + b1 X + b2 PostDivorceit + it where testit is the test score of student i at year t and X is a vector of covariates one expects to affect test scores. The variable PostDivorce is equal to one if the test was taken after the child’s parents finalized their divorce. The results for reading and math test scores are given in Tables 5 and 6, respectively. The p-values are given in the second row of each cell, which were calculated using standard errors clustered at the family level.11 When only student grade and year effects are included as covariates, pa rental divorce is associ ated with reductions of 1.97 and 1.31 percentile points in reading and math, resp ectively, although neither is statistically significant at conve ntional levels. As other re searchers have noted, however, there are significant differences in the obs ervable characteristics of children whose parents divorce compared to those of childre n whose parents remain married. My data allow me to condition on several important variables, including race, sex, school lunch status, and zip code median family inco me, and squared zip code income. Although including these variables may cause an upward bi as in the test score estimates due to the fact that some could themselves change as a consequence of divorce (e.g., subsidized lunch status), it is still worthwhile to include them to see if their inclusion explains the differences between children whose parents divorce and children whose parents do not divorce. The top sections of row (b) in Tabl es 5 and 6 contain these results and suggest that parental divorce is asso ciated with reductions of 2.19 and 1.32 percentile points in reading and math, respectively, the former of which is statistically significant at the 10% 11 The school district does not identify families, so although I identify families for children whose parents filed for divorce, for the other children I as sumed each was in a separate family.

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25 level. The top section of row (c ) also includes school fixed effects.12 There, the result indicates that parental divorce is associated with reading a nd math scores that are 0.78 and 0.48 percentile points lower, respectively, although neither estimate is statistically significant at the 10% level. These data also allow me to examine the extent to which the impact of divorce affects children differentially based on the grade at which they experienced parental divorce, represented by DivorceGrade variable in the equation below. In addition, I can examine how the effects of divorce grow or diminish over time by including an interaction term measuring the number of years after the divorce when the test was taken. Consequently, the general form of th e regression estimated is given by testit = b0 + b1 X + b2 PostDivorceit + b3 YearsAfter*PostDivorce +b4 DivorceGrade*PostDivorce + it. The results given in the bottom of row (b ) in Tables 5 and 6 suggest that the association between having experienced pare ntal divorce and lower test scores grows over time. I find that reading and math scores fall by approximately 0.79 and 1.26 statistically significant percentil e points, respectively, in every year after the divorce. In the case of reading achieveme nt, the statistically signifi cant coefficient of 1.23 on the grade of the student at the tim e of the divorce indicates that divorce is less negative for the child when it occurs when the child is older. As shown in the far right column, experiencing a parental divorce while in the 4th grade is associated with statistically significant declines of 3.87 a nd 5.25 percentile points on math and reading tests 6 years later. 12 The student’s school was only observed for students for whom I observed at least one test score in that year. In addition, prior to the 1999-2000 sc hool year, I observed the school only for 3rd – 5th graders.

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26 In the bottom of row (c), the results are shown when school fixed effects are included in the model. While the associati on between lower math scores and parental divorce is not changed much by the inclusi on of the school effect s, the association between parental divorce and worsening read ing scores over time is smaller than when school effects are not included, reducing that effect for the hypothetical 10th grader whose parents divorced 6 years pr ior to a statistically insi gnificant -1.79 percentile points.13 Tables 7 and 8 contain similar analyses using the number of days suspended per year and the number of discip linary infractions per year as outcome variables. From these tables, it is clear that having experienced parental divorce is associated with statistically significant increases in both the number of days suspended per year and the number of disciplinary infractions committed. Experiencing parental divorce is associated with 0.79 more days suspended per year and 0.39 more disciplinary infractions per year, both of which are statistically signi ficant at the 1% level. By comparison, the average student in the data set is suspended for 1.2 days and commits 1 infraction per year, implying that the cross-sectional correla tions found are quite larg e. When the effect of divorce was allowed to vary over time, each year after the divorce is associated with increases of 0.16 days suspended and 0.07 infr actions per year, although only the former is statistically significant at the 10% level. As shown in the far right column of each table, experiencing a pa rental divorce as a 4th grader is associated with committing 0.54 more disciplinary infractions and being su spended for 1.16 more days when in the 10th grade, both of which are statis tically significant at the 5% level. While the inclusion of 13 Just as with the income measures, it is possible that th e school fixed effects pick up some of the effect of parental divorce as well, which would cause these estimat es to be biased upward. This is due to the fact that moving to an area with a lower quality school may itself be a consequence of parental divorce.

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27 school fixed effects does reduce these correlatio ns to marginal statistical significance, on the whole it does appear that experiencing parental divorc e is correlated with more disciplinary problems. These cross-sectional correlations grow even stronger when using the more restrictive definition of child ren whose parents were and re mained married over the time period. For example, although unreported, the ne gative cross-sectional effect of divorce on reading scores for a 10th-grader 6 years goes from -3.87 (p=0.059) to -6.20 (p=0.004) when students whose last name differs from th at of a reported parent are not defined as children whose parents were and remained married. Similarly, the negative crosssectional effect on days suspended increas es to 1.46 (p=0.000) from 1.16 (p=0.004). Given the potential problems with estim ating the effects of divorce by comparing children of parental divorce to children of intact families conditional on observable characteristics, the important thing to note fr om the results in Tabl es 5 8 is not that divorce has a negative effect. Rather, the point is that there is a cross-sectional correlation between having experienced pare ntal divorce, lower academic achievement, and higher rates of disciplinary problems, even conditional on observable characteristics. Whether or not this is indeed the true causal e ffect remains to be seen, and is the focus of the remainder of the paper. 1.4.2 Do We Observe the Same Correlation when Comparing Children of Dismissed Divorce to Children of Intact Families? It is worth asking, however, whether or not similar associations are seen when comparing the outcomes of children whose pare nts filed for divorce but did not divorce to the outcomes of children in intact families. If experiencing a dismissed divorce case is associated with worsening outcomes relative to children whose parents do not file for

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28 divorce, it suggests that the correlations observed in the previous section are consequences of the factors that caused the pa rents to file for divorce rather than of the divorce itself. Results are contai ned in Tables 9 through 13. The results are striking. As seen in th e top of row b of Tables 9 and 10, a tenth grade student whose parent s filed for divorce 6 years earlier scores 6.42 and 3.78 percentile points lower on readi ng and math tests than his or her counterparts in intact families, although only the effect on reading scor es is statistically significant at the 5% level. Similarly, the results in Tables 11 and 12 show that a 10th grade student whose parents filed for divorce 6 years earlier co mmits a statistically significant 1.21 more infractions/year and is suspe nded for a statistically signifi cant 2.20 more days/year than a student whose parents never filed for divorce. As one would expect, the correlation be tween worse outcomes and experiencing a dismissed divorce are even stronger when the mo re restrictive definition of a child in an intact family is used. Although unreported, th e so-called “effect” of a dismissed divorce on the reading achievement of a 10th grader whose parents di vorced six years prior changes from -5.49 (p=0.170) to -8.03 (p=0.046 ) while the “effect” on math achievement goes from -6.08 (p=0.141) to -7.33 (0.080). Of course, these differences in the achiev ement and disciplinary behavior of these children whose parents filed for divorce canno t be a consequence of divorce since the parents did not in fact divorce. Again, this suggests that the correlations observed by comparing children whose parents divorced to children whose parent s did not are likely not the effects of divorce itself but rather of the underlying reasons that caused the parents to file for divorce.

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29 1.4.3 How Similar are Families That Experience Divorce to Those That Experienced a Dismissed Divorce? Since my primary identification strategy us es children whose parents file for and dismiss divorce cases as the “control” group against which to compare the children who experience parental divorce, it is important that I compare the characteristics of these two groups prior to the filing of the divorce cases. Table 13 presents desc riptive statistics for these two groups 0 to 3 years prior to filing the divorce in columns B and C. When a child was observed more than once in this time period, I calculated the average value of each variable from all observations of that child in that category. The numbers indicate that these two groups appear similar to each other among observable characteristics, with three exceptions. The first is that there are relatively more boys whose parents later filed and dismissed a divorce case (60.0%) than wh ose parents later divorced (47.3%). The second is that children whose parents later filed and dismisse d a divorce case tend to have more disciplinary problems than children whos e parents later divorced. The third is that children whose parents later filed and dismi ssed a divorce case are on average 1.6 years younger than children whose parents later di vorce. Despite the overall similarities between these two groups, to ensure that the results are not driven by unobserved differences between the two groups, I use indivi dual student fixed effects to control for any time-invariant differences in the fam ily backgrounds of these children. 1.4.4 The Effect of Parental Divorce on Family Income Before examining how parental divorce affects the academic achievement and disciplinary problems of children, it is benefici al to ensure that my data show what one would expect regarding the effect of parent al divorce on family income. Unfortunately, the only measure of family income recorded by the school district is school lunch status.

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30 Although there is a consensus that school lunch status is a good measure of family income for children in elementary school, the social stigma associated with free or reduced lunch for children in middle and high school that lowers take-up rates makes it much less reliable, particularly for my data set in which the vast majority of post-divorce observations are for middle and high school stud ents. This might especially be a concern if students whose parents divorced are particul arly unlikely to want to receive federally subsidized school lunch. For this reason a nd because only a small percentage of children are eligible for free or reduced lunches, I inst ead use the measure of family income at the zip code level, which has been used as a proxy for family income by others (e.g., Fryer and Levitt, 2004). The model estimated, which is the same as that estimated to determine the effect of parental divorce on test scores and disciplinary problems, was FamilyIncomeit = i + b0 Gradeit + b1 Grade2 it + b2 Yeart + b3 PostDivorceCaseit + b4 PostDivorceCaseit*Divorceit + b5 YearsAfterCaseClosureit +b6 YearsAfterCaseClosureit*Divorceit + it where FamilyIncomei is the median family income in the zip code of student i, i is a student fixed effect, Gradeit is the grade of student i at year t, and Yeart is a year fixed effect. The variable PostDivorceCase is a dummy variable equa l to one if the test was taken after the parental divor ce case was closed (whether du e to a judgment of dissolution or a dismissal) while the variable PostDivorceCase*Divorce is the interaction between PostDivorceCase and a dummy variable equal to one if the parents’ divorce case ended in divorce (as opposed to a dism issal). The variable YearsAfterCaseClosure is the number of years after the divorce case was closed (i ncluding dismissed cases) while the variable YearsAfterCaseClosure*Divorce is the interaction between the number of years after the

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31 divorce case was closed and a dum my variable equal to one if the divorce case ended in a judgment of divorce. The results are given in Tabl e 14 and indicate that every year after the divorce, the family income of children whose parents divor ce falls by $288 for every year afterwards (p=0.465). Six years after the divorce case ende d, average zip code family income fell by $1,223 relative to their dismissed divorce counte rparts, although that is not sta tistically significant at the 10% level. Still, this resu lt is comforting to the extent that one would expect children whose parents divorce to m ove to lower-income neighborhoods relative to children whose parents dismissed divorce cases. 1.4.5 The Pre-Divorce Trends of Children Whose Parents Later File for Divorce One might also be concerned that the student fixed effects approach may be insufficient if the pre-divorce trends of these two groups are diffe rent. In order to test whether there is a statistical difference be tween the pre-divorce trends of these two groups, I estimated the following equation similar to that which will be estimated to find the effects of divorce Outcomeit = i + b0 Gradeit + b1 Grade2 it +b2 Yeart + b3 PreDivorceCaseit + b4 PreDivorceCaseit*Divorceit + b5 YearsBeforeFilingit + b6 YearsBeforeFilingit*Divorceit + where Outcomeit is the outcome variable for student i at time t, i is a student fixed effect, Grade is the student’s grade, and Year is a student fixed effect. The variable PreDivorceCase is a dummy variable equal to one if the observation is prior to filing a divorce case, while PreDivorceCaseit*Divorce is a dummy variable equal to one only if the observation was for a child whose parents would later file a divorce case and get divorced. The variable YearsBeforeFiling is the number of years prior to filing a divorce

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32 case, while the variable YearsBeforeFilingit*Divorce is equal to the number of years prior to filing a divorce case that would end in divorce. The coefficient of interest is thus b6, which essentially captures the difference in the pre-divorce trends of children whose parent s would file for and then dismiss a divorce case relative to those of children whos e parents would later divorce. If b6<0, it means that as one goes back in time from the tim e of the divorce, childr en whose parents later divorce get worse off relative to those who will experience a dismissed parental divorce. Equivalently (and perhaps more intuitively), to the extent that b6<0, it implies that as the time of the divorce filing approaches, the di vorce group is gaini ng relative to the dismissal group. Conversely, to the extent that b6>0, as the time of the divorce filing approaches, the divorce group is droppi ng relative to the dismissal group. The equation was estimated on a sample that excluded observations more than 3 years prior to the filing of the divorce in an attempt to capture trend differences that occur relatively close to the decision to file for divorce. The results given in Table 15 show that for neither test scores nor disciplinary problems was there a statistically significant difference in the trends of these two groups prior to divorce.14 1.4.6 The Causal Time-Invariant Effect of Parental Divorce I now turn to the main question of how these outcomes compare after the divorce case has closed. By comparing the outcomes of children whose parents divorced to those of children whose parents filed divorce cases th at were later dismissed, I can effectively 14 When observations that occurred more than 3 y ears prior to the divorce filing are included, the differences between the pre-divorce tr ends in reading and math scores as well as days suspended remain statistically insignificant. However, there is a statis tically significant difference in the pre-divorce trends for the number of disciplinary infractions, suggestin g that as the time of divorce approaches, children whose parents later dismiss a divorce case commit 0.09 more infractions per year (p=0.095) than are children whose parents later divorce.

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33 separate out the effect of the divorce itself from the effects of the underlying causes of the divorce. First I examine whether or not experiencing parental divorce has a timeinvariant effect on student test scores and disciplinary prob lems. The regression equation estimated in order to address these issues was Outcomeit = i + b0 Gradeit + b1 Grade2 it + b2 Yeart + b3 PostDivorceCaseit + b4 PostDivorceCaseit*Divorceit + it. The variable PostDivorceCase is a dummy variable equal to one if the test was taken after the parental divor ce case was closed (whether du e to a judgment of dissolution or a dismissal) while the variable PostDivorceCase*Divorce is the interaction between PostDivorceCase and a dummy variable equal to one if the parents’ divorce case ended in divorce (as opposed to a dismissal) The standard errors used to calculate the p-values reported in the tables were cluste red at the family-year level. The coefficient of interest in this equation is b3, which effectively captures the effect of having experienced a parental di vorce relative to having experienced the dismissal of a parental divorce case. The resu lts given in 16 indicate that parental divorce does not have a statistically significant effect on reading or math test scores. Finally, the results suggest that parental divorce causes children to be suspended 0.75 more days per year and to commit 0.33 more disciplinary infractions per year, both of which are statistically significant at the 5% level. 1.4.7 The Causal Effects of Parental Divorce Over Time It may be, however, that the effect of pare ntal divorce is a cumulative effect that increases over time. My data allow me to examine how the outcomes of these two groups change over time and whether or not they diverge from each other. The regression equation estimated to address these issues was

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34 Outcomeit = i + b0 Gradeit + b1 Grade2 it + b2 Yeart + b3 PostDivorceCaseit + b4 PostDivorceCaseit*Divorceit + b5 YearsAfterCaseClosureit + b6 YearsAfterCaseClosureit*Divorceit + it. The variable YearsAfterCaseClosure is the number of years after the divorce case was closed (including dismisse d cases) while the variable YearsAfterCaseClosure*Divorce is the interaction between the number of years after the divorce case was closed and a dum my variable equal to one if the divorce case ended in a judgment of divorce. The coefficients of interest are b3 and b5, which estimate the time-invariant effect of parental divorce and the time-varying effect of parental divor ce, respectively. By utilizing data on children whose parents f iled for but dismissed divorce cases, both coefficients capture the effect of parental divorce relative to the effect of dismissed divorce. The estimated coefficients are given in the first several columns of Table 17, while the estimated effects of divorce after 1, 2, 4, and 6 years are calculated in the last 4 columns. The effect of parental divorce on reading and math scor es after 6 years is positive at 3.98 and 5.01 percentile points, re spectively, although neither effect is statistically significant at the 10% level. The results also show that although there is an initial statisti cally significant spike in disciplinary problems immediately after the divorce, parental divorce causes a reduction in disciplinary problem s after 6 years. For example, a student who experienced parental divorce gets suspended 2.13 more da ys per year thereafter but gets suspended 0.58 fewer days for every year after the divorce both of which are st atistically significant

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35 at the 1% level. The net effect is that 1 year after the divorce was finalized, parental divorce causes statistically significant increases of 0.67 infractions and 1.56 days suspended per year, while there is no statistica lly significant effect after 4 years. After 6 years the student who experienced divorce is suspended 1.32 fewer days on average than the student whose parents dismissed the divo rce case, an effect that is not quite statistically significant at the 10% level. These results sugge st that although experiencing a parental divorce causes more disciplinary problems for childr en in the short term, after an initial adjustment period ch ildren are no worse off and perhaps better off in terms of disciplinary problems at school as a consequence of the divorce. Given that the sample size here is relativel y small, as a sensitivity check I examined whether the results were changed when a ny given divorce case was excluded from the sample. For the case of the disciplinary re sults, although the magnitude of the effect on days suspended and disciplinary infractions after 6 years when any given divorce case is dropped is never closer to zero than -0.56 a nd -0.29, respectively. Consequently, while it seems likely that parental divorce causes a s hort-lived initial increase in disciplinary problems, the notion that disciplinary problem s for children overall are reduced in the long term is less certain. 1.4.8 Are the Effects of Parental Divorce Different for Boys than for Girls? It may be, however, that the consequences of parental divorce are different for boys than for girls. In order to address that que stion, the regression e quations were estimated separately for boys and for girls. The results are shown in Table 18. The most striking result is that the effect of parental divorce on reading test scores is very different for boys than for girls. Although the effect for boys after 6 years is a statistically insignificant -2.75 percentile points, girls score a statistically significant and

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36 large 14.68 percentile points higher on reading as a result of pare ntal divorce. Again, due to the small sample size I examined the extent to which these results were sensitive to any given divorce case. Although dropping any one divorce case does not cause the effect for the girls to be lower than 12.45 percentile points (p=0.018), the results for the boys are more sensitive. For the boys, dropping one divorce case can cause th e results to range from -0.08 after 6 years to -5.26 (p=0.093) after 2 years.15 Consequently, while the estimates show that daughters typically thrive in terms of reading comprehension as a result of divorce, there is only weak eviden ce to suggest that the reading scores of boys are affected in a negative way. The effect of divorce on the mathematics te st scores of girls was estimated as 6.68 percentile points afte r 6 years, although it is not st atistically significant (p=0.279). Dropping any one divorce case caused the effect for girls to range from 14.03 percentile points (p=0.016) to 2.16 percentile points (p=0.743), while the result for the boys ranged from 0.89 to 7.18 (p=0.328). The results also show that although both boys and girls appear to have more disciplinary problems immediately following the divorce, the effect for boys is larger. For example, the effect of parental di vorce on days suspended and disciplinary infractions for boys after one year is 2.27 days and 1.04 infractions, both of which are statistically significant. However, after 46 years, there is no st atistically significant effect for boys. Girls, while experiencing a smaller initial incr ease in disciplinary problems immediately following the divorce, if anything they appear to benefit from the parental divorce in the long term by committing 0.73 fewer infractions and being 15 The effect after six years in that case is -6.4 7 percentile points and has a p-value of 0.204.

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37 suspended 1.67 fewer days 6 years after the divorce, although neith er is statistically significant at the 10% level. 1.4.9 Does the Effect of Parental Divorce Depend on the Age of the Student at the Time of Divorce? It is also possible that th e effect of parental divorc e on a child depends on how old the child was at the time the parents filed for divorce. In order to examine that possibility, I included a variable equal to the grade of the student at the time the divorce was filed for all observations after parents di vorced (or zero if there was no divorce). The third column from the right of Table 19 gives the estimated coefficient of this variable while the last two columns estimate the effect of parental divorce 4 years after the fact. The first of those columns does so for a parental divorce that occurred when the child was in the 1st grade while that second column estim ates the effect of a divorce that occurred when the child was in the 6th grade. The results suggest that any age effects are small, at best, as the coefficient on the grad e-divorce interaction is never statistically significant at the 10% level. This suggests that a lthough the age of the student at the time of the divorce does not seem to be an important factor in the effect of divorce, at least for the range of ages examin ed in this paper. 1.5 Robustness of Results A frequent concern regarding st udies that utilize relatively small data sets is that the results may be driven by a small number of ou tliers. In order to address the concern that a subset of dismissed divorce cases is in fact driving my result, I es timated the effects of parental divorce again after making f our adjustments to the data set: Excluding dismissed divorce cases in wh ich at least one parent’s name was changed or dropped in the school district records. These cases were dropped due to the concern that the dropping or change of a parent name in a family not observed

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38 to experience divorce may be correlated with negative family unobserved characteristics. Excluding dismissed divorce cases in whic h a motion for default was entered. A motion for default is entered by a petitioner so that he or she can proceed with the divorce without the other spouse being present. As near as I can tell, however, the other spouse did eventually respond in court in all of the cases in my data. Still, one might be concerned that such a mo tion may be correlated with negative unobserved family characteristics. Including all children whose parents were married but did not file for divorce. Although the results are identified by co mparing the dismissed divorce group to the divorce group, these children were included to ensure th at their absence did not influence the results.16 Excluding all observations more than 5 years after the divorce case was closed. As discussed earlier, although 4 shows that the rate of attrition in the data set is approximately equal for children whose pa rents divorce compared to those whose parents file for and dismiss a divorce case, more than five years after the case is closed there are relatively more observa tions for the dismissal group than the divorce group. To ensure that the results are not sensitive to observations more than five years after the case was close d, those observations were excluded. The results are shown in Tables 20 – 23. In row (a) of each table, the main result presented earlier from using the full data se t is presented for comparison purposes. The results for reading scores presented in Table 20 show that the positive and statistically significant effect of parental divorce on girls is indeed r obust to the changes mentioned above. Similarly, the result that there may be a small negative effect on the reading achievement of boys is also consistent.17 16 The main reason for including the children whose parents did not divorce, besides allowing the crosssectional comparisons presented earlier in the paper, was to help identify the year fixed effects and grade effects. 17 One might also be concerned that although the pre-divorce test scores of children whose parents later divorce are similar to those whose parents later file and dismiss a divorce case, there may be differences between the groups when they are separated by gender. To some extent, this seems to be the case; the predivorce average reading and math scores for girls in the divorce group are 7.4 and 4.9 percentile points lower than those of the girls in the dismissal group. In contrast, the pre-divorce average reading and math scores for boys in the divorce group are 5.4 and 7.8 percentile points higher than those of boys in the dismissal group. To the extent that one would expect students with higher (lower) percentile test scores to see future gains (declines) in their scores relative to their peers nationwide this would cause my results for

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39 Table 21 shows the sensitivity results for mathematics scores. Again, the results show that the effect estimated for girls is not affected much by the various groups discussed above, although the effect still never reaches the point of statistical significance. Similarly, the eff ect of parental divorce for 5th and 10th grade boys four years after their parents divorced is never observed to be negative. Table 22 shows the sensitivity results for days suspended per year. Consistent with the results presented earli er, after 4 years there does not appear to be a statistically significant effect of parental divorce on days suspended per year, with one exception. As shown in row (e), when all observations more than 5 years after the divorce case was closed were excluded, the eff ect of divorce on girls after f our years is a statistically significant 1.06 additional day suspension pe r year. However, this result should be interpreted with caution since relatively few girls get suspended and the sample gets quite small after the deletion of all observations mo re than 5 years after the closure of the divorce cases. Table 23 shows the results us ing the number of disciplinar y infractions per year as the outcome variable. Again, although there is consistency to the idea that parental divorce causes a temporary spike in disciplin ary problems—especially for boys—after 4 years the results are consistent in showing that there is not a statistically significant effect. girls to be a lower bound while suggesting that the true effect for boys is more negative than my estimations show. However, clearly all students with high (or low) percentile scores in the country cannot move up (or down) relative to their peers over time, so it’s unclear that this should be a concern at all.

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40 1.6 Conclusions Previous research has used the conditi onal outcomes of children from two-parent families as an estimate of the counterfactua l that would be observed if parents who divorced were instead to stay together for an exogenous reason. In this paper, I argue that the performance of children whose parents fi led for divorce but did not divorce is a much more realistic estimate of the appropriate c ounterfactual. Consequently, this paper has identified the effects of parental divo rce on student performance by comparing the outcomes of children who experienced parental divorce to those whose parents filed for divorce but did not divorce, conditional on student fixed effects. The results indicate that parental divorce does not negatively affect acad emic achievement. In contrast, I find that parental divorce positively affects the reading scores of girls in a statistically significant and robust way; six years after the fact, gi rls score 14.68 percentile points higher as a result of the parental divorce. There is al so somewhat weaker evidence to suggest that parental divorce positively affects the mathema tics scores of girls, especially those who are older at the time of the divorce. The evidence on the effect of parental divorce on the academic achievement of boys is somewhat less clear. Although I find some evidence that parental divorce negatively affects the reading achievement of boys, the effects are considerably smaller and are never statistically significant. I find no evidence th at the mathematics achievement of boys is affected in a negative way by parental divorce. I also show that although experiencing parental divorce may increase disciplinary problems for children overall in the short term I find little evidence that it does so after 4 to 6 years and find that it may even redu ce disciplinary problems in the long run. However, this result should be interpreted with caution since children whose parents later

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41 dismiss a divorce case tend to have more di sciplinary problems than children whose parents later divorce. Although the inclusion of student fixe d effects in the estimation and the fact that I found no stat istically significant different in the pre-divorce trends of the two groups in the three years prior to filing for divorce should reduce this problem, one might still be concerned that higher levels of disciplinary problems might be associated with higher future trends after the divorce, which would cause the estimated effects of parental divorce on disciplinary behavior to be biased downward. Collectively, these results suggest that chil dren overall are not harmed and that girls stand to benefit significantly from their pare nts ending a troubled ma rriage relative to the alternative. Although my data force me to remain agnostic regarding the exact mechanism through which this occurs, potential explanations consistent with my results include a reduction in parental c onflict after the divorce or the refocusing of parental time from the marriage to the children. These results differ significantly from those of previous research that has consistently found negative effects of parent al divorce. The difference between these results and the results in previous research is most likely a direct consequence of the respective identification strategies used. Indeed, I show in this paper that although there is a strong correlation between having experi enced a parental divor ce and having lower outcomes, there is an even stronger correla tion between having one’s parents file and dismiss a divorce case and having lower outco mes. This suggests that the worse outcomes observed after parental divorce are largely not a conseque nce of the divorce itself but rather of the underlying problems th at caused the couples to file for divorce. The appropriate conclusion is thus not that family problems do not negatively affect the

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42 achievement and behavior of children, but rath er that, conditional on having rather family problems significant enough for a parent to f ile for divorce, on average children overall are made no worse off by divorce and daughters ar e made significantly better off. Although this paper did not examine unila teral divorce laws directly, the findings presented here may shed some light on that po licy issue. The fact that I find no evidence that the academic achievement of children overall is negatively affected by parental divorce lends no support to th e notion that policy-makers should make divorce more difficult in order to make children better o ff. Furthermore, my finding that divorce has large positive effects on the academic achievement of girls 6 years after the divorce suggests that there may well be significant soci al costs associated with using divorce laws to make divorce more difficult when children are involved.

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43 Table 1-1: Matchable Divorces in Alachua County, Florida General Divorce Cases Only (excludes Simplified Dissolutions) Cases with unique husband-wife name combinations Cases assuming that children are involved in 54% of General Divorces Cases with children in grades 1-12 (12/18=66.67%) Cases with children in the public school system (given 10% private enrollment) Cases after excluding nonunique parent names in school file ( 10% ) 924886478319287258 863802433289260234 875816441294264238 876820443295266239 965900486324292262 900840454302272245 909843455303273246 974904488325293264 878816441294264238 868817441294265238 18017092615550 9,2128,6144,6523,1012,7912,512 Table 1-2: Families Matched to Unique Divorces YearMatchable divorces given nonunique names in school data Divorce cases matched to school names Divorce cases linked to at least one test score Children with test scores linked to a divorce 1993258955165 1994234684756 1995238785676 1996239614564 1997262706389 1998245585374 1999246625880 20002648375114 2001238696893 2002238666588 200350141425 Total2,512724595824

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44 Table 1-3: Families Matched to Unique Divorces SampleCases Ending in Divorce Matched to Student Records Cases Ending in Divorce Matched to Student Test Scores Dismissed Divorce Cases Matched to Student Records Dismissed Divorce Cases Matched to Student Test Scores (c) Both (a) and (b) 658542164132 69 658542 (a) All Cases Matched Using Unique Parent Names -(f) Same as (e), but excluding dismissed divorce cases matched to student records in which only one parent name was listed prior to the divorce 123 (d) Same as (c), but excluding dismissed divorce cases not explicitly known to be dismissed voluntarily 164 62351193 92 (b) All cases matched using student names and birth dates retrieved from all dismissed divorce cases filed from 1993 2003 00 (e) Same as (d), but excluding dismissed divorce cases in which one parent name was matched to a domestic violence case 132 99 131 542 658 623511 Table 1-4: Distribution of Observations of Students Matched to a Parental Divorce Case DataGroupTotalPost-Divorce1 3 Years3 5 Years5+ Years 872667 663314185 100%76.5% 76.0%36.0%21.2% 156114 1035341 100%73.1% 66.0%34.0%26.3% 690530 399226137 100%76.8% 57.8%32.8%19.9% 11190 644132 100%81.1% 57.7%36.9%28.8% All students Students observed with at least one test score Children who Experience Parental Divorce Children who Experience a Dismissed Parental Divorce Children who Experience Parental Divorce Children who Experience a Dismissed Parental Divorce Students Observed in Post-Divorce Time Periods

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45 Table 1-5: The Cross-Sectional Effects of Parental Divorce on Reading Test Scores Obs.Parents Divorced Prior to Test Divorceyears after divorce interaction Divorcegrade of student interaction Effect of divorce on 10th grader whose parents divorced 6 years p rio r 26,252-1.97 0.192 26,252 -2.19 0.099 -4.03 -0.791.23 -3.87 0.157 0.0570.030 0.059 18,976-0.78 0.582 -2.51-0.64 1.15 -1.79 0.4080.131 0.046 0.363 (b) Also includes race, sex, free lunch, zip code income, income squared, and year dummies (c) Same as (b), but also includes school dummy variables (a) includes year dummy variables and g rade Coefficients and estimates that are statistically significant at the 10% level are in bold. Each row represents a different regression. Test scores are percentile rankings in the Io wa Test of Basic Skills and the Stanford 9 (FCAT) achievement tests. The first row of each cell presents the estimated coefficient, while the second row contains p-va lues calculated using robust standard errors. Table 1-6: The Cross-Sectional Effects of Pa rental Divorce on Mathematics Test Scores Obs.Parents Divorced Prior to Test Divorceyears after divorce interaction Divorcegrade of student interaction Effect of divorce on 10th grader whose parents divorced 6 years p rio r 23,228-1.31 0.380 23,228-1.32 0.319 1.32 -1.26 0.25 -5.25 0.670 0.006 0.674 0.015 18,962-0.48 0.719 2.51 -1.25 0.17 -4.27 0.420 0.005 0.762 0.034 (a) includes year dummy variables and grade (b) Also includes race, sex, free lunch, zip code income, income squared, and year dummies Coefficients and estimates that are statistically significant at the 10% level are in bold. Each row represents a different regression. Test scores are percentile rankings in the Io wa Test of Basic Skills and the Stanford 9 (FCAT) achievement tests. The first row of each cell presents the estimated coefficient, while the second row contains p-va lues calculated using robust standard errors. (c) Same as (b), but also includes school dummy variables

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46 Table 1-7: The Cross-Sectional Effects of Pa rental Divorce on Days Suspended Per Year Obs.Parents Divorced Prior to Test Divorceyears after divorce interaction Divorcegrade of student interaction Effect of divorce on 10th grader whose parents divorced 6 years p rio r 60,196 0.79 0.001 60,196 0.72 0.001 0.15 0.16 0.02 1.16 0.553 0.053 0.791 0.004 19,8410.21 0.295 0.060.11-0.06 0.49 0.8390.2610.441 0.266 (a) includes year dummy variables and g rade Coefficients and estimates that are statistically significant at the 10% level are in bold. Each row represents a different regression. The first row of each cell presents the estimated coefficient, while the second row contains p -values calculated usin g robust standard errors. (c) Same as (b), but also includes school dummy variables (b) Also includes race, sex, free lunch, zip code income, income squared, and year dummies Table 1-8: The Cross-Sectional Effects of Pa rental Divorce on Disciplinary Infractions Per Year Obs.Parents Divorced Prior to Test Divorceyears after divorce interaction Divorcegrade of student interaction Effect of divorce on 10th grader whose parents divorced 6 years p rio r 60,196 0.39 0.004 60,196 0.35 0.005 0.280.07-0.03 0.54 0.1090.1510.333 0.016 19,8410.10 0.398 0.020.07-0.04 0.27 0.9000.1720.316 0.254 Coefficients and estimates that are statistically significant at the 10% level are in bold. Each row represents a different regression. The first row of each cell presents the estimated coefficient, while the second row contains p -values calculated usin g robust standard errors. (c) Same as (b), but also includes school dummy variables (b) Also includes race, sex, free lunch, zip code income, income squared, and year dummies (a) includes year dummy variables and g rade

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47 Table 1-9: The Cross-Sectional “Effects” of Dismissed Divorce on Reading Test Scores Obs.Parents dismissed case prior to test Dismissalyears after dismissal interaction Dismissalgrade of student interaction "Effect" of dismissal on 10th grader whose parents dismissed case 6 y ears p rior 23,305-3.33 0.362 23,305 -6.42 0.023 -7.53-0.731.60 -5.49 0.1780.3730.152 0.170 17,068-3.40 0.250 0.10 -1.76 1.48 -4.57 0.989 0.058 0.289 0.326 (c) Same as (b), but also includes school dummy variables Coefficients and estimates that are statistically significant at the 10% level are in bold. Each row represents a different regression. Test scores are percentile rankings in the Io wa Test of Basic Skills and the Stanford 9 (FCAT) achievement tests. The first row of each cell presents the estimated coefficient, while the second row contains p-va lues calculated using robust standard errors. (a) includes year dummy variables and g rade (b) Also includes race, sex, free lunch, zip code income, income squared, and year dummies

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48 Table 1-10: The Cross-Sectional “Effects” of Dismissed Divorce on Mathematics Test Scores Obs.Parents dismissed case prior to test Dismissalyears after dismissal interaction Dismissalgrade of student interaction "Effect" of dismissal on 10th grader whose parents dismissed case 6 y ears p rior 20,533-4.24 0.297 20,533-3.78 0.219 -1.79-1.401.03 -6.08 0.7650.1240.331 0.141 17,029-3.52 0.256 -3.51-1.071.68 -3.20 0.6300.2880.184 0.452 (c) Same as (b), but also includes school dummy variables Coefficients and estimates that are statistically significant at the 10% level are in bold. Each row represents a different regression. Test scores are percentile rankings in the Io wa Test of Basic Skills and the Stanford 9 (FCAT) achievement tests. The first row of each cell presents the estimated coefficient, while the second row contains p-va lues calculated using robust standard errors. (a) includes year dummy variables and g rade (b) Also includes race, sex, free lunch, zip code income, income squared, and year dummies

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49 Table 1-11: The Cross-Sectional “Effects” of Dismissed Divorce on Days Suspended Per Year Obs.Parents dismissed case prior to test Dismissalyears after dismissal interaction Dismissalgrade of student interaction "Effect" of dismissal on 10th grader whose parents dismissed case 6 y ears p rior 54,2250.52 0.214 54,2250.44 0.208 -1.930.66 0.04 2.20 0.0090.013 0.588 0.028 17,7980.99 0.127 -3.210.96 0.18 3.22 0.0190.017 0.309 0.033 (c) Same as (b), but also includes school dummy variables Coefficients and estimates that are statistically significant at the 10% level are in bold. Each row represents a different regression. The first row of each cell presents the estimated coefficient, while the second row contains p -values calculated usin g robust standard errors. (a) includes year dummy variables and g rade (b) Also includes race, sex, free lunch, zip code income, income squared, and year dummies Table 1-12: The Cross-Sectional “Effects” of Dismissed Divorce on Disciplinary Infractions Per Year Obs.Parents dismissed case prior to test Dismissalyears after dismissal interaction Dismissalgrade of student interaction "Effect" of dismissal on 10th grader whose parents dismissed case 6 y ears p rior 54,2250.45 0.181 54,2250.38 0.190 -0.53 0.33 -0.06 1.21 0.257 0.016 0.421 0.036 17,7980.73 0.129 -1.02 0.49 -0.07 1.64 0.143 0.021 0.440 0.051 (c) Same as (b), but also includes school dummy variables Coefficients and estimates that are statistically significant at the 10% level are in bold. Each row represents a different regression. The first row of each cell presents the estimated coefficient, while the second row contains p -values calculated usin g robust standard errors. (a) includes year dummy variables and g rade (b) Also includes race, sex, free lunch, zip code income, income squared, and year dummies

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50Table 1-13: Descriptive Statistics (A)(B) ( C ) ( D ) ( E ) ( D ) ( E ) -( Not Used in Anal y sis ) ( Used in Main Anal y sis ) ( Used in Main Anal y sis ) Children in 2000 whose parents I think are married but never filed for divorce (met conditions 1-3 in Section 3.5) Children in 2000 whose parents I think are married but never filed for divorcemore restrictive (met conditions 1-4 in Section 3.5) Children whose parents later file for a divorce case that was dismissed but for which the petitioner did not specifically request the dismissal Children whose parents later file for and specifically request the dismissal of a divorce case Children whose parents later file a divorce case that ends in divorce Difference between Column B and Column C Age10.311.9 -1.6 (4.3)(3.3) p=0.000 % Black28.414.5 54.718.219.6-1.5 (45.1)(35.2) (50.3)(38.9)(39.7)p=0.798 % Male50.151.4 49.160.047.3 12.7 (50.0)(50.0) (50.5)(49.4)(50.0) p=0.075 % Subsidized Lunch33.617.3 77.739.432.47.0 (47.2)(37.8) (40.4)(48.0)(44.8)p=0.279 % Disabled13.311.1 32.118.217.11.1 (34.0)(31.4) (47.1)(38.9)(37.7)p=0.845 % Gifted9.610.6 5.712.710.02.7 (29.5)(30.8) (23.3)(33.6)(30.1)p=0.539 45,92348,143 39,94445,88747,405-1,518 (12,407)(11,703) (11,409)(11,422)(12,707)p=0.399 21.8 17.7 37.136.421.5 14.9 ( 41.30 ) (38.1) (42.2)(43.3)(36.1) p=0.005 0.78 0.60 1.381.270.65 0.62 ( 2.50 ) (2.2) (2.16)(2.8)(1.8) p=0.023 1.02 0.76 1.361.890.83 1.06 ( 4.18 ) (3.5) (2.56)(5.2)(3.2) p=0.033 Reading Score58.464.1 33.357.358.4-1.1 (29.8)(28.1) (28.03)(29.1)(27.5)p=0.781 Math Score60.066.0 38.656.559.8-3.3 (29.4)(27.8) (27.58)(30.9)(28.1)p=0.459 If children are observed more than once in each category, the average was used. Standard errors are in parentheses. Differenc es reported may not be equal to differences in the numbers in the table due to rounding. Statistically signific ant differences at the 10% level are in bold. Average number of times disciplined per year Average number of days suspended per year Average Zip Code Median Family Income % Committed Disciplinary Infraction in a year

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51Table 1-14: Estimated Effects of Pa rental Divorce on Student Family In come Using Student Fixed Effects Outcome Post-Divorce Case (including dismissed cases) Post-Divorce Case Divorce (interaction) Years after Divorce Case (including dismissed cases) Years after Divorce Case Divorce (interaction, finalized divorces only) 1 Year2 Years4 Years6 Years -84508395-288219-69-646-1,223 0.9470.690.3230.4650 .8510.9540.6790.574 Zip Code Family Income Coefficients and estimates that are statistically significant at th e 10% level are in bold. Each regression includes student f ixed effects, grade, grade squared, and year dummy variables as covariates. Each row repr esents a different regression. Estimated coefficients are given in the first row of each cell while p-values are given in the second row. Independent VariableEffect of Divorce after: Dummy VariableYears After Variable

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52 Table 1-15: Estimated Pre-Divorce Trends Pre-Divorce Case (including dismissed cases) Pre-Divorce Case Divorce (interaction) Years before Divorce Case was filed (including dismissed cases) Years before Divorce Case Divorce (Difference in Pre Divorce Trends ) Difference in Pre-Divorce Trends Reject null hypothesis that both groups have the same predivorce trend? Readin g -2.521.321.030.160.16 0.5330.7510.6330.9430.943 Math -1.812.082.21-0.95-0.95 0.6550.6200.3570.7030.703 0.49-0.95 0.19-0.14-0.14 0.1610.013 0.1730.3410.341 0.30 -0.55 0.040.010.01 0.150 0.012 0.6780.8920.892 Each regression includes student fixed effects, grade, grade squared, and year dummy variables as covariates. Each row represents a different regression. Estimated coefficients are given in the first row of each cell while p-values are given in the second row. Observations more than 3 years prior to filing were excluded from the sample. Hypothesis Test Disciplinary Infractions Days Suspended Outcome Independent Variable Dummy VariableYears Before Variable Coefficient of Interest No No No No Table 1-16: Estimated Time-Invariant Effects of Parental Divorce on Student Test Scores and Behavior OutcomePost-Divorce Case (including dismissed cases ) Post-Divorce Case Divorce ( interaction ) Effect of Divorce Readin g Score 0.39-0.18-0.18 0.8800.9430.943 Mathematics Score -3.412.992.99 0.2420.3200.320 Days Suspended -0.560.750.75 0.0340.0080.008 Disciplinary Infractions -0.330.330.33 0.0420.0480.048 Each regression includes student fixed effects, grade, grade squared, and year dummy variables as covariates. Each row represents a different regression. Estimated coefficients are given in the first row of each cell while p-values are given in the second row.

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53 Table 1-17: Estimated Effects of Parental Di vorce on Student Test Scores and Behavior Outcome Post-Divorce Case (including dismissed cases) Post-Divorce Case Divorce (interaction) Years after Divorce Case (including dismissed cases) Years after Divorce Case Divorce (interaction, finalized divorces onl y) 1 Year 2 Years 4 Years 6 Years Readin g 1.73-1.62-0.150.93-0.680.252.113.98 0.5250.5670.8310.1760.7950.9250.4980.324 Math -2.692.35-0.010.442.803.244.135.01 0.3760.4550.9920.6050.3510.2940.2860.328 -1.862.130.62-0.581.560.98 -0.17-1.32 0.0000.0000.0030.0050.0000.001 0.7170.110 -0.880.920.25-0.250.670.43 -0.07-0.56 0.0030.0030.0220.0260.0020.011 0.7840.202 Coefficients and estimates that are statistically significant at the 10% level are in bold. Each regression includes student fixed effects, grade, grade squared, and year dummy variables as covariates Each row represents a different regression. Estimated coefficients are given in the first row of each cell while p-values are given in the second row. Test scores are percentile rankings on the Iowa Test of Basic Skills and Stanford 9 Exams. Effect of Divorce after: Independent Variable Dummy VariableYears After Variable Days Suspended Disciplinary Infractions

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54 Table 1-18: Estimated Effects of Parental Di vorce on Student Test Scores and Behavior OutcomeSex PostDivorce Case (including dismissed cases ) PostDivorce Case Divorce (interaction) Years after Divorce Case (including dismissed cases ) Years after Divorce Case Divorce (interaction, finalized divorces onl y) 1 Year 2 Years 4 Years 6 Years Bo y s 3.82-3.730.010.16-3.57-3.41-3.08-2.75 0.2370.2770.9900.8670.2570.2800.4380.610 Girls -2.042.41-0.63 2.04 4.46 6.5010.5914.68 0.5690.5170.437 0.013 0.206 0.0640.0080.004 Bo y s -1.592.45-0.080.362.813.173.904.63 0.7070.5830.9450.7540.5070.4620.4620.506 Girls -4.352.56-0.260.693.243.945.316.68 0.1860.4590.8190.5430.3030.2240.2260.279 Boys -2.432.880.52-0.612.271.66 0.43-0.79 0.0000.0000.0620.0270.0000.000 0.4920.476 Girls-1.07 1.200.64-0.48 0.720.24-0.72-1.67 0.124 0.0950.0250.096 0.1460.5180.2750.154 Boys -1.281.31 0.22 -0.271.040.77 0.22-0.32 0.0010.002 0.146 0.0740.0010.001 0.4870.584 Girls-0.340.41 0.25 -0.190.220.03-0.35-0.73 0.3590.297 0.091 0.1930.4590.9130.3520.244 Reading Score Math Score Days Suspended Disciplinary Infractions Coefficients and estimates that are statistically significant at the 10% level are in bold. Each regression includes grade, grade squared, student fixed effects, and year dummy variables as covariates. Each row represents a different regression. Estimated coefficients are given in the first row of each cell while p-values are given in the second row. Test scores are percentile rankings on the Iowa Test of Basic Skills and Stanford 9 exams. Independent VariableEffect of Divorce after: Dummy VariableYears After Variable

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55Table 1-19: Estimated Effects of Parent al Divorce on Student Test Scores and BehaviorOutcomeSex Post-Divorce Case (including dismissed cases) Post-Divorce Case Divorce (interaction) Years after Divorce Case (including dismissed cases) Years after Divorce Case Divorce (interaction, finalized divorces only) Divorce Student Grade at Time of Divorce (finalized divorces only) Grade 1 Grade 6 Bo y s 3.81-3.410.010.15-0.06-2.87-3.19 0.2400.4320.9930.8790.9030.5000.438 Girls -1.951.10-0.59 2.09 0.26 9.7311.01 0.5870.8090.471 0.011 0.602 0.0290.007 Bo y s -1.602.48-0.080.36-0.013.933.90 0.7070.6550.9440.7540.9910.5050.464 Girls -4.190.05-0.200.730.453.425.67 0.2010.9910.8600.5190.3980.4770.199 Boys -2.391.950.54-0.57 0.16-0.160.63 0.0010.0430.0520.040 0.2060.8370.337 Girls-1.040.95 0.64 -0.470.04-0.87-0.68 0.1310.232 0.024 0.1070.3870.2000.303 Boys -1.271.09 0.22 -0.26 0.040.080.27 0.0010.025 0.138 0.084 0.4970.8250.410 Girls-0.340.41 0.25 -0.190.00-0.35-0.35 0.3600.359 0.092 0.1930.9960.3900.350 (d) Disciplinary Infractions Child Grade at Filing (a) Reading Score (b) Math Score (c) Days Suspended Coefficients and estimates that are statistically significant at the 10% level are in bold. Each regression includes grade, gr ade squared, student fixed effects, and year dummy variables as covariates. Each row represents a different regres sion. Estimated coefficients are given in the first row of eac h cell while p-values are given in the second row. Effect after 4 Years Dummy VariableYears After Variable Independent Variable

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56Table 1-20: Estimated Effects of Parental Divorce on Student Reading Test Scores RestrictionsSex Grade Interaction Post-Divorce Case (including dismissed cases) Post-Divorce Case Divorce (interaction) Years after Divorce Case (including dismissed cases) Years after Divorce Case Divorce (interaction, finalized divorces only) Divorce Student Grade at Time of Divorce (finalized divorces only) Grade 1Grade 6 Bo y s 3.81-3.410.010.15-0.06-2.87-3.19 0.2400.4320.9930.8790.9030.5000.438 Girls -1.951.10-0.59 2.09 0.26 9.7311.01 0.5870.8090.471 0.011 0.602 0.0290.007 Bo y s 4.14-3.820.030.17-0.05-3.20-3.43 0.2180.3860.9770.8740.9310.4640.420 Girls -1.891.09-0.63 2.13 0.25 9.8811.11 0.5980.8100.437 0.010 0.614 0.0270.006 Boys4.84-4.31-0.110.26-0.09-3.33-3.76 0.1730.3470.9160.8000.8700.4630.396 Girls-2.131.340.59 2.09 0.24 9.9611.18 0.5680.7730.469 0.012 0.617 0.0270.007 Boys3.740.240.67-0.41-0.58-1.97-4.86 0.3000.9580.5130.7080.2630.6800.282 Girls-2.893.34 -1.282.00 -0.20 11.1910.21 0.4350.470 0.0860.018 0.692 0.0150.016 Boys5.21-4.70-0.841.24-0.25-0.01-1.27 0.1450.3170.5760.4280.6410.9980.811 Girls-0.940.78-1.27 2.54 0.17 11.1111.96 0.8020.8700.161 0.011 0.736 0.0150.004 Independent VariableEffect after 4 Years Dummy VariableYears After VariableStudent Grade at Filing (a) None; Same data and specification as row (a) of Table 15 (b) Excludes dismissed divorce cases in which at least one parent's name was changed or dropped (c) Excludes dismissed divorce cases in which a motion for default was filed (d) Includes all children whose parents did not file for divorce (e) Excludes all observations more than 5 years after the divorce case was closed Coefficients and estimates that are statistically significant at the 10% level are in bold. Each regression includes grade, gr ade squared, student fixed effects, and year dummy variables as covariates. Each row represents a different regression. Estimated coefficients are given in the first row of each cell whi le p-values are given in the second row.

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57Table 1-21: Estimated Effects of Parental Divorce on Student Mathematics Test Scores RestrictionsSex Grade Interaction Post-Divorce Case (including dismissed cases) Post-Divorce Case Divorce (interaction) Years after Divorce Case (including dismissed cases) Years after Divorce Case Divorce (interaction, finalized divorces only) Divorce Student Grade at Time of Divorce (finalized divorces only) Grade 1Grade 6 Bo y s -1.602.48-0.080.36-0.013.933.90 0.7070.6550.9440.7540.9910.5050.464 Girls -4.190.05-0.200.730.453.425.67 0.2010.9910.8600.5190.3980.4770.199 Bo y s -2.303.02-0.050.340.024.424.52 0.6150.6000.9660.7740.9740.4700.419 Girls -4.190.07-0.230.750.443.505.72 0.2010.9870.8430.5110.4050.4670.195 Boys0.310.100.160.240.091.151.59 0.9450.9850.9000.8530.8770.8510.780 Girls-4.420.25-0.280.790.453.876.11 0.1950.9580.8140.5040.3990.4300.178 Boys-2.731.66-0.660.410.133.444.07 0.5430.7680.5710.7420.8320.5850.485 Girls-4.532.11-0.030.570.214.595.62 0.1970.6560.9770.6440.6960.3850.241 Boys-2.342.030.090.77-0.065.064.79 0.6100.7290.9620.6780.9240.4960.490 Girls-3.620.34-0.620.580.453.095.33 0.2890.9420.6520.6770.4190.5760.280 Coefficients and estimates that are statistically significant at the 10% level are in bold. Each regression includes grade, gr ade squared, student fixed effects, and year dummy variables as covariates. Each row represents a different regression. Estimated coefficients are given in the first row of each cell whi le p-values are given in the second row. (b) Excludes dismissed divorce cases in which at least one parent's name was changed or dropped (c) Excludes dismissed divorce cases in which a motion for default was filed (d) Includes all children whose parents did not file for divorce Effect after 4 Years (e) Excludes all observations more than 5 years after the divorce case was closed Independent Variable Dummy VariableYears After VariableStudent Grade at Filing (a) None; Same data and specification as row (b) of Table 15

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58Table 1-22: Estimated Effects of Parent al Divorce on Days Suspended per Year RestrictionsSex Grade Interaction Post-Divorce Case (including dismissed cases) Post-Divorce Case Divorce (interaction) Years after Divorce Case (including dismissed cases) Years after Divorce Case Divorce (interaction, finalized divorces only) Divorce Student Grade at Time of Divorce (finalized divorces only) Grade 1Grade 6 Bo y s -2.391.950.54-0.57 0.16-0.160.63 0.0010.0430.0520.040 0.2060.8370.337 Girls -1.040.95 0.64 -0.470.04-0.87-0.68 0.1310.232 0.024 0.1070.3870.2000.303 Bo y s -1.881.910.50-0.51 0.11-0.010.53 0.0050.0440.0730.066 0.3870.9870.431 Girls -1.01 1.00 0.64-0.45 0.03-0.76-0.59 0.147 0.214 0.0250.125 0.4570.2750.380 Boys -2.552.590.82-0.83 0.11-0.61-0.05 0.0010.0140.0140.013 0.3820.4730.945 Girls-1.111.12 0.68 -0.480.03-0.78-0.63 0.1280.179 0.023 0.1120.4980.2890.381 Boys -2.272.020.61-0.59 0.15-0.180.57 0.0030.0370.0470.063 0.1760.8240.430 Girls-1.121.23 0.53 -0.44-0.01-0.56-0.61 0.1310.124 0.083 0.1570.7840.4580.402 Boys -1.51 1.560.33-0.250.050.600.87 0.002 0.0620.1490.3260.6780.4450.213 Girls0.44-0.35-0.14 0.36 -0.01 1.091.05 0.3240.5350.232 0.013 0.818 0.0020.002 Independent VariableEffect after 4 Years Dummy VariableYears After VariableStudent Grade at Filing (a) None; Same data and specification as row (c) of Table 15 (b) Excludes dismissed divorce cases in which at least one parent's name was changed or dropped (c) Excludes dismissed divorce cases in which a motion for default was filed (d) Includes all children whose parents did not file for divorce (e) Excludes all observations more than 5 years after the divorce case was closed Coefficients and estimates that are statistically significant at the 10% level are in bold. Each regression includes grade, gr ade squared, student fixed effects, and year dummy variables as covariates. Each row represents a different regression. Estimated coefficients are given in the first row of each cell whi le p-values are given in the second row.

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59Table 1-23: Estimated Effects of Parental Di vorce on Disciplinary Infractions per Year RestrictionsSex Grade Interaction Post-Divorce Case (including dismissed cases) Post-Divorce Case Divorce (interaction) Years after Divorce Case (including dismissed cases) Years after Divorce Case Divorce (interaction, finalized divorces only) Divorce Student Grade at Time of Divorce (finalized divorces only) Grade 1Grade 6 Bo y s -1.271.09 0.22 -0.26 0.040.080.27 0.0010.025 0.138 0.084 0.4970.8250.410 Girls -0.340.41 0.25 -0.190.00-0.35-0.35 0.3600.359 0.092 0.1930.9960.3900.350 Bo y s -0.991.07 0.16-0.190.010.320.38 0.0100.027 0.2770.2000.8390.4000.257 Girls -0.330.43 0.25-0.18 0.00-0.30-0.31 0.3890.330 0.0960.218 0.9290.4750.415 Boys -1.401.490.37-0.39 0.01-0.08-0.01 0.0020.0070.0410.029 0.8210.8540.970 Girls-0.380.480.20-0.130.00-0.05-0.06 0.3280.2870.1970.3860.9250.9100.873 Boys -1.151.04 0.27-0.270.040.030.25 0.0100.049 0.1040.1230.3830.9420.496 Girls-0.340.420.21-0.17-0.01-0.27-0.30 0.4020.3420.1710.2810.8090.5320.469 Boys -0.690.90 0.08-0.100.050.480.35 0.0260.034 0.4980.4530.2940.2060.298 Girls0.29-0.05-0.100.16-0.030.560.39 0.4890.9090.5340.3340.2300.1570.300 Dummy VariableYears After VariableStudent Grade at Filing (e) Excludes all observations more than 5 years after the divorce case was closed Coefficients and estimates that are statistically significant at the 10% level are in bold. Each regression includes grade, gr ade squared, student fixed effects, and year dummy variables as covariates. Each row represents a different regression. Estimated coefficients are given in the first row of each cell whi le p-values are given in the second row. (a) None; Same data and specification as row (d) of Table 15 (b) Excludes dismissed divorce cases in which at least one parent's name was changed or dropped (c) Excludes dismissed divorce cases in which a motion for default was filed (d) Includes all children whose parents did not file for divorce Independent VariableEffect after 4 Years

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60 CHAPTER 2 THE EFFECT OF ATTENDING THE FLAGSHIP STATE UNIVERSITY ON EARNINGS: A REGRESSION DISCONTINUITY APPROACH 2.1 Introduction The question of the extent to which atte nding a more selective college affects subsequent earnings is of inte rest for several reasons. In addition to being of obvious significance to the students and parents maki ng decisions regarding whether to incur costs associated with either getting admitted and/or attending a more selective university, it is also tied to the question regarding p eer effects in educa tion—whether attending college with more highly qualified students in creases learning and ultimately productivity in the labor force. The issue also raises policy questions, especially with respect to affirmative action in admissions policies at flagship state universities. In the pa st, flagship state universities have used such policies in or der to admit more black and Hispanic students. However, beginning in the 1990’s, these po licies were challenged both legally and politically. For example, between 1996 and 1998 Texas and California eliminated affirmative action in college and university admissions; Florida followed suit in 2000. Finally, in 2003 the Supreme Court ruled in Gratz v. Bollinger that the University of Michigan’s undergraduate admissions policy violated the E qual Protection Clause of the Fourteenth Amendment because it was not “narrowly tailore d to achieve [the university’s] asserted

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61 compelling interest in diversity.”12 In addition, states may well be interested in how large the flagship university should become. The empirical difficulty in estimating th e effect of university selectivity on earnings is that attendance at more selectiv e universities is like ly correlated with unobserved characteristics that themselves will affect future earnings. Such biases could arise for two reasons. First, bias could arise if certain student abilities or characteristics are observed by college admissi ons committees by examining the student’s applications but not by the econometrician. Second, bias could arise if, conditional on all observable student and family characteristics and admi ssion to the more selective university, the decision to attend that univ ersity is correlated with unobserved student or family characteristics that would themselves affect subsequent earnings. For example, if the student chooses to attend the more selective university because she is more motivated than an observationally equivalent student w ho chose to attend a less selective school, the effect of selectivity on earnings will be ove rstated. On the other hand, if the student chooses to attend the more selective univers ity because she received more need-based financial aid at the selective school relative to an observationally eq uivalent student who chose a less selective school, the effect of selectivity on earnings will likely be understated. Researchers have taken several approaches to answering this question. Black and Smith (2004) describe problems that can arise fo r much of this literat ure that relies on the 1 Taken from the majority opinion written by Chief Justice Rehnquist and accessed at http://www.supremecourtus.gov/opinions/02pdf/02-516.pdf 2 This is not to say that states may not legally engage in any affirmative action, however. Indeed, in the same ruling the court upheld the affirmative action practices of the University of Michigan Law School.

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62 assumption of “selection on observables.” Se veral other approaches have been used. Dale and Krueger (2002) compare the earnings of one group of students to another group who were accepted at similarly selective colleg es but who chose to attend less selective colleges and find that attending more selective colleges has a positive effect on earnings only for students from low-income families. Brewer, Eide, and Ehrenberg (1999) estimate the payoff by explicitly modeling high school students’ choice of college type and find significant returns to attending an elite private institution for all students. Behrman, Rozenzweig, and Taubman (1996) id entify the effect by comparing female twin pairs and find evidence of a positive payoff for attending Ph.D.-granting private universities with well-paid senior faculty; Lindahl and Regner (2005) use Swedish sibling data and show that cross-sectional estimate s of the selective college wage premium are twice the within-family estimat es. Finally, in a rela ted debate, Sander (2004) found negative effects of attending more selective law schools for black stude nt beneficiaries of affirmative action, a conclusion that has b een vigorously challenged by others (e.g., Ayres and Brooks, 2005). In contrast to previous research, this paper identifies the effect of school selectivity on earnings by comparing the ea rnings of those just below the cutoff for admission to the flagship state university to those of applicants who were barely above the cutoff for admission. To do so, we comb ined confidential ad ministrative records from a large flagship state uni versity with earnings records collected by the state through the Unemployment Insurance program. The unique data set used a llows this paper to make tw o primary contributions to the existing literature. First, by using the a pplication data from a large flagship state

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63 university, this paper addresses the question of how college selectivity affects earnings in the context in which the public policy decisi on is made. Indeed, although determining the effect of attending an elite private college over a less selective one is interesting for several reasons, the pub lic policy question is largely confined to the extent to which admission at flagship state universities aff ects the subsequent earnings of various subgroups. Second, because we have actual admissions data from the university, we can use a regression discontinuity design to detect whether or not th ere is a discontinuity in earnings at the point of the ad mission cutoff. In this way we estimate an “intent-to-treat” effect—that is, the effect of admission to the flagship state un iversity. Doing so overcomes any biases that might arise due to the correlation of the decision to enroll at the flagship university with other unobserved f actors that may themselves affect earnings, so long as the assumptions for the regr ession discontinuity design are met. By combining confidential admissions da ta from a large university to earnings records collected by the state through the Unemployment Insurance program, we find suggestive evidence of positive discontinuitie s in the earnings of white men that correspond to 1% 27% higher earnings as a re sult of being admitted to the state flagship university, the magnitude and st atistical significance of wh ich depends largely on model specification. Furthermore, although there does not appear to be a consistent earnings effect for women overall, we do find that there is a positive fl agship earnings effect for the subset of women with strong attachment to the labor force. Finally, we find no evidence that admission to the flagship causes applicants to be more or less likely to be observed in the labor force 10 – 15 years later.

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64 2.2 Data The data used in this study are fr om two sources. First, we acquired administrative data on admissions from a large fl agship state universit y. As part of the agreement in acquiring the data, we agreed no t to disclose the name of the institution involved. The university was able to retrieve the following information for every student that applied for admission to the university from 1986 – 1989: Social Security Number, race, sex, term for which the student was a pplying for admission, ACT score, SAT math score, SAT verbal score, whether or not the student subsequently en rolled, year of birth, and whether or not the student subsequently graduated from the university. Finally, we also observe each student’s high school GPA, a discrete (to the nearest tenth of a point) number recalculated by the university after excluding certain courses and adjusting for different scales used by high schools. These data were then sent to a state office to which employers submit Unemployment Insurance tax reports. Usi ng the provided Social Security Numbers, quarterly earnings records from 1998 thr ough the second quarter of 2005 were matched to the university records. All nominal wage s were adjusted using the CPI so as to be measured in 2005 dollars. One advantage of these earnings data is th at they allow us to look at earnings well after nearly all applicants have completed th eir educations. The primary results in the paper are based on earnings observed 15 years after high school graduation—or when the individual is approximately 33 years old. These earnings are much more likely to be predictive of lifetime earnings than are earnings observed fo r people in their early and mid-twenties who are still finishing their edu cations and sorting themselves in the job market.

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65 Another advantage of these administrative da ta over survey data is that they likely contain less measurement error. A limitati on, however, relates to the fact that an individual’s earnings w ill not be observed if he or she is employed in a job not covered by the UI system or has moved out of state. The latter of these may be a particularly significant concern to the extent that working in state is endogenous to whether or not the student was admitted to the flagship state univ ersity. Fortunately, the data also allow us to examine if there is a discontinuity in wh ether or not an applicant is observed with earnings. There were 38,719 high school graduate s who applied for admission in the summer or fall of the 1985-86, 1986-87, 1987-8 8, 1988-89, or 1989-90 school years. Of those, there were 7,024 for whom we did not observe either a high school GPA or an ACT or SAT score. In addition, 992 applican ts were excluded because their high school GPA was lower than 2.0 or higher than 4.0. Two hundred fourteen more applicants were excluded because they cancelled their appl ication prior to the admission decision. Finally, 1,674 applicants were deleted becau se they did not meet the minimum GPA required for admission in that term/year.3 Thus, the final data set contains observations on 28,815 applicants. 2.3 Identification Strategy This paper uses a regression discontinuity design to estimate the causal effect of admission at a state’s flagship university on earnings. This design will distinguish the effect of admission to the flagship univers ity from other confounding factors so long as the unobservable determinants of earnings (e.g. motivation, parental support, etc.) are 3 In some of the years, a 2.0 was the minimum GPA required. Later on, however, this minimum was increased and there was no SAT scor e observed that would ensure admission for someone with that GPA.

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66 continuous at the admission cutoff. As l ong as this condition hol ds, any discontinuous jump in earnings at the admission cutoff is pr operly interpreted as the causal effect of admission to the flagship university on earnings. This condition will fail in this context if either applicants or the university can manipulate the side of the cutoff on which appli cants fall. For applicants, this would be a problem if those who would barely miss the cutoff were to retake the SAT until they surpassed the cutoff. In reality, such a scenario is unlikely for the simple reason that the admission rule was never published or reve aled by the university and, in fact, was changed from year to year. Consequently, it is very unlikely that the applicant would know, prior to applying, whether or not she was just above the cutoff or just below it. Furthermore, although there was an appeals pr ocess for rejected applicants, it affected relatively few students and was described by one admissions officer on the committee at the time as “very noisy”. Applying a regression discontinuity design in this context is somewhat different, however. The reason is that the admission cuto ff rule is two dimensional rather than one dimensional since it depends on both the SA T score and the high school GPA and took the form of a nonlinear slidi ng scale. To address this issue and convert the twodimensional sliding scale rule into a one-dim ensional rule, we created an adjusted SAT score for each student. We did so by subt racting the SAT score required for admission, given the student’s high school GPA, from each student’s actual SAT score. For example, if an SAT score of 1100 was neces sary for admission given a student’s high school GPA and that student scored an 1150 on the SAT, that student was assigned a score of 50. As a result, all students assigned scores of 0 or higher were predicted to be

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67 accepted to the flagship university. In case st udents with similar adjusted SAT scores have different earnings potenti als, we directly control for actual SAT and high school GPA when estimating the earnings effects. One approach to estimate the discontinuity at the cutoff is to compare the earnings of those who barely were admitted (e.g., those with adjusted SAT scores of 0 or 10) to those who were barely rejected (e.g., those which adjusted SA T scores of -20 or -10). However, if earnings increase with adjusted SAT scores as is likely the case, this will overstate the effect of admission to th e flagship university on earnings. The alternative approach is to estimate an equation for the outcome as a function of the adjusted SAT score. Specifically, we estimate the following equation using least squares regression: Outcomei = 0 + + 1X + 2( Admiti) + (f( Adjusted SAT Scorei)) + i where Admiti =1 if ( Adjusted SAT Scorei) > 0, f( Adjusted SAT Scorei) is a flexible polynomial function of the adjusted SAT score, and X is a vector of control variables, which included year-by-term of admission dummies, actual SAT score and high school grade point average.4 I then estimate this equation using various functions f(). 2.4 The Admission Rule 2.4.1 Estimating the Admission Rule Because the admissions records are nearly 20 years old, the university did not have records of the exact rules us ed to determine admissions. During the time in question, however, admissions decisions we re made using a discrete sliding scale of high school 4 By controlling directly for SAT score and high schoo l GPA, we control for th e fact that the earnings ability of an individual with a high SAT score and lo w GPA may be different from that of an individual with a high GPA and a low SAT score, even if both have the same adjusted SAT score.

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68 GPA (as adjusted by the univers ity to account for course cont ent and differences in high school GPA scales) and SAT score.5 That is, for a given high school GPA, the student was admitted if her SAT score met or exceeded the cutoff SAT score. Higher high school GPAs implied lower minimum SAT scores necessary for admission. For example, to compensate for a high school GPA that was one tenth of a point lower, a student may have to have an SAT scor e that is 20 points higher.6 In order to estimate the admission cutoff, the data were first partitioned by race and term of application (either summer or fall). The data were then partitioned further by high school GPA, after which the following eq uation was estimated using Ordinary Least Squares: Acceptance = 0 + 1(SAT_Cutoff) + where Acceptance is a dummy variable equal to one if the student was accepted and SAT_Cutoff was a dummy variable equal to one if the SAT score was greater than or equal to a given SAT score. For example, the SAT cutoff for the fall of 1986 for white males with a high school GPA of 3.5 was determined by estima ting this equation separately using all possible SAT scores (e.g., from 800 to 1400) as the cutoff. The SAT score that resulted in the estimation with the highest R2 was the cutoff that was then used.7 This process was 5 For some students, ACT scores were used instead. In those cases, we converted these to equivalent SAT scores using the university formula. 6 To assure the confidentiality of the university that provided the data, we cannot reveal the admission standards as we estimated them. However, we can note that the tradeoff between SAT score and high school GPA was nonlinear. 7 The “winning” R2 was typically around 0.50.

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69 repeated for all cohorts. For example, it wa s repeated for the fall of 1986 for white males with a high school GPA of 3.6, and then 3.7, etc. 2.4.2 Does the Admission Cutoff Predict Which Students Are Accepted and Which Are Rejected? After estimating the admission cutoff, the obvious question is whether or not the probability of acceptance at the university is discontinuous at the admission cutoff. This can be seen in Figure 1, which shows the pr obability of being accepted (the outcome) on the vertical axis and the number of SAT points above or below the cutoff given the student’s high school GPA on the horizontal axis This figure takes the same form as others presented after it. The open circles re present local averages. For example, at an adjusted SAT score of zero (i.e., for student s who barely made the estimated admissions cutoff), the open circle is the percentage of those applicants who were accepted at the flagship. The estimates of the discontinuity show n in Figure 1 are reported in Table 1. Row (1) reports estimates of the discontinuity without controlling for either a function of the adjusted SAT score or the actual SAT sc ore and high school GPA. In contrast, the regression equations that yiel ded the discontinuity estimates reported in rows (2) – (4) included polynomials of order 3 or higher in the adjusted SAT score. For example, the equation estimated in row (2) includes the variables (Adjusted SA T Score), (Adjusted SAT Score)2, and (Adjusted SAT Score)3 as well as those same va riables interacted with a dummy equal to one if the applicant was predicted to have been admitted by the flagship (i.e., those for whom the Adjusted SAT Score > 0). Specificat ions (2) and (4) also control for each applicant’s actual SA T score and adjusted High School GPA.

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70 The results are consistent in showing th at there is a large and statistically significant discontinuity in the likelihood of acceptance at the admission cutoff on the order of 68 – 69 percentage points. For exampl e, in the preferred specification in row (4) that allows for fourth-order polynomials in Adjusted SAT Score on both sides of the admission cutoff, the estimated discontinuity is 68.6 percentage points, which is statistically significant at all traditional levels. Furthermor e, a look at the underlying data in Figure 1 shows that this di scontinuity is not simply the consequence of an incorrect functional form. 2.4.3 Potential Causes of the ‘Fuzziness’ of the Estimated Admission Discontinuity The fact that this estimated discontinuity is less than one means that this design utilizes a ‘fuzzy’ discontinuit y. Several factors may be res ponsible for this all of which must be considered when interpreting the re sults on earnings. First, a handful of high schools had reputations for giving lower grades than average. While this was not taken into account by the university in calculating adjusted high school grade point averages, it was something taken into account during the ad missions process. Other exceptions were made for student-athletes and perhaps for the occasional son or daughter of donors. This, however, does not invalidate the regression-disc ontinuity design. Rather, any estimate of the effect of admission on earnings will be valid only for those who are affected by the admission guideline. While this is the major ity of applicants, it would not include, for example, student-athletes or those who a ttended one of the handful of high schools treated differently by the admissions committ ee. Indeed, the discontinuity shown in Figure 1 shows clearly that the estimated ad mission rule was the defining factor in admissions for the majority of applicants.

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71 There are other sources of noise that may cause the estimated discontinuity in the probability of being admitted to be less than one. As in any process with human involvement, errors in either the decision-ma king process or the reporting process almost certainly exist to some degree. Even more significantly, in any give n term the university aimed to enroll a certain number of student s. Given uncertainty about yields, the university would often change the admission ru le slightly during th e process to accept more or fewer students, thereby intr oducing noise into the admission rule.8,9 Finally, and perhaps most importantly, given the presence of any noise in the admission process such as that caused the factors mentioned above, th e estimation of the rule is itself probably characterized by some degree of error, especial ly for cells in which there were relatively few observations. However, there are less innocuous explanati ons of why the estimated discontinuity is less than one. Perhaps the most problem atic of these would be that the university observes something about the student unobserved to the researcher, wh ich is the type of bias about which Dale and Krueger (2002) were primarily concerned. The best evidence against this possibility comes from the a pplication form itself, which reveals the information about the student that was disclose d to the university. Contrary to what one might expect based on the appl ication process for universitie s at the current time, the application in the late 1980’s was very simple. On it, students were required to include 8 According to one admission official who served in the late 1980’s, the university aimed to err on the side of a policy that was too low at first, then toughened it slightly if more students chose to attend than expected. In this way the university didn’t reject applicants who it wo uld have accepted had the university processed the application somewhat more quickly. 9 This noise will not bias the earnings estimates so long as the applicants who were admitted did not have different earnings potential relative to those with identical SAT and high school GPAs who were not admitted. This seems, at least to us, like a reason able assumption given the applicant and bureaucratic noise that determines the processing order of applications.

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72 their race, age, nation of birth, address, high school name and address, emergency contact information, planned major, and current se mester high school cour ses. In addition, applicants were asked if they were found guilty of any non-minor offenses or to have interfered with the operation of any educational institution. Each applicant was also asked whether family members attended the university. Finally, the applicant was required to have official hi gh school transcripts and an SA T or ACT score sent to the university. Notably absent from the require d application materials were letters of recommendation and essays. As stated earlier, of the information cont ained in the applicat ion, the only parts used in making the application decision we re the SAT score and the (adjusted) high school grade point average. More important however, is that the simplicity of the admission rule consisting of a sliding s cale using adjusted high school GPA and SAT score that the university asserts to have used in this time period is reflected in the application itself. As a result of the ‘fuzzy’ admissions cuto ff, all wage discontinuity estimates must be reweighted by the estimated admission di scontinuity in order to determine the treatment effect. 2.4.4 Do Applicants Who Just Meet the Admission Cutoff Subsequently Attend and Graduate from the Flagship State University? Although we estimate an intent-to-treat eff ect in order to avoid the selection bias that might arise from choosing whether to a ttend the flagship state university conditional on acceptance, clearly the receipt of an accep tance letter by itself could not affect earnings later on. Rather, the mechanism thr ough which the effect could occur would be attending the flagship university.

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73 The data show that there are large diffe rences in the likelihood of subsequent attendance of the flagship university between those who barely met the admission cutoff and those who barely missed it. For example, among those who just met the admission cutoff (those with adjusted SAT scores of 0) 51.0% of them subsequently attended the flagship university compared to 10.4 % of those students who missed the cutoff by 10 SAT points, given their high school GPA. Among those who met or exceed the admission cutoff by no more than 20 SAT points (again, conditional on high school GPA), 53.3% subsequently attended the flagsh ip university compared to only 11.5% of those who missed the cutoff by no more than 30 SAT points. As one might expect, there are also signi ficant differences in the likelihood of graduating from the flagship university. Only 7.2% of those with adjusted SAT scores of -10 subsequently graduate from the flagship university compared to 32.5% of those who barely were accepted and had adjusted SA T scores of 0. Similarly, only 8.0% of applicants who missed the cutoff by no more than 30 SAT points (conditional on high school GPA) graduated from the flagship, co mpared to 36.3% of those who exceeded the cutoff by no more than 20 SAT points. 2.4.5 Do Admitted Applicants above th e Admission Cutoff Enroll and Graduate from the Flagship at Different Rates th an Applicants Just Below the Cutoff? One test of whether applicants on either si de of the discontinuity are similar is to see if, conditional on acceptan ce (or enrollment), those who barely met the estimated admission cutoff were more or less likely to enroll (or graduate) than those barely missed the estimated cutoff.10 This can best be seen by Fi gures 2 and 3. Figure 1 shows the 10 Unfortunately, this is one of the only tests we can perf orm to see if students on either side of the cutoff were similar, since we were unable to get additional ba ckground information on the applicants. Later in the paper we will show that controlling for SAT score and adjusted high school GPA does not change the

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74 likelihood of choosing to enroll at the flag ship university, conditional on being accepted to the flagship university.11 Figure 2 shows the likelihood of graduating from the flagship university, conditional on enrolling at th e flagship university. To the extent that the graduation rates were discontinuous at the admission cutoff, one might be concerned that the groups on either si de of the admission cutoff were not in fact similar. There does appear to be a difference in the likelihood of enrolling at the flagship university, conditional on admission, at the admission cutoff, as shown by Figure 1. There does not, however, appear to be a di scontinuity in the likelihood of graduating from the flagship university, conditional on enrollment, as shown in Figure 2. Although the results on enrollment may raise some ques tions, the fact that the graduation rates are no different for those who barely exceeded the cutoff than those who barely missed it supports the assumption that those on either si de of the admission cutoff are very similar except for their likelihood of being admitted. 2.5 Attrition from the Earnings Data As discussed earlier, one drawback to using these state-level wage data is that some applicants may not be observed with positiv e earnings 10 15 years after high school graduation because they moved to a different st ate. To the extent that the probability of working in-state is endogenous to admission a nd attendance at the flagship university, the discontinuity estimates may be biased. The da ta allow us to examine the extent to which this is the case by comparing the probability of observing applican ts who were barely discontinuity estimates, which shows that, even on the margin, the university was not selecting high GPA (or high SAT) students among others with equivalent adjusted SAT scores. 11 Since there are relatively few students below the cuto ff who were admitted to the flagship (as shown in Figure 1), these data were restricted to those who mi ssed the cutoff by fewer than 100 points. There were 58 applicants who missed the cutoff by 10 SAT points but still were accepted; 42 of those students enrolled.

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75 accepted to that of observing the earnings of applicants who were barely rejected. Furthermore, we do so separately for men th an women due to the differences in their respective labor force participa tion rates. We also do so using two definitions of being observed with positive earnings. For ex ample, we examine whether there is a discontinuity in the likelihood of being observe d with 4 consecutive quarters of earnings in the 10th year after high school graduation as we ll as in the likelihood of being observed with any positive quarter of earnings in that year. 2.5.1 The Attrition of White Males The best evidence of whether there is a disc ontinuity in the attrition of men in the earnings data is visual. Sp ecifically, Figures 4a – 4i show the likelihood of being observed with 4 consecutive quarter s of earnings in each of the 7th – 15th years after high school graduation. Shown on each figure are the local averages as well as the predicted probability based on a cubic polynomial of adjusted SAT score on either side of the admission cutoff. These discontinuity estimat es are summarized in Table 2. Of the estimated discontinuities shown in Figures 4a – 4i, the estimated discontinuity is statistically significant at the 10% level only for 14 years (Figure 4h, estimate = 0.048, p=0.061). More importantly, perhaps, is that it is difficult to see a distinct discontinuity in the underlying data in a ny of the nine figures. Figures 5a – 5i show the likelihood of be ing observed with any positive earnings in the years following high school graduation, beginning in the 7th year when the applicants were approximately 25 years old. Here, none of the estimates is statis tically significant at the 10%, although the estimate for 11 years comes close (p = 0.105). Thus, of the eighteen estimations shown on the first two co lumns of Table 2 (and in Figures 4 and 5), only one estimate is statistically significant at the 5% level, which coincidentally is what

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76 one would expect by chance alone. In additi on, the underlying data shown in the figures hardly reveal compelling evidence of a discontin uity in any of the graphs. Consequently, it seems unlikely that the wage discontinuity estimates should be biased because those who were barely accepted at the flagship state university were more or less likely to show up in the earnings data 7 – 15 years after entering college. 2.5.2 The Attrition of White Females The story is remarkably similar for wh ite women. Figures 6a – 6i show the probability of being observed with 4 consecutive quarters of earnings 7 – 15 years after high school graduation. Similarl y, Figures 7a – 7i show the probability of being observed with any positive earnings 7 – 15 years after graduating from high school. Of all the discontinuity estimates from those graphs, onl y the discontinuity fo r being observed with any positive earnings after 9 years (Figure 7c, estimate = -0.067) was statistically significant at either the 10% or 5% level. Coincidentally, out of 18 estimates summarized in the last two columns of Table 2, one would expect roughly one sta tistically significant estimate by chance alone. And again, no compelling discontinuities seem evident in the underlying data graphed in Figures 6a – 6i and Figures 7a – 7i. 2.5.3 The Admission Discontinuity for Thos e Observed with Positive Earnings Even though there does not appear to be co mpelling evidence of attrition in the data caused by admission to the flagsh ip state university, since the wage estimate results are based on the sample of applicants observed with positive earnings, it is instructive to ensure that the admission disc ontinuity is also observed with this group. The underlying data and estimated admission discontinuity is shown on Figure 8a and 8b for that group of individuals for whom we observe 25 consecutive quarters of earnings in the 12th and 15th year following high school graduation, respectively. Fi gures 9a and 9b show the

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77 underlying data and regression discontinuity es timates for the applicants observed with any positive earnings in the 12th and 15th years following high school graduation, respectively. The result is clear, if unsurprising: There is still a statistically significant discontinuity of approximately 0.70 even for those who stayed in the sample and were observed with positive earnings 12 and 15 years after high school graduation. 2.6 The Effect of Admission at the Flagshi p University on Labor Market Outcomes 2.6.1 The Earnings of White Males Since the effect of attending a flagship state university may very well vary by race and sex, I first examine the effect of admission at the flagship university on the subsequent earnings of white males. To do s o, I used two definitions of earnings. The first was the natural log of the sum of four quarters of consecutive real earnings in the 10th – 15th years following high school graduatio n, or when the individuals were approximately 28 33 years old.12 Consequently, for those who applied for admission in the fall of 1986, I used earnings received from the 3rd quarter of 2001 through the 2nd quarter of 2002. Similarly, for those who app lied for admission in the fall of 1987, I used earnings received from the 3rd quarter of 2002 through the 2nd quarter of 2003, and so on. 12 The advantage of examining earnings in this time period was shown by Mincer (1974), who showed that the return to schooling can be underestimated if ear nings prior to the “year of overtaking” are used. Assuming that the cost of investment is constant over time, that year is equal to (1+1/r) years after the completion of formal education, where r is the intere st rate. Thus, assuming r=0.09 and an applicant finishes schooling at age 22, the year of overtaking is 22 + 12.1 = 34.1, which is approximately the age examined in this paper. This matters to the extent th at attending the flagship un iversity causes differences in post-schooling investment.

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78 The second measure of earnings is the natural log of the annualized average earnings in the four quarters of c onsecutive earnings in each of the 10th – 15th years following high school graduation.13 The results for the 10th – 15th years following high school graduation are shown in Figures 10a – 10f for the consecutive quarter earnings measure and in Figures 11a – 11f for the annualized earnings measure. Plo tted on each figure are the local averages for each adjusted SAT score along with two fitted lines. Since the underlying data appear— at least to us—to be linear in the adjusted SAT score, the first fitted line of predicted earnings is from an OLS regression in which we control for adjusted test score in a linear fashion allowing for a different slope on either side of the admission cutoff. The second fitted line of predicted earnings is from an OLS regression in which we control for a cubic polynomial of adjusted test score as well as a cubic interacted with a dummy variable equal to one for those with an adjust ed SAT score greater than or equal to 0. The discontinuity estimates from both approaches and for both measures of earnings are shown on the figures themselves as well as in Table 3. In the linear case, they range from 1% to 8%, which corresponds to an increase in wages due to admission at the flagship university on the order of 1.5% to 11%. However, only 4 of the 12 estimates are statistically significant at the 10% level, and only 2 of those are statistically significant at the 5% level. The linearity assumption in the functional fo rm is important, however, as is evident from the discontinuity estimates using the cubic functional form. Those discontinuity 13 It appears from the data that when positive earnings ar e observed in one quarter, they tend to be observed for many consecutive quarters. Still, to the extent that some individuals move out of (or in) state during, say, the 10th year after high school graduation, this second earnings measure will allow them to remain in the sample.

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79 estimates range from 0.123 to 0.193, which corresponds to an increase in wages due to admission at the flagship university on the order of 18% 28%. All but 3 of the 12 estimates shown in Figures 10a – 10f and Figur es 11a – 11f are statistically significant at the 5% level and all but 1 are statisti cally significant at the 10% level. This difference caused by the regression spec ification is largely driven by the fact that the earnings of those who just mi ssed the admission cutoff by 40 or fewer SAT points are lower than those of applicants who missed the cutoff by 50 – 70 points. The reason for this is not immediately clear; one w ould certainly expect earnings to rise as ability rises. One potential explanation is that those who barely were rejected still attended another 4-year univ ersity, while those who missed the cutoff by more either did not attend college or attended a community coll ege first. Consequently, those who just missed may have lower earnings because they have less work experience. However, this explanation is not entirely satisfactory both because one would expect college graduates to catch up with high school graduates by age 33. Furthermore, one would expect the difference to decline from age 28 – 33 as th e college graduates catch up on the earnings scale. It should be noted, however, that th is downward slope in th e fitted regression line cannot be driven by the selective admission of st udents on the left-hand side of the cutoff. Even if the university did selectively adm it students who just missed the cutoff on the basis of some unobserved (to us) factor that is correlated with highe r earnings potential, those admitted students remain on the left-hand side of the cutoff in the earnings graphs. Still, since the functional form assumptions do seem to be important, more sensitivity analysis will be performed later in the paper.

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80 One pattern that does become apparent from the discontinuity estimates is that they are quite similar across the two measures of earnings. For example, the discontinuity estimate using the linear functional form is 6.9% after 15 years for the measure that uses four consecutive quarters of ear nings and 6.3% using the annualized measure of earnings. 2.6.2 White Females 2.6.2.1 The effect of admission on subsequent earnings The underlying data and fitted regression lin es for women are shown in Figures 12a – 12f for the consecutive earnings measure and Figures 13a – 13f for the annualized earnings measure. The summary of the esti mates shown on these figures is given in Table 4. As shown there, the linear regres sion discontinuity estimat es on earnings 10 – 15 years after high school gradua tion for the two earnings m easures are all negative and range from -0.018 to -0.095, which implies a flag ship earnings effect of -2% to -13%. Only 3 of the 12 estimates are statistically significant at the 10% level, 2 of which are also statistically significa nt at the 5% level. However, once again there is significan t sensitivity to the functional form assumption used. Allowing for a cubic functiona l form of adjusted test score causes the regression discontinuity estimates to range from -0.108 to 0.136, although only 3 positive estimates are statistically significant at c onventional levels. The only statistically significant estimates are the estimates for the discontinuity in 4 c onsecutive quarters of earnings 11, 13, and 14 years after high sc hool graduation which range from 0.118 to 0.136. Once again, this difference in the disc ontinuity estimates appears to be driven largely by the fact that thos e who miss the admission cutoff by 20 or fewer points tend to have lower earnings than those who mi ssed the cutoff by 30 – 40 points, causing the cubic regression line to trend downward as it approaches the cutoff.

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81 There is also less consistency in the estim ates across the two measures of earnings, which could be a consequence of the fact th at women are more likely to work part-time or leave the labor force than are men. It does seem difficult, at least to us, to see any distinctive discontinuity in the underlying data themselves that are shown in Figures 12a – 12f and Figures 13a – 13f. Thus, it seems difficult to pin down the flagship university earnings effect for women. 2.6.2.2 The effect of admission on the labo r market attachment of white women It is possible that the wide range of es timated discontinuities in the earnings of women is due in part because women who ar e accepted at and subsequently attend the flagship state university are more or less likely to leave the la bor force. Such a difference could occur if the marriage market at the fl agship university differe d from that of the next-best-alternative university. To analyze this, we restrict the data to include only women for whom positive earnings are observed in the 15th year following high school graduation. We then examine the degree of labor force attachment by calculating the percentage of quarters in the 5 years prior to that in whic h the women were observed with positive earnings. The resulting outcome gives us a measure of labor force attachment for women from age 28 to age 33.14 The local averages of this measure of labor force participation are graphed in Figure 14. There is no discerni ble discontinuity in labor force participation at the admission cutoff, which is reassuring in that it suggests that the ea rnings estimates for 14 This age was chosen since by age 28 almost all women will have completed their educations. In addition, we include only those who are observed with earnings 15 years after high school graduation in order to distinguish labor force participation from the propensity to move out of state.

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82 women presented earlier are unlikely to have been driven by differences in labor force participation. 2.7 The Sensitivity of th e Earnings Estimates 2.7.1 White Men Given the sensitivity of the discontinuity estimates for white men to functional form, here I examine the sensitivity more fu lly to both functional form and specification. Since the results were very similar across bot h earnings measures, I only use the four consecutive quarter measure of earnings. Similarly, we only examine earnings 12 and 15 years after high school graduation. The results from these robustness checks are reported in Table 5. The first five rows examine the sensitivit y of the estimates to both the functional form of the adjusted SAT scor e and to the inclusion of cont rol variables. As for the latter, it is evident from comparing the estima tes in specification (1) to (2) and comparing specification (4) to (5) that the inclusion of control variables (year/term dummy variables and actual SAT score and GPA) does not a ffect the discontinuity estimates in a substantial way. This is consistent w ith the assumption underlying the regression discontinuity design that all other variable s that affect earnings (such as high school GPA) vary continuously at the admission cutoff. However, it is also clear that the choice of functional form of adjusted SAT score matters significantly. Specifically, the incl usion of a quadratic or higher order term allows the fitted regression line to slope dow nward as it approaches the admission cutoff from the left, as seen earlier in the earnings fi gures. This in turn results in estimates that are approximately twice as large as those resulting from the lin ear specification.

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83 In specifications number (6) and (7), th e sample is restricted to only those applicants who were observed with positive quarterly earnings in every quarter for 6 straight years st arting in the 10th year after high school graduation. Thus, these estimates can be interpreted as the flagship effect for those applicants who are particularly attached to the labor market. Although the estimates us ing the linear functional form are similar, the discontinuity estimates using a cubic f unctional form increase from approximately 0.08 to 0.25. Thus, although functional form matt ers here as well, if anything it appears that the flagship earnings effect is larger for applicants with a strong attachment to the (in-state) labor force. Specification (8) restricts the sample to only those applicants who missed or exceeded the admission cutoff by no more than 100 SAT points. As one might expect from looking at the data in Figures 10 a nd 11, the statistically significant regression discontinuity estimates of 0.167 and 0.157 are ve ry similar to those using a polynomial of order 2 or higher using the full data set. Finally, we examine the extent to which th ere is a discontinuity in earnings for the median earner in the sample. Here, the es timated discontinuities range from 0.034 to 0.098, none of which are statistically significan t at conventional levels and which are lower than the OLS estimates. This suggest s that although attending the state’s flagship state university may increase earnings on averag e relative to the alternative, there is less compelling evidence that it does so for the median earner. 2.7.2 White Women We also perform a similar set of robust ness checks for white women, the results of which are shown in Table 6. The results are c onsistent with those for the men in that the inclusion of the control vari ables does not affect the estimates in a meaningful way.

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84 Similarly, the functional form of adjusted SAT score does seem to matter somewhat; the quadratic and cubic specifications result in estimates that are less negative or even positive relative to the li near specification. However, the most striking result concerns the effect of attending the flagship state university for women who have strong attach ment to the labor force, as shown in specifications (6) and (7). For these women, the estimates are positive and, for three of the four estimates, are statistically significant at the 10% level. As shown in Table 6, the discontinuity estimates are 0.144 and 0.217 for 12 and 15 years after high school graduation using the cubic speci fication, both of which are sta tistically significant at the 1% level. Using the linear functional form the discontinuity estimates are 0.77 and 0.53 for 12 and 15 years after high school graduation, only the former of which is statistically significant at the 10% level. As shown in row (8), restricting the sa mple to only those applicants within 100 SAT points of the admission cutoff does not s ubstantially affect the estimates. And finally, the median regression discontinuity estimates reported in rows (9) and (10) confirm the result that the cubic specification results in more positive discontinuity estimates, although only the estimate for 12 year s is statistically si gnificant at the 10% level. 2.8 Conclusion In this paper, we identify the causal effect of attending the flagship state university by utilizing a regr ession discontinuity design that compares the earnings of those who were just accepted by the flagship to the earnings of those who just missed the admission cutoff. We do so by combining c onfidential student applicant records from a large flagship state university to earnings data collect ed by the state through the

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85 Unemployment Insurance Program. After li nking these two data sets together, we estimate the admission cutoff at the flagship and find that this estimated cutoff based on applicants SAT score and adjusted high school GPA coincides with a very large, distinct discontinuity in the likelihood of be ing admitted to the university. We then examine whether or not there is a discontinuity in the likelihood of being observed with positive earnings 7 – 15 years after high school graduation. We find little evidence that admission to the flagship cause s men or women to more or less likely to work in-state than their counterparts w ho barely missed the admission cutoff. Finally, we estimate the intent-to-treat e ffect of attending the flagship state university on total earnings. For white men, we find evidence of positive discontinuities that translate to increases in earnings from 1% to 27%, although the discontinuities are not estimated precisely in a ll specifications. The size of the coefficients and their statistical significance depend largely on the functional form; polynomials of adjusted SAT score of order 2 or higher result in larger, statistically significant earnings discontinuities. There does not appear to be an effect on the median earnings of those who are admitted to the flagship state university, however. For women overall, we find little consis tent evidence of either a positive or negative effect of attending the flagship st ate university on earnings. However, we do find evidence of a large and statistically significa nt effect on the earni ngs of the subset of women with strong attachment to the labor forc e; the estimates of th e effect on earnings range from 8% to 32%. The results provide some suggestive evid ence that being accep ted by and attending the flagship state university may indeed cause an increase in s ubsequent earnings.

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86 Consequently, the higher earnings that result fr om attending the flag ship state university may justify, at least to some extent, costs (i.e., SAT prep aration courses) undertaken by students and parents to gain admission to and/ or to attend the top university in the state, at least for men and for women with a strong attachment to the labor force. Perhaps more importantly, although this paper did not (yet) examine the effect of attending the flagship university on minority applicants, the results for whites may yield insight nonetheless into the potential c onsequences of the eliminatio n of affirmative action and the subsequent reduction in enrollment rates for minorities at the top state schools. To the extent that the effect for minorities is si milar to that of white applicants, one may well expect that the earnings of minorities may fall as a result of the elimination of affirmative action in the admissions of flag ship state universities.

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87 0 .2 .4 .6 .8 1 Admission Rate -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = 0.687 (t=26.33) Figure 2-1: Fraction Admitted to the Flagship State University

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88 Table 2-1: Regression Disc ontinuity Estimates for the Admission Rate of White Applicants Regression Estimated Discontinuity Function of Adjusted SATControls (1) 0.876 noneNo (0.013) [0.000] (2) 0.685 Yes (0.021) [0.000] (3) 0.687 No (Plotted in Figure 1) (0.026) [0.000] (4) 0.686 Yes (0.025) [0.000] cubic, cubic*Admit 4th order, 4th order*Admit 4th order, 4th order*Admit Notes: Each row represents a different OLS regression. Robust standard errors are in parentheses; p-values are given in brackets. Controls include a dummy variable for each year/term of application as well as actual SAT score and high school GPA. Estimates in bold are statistically significant at the 10% level.

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89 0 .1 .2 .3 .4 .5 .6 .7 .8 .9 1 Enrollment Rate Conditional on Admission -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted ProbabilityLocal AverageEstimated Discontinuity = -0.185 (t = -3.33) Figure 2-2: Enrollment Rates for Admitted White Applicants 0 .1 .2 .3 .4 .5 .6 .7 .8 .9 1 Graduation Rate Conditional on Enrollment -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted ProbabilityLocal AverageEstimated Discontinuity = -0.015 (t = -0.41) Figure 2-3: Graduati on Rates for Enrolling White Applicants

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90 .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 7 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = -.027 (t=-0.89) Figure 2-4a: The Likelihood of Being Observed with 4 Consecutive Quarters of Positive Earnings 7 Years after High Sc hool Graduation for White Men .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 8 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = 0.014 (t=0.50) Figure 2-4b: The Likelihood of Being Observed with 4 Consecutive Quarters of Positive Earnings 8 Years after High Sc hool Graduation for White Men

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91 .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 9 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = 0.051 (t=1.34) Figure 2-4c: The Likelihood of Being Observed with 4 Consecutive Quarters of Positive Earnings 9 Years after High Sc hool Graduation for White Men .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 10 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = 0.006 (t=0.30) Figure 2-4d: The Likelihood of Being Observed with 4 Consecutive Quarters of Positive Earnings 10 Years after High Sc hool Graduation for White Men

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92 .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 11 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = -0.019 (t=-0.80) Figure 2-4e: The Likelihood of Being Observed with 4 Consecutive Quarters of Positive Earnings 11 Years after High Sc hool Graduation for White Men .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 12 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = -0.042 (t=-1.65) Figure 2-4f: The Likelihood of Being Observed with 4 Consecutive Quarters of Positive Earnings 12 Years after High Sc hool Graduation for White Men

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93 .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 13 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = 0.034 (t=1.31) Figure 2-4g: The Likelihood of Being Observed with 4 Consecutive Quarters of Positive Earnings 13 Years after High Sc hool Graduation for White Men .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 14 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = 0.048 (t=1.91) Figure 2-4h: The Likelihood of Being Observed with 4 Consecutive Quarters of Positive Earnings 14 Years after High Sc hool Graduation for White Men

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94 .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 15 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = 0.036 (t=0.99) Figure 2-4i: The Likelihood of Being Observed with 4 Consecutive Quarters of Positive Earnings 15 Years after High Sc hool Graduation for White Men .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 7 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = -.020 (t=-0.74) Figure 2-5a: The Likelihood of Being Observ ed with Positive Earnings in the 7th Year after High School Graduation for White Men

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95 .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 8 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = -0.018 (t=-0.89) Figure 2-5b: The Likelihood of Being Observ ed with Positive Earnings in the 8th Year after High School Graduation for White Men .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 9 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = -0.011 (t=-0.41) Figure 2-5c: The Likelihood of Being Observ ed with Positive Earnings in the 9th Year after High School Graduation for White Men

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96 .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 10 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = -0.010 (t=-0.43) Figure 2-5d: The Likelihood of Being Observ ed with Positive Earnings in the 10th Year after High School Graduation for White Men .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 11 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = -0.034 (t=-1.64) Figure 2-5e: The Likelihood of Being Observ ed with Positive Earnings in the 11th Year after High School Graduation for White Men

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97 .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 12 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = -0.017 (t=-0.81) Figure 2-5f: The Likelihood of Being Observ ed with Positive Earnings in the 12th Year after High School Graduation for White Men .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 13 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = 0.019 (t=0.71) Figure 2-5g: The Likelihood of Being Observ ed with Positive Earnings in the 13th Year after High School Graduation for White Men

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98 .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 14 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = 0.022 (t=0.68) Figure 2-5h: The Likelihood of Being Observ ed with Positive Earnings in the 14th Year after High School Graduation for White Men .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 15 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = 0.037 (t=1.33) Figure 2-5i: The Likelihood of Being Observ ed with Positive Earnings in the 15th Year after High School Graduation for White Men

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99 .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 7 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = -.035 (t=-1.15) Figure 2-6a: The Likelihood of Being Observed with 4 Consecutive Quarters of Positive Earnings 7 Years after High Sc hool Graduation for White Women .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 8 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = -0.008 (t=-0.30) Figure 2-6b: The Likelihood of Being Observed with 4 Consecutive Quarters of Positive Earnings 8 Years after High Sc hool Graduation for White Women

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100 .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 9 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = -0.013 (t=-0.55) Figure 2-6c: The Likelihood of Being Observed with 4 Consecutive Quarters of Positive Earnings 9 Years after High Sc hool Graduation for White Women .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 10 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = -0.027 (t=-0.49) Figure 2-6d: The Likelihood of Being Observed with 4 Consecutive Quarters of Positive Earnings 10 Years after High Sc hool Graduation for White Women

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101 .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 11 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = -0.028 (t=-0.43) Figure 2-6e: The Likelihood of Being Observed with 4 Consecutive Quarters of Positive Earnings 11 Years after High Sc hool Graduation for White Women .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 12 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = -0.024 (t=-0.40) Figure 2-6f: The Likelihood of Being Observed with 4 Consecutive Quarters of Positive Earnings 12 Years after High Sc hool Graduation for White Women

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102 .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 13 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = -0.063 (t=-1.46) Figure 2-6g: The Likelihood of Being Observed with 4 Consecutive Quarters of Positive Earnings 13 Years after High Sc hool Graduation for White Women .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 14 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = -0.028 (t=-0.82) Figure 2-6h: The Likelihood of Being Observed with 4 Consecutive Quarters of Positive Earnings 14 Years after High Sc hool Graduation for White Women

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103 .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 15 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = 0.025 (t=0.84) Figure 2-6i: The Likelihood of Being Observed with 4 Consecutive Quarters of Positive Earnings 15 Years after High Sc hool Graduation for White Women .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 7 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = -.008 (t=-0.21) Figure 2-7a: The Likelihood of Being Observ ed with Positive Earnings in the 7th Year after High School Graduation for White Women

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104 .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 8 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = -0.007 (t=-0.31) Figure 2-7b: The Likelihood of Being Observ ed with Positive Earnings in the 8th Year after High School Graduation for White Women .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 9 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = -0.067 (t=-2.24) Figure 2-7c: The Likelihood of Being Observ ed with Positive Earnings in the 9th Year after High School Graduation for White Women

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105 .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 10 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = -0.024 (t=-0.77) Figure 2-7d: The Likelihood of Being Observ ed with Positive Earnings in the 10th Year after High School Graduation for White Women .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 11 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = -0.023 (t=-0.38) Figure 2-7e: The Likelihood of Being Observ ed with Positive Earnings in the 11th Year after High School Graduation for White Women

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106 .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 12 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = 0.003 (t=0.08) Figure 2-7f: The Likelihood of Being Observ ed with Positive Earnings in the 12th Year after High School Graduation for White Women .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 13 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = -0.036 (t=-0.83) Figure 2-7g: The Likelihood of Being Observ ed with Positive Earnings in the 13th Year after High School Graduation for White Women

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107 .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 14 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = -0.018 (t=-0.38) Figure 2-7h: The Likelihood of Being Observ ed with Positive Earnings in the 14th Year after High School Graduation for White Women .2 .3 .4 .5 .6 .7 .8 Fraction Observed with Earnings after 15 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted Probab ilityLocal AverageEstimated Discontinuity = -0.004 (t=-0.08) Figure 2-7i: The Likelihood of Being Observ ed with Positive Earnings in the 15th Year after High School Graduation for White Women

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108 Table 2-2: Regression Disc ontinuity Estimates for the Likelihood of Being Observed with Earnings 7 – 15 Years after Hi gh School Graduati on (a summary of estimates presented in Figures 2-4a -f, 2-5a-f, 2-6a-f, and 2-7a-f) 4 Consecutive Qtrs. A nnualized4 Consecutive Qtrs.Annualized 7-0.027-0.020-0.035-0.008 (0.031)(0.027)(0.030)(0.036) [0.376][0.459][0.253][0.834] 80.014-0.018-0.008-0.007 (0.028)(0.020)(0.025)(0.023) [0.620][0.377][0.764][0.758] 90.051-0.011-0.126 -0.067 (0.038)(0.026)(0.023) (0.030) [0.186][0.683][0.587] [0.028] 100.006-0.010-0.027-0.024 (0.021)(0.024)(0.055)(0.031) [0.762][0.666][0.625][0.446] 11-0.019-0.034-0.028-0.023 (0.0240)(0.021)(0.066)(0.060) [0.426][0.105][0.671][0.708] 12-0.042-0.017-0.0240.003 (0.025)(0.021)(0.060)(0.043) [0.104][0.424][0.688][0.936] 130.0340.019-0.063-0.036 (0.026)(0.027)(0.043)(0.043) [0.193][0.479][0.148][0.411] 14 0.048 0.022-0.028-0.018 (0.025) (0.033)(0.034)(0.047) [0.061] [0.502][0.416][0.703] 150.0360.0370.025-0.004 (0.037)(0.028)(0.030)(0.044) [0.328][0.189][0.402][0.933] Men Year After High School Graduation Earnings Measure Earnings Measure Women Notes: Robust standard errors clustered at the adjusted SAT score level are in parentheses; p-values are in brackets. Estimates in bold are statistically significant at the 10% level. All estimates are from regressions controlling for a cubic of adjusted SAT score

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109 0 .2 .4 .6 .8 1 Admission Rate -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted ProbabilityLocal AverageEstimated Discontinuity = 0.687 (t=26.33) Figure 2-8a: Regression Discontinuity Es timates for the Admission Rate of White Applicants Observed with 4 Consecu tive Quarters of Earnings in the 12th Year after High School Graduation

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110 0 .2 .4 .6 .8 1 Admission Rate -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted ProbabilityLocal AverageEstimated Discontinuity = 0.739 (t=21.13) Figure 2-8b: Regression Discontinuity Es timates for the Admission Rate of White Applicants Observed with 4 Consecu tive Quarters of Earnings in the 15th Year after High School Graduation

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111 0 .2 .4 .6 .8 1 Admission Rate -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted ProbabilityLocal AverageEstimated Discontinuity = 0.701 (t=26.95) Figure 2-9a: Regression Discontinuity Es timates for the Admission Rate of White Applicants Observed with Positive Earnings in the 12th Year after High School Graduation

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112 0 .2 .4 .6 .8 1 Admission Rate -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Predicted ProbabilityLocal AverageEstimated Discontinuity = 0.714 (t=25.45) Figure 2-9b: Regression Discontinuity Es timates for the Admission Rate of White Applicants Observed with Positive Earnings in the 15th Year after High School Graduation

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113 10.4 10.6 10.8 11 11.2 11.4 Natural Log Earnings after 10 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Local AveragePredicted Earnings (Linear) Predicted Earnings (Cubic)Estimated Discontinuity (Linear) = 0.013 (t=0.32) Estimated Discontinuity (Cubic) = 0.168 (t=3.41) Figure 2-10a: The Natural Log of 4 Consecu tive Quarters of Earnings for White Males 10 Years after High School Graduation 10.4 10.6 10.8 11 11.2 11.4 Natural Log Earnings after 11 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Local AveragePredicted Earnings (Linear) Predicted Earnings (Cubic)Estimated Discontinuity (Linear) = 0.054 (t=1.35) Estimated Discontinuity (Cubic) = 0.150 (t=2.06) Figure 2-10b: The Natural Log of 4 Consecu tive Quarters of Earnings for White Males 11 Years after High School Graduation

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114 10.4 10.6 10.8 11 11.2 11.4 Natural Log Earnings after 12 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Local AveragePredicted Earnings (Linear) Predicted Earnings (Cubic)Estimated Discontinuity (Linear) = 0.079 (t=2.04) Estimated Discontinuity (Cubic) = 0.168 (t=2.21) Figure 2-10c: The Natural Log of 4 Consecu tive Quarters of Earnings for White Males 12 Years after High School Graduation 10.4 10.6 10.8 11 11.2 11.4 Natural Log Earnings after 13 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Local AveragePredicted Earnings (Linear) Predicted Earnings (Cubic)Estimated Discontinuity (Linear) = 0.030 (t=0.75) Estimated Discontinuity (Cubic) = 0.179 (t=2.61) Figure 2-10d: The Natural Log of 4 Consecu tive Quarters of Earnings for White Males 13 Years after High School Graduation

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115 10.4 10.6 10.8 11 11.2 11.4 Natural Log Earnings after 14 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Local AveragePredicted Earnings (Linear) Predicted Earnings (Cubic)Estimated Discontinuity (Linear) = 0.050 (t=1.15) Estimated Discontinuity (Cubic) = 0.171 (t=2.18) Figure 2-10e: The Natural Log of 4 Consecu tive Quarters of Earnings for White Males 14 Years after High School Graduation 10.4 10.6 10.8 11 11.2 11.4 Natural Log Earnings after 15 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Local AveragePredicted Earnings (Linear) Predicted Earnings (Cubic)Estimated Discontinuity (Linear) = 0.069 (t=1.80) Estimated Discontinuity (Cubic) = 0.186 (t=2.45) Figure 2-10f: The Natural Log of 4 Consecutiv e Quarters of Earnings for White Males 15 Years after High School Graduation

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116 9.8 10.2 10.6 11 Natural Log Earnings after 10 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Local AveragePredicted Earnings (Linear) Predicted Earnings (Cubic)Estimated Discontinuity (Linear) = 0.022 (t=0.52) Estimated Discontinuity (Cubic) = 0.164 (t=1.68) Figure 2-11a: The Natural L og of Annualized Earnings fo r White Males 10 Years after High School Graduation 9.8 10.2 10.6 11 Natural Log Earnings after 11 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Local AveragePredicted Earnings (Linear) Predicted Earnings (Cubic)Estimated Discontinuity (Linear) = 0.053 (t=1.09) Estimated Discontinuity (Cubic) = 0.123 (t=1.65) Figure 2-11b: The Natural L og of Annualized Earnings fo r White Males 11 Years after High School Graduation

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117 9.8 10.2 10.6 11 Natural Log Earnings after 12 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Local AveragePredicted Earnings (Linear) Predicted Earnings (Cubic)Estimated Discontinuity (Linear) = 0.080 (t=1.81) Estimated Discontinuity (Cubic) = 0.135 (t=2.03) Figure 2-11c: The Natural L og of Annualized Earnings fo r White Males 12 Years after High School Graduation 9.8 10.2 10.6 11 Natural Log Earnings after 13 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Local AveragePredicted Earnings (Linear) Predicted Earnings (Cubic)Estimated Discontinuity (Linear) = 0.059 (t=1.61) Estimated Discontinuity (Cubic) = 0.070 (t=1.42) Figure 2-11d: The Natural L og of Annualized Earnings fo r White Males 13 Years after High School Graduation

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118 9.8 10.2 10.6 11 Natural Log Earnings after 14 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Local AveragePredicted Earnings (Linear) Predicted Earnings (Cubic)Estimated Discontinuity (Linear) = 0.071 (t=1.96) Estimated Discontinuity (Cubic) = 0.149 (t=2.51) Figure 2-11e: The Natural L og of Annualized Earnings fo r White Males 14 Years after High School Graduation 9.8 10.2 10.6 11 Natural Log Earnings after 15 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Local AveragePredicted Earnings (Linear) Predicted Earnings (Cubic)Estimated Discontinuity (Linear) = 0.063 (t=1.48) Estimated Discontinuity (Cubic) = 0.193 (t=2.89) Figure 2-11f: The Natural Log of Annualized Earnings for White Males 15 Years after High School Graduation

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119 Table 2-3: Summary of Regression Discontinuity Estimates for the Earnings of White Men Presented in Figures 10a – 10f and Figures 11a – 11f LinearCubicLinearCubic 100.013 0.168 0.022 0.164 (0.041) (0.049) (0.042) (0.098) [0.754] [0.001] [0.604] [0.099] 110.054 0.150 0.0530.123 (0.040) (0.073) (0.049)(0.075) [0.180] [0.043] [0.282][0.103] 12 0.0790.1680.0800.135 (0.039)(0.076)(0.044)(0.067) [0.046][0.031][0.074][0.046] 130.030 0.179 0.0590.070 (0.041) (0.069) (0.037)(0.049) [0.458] [0.011] [0.113][0.159] 140.050 0.1710.0710.149 (0.043) (0.079)(0.036)(0.059) [0.255] [0.033][0.054][0.015] 15 0.0690.186 0.063 0.193 (0.038)(0.076) (0.043) (0.067) [0.076][0.017] [0.143] [0.005] Notes: Robust standard errors clustered at the adjust ed SAT score level are in parentheses; p-values are in brackets. Estimates in bold are statis tically significant at the 10% level. Earnings Measure Year After High School GraduationFour Consecutive QuartersAnnualized

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120 10.2 10.4 10.6 10.8 11 11.2 Natural Log Earnings after 10 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Local AveragePredicted Earnings (Linear) Predicted Earnings (Cubic)Estimated Discontinuity (Linear) = -0.037 (t = -1.45) Estimated Discontinuity (Cubic) = 0.045 (t = 1.50) Figure 2-12a: The Natural Log of 4 Consecu tive Quarters of Earnings for White Women 10 Years after High School Graduation 10.2 10.4 10.6 10.8 11 11.2 Natural Log Earnings after 11 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Local AveragePredicted Earnings (Linear) Predicted Earnings (Cubic)Estimated Discontinuity (Linear) = -0.018 (t = -0.60) Estimated Discontinuity (Cubic) = 0.118 (t = 3.45) Figure 2-12b: The Natural Log of 4 Consecu tive Quarters of Earnings for White Women 11 Years after High School Graduation

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121 10.2 10.4 10.6 10.8 11 11.2 Natural Log Earnings after 12 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Local AveragePredicted Earnings (Linear) Predicted Earnings (Cubic)Estimated Discontinuity (Linear) = -0.077 (t = -3.23) Estimated Discontinuity (Cubic) = -0.015 (t = -0.33) Figure 2-12c: The Natural Log of 4 Consecu tive Quarters of Earnings for White Women 12 Years after High School Graduation 10.2 10.4 10.6 10.8 11 11.2 Natural Log Earnings after 14 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Local AveragePredicted Earnings (Linear) Predicted Earnings (Cubic)Estimated Discontinuity (Linear) = -0.020 (t = -0.54) Estimated Discontinuity (Cubic) = 0.136 (t = 2.24) Figure 2-12d: The Natural Log of 4 Consecu tive Quarters of Earnings for White Women 13 Years after High School Graduation

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122 10.2 10.4 10.6 10.8 11 11.2 Natural Log Earnings after 14 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Local AveragePredicted Earnings (Linear) Predicted Earnings (Cubic)Estimated Discontinuity (Linear) = -0.020 (t = -0.54) Estimated Discontinuity (Cubic) = 0.136 (t = 2.24) Figure 2-12e: The Natural Log of 4 Consecu tive Quarters of Earnings for White Women 14 Years after High School Graduation 10.2 10.4 10.6 10.8 11 11.2 Natural Log Earnings after 15 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Local AveragePredicted Earnings (Linear) Predicted Earnings (Cubic)Estimated Discontinuity (Linear) = -0.047 (t = -1.16) Estimated Discontinuity (Cubic) = 0.039 (t = 0.68) Figure 2-12f: The Natural Log of 4 Consecutiv e Quarters of Earnings for White Women 15 Years after High School Graduation

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123 9.8 10.2 10.6 11 Natural Log Earnings after 10 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Local AveragePredicted Earnings (Linear) Predicted Earnings (Cubic)Estimated Discontinuity (Linear) = -0.053 (t = -1.03) Estimated Discontinuity (Cubic) = 0.104 (t = 1.38) Figure 2-13a: The Natural L og of Annualized Earnings fo r White Women 10 Years after High School Graduation 9.8 10.2 10.6 11 Natural Log Earnings after 11 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Local AveragePredicted Earnings (Linear) Predicted Earnings (Cubic)Estimated Discontinuity (Linear) = -0.036 (t = -0.83) Estimated Discontinuity (Cubic) = 0.063 (t = 1.26) Figure 2-13b: The Natural L og of Annualized Earnings fo r White Women 11 Years after High School Graduation

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124 9.8 10.2 10.6 11 Natural Log Earnings after 12 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Local AveragePredicted Earnings (Linear) Predicted Earnings (Cubic)Estimated Discontinuity (Linear) = -0.079 (t = -1.89) Estimated Discontinuity (Cubic) = -0.108 (t = -1.55) Figure 2-13c: The Natural L og of Annualized Earnings fo r White Women 12 Years after High School Graduation 9.8 10.2 10.6 11 Natural Log Earnings after 13 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Local AveragePredicted Earnings (Linear) Predicted Earnings (Cubic)Estimated Discontinuity (Linear) = -0.028 (t = -0.64) Estimated Discontinuity (Cubic) = 0.094 (t = 1.14) Figure 2-13d: The Natural L og of Annualized Earnings fo r White Women 13 Years after High School Graduation

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125 9.8 10.2 10.6 11 Natural Log Earnings after 14 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Local AveragePredicted Earnings (Linear) Predicted Earnings (Cubic)Estimated Discontinuity (Linear) = -0.041 (t = -0.99) Estimated Discontinuity (Cubic) = 0.041 (t = 0.64) Figure 2-13e: The Natural L og of Annualized Earnings fo r White Women 14 Years after High School Graduation 9.8 10.2 10.6 11 Natural Log Earnings after 15 Years -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Local AveragePredicted Earnings (Linear) Predicted Earnings (Cubic)Estimated Discontinuity (Linear) = -0.095 (t = -2.07) Estimated Discontinuity (Cubic) = -0.065 (t = -0.72) Figure 2-13f: The Natural Log of Annualized Earnings for White Women 15 Years after High School Graduation

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126 Table 2-4: Summary of Regression Discontinuity Estimates for the Earnings of White Women Presented in Figures 12a – 12f and Figures 13a – 13f LinearCubicLinearCubic 10-0.0370.045-0.0530.104 (0.026)(0.030)(0.051)(0.075) [0.152][0.137][0.307][0.172] 11-0.018 0.118 -0.0360.063 (0.031) (0.034) (0.044)(0.050) [0.553] [0.001] [0.408][0.213] 12 -0.077 -0.015 -0.079 -0.108 (0.024) (0.045) (0.042) (0.069) [0.002] [0.746] [0.064] [0.125] 13-0.045 0.123 -0.0280.094 (0.038) (0.056) (0.044)(0.082) [0.243] [0.030] [0.527][0.259] 14-0.020 0.136 -0.0410.041 (0.036) (0.061) (0.041)(0.064) [0.592] [0.028] [0.324][0.525] 15-0.0470.039 -0.095 -0.065 (0.040)(0.057) (0.046) (0.090) [0.249][0.498] [0.042] [0.474] Notes: Robust standard errors clustered at the adjust ed SAT score level are in parentheses; p-values are in brackets. Estimates in bold are statis tically significant at the 10% level. Earnings Measure Year After High School GraduationFour Consecutive QuartersAnnualized

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127 .7 .75 .8 .85 .9 Fraction of Quarters in Labor Force -300 -250 -200 -150 -100 -50 0 50 100 150 200 250 300 350 SAT Points Above or Below the Admission Cutoff Local Average Predicted % Quarters in Labor Force (Linear) Predicted % Quarters in Labor Force (Cubic)Estimated Discontinuity (Linear) = 0.000 (t = 0.02) Estimated Discontinuity (Cubic) = -0.006 (t = -0.24) Figure 2-14: The Labor Force Participation of White Women Age 28 – 33 Observed in the Labor Force at Age 33

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128 Table 2-5: Regression Disc ontinuity Estimates after 12 and 15 Years for Various Specifications and Subsamples ControlsSample ( 1 ) linear NoFull 0.0780.069 linear*Admitn = 4,943 ( 12 Years ) (0.039)(0.038) n = 4,911 ( 15 Years ) [0.046][0.076] (2) linear YesFull 0.078 0.060 linear*Admitn = 4,943 ( 12 Years ) (0.039) (0.040) n = 4,911 ( 15 Years ) [0.049] [0.136] (3) YesFull 0.1670.140 n = 4,943 ( 12 Years ) (0.059)(0.058) n = 4,911 ( 15 Years ) [0.006][0.019] (4)NoFull 0.1680.186 n = 4,943 ( 12 Years ) (0.076)(0.076) n = 4,911 ( 15 Years ) [0.031][0.017] (5)YesFull 0.1470.171 n = 4,943 ( 12 Years ) (0.077)(0.080) n = 4,911 ( 15 Years ) [0.061][0.036] (6) linear Yes 0.093 0.069 linear*Admit (0.050) (0.058) [0.069] [0.238] n = 1,947 (both years) (7)Yes 0.2600.254 (0.067)(0.094) [0.000][0.009] n = 1,947 (both years) (8) linear Yes 0.1670.157 linear*Admit (0.070)(0.065) [0.026][0.026] n = 2,196n = 2,162 (9) linear YesFull0.0340.056 linear*Admitn = 4,943 ( 12 Years ) (0.038)(0.042) n = 4,911 ( 15 Years ) [0.371][0.190] (10)Yes Full 0.0980.097 n = 4,943 ( 12 Years ) (0.076)(0.079) n = 4,911 ( 15 Years ) [0.196][0.220] cubic, cubic*Admit Only applicants always observed 10 15 years after high school graduation Estimated Discontinuity after Hi g h School Graduation Only applicants always observed 10 15 years after high school graduation cubic, cubic*Admit cubic, cubic*Admit Median Re g ression Median Regression Notes: Each row reports the estimated discontinuities for earnings after 12 and 15 years using the same functional form. Robust standard errors clustered at the adjusted SAT score level are in parentheses; p-values are in brackets. Controls include dummy variables for each year/term of application as well as actual SAT score and high school GPA. Estimates in bold are statistically significant at the 10% level. Only applicants who missed or exceeded the admission cutoff by no more than 100 SAT points Specification Number 12 Years15 Years Adjusted SAT Functional Form quadratic, quadratic*Admi t cubic, cubic*Admit Regression Specification

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129 Table 2-6: Regression Disc ontinuity Estimates after 12 and 15 Years for Various Specifications and Subsamples for White Women ControlsSample ( 1 ) linear NoFull -0.077 -0.047 linear*Admitn = 4,614 ( 12 Years ) (0.024) (0.040) n = 4,096 ( 15 Years ) [0.002] [0.249] (2) linear YesFull -0.082 -0.039 linear*Admitn = 4,614 ( 12 Years ) (0.024) (0.041) n = 4,096 ( 15 Years ) [0.001] [0.343] (3) YesFull-0.0260.010 n = 4,614 ( 12 Years ) (0.034)(0.051) n = 4,096 ( 15 Years ) [0.443][0.848] (4)NoFull-0.0150.039 n = 4,614 ( 12 Years ) (0.045)(0.057) n = 4,096 ( 15 Years ) [0.746][0.498] (5)YesFull-0.0310.034 n = 4,614 ( 12 Years ) (0.044)(0.057) n = 4,096 ( 15 Years ) [0.484][0.554] (6) linear Yes 0.077 0.053 linear*Admit (0.042) (0.048) [0.071] [0.268] n = 1,687 (both years) (7)Yes 0.1440.217 (0.052)(0.056) [0.007][0.000] n = 1,687 (both years) (8) linear Yes-0.0510.038 linear*Admit (0.035)(0.047) [0.158][0.429] n = 2,215n=1,943 (9) linear NoFull-0.025-0.019 linear*Admitn = 4,614 ( 12 Years ) (0.032)(0.035) n = 4,096 ( 15 Years ) [0.434][0.595] (10)No Full 0.098 0.037 n = 4,614 ( 12 Years ) (0.058) (0.071) n = 4,096 ( 15 Years ) [0.094] [0.605] Only applicants who missed or exceeded the admission cutoff by no more than 100 SAT points cubic, cubic*Admit Only applicants always observed 10 15 years after high school graduation Estimated Discontinuity after Hi g h School Graduation Only applicants always observed 10 15 years after high school graduation cubic, cubic*Admit cubic, cubic*Admit Median Re g ression Median Regression Notes: Each row reports the estimated discontinuities for earnings after 12 and 15 years using the same functional form. Robust standard errors clustered at the adjusted SAT score level are in parentheses; p-values are in brackets. Controls include dummy variables for each year/term of application as well as actual SAT score and high school GPA. Estimates in bold are statistically significant at the 10% level. Specification Number 12 Years15 Years Adjusted SAT Functional Form quadratic, quadratic*Admi t cubic, cubic*Admit Regression Specification

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130 LIST OF REFERENCES Amato, Paul R., and Alan Booth. 1991. “Conse quences of Parental Divorce and Marital Unhappiness for Adult Well-Being.” Social Forces 69 (3): 895-914. Arcidiacono, Peter. 2005. “Affirmativ e Action in Higher Education: How Do Admission and Financial Aid Rules Affect Future Earnings?” Econometrica 73 (5): 1477-4524. Ayres, Ian, and Richard Brooks. 2005. “Does Affirmative Action Reduce the Number of Black Lawyers?” Stanford Law Review 57 (6): 1807-1854. Behrman, Jere, Mark Rozenzweig, and Paul Taubman. 1996. “College Choice and Wages: Estimates Using Data on Female Twins.” The Review of Economics and Statistics 78: 672-685 Black, Dan, and Jeff Smith. 2004. “How Robust Is the Evidence on the Effects of College Quality? Evidence from Matching.” Journal of Econometrics 121: 99-124. Borgess, Scott. 1998. “Family Struct ure, Economic Status, and Educational Attainment.” Journal of Population Economics 11: 205-222. Bound, John. 1989. “The Health and Earnings of Rejected Disability Insurance Applicants.” American Economic Review 79 (3): 482-503. Brewer, Dominic, Eric Eide, and Ronald Eh renberg. 1999. “Does It Pay to Attend an Elite Private College? Cross-Cohort Evid ence on the Effects of College Type on Earnings.” Journal of Human Resources 34 (1): 104-123. Bush, George W. 2002a. “President A nnounces Welfare Reform Agenda.” Press Release from the Office of the Press Secr etary at the White House, February 26, 2002. Last accessed June 7, 2006 at http://www.whitehouse.gov/news/releases/2002/02/20020226-11.html Bush, George W. 2002b. “President Disc usses Welfare Reform and Job Training.” Press Release from the Office of the Press Secretary at the White House, February 27, 2002. Last accessed June 7, 2006 at http://www.whitehouse.gov/news/releases/2002/02/20020227-5.html

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131 Cherlin, Andrew J., Kathleen E. Kiernan, P. Lindsay Chase-Lansdale. 1995. “Parental Divorce in Childhood and Demographic Outcomes in Young Adulthood.” Demography 32 (3): 299-318. Clinton, Hillary Rodham. 1996. It Takes a Village New York: Simon & Schuster. Corak, Miles. 2001. “Death and Divorce: Th e Long-Term Consequences of Parental Loss on Adolescents.” Journal of Labor Economics 19 (3): 682-715. Dale, Stacy Berg and Alan Krueger. 2002. “Estimating the Payoff to Attending a More Selective College: An Application of Selection on Observables and Unobservables.” Quarterly Journa l of Economics 117 (4): 1491-1527. Deleire, Thomas, and Ariel Kalil. 2002. “Good Things Come in Threes: Single-Parent Multigenerational Family Structure and Adolescent Adjustment.” Demography 39 (2): 393-413. Ermisch, John F. and Marco Francesconi. 2001a. “Family Structure and Children’s Achievements.” Journal of Population Economics 14: 249-270. Ermisch, John F. and Marco Francesconi. 2001b “Family Matters: Impacts of Family Background on Educational Attainments.” Economica 68: 137-156. Friedberg, Leora. 1998. “Did Unilateral Di vorce Raise Divorce Rates? Evidence from Panel Data.” American Economic Review 88 (3): 608-627. Fronstin, Paul, David H. Greenberg, and Philip K. Robins. 2001. “Parental Disruption and the Labour Market Performance of Children When They Reach Adulthood.” Journal of Population Economics 14: 137-172. Fryer, Roland, and Steven Levitt. 2004. “The Causes and Consequences of Distinctively Black Names.” Quarterly Journal of Economics 119: 767-805. Furstenberg, Frank F. and Kathleen E. Kier nan. 2001. “Delayed Parental Divorce: How Much Do Children Benefit?” Journal of Marriage and the Family 63: 446-457. Gruber, Jonathan. 2004. “Is Making Divor ce Easier Bad for Children? The Long Run Implications of Unilateral Divorce.” Journal of Labor Economics 22 (4): 799-833. Haveman, Robert, Barbara Wolfe, and James Spaulding. 1991. “Childhood Events and Circumstances Influencing High School Completion.” Demography 28 (1): 133157. Hill, Martha S., Wei-Jun J. Yeung, and Gr eg J. Duncan. 2001. “Childhood Family Structure and Young Adult Behaviors.” Journal of Population Economics 14: 271299.

PAGE 146

132 Keith, Verna M., and Barbara Finlay. 1988. “The Impact of Parental Divorce on Children’s Educational Attainment, Mari tal Status, Timing, and Likelihood of Divorce.” Journal of Marriage and the Family 50: 797-809. Kreider, Rose M. and Jason M. Fields. 1996. Number, Timing, and Duration of Marriages and Divorces: Fall 1996 Current Population Reports, P70-80. U.S. Census Bureau, Washington, DC. Lang, Kevin, and Jay L. Zagorsky. 2000. “D oes Growing Up With a Parent Absent Really Hurt?” Journal of Human Resources 36 (2): 253-273. Lindahl, Lena and Hakan Regner. 2005. “C ollege Choice and Subsequent Earnings: Results using Swedish Sibling Data.” Scandinavian Journal of Economics 107 (3):437-457 McLanahan, Sara, and Gary Sandefur. 1994. Growing Up with a Single Parent: What Helps, What Hurts. Cambridge, MA: Harvard University Press. Mincer, Jacob. 1974. Schooling, Experience, and Earnings New York: National Bureau of Economic Research. Painter, Gary, and David I. Levine. 2000. “Family Structure and Youths’ Outcomes: Which Correlations Are Causal?” Journal of Human Resources 35 (3): 524-549. Rose, Heather. 2005. “The Effects of Affi rmative Action Programs: Evidence from the University of California at San Diego.” Educational Evaluation and Policy Analysis 27 (3): 263-289. Sandefur, Gary D., and Thomas Wells. 1999. “Does Family Structure Really Influence Educational Attainment?” Social Science Research 28: 331-357. Sander, Richard. 2004. “A Systematic Analys is of Affirmative Action in American Law Schools.” Stanford Law Review 57 (2): 367-483. U.S. Bureau of the Census. 1999. Statistical Abstract of the United States No. 155 and No. 159. Washington, D.C. U.S. Bureau of the Census. 1970. Statistical Abstract of the United States No. 75. Washington, D.C.

PAGE 147

133 BIOGRAPHICAL SKETCH Mark Hoekstra received his bachelor’s degree from Hope College in Holland, Michigan. After graduation he will begin employment as an assistant professor at the University of Pittsburgh.


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ESSAYS ON THE EFFECTS OF FAMILY AND SCHOOLING ON STUDENT
OUTCOMES















By

MARK HOEKSTRA


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


2006

































Copyright 2006

by

Mark Hoekstra















ACKNOWLEDGMENTS

This work has benefited tremendously from the instruction and encouragement of

David Figlio. I would also like to thank Larry Kenny, Rich Romano, Mark Rush, Damon

Clark, Francisco Martorell, Steve Slutsky and countless others who provided helpful

advice and comments throughout all of the stages of this research.

I would like to thank the School Board of Alachua County for providing school

data and the people at the Office of the Clerk of the Circuit Court at the Alachua County

Courthouse for help in acquiring the divorce data used in this analysis. I would also like

to thank an anonymous state university for sharing admissions data and a state office for

sharing earnings data.















TABLE OF CONTENTS


page

A CK N O W LED G M EN TS ............................... ................................... ......................... iii

LIST OF TABLES ............................. ............... ..................... vi

LIST OF FIGURES ............................. ... ........ .... ....... ................ .. viii

A B S T R A C T .......................................... ..................................................x iii

CHAPTER

1 "JUST KIDDING, DEAR": USING DISMISSED DIVORCE CASES TO
IDENTIFY THE EFFECT OF PARENTAL DIVORCE ON STUDENT
P E R F O R M A N C E .............................................................................. ................. ..

1.1 Introduction .............................................. ................................ ....... 1
1.2 Theoretical Considerations, Literature Review, and Identification Strategy.....6
1.2.1 How Divorce Affects Student Achievement............... ................6
1.2.2 A Review of the Literature ............ ..............................................7
1.2.3 Identification Strategy .................................. ..................................... 10
1.3 Parental Divorce and Student Test Scores....................................... 13
1.3 .1 S ch o o l D ata ........................................... ................ 13
1.3.2 D divorce D ata ............................................................. ............... .... ..... 14
1.3.3 Divorces in Alachua County, Florida .......... .............. .................. 15
1.3.4 Merging the Divorce Data with the School Data..............................16
1.3.5 The Final Data Set Used in the Analysis.......................................... 20
1.4 The Effects of Divorce on Student Performance ......................................23
1.4.1 Comparing the Test Scores of Children of Divorce to Those of
Children in Intact Fam ilies.......................................................................... 23
1.4.2 Do We Observe the Same Correlation when Comparing Children of
Dismissed Divorce to Children of Intact Families? .....................................27
1.4.3 How Similar are Families That Experience Divorce to Those That
Experienced a Dismissed Divorce? ..................................... ............... 29
1.4.4 The Effect of Parental Divorce on Family Income............................29
1.4.5 The Pre-Divorce Trends of Children Whose Parents Later File for
D iv orce........................... ........................ .... ............... .......... .. .... 3 1
1.4.6 The Causal Time-Invariant Effect of Parental Divorce ....................32
1.4.7 The Causal Effects of Parental Divorce Over Time ............................33
1.4.8 Are the Effects of Parental Divorce Different for Boys than for
G irls? ............................................................................... 3 5









1.4.9 Does the Effect of Parental Divorce Depend on the Age of the
Student at the Tim e of D ivorce? ............. ....................... ....... ...............37
1.5 R obustness of R results ......................................................... .............. 37
1.6 C on clu sion s ................................................................... ............... 4 0

2 THE EFFECT OF ATTENDING THE FLAGSHIP STATE UNIVERSITY ON
EARNINGS: A REGRESSION DISCONTINUITY APPROACH...........................60

2.1 Introduction ............................................................... ........ 60
2 .2 D ata .... ..... .. .............. ......... .......... ......................................64
2.3 Identification Strategy.............................. ............................. ............... 65
2.4 The Admission Rule ........................................................ 67
2.4.1 Estim ating the A dm mission Rule .................................................... .... 67
2.4.2 Does the Admission Cutoff Predict Which Students Are Accepted
and W which A re R ejected? ............................................................. ................ 69
2.4.3 Potential Causes of the 'Fuzziness' of the Estimated Admission
D isc o n tin u ity ...................................... .................................. ................ 7 0
2.4.4 Do Applicants Who Just Meet the Admission Cutoff Subsequently
Attend and Graduate from the Flagship State University? ...........................72
2.4.5 Do Admitted Applicants above the Admission Cutoff Enroll and
Graduate from the Flagship at Different Rates than Applicants Just Below
th e C u to ff? ........................................................................7 3
2.5 A attrition from the Earnings D ata ........................................ .....................74
2.5.1 The Attrition of W hite M ales.............. ..............................................75
2.5.2 The A ttrition of W hite Fem ales ...........................................................76
2.5.3 The Admission Discontinuity for Those Observed with Positive
E earnings .............. ...................... ........ ....... ......... ....................... 76
2.6 The Effect of Admission at the Flagship University on Labor Market
O utcom es .......................................................................................... 77
2.6.1 The Earnings of W hite M ales ............. ...............................................77
2.6.2 W hite Fem ales ......................................... ........ ..............80
2.6.2.1 The effect of admission on subsequent earnings ...................80
2.6.2.2 The effect of admission on the labor market attachment of
w white w om en ............................................... .................. 8 1
2.7 The Sensitivity of the Earnings Estimates ..................................................82
2 .7 .1 W hite M en ............................................... .. .. ...... .. ................82
2.7.2 W hite W om en ......................................... ............... ........ .......... 83
2 .8 C o n clu sio n .................................................................... 8 4

LIST OF REFEREN CES ........................................................... .. ............... 130

BIOGRAPHICAL SKETCH ............................................................. ............... 133
















LIST OF TABLES


Table p

1-1 Matchable Divorces in Alachua County, Florida................................. ... .....43

1-2 Families Matched to Unique Divorces.................. ..................43

1-3 Families Matched to Unique Divorces.................. ..................44

1-4 Distribution of Observations of Students Matched to a Parental Divorce Case ......44

1-5 The Cross-Sectional Effects of Parental Divorce on Reading Test Scores.............45

1-6 The Cross-Sectional Effects of Parental Divorce on Mathematics Test Scores.......45

1-7 The Cross-Sectional Effects of Parental Divorce on Days Suspended Per Year.....46

1-8 The Cross-Sectional Effects of Parental Divorce on Disciplinary Infractions Per
Y ear ............. .. .............. ................ ...... .. ............................ 46

1-9 The Cross-Sectional "Effects" of Dismissed Divorce on Reading Test Scores.......47

1-10 The Cross-Sectional "Effects" of Dismissed Divorce on Mathematics Test
S c o re s ............................................................................ 4 8

1-11 The Cross-Sectional "Effects" of Dismissed Divorce on Days Suspended Per
Y ear .................. .................. ..............................................4 9

1-12 The Cross-Sectional "Effects" of Dismissed Divorce on Disciplinary Infractions
Per Year ............... ............ ............... ............... 49

1-13 D descriptive Statistics ........................................ ................... ..... .... 50

1-14 Estimated Effects of Parental Divorce on Student Family Income Using Student
F ix ed E effects ................................................................5 1

1-15 Estim ated Pre-D ivorce Trends ........................................ ........................... 52

1-16 Estimated Time-Invariant Effects of Parental Divorce on Student Test Scores
and B behavior .........................................................................52

1-17 Estimated Effects of Parental Divorce on Student Test Scores and Behavior.........53









1-18 Estimated Effects of Parental Divorce on Student Test Scores and Behavior.........54

1-19 Estimated Effects of Parental Divorce on Student Test Scores and Behavior .........55

1-20 Estimated Effects of Parental Divorce on Student Reading Test Scores .................56

1-21 Estimated Effects of Parental Divorce on Student Mathematics Test Scores..........57

1-22 Estimated Effects of Parental Divorce on Days Suspended per Year....................58

1-23 Estimated Effects of Parental Divorce on Disciplinary Infractions per Year ..........59

2-1 Regression Discontinuity Estimates for the Admission Rate of White
A applicants ............................................................. .... ..... ......... 88

2-2 Regression Discontinuity Estimates for the Likelihood of Being Observed with
Earnings 7 15 Years after High School Graduation (a summary of estimates
presented in Figures 2-4a-f, 2-5a-f, 2-6a-f, and 2-7a-f) ......................................108

2-3 Summary of Regression Discontinuity Estimates for the Earnings of White Men
Presented in Figures 1Oa 1Of and Figures 1la 1 f .....................................119

2-4 Summary of Regression Discontinuity Estimates for the Earnings of White
Women Presented in Figures 12a 12f and Figures 13a 13f............................126

2-5 Regression Discontinuity Estimates after 12 and 15 Years for Various
Specifications and Subsam ples ........................................ ......................... 128

2-6 Regression Discontinuity Estimates after 12 and 15 Years for Various
Specifications and Subsamples for W hite W omen ............................................. 129















LIST OF FIGURES


Figure page

2-1 Fraction Admitted to the Flagship State University............... .... ............... 87

2-2 Enrollment Rates for Admitted White Applicants ................................................89

2-3 Graduation Rates for Enrolling White Applicants................................................89

2-4a The Likelihood of Being Observed with 4 Consecutive Quarters of Positive
Earnings 7 Years after High School Graduation for White Men.............................90

2-4b The Likelihood of Being Observed with 4 Consecutive Quarters of Positive
Earnings 8 Years after High School Graduation for White Men..........................90

2-4c The Likelihood of Being Observed with 4 Consecutive Quarters of Positive
Earnings 9 Years after High School Graduation for White Men..........................91

2-4d The Likelihood of Being Observed with 4 Consecutive Quarters of Positive
Earnings 10 Years after High School Graduation for White Men..........................91

2-4e The Likelihood of Being Observed with 4 Consecutive Quarters of Positive
Earnings 11 Years after High School Graduation for White Men........................92

2-4f The Likelihood of Being Observed with 4 Consecutive Quarters of Positive
Earnings 12 Years after High School Graduation for White Men........................92

2-4g The Likelihood of Being Observed with 4 Consecutive Quarters of Positive
Earnings 13 Years after High School Graduation for White Men.......................93

2-4h The Likelihood of Being Observed with 4 Consecutive Quarters of Positive
Earnings 14 Years after High School Graduation for White Men........................93

2-4i The Likelihood of Being Observed with 4 Consecutive Quarters of Positive
Earnings 15 Years after High School Graduation for White Men........................94

2-5a The Likelihood of Being Observed with Positive Earnings in the 7th Year after
High School Graduation for W hite M en................... ...................................... 94

2-5b The Likelihood of Being Observed with Positive Earnings in the 8th Year after
High School Graduation for W hite M en ............. ......................... ...... ............ 95









2-5c The Likelihood of Being Observed with Positive Earnings in the 9th Year after
High School Graduation for W hite Men........... ... ......... ....... ............... 95

2-5d The Likelihood of Being Observed with Positive Earnings in the 10th Year after
High School Graduation for W hite M en............................................................ 96

2-5e The Likelihood of Being Observed with Positive Earnings in the 11th Year after
High School Graduation for White Men...................................... .............. 96

2-5f The Likelihood of Being Observed with Positive Earnings in the 12th Year after
High School Graduation for W hite M en........................................................... 97

2-5g The Likelihood of Being Observed with Positive Earnings in the 13th Year after
High School Graduation for White Men......... .. .................. ............. ............ 97

2-5h The Likelihood of Being Observed with Positive Earnings in the 14th Year after
High School Graduation for W hite Men........... ... ......... ....... ............... 98

2-5i The Likelihood of Being Observed with Positive Earnings in the 15th Year after
High School Graduation for White Men......... .. .................. ............. ............ 98

2-6a The Likelihood of Being Observed with 4 Consecutive Quarters of Positive
Earnings 7 Years after High School Graduation for White Women........................99

2-6b The Likelihood of Being Observed with 4 Consecutive Quarters of Positive
Earnings 8 Years after High School Graduation for White Women.....................99

2-6c The Likelihood of Being Observed with 4 Consecutive Quarters of Positive
Earnings 9 Years after High School Graduation for White Women......................100

2-6d The Likelihood of Being Observed with 4 Consecutive Quarters of Positive
Earnings 10 Years after High School Graduation for White Women.................100

2-6e The Likelihood of Being Observed with 4 Consecutive Quarters of Positive
Earnings 11 Years after High School Graduation for White Women ....................101

2-6f The Likelihood of Being Observed with 4 Consecutive Quarters of Positive
Earnings 12 Years after High School Graduation for White Women .................101

2-6g The Likelihood of Being Observed with 4 Consecutive Quarters of Positive
Earnings 13 Years after High School Graduation for White Women.................102

2-6h The Likelihood of Being Observed with 4 Consecutive Quarters of Positive
Earnings 14 Years after High School Graduation for White Women.................102

2-6i The Likelihood of Being Observed with 4 Consecutive Quarters of Positive
Earnings 15 Years after High School Graduation for White Women.................103









2-7a The Likelihood of Being Observed with Positive Earnings in the 7th Year after
High School Graduation for W hite W omen.................................. ...........103

2-7b The Likelihood of Being Observed with Positive Earnings in the 8th Year after
High School Graduation for W hite W omen.................................. ...........104

2-7c The Likelihood of Being Observed with Positive Earnings in the 9th Year after
High School Graduation for W hite W omen.................................. ...........104

2-7d The Likelihood of Being Observed with Positive Earnings in the 10th Year after
High School Graduation for W hite W omen.................................. ...........105

2-7e The Likelihood of Being Observed with Positive Earnings in the 11th Year after
High School Graduation for W hite W omen.................................. ...........105

2-7f The Likelihood of Being Observed with Positive Earnings in the 12th Year after
High School Graduation for W hite W omen.................................. ...........106

2-7g The Likelihood of Being Observed with Positive Earnings in the 13th Year after
High School Graduation for W hite W omen.................................. ...........106

2-7h The Likelihood of Being Observed with Positive Earnings in the 14th Year after
High School Graduation for W hite W omen.................................. ...........107

2-7i The Likelihood of Being Observed with Positive Earnings in the 15th Year after
High School Graduation for W hite W omen.................................. ...........107

2-8a Regression Discontinuity Estimates for the Admission Rate of White Applicants
Observed with 4 Consecutive Quarters of Earnings in the 12th Year after High
School G radu ation ........ ................................................................ .. .... .. .... .. 109

2-8b Regression Discontinuity Estimates for the Admission Rate of White Applicants
Observed with 4 Consecutive Quarters of Earnings in the 15th Year after High
School G radiation ............... ........ ........ ......... ....... .......... 110

2-9a Regression Discontinuity Estimates for the Admission Rate of White Applicants
Observed with Positive Earnings in the 12th Year after High School Graduation .111

2-9b Regression Discontinuity Estimates for the Admission Rate of White Applicants
Observed with Positive Earnings in the 15th Year after High School Graduation .112

2-10a The Natural Log of 4 Consecutive Quarters of Earnings for White Males 10
Years after High School Graduation ............. ............................... ............... 113

2-10b The Natural Log of 4 Consecutive Quarters of Earnings for White Males 11
Y ears after H igh School G radiation ......................................................................113









2-10 The Natural Log of 4 Consecutive Quarters of Earnings for White Males 12
Y ears after H igh School G radiation ...................................................................... 114

2-1OdThe Natural Log of 4 Consecutive Quarters of Earnings for White Males 13
Years after High School Graduation ........... ................................ ...............114

2-10eThe Natural Log of 4 Consecutive Quarters of Earnings for White Males 14
Years after High School Graduation ............. .............................. ............... 115

2-1 Of The Natural Log of 4 Consecutive Quarters of Earnings for White Males 15
Years after High School Graduation ............................................ ...............115

2-11 a The Natural Log of Annualized Earnings for White Males 10 Years after High
School Graduation .................. ........................................ .... ......... 116

2-1 Ib The Natural Log of Annualized Earnings for White Males 11 Years after High
School Graduation .................. ........................................ .... ......... 116

2-1 Ic The Natural Log of Annualized Earnings for White Males 12 Years after High
School Graduation .................. ........................................ .... ......... 117

2-1 IdThe Natural Log of Annualized Earnings for White Males 13 Years after High
School Graduation .................. ........................................ .... ......... 117

2-1 le The Natural Log of Annualized Earnings for White Males 14 Years after High
School Graduation .................. ........................................ .... ......... 118

2-1 If The Natural Log of Annualized Earnings for White Males 15 Years after High
School Graduation .................. ........................................ .... ......... 118

2-12a The Natural Log of 4 Consecutive Quarters of Earnings for White Women 10
Years after High School Graduation ............. .............................. ............... 120

2-12b The Natural Log of 4 Consecutive Quarters of Earnings for White Women 11
Years after High School Graduation ............. ................................. ............... 120

2-12c The Natural Log of 4 Consecutive Quarters of Earnings for White Women 12
Years after High School Graduation ............ .. ................................ ............... 121

2-12dThe Natural Log of 4 Consecutive Quarters of Earnings for White Women 13
Years after High School Graduation ............. ................................. ............... 121

2-12e The Natural Log of 4 Consecutive Quarters of Earnings for White Women 14
Years after High School Graduation .......... ...... ... ................... .............. 122

2-12f The Natural Log of 4 Consecutive Quarters of Earnings for White Women 15
Y ears after H igh School G radiation .............................. ................. ...................122









2-13a The Natural Log of Annualized Earnings for White Women 10 Years after High
S ch ool G radu ation ......... ................................................................ .. .... .. .... .. 12 3

2-13b The Natural Log of Annualized Earnings for White Women 11 Years after High
S ch ool G radu ation ......... ................................................................ .. .... .. .... .. 12 3

2-13c The Natural Log of Annualized Earnings for White Women 12 Years after High
School G radu ation ......... ................................................................ .. .... .. .... .. 124

2-13d The Natural Log of Annualized Earnings for White Women 13 Years after High
School G radu ation ......... ................................................................ .. .... .. .... .. 124

2-13e The Natural Log of Annualized Earnings for White Women 14 Years after High
School G radu ation ......... ................................................................ .. .... .. .... .. 12 5

2-13f The Natural Log of Annualized Earnings for White Women 15 Years after High
School G radu ation ......... ................................................................ .. .... .. .... .. 12 5

2-14 The Labor Force Participation of White Women Age 28 33 Observed in the
L ab or F force at A g e 33 .................................................................. ................ .. 12 7















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

ESSAYS ON THE EFFECTS OF FAMILY AND SCHOOLING ON STUDENT
OUTCOMES

By

Mark Hoekstra

August 2006

Chair: David Figlio
Major Department: Economics

This dissertation examines the effect of changes in family structure and university

selectivity on the outcomes for students. In the first paper, I examine the effect of

parental divorce. Previous research has identified the effects of parental divorce

primarily by comparing the outcomes of children whose parents divorced to those of

children in intact families, conditional on observable characteristics. In contrast, this

paper identifies the effect of parental divorce on educational outcomes by comparing the

outcomes of children whose parents divorced to those of children whose parents filed for

divorce but later had the cases dismissed.

Using a panel of child-level administrative data on reading and mathematics

standardized test scores and disciplinary records for a large Florida school district, I find

no evidence that parental divorce negatively affects children overall. In contrast, I find

that experiencing parental divorce 6 years earlier causes girls to score over 14 percentile

points higher on tests of reading achievement, relative to the alternative. I also find some









evidence for a positive effect on the mathematics achievement of girls and a negative

effect on the reading achievement of boys, although those results are less precisely

estimated and less robust.

In the second paper, I estimate the effect of attending a state's flagship university

on earnings from ages 28-33. Doing so is typically difficult because those who are

accepted at and choose to attend more selective schools typically would have higher

earnings later on due to other factors such as higher ability, motivation, or family support.

To solve that problem, I use a regression discontinuity design that effectively compares

the earnings of students who were barely accepted at the flagship to those of students

who barely missed the cutoff. I find suggestive evidence of a positive effect on the

earnings of white men ranging from 1% to 25%, the magnitude and statistical

significance of which depend on the functional form used. I find no consistent evidence

of an effect on the earnings of women generally, although I do find that white women

with a strong attachment to the labor force have significantly higher earnings as a result

of being accepted at the state flagship university.














CHAPTER 1
"JUST KIDDING, DEAR": USING DISMISSED DIVORCE CASES TO IDENTIFY
THE EFFECT OF PARENTAL DIVORCE ON STUDENT PERFORMANCE

1.1 Introduction

The increased incidence of divorce in American families was undoubtedly one of

the most significant social trends of the 20th century. Although divorce rates have

declined slightly recently, the number of divorces per 1,000 married women aged 15 and

older more than doubled from 9.2 in 1960 to 19.5 in 1996, and demographers project that

if current rates of divorce continue, approximately 50% of recent first marriages will end

in divorce. The impact of this trend on children is clear: over 1 million children are

affected annually by divorce.

In a rare example of unity between liberals and conservatives, concern regarding

the implications of parental divorce for children's well-being has been expressed by

politicians across the political spectrum. President George W. Bush has stated that "the

most effective, direct way to improve the lives of children is to encourage the stability of

American families" (2002a). Senator and former First Lady Hillary Rodham Clinton has

also shown concern regarding the effect divorce has on children, saying, "The instability

of American households poses great risks to the healthy development of children" (1998,

p. 39). These concerns have resulted in several political movements toward divorce

reform. Three states have passed "covenant marriage" laws, which introduce a second

tier of marriage that offers more limited grounds for divorce and require pre-divorce

counseling. Perhaps more importantly, there has also been a political movement toward









legislation that would change no-fault and unilateral divorce laws to make it more

difficult to get a divorce when children are involved; at least eight states have considered

such legislation since 1996 (Friedberg, 1998).

The common belief underlying nearly all policy statements on this issue is that

divorce causes children to be worse off than they would be if their parents had stayed

together. An equally common view in policy circles is that this belief is not motivated by

ideological agenda but is rather a well-documented empirical fact. For example, in

remarks made to the Chamber of Commerce in Charlotte, North Carolina, President

George W. Bush stated

Research shows that two-parent families are more likely to raise a child that is
going to go to high school or college, that a child in a two-parent family is less likely to
get addicted to drugs. Now, I understand there are some families that just simply aren't
meant to be. I know that. I'm not-I'm wise about that. On the other hand, we ought to
aim for a goal, a goal that recognizes the power and importance of two-parent families in
America." (2002b)

Similarly, in It Takes a Village, Hillary Rodham Clinton wrote, "Recent studies

demonstrate convincingly that while many adults claim to have benefited from divorce

and single parenthood, most children have not" (1998, p. 39).

It seems, however, that this is one more area in which the causal link has been

made in the political arena before it has been convincingly demonstrated in academia.

Despite all of the interest in divorce and its effects on children, serious methodological

issues limit the extent to which academic researchers have been able to determine the

causal link. While there is clearly a strong association between family structure and child

well-being, the central problem is that it is difficult to determine what child outcomes

would result if troubled marriages that might otherwise end in divorce were to continue.

Put differently, the challenge at hand is to separate the underlying causes of divorce and









their effects on children from the effects of the divorce itself. Determining the nature of

these causal relationships is very important for public policy, since the scope of public

policy is largely limited to increasing the costs to the parents of getting a divorce and

forcing the couple to reconcile, rather than solving the underlying problems directly.

While researchers have made some progress toward meeting this challenge, data

limitations have continued to impair efforts at determining whether the effects captured

are those of the divorce or of some unobserved variable that is in fact causing both the

divorce and the child outcomes. Such limitations have caused McLanahan and Sandefur

to lament the fact that because no randomized experiment is feasible, analysts will never

be able to agree on the causal role of family structure in child outcomes (p. 11, 1994),

while Gruber states that the evidence "has yet to convincingly address potential selection

biases associated with the decision to divorce" (p. 2, 2000).

Clearly such pessimism is not the result of a lack of interest or effort by academics.

Indeed, as Gruber (2000) has noted, there are vast literatures in economics, sociology,

and developmental psychology that examine the consequences of divorce. Although the

early studies were cross-sectional, more recently the trend has been toward doing event

analyses of divorce that control for as many pre-divorce student and family

characteristics as possible. These studies essentially identify the effects of divorce by

comparing the outcomes of children who experienced parental divorce to those of

children in intact families, conditional on pre-divorce observables. However, this

identification strategy only works to the extent one is able to control for every

conceivable difference between families that divorce and families that do not, which is a

difficult if not impossible standard for any data set to meet. This problem is exacerbated









by the fact that the outcome variables used (such as high school graduation, years of

education, and earnings) are not observed prior to the parental divorce, so one cannot

even control for the pre-divorce level of the outcome measure used. Consequently, the

conditional outcomes of children of intact families may not represent the correct

counterfactual of how well off children of parental divorce would have been had their

parents stayed together for an exogenous reason. To estimate the true effect of divorce,

one must then be able to separate the effects of the unobserved process evident prior to

the filing of the divorce from the effects of the marriage dissolution itself, something that

is difficult to do by comparing children from intact families to children from families that

experienced divorce. A better approach would be to utilize data not only on children

whose parents divorce, but also on children whose parents file for a divorce that is later

dismissed, the latter of which would effectively form the control group. This is precisely

the identification strategy that I propose.

I am able to do this by combining two exceptional data sets. The first consists of

an eight-year panel of detailed data on every student in grades 1 through 12 in the

Alachua County school district, which is the 194th largest district in terms of enrollment

among the more than 16,000 school districts in the United States. The second data set

consists of public records on divorces filed in Alachua County from 1993 2003. I

merge these into one data set matching parent names, child names, and child birth dates

found in both data sets. By constructing a data set in this way, I can examine the effects

of parental divorce on children's standardized reading and mathematics test scores as

well as discipline problems at the micro level of the children themselves. This is the first

research that uses individual-level data for which the educational outcomes of students









are observed prior to parental divorce, which enables me to use student-specific fixed

effects. Furthermore, this is the first research that utilizes a data set that identifies the

children of parents who file for divorces that are eventually dismissed rather than granted,

in addition to children whose parents did divorce. By comparing children whose parents

dismissed divorce cases to the children of parents who actually divorced, I can

distinguish the effects of divorce from those of the underlying causes of divorce, the

latter of which are evident in both families.

The results lend little support to the idea that parental divorce negatively affects the

academic achievement of students overall. Although I find that students who

experienced parental divorce have lower reading and math scores and more disciplinary

problems afterward relative to children from intact families, I find a similar (and

stronger) result when comparing the outcomes of children whose parents filed for divorce

but later decided against it to those of children from intact families. This suggests that

the so-called consequences of divorce found by comparing children of divorce to children

of intact families are likely consequences of the factors that caused the parents to divorce

rather than of the divorce itself. Indeed, when comparing the outcomes of children whose

parents divorced to children whose parents filed for and dismissed a divorce case, I find

no negative effect of divorce overall. In fact, I find that experiencing a parental divorce

six years ago causes girls to score 14.68 percentile points higher on reading tests than

they would have had their parents stayed together, a result that is both statistically

significant and robust. I find somewhat weaker and less robust evidence that parental

divorce has a positive effect on the mathematics achievement of girls and a negative

effect on the reading achievement of boys. Finally, the results suggest that experiencing









parental divorce causes an increase in disciplinary problems immediately after the

divorce, but that there is no effect 4 years after the divorce.

1.2 Theoretical Considerations, Literature Review, and Identification Strategy

1.2.1 How Divorce Affects Student Achievement

There are several mechanisms through which divorce may affect the academic

achievement of children. A child whose parents divorce may experience less parental

attention and assistance with school work at home, thus reducing child learning. Parental

absence may also reduce the average quality of the assistance received at home, further

lowering school performance. For example, the custodial parent may now be the one to

assist a child in a subject area in which the absent parent would have been more able to

help. The child may also experience less parental guidance as a result of divorce,

allowing the student to lose focus in school. The overall trauma of the divorce and

family structure change may also distract a child from school activities, at least

temporarily. A divorce may lower the level of economic resources available for the

child, leading to a reduction in the quantity and quality of non-school educational inputs

purchased for the child, causing the child to be worse off. Finally, a child may have to

move as a result of the divorce, forcing the child to adapt to a new house, neighborhood,

and perhaps even school. Some research has suggested that moving itself negatively

affects academic achievement (e.g., Haveman, Wolfe, and Spaulding, 1991).

It is important to note, however, that not all of the ways in which divorce can affect

children are negative. For example, although the loss of contact with a divorced parent is

typically assumed to have negative consequences for the child, divorce may be beneficial

if the divorced parent is abusive or alcoholic. Furthermore, parental conflict itself may

lead to a reduction in the quantity or quality of parental inputs for the child's education as









well as distract the student from focusing on school. To the extent that divorce reduces

parental conflict, children may perform better academically. Consequently, while

divorce may affect child outcomes though any of several mechanisms, the net effect of

divorce is theoretically ambiguous.

The effect of divorce need not be permanent, either. Depending on the extent to

which parent and child overcome the trauma from the change in family structure and

successfully adapt to the new circumstances, it is quite possible that the effect of divorce

may change over time.

1.2.2 A Review of the Literature

The early research on divorce consisted mainly of cross-sectional studies that

compared the outcomes of children from intact families to those of children from

divorced families (e.g., Keith and Finlay, 1988). Several researchers have noted,

however, that there are significant differences in the pre-divorce observable

characteristics of families that experience divorce relative to those that do not. In an

effort to control for pre-divorce characteristics of families, some studies have used

retrospective data on variables such as self-reported parental conflict (e.g., Amato and

Booth, 1991). More recently, the trend throughout the literature is to use longitudinal

data to accurately control for some pre-divorce student and family characteristics such as

the student's cognitive test scores, family income, and parent's education (e.g., Cherlin,

Kiernan, and Chase-Lansdale, 1995; Borgess, 1998; Lang and Zagorsky, 2000; Painter

and Levine, 2000; Ermisch and Francesconi, 2001a and 2001b; Fronstin, Hill, Yeung,

and Duncan, 2001; Greenberg, and Robins, 2001; Deleire and Kalil, 2002;). With the

exception of Lang and Zagorsky (2000), these studies have found that divorce has

negative consequences for children.









Although this research does illustrate that it is important to control for pre-existing

differences in divorced and intact families, significant problems remain. First, several

studies rely on self-reported measures of parental conflict. For such measures to be

properly used, it must not only be the case that the measures accurately capture the

parental conflict that may impact children's outcomes, but it must also hold that such

measures of conflict are comparable across households. Similar problems exist when

using measures of children's psychological well-being.

Second, the primary child outcomes that researchers have used, such as marital

status, educational attainment, and earnings, are observable only when the child reaches

adulthood. Consequently, researchers examining those outcomes can only control for

pre-divorce differences in family characteristics and not in child outcomes themselves.

Third, and most importantly, there is significant reason to believe that controlling

for pre-existing levels of family characteristics and child outcomes may be inadequate.

For example, it is easy to conceive of an unobserved variable that determines both a

child's outcome and the family structure. This unobserved variable may be a process that

causes parental relations to worsen to the point that parents select into divorce, while at

the same time negatively affecting the children. Since this is a process and not merely a

level of family or child characteristics (after all, by definition the parents had not yet

divorced at the time of the pre-divorce observation), controlling for pre-divorce

characteristics or outcomes will not adequately measure how well off the children would

be if the parents did not divorce. Consequently, even conditional on pre-divorce

observables, the outcomes of children of intact families may not be the correct

counterfactual for children who experienced parental divorce. In contrast, by using the









outcomes of children whose parents file for a divorce that is later dismissed as an

estimate of the counterfactual, my identification strategy is able to separate the effect of

the divorce from the effects of the processes that caused the divorce.

There have been other attempts at overcoming the selection effects associated with

parental divorce. Sandefur and Wells (1999) used sibling information to identify the

effects of divorce by comparing siblings with varying exposures to single-parent families

or changes in family structure to each other. Ermisch and Francesconi (2001a) used a

similar sibling strategy. However, within-family comparisons will be flawed if siblings

are affected differently by divorce, whether due to age or other reasons. More

importantly, sibling strategies will also lead to downward-biased estimated effects of

divorce if there is an underlying family trend over time that determines both family

structure and child outcomes. Furstenberg and Kiernan (2001) used a slightly different

strategy and compared the outcomes of children who experienced divorce to those of

children whose parents divorced after the children had grown up. That approach,

however, will fail when there are significant pre-divorce trends or when there are

unobserved differences in the intensities of the underlying problems leading to the two

types of divorce, both of which are very plausible possibilities.

Gruber (2000) approached the selection problem by exploiting variation in the

unilateral divorce laws across states and over time. That approach, however, may not

overcome the selection problem if there were underlying trends that led states to pass

unilateral divorce laws at different times or if, as Gruber noted, those laws had an effect

on children in ways other than through divorce. Indeed, the basic problem is that in

addition to being concerned with unobserved variables in families that experience









divorce, since the variation used to identify the effects of divorce in Gruber's approach

occurred at the macro (state) level (instead of the individual level), one must also be

concerned about unobserved characteristics at the state level that might lead to worse

outcomes through means other than an increased propensity for divorce.

Other research on the consequences of divorce has focused on examining the

effects of separation by parental death (Fronstin, Greenberg, and Robins, 1999; Lang and

Zagorsky, 1999; Corak, 2001). This allows researchers to identify the effects of the

complete loss of parental contact and supervision as well as of economic support.1

However, in nearly all cases the underlying processes that cause divorce are substantially

different from those that cause spousal death.2 Consequently, an examination of the

effects of parental separation by death does little to shed light on the issue of what would

happen to children whose parents divorced if an exogenous force such as increased costs

of divorce had prevented them from doing so.

1.2.3 Identification Strategy

The identification strategy employed in this paper is most similar in spirit to that

used by Bound (1989), who estimated the disincentive effects of Social Security

Disability Benefits by comparing the labor outcomes of rejected disability applicants to

those of accepted disability applicants. Bound concluded that disability benefits

accounted for substantially less than half of the postwar decline in the labor force

participation rates of older men and that previous cross-sectional strategies had

exaggerated the causal disincentive effects. The purpose of this paper is to determine



1 Unobserved life insurance payouts may complicate the issue of economic support, however.
2 A notable but rare possible exception is spousal homicide.









whether or not a similar story is true with respect to the causal effects of parental divorce

on student outcomes.

To do that, I compare the annual standardized test scores and disciplinary records

(number of infractions per year and days suspended per year) of children whose parents

dismissed divorce cases to those of children whose parents divorced. Since I observe

outcomes for each student in every year, I am able to utilize student-specific fixed effects,

allowing for both a time-invariant shock effect of parental divorce as well as an effect

that changes over time. By identifying the effects of parental divorce by comparing not

the achievement levels but the changes in the test scores of children whose parents

divorce to those of children whose parents dismiss divorce cases, I lessen the possibility

that the effect I estimate is really an effect of an unobserved variable correlated with

divorce and not of the divorce itself. Still, my data allow me to test the validity of this

identification strategy in two ways:

* Do the observable characteristics of the two groups look similar prior to the parents
filing for divorce? To the extent that there are differences, one might be concerned
that these differences may cause one group to trend differently in the post-divorce
period regardless of whether the couples divorced or not. I address this question in
Section 1.4.3

* Are there differences in the trends of the outcomes prior to the filing of divorce?
Again, to the extent that there are, one might be concerned that these trends may
continue in the post-divorce period regardless of whether the marriages ended in
divorce or not. I address this question in Section 1.4.5.

Although the variation I exploit in this paper is not exogenous, there is reason to

believe that the selection at work would imply that the estimated effects of parental

divorce on student test scores will be biased downward, if at all. For example, those

couples who decide to have the divorce case dismissed may do so in part out of concern

that the divorce may adversely affect their children, which for reasons discussed earlier is









a widely held belief. To the extent that the increased concern for children in this group

(the control) might have caused the post-divorce case scores of their children to trend

upward over time relative to the divorce group even had they divorced, my estimates will

be downward biased. Second, it could also be the case that the parents who dismiss their

divorce cases do so because they experienced a positive shock to their marriage during

the divorce process that may cause them to rationally expect their marriage to improve

significantly in the future, whereas those couples who divorce do not. Again, to the

extent that this would cause the test scores of children whose parents dismissed divorce

cases to trend up relative to those of children whose parents divorced, my estimates will

be downward biased. Finally, those parents who choose not to divorce may do so simply

because their marriages are not as bad as those of parents who divorce.3 If this implies

that the children whose parents dismissed divorce cases would learn at a faster rate

afterward than would the appropriate control group ideally characterized by families that

would have experienced divorce if not for some exogenous force, then this too would

cause my estimates of the parental divorce effect on test scores to be biased downward.

Together, these possibilities suggest that the selection at work in my identification

strategy should, if anything, bias my estimates of the effect on test scores downward,

implying that any positive effect would be a lower bound.









3 This would be similar to the problem with the traditional identification strategy of comparing children
whose parents divorce to children whose parents stay together, although one might reasonably expect that
the extent of the bias would be smaller here since both groups of couples filed for divorce.









1.3 Parental Divorce and Student Test Scores

1.3.1 School Data

To address the effects of divorce, I use a confidential student-level data set

provided by the School Board of Alachua County in the state of Florida. This data set

consists of observations of students in the first through twelfth grades for the academic

years of 1993-94 through 2002-2003. The Alachua County School District is large

relative to school districts nationwide; in the 2000-2001 school year, there were on

average 2,200 students in each grade, making it the 194th largest school district among

the more than 16,000 districts nationwide. The student population was approximately

56% white, 36% African-American, 4% Hispanic, and 2% Asian. Forty-four percent of

students were eligible for subsidized lunches.

For each first- through tenth-grader I observe norm-referenced standardized test

scores in reading and mathematics. The test scores reflect the percentile ranking on one

of two national tests relative to all test-takers nationwide. Prior to the 1999-2000

academic year, nearly every student in the third through ninth grades took the Iowa Test

of Basic Skills (ITBS). In addition, at the discretion of the school principal, many first

and second-graders also took these exams. Starting in the 1999-2000 school year all

first- through tenth-graders were tested using the Stanford 9 test. This change was made

because the Stanford 9 test is used for the Florida Comprehensive Assessment Test

(FCAT) that was introduced in the 2000-01 school year to enable the state of Florida to

evaluate schools. Both the ITBS and the Stanford 9 are exams used by schools

nationwide to test mathematics and reading. Except for some first and second graders

prior to 2000, almost all students took the tests in a given year. As described later,









however, observations on some students were dropped in order to ensure a clean

comparison.

In addition, student records also contain the names and addresses of the parents of

each student for each year. This information is gathered primarily during August of each

year during registration, although it is updated continually throughout the year. The data

on names are crucial because that is the information used to match divorce information to

the student records. Discipline records are also observed for every first- through twelfth-

grader, beginning in 1993 (prior to when the standardized testing records begin). Finally,

I observe information on each student's race, sex, school lunch status, disability status,

and gifted status.

In the following analysis, I use four dependent variables from these school data.

The primary outcomes that are used are the mathematics and reading scores on the Iowa

Test of Basic Skills or Stanford 9 examinations. In addition, I also look at two outcomes

from the disciplinary records for each year, including the total number of days each

student was suspended and the total number of disciplinary infractions each student

committed.

1.3.2 Divorce Data

The divorce data used in this study were gathered from public records information

at the Alachua County Courthouse. This information includes the names of every

husband and wife who filed for a divorce at the Alachua County Courthouse between

January 1, 1993 and March 12, 2003. For each filing, I retrieved the filing date, the final

judgment date, and the final judgment type. In addition, I also obtained child names and

birth dates for certain divorce cases by personally examining the files at the Alachua

County Courthouse, as described in Section 1.3.4.









1.3.3 Divorces in Alachua County, Florida

In order to file for a divorce in Florida, at least one of the parties in the marriage

must have resided in Florida for at least six months. There are then two filing types. If

there are no minor or dependent children of the marriage parties and if the marriage

parties agree about how to divide property and that the marriage is irretrievably broken,

they may file for a Simplified Dissolution. However, if there are children involved, the

couple must file for a Dissolution of Marriage. All divorce information used in this study

is obtained for couples who have filed for the general Dissolution of Marriage.4

In order for the court to grant the dissolution of the marriage, the court must either

rule that the marriage is irretrievably broken or that one of the marriage parties has been

judged mentally incapacitated for a minimum of three years.5 The court may then choose

to do any of several things seen as in the best interests of the marriage parties and

dependent children, such as ordering that either or both marriage parties consult with a

person deemed qualified by the court (e.g., a marriage counselor) and found accepby the

ordered party or parties, or extending the proceedings no more than three months to

enable the parties themselves to effect a reconciliation. During any period of

continuance, the court can make orders regarding alimony and support for the parties,

child custody and visitation rights, property division, and so on. Although there is no

mandated pre-divorce waiting period in Florida, if there are minor children of the



4 This includes nearly all divorce-seeking couples with children. Although having children violates a
condition for filing for a Simplified Dissolution, some such couples may exist. For example, if a couple
files for a divorce and mistakenly claims that the wife is not pregnant when she in fact is, they may file for
a Simplified Dissolution. These sorts of exceptions are probably very rare, however, and to the extent
young children are involved, my data set would not be changed anyway.

5 Not surprisingly, the "irretrievably broken" clause is the path most commonly tread by those seeking
divorce in Alachua County, Florida.









marriage, then prior to obtaining a final hearing each parent is required to attend one of

seven four-hour parenting education classes approved by the 8th Judicial Circuit Court.

Finally, if after the final hearing the court finds that the marriage is irretrievably broken, a

final order of dissolution of marriage is given. Alternatively, if the parties work out the

problems, the petitioner may have the case voluntarily dismissed. The judge may also

notify the parties of intent to dismiss if they have not fulfilled their obligations to the

court. Within a month after this intent to dismiss is issued, the judge may order that the

case be dismissed. Within days of the resolution, the case is closed. For reasons

discussed in the next section and seen in 9, this study uses only those dismissed divorce

cases in which the petitioner specifically requested that the case be dismissed.

1.3.4 Merging the Divorce Data with the School Data

Since my primary identification strategy depends crucially on correctly matching

children in the school data to divorces filed in Alachua County, every effort was made to

ensure that those matches that were made were correctly made. Consequently, divorces

were matched to students' parents using a created variable:

FirstnameparentiLastnameparent Firstnameparent2Lastnameparent2.

Only unique couple-name combinations were used. Consequently, if John and

Mary Smith were observed to have filed for more than one divorce case from January 1,

1993 through March 12, 2003, those divorce cases were not matched to students.6

Similarly, if in the school district in any given year from 1993 through 2003 there were

two or more children who were not siblings but who had parents with identical names,


6 In reality, the uniqueness standard was applied more strictly than this. In the divorce data I observe up to
nine names for both the husband and the wife, due to the fact than any address or name changes must be
disclosed to the court. If any first-last name couple combination for a given divorce was identical to that in
another divorce case, that divorce case was not matched.









those children were not matched to any divorce. Siblings were defined as children who

shared the same last name and lived at the same residential address.

Divorces were matched to students on a year-by-year basis. Since the parental

name information from the school district is from fall registration in August of each year,

these parental names were matched to divorces filed from August lst of that year through

July 31st of the following year. This was done to increase the likelihood that the parent

names from the school district used to match to divorces were both present. In contrast,

if one were to try to match August names to a divorce filed in January of that same year,

the parent names in the school data may not both be present or may have changed since

the divorce was filed.

Table 1 shows how many divorces have been filed in Alachua County, Florida,

from January 1, 1993, through March 12, 2003. The also shows how the number of total

divorce cases varies from the number of divorce cases expected to be associated with

children in the public school system. For example, in the year 2000 there were 1,123

divorce cases filed, of which 974 were General Dissolutions (a necessary but not

sufficient condition for the case to have children involved.) Of those, 904 had unique

parent name combinations. A random check of 100 General Dissolutions from 1993-

2003 indicated that 54% of the marriages had minor children of that marriage, implying

that an estimated 488 of those divorce cases may be expected to have minor children of

the relevant marriage involved. Since I match divorces only to children in grades one

through twelve and approximately 10% of students in the county attend private schools,

there were approximately 293 divorces in 2000 that I could reasonably expect to match.

Given that about 10% of the parent name combinations in the school data were









nonunique, there remained approximately 264 divorces filed in the year 2000 that I could

expect to match. In all, I could reasonably expect to have matched at most 2,512

divorces. While I do not claim that this is the exact number of matchable divorces, it is

my best guess as to how many I could expect to match.

As shown in Table 2, I matched 724 divorce cases to names in the school data

using the parent name identifier7, for a match rate of 28.8%. Of those 724 divorce cases,

583 were matched to a student for whom I observed at least one test score. Of those

matches made to children observed with at least one test score, a random check of 100

children matched to divorces suggested that an estimated 97 percent of the matches made

were made correctly.8

However, only 66 of those 724 matched divorce cases had been dismissed. In

order to increase the sample size of dismissed divorce cases, I went to the Alachua

County Courthouse and looked up all dismissed divorce cases with unique parent name

combinations that were filed from January 1, 1993 March 12, 2003. I then matched

these dismissed divorce cases to children in the school data for which the first and last

name of the child matched along with at least one of the following two identifiers (and

none contradicted significantly9)



7 The matches in Table 2 include only matches made to children whose parents were believed to be the
natural or adoptive parents of that child. I defined parents as the natural or adoptive parents of a child when
the child shared his or her last name with at least one of the parents listed by the school district in the year
before or in the year in which the divorce case was filed.

8 This was done by manually looking up the divorce judgment papers for each of 100 randomly selected
matches made and comparing the child's name from my matched data to the names of the children in the
divorce papers. All observations matched to the three cases that were incorrectly matched were dropped
from the data set.

9 For example, if the date of birth in one file said 8/16/1985 and the date of birth in the other file said
8/16/1986, I made the match provided that the child name and parent names matched.









* child's date of birth

* parents' names

Furthermore, only dismissed divorce cases in which one spouse was not found to

be deceased were matched. At this point, some adjustments were made to the matched

set of students matched to a dismissed divorce case in order to ensure a proper

comparison, the impact of which is shown in Table 3. First, all observations matched to a

divorce case that had been dismissed by the judge (as opposed to ones in which the

petitioner requested the dismissal directly) were dropped from the data set. Although it

may not at first seem intuitive why one would want to eliminate those dismissed cases

from the data set, it becomes evident from looking at the characteristics of both groups

prior to filing for divorce, as shown in columns C and D of Table 9. For example, the

average reading score of children whose parents later filed for a divorce that was

dismissed due to something other than a direct request by the petitioner was 33.3, while

the average reading score of children whose parents later filed for and specifically

requested the dismissal of a divorce case was 57.3. Similar differences are evident

between these two groups with respect to math scores, subsidized lunch status, and the

percent black.

In addition, since I want to ensure that the dismissed divorce cases in the data set

were not caused by a threat of violence by one spouse to the other, I acquired data on

domestic violence cases filed from 1993-2003. I then matched domestic violence cases

to the school data by matching the parent name combinations in the domestic violence

cases to parent name combinations in the school data set. The observations of students

who were matched to a domestic violence case were then dropped from the data set.









Finally, all observations matched to students for whom only one parent name was

listed by the school district in the year prior to that in which the divorce was filed were

dropped from the data set, since those children could not have been matched to a case

that ended in divorce due to the nature of the matching algorithm described above. The

absence of a parent in the school records could reflect unobserved negative family

characteristics. In addition, it is unclear exactly what a divorce means for a family for

which only one parent name is listed by the school district.

1.3.5 The Final Data Set Used in the Analysis

Although my primary identification strategy is to compare the outcomes of children

of actual parental divorces to those of dismissed parental divorces, in order to replicate

the methodology of other papers in the literature, I need to be able to identify children

who did not experience parental divorce from 1993 through March of 2003.

Unfortunately, the data do not contain this information. Consequently, I try to identify

these children in two ways. First, in the less restrictive method, I define two groups by

trying to eliminate those children who a) could not have been matched to a divorce, or b)

were likely to be in a single-parent family. Specifically, I removed from the data set all

observations of any child who met one of the following conditions:

1. Was observed with at most one parent's name for one year and was not matched to
a divorce in another year.
2. Was observed with parents whose names were not unique for any year from 1993-
2003 (after accounting for siblings) and thus could not have been matched to a
divorce case in that year.
3. Was observed with parents whose names were the same as those associated with
more than one divorce from 1993-2003.









Although the primary cross-sectional results excluded students only on the basis of

the above conditions, as a check I also performed the cross-sectional analysis using data

in which I also excluded each student that met the following condition as well:

4. Was observed to have a different last name than at least one of the parents listed by
the school district.


The purpose of these deletions is to ensure that those students who remained did

not experience parental divorce and form the counterfactual used in previous researchers'

identification strategies. In addition, I drop all observations of students for whom the

first and last names of both parents changed over time.

The result of leaving out these students based on conditions 1 through 3 is to reduce

the overall sample size from 1,500-2,000 students/grade/year to 400-700

students/grade/year. In all, the data used to compare children of divorce to children

whose parents did not divorce consist of 60,196 observations on 17,241 children from

1993-2003 (35,055 observations on 9,654 children when conditions 1-4 are used). The

descriptive statistics of these students in the year 2000 can be seen in columns A and B of

Table 9. It is clear from these columns that the more restrictive sample (column B) does

appear to eliminate students whose parents are not married or for whom a grandparent is

listed as a parent, even though it may also eliminate children whose parents are in fact

married.

In the main analysis in which only children whose parents filed for divorce are

included, there are 6,761 observations on 1,028 children whose parents filed for one of

716 divorce cases. A total of 93 of those divorce cases were dismissed, affecting 156

children. The first row of Table 4 shows how observations of these two groups of









students are distributed over time. It shows that approximately 75% of the children

linked to a divorce case are observed after the divorce. This proportion of children

declines steadily; approximately 20-25% of students linked to a divorce are observed at

least five years after their parents' divorce case was closed.

When only observations linked to at least one test score are included, there are

27,102 observations on 9,388 children in the data set that includes children whose parents

never filed for divorce and those whose parents did file for divorce. In the data set used

in the main analysis in which only children whose parents filed for divorce were

included, there are 3,525 observations on 801 children, representing 580 divorce cases.

There are 111 children linked to 93 dismissed divorce cases. The second row of Table 4

shows how observations on students matched to parental divorce cases were distributed

over time. Approximately 75-80% of the students matched in each group are observed

with a test score after the divorce case was closed. As shown in Table 4, approximately

35% of students matched to divorce are observed 3 to 5 years after the case is closed,

while approximately 20-30% are observed with a test score more than 5 years after the

divorce case was closed.10

Overall, the distribution for the group of children whose parents divorced is quite

similar to the distribution for the group of children whose parents filed for a divorce that

was later dismissed, with the exception that more than 5 years after the divorce or

dismissal, I tend to observe relatively more (5 to 10 percentage points) students who



10 For the entire sample of observations (some of which do not have a test score), the time after the divorce
is defined as the calendar year of the observation minus the year in which the divorce case was closed. For
the subset of observations for which there is at least one test score, the time after the divorce is defined as
the number of years between the date the divorce case was closed and the date of the test and thus is not
necessarily an integer.









experienced a dismissed divorce than those who experienced parental divorce. While

this could be due to the fact that children whose parents later divorce are on average

slightly older (1.6 years) than their peers whose parents file and dismiss a divorce case,

later in the paper I nevertheless examine the sensitivity of the results by reestimating the

results after excluding all observations 5 or more years after the closure of the divorce

case. However, the overall similarities in the distributions of the observations in the two

groups is important because one might be concerned that children who are negatively

affected by divorce leave the county and thus the sample. The overall similarities in the

distributions indicates, however, that for attrition to bias the results, it must not only be

the case that children whose parents divorced do so at the same rate as those whose

parents dismissed a divorce case (at least for the first five years afterwards) but also that

those in the two groups who did leave were affected by the closure of the case in different

ways. While not impossible, such a scenario does seem unlikely.

1.4 The Effects of Divorce on Student Performance

1.4.1 Comparing the Test Scores of Children of Divorce to Those of Children in
Intact Families

A common finding in the divorce literature is that children of divorced parents

experience poorer outcomes than do children who are brought up in two-parent

households. Even though this approach has serious flaws, it is still constructive to test

whether my data appear to be qualitatively similar to data used in previous research. To

test for the unconditional cross-sectional effects of divorce, I estimated a regression using

pooled data in which I control only for year and grade effects to remove the effect of any

trend over time in percentile test scores in the school district (whether caused by a change

in the test used or something else.) The general regression equation was









test,t = bo + bl X + b2 PostDivorcet + ,t

where testit is the test score of student i at year t and Xis a vector of covariates one

expects to affect test scores. The variable PostDivorce is equal to one if the test was

taken after the child's parents finalized their divorce.

The results for reading and math test scores are given in Tables 5 and 6,

respectively. The p-values are given in the second row of each cell, which were

calculated using standard errors clustered at the family level.1l When only student grade

and year effects are included as covariates, parental divorce is associated with reductions

of 1.97 and 1.31 percentile points in reading and math, respectively, although neither is

statistically significant at conventional levels. As other researchers have noted, however,

there are significant differences in the observable characteristics of children whose

parents divorce compared to those of children whose parents remain married. My data

allow me to condition on several important variables, including race, sex, school lunch

status, and zip code median family income, and squared zip code income. Although

including these variables may cause an upward bias in the test score estimates due to the

fact that some could themselves change as a consequence of divorce (e.g., subsidized

lunch status), it is still worthwhile to include them to see if their inclusion explains the

differences between children whose parents divorce and children whose parents do not

divorce. The top sections of row (b) in Tables 5 and 6 contain these results and suggest

that parental divorce is associated with reductions of 2.19 and 1.32 percentile points in

reading and math, respectively, the former of which is statistically significant at the 10%



1 The school district does not identify families, so although I identify families for children whose parents
filed for divorce, for the other children I assumed each was in a separate family.









level. The top section of row (c) also includes school fixed effects.12 There, the result

indicates that parental divorce is associated with reading and math scores that are 0.78

and 0.48 percentile points lower, respectively, although neither estimate is statistically

significant at the 10% level.

These data also allow me to examine the extent to which the impact of divorce

affects children differentially based on the grade at which they experienced parental

divorce, represented by DivorceGrade variable in the equation below. In addition, I can

examine how the effects of divorce grow or diminish over time by including an

interaction term measuring the number of years after the divorce when the test was taken.

Consequently, the general form of the regression estimated is given by

test, = bo + bl X + b2 PostDivorcet + b3 YearsAfter*PostDivorce

+b4 DivorceGrade *PostDivorce + ,t.

The results given in the bottom of row (b) in Tables 5 and 6 suggest that the

association between having experienced parental divorce and lower test scores grows

over time. I find that reading and math scores fall by approximately 0.79 and 1.26

statistically significant percentile points, respectively, in every year after the divorce. In

the case of reading achievement, the statistically significant coefficient of 1.23 on the

grade of the student at the time of the divorce indicates that divorce is less negative for

the child when it occurs when the child is older. As shown in the far right column,

experiencing a parental divorce while in the 4th grade is associated with statistically

significant declines of 3.87 and 5.25 percentile points on math and reading tests 6 years

later.

12 The student's school was only observed for students for whom I observed at least one test score in that
year. In addition, prior to the 1999-2000 school year, I observed the school only for 3rd 5th graders.









In the bottom of row (c), the results are shown when school fixed effects are

included in the model. While the association between lower math scores and parental

divorce is not changed much by the inclusion of the school effects, the association

between parental divorce and worsening reading scores over time is smaller than when

school effects are not included, reducing that effect for the hypothetical 10th grader whose

parents divorced 6 years prior to a statistically insignificant -1.79 percentile points.13

Tables 7 and 8 contain similar analyses using the number of days suspended per

year and the number of disciplinary infractions per year as outcome variables. From

these tables, it is clear that having experienced parental divorce is associated with

statistically significant increases in both the number of days suspended per year and the

number of disciplinary infractions committed. Experiencing parental divorce is

associated with 0.79 more days suspended per year and 0.39 more disciplinary infractions

per year, both of which are statistically significant at the 1% level. By comparison, the

average student in the data set is suspended for 1.2 days and commits 1 infraction per

year, implying that the cross-sectional correlations found are quite large. When the effect

of divorce was allowed to vary over time, each year after the divorce is associated with

increases of 0.16 days suspended and 0.07 infractions per year, although only the former

is statistically significant at the 10% level. As shown in the far right column of each

table, experiencing a parental divorce as a 4th grader is associated with committing 0.54

more disciplinary infractions and being suspended for 1.16 more days when in the 10th

grade, both of which are statistically significant at the 5% level. While the inclusion of



13 Just as with the income measures, it is possible that the school fixed effects pick up some of the effect of
parental divorce as well, which would cause these estimates to be biased upward. This is due to the fact
that moving to an area with a lower quality school may itself be a consequence of parental divorce.









school fixed effects does reduce these correlations to marginal statistical significance, on

the whole it does appear that experiencing parental divorce is correlated with more

disciplinary problems.

These cross-sectional correlations grow even stronger when using the more

restrictive definition of children whose parents were and remained married over the time

period. For example, although unreported, the negative cross-sectional effect of divorce

on reading scores for a 10th-grader 6 years goes from -3.87 (p=0.059) to -6.20 (p=0.004)

when students whose last name differs from that of a reported parent are not defined as

children whose parents were and remained married. Similarly, the negative cross-

sectional effect on days suspended increases to 1.46 (p=0.000) from 1.16 (p=0.004).

Given the potential problems with estimating the effects of divorce by comparing

children of parental divorce to children of intact families conditional on observable

characteristics, the important thing to note from the results in Tables 5 8 is not that

divorce has a negative effect. Rather, the point is that there is a cross-sectional

correlation between having experienced parental divorce, lower academic achievement,

and higher rates of disciplinary problems, even conditional on observable characteristics.

Whether or not this is indeed the true causal effect remains to be seen, and is the focus of

the remainder of the paper.

1.4.2 Do We Observe the Same Correlation when Comparing Children of Dismissed
Divorce to Children of Intact Families?

It is worth asking, however, whether or not similar associations are seen when

comparing the outcomes of children whose parents filed for divorce but did not divorce to

the outcomes of children in intact families. If experiencing a dismissed divorce case is

associated with worsening outcomes relative to children whose parents do not file for









divorce, it suggests that the correlations observed in the previous section are

consequences of the factors that caused the parents to file for divorce rather than of the

divorce itself. Results are contained in Tables 9 through 13.

The results are striking. As seen in the top of row b of Tables 9 and 10, a tenth

grade student whose parents filed for divorce 6 years earlier scores 6.42 and 3.78

percentile points lower on reading and math tests than his or her counterparts in intact

families, although only the effect on reading scores is statistically significant at the 5%

level. Similarly, the results in Tables 11 and 12 show that a 10th grade student whose

parents filed for divorce 6 years earlier commits a statistically significant 1.21 more

infractions/year and is suspended for a statistically significant 2.20 more days/year than a

student whose parents never filed for divorce.

As one would expect, the correlation between worse outcomes and experiencing a

dismissed divorce are even stronger when the more restrictive definition of a child in an

intact family is used. Although unreported, the so-called "effect" of a dismissed divorce

on the reading achievement of a 10th grader whose parents divorced six years prior

changes from -5.49 (p=0.170) to -8.03 (p=0.046) while the "effect" on math achievement

goes from -6.08 (p=0.141) to -7.33 (0.080).

Of course, these differences in the achievement and disciplinary behavior of these

children whose parents filed for divorce cannot be a consequence of divorce since the

parents did not in fact divorce. Again, this suggests that the correlations observed by

comparing children whose parents divorced to children whose parents did not are likely

not the effects of divorce itself but rather of the underlying reasons that caused the

parents to file for divorce.









1.4.3 How Similar are Families That Experience Divorce to Those That
Experienced a Dismissed Divorce?

Since my primary identification strategy uses children whose parents file for and

dismiss divorce cases as the "control" group against which to compare the children who

experience parental divorce, it is important that I compare the characteristics of these two

groups prior to the filing of the divorce cases. Table 13 presents descriptive statistics for

these two groups 0 to 3 years prior to filing the divorce in columns B and C. When a

child was observed more than once in this time period, I calculated the average value of

each variable from all observations of that child in that category. The numbers indicate

that these two groups appear similar to each other among observable characteristics, with

three exceptions. The first is that there are relatively more boys whose parents later filed

and dismissed a divorce case (60.0%) than whose parents later divorced (47.3%). The

second is that children whose parents later filed and dismissed a divorce case tend to have

more disciplinary problems than children whose parents later divorced. The third is that

children whose parents later filed and dismissed a divorce case are on average 1.6 years

younger than children whose parents later divorce. Despite the overall similarities

between these two groups, to ensure that the results are not driven by unobserved

differences between the two groups, I use individual student fixed effects to control for

any time-invariant differences in the family backgrounds of these children.

1.4.4 The Effect of Parental Divorce on Family Income

Before examining how parental divorce affects the academic achievement and

disciplinary problems of children, it is beneficial to ensure that my data show what one

would expect regarding the effect of parental divorce on family income. Unfortunately,

the only measure of family income recorded by the school district is school lunch status.









Although there is a consensus that school lunch status is a good measure of family

income for children in elementary school, the social stigma associated with free or

reduced lunch for children in middle and high school that lowers take-up rates makes it

much less reliable, particularly for my data set in which the vast majority of post-divorce

observations are for middle and high school students. This might especially be a concern

if students whose parents divorced are particularly unlikely to want to receive federally

subsidized school lunch. For this reason and because only a small percentage of children

are eligible for free or reduced lunches, I instead use the measure of family income at the

zip code level, which has been used as a proxy for family income by others (e.g., Fryer

and Levitt, 2004). The model estimated, which is the same as that estimated to determine

the effect of parental divorce on test scores and disciplinary problems, was

Familyncomet = 0, + bo Gradet + bl Grade2 t + b2 Yeart + b3 PostDivorceCaset +

b4 PostDivorceCaset *Divorcet + b5 YearsAfterCaseClosuret

b6 YearsAfterCaseClosuret *Divorcet + et

where Familylncome, is the median family income in the zip code of student i, 8, is

a student fixed effect, Gradet is the grade of student i at year t, and Yeart is a year fixed

effect. The variable PostDivorceCase is a dummy variable equal to one if the test was

taken after the parental divorce case was closed (whether due to a judgment of dissolution

or a dismissal) while the variable PostDivorceCase *Divorce is the interaction between

PostDivorceCase and a dummy variable equal to one if the parents' divorce case ended in

divorce (as opposed to a dismissal). The variable YearsAfterCaseClosure is the number

of years after the divorce case was closed (including dismissed cases) while the variable

YearsAfterCaseChni e "'Divorce is the interaction between the number of years after the









divorce case was closed and a dummy variable equal to one if the divorce case ended in a

judgment of divorce.

The results are given in Table 14 and indicate that every year after the divorce, the

family income of children whose parents divorce falls by $288 for every year afterwards

(p=0.465). Six years after the divorce case ended, average zip code family income fell by

$1,223 relative to their dismissed divorce counterparts, although that is not statistically

significant at the 10% level. Still, this result is comforting to the extent that one would

expect children whose parents divorce to move to lower-income neighborhoods relative

to children whose parents dismissed divorce cases.

1.4.5 The Pre-Divorce Trends of Children Whose Parents Later File for Divorce

One might also be concerned that the student fixed effects approach may be

insufficient if the pre-divorce trends of these two groups are different. In order to test

whether there is a statistical difference between the pre-divorce trends of these two

groups, I estimated the following equation similar to that which will be estimated to find

the effects of divorce

Outcome,, = 0, + bo Grade,t + bl Grade2, +b2 Yeart + b3 PreDivorceCaset +

b4 PreDivorceCaset*Divorcet + b5 YearsBeforeFiling +

b6 YearsBeforeFilingt*Divorcet + e

where Outcomet is the outcome variable for student i at time t, 0, is a student fixed

effect, Grade is the student's grade, and Year is a student fixed effect. The variable

PreDivorceCase is a dummy variable equal to one if the observation is prior to filing a

divorce case, while PreDivorceCaset*Divorce is a dummy variable equal to one only if

the observation was for a child whose parents would later file a divorce case and get

divorced. The variable YearsBeforeFiling is the number of years prior to filing a divorce









case, while the variable YearsBeforeFiling, *Divorce is equal to the number of years prior

to filing a divorce case that would end in divorce.

The coefficient of interest is thus b6, which essentially captures the difference in

the pre-divorce trends of children whose parents would file for and then dismiss a divorce

case relative to those of children whose parents would later divorce. If b6<0, it means

that as one goes back in time from the time of the divorce, children whose parents later

divorce get worse off relative to those who will experience a dismissed parental divorce.

Equivalently (and perhaps more intuitively), to the extent that b6<0, it implies that as the

time of the divorce filing approaches, the divorce group is gaining relative to the

dismissal group. Conversely, to the extent that b6>0, as the time of the divorce filing

approaches, the divorce group is dropping relative to the dismissal group.

The equation was estimated on a sample that excluded observations more than 3

years prior to the filing of the divorce in an attempt to capture trend differences that occur

relatively close to the decision to file for divorce. The results given in Table 15 show that

for neither test scores nor disciplinary problems was there a statistically significant

difference in the trends of these two groups prior to divorce.14

1.4.6 The Causal Time-Invariant Effect of Parental Divorce

I now turn to the main question of how these outcomes compare after the divorce

case has closed. By comparing the outcomes of children whose parents divorced to those

of children whose parents filed divorce cases that were later dismissed, I can effectively


14 When observations that occurred more than 3 years prior to the divorce filing are included, the
differences between the pre-divorce trends in reading and math scores as well as days suspended remain
statistically insignificant. However, there is a statistically significant difference in the pre-divorce trends
for the number of disciplinary infractions, suggesting that as the time of divorce approaches, children
whose parents later dismiss a divorce case commit 0.09 more infractions per year (p=0.095) than are
children whose parents later divorce.









separate out the effect of the divorce itself from the effects of the underlying causes of the

divorce. First I examine whether or not experiencing parental divorce has a time-

invariant effect on student test scores and disciplinary problems. The regression equation

estimated in order to address these issues was

Outcome = + bo Gradet + bl Grade2t + b2 Yeart + b3 PostDivorceCase,t +

b4 PostDivorceCase,t *Divorce,t + et.

The variable PostDivorceCase is a dummy variable equal to one if the test was

taken after the parental divorce case was closed (whether due to a judgment of dissolution

or a dismissal) while the variable PostDivorceCase *Divorce is the interaction between

PostDivorceCase and a dummy variable equal to one if the parents' divorce case ended in

divorce (as opposed to a dismissal). The standard errors used to calculate the p-values

reported in the tables were clustered at the family-year level.

The coefficient of interest in this equation is b3, which effectively captures the

effect of having experienced a parental divorce relative to having experienced the

dismissal of a parental divorce case. The results given in 16 indicate that parental divorce

does not have a statistically significant effect on reading or math test scores. Finally, the

results suggest that parental divorce causes children to be suspended 0.75 more days per

year and to commit 0.33 more disciplinary infractions per year, both of which are

statistically significant at the 5% level.

1.4.7 The Causal Effects of Parental Divorce Over Time

It may be, however, that the effect of parental divorce is a cumulative effect that

increases over time. My data allow me to examine how the outcomes of these two

groups change over time and whether or not they diverge from each other. The

regression equation estimated to address these issues was









Outcome = O0 + bo Gradet + bl Grade2t + b2 Yeart + b3 PostDivorceCaset +

b4 PostDivorceCaset*Divorcet + b5 YearsAfterCaseClosuret +

b6 YearsAfterCaseClosureit*Divorceit + et.

The variable YearsAfterCaseClosure is the number of years after the divorce case

was closed (including dismissed cases) while the variable

YearsAfterCaseChi e '"Divorce is the interaction between the number of years after the

divorce case was closed and a dummy variable equal to one if the divorce case ended in a

judgment of divorce.

The coefficients of interest are b3 and b5, which estimate the time-invariant effect of

parental divorce and the time-varying effect of parental divorce, respectively. By

utilizing data on children whose parents filed for but dismissed divorce cases, both

coefficients capture the effect of parental divorce relative to the effect of dismissed

divorce.

The estimated coefficients are given in the first several columns of Table 17, while

the estimated effects of divorce after 1, 2, 4, and 6 years are calculated in the last 4

columns. The effect of parental divorce on reading and math scores after 6 years is

positive at 3.98 and 5.01 percentile points, respectively, although neither effect is

statistically significant at the 10% level.

The results also show that although there is an initial statistically significant spike

in disciplinary problems immediately after the divorce, parental divorce causes a

reduction in disciplinary problems after 6 years. For example, a student who experienced

parental divorce gets suspended 2.13 more days per year thereafter but gets suspended

0.58 fewer days for every year after the divorce, both of which are statistically significant









at the 1% level. The net effect is that 1 year after the divorce was finalized, parental

divorce causes statistically significant increases of 0.67 infractions and 1.56 days

suspended per year, while there is no statistically significant effect after 4 years. After 6

years the student who experienced divorce is suspended 1.32 fewer days on average than

the student whose parents dismissed the divorce case, an effect that is not quite

statistically significant at the 10% level. These results suggest that although experiencing

a parental divorce causes more disciplinary problems for children in the short term, after

an initial adjustment period children are no worse off and perhaps better off in terms of

disciplinary problems at school as a consequence of the divorce.

Given that the sample size here is relatively small, as a sensitivity check I examined

whether the results were changed when any given divorce case was excluded from the

sample. For the case of the disciplinary results, although the magnitude of the effect on

days suspended and disciplinary infractions after 6 years when any given divorce case is

dropped is never closer to zero than -0.56 and -0.29, respectively. Consequently, while it

seems likely that parental divorce causes a short-lived initial increase in disciplinary

problems, the notion that disciplinary problems for children overall are reduced in the

long term is less certain.

1.4.8 Are the Effects of Parental Divorce Different for Boys than for Girls?

It may be, however, that the consequences of parental divorce are different for boys

than for girls. In order to address that question, the regression equations were estimated

separately for boys and for girls. The results are shown in Table 18.

The most striking result is that the effect of parental divorce on reading test scores

is very different for boys than for girls. Although the effect for boys after 6 years is a

statistically insignificant -2.75 percentile points, girls score a statistically significant and









large 14.68 percentile points higher on reading as a result of parental divorce. Again, due

to the small sample size I examined the extent to which these results were sensitive to any

given divorce case. Although dropping any one divorce case does not cause the effect for

the girls to be lower than 12.45 percentile points (p=0.018), the results for the boys are

more sensitive. For the boys, dropping one divorce case can cause the results to range

from -0.08 after 6 years to -5.26 (p=0.093) after 2 years.15 Consequently, while the

estimates show that daughters typically thrive in terms of reading comprehension as a

result of divorce, there is only weak evidence to suggest that the reading scores of boys

are affected in a negative way.

The effect of divorce on the mathematics test scores of girls was estimated as 6.68

percentile points after 6 years, although it is not statistically significant (p=0.279).

Dropping any one divorce case caused the effect for girls to range from 14.03 percentile

points (p=0.016) to 2.16 percentile points (p=0.743), while the result for the boys ranged

from 0.89 to 7.18 (p=0.328).

The results also show that although both boys and girls appear to have more

disciplinary problems immediately following the divorce, the effect for boys is larger.

For example, the effect of parental divorce on days suspended and disciplinary

infractions for boys after one year is 2.27 days and 1.04 infractions, both of which are

statistically significant. However, after 4-6 years, there is no statistically significant

effect for boys. Girls, while experiencing a smaller initial increase in disciplinary

problems immediately following the divorce, if anything they appear to benefit from the

parental divorce in the long term by committing 0.73 fewer infractions and being


15 The effect after six years in that case is -6.47 percentile points and has a p-value of 0.204.









suspended 1.67 fewer days 6 years after the divorce, although neither is statistically

significant at the 10% level.

1.4.9 Does the Effect of Parental Divorce Depend on the Age of the Student at the
Time of Divorce?

It is also possible that the effect of parental divorce on a child depends on how old

the child was at the time the parents filed for divorce. In order to examine that

possibility, I included a variable equal to the grade of the student at the time the divorce

was filed for all observations after parents divorced (or zero if there was no divorce).

The third column from the right of Table 19 gives the estimated coefficient of this

variable while the last two columns estimate the effect of parental divorce 4 years after

the fact. The first of those columns does so for a parental divorce that occurred when the

child was in the 1st grade while that second column estimates the effect of a divorce that

occurred when the child was in the 6th grade. The results suggest that any age effects are

small, at best, as the coefficient on the grade-divorce interaction is never statistically

significant at the 10% level. This suggests that although the age of the student at the time

of the divorce does not seem to be an important factor in the effect of divorce, at least for

the range of ages examined in this paper.

1.5 Robustness of Results

A frequent concern regarding studies that utilize relatively small data sets is that the

results may be driven by a small number of outliers. In order to address the concern that

a subset of dismissed divorce cases is in fact driving my result, I estimated the effects of

parental divorce again after making four adjustments to the data set:

S Excluding dismissed divorce cases in which at least one parent's name was
changed or dropped in the school district records. These cases were dropped due to
the concern that the dropping or change of a parent name in a family not observed









to experience divorce may be correlated with negative family unobserved
characteristics.

* Excluding dismissed divorce cases in which a motion for default was entered. A
motion for default is entered by a petitioner so that he or she can proceed with the
divorce without the other spouse being present. As near as I can tell, however, the
other spouse did eventually respond in court in all of the cases in my data. Still,
one might be concerned that such a motion may be correlated with negative
unobserved family characteristics.

* Including all children whose parents were married but did not file for divorce.
Although the results are identified by comparing the dismissed divorce group to the
divorce group, these children were included to ensure that their absence did not
influence the results.16

* Excluding all observations more than 5 years after the divorce case was closed. As
discussed earlier, although 4 shows that the rate of attrition in the data set is
approximately equal for children whose parents divorce compared to those whose
parents file for and dismiss a divorce case, more than five years after the case is
closed there are relatively more observations for the dismissal group than the
divorce group. To ensure that the results are not sensitive to observations more
than five years after the case was closed, those observations were excluded.

The results are shown in Tables 20 23. In row (a) of each table, the main result

presented earlier from using the full data set is presented for comparison purposes. The

results for reading scores presented in Table 20 show that the positive and statistically

significant effect of parental divorce on girls is indeed robust to the changes mentioned

above. Similarly, the result that there may be a small negative effect on the reading

achievement of boys is also consistent.17



16 The main reason for including the children whose parents did not divorce, besides allowing the cross-
sectional comparisons presented earlier in the paper, was to help identify the year fixed effects and grade
effects.

17 One might also be concerned that although the pre-divorce test scores of children whose parents later
divorce are similar to those whose parents later file and dismiss a divorce case, there may be differences
between the groups when they are separated by gender. To some extent, this seems to be the case; the pre-
divorce average reading and math scores for girls in the divorce group are 7.4 and 4.9 percentile points
lower than those of the girls in the dismissal group. In contrast, the pre-divorce average reading and math
scores for boys in the divorce group are 5.4 and 7.8 percentile points higher than those of boys in the
dismissal group. To the extent that one would expect students with higher (lower) percentile test scores to
see future gains (declines) in their scores relative to their peers nationwide, this would cause my results for









Table 21 shows the sensitivity results for mathematics scores. Again, the results

show that the effect estimated for girls is not affected much by the various groups

discussed above, although the effect still never reaches the point of statistical

significance. Similarly, the effect of parental divorce for 5th and 10th grade boys four

years after their parents divorced is never observed to be negative.

Table 22 shows the sensitivity results for days suspended per year. Consistent

with the results presented earlier, after 4 years there does not appear to be a statistically

significant effect of parental divorce on days suspended per year, with one exception. As

shown in row (e), when all observations more than 5 years after the divorce case was

closed were excluded, the effect of divorce on girls after four years is a statistically

significant 1.06 additional day suspension per year. However, this result should be

interpreted with caution since relatively few girls get suspended and the sample gets quite

small after the deletion of all observations more than 5 years after the closure of the

divorce cases.

Table 23 shows the results using the number of disciplinary infractions per year as

the outcome variable. Again, although there is consistency to the idea that parental

divorce causes a temporary spike in disciplinary problems-especially for boys-after 4

years the results are consistent in showing that there is not a statistically significant

effect.


girls to be a lower bound while suggesting that the true effect for boys is more negative than my
estimations show. However, clearly all students with high (or low) percentile scores in the country cannot
move up (or down) relative to their peers over time, so it's unclear that this should be a concern at all.









1.6 Conclusions

Previous research has used the conditional outcomes of children from two-parent

families as an estimate of the counterfactual that would be observed if parents who

divorced were instead to stay together for an exogenous reason. In this paper, I argue that

the performance of children whose parents filed for divorce but did not divorce is a much

more realistic estimate of the appropriate counterfactual. Consequently, this paper has

identified the effects of parental divorce on student performance by comparing the

outcomes of children who experienced parental divorce to those whose parents filed for

divorce but did not divorce, conditional on student fixed effects. The results indicate that

parental divorce does not negatively affect academic achievement. In contrast, I find that

parental divorce positively affects the reading scores of girls in a statistically significant

and robust way; six years after the fact, girls score 14.68 percentile points higher as a

result of the parental divorce. There is also somewhat weaker evidence to suggest that

parental divorce positively affects the mathematics scores of girls, especially those who

are older at the time of the divorce.

The evidence on the effect of parental divorce on the academic achievement of

boys is somewhat less clear. Although I find some evidence that parental divorce

negatively affects the reading achievement of boys, the effects are considerably smaller

and are never statistically significant. I find no evidence that the mathematics

achievement of boys is affected in a negative way by parental divorce.

I also show that although experiencing parental divorce may increase disciplinary

problems for children overall in the short term, I find little evidence that it does so after 4

to 6 years and find that it may even reduce disciplinary problems in the long run.

However, this result should be interpreted with caution since children whose parents later









dismiss a divorce case tend to have more disciplinary problems than children whose

parents later divorce. Although the inclusion of student fixed effects in the estimation

and the fact that I found no statistically significant different in the pre-divorce trends of

the two groups in the three years prior to filing for divorce should reduce this problem,

one might still be concerned that higher levels of disciplinary problems might be

associated with higher future trends after the divorce, which would cause the estimated

effects of parental divorce on disciplinary behavior to be biased downward.

Collectively, these results suggest that children overall are not harmed and that girls

stand to benefit significantly from their parents ending a troubled marriage relative to the

alternative. Although my data force me to remain agnostic regarding the exact

mechanism through which this occurs, potential explanations consistent with my results

include a reduction in parental conflict after the divorce or the refocusing of parental time

from the marriage to the children.

These results differ significantly from those of previous research that has

consistently found negative effects of parental divorce. The difference between these

results and the results in previous research is most likely a direct consequence of the

respective identification strategies used. Indeed, I show in this paper that although there

is a strong correlation between having experienced a parental divorce and having lower

outcomes, there is an even stronger correlation between having one's parents file and

dismiss a divorce case and having lower outcomes. This suggests that the worse

outcomes observed after parental divorce are largely not a consequence of the divorce

itself but rather of the underlying problems that caused the couples to file for divorce.

The appropriate conclusion is thus not that family problems do not negatively affect the









achievement and behavior of children, but rather that, conditional on having rather family

problems significant enough for a parent to file for divorce, on average children overall

are made no worse off by divorce and daughters are made significantly better off

Although this paper did not examine unilateral divorce laws directly, the findings

presented here may shed some light on that policy issue. The fact that I find no evidence

that the academic achievement of children overall is negatively affected by parental

divorce lends no support to the notion that policy-makers should make divorce more

difficult in order to make children better off. Furthermore, my finding that divorce has

large positive effects on the academic achievement of girls 6 years after the divorce

suggests that there may well be significant social costs associated with using divorce laws

to make divorce more difficult when children are involved.










Table 1-1: Matchable Divorces in Alachua County, Florida
General Cases with Cases Cases with Cases with Cases after
Divorce unique assuming children in children in the excluding
Cases Only husband-wife that children grades 1-12 public school nonunique
(excludes name are involved (12/18=66.67%) system (given parent
Simplified combinations in 54% of 10% private names in
Dissolutions) General enrollment) school file
Divorces (10%)
924 886 478 319 287 258
863 802 433 289 260 234
875 816 441 294 264 238
876 820 443 295 266 239
965 900 486 324 292 262
900 840 454 302 272 245
909 843 455 303 273 246
974 904 488 325 293 264
878 816 441 294 264 238
868 817 441 294 265 238
180 170 92 61 55 50
9,212 8,614 4,652 3,101 2,791 2,512




Table 1-2: Families Matched to Unique Divorces
Year Matchable divorces Divorce cases Divorce cases Children with test
given nonunique matched to linked to at least scores linked to a
names in school data school names one test score divorce
1993 258 95 51 65
1994 234 68 47 56
1995 238 78 56 76
1996 239 61 45 64
1997 262 70 63 89
1998 245 58 53 74
1999 246 62 58 80
2000 264 83 75 114
2001 238 69 68 93
2002 238 66 65 88
2003 50 14 14 25
Total 2,512 724 595 824











Table 1-3: Families Matched to Unique Divorces
Sample Cases Ending Cases Ending Dismissed Dismissed
in Divorce in Divorce Divorce Cases Divorce Cases
Matched to Matched to Matched to Matched to
Student Student Test Student Student Test
Records Scores Records Scores
(a) All Cases Matched Using Unique 658 542
Parent Names

(b) All cases matched using student
names and birth dates retrieved from all 14
0 0 164 132
dismissed divorce cases filed from 1993 -
2003
(c) Both (a) and (b)
658 542 164 132

(d) Same as (c), but excluding dismissed
divorce cases not explicitly known to be 658 542 131 99
dismissed voluntarily


(e) Same as (d), but excluding dismissed 623 511 123 92
divorce cases in which one parent name
was matched to a domestic violence case

(f) Same as (e), but excluding dismissed
divorce cases matched to student records 623 511 93 69
in which only one parent name was listed
prior to the divorce




Table 1-4: Distribution of Observations of Students Matched to a Parental Divorce Case
Students Observed in Post-Divorce Time Periods
Data Group Total Post-Divorce 1 3 Years 3 5 Years 5+ Years
All students Children who Experience 872 667 663 314 185
Parental Divorce 100% 76.5% 76.0% 36.0% 21.2%

Children who Experience a 156 114 103 53 41
Dismissed Parental Divorce 100% 73.1% 66.0% 34.0% 26.3%

Students Children who Experience 690 530 399 226 137
observed with Parental Divorce 100% 76.8% 57.8% 32.8% 19.9%
at least one test
score Children who Experience a 111 90 64 41 32
Dismissed Parental Divorce 100% 81.1% 57.7% 36.9% 28.8%











Table 1-5: The Cross-Sectional Effects of Parental Divorce on Reading Test Scores
Obs. Parents Divorce- Divorce- Effect of divorce
Divorced years after grade of on 10th grader
Prior to divorce student whose parents
Test interaction interaction divorced 6 years
prior
(a) includes year dummy variables 26,252 -1.97
and grade 0.192

(b) Also includes race, sex, free 26,252 -2.19
lunch, zip code income, income 0.099
squared, and year dummies
-4.03 -0.79 1.23 -3.87
0.157 0.057 0.030 0.059

(c) Same as (b), but also includes 18,976 -0.78
school dummy variables 0.582

-2.51 -0.64 1.15 -1.79
0.408 0.131 0.046 0.363
Coefficients and estimates that are statistically significant at the 10% level are in bold. Each row
represents a different regression. Test scores are percentile rankings in the Iowa Test of Basic Skills
and the Stanford 9 (FCAT) achievement tests. The first row of each cell presents the estimated
coefficient, while the second row contains p-values calculated using robust standard errors.



Table 1-6: The Cross-Sectional Effects of Parental Divorce on Mathematics Test Scores
Obs. Parents Divorce- Divorce- Effect of divorce
Divorced years after grade of on 10th grader
Prior to divorce student whose parents
Test interaction interaction divorced 6 years
prior
(a) includes year dummy variables 23,228 -1.31
and grade 0.380

(b) Also includes race, sex, free 23,228 -1.32
lunch, zip code income, income 0.319
squared, and year dummies
1.32 -1.26 0.25 -5.25
0.670 0.006 0.674 0.015

(c) Same as (b), but also includes 18,962 -0.48
school dummy variables 0.719

2.51 -1.25 0.17 -4.27
0.420 0.005 0.762 0.034
Coefficients and estimates that are statistically significant at the 10% level are in bold. Each row
represents a different regression. Test scores are percentile rankings in the Iowa Test of Basic Skills
and the Stanford 9 (FCAT) achievement tests. The first row of each cell presents the estimated
coefficient, while the second row contains p-values calculated using robust standard errors.











Table 1-7: The Cross-Sectional Effects of Parental Divorce on Days Suspended Per Year
Obs. Parents Divorce- Divorce- Effect of divorce
Divorced years after grade of on 10th grader
Prior to divorce student whose parents
Test interaction interaction divorced 6 years
prior


(a) includes year dummy variables 60,196
and grade

(b) Also includes race, sex, free 60,196
lunch, zip code income, income
squared, and year dummies


(c) Same as (b), but also includes 19,841
school dummy variables


0.79
0.001

0.72
0.001

0.15
0.553

0.21
0.295


0.16
0.053


0.02
0.791


1.16
0.004


0.06 0.11 -0.06 0.49
0.839 0.261 0.441 0.266
Coefficients and estimates that are statistically significant at the 10% level are in bold. Each row
represents a different regression. The first row of each cell presents the estimated coefficient, while
the second row contains p-values calculated using robust standard errors.



Table 1-8: The Cross-Sectional Effects of Parental Divorce on Disciplinary Infractions
Per Year
Obs. Parents Divorce- Divorce- Effect of divorce
Divorced years after grade of on 10th grader
Prior to divorce student whose parents
Test interaction interaction divorced 6 years
prior
(a) includes year dummy variables 60,196 0.39
and grade 0.004

(b) Also includes race, sex, free 60,196 0.35
lunch, zip code income, income 0.005
squared, and year dummies
0.28 0.07 -0.03 0.54
0.109 0.151 0.333 0.016

(c) Same as (b), but also includes 19,841 0.10
school dummy variables 0.398

0.02 0.07 -0.04 0.27
0.900 0.172 0.316 0.254
Coefficients and estimates that are statistically significant at the 10% level are in bold. Each row
represents a different regression. The first row of each cell presents the estimated coefficient, while
the second row contains p-values calculated using robust standard errors.







47


Table 1-9: The Cross-Sectional "Effects" of Dismissed Divorce on Reading Test Scores
Obs. Parents Dismissal- Dismissal- "Effect" of
dismissed years after grade of dismissal on 10th
case prior dismissal student grader whose
to test interaction interaction parents dismissed
case 6 years prior
(a) includes year dummy variables 23,305 -3.33
and grade 0.362

(b) Also includes race, sex, free 23,305 -6.42
lunch, zip code income, income 0.023
squared, and year dummies
-7.53 -0.73 1.60 -5.49
0.178 0.373 0.152 0.170

(c) Same as (b), but also includes 17,068 -3.40
school dummy variables 0.250

0.10 -1.76 1.48 -4.57
0.989 0.058 0.289 0.326
Coefficients and estimates that are statistically significant at the 10% level are in bold. Each row
represents a different regression. Test scores are percentile rankings in the Iowa Test of Basic Skills
and the Stanford 9 (FCAT) achievement tests. The first row of each cell presents the estimated
coefficient, while the second row contains p-values calculated using robust standard errors.










Table 1-10: The Cross-Sectional "Effects" of Dismissed Divorce on Mathematics Test
Scores
Obs. Parents Dismissal- Dismissal- "Effect" of
dismissed years after grade of dismissal on 10th
case prior dismissal student grader whose
to test interaction interaction parents dismissed
case 6 years prior
(a) includes year dummy variables 20,533 -4.24
and grade 0.297

(b) Also includes race, sex, free 20,533 -3.78
lunch, zip code income, income 0.219
squared, and year dummies
-1.79 -1.40 1.03 -6.08
0.765 0.124 0.331 0.141

(c) Same as (b), but also includes 17,029 -3.52
school dummy variables 0.256

-3.51 -1.07 1.68 -3.20
0.630 0.288 0.184 0.452
Coefficients and estimates that are statistically significant at the 10% level are in bold. Each row
represents a different regression. Test scores are percentile rankings in the Iowa Test of Basic Skills
and the Stanford 9 (FCAT) achievement tests. The first row of each cell presents the estimated
coefficient, while the second row contains p-values calculated using robust standard errors.










Table 1-11: The Cross-Sectional "Effects" of Dismissed Divorce on Days Suspended Per
Year
Obs. Parents Dismissal- Dismissal- "Effect" of
dismissed years after grade of dismissal on 10th
case prior dismissal student grader whose
to test interaction interaction parents dismissed
case 6 years prior
(a) includes year dummy variables 54,225 0.52
and grade 0.214

(b) Also includes race, sex, free 54,225 0.44
lunch, zip code income, income 0.208
squared, and year dummies
-1.93 0.66 0.04 2.20
0.009 0.013 0.588 0.028

(c) Same as (b), but also includes 17,798 0.99
school dummy variables 0.127

-3.21 0.96 0.18 3.22
0.019 0.017 0.309 0.033
Coefficients and estimates that are statistically significant at the 10% level are in bold. Each row
represents a different regression. The first row of each cell presents the estimated coefficient, while
the second row contains p-values calculated using robust standard errors.



Table 1-12: The Cross-Sectional "Effects" of Dismissed Divorce on Disciplinary
Infractions Per Year
Obs. Parents Dismissal- Dismissal- "Effect" of
dismissed years after grade of dismissal on 10th
case prior dismissal student grader whose
to test interaction interaction parents dismissed
case 6 years prior
(a) includes year dummy variables 54,225 0.45
and grade 0.181

(b) Also includes race, sex, free 54,225 0.38
lunch, zip code income, income 0.190
squared, and year dummies
-0.53 0.33 -0.06 1.21
0.257 0.016 0.421 0.036

(c) Same as (b), but also includes 17,798 0.73
school dummy variables 0.129

-1.02 0.49 -0.07 1.64
0.143 0.021 0.440 0.051
Coefficients and estimates that are statistically significant at the 10% level are in bold. Each row
represents a different regression. The first row of each cell presents the estimated coefficient, while
the second row contains p-values calculated using robust standard errors.















Table 1-13: Descriptive Statistics
(A) (B) (C) (D) (E) (D)- (E)
(Not Used in Analysis) (Used in Main Analysis) (Used in Main Analysis)
Children in 2000 whose Children in 2000 whose Children whose parents Children whose parents Children whose parents Difference
parents I think are married parents I think are married later file for a divorce later file for and later file a divorce case that between
but never filed for divorce but never filed for divorce- case that was dismissed specifically request the ends in divorce Column B
(met conditions 1-3 in more restrictive (met but for which the dismissal of a divorce case and
Section 3.5) conditions 1-4 in Section petitioner did not Column C
3.5) specifically request the
dismissal
Age 10.3 11.9 -1.6
(4.3) (3.3) p=0.000
% Black 28.4 14.5 54.7 18.2 19.6 -1.5
(45.1) (35.2) (50.3) (38.9) (39.7) p=0.798
% Male 50.1 51.4 49.1 60.0 47.3 12.7
(50.0) (50.0) (50.5) (49.4) (50.0) p=0.075
% Subsidized Lunch 33.6 17.3 77.7 39.4 32.4 7.0
(47.2) (37.8) (40.4) (48.0) (44.8) p=0.279
% Disabled 13.3 11.1 32.1 18.2 17.1 1.1
(34.0) (31.4) (47.1) (38.9) (37.7) p=0.845
% Gifted 9.6 10.6 5.7 12.7 10.0 2.7
(29.5) (30.8) (23.3) (33.6) (30.1) p=0.539
Average Zip Code Median 45,923 48,143 39,944 45,887 47,405 -1,518
Family Income (12,407) (11,703) (11,409) (11,422) (12,707) p=0.399
% Committed Disciplinary 21.8 17.7 37.1 36.4 21.5 14.9
Infraction in a year (41.30) (38.1) (42.2) (43.3) (36.1) p=0.005
Average number of times 0.78 0.60 1.38 1.27 0.65 0.62
disciplined per year (2.50) (2.2) (2.16) (2.8) (1.8) p=0.023
Average number of days 1.02 0.76 1.36 1.89 0.83 1.06
suspended per year (4.18) (3.5) (2.56) (5.2) (3.2) p=0.033
Reading Score 58.4 64.1 33.3 57.3 58.4 -1.1
(29.8) (28.1) (28.03) (29.1) (27.5) p=0.781
Math Score 60.0 66.0 38.6 56.5 59.8 -3.3
(29.4) (27.8) (27.58) (30.9) (28.1) p=0.459
If children are observed more than once in each category, the average was used. Standard errors are in parentheses. Differences reported may not be equal to differences in the numbers in
the table due to rounding. Statistically significant differences at the 10% level are in bold.














Table 1-14: Estimated Effects of Parental Divorce on Student Family Income Using Student Fixed Effects
Outcome Independent Variable Effect of Divorce after:
Dummy Variable Years After Variable
Post-Divorce Case Post-Divorce Case Years after Divorce Years after Divorce 1 Year 2 Years 4 Years 6 Years
(including dismissed Divorce (interaction) Case (including Case Divorce
cases) dismissed cases) (interaction, finalized
divorces only)
Zip Code Family -84 508 395 -288 219 -69 -646 -1,223
Income 0.947 0.69 0.323 0.465 0.851 0.954 0.679 0.574
Coefficients and estimates that are statistically significant at the 10% level are in bold. Each regression includes student fixed effects, grade, grade
squared, and year dummy variables as covariates. Each row represents a different regression. Estimated coefficients are given in the first row of each
cell while p-values are given in the second row.











Table 1-15: Estimated Pre-Divorce Trends
Outcome Independent Variable Coefficient Hypothesis Test
Dummy Variable Years Before Variable of Interest
Pre-Divorce Case Pre-Divorce Case Years before Years before Difference in Reject null
(including Divorce Divorce Case was Divorce Case Pre-Divorce hypothesis that
dismissed cases) (interaction) filed (including Divorce Trends both groups have
dismissed cases) (Difference in Pre- the same pre-
Divorce Trends) divorce trend?
Reading -2.52 1.32 1.03 0.16 0.16
No
0.533 0.751 0.633 0.943 0.943

Math -1.81 2.08 2.21 -0.95 -0.95
No
0.655 0.620 0.357 0.703 0.703

Days 0.49 -0.95 0.19 -0.14 -0.14 No
No
Suspended 0.161 0.013 0.173 0.341 0.341

Disciplinary 0.30 -0.55 0.04 0.01 0.01
No
Infractions 0.150 0.012 0.678 0.892 0.892
Each regression includes student fixed effects, grade, grade squared, and year dummy variables as covariates. Each row
represents a different regression. Estimated coefficients are given in the first row of each cell while p-values are given in the
second row. Observations more than 3 years prior to filing were excluded from the sample.


Table 1-16: Estimated Time-Invariant Effects of Parental Divorce on Student Test Scores
and Behavior
Outcome Post-Divorce Case Post-Divorce Effect of
(including Case Divorce Divorce
dismissed cases) (interaction)
Reading Score 0.39 -0.18 -0.18
0.880 0.943 0.943

Mathematics Score -3.41 2.99 2.99
0.242 0.320 0.320

Days Suspended -0.56 0.75 0.75
0.034 0.008 0.008

Disciplinary Infractions -0.33 0.33 0.33
0.042 0.048 0.048
Each regression includes student fixed effects, grade, grade squared, and year
dummy variables as covariates. Each row represents a different regression.
Estimated coefficients are given in the first row of each cell while p-values
are given in the second row.











Table 1-17: Estimated Effects of Parental Divorce on Student Test Scores and Behavior
Outcome Independent Variable Effect of Divorce after:
Dummy Variable Years After Variable
Post-Divorce Post-Divorce Years after Years after 1 2 4 6
Case (including Case Divorce Divorce Case Divorce Case Year Years Years Years
dismissed cases) (interaction) (including Divorce
dismissed cases) (interaction,
finalized
divorces onlv)
Reading 1.73 -1.62 -0.15 0.93 -0.68 0.25 2.11 3.98
0.525 0.567 0.831 0.176 0.795 0.925 0.498 0.324

Math -2.69 2.35 -0.01 0.44 2.80 3.24 4.13 5.01
0.376 0.455 0.992 0.605 0.351 0.294 0.286 0.328

Days -1.86 2.13 0.62 -0.58 1.56 0.98 -0.17 -1.32
Suspended 0.000 0.000 0.003 0.005 0.000 0.001 0.717 0.110

Disciplinary -0.88 0.92 0.25 -0.25 0.67 0.43 -0.07 -0.56
Infractions 0.003 0.003 0.022 0.026 0.002 0.011 0.784 0.202

Coefficients and estimates that are statistically significant at the 10% level are in bold. Each regression includes
student fixed effects, grade, grade squared, and year dummy variables as covariates. Each row represents a
different regression. Estimated coefficients are given in the first row of each cell while p-values are given in the
second row. Test scores are percentile rankings on the Iowa Test of Basic Skills and Stanford 9 Exams.











Table 1-18: Estimated Effects of Parental Divorce on Student Test Scores and Behavior
Outcome Sex Independent Variable Effect of Divorce after:
Dummy Variable Years After Variable
Post- Post- Years after Years after 1 2 4 6
Divorce Divorce Divorce Divorce Case Year Years Years Years
Case Case Case Divorce
(including Divorce (including (interaction,
dismissed (interaction) dismissed finalized
cases) cases) divorces onlv)
Reading Score Boys 3.82 -3.73 0.01 0.16 -3.57 -3.41 -3.08 -2.75
0.237 0.277 0.990 0.867 0.257 0.280 0.438 0.610

Girls -2.04 2.41 -0.63 2.04 4.46 6.50 10.59 14.68
0.569 0.517 0.437 0.013 0.206 0.064 0.008 0.004

Math Score Boys -1.59 2.45 -0.08 0.36 2.81 3.17 3.90 4.63
0.707 0.583 0.945 0.754 0.507 0.462 0.462 0.506

Girls -4.35 2.56 -0.26 0.69 3.24 3.94 5.31 6.68
0.186 0.459 0.819 0.543 0.303 0.224 0.226 0.279

Days Boys -2.43 2.88 0.52 -0.61 2.27 1.66 0.43 -0.79
Suspended 0.000 0.000 0.062 0.027 0.000 0.000 0.492 0.476

Girls -1.07 1.20 0.64 -0.48 0.72 0.24 -0.72 -1.67
0.124 0.095 0.025 0.096 0.146 0.518 0.275 0.154

Disciplinary Boys -1.28 1.31 0.22 -0.27 1.04 0.77 0.22 -0.32
Infractions 0.001 0.002 0.146 0.074 0.001 0.001 0.487 0.584

Girls -0.34 0.41 0.25 -0.19 0.22 0.03 -0.35 -0.73
0.359 0.297 0.091 0.193 0.459 0.913 0.352 0.244
Coefficients and estimates that are statistically significant at the 10% level are in bold. Each regression
includes grade, grade squared, student fixed effects, and year dummy variables as covariates. Each row
represents a different regression. Estimated coefficients are given in the first row of each cell while p-values
are given in the second row. Test scores are percentile rankings on the Iowa Test of Basic Skills and Stanford
9 exams.















Table 1-19: Estimated Effects of Parental Divorce on Student Test Scores and
Behavior
Outcome Sex Independent Variable Effect after 4 Years
Dummy Variable Years After Variable Child Grade at Filing
Post-Divorce Case Post-Divorce Case Years after Divorce Years after Divorce Divorce Student Grade 1 Grade 6
(including dismissed Divorce (interaction) Case (including Case Divorce Grade at Time of
cases) dismissed cases) (interaction, finalized Divorce (finalized
divorces only) divorces only)
(a) Reading Score Boys 3.81 -3.41 0.01 0.15 -0.06 -2.87 -3.19
0.240 0.432 0.993 0.879 0.903 0.500 0.438

Girls -1.95 1.10 -0.59 2.09 0.26 9.73 11.01
0.587 0.809 0.471 0.011 0.602 0.029 0.007

(b) Math Score Boys -1.60 2.48 -0.08 0.36 -0.01 3.93 3.90
0.707 0.655 0.944 0.754 0.991 0.505 0.464

Girls -4.19 0.05 -0.20 0.73 0.45 3.42 5.67
0.201 0.991 0.860 0.519 0.398 0.477 0.199

(c) Days Suspended Boys -2.39 1.95 0.54 -0.57 0.16 -0.16 0.63
0.001 0.043 0.052 0.040 0.206 0.837 0.337

Girls -1.04 0.95 0.64 -0.47 0.04 -0.87 -0.68
0.131 0.232 0.024 0.107 0.387 0.200 0.303

(d) Disciplinary Boys -1.27 1.09 0.22 -0.26 0.04 0.08 0.27
Infractions 0.001 0.025 0.138 0.084 0.497 0.825 0.410

Girls -0.34 0.41 0.25 -0.19 0.00 -0.35 -0.35
0.360 0.359 0.092 0.193 0.996 0.390 0.350
Coefficients and estimates that are statistically significant at the 10% level are in bold. Each regression includes grade, grade squared, student fixed effects, and year dummy
variables as covariates. Each row represents a different regression. Estimated coefficients are given in the first row of each cell while p-values are given in the second row.
















Table 1-20: Estimated Effects of Parental Divorce on Student Reading Test Scores
Restrictions Sex Independent Variable Effect after 4 Years
Dummy Variable Years After Variable Grade Interaction Student Grade at Filing
Post-Divorce Case Post-Divorce Case Years after Divorce Years after Divorce Divorce Student Grade 1 Grade 6
(including dismissed Divorce (interaction) Case (including Case Divorce Grade at Time of
cases) dismissed cases) (interaction, finalized Divorce (finalized
divorces only) divorces only)


(a) None; Same data and
specification as row (a) of Table
15




(b) Excludes dismissed divorce
cases in which at least one
parent's name was changed or
dropped


(c) Excludes dismissed divorce
cases in which a motion for
default was filed




(d) Includes all children whose
parents did not file for divorce





(e) Excludes all observations
more than 5 years after the
divorce case was closed


-3.41
0.432

1.10
0.809

-3.82
0.386

1.09
0.810

-4.31
0.347

1.34
0.773

0.24
0.958

3.34
0.470

-4.70
0.317

0.78
0.870


0.01
0.993

-0.59
0.471

0.03
0.977

-0.63
0.437

-0.11
0.916

0.59
0.469

0.67
0.513

-1.28
0.086

-0.84
0.576

-1.27
0.161


0.15
0.879

2.09
0.011

0.17
0.874

2.13
0.010

0.26
0.800

2.09
0.012

-0.41
0.708

2.00
0.018

1.24
0.428

2.54
0.011


-2.87 -3.19
0.500 0.438

9.73 11.01
0.029 0.007

-3.20 -3.43
0.464 0.420

9.88 11.11
0.027 0.006

-3.33 -3.76
0.463 0.396

9.96 11.18
0.027 0.007

-1.97 -4.86
0.680 0.282

11.19 10.21
0.015 0.016

-0.01 -1.27
0.998 0.811

11.11 11.96
0.015 0.004


Coefficients and estimates that are statistically significant at the 10% level are in bold. Each regression includes grade, grade squared, student fixed effects, and year dummy variables
as covariates. Each row represents a different regression. Estimated coefficients are given in the first row of each cell while p-values are given in the second row.


3.81
0.240

-1.95
0.587

4.14
0.218

-1.89
0.598

4.84
0.173

-2.13
0.568

3.74
0.300

-2.89
0.435

5.21
0.145

-0.94
0.802
















Table 1-21: Estimated Effects of Parental Divorce on Student Mathematics Test Scores
Restrictions Sex Independent Variable Effect after 4 Years
Dummy Variable Years After Variable Grade Interaction Student Grade at Filing
Post-Divorce Case Post-Divorce Case Years after Divorce Years after Divorce Divorce Student Grade 1 Grade 6
(including dismissed Divorce (interaction) Case (including Case Divorce Grade at Time of
cases) dismissed cases) (interaction, finalized Divorce (finalized
divorces only) divorces only)


(a) None; Same data and
specification as row (b) of Table
15




(b) Excludes dismissed divorce
cases in which at least one
parent's name was changed or
dropped


(c) Excludes dismissed divorce
cases in which a motion for
default was filed




(d) Includes all children whose
parents did not file for divorce





(e) Excludes all observations
more than 5 years after the
divorce case was closed


-1.60
0.707

-4.19
0.201

-2.30
0.615

-4.19
0.201

0.31
0.945

-4.42
0.195

-2.73
0.543

-4.53
0.197

-2.34
0.610

-3.62
0.289


2.48
0.655

0.05
0.991

3.02
0.600

0.07
0.987

0.10
0.985

0.25
0.958

1.66
0.768

2.11
0.656

2.03
0.729

0.34
0.942


-0.08
0.944

-0.20
0.860

-0.05
0.966

-0.23
0.843

0.16
0.900

-0.28
0.814

-0.66
0.571

-0.03
0.977

0.09
0.962

-0.62
0.652


0.36
0.754

0.73
0.519

0.34
0.774

0.75
0.511

0.24
0.853

0.79
0.504

0.41
0.742

0.57
0.644

0.77
0.678

0.58
0.677


3.93 3.90
0.505 0.464

3.42 5.67
0.477 0.199

4.42 4.52
0.470 0.419

3.50 5.72
0.467 0.195


1.15
0.851


1.59
0.780


3.87 6.11
0.430 0.178

3.44 4.07
0.585 0.485


4.59
0.385


5.62
0.241


5.06 4.79
0.496 0.490


3.09
0.576


5.33
0.280


Coefficients and estimates that are statistically significant at the 10% level are in bold. Each regression includes grade, grade squared, student fixed effects, and year dummy variables
as covariates. Each row represents a different regression. Estimated coefficients are given in the first row of each cell while p-values are given in the second row.
















Table 1-22: Estimated Effects of Parental Divorce on Days Suspended per Year
Restrictions Sex Independent Variable Effect after 4 Years
Dummy Variable Years After Variable Grade Interaction Student Grade at Filing
Post-Divorce Case Post-Divorce Case Years after Divorce Years after Divorce Divorce Student Grade 1 Grade 6
(including dismissed Divorce (interaction) Case (including Case Divorce Grade at Time of
cases) dismissed cases) (interaction, finalized Divorce (finalized
divorces only) divorces only)


(a) None; Same data and
specification as row (c) of Table
15




(b) Excludes dismissed divorce
cases in which at least one
parent's name was changed or
dropped


(c) Excludes dismissed divorce
cases in which a motion for
default was filed




(d) Includes all children whose
parents did not file for divorce





(e) Excludes all observations
more than 5 years after the
divorce case was closed


1.95
0.043

0.95
0.232

1.91
0.044

1.00
0.214

2.59
0.014

1.12
0.179

2.02
0.037

1.23
0.124

1.56
0.062

-0.35
0.535


0.54
0.052

0.64
0.024

0.50
0.073

0.64
0.025

0.82
0.014

0.68
0.023

0.61
0.047

0.53
0.083

0.33
0.149

-0.14
0.232


-0.57
0.040

-0.47
0.107

-0.51
0.066

-0.45
0.125

-0.83
0.013

-0.48
0.112

-0.59
0.063

-0.44
0.157

-0.25
0.326

0.36
0.013


-0.16 0.63
0.837 0.337

-0.87 -0.68
0.200 0.303

-0.01 0.53
0.987 0.431

-0.76 -0.59
0.275 0.380

-0.61 -0.05
0.473 0.945

-0.78 -0.63
0.289 0.381

-0.18 0.57
0.824 0.430

-0.56 -0.61
0.458 0.402

0.60 0.87
0.445 0.213


-2.39
0.001

-1.04
0.131

-1.88
0.005

-1.01
0.147

-2.55
0.001

-1.11
0.128

-2.27
0.003

-1.12
0.131

-1.51
0.002

0.44
0.324


1.05
0.002


Coefficients and estimates that are statistically significant at the 10% level are in bold. Each regression includes grade, grade squared, student fixed effects, and year dummy variables
as covariates. Each row represents a different regression. Estimated coefficients are given in the first row of each cell while p-values are given in the second row.


1.09
0.002
















Table 1-23: Estimated Effects of Parental Divorce on Disciplinary Infractions per Year
Restrictions Sex Independent Variable Effect after 4 Years
Dummy Variable Years After Variable Grade Interaction Student Grade at Filing
Post-Divorce Case Post-Divorce Case Years after Divorce Years after Divorce Divorce Student Grade 1 Grade 6
(including dismissed Divorce (interaction) Case (including Case Divorce Grade at Time of
cases) dismissed cases) (interaction, finalized Divorce (finalized
divorces only) divorces only)


(a) None; Same data and
specification as row (d) of Table
15




(b) Excludes dismissed divorce
cases in which at least one
parent's name was changed or
dropped


(c) Excludes dismissed divorce
cases in which a motion for
default was filed




(d) Includes all children whose
parents did not file for divorce





(e) Excludes all observations
more than 5 years after the
divorce case was closed


1.09
0.025

0.41
0.359

1.07
0.027

0.43
0.330

1.49
0.007

0.48
0.287

1.04
0.049

0.42
0.342

0.90
0.034

-0.05
0.909


0.22
0.138

0.25
0.092

0.16
0.277

0.25
0.096

0.37
0.041

0.20
0.197

0.27
0.104

0.21
0.171

0.08
0.498

-0.10
0.534


-0.26
0.084

-0.19
0.193

-0.19
0.200

-0.18
0.218

-0.39
0.029

-0.13
0.386

-0.27
0.123

-0.17
0.281

-0.10
0.453

0.16
0.334


0.08 0.27
0.825 0.410

-0.35 -0.35
0.390 0.350

0.32 0.38
0.400 0.257

-0.30 -0.31
0.475 0.415

-0.08 -0.01
0.854 0.970

-0.05 -0.06
0.910 0.873

0.03 0.25
0.942 0.496

-0.27 -0.30
0.532 0.469

0.48 0.35
0.206 0.298

0.56 0.39
0.157 0.300


Coefficients and estimates that are statistically significant at the 10% level are in bold. Each regression includes grade, grade squared, student fixed effects, and year dummy variables
as covariates. Each row represents a different regression. Estimated coefficients are given in the first row of each cell while p-values are given in the second row.


-1.27
0.001

-0.34
0.360

-0.99
0.010

-0.33
0.389

-1.40
0.002

-0.38
0.328

-1.15
0.010

-0.34
0.402

-0.69
0.026

0.29
0.489














CHAPTER 2
THE EFFECT OF ATTENDING THE FLAGSHIP STATE UNIVERSITY ON
EARNINGS: A REGRESSION DISCONTINUITY APPROACH

2.1 Introduction

The question of the extent to which attending a more selective college affects

subsequent earnings is of interest for several reasons. In addition to being of obvious

significance to the students and parents making decisions regarding whether to incur

costs associated with either getting admitted and/or attending a more selective university,

it is also tied to the question regarding peer effects in education-whether attending

college with more highly qualified students increases learning and ultimately productivity

in the labor force.

The issue also raises policy questions, especially with respect to affirmative action

in admissions policies at flagship state universities. In the past, flagship state universities

have used such policies in order to admit more black and Hispanic students. However,

beginning in the 1990's, these policies were challenged both legally and politically. For

example, between 1996 and 1998 Texas and California eliminated affirmative action in

college and university admissions; Florida followed suit in 2000. Finally, in 2003 the

Supreme Court ruled in Gratz v. Bollinger that the University of Michigan's

undergraduate admissions policy violated the Equal Protection Clause of the Fourteenth

Amendment because it was not "narrowly tailored to achieve [the university's] asserted









compelling interest in diversity."12 In addition, states may well be interested in how large

the flagship university should become.

The empirical difficulty in estimating the effect of university selectivity on

earnings is that attendance at more selective universities is likely correlated with

unobserved characteristics that themselves will affect future earnings. Such biases could

arise for two reasons. First, bias could arise if certain student abilities or characteristics

are observed by college admissions committees by examining the student's applications

but not by the econometrician. Second, bias could arise if, conditional on all observable

student and family characteristics and admission to the more selective university, the

decision to attend that university is correlated with unobserved student or family

characteristics that would themselves affect subsequent earnings. For example, if the

student chooses to attend the more selective university because she is more motivated

than an observationally equivalent student who chose to attend a less selective school, the

effect of selectivity on earnings will be overstated. On the other hand, if the student

chooses to attend the more selective university because she received more need-based

financial aid at the selective school relative to an observationally equivalent student who

chose a less selective school, the effect of selectivity on earnings will likely be

understated.

Researchers have taken several approaches to answering this question. Black and

Smith (2004) describe problems that can arise for much of this literature that relies on the



1 Taken from the majority opinion written by Chief Justice Rehnquist and accessed at
hIlp \ \ \ .supremecourtus.gov/opinions/02pdf/02-516.pdf.
2 This is not to say that states may not legally engage in any affirmative action, however. Indeed, in the
same ruling the court upheld the affirmative action practices of the University of Michigan Law School.









assumption of "selection on observables." Several other approaches have been used.

Dale and Krueger (2002) compare the earnings of one group of students to another group

who were accepted at similarly selective colleges but who chose to attend less selective

colleges and find that attending more selective colleges has a positive effect on earnings

only for students from low-income families. Brewer, Eide, and Ehrenberg (1999)

estimate the payoff by explicitly modeling high school students' choice of college type

and find significant returns to attending an elite private institution for all students.

Behrman, Rozenzweig, and Taubman (1996) identify the effect by comparing female

twin pairs and find evidence of a positive payoff for attending Ph.D.-granting private

universities with well-paid senior faculty; Lindahl and Regner (2005) use Swedish sibling

data and show that cross-sectional estimates of the selective college wage premium are

twice the within-family estimates. Finally, in a related debate, Sander (2004) found

negative effects of attending more selective law schools for black student beneficiaries of

affirmative action, a conclusion that has been vigorously challenged by others (e.g.,

Ayres and Brooks, 2005).

In contrast to previous research, this paper identifies the effect of school

selectivity on earnings by comparing the earnings of those just below the cutoff for

admission to the flagship state university to those of applicants who were barely above

the cutoff for admission. To do so, we combined confidential administrative records

from a large flagship state university with earnings records collected by the state through

the Unemployment Insurance program.

The unique data set used allows this paper to make two primary contributions to

the existing literature. First, by using the application data from a large flagship state









university, this paper addresses the question of how college selectivity affects earnings in

the context in which the public policy decision is made. Indeed, although determining

the effect of attending an elite private college over a less selective one is interesting for

several reasons, the public policy question is largely confined to the extent to which

admission at flagship state universities affects the subsequent earnings of various

subgroups.

Second, because we have actual admissions data from the university, we can use a

regression discontinuity design to detect whether or not there is a discontinuity in

earnings at the point of the admission cutoff. In this way we estimate an "intent-to-treat"

effect-that is, the effect of admission to the flagship state university. Doing so

overcomes any biases that might arise due to the correlation of the decision to enroll at

the flagship university with other unobserved factors that may themselves affect earnings,

so long as the assumptions for the regression discontinuity design are met.

By combining confidential admissions data from a large university to earnings

records collected by the state through the Unemployment Insurance program, we find

suggestive evidence of positive discontinuities in the earnings of white men that

correspond to 1% 27% higher earnings as a result of being admitted to the state flagship

university, the magnitude and statistical significance of which depends largely on model

specification. Furthermore, although there does not appear to be a consistent earnings

effect for women overall, we do find that there is a positive flagship earnings effect for

the subset of women with strong attachment to the labor force. Finally, we find no

evidence that admission to the flagship causes applicants to be more or less likely to be

observed in the labor force 10 15 years later.









2.2 Data

The data used in this study are from two sources. First, we acquired

administrative data on admissions from a large flagship state university. As part of the

agreement in acquiring the data, we agreed not to disclose the name of the institution

involved. The university was able to retrieve the following information for every student

that applied for admission to the university from 1986 1989: Social Security Number,

race, sex, term for which the student was applying for admission, ACT score, SAT math

score, SAT verbal score, whether or not the student subsequently enrolled, year of birth,

and whether or not the student subsequently graduated from the university. Finally, we

also observe each student's high school GPA, a discrete (to the nearest tenth of a point)

number recalculated by the university after excluding certain courses and adjusting for

different scales used by high schools.

These data were then sent to a state office to which employers submit

Unemployment Insurance tax reports. Using the provided Social Security Numbers,

quarterly earnings records from 1998 through the second quarter of 2005 were matched

to the university records. All nominal wages were adjusted using the CPI so as to be

measured in 2005 dollars.

One advantage of these earnings data is that they allow us to look at earnings well

after nearly all applicants have completed their educations. The primary results in the

paper are based on earnings observed 15 years after high school graduation-or when the

individual is approximately 33 years old. These earnings are much more likely to be

predictive of lifetime earnings than are earnings observed for people in their early and

mid-twenties who are still finishing their educations and sorting themselves in the job

market.









Another advantage of these administrative data over survey data is that they likely

contain less measurement error. A limitation, however, relates to the fact that an

individual's earnings will not be observed if he or she is employed in a job not covered

by the UI system or has moved out of state. The latter of these may be a particularly

significant concern to the extent that working in state is endogenous to whether or not the

student was admitted to the flagship state university. Fortunately, the data also allow us

to examine if there is a discontinuity in whether or not an applicant is observed with

earnings.

There were 38,719 high school graduates who applied for admission in the

summer or fall of the 1985-86, 1986-87, 1987-88, 1988-89, or 1989-90 school years. Of

those, there were 7,024 for whom we did not observe either a high school GPA or an

ACT or SAT score. In addition, 992 applicants were excluded because their high school

GPA was lower than 2.0 or higher than 4.0. Two hundred fourteen more applicants were

excluded because they cancelled their application prior to the admission decision.

Finally, 1,674 applicants were deleted because they did not meet the minimum GPA

required for admission in that term/year.3 Thus, the final data set contains observations

on 28,815 applicants.

2.3 Identification Strategy

This paper uses a regression discontinuity design to estimate the causal effect of

admission at a state's flagship university on earnings. This design will distinguish the

effect of admission to the flagship university from other confounding factors so long as

the unobservable determinants of earnings (e.g., motivation, parental support, etc.) are

3 In some of the years, a 2.0 was the minimum GPA required. Later on, however, this minimum was
increased and there was no SAT score observed that would ensure admission for someone with that GPA.









continuous at the admission cutoff. As long as this condition holds, any discontinuous

jump in earnings at the admission cutoff is properly interpreted as the causal effect of

admission to the flagship university on earnings.

This condition will fail in this context if either applicants or the university can

manipulate the side of the cutoff on which applicants fall. For applicants, this would be a

problem if those who would barely miss the cutoff were to retake the SAT until they

surpassed the cutoff. In reality, such a scenario is unlikely for the simple reason that the

admission rule was never published or revealed by the university and, in fact, was

changed from year to year. Consequently, it is very unlikely that the applicant would

know, prior to applying, whether or not she was just above the cutoff or just below it.

Furthermore, although there was an appeals process for rejected applicants, it affected

relatively few students and was described by one admissions officer on the committee at

the time as "very noisy".

Applying a regression discontinuity design in this context is somewhat different,

however. The reason is that the admission cutoff rule is two dimensional rather than one

dimensional since it depends on both the SAT score and the high school GPA and took

the form of a nonlinear sliding scale. To address this issue and convert the two-

dimensional sliding scale rule into a one-dimensional rule, we created an adjusted SAT

score for each student. We did so by subtracting the SAT score required for admission,

given the student's high school GPA, from each student's actual SAT score. For

example, if an SAT score of 1100 was necessary for admission given a student's high

school GPA and that student scored an 1150 on the SAT, that student was assigned a

score of 50. As a result, all students assigned scores of 0 or higher were predicted to be









accepted to the flagship university. In case students with similar adjusted SAT scores

have different earnings potentials, we directly control for actual SAT and high school

GPA when estimating the earnings effects.

One approach to estimate the discontinuity at the cutoff is to compare the earnings

of those who barely were admitted (e.g., those with adjusted SAT scores of 0 or 10) to

those who were barely rejected (e.g., those which adjusted SAT scores of-20 or -10).

However, if earnings increase with adjusted SAT scores as is likely the case, this will

overstate the effect of admission to the flagship university on earnings.

The alternative approach is to estimate an equation for the outcome as a function

of the adjusted SAT score. Specifically, we estimate the following equation using least

squares regression:

Outcome, = o3 + + P1X + 02(Admit,) + y(f(Adjusted SAT Score,)) + Ei

where Admit, =1 if (Adjusted SAT Score,) >0, f(Adjusted SAT Score,) is a flexible

polynomial function of the adjusted SAT score, and X is a vector of control variables,

which included year-by-term of admission dummies, actual SAT score and high school

grade point average.4 I then estimate this equation using various functions f(-).

2.4 The Admission Rule

2.4.1 Estimating the Admission Rule

Because the admissions records are nearly 20 years old, the university did not have

records of the exact rules used to determine admissions. During the time in question,

however, admissions decisions were made using a discrete sliding scale of high school



4 By controlling directly for SAT score and high school GPA, we control for the fact that the earnings
ability of an individual with a high SAT score and low GPA may be different from that of an individual
with a high GPA and a low SAT score, even if both have the same adjusted SAT score.









GPA (as adjusted by the university to account for course content and differences in high

school GPA scales) and SAT score. That is, for a given high school GPA, the student

was admitted if her SAT score met or exceeded the cutoff SAT score. Higher high

school GPAs implied lower minimum SAT scores necessary for admission. For example,

to compensate for a high school GPA that was one tenth of a point lower, a student may

have to have an SAT score that is 20 points higher.6

In order to estimate the admission cutoff, the data were first partitioned by race

and term of application (either summer or fall). The data were then partitioned further by

high school GPA, after which the following equation was estimated using Ordinary Least

Squares:

Acceptance = fo + fl(SAT Cutof) + e

where Acceptance is a dummy variable equal to one if the student was accepted and

SAT Cutoff was a dummy variable equal to one if the SAT score was greater than or

equal to a given SAT score.

For example, the SAT cutoff for the fall of 1986 for white males with a high

school GPA of 3.5 was determined by estimating this equation separately using all

possible SAT scores (e.g., from 800 to 1400) as the cutoff. The SAT score that resulted

in the estimation with the highest R2 was the cutoff that was then used.7 This process was





5 For some students, ACT scores were used instead. In those cases, we converted these to equivalent SAT
scores using the university formula.
6 To assure the confidentiality of the university that provided the data, we cannot reveal the admission
standards as we estimated them. However, we can note that the tradeoff between SAT score and high
school GPA was nonlinear.

7 The "winning" R2 was typically around 0.50.









repeated for all cohorts. For example, it was repeated for the fall of 1986 for white males

with a high school GPA of 3.6, and then 3.7, etc.

2.4.2 Does the Admission Cutoff Predict Which Students Are Accepted and Which
Are Rejected?

After estimating the admission cutoff, the obvious question is whether or not the

probability of acceptance at the university is discontinuous at the admission cutoff. This

can be seen in Figure 1, which shows the probability of being accepted (the outcome) on

the vertical axis and the number of SAT points above or below the cutoff given the

student's high school GPA on the horizontal axis. This figure takes the same form as

others presented after it. The open circles represent local averages. For example, at an

adjusted SAT score of zero (i.e., for students who barely made the estimated admissions

cutoff), the open circle is the percentage of those applicants who were accepted at the

flagship.

The estimates of the discontinuity shown in Figure 1 are reported in Table 1.

Row (1) reports estimates of the discontinuity without controlling for either a function of

the adjusted SAT score or the actual SAT score and high school GPA. In contrast, the

regression equations that yielded the discontinuity estimates reported in rows (2) (4)

included polynomials of order 3 or higher in the adjusted SAT score. For example, the

equation estimated in row (2) includes the variables (Adjusted SAT Score), (Adjusted

SAT Score)2, and (Adjusted SAT Score)3 as well as those same variables interacted with

a dummy equal to one if the applicant was predicted to have been admitted by the

flagship (i.e., those for whom the Adjusted SAT Score > 0). Specifications (2) and (4)

also control for each applicant's actual SAT score and adjusted High School GPA.









The results are consistent in showing that there is a large and statistically

significant discontinuity in the likelihood of acceptance at the admission cutoff on the

order of 68 69 percentage points. For example, in the preferred specification in row (4)

that allows for fourth-order polynomials in Adjusted SAT Score on both sides of the

admission cutoff, the estimated discontinuity is 68.6 percentage points, which is

statistically significant at all traditional levels. Furthermore, a look at the underlying data

in Figure 1 shows that this discontinuity is not simply the consequence of an incorrect

functional form.

2.4.3 Potential Causes of the 'Fuzziness' of the Estimated Admission Discontinuity

The fact that this estimated discontinuity is less than one means that this design

utilizes a 'fuzzy' discontinuity. Several factors may be responsible for this, all of which

must be considered when interpreting the results on earnings. First, a handful of high

schools had reputations for giving lower grades than average. While this was not taken

into account by the university in calculating adjusted high school grade point averages, it

was something taken into account during the admissions process. Other exceptions were

made for student-athletes and perhaps for the occasional son or daughter of donors. This,

however, does not invalidate the regression-discontinuity design. Rather, any estimate of

the effect of admission on earnings will be valid only for those who are affected by the

admission guideline. While this is the majority of applicants, it would not include, for

example, student-athletes or those who attended one of the handful of high schools

treated differently by the admissions committee. Indeed, the discontinuity shown in

Figure 1 shows clearly that the estimated admission rule was the defining factor in

admissions for the majority of applicants.









There are other sources of noise that may cause the estimated discontinuity in the

probability of being admitted to be less than one. As in any process with human

involvement, errors in either the decision-making process or the reporting process almost

certainly exist to some degree. Even more significantly, in any given term the university

aimed to enroll a certain number of students. Given uncertainty about yields, the

university would often change the admission rule slightly during the process to accept

more or fewer students, thereby introducing noise into the admission rule.8'9 Finally, and

perhaps most importantly, given the presence of any noise in the admission process such

as that caused the factors mentioned above, the estimation of the rule is itself probably

characterized by some degree of error, especially for cells in which there were relatively

few observations.

However, there are less innocuous explanations of why the estimated discontinuity

is less than one. Perhaps the most problematic of these would be that the university

observes something about the student unobserved to the researcher, which is the type of

bias about which Dale and Krueger (2002) were primarily concerned. The best evidence

against this possibility comes from the application form itself, which reveals the

information about the student that was disclosed to the university. Contrary to what one

might expect based on the application process for universities at the current time, the

application in the late 1980's was very simple. On it, students were required to include


8 According to one admission official who served in the late 1980's, the university aimed to err on the side
of a policy that was too low at first, then toughened it slightly if more students chose to attend than
expected. In this way the university didn't reject applicants who it would have accepted had the university
processed the application somewhat more quickly.

9 This noise will not bias the earnings estimates so long as the applicants who were admitted did not have
different earnings potential relative to those with identical SAT and high school GPAs who were not
admitted. This seems, at least to us, like a reasonable assumption given the applicant and bureaucratic
noise that determines the processing order of applications.









their race, age, nation of birth, address, high school name and address, emergency contact

information, planned major, and current semester high school courses. In addition,

applicants were asked if they were found guilty of any non-minor offenses or to have

interfered with the operation of any educational institution. Each applicant was also

asked whether family members attended the university. Finally, the applicant was

required to have official high school transcripts and an SAT or ACT score sent to the

university. Notably absent from the required application materials were letters of

recommendation and essays.

As stated earlier, of the information contained in the application, the only parts

used in making the application decision were the SAT score and the (adjusted) high

school grade point average. More important, however, is that the simplicity of the

admission rule consisting of a sliding scale using adjusted high school GPA and SAT

score that the university asserts to have used in this time period is reflected in the

application itself.

As a result of the 'fuzzy' admissions cutoff, all wage discontinuity estimates must

be reweighted by the estimated admission discontinuity in order to determine the

treatment effect.

2.4.4 Do Applicants Who Just Meet the Admission Cutoff Subsequently Attend and
Graduate from the Flagship State University?

Although we estimate an intent-to-treat effect in order to avoid the selection bias

that might arise from choosing whether to attend the flagship state university conditional

on acceptance, clearly the receipt of an acceptance letter by itself could not affect

earnings later on. Rather, the mechanism through which the effect could occur would be

attending the flagship university.









The data show that there are large differences in the likelihood of subsequent

attendance of the flagship university between those who barely met the admission cutoff

and those who barely missed it. For example, among those who just met the admission

cutoff (those with adjusted SAT scores of 0), 51.0% of them subsequently attended the

flagship university compared to 10.4 % of those students who missed the cutoff by 10

SAT points, given their high school GPA. Among those who met or exceed the

admission cutoff by no more than 20 SAT points (again, conditional on high school

GPA), 53.3% subsequently attended the flagship university compared to only 11.5% of

those who missed the cutoff by no more than 30 SAT points.

As one might expect, there are also significant differences in the likelihood of

graduating from the flagship university. Only 7.2% of those with adjusted SAT scores of

-10 subsequently graduate from the flagship university compared to 32.5% of those who

barely were accepted and had adjusted SAT scores of 0. Similarly, only 8.0% of

applicants who missed the cutoff by no more than 30 SAT points (conditional on high

school GPA) graduated from the flagship, compared to 36.3% of those who exceeded the

cutoff by no more than 20 SAT points.

2.4.5 Do Admitted Applicants above the Admission Cutoff Enroll and Graduate
from the Flagship at Different Rates than Applicants Just Below the Cutoff?

One test of whether applicants on either side of the discontinuity are similar is to

see if, conditional on acceptance (or enrollment), those who barely met the estimated

admission cutoff were more or less likely to enroll (or graduate) than those barely missed

the estimated cutoff.10 This can best be seen by Figures 2 and 3. Figure 1 shows the



10 Unfortunately, this is one of the only tests we can perform to see if students on either side of the cutoff
were similar, since we were unable to get additional background information on the applicants. Later in the
paper we will show that controlling for SAT score and adjusted high school GPA does not change the









likelihood of choosing to enroll at the flagship university, conditional on being accepted

to the flagship university." Figure 2 shows the likelihood of graduating from the

flagship university, conditional on enrolling at the flagship university. To the extent that

the graduation rates were discontinuous at the admission cutoff, one might be concerned

that the groups on either side of the admission cutoff were not in fact similar.

There does appear to be a difference in the likelihood of enrolling at the flagship

university, conditional on admission, at the admission cutoff, as shown by Figure 1.

There does not, however, appear to be a discontinuity in the likelihood of graduating

from the flagship university, conditional on enrollment, as shown in Figure 2. Although

the results on enrollment may raise some questions, the fact that the graduation rates are

no different for those who barely exceeded the cutoff than those who barely missed it

supports the assumption that those on either side of the admission cutoff are very similar

except for their likelihood of being admitted.

2.5 Attrition from the Earnings Data

As discussed earlier, one drawback to using these state-level wage data is that some

applicants may not be observed with positive earnings 10 15 years after high school

graduation because they moved to a different state. To the extent that the probability of

working in-state is endogenous to admission and attendance at the flagship university, the

discontinuity estimates may be biased. The data allow us to examine the extent to which

this is the case by comparing the probability of observing applicants who were barely

discontinuity estimates, which shows that, even on the margin, the university was not selecting high GPA
(or high SAT) students among others with equivalent adjusted SAT scores.

11 Since there are relatively few students below the cutoff who were admitted to the flagship (as shown in
Figure 1), these data were restricted to those who missed the cutoff by fewer than 100 points. There were
58 applicants who missed the cutoff by 10 SAT points but still were accepted; 42 of those students
enrolled.









accepted to that of observing the earnings of applicants who were barely rejected.

Furthermore, we do so separately for men than women due to the differences in their

respective labor force participation rates. We also do so using two definitions of being

observed with positive earnings. For example, we examine whether there is a

discontinuity in the likelihood of being observed with 4 consecutive quarters of earnings

in the 10th year after high school graduation as well as in the likelihood of being observed

with any positive quarter of earnings in that year.

2.5.1 The Attrition of White Males

The best evidence of whether there is a discontinuity in the attrition of men in the

earnings data is visual. Specifically, Figures 4a 4i show the likelihood of being

observed with 4 consecutive quarters of earnings in each of the 7th- 15th years after high

school graduation. Shown on each figure are the local averages as well as the predicted

probability based on a cubic polynomial of adjusted SAT score on either side of the

admission cutoff. These discontinuity estimates are summarized in Table 2. Of the

estimated discontinuities shown in Figures 4a 4i, the estimated discontinuity is

statistically significant at the 10% level only for 14 years (Figure 4h, estimate = 0.048,

p=0.061). More importantly, perhaps, is that it is difficult to see a distinct discontinuity

in the underlying data in any of the nine figures.

Figures 5a 5i show the likelihood of being observed with any positive earnings in

the years following high school graduation, beginning in the 7th year when the applicants

were approximately 25 years old. Here, none of the estimates is statistically significant at

the 10%, although the estimate for 11 years comes close (p = 0.105). Thus, of the

eighteen estimations shown on the first two columns of Table 2 (and in Figures 4 and 5),

only one estimate is statistically significant at the 5% level, which coincidentally is what









one would expect by chance alone. In addition, the underlying data shown in the figures

hardly reveal compelling evidence of a discontinuity in any of the graphs. Consequently,

it seems unlikely that the wage discontinuity estimates should be biased because those

who were barely accepted at the flagship state university were more or less likely to show

up in the earnings data 7 15 years after entering college.

2.5.2 The Attrition of White Females

The story is remarkably similar for white women. Figures 6a 6i show the

probability of being observed with 4 consecutive quarters of earnings 7 15 years after

high school graduation. Similarly, Figures 7a 7i show the probability of being observed

with any positive earnings 7 15 years after graduating from high school. Of all the

discontinuity estimates from those graphs, only the discontinuity for being observed with

any positive earnings after 9 years (Figure 7c, estimate = -0.067) was statistically

significant at either the 10% or 5% level. Coincidentally, out of 18 estimates summarized

in the last two columns of Table 2, one would expect roughly one statistically significant

estimate by chance alone. And again, no compelling discontinuities seem evident in the

underlying data graphed in Figures 6a 6i and Figures 7a 7i.

2.5.3 The Admission Discontinuity for Those Observed with Positive Earnings

Even though there does not appear to be compelling evidence of attrition in the data

caused by admission to the flagship state university, since the wage estimate results are

based on the sample of applicants observed with positive earnings, it is instructive to

ensure that the admission discontinuity is also observed with this group. The underlying

data and estimated admission discontinuity is shown on Figure 8a and 8b for that group

of individuals for whom we observe 25 consecutive quarters of earnings in the 12th and

15th year following high school graduation, respectively. Figures 9a and 9b show the









underlying data and regression discontinuity estimates for the applicants observed with

any positive earnings in the 12th and 15th years following high school graduation,

respectively.

The result is clear, if unsurprising: There is still a statistically significant

discontinuity of approximately 0.70 even for those who stayed in the sample and were

observed with positive earnings 12 and 15 years after high school graduation.

2.6 The Effect of Admission at the Flagship University on Labor Market Outcomes

2.6.1 The Earnings of White Males

Since the effect of attending a flagship state university may very well vary by race

and sex, I first examine the effect of admission at the flagship university on the

subsequent earnings of white males. To do so, I used two definitions of earnings. The

first was the natural log of the sum of four quarters of consecutive real earnings in the

10th 15th years following high school graduation, or when the individuals were

approximately 28 33 years old.12 Consequently, for those who applied for admission in

the fall of 1986, I used earnings received from the 3rd quarter of 2001 through the 2nd

quarter of 2002. Similarly, for those who applied for admission in the fall of 1987, I used

earnings received from the 3rd quarter of 2002 through the 2nd quarter of 2003, and so on.








12 The advantage of examining earnings in this time period was shown by Mincer (1974), who showed that
the return to schooling can be underestimated if earnings prior to the "year of overtaking" are used.
Assuming that the cost of investment is constant over time, that year is equal to (1+1/r) years after the
completion of formal education, where r is the interest rate. Thus, assuming r=0.09 and an applicant
finishes schooling at age 22, the year of overtaking is 22 + 12.1 = 34.1, which is approximately the age
examined in this paper. This matters to the extent that attending the flagship university causes differences
in post-schooling investment.









The second measure of earnings is the natural log of the annualized average

earnings in the four quarters of consecutive earnings in each of the 10th 15th years

following high school graduation.13

The results for the 10th 15th years following high school graduation are shown in

Figures 10a 1 Of for the consecutive quarter earnings measure and in Figures 1 la 1 If

for the annualized earnings measure. Plotted on each figure are the local averages for

each adjusted SAT score along with two fitted lines. Since the underlying data appear-

at least to us-to be linear in the adjusted SAT score, the first fitted line of predicted

earnings is from an OLS regression in which we control for adjusted test score in a linear

fashion allowing for a different slope on either side of the admission cutoff. The second

fitted line of predicted earnings is from an OLS regression in which we control for a

cubic polynomial of adjusted test score as well as a cubic interacted with a dummy

variable equal to one for those with an adjusted SAT score greater than or equal to 0.

The discontinuity estimates from both approaches and for both measures of

earnings are shown on the figures themselves as well as in Table 3. In the linear case,

they range from 1% to 8%, which corresponds to an increase in wages due to admission

at the flagship university on the order of 1.5% to 11%. However, only 4 of the 12

estimates are statistically significant at the 10% level, and only 2 of those are statistically

significant at the 5% level.

The linearity assumption in the functional form is important, however, as is evident

from the discontinuity estimates using the cubic functional form. Those discontinuity


13 It appears from the data that when positive earnings are observed in one quarter, they tend to be observed
for many consecutive quarters. Still, to the extent that some individuals move out of (or in) state during,
say, the 10th year after high school graduation, this second earnings measure will allow them to remain in
the sample.









estimates range from 0.123 to 0.193, which corresponds to an increase in wages due to

admission at the flagship university on the order of 18% 28%. All but 3 of the 12

estimates shown in Figures 10a 10f and Figures 1 la 1 If are statistically significant at

the 5% level and all but 1 are statistically significant at the 10% level.

This difference caused by the regression specification is largely driven by the fact

that the earnings of those who just missed the admission cutoff by 40 or fewer SAT

points are lower than those of applicants who missed the cutoff by 50 70 points. The

reason for this is not immediately clear; one would certainly expect earnings to rise as

ability rises. One potential explanation is that those who barely were rejected still

attended another 4-year university, while those who missed the cutoff by more either did

not attend college or attended a community college first. Consequently, those who just

missed may have lower earnings because they have less work experience. However, this

explanation is not entirely satisfactory both because one would expect college graduates

to catch up with high school graduates by age 33. Furthermore, one would expect the

difference to decline from age 28 33 as the college graduates catch up on the earnings

scale. It should be noted, however, that this downward slope in the fitted regression line

cannot be driven by the selective admission of students on the left-hand side of the cutoff.

Even if the university did selectively admit students who just missed the cutoff on the

basis of some unobserved (to us) factor that is correlated with higher earnings potential,

those admitted students remain on the left-hand side of the cutoff in the earnings graphs.

Still, since the functional form assumptions do seem to be important, more sensitivity

analysis will be performed later in the paper.









One pattern that does become apparent from the discontinuity estimates is that they

are quite similar across the two measures of earnings. For example, the discontinuity

estimate using the linear functional form is 6.9% after 15 years for the measure that uses

four consecutive quarters of earnings and 6.3% using the annualized measure of earnings.

2.6.2 White Females

2.6.2.1 The effect of admission on subsequent earnings

The underlying data and fitted regression lines for women are shown in Figures 12a

- 12f for the consecutive earnings measure and Figures 13a 13f for the annualized

earnings measure. The summary of the estimates shown on these figures is given in

Table 4. As shown there, the linear regression discontinuity estimates on earnings 10 -

15 years after high school graduation for the two earnings measures are all negative and

range from -0.018 to -0.095, which implies a flagship earnings effect of -2% to -13%.

Only 3 of the 12 estimates are statistically significant at the 10% level, 2 of which are

also statistically significant at the 5% level.

However, once again there is significant sensitivity to the functional form

assumption used. Allowing for a cubic functional form of adjusted test score causes the

regression discontinuity estimates to range from -0.108 to 0.136, although only 3 positive

estimates are statistically significant at conventional levels. The only statistically

significant estimates are the estimates for the discontinuity in 4 consecutive quarters of

earnings 11, 13, and 14 years after high school graduation which range from 0.118 to

0.136. Once again, this difference in the discontinuity estimates appears to be driven

largely by the fact that those who miss the admission cutoff by 20 or fewer points tend to

have lower earnings than those who missed the cutoff by 30 40 points, causing the

cubic regression line to trend downward as it approaches the cutoff









There is also less consistency in the estimates across the two measures of earnings,

which could be a consequence of the fact that women are more likely to work part-time

or leave the labor force than are men.

It does seem difficult, at least to us, to see any distinctive discontinuity in the

underlying data themselves that are shown in Figures 12a 12f and Figures 13a 13f.

Thus, it seems difficult to pin down the flagship university earnings effect for women.

2.6.2.2 The effect of admission on the labor market attachment of white women

It is possible that the wide range of estimated discontinuities in the earnings of

women is due in part because women who are accepted at and subsequently attend the

flagship state university are more or less likely to leave the labor force. Such a difference

could occur if the marriage market at the flagship university differed from that of the

next-best-alternative university. To analyze this, we restrict the data to include only

women for whom positive earnings are observed in the 15th year following high school

graduation. We then examine the degree of labor force attachment by calculating the

percentage of quarters in the 5 years prior to that in which the women were observed with

positive earnings. The resulting outcome gives us a measure of labor force attachment

for women from age 28 to age 33.14

The local averages of this measure of labor force participation are graphed in

Figure 14. There is no discernible discontinuity in labor force participation at the

admission cutoff, which is reassuring in that it suggests that the earnings estimates for





14 This age was chosen since by age 28 almost all women will have completed their educations. In
addition, we include only those who are observed with earnings 15 years after high school graduation in
order to distinguish labor force participation from the propensity to move out of state.









women presented earlier are unlikely to have been driven by differences in labor force

participation.

2.7 The Sensitivity of the Earnings Estimates

2.7.1 White Men

Given the sensitivity of the discontinuity estimates for white men to functional

form, here I examine the sensitivity more fully to both functional form and specification.

Since the results were very similar across both earnings measures, I only use the four

consecutive quarter measure of earnings. Similarly, we only examine earnings 12 and 15

years after high school graduation. The results from these robustness checks are reported

in Table 5.

The first five rows examine the sensitivity of the estimates to both the functional

form of the adjusted SAT score and to the inclusion of control variables. As for the

latter, it is evident from comparing the estimates in specification (1) to (2) and comparing

specification (4) to (5) that the inclusion of control variables (year/term dummy variables

and actual SAT score and GPA) does not affect the discontinuity estimates in a

substantial way. This is consistent with the assumption underlying the regression

discontinuity design that all other variables that affect earnings (such as high school

GPA) vary continuously at the admission cutoff.

However, it is also clear that the choice of functional form of adjusted SAT score

matters significantly. Specifically, the inclusion of a quadratic or higher order term

allows the fitted regression line to slope downward as it approaches the admission cutoff

from the left, as seen earlier in the earnings figures. This in turn results in estimates that

are approximately twice as large as those resulting from the linear specification.









In specifications number (6) and (7), the sample is restricted to only those

applicants who were observed with positive quarterly earnings in every quarter for 6

straight years starting in the 10th year after high school graduation. Thus, these estimates

can be interpreted as the flagship effect for those applicants who are particularly attached

to the labor market. Although the estimates using the linear functional form are similar,

the discontinuity estimates using a cubic functional form increase from approximately

0.08 to 0.25. Thus, although functional form matters here as well, if anything it appears

that the flagship earnings effect is larger for applicants with a strong attachment to the

(in-state) labor force.

Specification (8) restricts the sample to only those applicants who missed or

exceeded the admission cutoff by no more than 100 SAT points. As one might expect

from looking at the data in Figures 10 and 11, the statistically significant regression

discontinuity estimates of 0.167 and 0.157 are very similar to those using a polynomial of

order 2 or higher using the full data set.

Finally, we examine the extent to which there is a discontinuity in earnings for the

median earner in the sample. Here, the estimated discontinuities range from 0.034 to

0.098, none of which are statistically significant at conventional levels and which are

lower than the OLS estimates. This suggests that although attending the state's flagship

state university may increase earnings on average relative to the alternative, there is less

compelling evidence that it does so for the median earner.

2.7.2 White Women

We also perform a similar set of robustness checks for white women, the results of

which are shown in Table 6. The results are consistent with those for the men in that the

inclusion of the control variables does not affect the estimates in a meaningful way.









Similarly, the functional form of adjusted SAT score does seem to matter somewhat; the

quadratic and cubic specifications result in estimates that are less negative or even

positive relative to the linear specification.

However, the most striking result concerns the effect of attending the flagship state

university for women who have strong attachment to the labor force, as shown in

specifications (6) and (7). For these women, the estimates are positive and, for three of

the four estimates, are statistically significant at the 10% level. As shown in Table 6, the

discontinuity estimates are 0.144 and 0.217 for 12 and 15 years after high school

graduation using the cubic specification, both of which are statistically significant at the

1% level. Using the linear functional form, the discontinuity estimates are 0.77 and 0.53

for 12 and 15 years after high school graduation, only the former of which is statistically

significant at the 10% level.

As shown in row (8), restricting the sample to only those applicants within 100

SAT points of the admission cutoff does not substantially affect the estimates. And

finally, the median regression discontinuity estimates reported in rows (9) and (10)

confirm the result that the cubic specification results in more positive discontinuity

estimates, although only the estimate for 12 years is statistically significant at the 10%

level.

2.8 Conclusion

In this paper, we identify the causal effect of attending the flagship state

university by utilizing a regression discontinuity design that compares the earnings of

those who were just accepted by the flagship to the earnings of those who just missed the

admission cutoff. We do so by combining confidential student applicant records from a

large flagship state university to earnings data collected by the state through the









Unemployment Insurance Program. After linking these two data sets together, we

estimate the admission cutoff at the flagship and find that this estimated cutoff based on

applicants SAT score and adjusted high school GPA coincides with a very large, distinct

discontinuity in the likelihood of being admitted to the university.

We then examine whether or not there is a discontinuity in the likelihood of being

observed with positive earnings 7 15 years after high school graduation. We find little

evidence that admission to the flagship causes men or women to more or less likely to

work in-state than their counterparts who barely missed the admission cutoff.

Finally, we estimate the intent-to-treat effect of attending the flagship state

university on total earnings. For white men, we find evidence of positive discontinuities

that translate to increases in earnings from 1% to 27%, although the discontinuities are

not estimated precisely in all specifications. The size of the coefficients and their

statistical significance depend largely on the functional form; polynomials of adjusted

SAT score of order 2 or higher result in larger, statistically significant earnings

discontinuities. There does not appear to be an effect on the median earnings of those

who are admitted to the flagship state university, however.

For women overall, we find little consistent evidence of either a positive or

negative effect of attending the flagship state university on earnings. However, we do

find evidence of a large and statistically significant effect on the earnings of the subset of

women with strong attachment to the labor force; the estimates of the effect on earnings

range from 8% to 32%.

The results provide some suggestive evidence that being accepted by and attending

the flagship state university may indeed cause an increase in subsequent earnings.









Consequently, the higher earnings that result from attending the flagship state university

may justify, at least to some extent, costs (i.e., SAT preparation courses) undertaken by

students and parents to gain admission to and/or to attend the top university in the state,

at least for men and for women with a strong attachment to the labor force. Perhaps

more importantly, although this paper did not (yet) examine the effect of attending the

flagship university on minority applicants, the results for whites may yield insight

nonetheless into the potential consequences of the elimination of affirmative action and

the subsequent reduction in enrollment rates for minorities at the top state schools. To

the extent that the effect for minorities is similar to that of white applicants, one may well

expect that the earnings of minorities may fall as a result of the elimination of affirmative

action in the admissions of flagship state universities.