ESSAYS ON THE ECONOMICS OF JUVENILE CRIME AND EDUCATION By Daniel Litwok A DISSERTATION Submitted to Michigan State University in partial fulfillment of the requirements for the degree of Economics Doctor of Philosophy 2015 ABSTRACT ES SAYS ON THE ECONOMICS OF JUVENILE CRIME AND EDUCATION By Daniel Litwok This dissertation consists of three independent chapters. The first chapter focuses on the effects of expungement of records of juvenile delinquency. Despite differing terminology, a ll fifty states and the District of Columbia have statutory remedies allowing records of juvenile delinquency to be treated as if they do not exist, eliminating the possibility that a future college or employer may learn of the record. Whereas most states require an application for such the effect of expungement on youths, I develop a conceptual model to consider the dynamic incentives created by automatic expung ement that predicts an increase in the incen tives to initially commit crime but a reduction in the incentives to commit additional crime as an adult . Using unique data I obtain from three application states, I show that expungement is rarely used when an application is required. Based on these statistics and predictions in the conceptual framework, I use survey data to estimate the effects of expungement on juvenile arrest, recidivism as an adult, educational attainment, and future labor market outcomes. I find no response to the incentive for first time offenders in automatic states, but I do find a negative effect on long - term recidivism. I also find modest positive effect s of expungement on pursuit of higher education and future earnings . These findi ngs suggest that expungement is socially beneficial with limited social costs. The second chapter continues to focus on juvenile crime by studying the effects of Graduated Driver Licensing (GDL) laws on teenage crime. Although GDL laws were adopted to re duce the risk associated with novice driving, I investigate a different potential effect of these laws: might the benefits of GDL extend beyond driver safety and also reduce juvenile crime? GDL laws effectively impose a statutory driving curfew and a limi tation on the number of passengers in motor vehicles. Both the timing of motor vehicle access and a limitation on the peer influences available in a motor vehicle could significantly affect the set of potential offenders and the marginal costs for certain crimes. Using a differencing strategy based on the implementation of GDL, I find e vidence that these laws reduce violent and property crime among 16 year olds. I then show that nighttime restrictions are the component of GDL most responsible for the red uction in crime. These results suggest that there is another benefit to states for adopting GDL laws and provide insight into the production of teenage crime. The third chapter, co - authored with Leslie Papke, studies the response of young teachers to cha nges in their retirement compensation. S everal states have recently enacted reforms in an effort to reduce their future pension obligations , but the vast majority of public school teachers continue to be covered by defined benefit plans. While these defi ned benefit retirement incentives have been the focus of much research, we focus instead on the early years pension wealth upon vesting . Th en, we show that pension characteristics relevant to the early are negatively related to the fraction of younger teachers in a state. Finally , we use data from the National Longitudinal Survey of Youth to study the first exit f rom teaching for new teachers. We find that pension parameters, such as vesting requirements and availability of defined contribution alternatives, are significantly related to first exit from teaching. Our preferred estimates indicate that young teacher s are 11 percentage points more likely to exit teaching in a state that increases its vesting rule from five to 10 years. Copyright by DANIEL LITWOK 2015 v For my family. vi ACKNOWLEDGEMENTS I would like to begin by acknowledging my advisor, Steven Haider, for his endless guidance and support in navigating the tides of graduate school. He has helped me grow and develop as an economist, a thinker, and a human being. After each and every meeting with Steven throughout graduate scho ol I felt better about my work a testament to his outstanding mentorship. Special thanks also go to Stacy Dickert - Conlin, Jeff Biddle, and Chris Melde, the remainder of my committee. Their constructive and insightful feedback was instrumental in develo ping the projects that ultimately comprise this dissertation. I am also thankful for the relationships I developed during my tenure at Michigan State with faculty members , staff members, and fellow graduate students . I would like to specifically recogniz e Soren Anderson, Michael Conlin, Todd Elder, Scott Imberman, Lori Jean Nichols, Leslie Papke, Gary Solon, and Jeff Wooldridge. Their support of my work, whether through coursework , co - authorship, feedback on my research, or friendship, was invaluable to my experience at Michigan State. Thanks also to Barbara Schneider for allowing access to her restricted data lab. Similarly , my peers in the program were able to provide constructive feedback on my work while also becoming close friends . I owe many than ks to Michael Bates, Andrew Bibler, Quentin Brummet, Paul Burkander, Hassan Enayati, Christopher Khawand, and Gregory Wallsworth . I would also like to recognize the funding sources that generously supported my progress toward my Ph.D as well as the restricted data agreements that allowed me to pursue my research agenda. My support from the Michigan State University Distinguished Fellowship and the vii Institute for Education Sciences f unded Doctoral Specialization in the Economics of Education ( Grant R305B090011 ) gave me the freedom to focus on the development of my research . The research included in this dissertation was conducted with restricted access to Bureau of Labor Statistics ( BLS) data. The views expressed are my own and do not represent the views of the U.S. Department of Education or the BLS. Last, I would like to acknowledge the support of my family. My siblings, Yoni and Anat, rovide inspiration and motivation to follow my dreams. Abba and Ima, my biggest role models, continue to lead by example in the ways of Derech Eretz . Finally, to Carly, who sacrificed everything so I could pursue my Ph.D., words cannot express my sincere gratitude for your endless love and support. You amaze me every day with your humor, humility, demeanor, and wisdom. viii TABLE OF CONTENTS LIST OF TABLE S ................................ ................................ ................................ ............. x LIST OF FIGURES ................................ ................................ ................................ ........ xii CHAPTER 1: HAVE YOU EVER BEEN CONVICTED OF A CRIME? THE EFFECTS OF JUVENILE E XPUNGEMENT ON CRIME, EDUCATIONAL, AND LABOR MARKET OUTCOMES ................................ ................................ .......... 1 1.1 Introduction ................................ ................................ ................................ ........ 1 1.2 Institutional Details ................................ ................................ ............................ 4 1.3 Literature Review ................................ ................................ ............................... 6 1.4 Conceptual Framework ................................ ................................ ...................... 8 1.5 Data ................................ ................................ ................................ .................. 11 1.6 Empirical Strategy ................................ ................................ ........................... 13 1.6.1 Empirical Concerns ................................ ................................ ........... 1 4 1.6.2 Empirical Techniques ................................ ................................ ....... 16 1.6.3 Do Juveniles Apply For Expungement? ................................ ........... 19 1.7 Results ................................ ................................ ................................ .............. 2 1 1.8 Discussion and Conclusion ................................ ................................ .............. 29 CHAPTER 2: DID GRADUATED DRIVER LICENSING LAWS DRIVE A REDUCTION IN CRIME? ................................ ................................ ............................. 33 2.1 Introduction ................................ ................................ ................................ ...... 33 2.2 Policy Background and Literature Review ................................ ...................... 35 2.2.1 GDL and Mo tor Vehicle Fatality ................................ ...................... 35 2.2.2 Crime ................................ ................................ ................................ . 36 2.3 Data ................................ ................................ ................................ .................. 39 2.3.1 GDL Policy Data ................................ ................................ ............... 39 2.3.2 Outcome Data ................................ ................................ ................... 39 2.4 Methodology ................................ ................................ ................................ .... 43 2.5 Results ................................ ................................ ................................ .............. 43 2.5.1 Effects on Crime ................................ ................................ ............... 43 2.5.2 Threats to Validity ................................ ................................ ............ 45 2.5.3 Robustness ................................ ................................ ........................ 47 2.5.4 Heterogeneity and Dynamics ................................ ............................ 49 2.5.5 Mechani sms ................................ ................................ ...................... 51 2.6 Discussion and Conclusion ................................ ................................ .............. 53 CHAPTER 3: INTERSTATE DIFFERENCES IN PENSION VESTING RULES, K - 12 TEACHER EXPERIENCE, AND TEACHER EXIT ................................ ......... 55 3.1 Introduction ................................ ................................ ................................ ...... 55 3.2 Related Literature ................................ ................................ ............................. 58 3.3 Vesting Rules and Teacher Pension Wealth ................................ .................... 60 ix 3.4 Pension Plan Characteristics and the Distribution of Teacher Experience ...... 65 3.5 Evidence from the National Longitudinal Survey of Youth of 1997 ............... 67 3.6 Conclusion ................................ ................................ ................................ ....... 73 APPENDICES ................................ ................................ ................................ .................. 75 Effects of Juvenile Expungement on Crime, Educational, and Labor ................................ ................................ ..................... 76 ................................ ................................ ................ 84 K - 12 Teacher Experienc ................................ ........... 93 Effects of Juvenile Expungement on Crime, Educational, and Labor ................................ ................................ ................... 104 Red ................................ ................................ .............. 107 K - ................................ ......... 112 The Effects of Juvenile Expungement on Cr ime, Educational, and ................................ ................................ ........ 115 ................................ ................................ .............. 144 K - 12 Teacher Experience, and Tea ................................ ......... 148 BIBLIOGRAPHY ................................ ................................ ................................ .......... 152 x LIST OF TABLES Table A.1: State Level Descriptive Statistics ................................ ................................ .... 77 Table A.2: Aggregate Expungement Statistics in Application States ................................ 78 Table A.3: Descriptive Statistics by Regime ................................ ................................ ..... 79 Table A.4: Baseline Differences in Arrest s ................................ ................................ ....... 80 Table A.5: Effect of Arrest and Conviction on Long - Term Outcomes ............................. 81 Table A.6: Long - Term Effects of Automatic Expungement: Proxy Variable Analysis .... 82 Table A.7: Long - Term Effects of Automatic Expungement: Difference - in - Differences Analysis ................................ ................................ ................................ .............................. 83 Table B. 1: State Level Summary Statistics ................................ ................................ ........ 85 Table B.2: Effect on Arrest Ratio by Age ................................ ................................ .......... 86 Table B.3: Primary and Secondary Enforcement, Age 16 ................................ ................. 87 Table B.4: Robustness of Dependent Variable, Age 16 ................................ .................... 88 Table B.5: Effect on Arrest Ratio by Gender, Age 16 ................................ ....................... 89 Table B.6 : Effect on Specific Offenses by Gender, Age 16 ................................ .............. 90 Table B.7: Permanent Effects for Older Age Groups ................................ ........................ 91 Table B.8: Effect of Nighttime and Passenger Restrictions, Age 16 ................................ . 92 Table C.1: State Teacher Pension Parameters ................................ ................................ ... 94 Table C.2: Cost of Living Adjustment s ................................ ................................ ............. 95 Table C.3: Simulation Results ................................ ................................ ........................... 96 Table C.4: Summary Statistics ................................ ................................ ........................... 97 Table C.5: Regression Results for Teacher Experience ................................ ..................... 98 Table C.6: NLSY Descriptive Statistics 2002 - 2010 ................................ .......................... 99 xi Table C.7: NLSY Regression Results ................................ ................................ .............. 100 Table C.8: NLSY Regression Results by Teacher Type ................................ .................. 102 Table G.1: Overview of Current Expungement Statutes by State ................................ ... 116 Table G.2: Summary of Expungement Statutes ................................ ............................... 123 Table G.3: All Expungement Data ................................ ................................ ................... 131 Table G.4: NLSY Descriptive Statistics ................................ ................................ .......... 132 Table G.5: Descriptive Statistics by Crime ................................ ................................ ...... 133 T able G.6: State Level Juvenile Crime Regressions ................................ ........................ 136 Table G.7: State Level Adult Crime Regressions ................................ ............................ 137 Table G.8: Long - Term Effects of Automatic Expungement: Proxy Variable Analysis (Unweighted) ................................ ................................ ................................ ................... 138 Table G.9: Long - Term Effects of Automatic Expungement: D ifference - in - Differences Analysis (Unweighted) ................................ ................................ ................................ .... 139 Table G.10: Long - Term Effects of Automatic Expungement: Proxy Variable Analysis (Non - clustered) ................................ ................................ ................................ ................ 140 Table G.11: Long - Term Effects of Automatic Expungement: Difference - in - Differences Analysis (Non - cluste red) ................................ ................................ .............. 141 Table G.12: Effect on College Attendance for Juvenile Convicts (Full Output) ............. 142 Table H.1: Effective Dates of GDL Implementation ................................ ....................... 145 Table H.2: Descriptive Statistics, Traffic Fatalities ................................ ......................... 146 Table H.3: Extension of Previous Results on GDL and Fat alities ................................ ... 147 xii LIST OF FIGURES Figure D.1: Crime Decision by Ability and Expungement Policy ................................ .. 105 Figure D.2: Automatic Expungement States ................................ ................................ ... 106 Figure E.1: Motor Vehicle Access and Crime ................................ ................................ . 108 Figure E.2: Event Study, Violent Crime ................................ ................................ .......... 109 Figure E.3: Event Study, Property Crime ................................ ................................ ........ 110 Figure E.4: Arrests by Time of Day ................................ ................................ ................. 111 Figure F.1: Pension Wealth over the Teaching Career ................................ .................... 113 Figure F.2: Pension Wealth Early in the Teaching Career ................................ .............. 114 Figure G.1: Game Tree and Payoffs ................................ ................................ ................ 124 1 CHAPTER 1 HAVE YOU EVER BEEN CONVICTED OF A CRIME? THE EFFECTS OF JUVENILE EXPUNGEMENT ON CRIME, EDUCATIONAL, AND LABOR MARKET OUTCOMES 1.1 Introduction Since the first juvenile court began hearing cases in 1899, the overarching philosophy of the juvenile court system has been to focus on th e offen der as opposed to the offense. Consequently, the juvenile court tends to provide more rehabilitative sanctions than punitive ones and most states maintain confidentiality of juvenile court proceedings and records, presumably to limit the stigma ass ociated with appearance in juvenile court (Bilchik 1999). However, state statutes determine whether these records can be obtained by anyone from employers in sensitive industries, such as nursing homes or school districts, to the general public. 1 A uniq ue feature of the juvenile court system is the process of expungement. The ability available to juvenile offenders in every state. 2 Despite cross - state differences in terminology, juvenile expung ement statutes contain a number of similar clauses. 3 Conditional on certain requirements, these statutes allow those with records of juvenile delinquency to have their records either closed from all inspection or 1 Anecdotally, many citizens first learn that their juvenile record followed them when they apply for public assistance or certain jobs (Whigham 2012; Quevedo 2013). 2 While expungement is also available to adults in many states, I focus on juven iles for two reasons. First, expungement is typically made more difficult for adults through more stringent eligibility requirements. More importantly, crimes committed by adults are not covered by the same confidentiality provisions available to many ju venile offenders, particularly with respect to the publication of names. Therefore, the growth of the internet has called the effectiveness of adult expungement into question (Calvert and Bruno 2010). 3 The terminology and specifics of these statutes di ffer by state. Other names include setting aside, destruction, expunction, erasure, and closing (see Table G.1) . Despite the differences in terminology, these statutes all describe a process that results in the delinquent activity being legally treated a s if it never occurred. 2 physically destroyed. However, the manner by which expungement is initiated is quite different: whereas most states require a petition of the court to expunge a juvenile record , fourteen states automatically expunge the record. Once the record has been expunged the event can be treated as if it did not occur on college and employment applications, and a criminal background check will not return any juvenile history. 4 The existence of a juvenile record is important because previous studies have found that a criminal history can be a barrier in many important economic markets. For example, prior literature documents that individuals with criminal histories can face struggles in the labor market (Grogger 1995; Pager 2003; Bushway 2004; Holzer et al. 2006; Holzer et al. 2007; Stoll and Bushway 200 8; Finlay 2009). Criminal records can also affect the ability to gain higher education through eligibility for federal loans (Lovenheim and Owens 2014). The American Bar Association (2013) recently argued that the collateral consequences associated with having a record of juvenile delinquency can be more severe than the actual punishment for the crime, and further argued that expungement reduces these consequences. In response to these potential collateral consequences, a recent federal bill titled the R ecord Expungement Designed to Enhance Employment (REDEEM) Act (2014) attempts to make the process of expungement automatic for all nonviolent juvenile offenses. This paper focuses on three primary research questions. First, what are the incentives that ar e created by automatic expungement? Second, do expungement rates differ for states with automatic expungement and states that require a petition? Third, is there an empirical effect of automatic expungement on crime, educational, and labor market outcome s? Answering these 4 There are some exceptions to this claim. State law enforcement officials may have access to expunged rec ords. For example, in many states if the offender later commits a felony the expunged record can be used for sentencing purposes. 3 questions, which have never appeared in the literature, makes this the first empirical paper to focus on juvenile expungement. To answer these questions, I proceed in three steps. First, I develop a conceptual framework that captures t he incentives created by a policy of automatic expungement in the market for crime. Specifically, my model predicts an increase in the propensity to commit juvenile crime and a decrease in recidivism as an adult in automatic expungement states. Next, I present unique data collected from state agencies on the number of annual expungements in three application states. These data indicate a large difference in the expungement rate between automatic and application states, presumably due to lack of knowledg e, myopia , or the different costs associated with the application process. This allows me to infer that the policy effect of automatic expungement can be interpreted as the overall effect of expungement. I use this variation in my empirical work to ident ify the effects of expungement on crime, educational, and labor market outcomes. As a preview of the empirical results, I find that automatic e xpungement does not affect the propensity to commit juvenile crime, but that it does lead to lower rates of rec idivism , higher rates of college attendance and graduation, and higher average earnings for tho se with records of juvenile delinquency. One plausible explanation consistent with these results is that juveniles are unaware of expungement policies and their potential benefits. Overall, my findings suggest that there are large benefits to expungement with limited costs to society. 4 1.2 Institutional Details A record of juvenile delinquency typically begins with an interaction with law enforcement. 5 Once the juvenile offender is in custody , prosecutors and the police determine whether to file a delinquency petition. 6 As defined by the federal Office of Juvenile Justice and delinquency petition states the allegations and requests the juvenile court to adjudicate (or judge) the youth a delinquent, making the juvenile a ward of the court. This language differs from that used in the criminal court system (where an offender is convicted and sentenced) (2013b). Each state a lso has provisions allowing a juvenile to be tried in the criminal court instead of the juvenile court, but use of these waivers is fairly uncommon. For example, in 2009 fewer than five percent of all drug, person, property, or public order cases involvin g juveniles were waived to criminal court (Puzzanchera et al. 2012). A court appearance by a juvenile results in the production of an official court record. There are separate provisions regarding the treatment of juvenile records that depend on whethe r the juvenile is adjudicated delinquent. I focus on individuals that are adjudicated delinquent because these records have potential to be a significant barrier to future educational endeavors or employment. 7 5 According to the Office of Juvenile Justice and Delinquency Prevention law enforce ment referrals accounted for 83 percent o f all delinquency cases referred to juvenile court in 2009. The remaining referrals were made by others such as parents, victims, schools, and probation officers (2013 a ). 6 A petition is filed for all cases that appear in juvenile court . Cases that are no t petitioned are diverted out of the official juvenile court system, either to a formal diversion program or by the juvenile simply being released to a parent or guardian. 7 For example, the American Bar Association details the availabi lity of juvenile r ecords in different states to anyone from sensitive employers, to law enforcement officials , to the general public (2013). Regarding higher education, the Common Application asks college applicants to report if they have been adjudicated delinquent, but i nforms 5 There are two mechanisms by which expungem ent can affect the application process for education or employment for those with a record of juvenile delinquency. First, in the majority of states expungement allows the underlying criminal activity to be treated as if it never occurred, meaning an appl 8 Second, an expunged record will not be returned in a criminal background check if conducted by any employer or institution. Therefore, a nineteen year old wh o committed assault at age fourteen will have a record of juvenile delinquency if he lives in a state where it is not expunged , while a similar nineteen year old will have no record in a state where it is expunged. While all states offer juveniles the op tion to expunge a criminal history, there is an important difference in the process that I use in my empirical work to identify the effect of expungement. Conditional on eligibility, fourteen states are automatic expungement states, meaning the criminal r ecord is expunged at some point in the future with no action required by the juvenile. 9 The remaining states are application states, meaning a record of juvenile adjudication will not be expunged without a formal petition of the court. 10 This petition may require various costs, including knowledge of institutional details, hiring of legal counsel, and payment of administrative fees. Understanding the effects of automatic expungement is particularly important in the current atmosphere of juvenile justice r eform. The REDEEM Act 8 Some states statutorily define adjudication separately from conviction, meaning those with a record of juvenile delinquency can still 9 Eligibility for expungement varies by state. Some examples of eligibility requirements are age thresholds, remaining arrest free for a certain period of time, and providing evidence of rehabilitation. Statutory rules rega rding expungement can also differ by crime within state. For example, in many states certain crimes are ineligible for expungement. These crimes are typically either violent in nature or require registration on an offender registry, as is the case with m any sexual assaults. 10 6 (2014), currently a bill in the Senate, would make expungement automatic for all nonviolent juvenile offenses. In Table G.1 I briefly summarize the pertinent expungement statutes in each of the 50 states and the District of Columbia. I present further descriptive comparisons between the language of the state statutes in Table G.2, including the number of states that specify the event can be treated as if it never occurred and the number of states where an expunged record can be used against an off ender if he or she recidivates. 1.3 Literature Review While the effects of expungement have not been empirically studied , several conceptual analyses exist . These papers typically argue the advantages and disadvantages of confidentiality of records and expungement for society (Gough 1966; Volenick 1975; Snow 1992; Funk 1995 ; Funk and Polsby 1998; Henning 2004; Ruddell and Winfree, Jr. 2006; Raphael 2007; Calvert and Bruno 2010; Pyne 2010; Weissman et al. 2010 ). The majority of these papers conclude that the benefits outweigh the costs and that society should make expungement easier for former offenders. However, Funk (1995) and Funk and Polsby (1998) warn that expungement could have large costs for first time offenders and for society more broadly if former offenders recidivate after the record has been expunged. Other literatures provide insight into various effects that can be used to further understand the impact of expungement. For example, one pertinent literature investigates the ca uses of crime and recidivism. Expungement statutes alter the incentives for potential offenders by lowering the marginal cost of being caught committing a first offense as a juvenile. Prior economic literature shows that juvenile criminals may respond ra tionally to incentives (Levitt 7 1998; Jacob and Lefgren 2003; Conlin et al. 2005; Mocan and Rees 2005; Carpenter 2007 ; Lochner 2010). For example, Levitt (1998) shows that juvenile criminals are responsive to the severity of criminal punishment in their st ate of residence. However, other literature provides evidence that juvenile criminals appear to be myopic (Lee and McCrary 2005). Another pertinent literature discusses the effect of interaction with the justice system on recidivism. Generally, this li terature finds that formal labeling and incarceration can lead to increased rates of recidivism (Becker 1963; Bernburg and Krohn 2003; Bernburg et al. 2006; Kurleycheck et al. 2006; Lanctôt et al. 2007; Bayer et a l. 2009; Wilson and Hoge 2012; Aizer and Do yle, Jr. 2013). This literature is particularly applicable because expungement directly removes the formal label associated with a record of juvenile delinquency. Focusing on the long - term outcomes, much literature in criminology, sociology, and economics studies the effect of delinquent behavior and official court involvement on educational attainment (Tanner et al. 1999; Sweeten 2006; Hjalmarsson 200 8 ; Merlo and Wolpin 2008; Burdick et al. 2011; Gowen et al. 2011; Aizer and Doyle, Jr. 2013; Kirk and Samp son 2013). Generally, these papers conclude that delinquent behavior, court appearance, and incarceration have negative effects on high school completion and college enrollment, depending on the severity of the involvement. For example, Hjalmarsson (2008 ) finds that individuals with convictions before age 16 are 16 percentage points less likely to graduate from high school. Coincidentally, using completely different data, Kirk and Sampson (2013) estimate that individuals who have been arrested are 16 per centage points less likely to enroll in college than otherwise identical individuals who have not been arrested. Tanner et al. (1999) find significant negative effects of contact with the criminal justice system on college graduation. 8 There are also stu dies, although fewer, on delinquency and labor market outcomes. Generally, adult w orkers who apply for employment with a criminal record can face significant scrutiny compared to their peers without a criminal history ( Grogger 1995; Pager 2003; Bushway 20 04; Holzer et al. 2006; Holzer et al. 2007; Stoll and Bushway 2008; Finlay 2009 ). Literature specific to juvenile offenders also confirms this result (Snow 1992; Tanner et al. 1999; Bernburg and Krohn 2003; Lanctôt et al. 2007; Gowen et al. 2011). These papers show that former juvenile offenders are more likely to be unemployed and have shorter job tenures, even ten or more years after the offense (Tanner et al. 1999). 1.4 Conceptual Framework To consider how expungement affects the incentives to commi t crimes, I construct a simple two - period model that captures the dynamic incentives created by expungement statutes for the criminal behavior of individuals, ignoring any potential reactions of the juvenile justice system, police, or the labor market. I briefly lay out the structure and implications of the model here; see Appendix G.2 for its complete development. Suppose each individual has ability , where is distributed over (0,1) . In the first period everyone is simultaneously enrolled in school and participating in the low wage labor market, earning salary . In the second period those individuals who have no criminal record move to the high wage market and earn , where . Therefore, this model assumes that having a criminal record results in a future labor market penalty. In thinking about this framework, one can equate the first period of the model with being a juvenile and the second period with being an adult. 9 In each period the individual can choose whether to commit a crime or not. I descri be the crime decision in period t using the binary variable C t , where C t = 0 denotes choosing no crime and C t = 1 deno tes choosing to commit a crime. Assume that the individual earns his salary in each period wheth er or not he commits a crime and a ll individuals are caught committing a crime with probability . If he succeeds in committing the crime without being caught t he individual earns an additional payoff . However, if he is caught committing a crime he has to give up a fraction of his salary in that period. I use this framework to assess crimi nal behavior under two different policy regimes: automatic expungement and no expungement. First, consider the regime with no expungement. Given the simple specification of this framework, there exists a unique cutoff value in that separates the indiv iduals into two distinct types: those who commit a crime in both periods and those who commit crimes in neither period. 11 Those who commit crimes never choose (C 1 , C 2 ) = (1, 0). The intuition for this result is apparent in the marginal benefits and costs. The marginal benefit from committing a crime is the same in both periods. However, the wage penalty associated with a criminal record implies that the marginal cost of committing a crime in the first period is larger than the marginal cost of committing a crime in the second period conditional on committing a crime in the first period. Therefore, one would never choose (C 1 , C 2 ) = (1, 0). Lastly, the human capital development aspect of the model, where second period earnings are greater than first perio d earnings if the individual is not captured committing a crime , implies that no one will choose (C 1 , C 2 ) = (0, 1). 11 This finding, which is clearly unrealistic, is a result of the simplicity of the model. T he model could easily be ext e nded to allow for the other outcomes; for example, adding a period - specific idiosyncratic marginal benefit of crime would cause the other outcomes to be chosen as well . However, since my goal is only to understand the incentives, I keep the model simple. 10 Next consider the regime with automatic expungement. In this regime no one incurs the labor market penalty in the second period because no one has a criminal record. There also exist unique cutoff values in with automatic expungement separating the individuals into three types: low , medium , and high . As in the regime with no expungement, the individuals with low choose to commit a crime in both periods. However, the removal of the labor market penalty changes behavior in two ways: it reduces the marginal cost of committing a crime in the first period and it increases the marginal cost of committing a crime in the second pe riod conditional on committing a crime in the first period. This implies that individuals with medium will choose (C 1 , C 2 ) = (1, 0). Lastly, as in the regime with no expungement, individuals with high will choose not to commit a crime in either period. Figure D.1 summarizes how criminal behavior varies with across these two policy regimes. In th ability relative to . In the automatic expungement regime, the behavior changes as described above, but only between and . Automatic expungement takes the individuals with , who commit a crime in both periods in the regime with no expungement, and creates an incentive for these individuals to choose C 2 = 0. Automatic expungement also takes the individuals with , who commit a crime in neither period without expungement, and creates an incentive for these individuals to choose C 1 = 1. The model predicts that automatic expungement states will have higher rates of first time juvenile offense and lower rates of recidivism, where r ecidivism is defined as committing a crime as both a juvenile and an adult. 12 These predictions, which assume a rational, forward - 12 As in footnote 11, the simplifying assumptions of this model imply the unrealistic finding that those with low a have perfect recidivism. However, the takeaway from the model is the reduction in recidivism due to automatic expungement, not the magnitud e of this reduction. 11 looking juvenile criminal, remain largely unchanged if I instead assume juveniles know nothing about the possibility of expung ement as long as the penalty imposed by a record of juvenile delinquency is sufficiently large. The only difference is that I would not expect to find a higher propensity to offend in automatic expungement states because the juveniles are not aware that e xpungement has reduced the marginal cost of offending. However, because of the hurdle created by a record of juvenile delinquency, I would expect the effects on earnings and recidivism to remain unchanged. I proceed by empirically estimating the effect of automatic expungement on criminal behavior, the pursuit of education, and labor market outcomes. I can also test some of the assumptions of the model by analyzing the effect of automatic expungement on pursuit of higher education and future income. A co mparison of these outcomes can provide the first evidence of the impact of expungement policies. 1.5 Data The very nature of the expungement process presents a challenge for empirical work. No survey asks former offenders if they have had a record exp unged, and some states do not keep administrative records regarding individual expungements. To obtain evidence on the usage of expungement , I contacted officials in the State Administrative Office of the Courts as well as the State Police or Criminal Jus tice Information System in all 50 states and the District of Columbia . In response to this inquiry, three application states (Colorado, Mic higan, and Washington) were able to provide comprehensive aggregate statistics and one other application state (Main e) 12 responded with anecdotal evidence. 13 I use these data to understand how often juveniles use expungement by application . The primary data sources for the empirical work are the pertinent state statutes detailed in Table G.1 and the National Longitudinal Survey of Youth of 1997 (NLSY97). The NLSY97 is an annual longitudinal survey of 8,984 individuals who were between age 12 and 16 on December 31, 1996. The survey is unique in its collection of data related to crime. Each wave collects self - reported in formation about arrests, charges, convictions , and incarcerations, along with a rich set of demographic and economic information about the respondent and his or her family. 14 While self - reported data may suffer from underreporting bias, this bias will not affect my identification as long as it is uncorrelated with state expungement status. 15 Many previous studies use this dataset to analyze juvenile arrest and criminal be havior despite the data being self - reported (Levitt and Lochner 2001; Sweeten 2006; Loc hner 2007; Hjalmarsson 2008 ; Merlo and Wolpin 2008; Hjalmarsson 2009 ; Finlay 2009; Brame et al. 2014; Lovenheim and Owens 2014 ). Throughout my analy sis of NLSY97 data I assume individuals have a record of delinquency if they report that they were convict ed or adjudicated in juvenile court and their age at the time of survey is less than the age of criminal majority in their state of residence. During the years of analysis in this paper, the age of criminal majority is 16 in three states, 17 in ten states , and 18 in the remaining states. 16 This could raise concerns if the age of criminal majority 13 Table G.3 presents all of the data I collected from various states. Note that this table includes some data from automatic states that reported statistics for expungements by application. Expungement by application is available in these states for those interested in expungement before the automatic process occurs. 14 Thornberry and Krohn (2000) argue that self - report data on delinquency are valid for research purposes. 15 There is no reason to suspect that reporting is correlated with expungement status because respondents are interviewed annually and eligibility for expungement typically takes longer than one year. 16 There have been two recent changes: Connecticut raised its age from 16 to 18 (beginning to take effect in 2010) and Massachusetts raised its age from 17 to 18 in 2013 (Mendel 2013; OJJDP 2013b). 13 age of the sample. As a result, I test the robustness of my pr imary results to changes i n this assumption at the end of S ection 1.7 . For the purpose of my analysis I assign the state of residence for the individual in 1997. State assignment is critical as it determines whether the individual lives in an automatic or application state. While this method of assignment ensures that the state of residence is known for all respondents, it could introduce bias if juvenile offenders are mobile across states, particularly if they commit a crime in a state other than their a ssigned state. My results are robust to a number of different assignment strategies, such as the state of residence in other years. The preferred assignment strategy results in 20 percent of the sample residing in automatic expungemen t states, consistent with the average fraction of the juvenile population that lived in automatic expungeme nt states between 2006 and 2010. I use data from a number of other sources to provide important covariates throughout my analysis. See Appendix G.4 for a discussion of these data sources. 1.6 Empirical Strategy The preceding discussion highlights the importance of understanding the effect of expungement. However, the nature of the statues and available data limit the options for empirically estimating this effect . F or example, only one state , Vermont, has changed from application to automatic status in the past thirty years, and data are not available for analysis around the timing of the change in 1995. Because of these concerns with identification, the typical emp irical tools used to estimate clear causal effects are not suitable. 17 Instead, I use 17 For example, an instrumental variables framework is not feasible as there does not appear to be a valid instrument -- something that affects expungement policy but not the other outcomes . 14 several simpler, but distinct, strategies that exploit cross - state variation to provide a collage of evidence on the effects of the policy. 1.6.1 Empirical Concerns To f ocus the discussion regarding empirical concerns t hat exist with exploiting cross - state variation, consider the regression model: The outcome variable contains measures of crime, ed ucational, and labor market outcomes for individual i who lives in state s . The vector contains race, ethnicity, gender, parental characteristics, and household composition, among other important predictors for the outcomes of interest. The coef ficient of interest, , measures the effect of automatic expungement on the given outcome conditional on all of the other covariates. The other state level covariates labeled reflect the unobserved juvenile justice environment. Some examples of the covariates that comprise this vector include the intensity of police scrutiny of teenagers, the severity of the punishments imposed by the juvenile justice system, and the likelihood a state forgives an individual who interacts with law enforcement . One advantage of using the NLSY97 is that I have an extremely rich set of individual level covariates available to include in . Importantly for my identification strategy, these data allow me to control for underlying propensities to commit crime or succeed in the education and labor markets. There are two major concerns that threaten estimation of , the first of which is reverse causality. More specifically, it may be the case that states with lower arrest rates choose to have more lenient expungement policies. This argument does not appear to be a major concern (1) 15 because many of the expungement statutes date back to th e early twentieth century when juvenile crime rates were much lower. Despite fluctuations in the crime and arrest rates over time, virtually none of the statutes have been changed. The second concern with this model is omitted variable bias. More speci fically, Justice s in equation (1) is unobserved and likely to be positively correlated with Auto s . 18 Quite simply, it is likely that states choosing to automatical ly expunge records of juvenile delinquency also focus their juvenile justice environment on m aximizing the chance of rehabilitation. In such a case, if Justice s was not appropriately controlled for, the estimated effect of the automatic expungement policy would reflect the direct effect of the expungement pol icy as well as this other unmeasured j uvenile justice environment. 19 To provide more empirical evidence regarding these potential concerns, I compare observable covariates across automatic and application states in Table A.1. In the crime - specific covariates at the top of Table A.1 there are no significant differences in arrest or incarceration rates. Furthermore, while the arrest rate or incarceration rate is slightly higher in application states, in other categories, such as the violent crime rate or state expenditures on the justice syste m, the means are larger for automatic states. Similarly, the bottom panel of Table A.1 shows that there do not appear to be significant differences in demographics and economic indicators between the states. 20 The only means that are statistically differ ent from each other in Table A.1 are the fraction of the population that is 18 The implication of this argument is that Justice s conditional on the detailed covariates in X is is is not likely to be correlated with Auto s . 19 While o ne could tell a story where states with an automatic expungement policy tend to adopt a stricter juvenile justice system to offset this lenience, therefore suggesting that the correlation is negative, such an argument would seem to be more applicable when the policy environment was simpler, with perhaps just two or three policies counteracting each other. 20 Figure D. 2 shows that there does not appear to be any systematic geographical difference between the states. Additionally, although not listed in Tab le A.1 , there do not appear to be any discernible political differences, as measured by the political party of the governor, senators, and other state officials, between the states. 16 black, which is larger in application states, and the fraction of the population that is Hispanic, which is larger in automatic states. The concerns created by these differences a re diminished given the rich set of individual level covariates I include in my analysis. Therefore, the findings in both panels support the notion that automatic and application states do not appear to be systematically different. 1.6.2 Empirical Tech niques I use two different techniques to mitigate the concern of omitted variable bias. In the first technique I add a vector of covariates to my weighted least squares regression that are likely to be correlated with Justice s . I use four distinct proxy variables. The first divides the number of juveniles in residential placement by the total level of reported crime to measure the severity of the state juvenile justice system as in Levitt (1998). I also include a measure of sentencing severity within st ate prisons and the state level imprisonment rate for adults. 21 The fourth variable, which I define as the forgiveness ratio, measures the propensity of a state to parole prisoners. I divide the number of released prisoners by the population in custody fo r each state. This measure focuses on the level of forgiveness within the state as opposed to the severity of punishment. My second technique identifies within - state treatment and control groups, allowing me to include state fixed effects in a difference - in - differences framework. To implement the first technique I estimate a cross - sectional regression by weighted least squares and include the detailed covariates available in the NLSY97. Using these covariates as well as the results of Table A.1, where there do not appear to be systematic differences between the states, the remaining major concern is failing to capture the underlying juvenile justice 21 I measure sentencing severity as the fraction of state prisoners under j urisdiction with a maximum sentence of greater than one year. 17 environment. I compare the results of the regression without the proxy variables to those that include the proxies, thereby partially controlling for Justice s . This technique also provides some insight into the degree of omitted variable bias, assuming the proxy variables are valid. My second technique uses difference - in - differences to effectively remove all fixed attributes from equation (1), including Justice s , by focusing on within - state variation. I include state fixed effects to compare individuals who have been convicted of juvenile crimes to their peers who have not been convicted within the same state. 22 This alleviates the concern of unobserved cross - state differences biasing the estimated effect of automatic expungement. An example of this difference - in - differences strategy can be expressed as follows: The outcomes I consider in this analysis are long - term recidivism, college attendance and graduation, and average future income. 23 I define in equation (2) as in equation (1). In this framework the coefficient of interest is , the coefficient on the interaction between living in an automatic expungement state and being convicted in a juvenile court. The key aspect to the validity of this strategy is selection of the control group. A potential concern with this method is that the effects of the juvenile justice system may differ for these groups and therefore not be captured by this technique. The strength of the assumption of constant ef fects of Justice s across treatment and control group varies by the outcome I use. For example, consider the market for higher education. It seems plausible that the effects of the 22 of the question itself the survey is specific in asking if the respondent was ei ther convicted or adjudicated. 23 Because the treatment and control groups are defined by arrest and conviction, I am unable to use this technique to analyze the probability of initial arrest. I measure long - term recidivism using an indicator for ever bein g arrested after age 20. I choose age 20 because this will allow sufficient time for individuals who are incarcerated as juveniles to be released. According to the Census of Juveniles in Residential Placement, in 2010 the median range of days since commi tted individuals had been admitted was 91 to 180 days (Sickmund et al. 2013). (2) 18 juvenile justice system are similar for those who are convicted and those who are arrested but not convicted. However, in the market for long - term recidivism this assumption is much stronger. I test the robustness of my results to different treatment and control groups to alleviate this concern. For example, consider a change of the treatmen t group to individuals arrested but not convicted. These individuals likely interact with a similar juvenile justice environment as those who are arrested and convicted, but expungement should not have an impact on their outcomes. Therefor e, if I use those arrested but not convicted as the treatment group and those never arrested as the control group, I change the expected results of the analysis holding constant the unobserved juvenile justice environment. If the results of this analysis, where I expect no effect, are similar to the analysis using juvenile convicts as the treatment group, this would be evidence that the effect I am capturing is due to the unobserved juvenile justice environment and not to expungement. However, finding a l arge effect for those convicted but zero for those arrested and not convicted would be compelling evidence that I am capturing the effect of expungement. For all empirical analyses my preferred calculations of standard errors are clustered at the state le vel to correct for the within - state correlation that exists in my data (Donald and Lang 2007). However, in some cases this causes the standard errors to shrink. Therefore , I also present non - cl ustered standard errors in Appendix G .6 for all key results . The nature of the sampling framework used by the NLSY97, where black and Hispanic respondents are oversampled, implies that the sampling is endogenous because race is a significant predictor of arrest. As a result, I present weighted estimates in all ana lyses to ensure 19 consistency (Solon et al. 2013). 24 I report unweighted analogs of the primary findings in Appendix G. 6. 1.6.3 Do Juveniles Apply For Expungement? In Table A.2 I provide the years of data that are available and average annual expungements I collected from the application states. To interpret the data more easily , I include the average number of cases handled formally in each of the st ates over the years 1997 to 2010 . This is a measure of the amount of court activity that leads to the produ ction of records of juvenile delinquency . I calculate the expected adjudication rate by multiplying the average number of formally handled cases by 60 percent, the approximate rate for petitioned delinquency hearings to result in adjudication since 1985 ( Puzzanchera et al. 2012). Dividing expungements by expected adjudications gives a rough estimate of a rate of expungement of records for each state. Table A.2 shows that rates of expungement are extremely low in states that do not allow for automatic ex pungement, both in raw levels and as a percentage of expected adjudications. I estimate that the average expungement rate among these three application states is between 0.2 percent and 10.7 percent. Additionally, although unable to provide statistics, a representative from the Maine Juvenile Justice Advisory Group informed me that leading juvenile prosecutors in Maine recalled handling fewer than 50 motions to expunge juvenile records during the past 20 years (K. McGloin, personal communication, August 2 6, 2013). 24 In particular, the NLSY samples 100 primary sampling units (PSUs) in the cross - sectional sample and 100 PSUs in the oversample, with only 147 of the PSUs not overlapping betwee n the two. The nonrandom nature of the oversampling requires weighting for consistency (National Longitudinal Surveys 2014). 20 There are multiple explanations for this finding. One possibility is that the monetary and non - monetary costs associated with application for expungement are too high, deterring individuals from applying. 25 Another possibility, consistent with findings in the literature specific to youth, is that juveniles are extremely myopic (Lee and McCrary 2005; Oreopoulos 2007). Thus, they choose not to apply for expungement because the benefits of such application will not be realized until much later in their lifetimes. 26 A third explanation is that juveniles are unaware of the expungement laws in their state, particularly in application states. This explanation is most consistent with the low rate of expungement in application states. If former offend ers knew about expungement statutes, I would expect to find more juveniles applying for expungement upon learning that their record of juvenile delinquency prevented them from gaining employment or education. In the remainder of the paper I directly examin e the overall policy effect of a state adopting automatic expungement. Importantly, the empirical results in Table A.2 imply that the rate of expungement in application states is near zero, suggest ing that this policy effect is approximately equivalent to studying the effects of expungement itself. 25 For example, some states require affidavits from the applicant reflecting his or her behavior as well as affidavits from others regarding the character of the applicant. There are also direct monetary costs, such as remittance of court fees or hiring of legal assistance. 26 Myopia does not explain why former offenders do not apply for expungement when they are older. One explanati on for this result is that the negative effect of a juvenile record slowly diminishes over time. Another is that former offenders never revisit their decision not to pursue expungement. 21 1.7 Results The NLSY97 data I use contain 1,267 individuals who were arrested as a juven ile, 779 juveniles who were charged, 4 03 juveni les who were convicted, and 181 juveniles who were incarcerated. Table G.4 provide s additional descriptive statistics for the overall sample. 27 In Table A.3 I focus on the differences in the means of important covariates across automatic and application states for those never arrested, those arrested but not convicted, and those convicted as a juvenile. First, I compare the probability that a respondent reports being arrested as a juvenile in automatic and application states. I also report the probability that the respondent is convicted in juvenile court conditional on ha ving been arrested. While the rate of arrest appears to be slightly higher in automatic states, there is no statistically significant difference in the reported conviction rate. This finding helps to alleviate the concern that states may be endogenously determining their juvenile conviction rates in response to their expungement policy. Among those individuals who were convicted of a crime, the descriptive statistics suggest that outcomes in automatic expungement states are consistent with the conceptua l framework; average rates of recidivism are smaller in automatic states, while rates of college attendance, college graduation, and average future income are all larger in automatic states than in application states. Furthermore, the means for these vari ables in the automatic states are very similar to the means for those arrested but not convicted. These findings are consistent if automatic expungement serves to increase the means of these variables and the policy itself is exogenous to the se outcomes . 27 I drop 1,515 observations from the original sample . These individu als missed at least one of the first five waves of the survey, and I am therefore unable to determine if these individuals had an arrest as a juvenile. These statistics are weighted by the NLSY97 sampling weights for 1997 that use the cumulative cases met hod. This method provides a weight for everyone in the sample and adjusts for the oversampling of blacks and Hispanics. 22 In Table A.4 I compare the baseline difference in the probability of juvenile arrest among the respondents in the NLSY97 from the different states. Each of the columns of this table report results from a linear probability model estimated using weighted l east squares where the outcome is a binary indicator of ever being arrested as a juvenile. In column (1) I present results from a regression using all of the detailed NLSY97 covariates but excluding the vector of proxy variables. In column (2) I add the proxy variables to the regression to determine the level of concern raised by the unobserved juvenile justice environment. In columns (3) and (4) I repeat this exercise, but I also include a standardized measure of ability, the Armed Services Verbal Aptit ude Battery (ASVAB), which contains the Armed Forces Qualifying Test (AFQT). 28 This and Johnson 1996). Across all columns I find no statistically significan t effect of automatic expungement on juvenile arrest in this sample. 29 Although the direction of the estimated coefficient is positive, the magnitude of this effect is very small. Assuming that I use feasible proxy variables for Justice s , the lack of a si gnificant change from column (1) to column (2) and column (3) to column (4) suggests that the unobserved juvenile justice environment is not a big concern in this 28 The ASVAB was administered voluntarily in the first wave of the NLSY97. As a result, ASVAB scores are missing for many of the indi viduals who are arrested as juveniles. When I include ASVAB in the analysis I also include an indicator for ASVAB being missing. However, this fundamental difference in the sample with ASVAB scores affects both the magnitude and the interpretation of the ASVAB estimate. Another measure of ability that is available is self - reported eighth grade achievement. Respondents in the NLSY97 are asked to report their grades in f I def ine good grades as receiving mostly Bs or better and include this indicator in the analysis instead of ASVAB, the results are generally similar . 29 Tables G.6 and G.7 show similar analysis using arrest rates from the Uniform Crime Reports. The estimated coefficients are from a regression of average arrest rates for the specified population for specific crimes over the years 2006 to 2010 on a number of pertinent state level covariates. The crimes in the eight columns are ordered in terms of likelihood to be expunged. Therefore, this analysis determines if juveniles are committing less serious crimes at differential rates between the states, possibly as a result of the incentives created by expungement statutes. This also tests the predicted unconditional reduction in second period crime from the conceptual framework by using adult arrest rates . The estimated coefficient on the automatic identifier in these tables is never statistically significant at conventional levels, indicating that the arrest rates for all of the crimes are not different across automatic and application states. 23 analysis once I have conditioned on the rich set of covariates. This result continues to sup port the finding that there are not large differences between automatic and application states other than their expungement policy. This finding also conflicts with the predictions of the conceptual framework, where I predicted that there would be higher levels of juvenile crime in automatic expungement states. However, this result is plausible if juveniles are unaware of expungement policies in their state of residence. The signs and significance of the other covariates in Table A.4 are generally consist ent with expectations and previous studies. The small, insignificant effect of black is surprising given the national trend in arrests showing black juveniles arrested at much higher rates than whites (OJJDP 2013a). However, this is not the first paper t o find that the difference in arrest rates across races appears to be much smaller in the NLSY97 than in national s tatistics (Brame et al. 2014). 30 Additionally, other studies have found that conditioning on important covariates, such as family socioeconom ic status, make s the effect of race insignificant in determining risk of juvenile arrest (Fite et al. 2009). After analyzing the effect of expungement on arrest propensities, I shift the focus of the analysis to long - term outcomes for former offenders. Fi rst, to provide a baseline estimate for the negative effects of juvenile arrest and conviction on these outcomes, I estimate these effects for the entire NLSY97 sample in Table A.5. Each column presents the estimates from a regression of the outcome of in terest on the same set of covariates as column (2) of Table A.4. However, instead of including an indicator for automatic expungement, I include an indicator for juvenile arrest in the top panel and an indicator for juvenile arrest and juvenile conviction in the bottom panel. The results confirm the negative effects of juvenile arrest and conviction across the 30 A comparison of means test shows that black juveniles are arrested at a significantly higher rate than white juveniles in the NLSY97. 24 different outcomes and provide magnitudes that can be used for comparison with the results for expungement. For example, in the top panel I estima te that individuals who are arrested as juveniles are 18.2 percentage points more likely to be rearrested after age 20. The bottom panel shows that this rate is 15.0 percentage points for those who are arrested but not convicted, while the rate is 25 .1 pe rcentage points for those who are arrested and convicted. Once I establish the negative effects of juvenile arrest and conviction, I focus on estimating the effect of expungement. In Table A.6 I present the results of weighted least squares regressions us ing dependent variables that reflect the long - term costs and benefits associated with expungement in my conceptual framework. 31 Each panel of Table A.6 contains the results from estimation of equation (1) for a different subset of the population, includin g those who are convicted as a juvenile, those who are arrested but not convicted, and those who are never arrested. 32 Columns (1) through (4) measure reduced recidivism, pursuit of higher education, and legal employment, where these outcomes are defined such that positive results would be considered social benefits. As in columns (2) and (4) of Table A.4, these estimates include the proxy variables to control for unobserved differences in the juvenile justice system, and the coefficients of interest are those on the indicator for automatic expungement. The coefficient in the top panel of column (1) shows that individuals convicted as a juvenile who live in an automatic expungement state are 14.3 percentage points more likely to remain arrest - free after age 20, with this coefficient statistically significant at the five percent level. 33 This result is consistent with the prediction in my conceptual framework that automatic 31 The unweighted analogs to Tables A.6 and A.7 appear in Tables G.8 and G.9. 32 I cluster standard errors at the state level in Tables A.6 and A.7. Tables G.10 and G.11 show the standard errors for Table A.6 and Table A.7 without clustering. 33 One concern with this analysis is that individual s who are incarcerated for long periods may be incapacitated, resulting in no future arrests. However, including an indicator in the regression for ever being incarcerated does not change the results. 25 expungement causes a reduction in crime in the second period. It is reassuring tha t I do not find this reduction among those who are arrested and not convicted or those who are never arrested, as the incentive created by expungement should not affect these populations. The next two long - term outcome variables are educational outcomes. College 34 The outcome variable in column (3) is an indicator for college graduation defined as receivin outcomes are important for two reasons: first, a record of delinquency may need to be disclosed in the college application process, affecting the probability of admission for former delinquents, and second, having a record of juvenile delinquency can affect the incentives to invest in human capital development. The estimated coefficients imply that living in an automatic expungement state increases the probability of college attendance for juvenile convicts by 7.7 pe rcentage points and college graduation by 5.1 percentage points, although neither estimate is statistically significant at conventional levels. Again, the findings for the other two panels are close to zero and not statistically significant. 35 In column (4 ) I further extend the analysis of long - term outcomes to the labor market. To understand the effects of a record of delinquency, I focus on the natural logarithm of average income between 2008 and 2010 , when the average age among the responde nts is 25.8 t o 27.8 . 36 34 I n unreported results I do not find an effect of e xpungement on high school graduation. While one can imagine a story where a teenager who is convicted in an application state responds by dropping out of high school, this story is not apparent in the data. 35 The marginal significance in the bottom row of column (3) is puzzling. However, the negative coefficient implies that those who are never arrested may be less likely to graduate college in automatic expungement states, strengthening the interpretation of the positive, albeit insignificant, coeffici ent in the top row. 36 T he timing of this analysis, when many of the respondents have not yet reached age 30, implies that this measure of current income may not be a good proxy for permanent income (Haider and Solon 2006). I use the income measure over multiple years to draw conclusions about labor market implications, not to make statements about permanent income. 26 The results of this analysis suggest a positive effect of automatic expungement on average income for those convicted as a juvenile. The reported coefficient on income implies that, among those with a record of juvenile delinquency, individuals w ho lived in automatic expungement states earned 25.3 percent higher income, on average, between 2008 and 2010 than those who lived in application states. Some or all of this difference may be driven by the difference in college attendance, as it is a well - documented fact that the earnings profile of individuals with a college education, never attend college (Chenevert and Litwok 2013). While the coefficient on average income in the top panel is not statistically significant at conventional levels, the magnitude of this coefficient is much larger than the estimate in the other two panels, where I do not expect to find an effect. Generally, the results in Table A.6 show strong, compelling results for a reduction in recidivism, as I predicted in the conceptual framework. Furthermore, if I include the ASVAB measure from Table A.4 the magnitude for recidivism does not change and remains statistically significant. The effects on income and education rema in positive and not statistically significant when I include the ASVAB measure, although the education effects are slightly smaller in magnitude. In Table A.7 I turn to the difference - in - differences identification strategy. In each panel of Table A.7 I s pecify a different treatment and control group and report estimates of equation (2). In the first two panels, where juvenile convicts are the treatment group, I would expect to find an effect of expungement. The different control groups provide robustnes s for the assumption that the unobserved juvenile justice environment affects the treatment and control group equally. The bottom panel of Table A.7 acts as a falsification exercise for this analysis 27 while holding the juvenile justice environment fixed. The coefficients of interest in this table are the coefficients on the interaction between either juvenile conviction or juvenile arrest and living in an automatic expungement state. In column (1) the effect of expungement on future arrest remains statist ically significant at conventional levels, implying either a 15.3 or a 12.0 percentage point increase in the probability of remaining arrest - free after age 20, depending on the control group. Thus, consistent with my conceptual framework, there remains su pportive evidence that expungement of a record has an effect on future criminal behavior. The positive estimate on educational outcomes in Table A.7 is fairly similar to Table A.6. Taking all of these results together, I find that automatic expungement ra ises the rate of college attendance among former juvenile offenders by approximately five to eight percentage points, although this is not statistically significant at standard levels. Similarly, although the direction of the coefficient is still positive , there is not a statistically significant effect on college graduation across the two tables. Moving to labor market outcomes, there remains a large difference in average income of either 27.6 or 22.5 percent, depending on the control group. These esti mates are similar in magnit ude to the estimate in Table A.6 . However, unlike the estimates in Table A.6, the coefficients in Table A.7 are both statistically significant. Comparing the estimated effect for juvenile convicts to the control group in the fir st two panels of Table A.7 provides a simple plausibility check. Despite the consistent finding of positive effects across the columns, the magnitude of the estimates on the interaction terms is almost always smaller than the primary effect of juvenile co nviction. For example, while juvenile convicts in automatic expungement states may be 8.6 percentage points more likely to 28 attend college than their peers who were never arrested, the primary effect of being a juvenile convict suggests they will remain si gnificantly less likely to attend college. As was the case with Table A.6, the results in Table A.7 show positive outcomes for former offenders as a result of automatic expungement. 37 Similarly, adding ASVAB to Table A.7 does not affect the estimates fo r recidivism or income. Lastly, as with the falsification exercises in Table A.6, the magnitudes of the effects of automatic expungement are very small and statistically no different from zero in all regressions in the bottom panel. Despite the differing sources of variation that are identifying the effect of expungement with each method, the estimates in Table A.6 and Table A.7 are remarkably similar. This lends further credence to the claim that the estimation in the top panels is capturing the effect of expungement. A comparison of the results from Table A.6 and Table A.7 to the estimates from Table A.5 gives some insight into the magnitude of the effect of expungement. In theory, expungement eliminates the effect of juvenile conviction. This would imply that, all else equal, I would expect the effect of expungement to be the same magnitude but opposite sign of the effect of being arrested and convicted. My results suggest that expungement removes a large percentage of the negative effects of arrest and conviction, but does not entirely undo them. This is a plausible result if, for example, there are scarring effects of appearing in juvenile court and being adjudicated delinquent. 37 One way to generalize the results of Tables A.6 and A.7 is to statistically test the direction of the coeffic ient of interest across all of the estimated equations. I estimate the system of eq uations in each panel of Table A.6 and Table A.7 as seemingly unrelated regressions , allowing for some correlation to exist between the underlying error terms in each of th e regressions, and test the coefficients on automatic expungement across the entire system. I run this test for each panel separately. In all cases where I expect to estimate the effect of expungement (excluding falsification exercises), I can reject the null hypothesis that the effect of automatic expungement is zero . These findings suggest that there is an overall effect of juvenile expungement, despite the weaker results for each of the outcomes individually. 29 I perform a number of robustness exercises for the primary results i n Table A.6 and Table A.7. First, I try numerous strategies for assigning the state of residence to each respondent. For example, one strategy assigns the state of residence where the juvenile offender commits his or her first crime while using the 1997 state of residence for those who never commit crimes. This check does not have any significant impact on the results. Another robustness check focuses on the age of criminal majority. Instead of using the age of criminal majority specific to each state, I change the analysis to assume the definition of juvenile is age 16 or younger. The estimated results are no different as a result of this adjustment. The results are similarly robust to inclusion of the ASVAB measures. All linear probability models a re robust to functional form assumptions; estimating the equations via probit and logit does not affect the results. I also use a falsification exercise to understand if there are systematic differences between respondents in automatic and application st ates. For this exercise I use the preferred specifications but define the outcome variable as the measure of good grades in eighth grade. I do not find any statistically significant differences between au tomatic and application states . Generally, the re sults of these robustness checks and falsification exercises continue to support the finding that the effects I estimate are due to expungement and not influenced by a number of the assumptions I make in my preferred specifications. 1.8 Discussion and Con clusion This paper is the first to empirically evaluate cross - state variation in the usage and effectiveness of expungement. I identify the existence of automatic and application states and present a conceptual framework that captures the dynamic incentiv es created by a policy of 30 automatic expungement. I also provide evidence from unique data that the rate of expungement in automatic states is near one while the rate in application states is near zero. My empirical analysis uses two very different estim ation strategies, and both of these analyses support the implications of the conceptual framework. I do not find any evidence that the nature of expungement statutes affects the incidence of juvenile crime, the primary avenue through which there could be social costs from expungement. I then investigate the impact of expungement on future crime, education, and labor market outcomes. Using data from the NLSY97 I show that there are benefits to former delinquents as a result of automatic expungement. Spec ifically, my results suggest that former offenders living in an automatic expungement state are less likely to recidivate after age 20, more likely to attend college, and earn a higher average salary in their late twenties. The incentives I discuss in th e conceptual framework along with the empirical evidence on response to these incentives suggest that juvenile criminals are unaware of the expungement process. This conclusion supports all of the empirical findings in the paper: low rates of expungement in application states, no effect of automatic expungement on arrest propensities, and large effects of automatic expungement on long - term outcomes. The results of this paper also address a new mechanism behind the findings in the crime literature: the ef fect of an observable record of juvenile delinquency. The coefficient estimates application process, and this is creating a significant barrier for many ex - offender s. The removal of these barriers to education and legal employment in automatic expungement states is another plausible explanation for my findings in these markets for adults. My analysis shows that the barrier created by the record of juvenile delinque ncy is separate from the effects of important 31 covariates, and unobserved differences in state justice systems do not play a big role in explaining these results. Even when I add an ability measure to the model, the effects on future recidivism and employm ent remain significant. One of the challenges with this work is finding a strong source of identification. Unfortunately, states have not changed their expungement process significantly over time, and many of the statutes date back to the first half of th e twentieth century. Despite my efforts to reduce the bias caused by differences across state justice systems, my current identification strategy fails to capture any other unobserved differences, such as community programs that may have an impact on the outcomes of former offenders. While I am unable to control for some of this unobserved heterogeneity, my results provide compelling evidence that there are not large, systematic differences between the two types of states. Therefore, I conclude that I am identifying the underlying relationship between juvenile records and important economic outcomes. While I do not perform a complete cost - benefit analysis for the policy, I use my results to think about the notable costs and benefits of expungement. Cle arly, the results imply that automatic expungement has significant benefits for former offenders. One can imagine numerous other potential social benefits, such as the tax revenue if these individuals contribute to society via legal employment as opposed to a socially costly life of crime or the reduction in administrative costs caused by appearances in court. Turning to social costs, while the effect of automatic expungement on crime is not distinguishable from zero, I also cannot reject small, positive effects. To appropriately account for these costs, one would have to weigh the cost of these specific crimes, and it seems likely that the value of the costs is small. 38 Therefore, my 38 In estimating the value of this social cost one should only consider crimes that are eligible for expungement. The costliest of crimes from a social perspective, such as murder, should not be included in this calculation. As an 32 sketch of a cost - benefit analysis concludes that the social benefits of expungement outweigh the social costs. Generally, the process of expungement is one that deserves more attention in the remedy, and one that is not used due to l ack of knowledge about the policy. There remains room in the literature for a precise estimate of the impact of expungement on a number of important outcomes. However, given the estimated return to former offenders of expungement of records of juvenile d elinquency, the social benefits of such expungement, and the lack of evidence indicating social costs, policy makers should focus on raising awareness of expungement policies. example of the magnitude of these costs, a realistic value is an estimate of assault victim cost at $13,000 instead of the statistical value of a life at $4.1 million (Heckman et al. 2010). 33 CHAPTER 2 DID GRADUATED DRIVER LICENSING LAWS DRIVE A REDUCTION IN CRIME? 2. 1 Introduction Over the past three decades each of the Healthy People publications, which outline the primary public health agenda for the United States, contains objectives regarding implementation of Graduated Driver Licensing (GDL) laws (United States D epartment of Health and Human Services 2000; National Center for Health Statistics 2001; United States Department of Health and Human Services 2013). GDL is a three tiered program designed to reduce the risk associated with novice driving by requiring the driver to complete two stages and provisional license) before receiving an unrestricted license. 39 The National Committee on Unif orm Traffic Laws and Ordinances developed the original model GDL law, and state specific laws have been targ eted at young drivers in the United States since 1996. Numerous studies conclude that adoption of a GDL law causes a significant reduction i n fatalities among young drivers ( Dee et al. 2005; Karaca - Mandic and Ridgeway 2010; McCartt et al. 2010; Masten et al. 2011 ; Williams et al. 2012 ). Empirical evidence shows that strong passenger and nighttime driving restrictions in the intermediate stage are the components that are most important in explaining the redu ction in teenage fatalities ( Karaca - Mandic and R idgeway 2010; McCartt et al. 2010; Masten et al. 2011). While accidents and fatalities may be the most direct measures of risk reduction, GDL restrictions have the potential to affect other youth behaviors. One can view these policies as the introducti on of both a statutory curfew and a limitation on the number of passengers that can be 39 Therefore, one c an view the primary innovation of GDL laws as the introduction of the provisional license. 34 in the vehicle. The response of teenage drivers to these restrictions can subsequently affect other outcomes that involve motor vehicle use among the target population. One important such behavior is teenage crime. Specifically, restricting access to motor vehicles may prevent the opportunities to commit violent and property crimes. 40 For instance, GDL restricts driving at night, a time of day when some criminal acti vities, such as robberies, are more likely (Doleac and Sanders 2013). In addition, the interaction of motor vehicle access with risky behaviors, such as alcohol use, can lead to the production of violent and property crimes (Carpenter 2007). Unrestricted access to motor vehicles can also create social situations where multiple teenagers are in the vehicle at once, a significant input in the production of criminal activity (Zimring 1998). This study provides the first estimates of the causal effect of GD L implementation on criminal behavior among teenagers. As a preview of the results, I find that GDL restrictions cause a decline in violent and property crime, particularly among 16 year olds. These results are generally consistent with previous literatu re regarding the effect on crime of similar policies, such as zero tolerance laws and curfews. I then show that the nighttime restrictions associated with GDL implementation are the primary mechanism causing the reduction in crime. The remainder of th e paper is organized as follows. First, I describe the GDL policy further and pr ovide a review of the literature. Next, I describe the data sources and methodology . Then, I present my primary results along with a discussion of threats to validity and robu stness checks, followed by an examination of heterogeneity in the results, the dynamics 40 Criminology literature generally focuses on violent a nd property crime when analyzin g criminal behavior. Violent crime s include murder, non - negligent manslaughter, forcible rape, robbery, and aggravated assault. P roperty crime s include burglary, larceny - theft, and motor vehicle theft . 35 of the policy, and the potential mechanisms causing my results. Finally, I draw conclusions based on the analyses . 2.2 Policy Background and Literature Review 2.2.1 G DL and Motor Vehicle Fatality While the specifics of GDL policies vary by state, all GDL laws generally have a similar structure. A young driver enter s the learner s tage at a minimum entry age, remain s in the stage for a mandatory holding period, and com pletes a minimum amount of supervised drivi ng. 41 When the learner stage is complete the driver the teen can drive without supervision. However, there are restrictions on the number of teenage passengers that ca n be in the vehicle as well as a timeframe at night when unsu pervised driving is prohibited. Once the driver holds this provisional license for a sufficient amount of time and reaches another age milestone these restrictions are lifted, leaving the driver with an unrestricted license. 42 Today all 50 states and the District of Columbia have some version of a GDL law in place, though the severity of the restrictions varies across states . The staggered implementation of a wide variety of GDL laws allows for analysis of the effect of the GDL law and its components on teenage fatalities. The literature concludes th at adoption of a GDL law causes a reduction in driving - related fatalities for the target age group (Dee et al. 2005; Karaca - Mandic and Ridgeway 201 0; McCartt et al. 2010; Masten et al. 2011). Furthermore, empirical evidence shows that more stringent nighttime and passenger restrictions 41 nse at an older age, particularly over 18, is not be required to go through GDL. 42 States vary on the specifics of their driver education program, which is different from their GDL law. In most states teenagers must complete driver education (or pass a wr some states, like Michigan, driver education requirements are intertwined with GDL restrictions. This paper focuses specifically on the GDL law and not on the driver education requirements. 36 cause a larger reduction in fatalities (Karaca - Mandic and Ridgeway 2010; McCartt et al. 2010; Masten et al. 2011 ). For a general review of the most recent literature pertaining to GDL laws and traffic safety , refer to Williams et al. (2012). The literature on traffic fatalities also tries to identify the causal mechanism for the reduction in teenage fatalities. Un derstanding whether this result is caused by a decline in the prevalence of teenage drivers on the road, as opposed to an improvement in the habits of teenage drivers, can have important policy implications. However, reliable statistics regarding the inci dence of teenage driving do not exist. The National Household Travel Survey is only administered every few years and gathers data among drivers of all ages . As a result, the sample of individu als between 16 and 17 years old is very small. Similarly, the American Time Use Survey has a very small sample of respondents between 16 and 17 years old and collects little data about driving activities. 43 Because of this lack of reliable data directly measuring the outcome of interest , Karaca - Mandic and Ridgeway ( 2010) use a structural model to infer the effect of GDL restrictions on teenage driving behavior . Their results support the claim that the reduction in fatalities is caused by a reduction of teenagers on the road. 2.2.2 Crime The effect of GDL implementa tion and, more broadly, the effect of motor vehicle access on crime has not been previously studied in the literature. However, there is a rich literature in juvenile crime that provides guidance as to how GDL may affect crime among the target population (McDowall et al. 2000; Levitt and Lochner 2001; Jacob and Lefgren 2003; Mocan and Rees 2005; Bayer et al. 2009; Kline 2012; Aizer and Doyle, Jr. 2013; Eriksson et al. 2013; 43 For exa mple, between 2003 and 2013 there are only 2,078 unique respondents across all 50 states between 16 and 17 years old who report any driving activity. 37 Anderson 2014). While it is outside the scope of this paper to completely characte rize the model underlying juvenile crime, I briefly describe the potential effects of GDL restrictions on juvenile crime in the context of criminal opportunities. Consider a model describing criminal behavior, such as the model described in Becker (1968) or Cook (1986). Before choosing his or her action a potential criminal weighs the expected payoff to successfully committing the crime against the expected punishment if he or she is caught. Such a model of criminal behavior suggests that GDL restriction s could affect crime either by altering the set of potential criminals or by affecting the marginal costs and benefits of crimes. While the direction of this effect is ultimately an empirical question, I provide a number of predictions for how GDL restric tions may affect crime. The GDL restrictions may change the set of potential criminals in a number of ways. First, access to motor vehicles can affect criminal opportunities, where the potential criminal has a chance to compare the marginal costs and bene fits of committing a crime. For example, the nighttime restrictions associated with GDL can act as a curfew, restricting criminal opportunities at a time when crime is common among the juvenile population. Prior literature shows that curfews among the ju venile population can lead to significantly lower rates of crime and arrest, particularly among certain violent and property crimes (McDowall et al. 2000; Kline 2012). GDL restrictions may also affect potential offenders through passenger restrictions. P assenger restrictions influence the peer pressures in a motor vehicle, and it is well documented that delinquent behavior occurs more commonly in groups (Zimring 1998). Similarly, a large literature argues that teens associating with delinquent peers, par ticularly during times of unstructured socializing, are significantly more likely to participate in delinquent behavior 38 (Agnew 1991; Osgood et al. 1996; Gaviria and Raphael 2001; Osgood and Anderson 2004; Bayer et al. 2009; Monahan et al. 2009; Mennis and Harris 2011). There is also the theoretical effect of the increased costs associated with crime in the GDL system. Becker (1968) and Cook (1986) show that changes in the costs associated with the context of GDL there may be changes in the probability of being caught and convicted as well as the punishment for the crime, giving two direct predictions. First, enforcement of the restrictions raises the probability that a young driver with numero us passengers will be stopped by a police officer, particularly in states with primary enforcement. Second, the threat of punishment under GDL can deter adolescents from criminal behavior. Teens who commit minor crimes while in the GDL system typically h ave their restrictions extended or their license suspended, imposing an additional cost for committing the crime (National Conference of State Legislatures 2011). Overall, the intuition of this paper is comp arable to the analysis of the effect of z ero t olerance laws on criminal behaviors in Carpenter (2007) . Zero tolerance laws prohibit the operation of motor vehicles by a driver under age 21 with any trace of alcohol in their system. Carpenter (2007) shows that zero tolerance laws cause a 3.4 percent r eduction in property crimes among 18 to 20 year olds with no decline in violent crimes. GDL laws are very similar to zero t olerance laws: they were implemented by states toward the end of the twentieth century , they pertain to teenage driving behavior, an d they interact with other teenage risky behaviors. 44 However, the effect of GDL laws may be more widespread among teenage drivers, as zero tolerance laws only refer to consumption of alcohol and driving. This difference can cause the effects of the polic ies to vary significantly , warranting further investigation. 44 Because my panel runs from 1997 to 2010, there is no variation in zero tolerance laws for my primary ana lysis. 39 2.3 Data 2.3.1 GDL Policy Data The I nsurance I nstitute for H ighway S afety (IIHS) collects data on the stringency of GDL policies by state as well as effective dates of implementation when GDL p olicies change. I use this resource as well as prior literature and state statutes to characterize the policy in effect in each year. For my primary specification I follow prior literature by coding the GDL policy variable as a binary variable that equal s one when the state implements a three tiered driving system . In the year of implementation I use a fractional value that reflects the portion of the year where GDL restrictions are effective. Table H.1 summarizes the different dates of implementation f or each state. 2.3.2 Outcome Data For my analysis of crime I draw counts of arrest from the National Archive of Criminal Justice Data. These counts come from the Uniform Crim e Reporting system operated by the Federal Bureau of Investigation. This system collects crime statistics from law enforcement agencies that voluntarily agree to participate and covers over 18,000 reporting agencies representing 95 percent of the United S tates population (Federal Bureau of Investigation 2013) . Justice Statistics and the Census of Juveniles in Residential Placement to proxy for the severity of the crim inal justice system in each state. 45 Data for these sources only go back to 1997, which 45 Counts of juvenile offenders are not available for every year. As a result, I linearly interpolate the years that are not available between 1997 and 2010. 40 is where I begin my crime panel. I analyze data until 2010, resulting in a panel that has 51 states over 14 years (N=714). 46 The measurement of crime is very difficult in empirical research because data are typically only available for either arrests or reported crime, two subsets of the outcome of interest. As a result, researchers typically make assumptions about the relationship between crime and arrest and use avail able data to draw conclusions about crime more broadly. My preferred measure of crime is the percentage of total arrests attributed to the target population. As a specific example, for 16 year olds this would be 100 times the number of arrests of 16 year olds divided by total arrests across all ages. 47 I refer to this measure as the arrest ratio throughout the paper. It is important to note the specific assumptions I make by using this measure of crime. Using the arrest ratio as a proxy for crime implic itly assumes that the proportional relationship between arrests for a specific age group and the rest of the population is equivalent for crime among that age group. The measure also implicitly controls for state level policing behavior as long as police activity is uncorrelated with the age of the offender. Additionally, the coverage issues that exist in some states with the Uniform Crime Reports are not a concern with this outcome as long as consistency in reporting is not correlated with age. 48 A seco nd crime measure that I use to test for robustness, discussed i n Levitt (1998), equates the proportion of arrests for a particular age group to the proportion of reported crime committed by that population . An advantage of this measure is that it produces interpretable and 46 In the analytical sample I drop data from Florida and the District of Columbia due to poor data coverage. Additionally, I treat 5 other observations as missing due to no arrests being reported in the state and year. 47 Crime literatur e typically does not use arrest levels as an outcome measure because arrests depend on both criminal activity an d police activity. For example, an estimated decline in arrests could be the result of a reduced police presence or a reduction in criminal behavior. 48 The Federal Bureau of Investigation reports data cov erage indicators by state that reflect the overall quality of the arrest data collected for e ach state (Puzzanchera and Kang 2013). 41 comparable estimates of the effect of GDL implementation on the crime rate . However, because reported crime is collected at the state level, the proportion of arrests should be reflective of the entire state . To reduce any error associ ated with underreporting of arrests, I treat as missing any state with a reported coverage rate for arrests below 85 percent. 49 Table B.1 contains summary statistics for the key variables that I use in the analysis. The top panel summarizes the outcome v ariables that I use throughout the paper . First, I present the pre - policy arrest ratios and crime levels for violent and property crime separately by gender to underscore the differences in baseline criminal activity between boys and girls. 50 These statis tics also allow for comparison of the different measures of crime: the pre - GDL arrest ratio for violent crime among 16 year old boys implies that 3.55 percent of all arrests for violent crimes prior to GDL implementation were of 16 year old boys, while the crime measure in the top panel of Table B. 1 implies that prior to GDL implementation 16 year old boys committed 10.46 violent crimes per 1,000 population on average. It is not surprising to find that young men commit much more crime than young women and the rate of property crime is much higher than the rate of violent crime among this age group. I focus on the different effects of GDL implementation on criminal activity among boys and girls when I examine heterogeneity in my results. The bottom panel of Table B.1 reports descriptive statistics for the covariates in the regression analysis. First, I include a number of driving and alcohol related policies, such as highway speed limits, seat belt enforcement, legal blood alcohol concentration limits, zero tolerance laws, and administrative license revocation laws. Some of these laws, such as zero tolerance and administrative license revocation laws, have little independent variation because 49 All results using this measure are robust to removing this sample adjustment. 50 To be clear, only the numerator of the arrest ratio is sex - specific. These ratios are the number of arrests of 16 to 17 year old males or females divided by the total number of arrests regardless of gender. The level of reported crime and population measure I use in the crime calculations are not gender specific. 42 most states had implemented them by 1997. Others, like speed lim its, seat belt enforcement, and Conditional on GDL implementation, 22 percent of states have secondary enforcement of the restrictions, meaning an officer may issue a citation for violation of the restrictions if and only if the officer has stopped the vehicle for some other reason. The panel also contains a number of demographic and economic in dicators intended to partially explain state level differences in the level of crime. Lastly, I include a number of indicators of the justice system in each state. Among these covariates I include the number of police officers employed by the state per capita, total state expenditures on the justice system per capit a, and a measure of prisoners in custody as a proxy for the severity of the state justice system. Following Levitt (1998), my measures of custody rates are the stock of juveniles in state facilities divided by the population age 15 to 17 (consistent with criminal deterrence) and the stock of juvenile in state facilities divided by the total number of reported crimes (consistent with criminal incapacitation). 51 Figure E.1 shows a graphical correlation that motivates one aspect of my empirical work. The soli d line in the figure shows the number of arrests per population for a specific age group in 2010. In the other two lines I show the number of states that allow for a person in this age group ation in this figure implies that the ages when teenagers gain access to motor vehicles are also the ages when there is a large increase in teenage arrest rates, consistent with the theoretical relationship between motor vehicle access and criminal behavio r. However, this correlation is also consistent with many other explanations, so I use the implementation of GDL restrictions to isolate a causal effect. 51 Levitt (1998) shows tha t criminal activity among both adults and juveniles is sensitive to a measure of criminal justice severity. 43 2.4 Methodology Like nearly all of the previous studies focusing on GDL implementation , I use a di fference - in - difference s estimation strategy, exploiting the variation in GDL adoption across states. 52 Many previous traffic fatality studies use models that incorporate count data , such as P oisson and n egative b inomial models . However, because the primar y crime measure I investigate is a continuous variable , I rely on ordinary least squares in my preferred specification . Formally, I use the following econometric model to understand how GDL affects crime: ( 1) The outcome variable y st contains the arrest ratio for the crime of interest. In this setup X st contains demographic, economic, and other policy related control variables for each state year cell. GDL st is the binary indicator of GDL implementation. Equation (1 ) also includes state s ) and year fixed effects (µ t ) to control for any time invariant or year specific unobserved heterogeneity. st captures any other idiosyncratic shocks. I cluster standard errors at the state level to mitigate concerns of within - state serial correlation that could affect inference in a difference - in - difference s framework (Bertrand et al. 2004; Dee et al. 2005). 2.5 Results 2.5.1 Effects on Crime Table B.2 reports the effects of GDL restrictions on the arrest ratio for violent and property crimes by specific years of age. 53 Each column of Table B.2 contains the coefficient on 52 Given I revisit Dee et al. (2005) with additional years of data and additional states that have implemented GDL, I confirm the original results and test the estimates for robustness to additional years of data and changes in the definition of the outcome measure. The descriptive statistics and regression results appear in Tables H.2 and H.3. 53 I exclude 15 year olds from Table B.2 because this age group is on the margin of being affected by the policy. For example, 15 year olds who interact with 16 year olds may be affected by the policy, while younger 15 year olds 44 GDL for the listed crime and age group from the preferred specification, which is a linear regression of the arrest ratio for the given age group and crime type on GDL implementation, indicators for driving policies, demographic and economic covariates, measures of the justice system, state fixed effects, and year fixed effects. 54 The custody measure, which proxies for severity, is lagged because of the concern that contemporaneous severity could have an effect on criminal behavior. 55 The results in Table B.2 present the total effect for boys and girls together to focus the discussion on the differences between age groups. The esti mates indicate a statistically significant reduction in the arrest ratios for violent and property crimes for 16 year olds with no significant effects for any other age group. These coefficients can be interpreted as the effect on the percent of arrests p ertaining to each age group. Therefore, the results for 16 year olds imply a 0.322 and a 0.503 percentage point reduction in the percentage of arrests of 16 year olds relative to the rest of the population for violent crime and property crime, respectivel y. 56 These are reductions of approximately seven percent in the mean of the arrest ratios for violent and property crime prior to GDL implementation. There are generally reductions in crime for the other age groups, indicating spillover from the restricti on of 16 year olds, but these estimates are not statistically significant. Also, the general decline in the magnitude of the coefficients as I move further away from the target population makes intuitive sense. may not be affected at all. I choose to exclude this age group because this het erogeneity complicates interpretation of the results. 54 Employed police officers, state expenditures on the justice system, and juveniles in custody all have the potential to be endogenous. However, exclusion of these covariates does not affect the estima ted coefficients; the estimated reduction for 16 year olds is 0.344 for violent crime (standard error is 0.156) and 0.488 for property crime (standard error is 0.187). 55 In Table B.2 I use the incapacitation measure of severity, but results do not change i f I use the deterrence measure. Results are similarly robust to excluding this measure altogether. 56 My preferred specification is not weighted (Solon et al. 2013). However, weighting by population size does not influence the estimates. For example, the estimates for 16 year olds with population weights are - 0.397 (standard error = 0.134) for violent crime and - 0.430 (standard error = 0.183) for property crime. 45 The last column in Table B.2 also serve s as a falsification exercise for the finding, a s I should not expect to find a contemporaneous effect of the policy on older age groups. Motor vehicle access for this population is unrestricted both before and after implementation of the policy, so GDL implem entation should not affect crime among these individuals. I report coefficients from regressions for violent and property crime by gender for age 18 to 20 , finding point estimates that are statistically no different from zero. 57 This falsification exercis e lends credibility to the finding that GDL implementation reduce s violent and p roperty crime among 16 year olds. 2.5.2 Threats to Validity The difference - in - difference s identification strategy relies on the common trends assumption to consistently estima te the effect of interest. In the framework of this paper this assumption implies that the observed trend in crime for states where GDL has not been implemented is identical to the trend that would have existed after GDL implementation. Comparing pretrea tment trends across states provides an indication of the appropriateness of this assumption. The event study analyses that correspond with the preferred estimates for 16 year olds appear in Figure E.2 and Figure E.3. The samples in these analyses are ba lanced such that I only include states with three years of data before and after GDL implementation. To operationalize these analyses, I include seven dummy variables instead of the binary GDL indicator in equation (1). These dummy variables include thre e years of leads, an indicator for the year of implementation, and three years of lags (where the last lag indicates three or more years after 57 Although not reported in Table B.2, the same falsification exercise for older ages shows sim ilar results. When applying the same specification to older age groups I adjust the measure of custody to reflect adult prisons. 46 GDL is implemented). Therefore, the reference group for interpretation of these estimates is the state mean four or more years prior to implementation of GDL. In Figure E.2 there does not appear to be a systematic trend in violent crime before implementation of GDL, implying that states did not implement GDL restrictions in response to high violent crime rates. 58 Th ere is a distinct decline in the arrest ratio in the first year after GDL implementation that remains unchanged two and three years after GDL. Similarly, the event study analysis for property crime in Figure E.3 shows no evidence of trends in the arrest r atio prior to the implementation of GDL restrictions, with a similar decline that begins after the implementation of the restrictions. While these models lack the statistical power to estimate precise effects, the result s mitigate concern of policy endoge neity and provide support for the feasibility of the common trends assumption. Another threat to the validity of the identification strategy is an unobserved shock that is correlated with the timing of GDL implementation. For example, if police decide to increase the targeting of young drivers upon GDL implementation, any observed effect on crime may be mistakenly attributed to the policy. In addition to the pertinent observables in equation (1), the falsification tests in Table B.2 alleviate concerns tha t any estimated reduction is not being caused by the policy itself. In the context of targeted enforcement, it seems unlikely that a targeted increase would affect 16 year olds but not 17 and 18 year olds. There are a number of other approaches to unders tand the effect of the policy on the behavior of police. One way to test this concern is to use indicators of police enforcement, such as the number of employed police officers per capita, as the dependent variable in the preferred 58 Generally, the pattern of estimates in prior literature that focuses on traffic fatalities also shows no evidence of polic y endogeneity; there is no distinct trend in motor vehicle fatalities prior to GDL implementation and a noticeable decline in fatalities within states after GDL restr ictions take effect (Dee et al. 2 005; Karaca - Mandic and Ridgeway 2010). 47 specification. Such a regression does not yield statistically significant estimates of GDL implementation (coefficient: - 0.006; standard error: 0.008). Alternatively, one could directly test this theory by analyzing the frequency of traffic citations or contact with the police among the target population. However, sources of such data, like the Police Public Contact Survey, are not suitable for analysis at the state level. Instead, I present more suggestive evidence in Table B.3 by comparing the effects of GDL restrictions in states with primary enforcement of nighttime and passenger restrictions to those with secondary enforcement. The intuition behind this analysis is that increased enforcement targeting young drivers upon GDL implementation would be more evident in states with primary enforcement of the restrictions. In Table B.3 I present estimates from the primary specification but also include an interaction between GDL implementation and secondary enforcement of nighttime and passenger restrictions. Therefore, the c oefficient on GDL reflects the effect in states with primary enforcement, while the sum of the two coefficients is the effect in states with secondary enforcement. Generally, the estimates in Table B.3 are consistent with the primary results in Table B.2. There do not appear to be statistically significant differences between states with primary and secondary enforcement of restrictions, providing additional evidence that an increased level of police enforcement is not a major threat to the validity of th e preferred estimates. 2.5.3 Robustness In Table B.4 I test for robustness of my primary findings to different measures of crime. In each of the columns I report estimates for the effect on violent and property crimes using the arrest ratio, an adjust ment to the arrest ratio where I remove 16 year olds from the denominator, 48 the natural logarithm of arrests , the natural logarithm of the arrest ratio, and the crime rate described in Levitt (1998), respectively. These estimates continue to reflect the to tal effect across both genders. I include column (1) of Table B. 4, the preferred estimate for 16 year olds from Table B.2, to simplify comparison. The adjustment to the arrest ratio corrects for the fact that total arrests of the target population appea r in both the numerator and the denominator of the arrest ratio. Therefore, instead of including all arrests in the denominator, the adjusted arrest ratio only includes arrests for age 25 and older in the denominator. As a result, the coefficient can no longer be interpreted as the effect on the percentage of crimes committed by 16 year olds. However, it is reassuring to find that there is still a negative, marginally significant effect of the policy on the adjusted arrest ratio. Using the natural log arithm of total arrests of 16 year olds is another way to eliminate the division bias in the arrest ratio. However, using only the numerator of the arrest ratio sacrifices the information on total arrests that was included in the denominator. As a result , in this specification I also include the natural logarithm of arrests age 25 and older as a covariate. This allows me to continue to control for aspects of the justice system that are constant across age, such as the intensity of police enforcement. I continue to find negative and statistically significant effects of GDL restrictions using the natural logarithm of total arrests. Using the natural logarithm of the arrest ratio I estimate an 8.4 percent reduction in the arrest ratio for violent crime and a 7.7 percent reduction in the arrest ratio for property crime, with both statistically significant at conventional levels. Finally, in the last column I use the measure of crime from Levitt (1998), which has the added benefit of estimates that can be int erpreted as effects on the crime rate. I estimate a 13.1 percent reduction in violent crime and 49 an 8.2 percent reduction in property crime. The estimates across all of the columns show the robustness of the results to different measures of crime and arre st that have been used in the literature. An added benefit of the results in Table B.4 is that they allow for comparison with other papers in the literature. For example, Carpenter (2007) finds that zero tolerance laws cause a reduction of 0.005 in the ar rest ratio for property crime among 18 year olds as a result of the policy. 59 However, while Carpenter (2007) finds no effect on violent crime, I find marginal reductions in violent crime as a result of GDL. Kline (2012) finds a reduction of around 10 per cent in arrests for both violent and property crimes in the target population as a result of curfew laws. This is generally consistent with the reduction I find in total arrests, the arrest ratio, and the crime rate for violent and property crime. The co nsistency of my findings with the previous literature on zero tolerance laws and juvenile curfews confirms that the magnitudes of my estimates are feasible. 2.5.4 Heterogeneity and Dynamics Given the significant effects of the policy on 16 year olds, I focus on the heterogeneity in the results for this population. In Table B.5 I show the effects by gender. Given the pre - policy arrest ratios by gender and the theoretical effect of GDL restrictions on crime, I expect to find effects that are larger for m ales than for females and larger for property crime than violent crime. The coefficient estimates in Table B.5 support this hypothesis, with the largest magnitudes and most significant estimates coming from males. However, the 0.145 percentage point redu ction in the arrest ratio for property crime among females suggests that the policy has an impact for 59 Recall the est imate from Carpenter (2007) should be multiplied by 100 for comparison with my estimates. 50 females as well. This result makes intuitive sense because there is no reason to suspect that this policy should affect males but not, to a lesser degree , females. Disaggregating the results by type of crime is also informative because the link between GDL restrictions and crime should be more apparent for certain crimes. For example, murder is unlikely to be affected by GDL restrictions because restrict ing motor vehicle access is unlikely to affect potential murderers and the change in the marginal cost of murder created by penalties under GDL is extremely small. However, less severe crimes, such as burglary and larceny, may be significantly affected by GDL restrictions because the restrictions are likely to influence a larger set of potential offenders and the change in the marginal cost of crimes is much larger. The disaggregated results by specific crime appear in Table B.6. 60 The first set of column s indicate that changes in aggravated assault drive the results for violent crime in males. The estimates of violent crime for females show no significant effects for any particular crime, but the largest reduction is in aggravated assault. This is not s urprising as there was no overall effect for females in Table B.5. Focusing on property crime, the reductions in burglary and larceny for males and larceny for females drive the effect on the arrest ratios for property crime. Generally, the lack of stati stical significance for more serious crimes, such as murder, rape, and robbery, is reassuring in the context of this policy and the theoretical framework for its effect on criminal behavior. Given the contemporaneous reduction in crime for 16 year olds, it is logical to ask if these results are permanent for 16 year olds who are exposed to GDL restrictions. I answer this question by comparing the arrest ratios for older age groups who were all exposed to GDL restrictions to the arrest ratios for that ag e group before GDL implementation. Table B.7 60 As with heterogeneity by gender, I only adjust the numerator of the arrest ratio by specific type of crime so that the sum of the disaggregated estimates in Table B .6 equals the estimate from Table B.5. 51 presents the results of this analysis for ages 18, 19, and 20. For the 18 year old column I compare the arrest ratios among 18 year olds for violent and property crime after GDL implementation to the same arre st ratios before GDL implementation, but I exclude the year of GDL implementation and the next two years. This ensures that everyone in the treatment group was exposed to GDL restrictions. For the analysis of 19 year olds I drop the first three years aft er GDL implementation, and for the analysis of 20 year olds I drop the first four years. None of the estimates in Table B.7 are statistically significant at standard levels, indicating that the reduction in crime among 16 year olds disappears by age 18. 2.5.5 Mechanisms While the robust reduction in violent and property crimes due to GDL restrictions is informative, a complete understanding of the mechanisms causing this reduction is useful for policymakers. I first examine the effects of the underlying components of the policy, specifically nighttime and passenger restrictions. I focus on these components because the restrictions have direct implications for criminal behavior. 61 Additionally, empirical evidence shows that nighttime and passenger restric tions are the primary mechanism by which GDL laws affect traffic fatalities ( Karaca - Mandic and Ridgeway 2010; McCartt et al. 2 010; Masten et al. 2011) . In Table B.8 I replace the binary GDL indicator in the preferred specification with indicators for the implementation of nighttime and passenger restrictions. This allows me to separately identify the effects of these restrictions with the caveat that the identification is coming from states where nighttime or passenger restrictions were not implemented 61 The other components of GDL that I ignore are less applicable to crime, such as mandatory holding periods and minimum amounts of supervised driving that must be completed during the learner stage. 52 s imultaneously with the three tiered adoption. 62 The estimates for violent and property crime suggest that the nighttime restrictions are the primary mechanism causing the overall reduction in crime with marginally significant reductions of 0.407 and 0.480 percentage points, respectively (standard errors are 0.213 and 0.259, respectively). The positive coefficients on passenger restrictions, although not statistically significant, are puzzling. Passenger restrictions reduce peer influences in the vehicle, which should theoretically reduce the propensity to commit crime. However, the large standard errors on the estimated coefficients do not rule out the possibility of large effects of passenger restrictions in either direction. Because nighttime restricti ons appear to be the primary mechanism causing the reduction in crime, I further analyze the effect of hourly restrictions on crime and arrest by time of day. This introduces a new source of variation to my analysis: the hours of the day restricted by GDL . To estimate the effect on crime by time of day I use data on arrestees from the National Incident Based Reporting System (NIBRS). These data provide the hour of the day when the offense occurred as well as the age of the arrestee. 63 The NIBRS data I us e in this analysis come from reporting agencies in 37 states over 14 years (1997 to 2010), although many of the states do not have 14 years of data available. To overcome potential data coverage issues, I continue to measure the criminal activity of 16 ye ar olds relative to the rest of the population in the agencies that report in the state. While there could be potential selection issues with the reporting agencies, the NIBRS is the only available data source with information on the hour of offenses, whi ch is vital for using the hourly variation in nighttime restrictions. 62 The implementati on of nighttime and passenger restrictions was not simultaneous to the implementation of a three tiered system in 23 out of the 51 states (includes the District of Columbia). 63 I drop all cases where the relevant age or incident hour is missing. 53 In Figure E.4 I show graphical evidence of the effect of hourly restrictions on the arrest ratio for violent and property crime for 16 year olds. I plot the average arrest ratio for 16 year olds for each hour of the day separately by states where the hour is restricted. There are no restrictions between 6:00 A.M. and 8:00 P.M., so there is only one line during these hours. However, between 8:00 P.M. and 6:00 A.M. I show significantl y lower arrest ratios in the states where the hour is restricted. 64 While the average arrest ratio is lower during all restricted hours, the reduction is most striking between 8:00 P.M. and midnight. In addition, while this figure shows the overall reduct ion in violent and pr operty crime, unreported analyse s by individual crime shows the largest reductions in larceny and no reduction in murder, rape, robbery, or motor vehicle theft, consistent with Table B.6. This general reduction in the arrest ratio dur ing the restricted hours is consistent with the findings in Table B.8. 2.6 Discussion and Conclusion This paper provides a discussion of the effects of GDL implementation on juvenile criminal behavior. I show evidence that GDL laws cause a reduction of 0.322 and 0.503 percentage points in the relative arrests of 16 year olds for violent and property crime, and I confirm this result using a number of different measures of crime. There is no evidence that the estimates are being caused by other policies t hat may be correlated with GDL implementation, such as targeted enforcement policies. The magnitudes of my estimates are consistent with prior literature on similar policies, such as zero tolerance laws and juvenile curfews. I also show this reduction am ong both boys and girls, that the reduction is being driven by a decline in 64 Althoug h not included, regression analysis using the hourly data support this finding. For example, if I use a panel of hourly arrest ratios in the primary specification and also add hour of day fixed effects, I find a negative and statistically significant effe ct of the hour being restricted. 54 aggravated assault and larceny, and no permanent effects of the policy. Once I establish the reduction in crime, I focus on understanding the causal mechanisms for these results. I use multiple analyses to show that nighttime restrictions are the primary mechanism causing the decline in crime. Data limitations prohibit me from exploring important questions, and future work should focus on sharpening the answers to these question s. For example, I am unable to test for a demographic shift in the population of drivers in response to GDL restrictions. It would be restrictions, particul arly if this is correlated with criminal behaviors. In addition, data sources describing the peer influences in motor vehicles could help determine if young drivers are responsive to passenger restrictions and if peer effects in the vehicle play any role in the production of crime. Overall, this study presents an example of an unintended effect of a policy that impacts teenage behavior. The reduction in crime caused by GDL is an added benefit of the implementation of GDL policies that is not discussed i n prior literature. The conclusive evidence I show regarding the effect of GDL policies, specifically nighttime restrictions, on crime is important for policymakers as states implement GDL laws to be in compliance with the Healthy People publications. 55 CH APTER 3 INTERSTATE DIFFERENCES IN PENSION VESTING RULES, K - 12 TEACHER EXPERIENCE, AND TEACHER EXIT 3.1 Introduction Recent education policies in the United States adjust teacher compensation in a number of different ways. While some policies tie teacher compensation to tangible results, such as value - added to student test scores, other policies focus on restructuring retirement compensation. For instance, responding to the stress of rampant underfunding, recent reforms to teacher pension systems attempt to alleviate fiscal stress by increasing vesting requirements and raising teacher and employer contributions. 65 These changes to retirement compensation for public school teachers have implications both for state budgets and for the composition of the tea cher workforce if pensions influence labor market entry and exit decisions, employer changes, and mobility across state lines. While the private sector has moved to defined contribution plans, and pension reform has made some inroads in public plans for general government workers, the vast majority of public school K - 12 teachers continue to be covered by mandatory defined benefit plans with influential pension accrual patterns and limits to portability. 66 While the deferred compensation inherent in these defined benefit plans is designed to encourage teachers to remain on the job, t he se accrual pattern s can 65 Actuarial valuations from state financial reports estimate a total of approximately $325 billion in unfunded liabilities, which the literature considers to be an underestimate due to unrealistic actuarial assumptions (Doh erty et al. 2012; Novy - Marx and Rauh 2011). See the National Conference on State Legislatures (2013) for recent reforms . 66 States vary in the availability of supplemental defined contribution plans as well as teacher contributions to Social Security. For example, in 2010 there were 15 states (includes the District of Columbia) where teachers were not covered by Social Security. 56 the private sector changing jobs mid - career. Changes to pensi on parameters designed to reduce state pension obligations may have important unintended effects on teacher experience. Depending on how teachers respond to such reforms , the changes to a - 12 teacher workforce age and experience may have implicat ions for the educational quality of the future workforce. In this paper we focus on vesting rules, portability through service credits, and pension wealth differences across states for public school teachers in the early years of their career. 67 Pension vesting rules have received little attention in the literature on teacher experience , yet they may have unintended effects on new teacher retention or teacher preferences for shorter - term employment , particularly for teachers who are forward - lookin g . For example, in 2012 the to 10 years for new teachers. Additionally, they now require the teacher to contribute to his or her pension for the length of active m embership, as opposed to only the first ten years of employment. There were similar reforms to pension parameters in 21 other states in 2012 alone (Doherty et al. 2012) . All else equal, t hese changes may reduce the incentive for new teachers to stay in teaching for several years. Yet these early years of teaching are critical for teacher effectiveness. Several recent studies find that new teachers are less effective than those with some experience. 68 Restrictions across state borders on purchasing cr edits may also reduce young teacher mobility. The formulaic nature of the defined benefit pension calculation implies that teachers 67 Our results throughout the paper are applicable to public school teachers. These results are applicable to charter school teac hers if the charter school opts to participate in the state retirement system. Olberg and Podgursky (2011) discuss the different retirement compensation programs for charter school teachers across a number of different states. 68 For an overview, see Rice (2010), and for individual studies see Kane, Rockoff, and Staiger (2006), Ladd (2008), and Sass (2007). 57 who change retirement systems in mid - career can pay a significant penalty in pension wealth if they do not receive credit f or prior time as a teacher. Some states allow teachers to purchase credits for prior service, limiting the severity of this penalty. However, other states limit the credits one can purchase or do not allow for purchases at all. We illustrate the magnit ude of differences in pension wealth, both across states and at across four states with different vesting rules. We construct the actuarial present value of pension liability (or, wealt h as Qualified Domestic Relations Orders following divorce. 69 This termination liability, or accrued benefit obligation, is a measure of the pension liability owed at different points through a 70 Next, we use cross - sectio nal aggregate data on the state level experience distribution of teachers to calculate the relationship between important pension parameters, such as vesting requirements, and the composition of teacher experience. Our results suggest a negative relationship between the years required to vest and the percentage of teachers with experience between zero and four years. This finding implies that the current system of teacher retirement compensation is not helping to retain young teachers. Lastly, we use the variation in characteristics of the state pension system to predict first exit from teaching among a sample of new teachers in the National L ongitudinal Survey of Youth of 1997 (NLSY97). We show that vesting requirements and availability of defined contribution alternatives significantly affect the hazard of first exit from teaching. These results 69 Papke thanks Robert Raasche for providing detailed information about these arrangements. 70 This is similar to the accrued benefit obligations emph asized in Rauh (2010). 58 imply that adjustments to teacher retirement compensation may significantly affect the composition of the teacher labor force. The next section briefly reviews the literature on mobility and retirement effects of defined benefit plans with an emp hasis on teacher pensions. In Section 3.3 we discuss o ur calculations of individual teacher pension wealth and compare wealth for teachers upon vesting across four states as an illustration. Section 3.4 provides evidence that these interstate differences in pension vesting rules may affect the distribution o f teacher experience across states. In Section 3.5 we use data from individual teachers to calculate the effect of different pension parameters on the hazard of first exit from teaching. Section 3.6 concludes. 3 . 2 Related Literature Previous studies of mobility and pension wealth focus on retirement incentives at the end of the career for public sector workers. Friedberg (2011) reviews retirement and mobility implications of defined benefit plans and the related literature for public employees and teac hers in particular. She finds that defined benefit pension incentives play a significant role in the suggests that younger workers with defined benefit plans are less likely to switch jobs as pension wealth accrues , but the evidence is not definitive. Using the Survey of Consumer Finances (SCF) data from 1983, Friedberg and Owyang (2002) find that private sector workers with a defined benefit pension have total e xpected tenure that is 5 - 7 years longer on average than workers without any pensions, but that workers with defined contribution plans also have longer tenure than workers without pensions. Using the C urrent P opulation S urvey and Public Plans Database, Mu nnell et al . (2012) find that the probability of remaining with a single plan until 59 retirement eligibility is reduced if the employee also has a defined contribution plan and is covered by Social Security. A similar literature focuses specifically on te acher retirement incentives associated with defined benefit pla ns (Furgeson, Strauss, and Vogt 2005; Costrell and Podgursky 2009; Friedberg and Turner 2010; Friedberg and Turner 2011) . This literature describes the incentives created by the defined benefi t programs and provides state - specific and national studies of teacher response to these incentives. For example, there was a large increase in teacher retirement in Pennsylvania from 1997 - 1998 to 1998 - 1999 in response to more generous retirement benefi ts (Furgeson, Strauss, and Vogt 2005). A nother related literature on the retirement incentives imbedded in Social Security benefits examines the effect of the peak value of benefits on retirement. The peak value concept subtracts current pension wealth fr om the peak of pension wealth that is available in the future. 71 Costrell and McGee (2009 ) use administrative data from Arkansas to describe pension wealth differences , particularly at the peak value, and their effects on retirement behavior . Friedberg an d Turner (2011) use the Teacher Follow - Up Survey of the Schools and Staffing Survey in 2000 and 2004 (SASS). Using a peak value approach along with data on teacher satisfaction, they find that teachers who are dissatisfied with their jobs respond more st rongly to pension retirement incentives. Teachers who express job satisfaction still respond to retirement incentives, but with a much smaller magnitude. A subset of the teacher retirement literature focuses specifically on cross - state variation in teache r pension wealth and provides simulation evidence of peak wealth (Costrell and Podgursky 2009; Toutkoushian et al. 2011) . These calculations, like ours in Section 3.3 , use the 71 Coile and Gruber (2007) use peak value to measure Social Security incentives and Friedberg and Webb (2005) use data from the Health and Retirement Survey for individuals aged 50 and over. 60 characteristics of state pension programs to calculate the present discounted v pension benefits under a number of different assumptions about teacher age, experience, and salary growth. Costrell and Podgursky (2009) focus on six states in their simulation, and show the cross - state variation in spikes in pension w ealth. Toutkoushian et al. (2011) calculate a simulation for one identical career teacher in all 50 states, providing a ranking for the most generous pension plans. 72 3.3 Vesting Rules and Teacher Pension Wealth In this section we describe our simulatio n of pension wealth. Rather than focusing on the generosity of plans at the normal retirement age, our simulations provide insight into the present discounted value of pension wealth upon vesting for new teachers . In addition, we improve upon earlier ass umptions by using actual state starting salaries and salary caps so that teacher salaries do not grow to unrealistic values. The four states we include in this simulation show the variability in pension wealth upon vesting due to pension plan parameters. Specifically, the four states (California, Florida, Michigan, and Wisconsin) all have different vesting rules some as a result of recent changes. Table C.1 describes the specific parameters that go into the pension calculation for each state. Michiga n requires ten years of service before a teacher is vested, while Florida only requires six years. California requires five years for vesting, but teachers do not contribute to Social Security and are no longer allowed to retire prior to the traditional r etirement age with full l ifetime benefits (Doherty et al 2012). Prio r to 2011 teachers were immediately vested in Wisconsin , but 72 Because of the large scope of this si mulation, they only present results for one type of teacher who spent their entire career in the teaching profession with no salary cap. In addition, they assume one starting salary across all states and a salary growth rate of 3 percent with no cap. The se assumptions result in six figure final salaries for lifetime teachers. 61 today Wisconsin has a vesting rule of five years. The national average for vesting in similar plans is 5.78. The remainder o f Table C.1 shows that these states also differ in the age for retirement with full benefits, teacher contribution rates , teacher salaries, and Social Security coverage . We collect information on pension plan parameters from a number of sources. Firs t, we use plan participation measures from 2001 to 2010 of the Public Fund Survey, which collects statistics on public retirement systems. We supplement these statistics with vesting rules, benefit formulas, and contribution rates from summary plan handbo oks as well as portability measures defined by the National Council on Teacher Quality (Doherty et al. 2012). Based on these pension plan parameter values and assumptions described below, we can calculate the present discounted value of pension wealth at any point in time for a hypothetical teacher. We calculate the annual pension benefit as follows: Final average salary and the multiplicative factor are plan - specific parameters that we obtain fr at each age to get the actuarial value of annual benefits , assuming the individual will live until age 100. Lastly, we calculate the present discounted value of pension wealth using a discount rate r as follows: Here A is the actuarial value of annual benefits, t indicates the year at which the calculation is . 62 This calculation requires that we make a number of assumptions. First, we set the equal to from the 2008 SASS . This implies that there is no difference in the s tarting salaries for individuals who hypothetically begin working in different years. Salaries grow at three percent per year until they reach the top step reported by the SASS. Once the salary reaches the top step for the state, it remains constant. Ou r reported present value deducts contributions and assumes they are returned if the teacher leaves the system early , but we omit the possible interest payments. 73 We assume a three percent di scount rate in our calculations and use the 2008 female combined - race life tables to estimate the probability of s urvival to the next year (Arias 2012). In footnote 74 we illustrate variations due to racial differences in mortality. Defined benefit plans also typically include cost of living adjustments (COLAs). In some states, such as Michigan, COLAs are a constant predetermined percent of initial benefit. In other states, the legislature votes annually on the possibility of a COLA that year. In other plans, COLAs are linked to an inflation index with a cap. Bec ause our focus is on the front end of a assumptions across states, we do not include COLAs in our empirical work. For illustration, in Table C. 2 we compare pension wealth estimates for Michigan teachers with and without the COLA three percent per year (not compounded) starting in October after one full year of retirement. Clearly, COLAs can have significant effects on present discounted values for retirees who work as t eachers throughout their careers (depending on actual levels of inflation). 73 While teachers typically begin contributing to the pension as soon as they begin working, if th e teacher leaves before vesting these contributions are refunded (sometimes with in terest or employer contributions as well). In California, Michigan, and Wisconsin employees who leave receive interest. However, teachers who leave early in Florida receive less than or equal to their own contributions (Doherty et al. 2012). We omit the interest payments to remain consistent across states. 63 interest. Figure F. 1 shows our calculation of the present dis counted value of pen sion wealth - net of teacher contributions - The x - axis displays the exit ages when t he teacher stops teaching and accruing pension benefits. The y - axis displays the present discounted values of pension wealth assuming a three percent discount rate and taking into account the probability of survival and salary growth . The shape of Figure F. 1 is commonly found in analyses of defined benefit pension plans. The accrual pattern of these plans creates significant jumps in pension wealth at particular ages and strong incentives ement age. Our focus is on the front end of the career trajectory. In Figure F. 2, we zoom in on the vested at different levels of experience in the four stat es. The magnitude of this windfall can be approximately an additional year of salary or more for the young teachers; for example, the While the pension formulas differ with respect to salary and pension multiplier, the cross - state variation in vesting requirements alone accounts for timing differences in any pension wealth. Recall, several states recently increased th e years required before vesting. This policy may reduce the future pension obligation but may also make it harder to retain young teachers . Depending on the quality of the teachers that exit and the teachers who replace them, this could have significant implications for student achievement. 64 The sig nificant differenc es between the states in Figure F.1 and Figure F.2 highlight the differences in pension wealth that are caused by plan parameters. Many of the parameters in the simulation contribute to these differences, including c ontribution rates, sa lar y levels , and benefit formulas. For example, consider the calculation of the final average salary used in the defined benefit formula. In Michigan and Wisconsin this number is the average of the highest three years of compensation, in California it is the highest consecutive twelve months, and in Florida it is the average of the highest eight years. Wisconsin in Figure F. 1 is a result of a relatively high contribution rate coupled with a significantly lower salary. At $30,700 t he average starting salary for a new substantially lower than it would be in the other states. Furthermore, the Wisconsin peak salary sion plan also includes a relatively high teacher contribution rate of 6.65 percent of salary. In Table C. egree, we compare the present discounted value of her pension if she quits after two years, five years, and 10 years and also at typical retirement ages. The first column highlights interstate differences in the peak value of her pension along with the age at which the peak will occur. The remaining columns include the difference from the peak value in parentheses. This difference is one measure of the opportunity cost of quitting or moving across state (district) boundaries in terms of pension wealth. 74 74 We can incorporate race into our calculations by adjusting the life tables in our calculations . If the teacher is white, the peak value of her pension (from Table C. 3) in California, Florida, Michig an, and Wisconsin, respectively, would be $693,921, $684,392, $666,664, and $372,561. If she is black these values would be $638,249, $634,157, $614,999, and $342,051. 65 The simulated values of pension wealth in Table C. 3 indicate that young teachers with a defined benefit pension earn virtually nothing toward their pension wealth before they are vested. In contrast, in the bottom row of Table C. 3 we also simulate the va pension if she were contributing to a defined contribution plan, using the Michigan teacher defined contribution plan offered to new hires as of September 2012 as an example. 75 The defined contribution pension wealth steadily grow s for this worker, even in the early years. For instance, i f a teacher quits after two or five years she still earns $6,341 or $17,322, respectively, a sizable amount of pension wealth if she participates fully in this defined contribution plan. Further, this benefit is portable to other plans or can be rolled over into an IRA. 3.4 Pension Plan Characteristics and the Distribution of Teacher E xperience In this section, we analyze the relationship between two key pension plan characteristics and the dist ribution of teacher experience across 50 states. We add data from the 2008 and 2011 SASS on the age and experience distribution s for teachers as well as starting salary to our data on pension information across states . 76 The SASS provides the percentage of teachers in each state in the f ollowing experience categories: fewer than four years of experience, between four and nine years, 10 to 14 years, and 15 plus. Table C.4 provides summary statistics that highlight the cross - state variation in the experien ce distribution of teachers, vesting requirements, the ability to purchase service credits, and starting salary. These statistics show that around 15 percent of teachers in the survey have less than four years of experience and around 27 percent 75 We assume that a teacher contributes six percent of her salary to the account with a 50 percent match rate (up to three percent) by the employer. We further assume that this account grows at three percent per year. 76 Data on starting salary are only available for 2008. Data on average age are not available in the District of Columbia, Florida, Hawaii, Maryland, and Rhode Island for 2011. We use the estimates from 2008 for 2011 for these states. 66 hav e betw een four and nine years. The average plan vests its members in more than five years because the vesting requirement in 16 states is 10 years. 77 The variation in the starting salary for young teachers is also striking, ranging from $24,800 to $42,700. Tabl e C.5 reports results from a regression of the state level experience categories on pension characteristics to understand the relationship between pension characteristics that affect the early career and the distribution of teacher experience . The caveat to the analysis in Table C.5 is that it uses cross - sectional variation from two snapshots in time; as a result, one should not try to draw causal inference from these estimates. We focus on years until vesting and the ability to purchase credits in a new district/state. We also include as controls the average age among teachers in the state, the natural logarithm of the starting salary for a teacher with no prior experience , and an estimate of pension wealth for a hypothetical teacher . 78 In the first pan el percentage of teachers with less than four years of full time teaching experience the vesting co efficient of - .0361 (p - value .015 ) suggests that for each additional year of waiting time required until any pension wealth is owned, a state will have m ore than one third a percent fewer new teachers. A vesting period of 5 years is common 31 of these 50 largest public plans require five years. Those states will have 1.8 percentage points fewer teachers in early career stages. Ten states require 10 ye ar s they are predicted to have 3 .6 percentage points fewer newer teachers almost one standard deviation in the mean of this variable. Vesting rules do not have a statistically significant effect on the percentage of teachers with four to nine years of experience many of these are already vested and the rest are close. 79 Years to vesting is 77 Some states have made changes to their vesting rules. The 16 states we reference vest at 10 years at some point between 2002 and 2010, but n ot necessarily for the entire period. For example, seven states have raised the vesting rule from five to 10 years between 2008 and 2012 (Doherty et al. 2012). 78 The estimate of pension wealth, which comes from Table 8 of Toutkoushian et al. (2011), is ne t of contributions. While we prefer our assumptions for the simulation exercise, their estimates of pension wealth are highly correlated with our results. We use their estimates for this analysis so we have estimates for all states. 79 Papke (2004) finds that quit rates in public employment drop off steeply right before vesting. 67 positively related to the percentage of teachers with 10 to 14 years experience since these percentages sum to 100 the vesting coefficients must be of opposite s ign at some point, and vesting cannot have any influence at this point in their career. This cohort is vested near mid - career. Credit purchasing has a negative relationship for the younger experience categories and positive for the higher experience categ ories. The positive relationship with the higher categories makes intuitive sense because the ability to purchase service credits may result in higher retention in the teaching field for older teachers, making them more experienced. Also note that highe r starting salaries are generally positively correlated with the percentage of younger teachers . Lastly, the relationship between pension wealth and the distribution of experience reflects the incentives for remaining on the job; states with higher values of pension wealth have a larger fraction of teachers in the most experienced category. 3.5 Evidence from the National Longitudinal Survey of Youth of 1997 In this section we focus on the relationship between pension plan characteristics and first labor market exit for young teachers. Our data for this analysis comes from the NLSY97. This nationally representative survey began following a cohort of teenagers in 1997 and interviews them every year, covering topics including income, employment, family, fe rtility, and health. This survey is most appropriate for us because it allows us to focus on the labor market behavior of young teachers across different states. It also allows us to include covariates in our analysis that are not typically available whe n using administrative data, as is the case in much other retirement compensation literature. We identify a ll individuals who ever report teaching between 2002 and 2010 and follow their teaching career over time. We choose to begin our 68 analysis in 2002 b ecause this ensures all respondents were old enough to teach. For a complete description of the data in this analysis, see Appendix I.1. Our methodological strategy for this analysis is to use a discrete time hazard model to isolate the effect of pension characteristics, specifically vesting requirements, measures of portability, and existence of defined contribution alternatives, on the period - specific hazard of (1) In equation (1) we model the hazard of first exit from the labor market ( ) as a function of year effects (t), state level covariates (s) including the pension parameters of interest, and indiv idual level covariates (i). Therefore, the vector X ist contains the covariates that vary by individual, state, and year, such as marital status or number of children in the household. The vector R st contains our variables of interest, such as pension pla n characteristics, as well as other covariates that only vary at the state and year level. Our preferred estimates of equation (1) are estimated with standard logit assumptions, although results are robust to estimating via probit or linear probability mo deling. We choose to model the hazard of first exit from teaching because we only see one exit from teaching for the majority of this sample. 80 Table C.6 provides an overview of the teacher panel we use from the NLSY97. In the top panel of the table we p rovide descriptive statistics pertaining to the individual teachers. It is not surprising to find that a majority of the population of our teachers, 66 percent, are female. It is also not surprising to find that a large majority of the teachers are white . According to the National Center for Education Statistics, in 2011 - 2012 76 percent of teachers were female and 81 80 Of the 779 teachers in the sample, we see 425 exits from teaching. Only 79 individuals, around 10 percent, return to teaching during our sample, and 64 of the 79 move to a new employer. 69 percent identified as white, not Hispanic (Goldring et al. 2013). The discrepancy between our statistics and the national averages is like ly because we focus only on a cohort of younger teachers, while the national averages include the entire distribution of teachers. Given the relatively young ages of the sample population, it is also not surprising to find that respondents are single for the majority of the observations. We condition on marital status and children in the household in our analyses because changes to these covariates could significantly affect the probability of exit from employment. The Armed Services Vocational Aptitud e Battery is an ability exam that is given to all respondents in the fir st round of the NLSY97. T hose teachers who opted to take this exam scored in approximately the 69 th percentile , on average, among all NLSY97 respondents. 81 Prior literature shows that underlying ability is positively related to exit from teaching (Podgursky et al. 2004). One concern in this analysis of teachers is that individuals select into teaching or accept a specific position because of the pension benefits. Selection of a spec ific teaching position is not a concern as long as teachers are not comparing options across state lines. Regarding career selection, one plausible way to compare the outside options for these teachers is to use information on the industries where these i ndividuals work when they are not teaching. In unreported tabulations, the largest industries (other than educational services) are retail trade, accommodations and food services, and arts, entertainment, and recreation. It is hard to draw any conclusion regarding selection based on this analysis alone. However, positions in these industries are likely in the private sector where employees will be covered by defined contribution plans. 81 A total of 110 individual teachers, or 14.1 percent of the sample, opted not to take the ASVAB. 70 The middle panel of Table C.6 focuses on the characteristics of the different employment relationships we see among the teacher sample. For example, the average among those teachers who report a starting salary is $17.50 per hour, or approximately $35,000 per year. 82 Among those who remain teachers for five years or more, the salary grows to $21.28 per hour, or approximately $42,500 per year. Next, we indicate the type of teacher we see in the sample: preschool/kindergarten, elementary/middle school, secondary, postsecondary, and other teacher. 83 Last, we show that the av erage job tenure among the teacher sample is 2.16 years. This average would fall well below the median vesting requirement of five years. However, because we focus on young teachers, a demographic with high turnover rates, this result is not surprising. In the bottom panel of Table C.6 we focus on the pension parameters that pertain to our sample between 2002 and 2010. 84 We include the number of years required to vest in the state pension plan, indicators for supplemental defined contribution options, an indicator for a choice between defined benefit and defined contribution plans, the retirement factor used in benefit calculations, an indicator for coverage by Social Security, and the required employee pension contribution rate. The average time to vest ing for respondents in our sample is similar to the national average in Table C.4. Note that while 33 percent of plans offer a defined contribution add - on option, only 11 percent of plans offer a choice between defined benefit and defined contribution pla ns, indicating that the defined contribution plan is usually supplemental to the mandatory defined benefit plan. There is little variability in the retirement factor (it typically lies 82 The NLSY converts all reported earnings and units of time to an hourly wage. Wage data are available for 73 percent of all observations where a teacher is employed. 83 These categories are not mutually exclusive. They indicate that the individual teacher ever fell into the category w ho do not fall into one of the other categories. 84 We assume that teachers work in the state where they reside. The NLSY geocode data allow us to determine state of residence but not state of employment or any specific information about the employer. 71 between one and two percent), although states where teachers are not c overed by Social Security tend to have higher retirement factors. Lastly, the average employee contribution rate for individuals in contributory plans is six percent. . As a result, we control for statutory requirements for tenure in each state. Table C.6 shows that, on average, states will grant a teacher tenure after 3.15 years. Lastly, at the bottom of Table C.6 we summarize six indicator variables that describe t he portability of the state pension plan. The first three indicate the return of contributions if a teacher withdraws from the plan before vesting: a refund of their contributions, a refund of their contributions with accumulated interest, or a refund of their contributions, accumulated interest, and some of the employer contributions. The last three indicate the ability to purchase credits in the system for prior service: unlimited purchasing of service credits, limited purchasing of service credits, or no purchasing of service credits. Table C.7 reports the results of the discrete time hazard model described in equation (1) estimated via logit. The dependent variable in each column is a binary variable that equals zero when the individual is teaching a nd equals one when the individual first exits teaching. In column (1) we control for a number of individual covariates as well as year dummies. The estimate for the ASVAB percentile implies that a ten unit increase in the ASVAB percentile increases the h azard of exit by 0.02. This finding, consistent with prior work in the literature, suggests that teachers with higher ability scores are more likely to exit teaching (Podgursky et al. 2004). We also find that women are less likely to leave teaching, as a re respondents who are married. Although children in the household are not statistically significant, the positive relationship between fertility and exit from teaching is intuitive. 72 sion wealth. 85 These variables include a person - specific variable that reflects the number of years until the individual is vested in their retirement system, an indicator for availability of a defined contribution plan, an indicator for choice between th e defined benefit and defined contribution ules, the retirement factor, an indicator for Social Security coverage, and the teacher contribution rate. 86 Time to vest ing and avail ability of a defined contribution plan are both positive and significantly related to the hazard of first exit. The coefficient on time to vest ing implies that a young teacher is 2.3 percentage points more likely to exit teaching for each additional year he or she must work before vesting. This implies that a change in vesting from five to 10 years would increase the hazard of exit by 11.5 percentage points. The effect of offering a defined contribution add - on is positive, statistically significant, and sizeable. The magnitude of the effect is more than five times as large as the effect of time to vesting in column (2). The positive relationship suggests that teachers with more portable pension wealth take advantage of the portability by exiting the tea ching market. In column (3) we repeat the estimation from column (2) but control for time to vest ing more flexibly by including dummy variables for one through five or more years until vesting and an indicator after the individual is vested. The omitted category for interpretation is the year the teacher vests. The estimated coefficients imply that teachers are significantly more likely to exit when they remain multiple years from vesting. The hazard declines as teachers approach vesting 85 I n unreported results w e include a lagged measure of hourly wage , when available, in columns (2) and (3 ) to control for the opportunity cost of leaving teaching . The estimates across these columns are qualitatively similar to the estimates in Table C. 7. H owever, the effect of the lagged wage is not statistically different from zero. We drop this analysis because many teachers do not report a wage, significantly reducing our sample size. 86 In column (2) the Time to Vesting variable remains at zero after th e individual is vested. 73 and becomes ne gative and statistically significant after vesting, implying teachers are less likely to leave once they are vested in the state pension system. This makes intuitive sense because teachers should respond to the incentives created by the deferred compensat ion in their defined benefit plan upon vesting by remaining with their employer. Overall, these results are consistent with forward - looking behavior among these teachers. Lastly, in Table C.8 we show the preferred specification from Table C.7 for subse ts of teachers in elementary and middle school, and for teachers in secondary school. Generally, the estimates in Table C.8 are consistent with the prior analyses. Focusing on the pension parameters, the effect of time to vesting is consistent with the r esults from Table C.7 for both populations. However, the availability of a defined contribution option has a much stronger effect for secondary school teachers, nearly three times as large as the effect for elementary and middle school teachers. Among the other covariates, the effects of marriage and the number of children in the household are positive, sizeable, and statistically significant for secondary school teachers, but do not appear to affect the hazard of first exit for elementary and middle schoo l teachers. 3.6 Conclusion This paper adds to the literature on the incentives created by teacher pension benefits by focusing on the early career, specifically the incentives created by vesting requirements. Our simulations of pension wealth at vario across four states in the initial jump in pension wealth that occurs upon vesting. We also provide cross - sectional evidence that vesting requirements are related to the experience distribution of the teaching labor force. Lastly, we show that pension parameters, such as time to vest ing and 74 availability of defined contribution options, have significant effects on the probability of exit from teaching. These findings have important implications f or policies affecting the accumulation of teacher pension wealth, particularly in the current climate of pension reform. Using our baseline estimate, which suggests that an additional year to vesting increases the hazard of first exit by 0.023, we predic the hazard of first exit by 0.11, an estimate that negates roughly one third of the effect of being granted tenure. Given the literature relating teacher experience to stud ent achievement, our findings could have important implications for student achievement. Future work in this literature should focus on identifying the teachers that are exiting the labor force in response to changes in retirement compensation. Improvi ng our understanding of the exiting teachers will allow us to determine if the changes to the teaching distribution are helping or hurting students. While our current results do not extend to students directly, our evidence implies that young teachers are responsive to changes in pension wealth, and these effects need to be considered by policymakers. 75 APPENDICES 76 APPENDIX A Tables f icted of a Crime? The Effects of Juvenile Expungement on Crime, Educational, a nd Labor Marke 77 Table A.1: State Level Descriptive Statistics Application (N=37) Automatic (N=14) Mean Std. Error Mean Std. Error Crime Indicators Juvenile Arrest Rate (Violent and Property Crime, per 1,000 population) 6.306 0.396 5.607 0.529 Ju veniles in Residential Placement ( per 1,000 juvenile population ) 0.230 0.016 0.213 0.022 Violent Crime Rate (per 1,000 population) 3.628 0.210 3.736 0.492 Property Crime Rate (per 1,000 population) 28.844 0.971 27.986 1.682 Adult Prison Population (per 1,000 adult population) 1.164 0.075 1.144 0.120 Fraction of Prisoners with Maximum Sentence more than One Year 0.960 0.015 0.900 0.043 Forgiveness Ratio 0.272 0.038 0.392 0.103 Employed Police Officers (per 1,000 population) 2.590 1.153 2.145 0.253 State Expenditures (per 1,000 population) 269.612 92.990 311.342 150.506 Background Indicators Fraction of Pop ulation < 15 0.200 0.003 0.193 0.005 Fraction of Pop ulation 15 to 65 0.608 0.003 0.609 0.004 Median Household Income (1,000s) 52.881 1.229 53.695 2.428 Fraction of Population 25+ with High School Diploma 86.313 0.549 86.020 1.094 27.468 0.937 26.514 1.332 Fraction Black 0.137 0.020 0.072 0.018 Fraction Hispanic 0.088 0.005 0.126 0.016 Fraction Urban 0.750 0.022 0.705 0.049 Fraction of Population Living in Poverty 0.134 0.002 0.130 0.004 Fraction of Population Blue Collar Workers 0.237 0.003 0.225 0.004 Unemployment Rate 0.064 0.002 0.058 0.004 Hea d Start Participants ( per 1,000 population ) 3.796 0.250 3.669 0.409 Note: All variables are averaged over 2006 to 2010. Forgiveness ratio measures the fraction of released prisoners per popula tion in custody. State expe nditures are state expenditures on the justice system. Crime rates and state expenditures unavailable for the District of Columbia. State level education data unavailable in 2010, so these variables are averaged from 2006 to 2009. Blue Collar workers ar e defined as workers in production, transportation, construction, installation, and maintenance. 78 Table A.2: Aggregate Expungement Statistics in Application States State Colorado Michigan Washington Average Formal Handlings (1997 - 2010) 16,112 47,351 1 8,711 Expected Adjudications (1997 - 2010) 9,667 28,411 11,263 Average Expungements 187.18 50 1,210.65 Average Expungements ÷ Expected Adjudications 0.019 0.002 0.107 Years of Data Available 2003 - 2013 2009 - 2013 1997 - 2013 Source : Colorado: Expungement c ase numbers come from Table 19 of the Annual Reports of the Judicial Branch of the State of Colorado. Michigan: The number of juvenile set asides come from the Criminal History Unit of the Criminal Justice Information Center of the Michigan State Polic e. Washington: Expungement numbers come from the Washington Administrative Office of the Courts. Note: Formal handlings (delinquency petitions) come from the National Juvenile Court Data Archive, available at www.ojjdp.gov /ojstatbb/ezaco. The unit of cou nt is cases disposed in all states with the exception of Colorado, where the unit of count is petitioned case filings by fisc al year, which include both delinquency and status offense cases. Therefore, the number reported as Average Formal Handlings for C olorado is likely biased upward. Note, however, that in the United States in 2009 there were 4.7 status offense cases for every 1,000 juveniles, while there were 49.3 delinquency ca ses per 1,000 juveniles (Puzzanchera et al. (2012). This implies that the magnitude of the bias is not likely to be particularly large. 79 Table A.3: Descriptive Statistics by Regime Application Automatic Mean Std. Error Mean Std. Error Total Sample (N=7469) Arrested as a Juvenile 0.159 0.014 0.188 0.014 Convi cted as a Juvenile 0.316 0.015 0.332 0.027 Juvenile Conviction (N=403) Not arrested after age 20 0.532 0.031 0.639 0.051 Ever Attended College 0.239 0.027 0.314 0.052 Graduated College 0.063 0.016 0.111 0.037 Average Income (1,000 s, 2 008 - 2010) 21.467 1.345 23.782 2.142 Arrested, Not Convicted (N=859) Not arrested after age 20 0.671 0.020 0.639 0.037 Ever Attended College 0.344 0.020 0.342 0.038 Graduated College 0.098 0.014 0.089 0.023 Average Income (1,000s , 2008 - 2010) 25.772 1.016 23.892 1.524 Never Arrested (N=6188) Not arrested after age 20 0.860 0.005 0.846 0.011 Ever Attended College 0.658 0.007 0.611 0.015 Graduated College 0.349 0.007 0.301 0.014 Average Income (1,000 s, 2008 - 2010) 29.996 0.366 29.793 0.704 s calculations . Note: These statistics reflect responses from 7,469 respondents in the NLSY97 weighted by 1997 sampling weights (cumulative cases method). I drop 1,515 observations of individuals who missed at least on e of the first five waves. I am unable to identify if these individuals had an arrest as a juvenile. Convicted as a juvenile is conditional on 80 Table A.4: Baseline Differences in Arrests (1) Juvenile Arrest (2 ) Juvenile Arrest (3 ) Juvenile Arrest (4 ) Juvenile Arrest Automatic Expunge 0.006 0.009 0.007 0.008 (0.022) (0.021 ) (0.019) (0.019) Parental Income (1997) - 0.003* - 0.003* - 0.001 - 0.001 (0.001) (0.001) (0.001) (0.001) Age (1997) 0.000 0.000 - 0.000 - 0.000 (0.003) (0.002 ) (0.002) (0.002) Black 0.005 0.005 - 0.025 + - 0.025 (0.015) (0.015 ) (0.014) (0.015) Hispanic - 0.014 - 0.014 - 0.034* - 0.034 + (0.017) (0.018 ) (0.017) (0.018) Female - 0.097** - 0.097** - 0.091** - 0.092** (0.012) (0.012 ) (0.012) (0.012) Living with Biological Mom 0.091** 0.092** 0.079** 0.079** (0.012) (0.012 ) (0.012) (0.012) Other Household Composition 0.117** 0.117 ** 0.100** 0.100** (0.022) (0.021 ) (0.021) (0.02 0) Custody Measure 2.424 2.454 (2.803) (2.540) Sentencing Measure 0.004 - 0.021 (0.136) (0.125) Imprisonment Rate - 0.002 - 0.001 (0.009) (0.008) Forgiveness Ratio 0.015 0.027 (0.038) (0.035) ASVAB - 0.054** - 0.054** (0.006) (0.006) R 2 0.063 0.063 0.082 0.083 Note: The dependent variable is a binary indicator of arrest as a juvenile. All regressions are weighted using 1997 sampling weights and also include log of number of employed polic e officers per capita, log of expenditures on the an urban area, log of Head Start enrollment, number of household members under 6 years old in 1997, household an indicator for ASVAB missing. The reference group for household composition is living with both biological parents. Custody measure is the average number of juveniles in residential placement divided by average reported crime over 2006 to 2010. Sentencing measure is the fraction of prisoners under jurisdiction with maximum sentence greater than one year. Forgiveness ratio measures the fraction of released prisoners per population in custody. Nineteen observations are lost because expenditures are unavailable for the District of Columbia. Standard errors are clustered at the state level. Sample size is 7450 in all regressions. + P<0.10, * P<0.05, ** P<0.01 . 81 Table A.5: Effect of Arrest and Conviction on Long - Term Outcomes (1 ) Not Arrested After Age 20? (2 ) Attend ed College (3 ) Graduated College (4 ) log( Average Income ) NLSY Sample (N=7450) Juvenile Arrest - 0.182** - 0.284** - 0.160** - 0.287** (0.016) (0.018) (0.012) (0.036) R 2 0.097 0.192 0.209 0.120 NLSY Sample (N=7450) Juvenile Arrest - 0.150** - 0.223** - 0.155** - 0.229** (0.017) (0.023) (0.013) (0.039) Juvenile Convict - 0.101** - 0.080** - 0.014 - 0.184** (0.037) (0.030) (0.016) (0.063) R 2 0.099 0.193 0.209 0.121 Note: Each panel presents the results of a regres sion of the outcome of interest on an indicator for juvenile arrest (top panel) or indicator for juvenile arrest and juvenile conviction (bottom panel). Additional covariates are the same as column (2) in Table A.4. All regressions are weig hted using 199 7 sampling weights (cumulative cases method). Standard errors are clustered at the state level. Average income is calculated over 2008 to 2010 . Nineteen observations are lost in this analysis because expenditures are unavailable for the District of Colu mbia. An example of the full regression output appears in Table G.12. + P<0.10, * P<0.05, ** P<0.01 . 82 Table A.6: Long - Term Effects of Automatic Expungement : Proxy Variable Analysis (1 ) Not Arrested After Age 20? (2 ) Attended College (3 ) Graduated Colle ge (4 ) log( Average Income ) Juvenile Convict Sample (N=403) Automatic Expunge 0.143* 0.077 0.051 0.253 (0.060) (0.067) (0.037) (0.157) R 2 0.094 0.153 0.238 0.184 Juvenile Arrest Sample (N=859) Automatic Expunge - 0.000 0.017 - 0.003 0.030 (0.036) (0.050) (0.032) (0.081) R 2 0.070 0.203 0.178 0.177 Never Arrested Sample (N=6188) Automatic Expunge 0.010 - 0.021 - 0.028 + - 0.001 (0.012) (0.017) (0.014) (0.043) R 2 0.056 0.142 0.182 0.107 Note: Each panel restricts the sample to one of three categories: those who are never arrested as a juvenile, those who are arrested but not convicted, and those who are convicted. All regressions are weighted using 1997 sampling weights (cumulative cases method). Standard errors are clustered at the state level. Average income is calculated over 2008 to 2010. Additional covariates are the same as column (2) in Table A.4. Nineteen obs ervations are lost in this analysis because expenditures are unavailable for th e District of Columbia. An example of the full regression output appears in Table G.12. + P<0.10, * P<0.05, ** P<0.01 . 83 Table A.7: Long - Term Effects of Automatic Expungement : Difference - in - Differences Analysis (1 ) Not Arrested After Age 20? (2 ) Attend ed College (3 ) Graduated College (4 ) log( Average Income ) Treatment: Convicted Control: Arrested, Not Convicted Juvenile Convict x Automatic Expunge 0.153* 0.053 0.045 0.276 + (0.057) (0.056) (0.056) (0.159) Juvenile Convict - 0.133** - 0.108* - 0. 027* - 0.320** (0.045) (0.043) (0.012) (0.083) R 2 0.087 0.198 0.205 0.178 Treatment: Convicted Control: Never Arrested Juvenile Convict x Automatic Expunge 0.120* 0.086 0.055 0.225* (0.047) (0.054) (0.054) (0.104) Juvenile Convict - 0.27 9** - 0.316** - 0.177** - 0.473** (0.038) (0.024) (0.012) (0.077) R 2 0.094 0.176 0.198 0.124 Treatment: Arrested, Not Convicted Control: Never Arrested Juvenile Arrest x Automatic Expunge - 0.031 0.026 0.012 0.003 (0.038) (0.052) (0.031) (0 .090) Juvenile Arrest - 0.145** - 0.226** - 0.155** - 0.236** (0.017) (0.026) (0.015) (0.047) R 2 0.086 0.182 0.205 0.126 Note: Each panel specifies the assumed treatment and control group for this difference - in - differences analysis. All regressions are weighted using 1997 sampling weights (cumulative cases method). Standard errors are clustered at the state level. Average income is calculated over 2008 to 2010. Additional covariates are the same as column (2). Nineteen observations are lost in this analysis because expenditures are unavailable for the District of Columbia. An example of the full regression output appears in Table G.12. + P<0.10, * P<0.05, ** P<0.01 . 84 APPENDIX B Tables f Did Graduated Driver Licensi ng Laws Drive a Reduction in Crime? 85 Table B. 1 : State Level Summary Statistics Note: The unit of observation is state*year between 1997 and 2010. Arrest ratio proxies for the percent of all crimes committed by the specific population. Median household income is in 2011 dollars. Secondary enforcement mean is conditional on having GDL restrictions implemented. Following Levitt (1998), my measures of custody rates are the stock of juveniles in state facilities divided by the population age 15 to 17 (consistent with criminal deterrence) and the stock of juvenile in state facilities divided by the total number of reported crimes (consistent with criminal incapacitation). Variables Mean Std. Dev. Outcome Variables Pre - GDL Violent Arrest Ratio: Boys Age 16 3.55 1.073 Pre - GDL Violent Arrest Ratio: Girls Age 16 0.64 0.281 Pre - GDL Property Arrest Ratio: Boys Age 16 5.03 1.233 Pre - GDL Property Arrest Ratio: Girls Age 16 2.22 0.655 Pr e - GDL Violent Crime: Boys Age 16 (per 1,000 pop) 10.46 5.201 Pre - GDL Violent Crime: Girls Age 16 (per 1,000 pop) 1.95 1.152 Pre - GDL Property Crime: Boys Age 1 6 (per 1,000 pop) 130.97 32.571 Pre - GDL Property Crime: Girls Age 16 (per 1,000 pop) 57.51 17.137 Covariates Speed Limit - 65 0.37 0.480 Speed Limit - 70+ 0.59 0.490 Seat Belt (Primary Enforcement ) 0.39 0.485 Seat Belt (Secondary Enforcement ) 0 .60 0.487 B lood A lcohol C oncentration 0.08 0.71 0.439 B lood A lcohol C oncentration 0.10 0.27 0.432 Admin License Revocation 0.92 0.270 Zero Tolerance 0.99 0.087 Secondary Enforcement of GDL Restrictions 0.22 0.412 Percent Black 0.12 0.116 Percent Les s Than 15 Years Old 0.21 0.018 Percent 15 - 19 Years Old 0.07 0.006 Percent 20 - 24 Years Old 0.07 0.007 Percent 25 - 44 Years Old 0.28 0.022 Percent 45 - 64 Years Old 0.19 0.016 Percent 65 or Older 0.18 0.022 Percent Urban 0.73 0.150 Unemployment Rate 0.05 0.019 Median Household Income (thousands) 53.19 8.003 Total Number of Police Officers (per 1,000 population) 2.42 0.964 Total Expenditure on Justice System (per 1,000 population) 239.92 100.70 Custody Deterrence 0.01 0.003 Custody Incapacitation 0.01 0.004 86 Table B.2: Effect on Arrest Ratio by Age Age 13 14 Age 16 Age 17 Age 18 - 20 Violent Crime GDL - 0.095 - 0.322 + 0.0 07 - 0.076 (0.200) (0.162) (0.109) (0.181) Pre - GDL Mean 3.995 4.185 4.748 14.542 Property Crime GDL - 0.175 - 0.503* - 0.219 - 0.103 (0.192) (0.196) (0.154) (0.198) Pre - GDL Mean 9.281 7.256 7.015 15.943 Note: T he d ependent variable in each regression is the arrest ratio for the specified crime and age categories . Arrest ratio can be interpreted as the percent of all crimes committed by the specific population. The additional covariates included in the regressi on are: a lagged measure of custody to proxy for severity, the natural logarithm of the state population, the natural logarithm of the number of employed police officers per capita, the na tural logarithm of state expenditures on the justice system per capi ta, the fraction of the state population less than 15 years old, 20 to 24 years old, 25 to 44 years old, 45 to 64 years old, and older than 65, the fraction of the state that is urban, median household income, state policies related to driving, year fixed effects, and state fixed effects. Standard errors (in parentheses) are adjusted for clustering at the state level. Sample size is 632 in all regressions. + P<0.10, * P<0.05, ** P<0.01 . 87 Table B.3: Primary and Secondary Enforcement, Age 16 Arrest Ratio Violent Crime GDL - 0.347* (0.166) GDL x Secondary 0.272 (0.209) Property Crime GDL - 0.500* (0.203) GDL x Secondary - 0.035 (0.257) Note: The d ependent variable in each regression is the arrest ratio for the specified crime categories for age 16 . Arrest ratio can be interpreted as the percent of all crimes committed by 16 year olds. The additional covariates included in the regression are: a lagged measure of custody to proxy for severity, the natural logar ithm of the state population, the natural logarithm of the number of employed police officers per capita, the natural logarit hm of state expenditures on the justice system per capita, the fraction of the state population less than 15 years old, 20 to 24 ye ars old, 25 to 44 years old, 45 to 64 years old, and older than 65, the fraction of the state that is urban, median household income, state policies related to driving, year fixed effects, and state fixed effects. Standard errors (in parentheses) are adju sted for clustering at the state level. Sample size is 632 in all regressions. + P<0.10, * P<0.05, ** P<0.01 . 88 Table B.4: Robustness of Dependent Variable, Age 16 Arrest Ratio Adjusted Arrest Ratio Log(Arrests Age 16) Log(Arrest Ratio) Crime Rate Viole nt Crime GDL - 0.322 + - 0.815 + - 0.084* - 0.084* - 0.131* (0.162) (0.482) (0.040) (0.037) (0.063) Pre - GDL Mean 4.185 8.169 5.001 1.388 2.409 Property Crime GDL - 0.503* - 1.271 + - 0.063 + - 0.077* - 0.085** (0.196) (0.661) (0.035) (0.030) (0. 030) Pre - GDL Mean 7.256 20.331 6.917 1.955 5.208 Note: The d ependent variable in each regression is the listed measure fo r the specified crime for age 16 . Arrest ratio can be interpreted as the percent of all crimes commit ted by 16 year olds. The additional covariates included in the regression are: a lagged measure of custody to proxy for seve rity, the natural logarithm of the state population, the natural logarithm of the number of employed police officers, the natural l ogarithm of state expenditures on the justice system, the fraction of the state population less than 15 years old, 20 to 24 years old, 25 to 44 years old, 45 to 64 years o ld, and older than 65, the fraction of the state that is urban, median household inco me, state policies related to driving, year fixed effects, and state fixed effects. When using Log(Arrests Age 16) as the dependent variable I also include the natural logarithm of total arrests age 25 and older as a covariate. Standard errors (i n parent heses) are adjusted for clustering at the state level. Sample size is 632 in all columns other than Crime Rate. The sample size for Crime Rate is 529. This r eflects data from 49 states for the years that have over 85 percent coverage according to the Fe deral Bureau of Investigation. + P<0.10, * P<0.05, ** P<0.01 . 89 Table B.5: Effect on Arrest Ratio by Gender, Age 16 Male Female Violent Crime GDL - 0.293* - 0.029 (0.141) (0.045) Pre - GDL Mean 3.548 0.637 Property Crime GDL - 0.358* - 0.145 + (0.144) (0.076) Pre - GDL Mean 5.032 2.224 Note: The d ependent variable in each regression is the arrest ratio for the specified crime and gender for age 16 . Arrest ratio can be interpreted as the percent of all crimes comm itted by the specific population. The additional covariates included in the regression are: a lagged measure of custody to p roxy for severity, the natural logarithm of the state population, the natural logarithm of the number of employed police officers p er capita, the natural logarithm of state expenditures on the justice system per capita, the fraction of the state population less than 15 years old, 20 to 24 years old, 25 to 44 y ears old, 45 to 64 years old, and older than 65, the fraction of the state t hat is urban, median household income, state policies related to driving, year fixed effects, and state fixed effects. Stand ard errors (in parentheses) are adjusted for clustering at the state level. Sample size is 632 in all regressions. + P<0.10, * P<0 .05, ** P<0.01 . 90 Table B.6: Effect on Specific Offenses by Gender, Age 16 Violent Crime Property Crime Murder Rape Robbery Aggravated Assault Burglary Larceny Motor Vehicle Theft Male GDL - 0.003 0.017 - 0.077 - 0.231** - 0.081 + - 0.240* - 0.037 (0.008) (0.020) (0.084) (0.084) (0.042) (0.099) (0.036) Female GDL 0.000 0.001 - 0.005 - 0.025 0.000 - 0.129 + - 0.016 (0.002) (0.001) (0.009) (0.042) (0.007) (0.075) (0.010) Note: The d ependent variab le in each regression is the arrest ratio for the specified crime and gender for age 16 . Arrest ratio can be interpreted as the percent of all crimes committed by the specific population. The additional covariates included in the regression are: a lagged measure of custody to proxy for severity, the natural logarithm of the state population, the natural logarithm of the number of employed police officers per capita, the na tural logarithm of state expenditures on the justice system per capita, the fraction of the state population less than 15 years old, 20 to 24 years old, 25 to 44 years old, 45 to 64 years old, and older than 65, the fraction of the state that is urban, median household income, state policies related to driving, year fixed effe cts, and sta te fixed effects. Standard errors (in parentheses) are adjusted for clustering at the state level. Sample size is 632 in all regressions. + P<0.10, * P<0.05, ** P<0.01 . 91 Table B.7: Permanent Effects for Older Age Groups Age 18 Age 19 Age 20 Violent Cr ime GDL - 0.225 - 0.073 - 0.123 (0.144) (0.216) (0.198) Pre - GDL Mean 5.233 4.953 4.356 Property Crime GDL - 0.143 - 0.107 0.088 (0.162) (0.154) (0.149) Pre - GDL Mean 6.680 5.248 4.015 N 448 406 365 Note: The d ependent variable in each regression is the arrest ratio for the specified crime and age categories . For Age 18 I drop observations within two years of GDL implementation to ensure all 18 year olds have been exposed to the policy. For Age 19 I drop obse rvations within three years of GDL implementation, and for Age 20 I drop observations within four years of GDL implementation. Therefore, these results can be interpreted as the d ifference in the arrest ratio for the specified age between those who were n ot exposed to GDL and those who were exposed to GDL. Arrest ratio can be interpreted as the percent of all crimes committed by the specific population. The additional covariates included in the regression are: a lagged measure of custody to proxy for sev erity, the natural logarithm of the state population, the natural logarithm of the number of employed police officers per capita, the natural lo garithm of state expenditures on the justice system per capita, the fraction of the state population less than 1 5 years old, 20 to 24 years old, 25 to 44 years old, 45 to 64 years old, and older than 65, the fraction of the state that is urban, median household income, state policies related to driving, year fixed effects, and state fixed effects. Standard errors ( in parentheses) are adjusted for clustering at the state level. + P<0.10, * P<0.05, ** P<0.01 . 92 Table B.8: Effect of Nighttime and Passenger Restrictions, Age 16 Arrest Ratio Violent Crime Nighttime Restrictions - 0.407 + (0.213) Passenger Restric tions 0.284 (0.180) Property Crime Nighttime Restrictions - 0.480 + (0.259) Passenger Restrictions 0.161 (0.195) Note: The d ependent variable in each regression is the arrest ratio for the specified crime categori es for age 16 . Arrest ratio can be interpreted as the percent of all crimes committed by 16 year olds. The additional covariates included in the regression are: a lagged measure of custody to proxy for severity, the natural logarithm of the state populat ion, the natural logarithm of the number of employed police officers per capita, the natural logarithm of state expenditures on the justice system per capita, the fraction of the state population less than 15 years old, 20 to 24 years old, 25 to 44 years o ld, 45 to 64 years old, and older than 65, the fraction of the state that is urban, median household income, state policies related to driving, year fixed effects, and state fixed effects. Standard errors (in parentheses) are adjusted for clustering at th e state level. Sample size is 632 in all regressions. + P<0.10, * P<0.05, ** P<0.01 . 93 APPENDIX C Tables f Interstate Differences i n Pension Vesting R ules, K - 12 Teacher Experience, a nd Teacher Exit 94 Table C.1: S tate Teacher Pension Parameters Stat e Retirement Rule Factor Experience=0) Salary (Top Step) Contribution Rate Covered by Social Security? California 60/5 Vesting = 5 FAS = highest year salary 1.4% to 2.4%, depending on age at retirement $40,100 $75,400 8% No Florida 6 2/6, A/30 Vesting = 6 FAS = average of highest 8 years 1.6% $33,300 $60,800 3% Yes Michigan 60/10, 46/30 Vesting = 10 FAS = average of highest 3 years 1.5% $34,200 $66,700 $510 + 6.4% of any income over $15,000 Yes Wisconsin 65/5, 57/30 Vesting = 5 FAS = average of highest 3 years 1.6% $30,700 $57,100 6.65% Yes Source: SASS and state - specific handbooks detailed below. California: CALSTRS 2013 Member Handbook (available at http://www.calstrs.com/sites/main/files/file - attachments/memberhandbook2013_web_v 4.pdf) Florida: Florida Retirement System Pension Plan Summary Plan Description (available at https://www.rol.frs.state.fl.us/forms/ spd - pp.pdf) Michigan: Michigan Public School Employees Retirement Syste m Member Handbook (available at http://www.michigan.g ov/documents/MPSERS1_92795_7.pdf) Wisconsin: Wisconsin Retirement System Benefit Handbook (available at http://etf.wi.gov/publications/et2119.pdf) Note: Retirement rule provides the minimum age and minimum years of service required for full retirement bene fits. This is written as a fraction: minimum service). FAS stands for Final Average Salary. 95 Table C. 2 : Cost of Living Adjustme nts Note: This table compares the present discounted value of pension wealth for a simulated teacher in Michigan both with and wi thout Cost of Living Adjustments (COLA). The assumed formula for Cost of Living Adjustments is three percent of annual benefit each year (not compounded) starting the October aft er one full year of retirement. State Peak Value Quit After 10 Years Retire at 55 Retire at 60 Retire at 65 Michigan No COLA $457,101 Age 55 $ 48,963 ( - 408,138) $ 457,101 (0) $ 443,489 ( - 13,612) $ 399,078 ( - 58,023) Michigan With COLA $663,788 Age 55 $65,909 ( - 597,879) $663,788 (0) $63 2,911 ( - 30,877) $561,805 ( - 101,983) 96 Table C. 3 : Simulation Results State Peak Value Quit after 2 years Quit after 5 Years Quit After 10 Years Retire at 55 Retire at 60 Retire at 65 California $691,288 Age 60 $0 ( - 691,288) $27,069 ( - 664,219) $56,223 ( - 635,065) $487,271 ( - 204,017) $691,288 (0) $612,237 ( - 79,051) Florida $681,595 Age 55 0 ( - 681,595) 0 ( - 681,595) 49,971 ( - 631,624) 681,59 5 (0) 667,366 ( - 14,229) 616,536 ( - 65,059) Michigan $663,788 Age 55 0 ( - 663,788) 0 ( - 663,788) 65,909 ( - 597,879) 663,788 (0) 632,911 ( - 30,877) 561,805 ( - 101,983) Wisconsin $370,893 Age 57 0 ( - 370,893) 11,279 ( - 359,614) 19,237 ( - 351,656) 322,055 ( - 48,838) 3 54,977 ( - 15,916) 304,814 ( - 66,079) Michigan (Defined Contribution Plan) --------- 6,341 17,322 40,161 664,480 802,186 927,981 Note: Calculations assume teacher began work at a ge 25 with a . Difference fr om peak value appears in parentheses below the present discounted value. 97 Table C.4: Summary Statistics Mean Standard Deviation Minimum Maximum Experience < 4 years 15.39 4.864 6.04 28.30 4 < experience <= 9 27.12 4.669 18.60 52.01 10 15 39.67 6.218 20.65 55.36 Years until vested 5.78 2.431 0 10 Purchase credits 0.63 0.486 0 1 Starting salary $33,172 4,181 24,800 42,700 Source: . Notes: Experience measures the fraction of te achers that fall into each experience bin in each state. Purchase credits refers to the ability to purchase credits for prior service as a teacher. 98 Table C.5: Regression Results for Teacher Experience Percent with fewer than 4 years exper Percent with 4 to 9 years exper Percent with 10 to 14 years exper Percent with 15 or more years exper Years until vested - 0.361* (0.145) - 0.377* (0.163) 0.201 (0.156) - 0.054 (0.198) 0.376** (0.118) 0.276* (0.135) - 0.217 (0.232) 0.156 (0.255) Purchase credits - 0.81 2 (0.735) - 2.128* (1.025) 0.476 (0.784) 2.457* (1.114) Average age - 0.929** (0.178) - 1.154** (0.281) - 0.036 (0.233) 2.114** (5.59) Log (starting salary) 0.611 (2.731) 15.837** (4.581) 4.667 (3.678) - 21.156** (4.331) Log (pension wealth) 0.26 8 (1.788) - 1.999 (2.101) - 2.859 + (1.675) 4.546 (2.962) Constant 14.227** (1.014) 44.218 (36.421) 26.365** (1.360) - 59.696 (49.864) 17.421** (0.884) 8.750 (41.301) 41.991** (1.889) 107.959 (65.177) Obs. 102 102 102 102 102 102 102 102 R 2 0.4 8 0.62 0.02 0.36 0.29 0.34 0.04 0.48 Notes: Pension data are from the Public Fund Survey (2001 - 2010) . Dependent variables are distribution of teacher experience from Schools and Staffing Survey (2008 and 2011). Pension w ealth estimates come from Table 8 of Toutkoushian et al. (2011). Regressions also contain year dummies. Robust standard errors are in parentheses. + P<0.10, * P<0.05, ** P<0.01 . 99 Table C.6: NLSY Descriptive Statistics 2002 - 2010 Notes: ASVAB is an ability exam administered in the first wave of the NLSY . Other Teacher includes special education teachers and other teachers who do not fall into the other teaching categories. Contribution rate is conditional on rate being nonzero. Withdraw variables describe refund of contributions if teacher leaves the system before vesting. Service credits (for prior work as a teacher) are available for purchase in some states. Variables Mean Std. Dev. Teacher Population (779 individuals) Age when Begin Teaching 23.78 2.314 Female 0.66 0.473 Black 0.17 0.372 Hispanic 0.15 0.353 Married 0.20 0.399 Single 0.76 0.426 Number of Kids in Household 0.23 0.624 Family Income (Thousands) 66.51 65.9 31 ASVAB Percentile 68.72 24.143 Employment Characteristics Starting Wage (Hourly) 17.50 18.984 Wage After 5 Years (Hourly) 21.28 9.886 Postsecondary Teacher 0.25 0.432 Preschool/Kindergarten Teacher 0.05 0.210 Elementary/Middle School Teacher 0.40 0.490 Secondary School Teacher 0.19 0.390 Other Teacher 0.41 0.492 Job Tenure 2.16 1.424 Pension Characteristics Years to Vesting 5.88 2.316 DC Plan Available? 0.33 0.469 Choice Between DB and DC? 0.11 0.313 Retirement Factor 0.02 0.004 Covered by Social Security? 0.60 0.490 Employee Contribution Rate 0.06 0.022 Years to Tenure 3.15 0.738 Withdraw: Less or Equal Own Contribution 0.11 0.316 Withdraw: Own and Interest 0.77 0.423 Withdraw: Own, Interest, and Employer 0.12 0.320 Purch ase Credits: No 0.29 0.456 Purchase Credits: Limited 0.29 0.456 Purchase Credits: Unlimited 0.41 0.491 100 Table C.7: NLSY Regression Results (1) (2) (3) Time to Vesting 0.092** (0.021) [0.023] 5+ Years from Vesting 0.567* (0.250) [0.141] 4 Years from Vesting 0.578* (0.257) [0.143] 3 Years from Vesting 0.439 + (0.254) [0.109] 2 Years from Vesting 0.548* (0.244) [0.136] 1 Year from Vesting - 0.120 (0.274) [ - 0.030] Vested - 1.048** (0.328) [ - 0.238] DC Also 0.538** 0.466** (0.122) (0.123) [0.134] [0.116] Choice between DB/DC - 0.219 - 0.282 (0.189) (0.192) [ - 0.054] [ - 0.070] ASVAB Percentile 0.008** 0.008** 0.009** (0.002) (0.002) (0.002) [0.002] [0.002] [0.002] Age 0.008 0.059 + 0.065 + (0.032) (0.034) (0.035) [0.002] [0.015] [0.016] Female - 0.187* - 0.191 + - 0.216* (0.091) (0.098) (0.099) [ - 0.047] [ - 0.048] [ - 0.054] Black 0.045 0.133 0.127 (0.124) (0.134) (0.136) [0.011] [0.033] [0.032] Hispanic 0.240 + 0.217 0.170 (0.133) (0.147) (0.149) [0.060] [0.054] [0.042] Married - 0.198 + - 0.186 - 0.143 (0.107) (0.116) (0.117) 101 [ - 0.049] [ - 0.046] [ - 0.036] Number of Kids in HH 0.076 0.052 0.093 (0.071) (0.078) (0.080) [0.019] [0.013] [0.023] Has Tenure - 1.410** - 1.303** (0.113) (0.134) [ - 0.330] [ - 0.307] Retirement Factor 46.968* 28.681 (21.921) (22.252) [5.471] [7.155] Covered by Social Security 0.138 0.165 (0.152) (0.153) [0.034] [0.041] Employee Contribution Rate - 3.204 - 1.505 (3.408) (3.456) [ - 0.800] [ - 0.375] N 2479 2479 2479 Notes: Dependent variable is the hazard of first exit from teaching. Regressions in columns (2) and (3) also contain year dummies, reported family income, indicator for mixed race, indicator for marital status unknown, indicator for separated/divorced, and indicators for pension portability. Standard errors in parentheses. Marginal effects in brackets. + P<0.10, * P<0.05, ** P<0.01 . 102 Tab le C.8: NLSY Regression Results by Teacher Type (1) Elementary & Middle (2) Secondary Time to Vesting 0.117** 0.139* (0.034) (0.066) [0.024] [0.028] DC Also 0.250 0.710* (0.219) (0.329) [0.053] [0.151] Choice between DB/DC - 0.341 0.703 (0.364 ) (0.612) [ - 0.067] [0.157] ASVAB Percentile 0.000 - 0.002 (0.004) (0.006) [0.000] [ - 0.000] Age 0.121 + 0.499** (0.067) (0.123) [0.025] [0.100] Female - 0.472* - 0.433 + (0.191) (0.247) [ - 0.103] [ - 0.088] Black 0.418 + - 0.232 (0.222) (0.383) [0.092] [ - 0.045] Hispanic 1.187** 0.974** (0.251) (0.364) [0.277] [0.220] Married - 0.010 - 0.620* (0.204) (0.291) [ - 0.002] [ - 0.120] Number of Kids in HH 0.073 0.394* (0.130) (0.199) [0.015] [0.079] Has Tenure - 2.109** - 1.897** (0.218) (0.3 05) [ - 0.381] [ - 0.347] Retirement Factor - 48.492 8.479 (43.856) (62.129) [ - 10.157] [1.704] Covered by Soc Security 0.664* - 0.133 (0.275) (0.434) [0.135] [ - 0.027] Employee Contrib Rate 5.951 3.764 (6.903) (10.047) [1.247] [0.756] 103 Table C.8 N 999 483 Notes: Dependent variable is the hazard of first exit from teaching for the specific population. Regressions also contain year dummies, reported family income, indicator for mixed race, indicator for marital status unknown, indicator for separated/divorced, and indicators for pension portability. Standard errors in parentheses. Marginal effects in brackets. + P<0.10, * P<0.05, ** P<0.01. 104 APPENDIX D Figures f or ime? The Effects of Juvenile Expungement on Crime, Educational, a 105 Figure D.1: Crime Decision by Ability and Expungement Policy 106 Figure D.2: Automatic Expungement States Source: Statutes detailed in Table G.1. Note: Stat es with automatic expungement statutes appear in dark gray. Alaska and Hawaii (excluded from this picture) both have automat ic expungement statutes . 107 APPENDIX E Figures f Did Graduated Driver Licensing Laws Drive a Reduction in Crime? 108 Figure E.1: Motor Vehicle Access and Crime Source: Uniform Crime Reports (2010), Insurance Institute for Highway Safety (2013) Note: All data in the figure are as of 2010. Arrest data come from Uniform Crime Reports and are national counts of arres ts for violent and property crime divided by the population for the specified age group. The District of Columbia and Florida are excluded from the arrest data because arrests by age are unavailable. 109 Figure E.2: Event Study, Violent Crime Source: Note: Each estimate comes from the preferred specification including dummy variables for leads and lags , pertinent covariates, state fixed effects, and year fixed effects. Arrest ratio can be interpreted as the perce nt of all crimes committed by 16 year olds. The reference gr oup for the event study is four or more years prior to GDL implementation. The unit of observation is state*year. S tandard errors are adjusted for c lustering at the state level. Standard error bars are the 90 percent confidence interval for the estimates. 110 Figure E.3: Event Study, Property Crime Source: Note: Each estimate comes from the preferred specification including dummy variables for leads an d lags , pertinent covariates, state fixed effects, and year fixed effects. Arrest ratio can be interpreted as the percent of all crimes committed by 16 year olds. The reference gr oup for the event study is four or more years prior to GDL implementation. The unit of observation is state*year. S tandard errors are adjusted for c lustering at the state level. Standard error bars are the 90 percent confidence interval for the estimates. 111 Figure E. 4: Arrests by Time of Day Source: Auth ncident Based Reporting System. Note: Each curve shows the fraction of total arrests that were 16 years old at each hour of the day. For each hour I plot the fraction in states where that hour is restricted due to a GDL restri ction and the fraction in states where the hour is not restricted. No states have restrictions between 6:00 AM and 8:00 PM. Dashed lines are the 90% confidence interval for the estimates. The vertical dashed line represents midnight. 112 APPENDIX F Figu res f Interstate Differences i n Pension Vesting R ules, K - 12 Teacher Experience, a nd Teacher Exit 113 Figure F. 1 : Pension Wealth o ver the Teaching Career Source: Authors . Notes: Calculations assume teacher was hired at age 25 with a Bac 0.00 100,000.00 200,000.00 300,000.00 400,000.00 500,000.00 600,000.00 700,000.00 800,000.00 29 35 40 45 46 47 48 49 50 51 52 53 54 55 56 57 58 59 60 61 62 63 64 65 66 67 68 69 70 Present Discounted Value Age California Wisconsin Michigan Florida 114 Figure F. 2 : Pension Wealth Early in the Teaching Career Source: Autho . 115 APPENDIX G Appendices f or o f a Crime? The Effects o f Juvenile Expungement o n Crime, Educational, a 116 G.1: Expungement Statutes This appendix presents tables focusing on expungement statutes. Table G.1: Overview of C urren t Expungement Statutes by State State Current Statute Alabama Citation: Ala.Code 1975 § 12 - 15 - 136 Terminology: Seal Brief Summary: Requires application: 2 years since entry of order or final discharge from supervision and no other convictions. Alask a Citation: AS § 47.10.090 Terminology: Seal Brief Summary: th birthday or the day on which jurisdiction is released (whichever is later). Arizona Citation: A.R.S. § 8 - 348, 349 Terminology: Set Aside, Dest ruction Brief Summary: Requires application: must be at least 18 years old, not convicted of a felony, and no pending criminal charges. Certain crimes require waiting until 25 years old. More specifics depend on the initial crime. Arkansas Citation: A.C .A. § 9 - 27 - 309 , A.C.A. § 16 - 90 - 901 through 16 - 90 - 905 Terminology: Expunge, Seal Brief Summary: Court may expunge record at any time and shall expunge record on 21 st birthday. No specific requirements given for when an individual can apply for sealing. Ca lifornia Citation: Cal.Welf. & Inst.Code § 781 Terminology: Seal Brief Summary: Requires application: must be either 18 years old or five years after end of jurisdiction/final discharge; certain offenses cannot be sealed Colorado Citation: C.R.S. § 19 - 1 - 3 06 Terminology: Expunge Brief Summary: Requires application: certain offenses cannot be expunged, no pending charges, proof of rehabilitation to the court; amount of time required to wait depends on final disposition of the case. 117 Conne cticut Citation: C.G.S.A. § 46b - 146 Terminology: Erasure Brief Summary: Requires application: amount of time required to wait depends on nature of offense; no pending charges, child has reached 18 years of age. Delaware Citation: Del. Code Ann. tit. 10, § 1015 Terminology: Expunge Brief Summary: Requires application: amount of time required to wait depends on nature of offense; no pending charges. District of Columbia Citation: DC ST § 16 - 2335 Terminology: Seal Brief Summary: Requires motion of petitioner supervision, no subsequent convictions or adjudications. Florida Citation: F.S.A. § 943.059, F.S.A. § 943.0585 , F.S.A. § 943.05 1 5 Terminology: Seal, Expunge Brief Sum mary: Petition required for sealing or early expungement: petitioner must obtain Certificate of Eligibility, certain crimes Georgia Citati on: Ga. Code Ann., § 15 - 11 - 79.2 Terminology: Seal Brief Summary: charges, person has been rehabilitated. Hawaii Citation: HRS § 571 - 84 Terminolog y: N/A Brief Summary: The statute states that all records are open to inspection only by the persons whose official duties are concerned with the juvenile court, except as otherwise ordered by the court. According to the Hawaii Office of the Public Defend er, this statute Idaho Citation: I.C. § 20 - 525A Terminology: Expunge Brief Summary: Requires application: petitioner must be at least 18 years old, amount of time depends on the nature of the offense, certain crimes ineligible to be expunged. Illinois Citation: 705 ILCS 405/5 - 915 Terminology: Expunge Brief Summary: Requires application: can apply when person has reached 17 years of age or all court proceed ings have been terminated (whichever is later), certain crimes ineligible to be expunged, for more serious offenses must wait longer amount of time to apply. Indiana Citation: IC 31 - 39 - 8 Terminology: Expunge Brief Summary: Requires application: any person may petition at any time; court will consider a number of factors in determining whether to grant the expungement. 118 Iowa Citation: I .C.A. § 232.150 Terminology: Seal Brief Summary: son must be 18 years or older and two years must have elapsed since last action in case, no subsequent adjudications or convictions and no pending charges, restitution paid. Kansas Citation: K.S.A. 38 - 2312 Terminology: Expunge Brief Summary: Requires appl ication: person must be 23 years old or two years have elapsed since final discharge, certain crimes ineligible for expungement, no subsequent adjudications or convictions and no pending charges. Kentucky Citation: KRS § 610.330 Terminology: Expunge Brief Summary: unconditional release, certain crimes ineligible for expungement, no subsequent adjudications or convictions and no pending c harges. Lo uisiana Citation: LSA - Ch.C. Art. 917 - 920 Terminology: Expunge Brief Summary: Requires a motion: person must be 17 years of age or older, certain crimes ineligible for expungement, five or more years elapsed since most recent judgment, no criminal felony convictions and no criminal court convictions for misdemeanors involving a weapon, no outstanding indictment or charges. Maine Citation: 15 M.R.S.A. § 3308 Terminology: Seal Brief Summary: Requires a petition: three years must have passed since discharge from the disposition ordered for the crime, no subsequent adjudications or convictions, no pending charges. Maryland Citation: MD Code, Courts and Judicial Proceedings, § 3 - 8A - 27 Terminology: Seal Brief Summary: on. Records will be sealed if petitioner is over age 21. Massachusetts Citation: M.G.L.A. 276 § 100B Terminology: Seal Brief Summary: Requires a petition: three years since court appearance or final disposition, no subsequent adjudications or convictions (excluding certain motor vehicle offenses). Michigan Citation: M.C.L.A. 712A.18e Terminology: Set Aside Brief Summary: Requires application: offenses determine how many and which adjudications are eligible to be set aside; must wait one year following im position of the disposition, one year following completion of any term of detention, or age 18 (whichever occurs latest). Minnesota Citation: M.S.A. § 260B.198 Subd. 6 Terminology: Expunge Brief Summary: Requires application. The court may expunge the ad judication of delinquency at any time that it deems advisable. 119 Mississippi Citation: Miss. Code Ann. § 43 - 21 - 263 Terminology: Seal Brief Summary: Requires application or its own motion: child who was the subject of the cause has attained 20 years of age, if the youth court dismisses the cause or if the youth court sets aside an adjudication in the cause. Missouri Citation: V.A.M.S. 211.321 Terminology: Seal, Destroy Brief Summary: Requires application by the child or its own moti on: child must have reached 17 th birthday, must be in best interests of the child. Montana Citation: Mont. Code Ann. § 41 - 5 - 216 Terminology: Seal Brief Summary: th birthday; if jurisdiction extends beyond 18 th birthday records must be sealed upon termination of jurisdiction. Nebraska Citation: Neb.Rev.St. § 43 - 2,108.01 through Neb.Rev.St. § 43 - 2,108.05 Terminology: Seal Brief Summary: Requires a proceeding to seal the record: the court may order the record sea led if it finds the juvenile has been rehabilitated to a satisfactory degree; factors determining rehabilitation include age of the juvenile, nature of the offense , behavior of the juvenile after the disposition or sentence, and education and employment hi story of the juvenile. Nevada Citation: N.R.S. 62H.1 3 0 - 150 Terminology: Seal Brief Summary: IF UNDER 21: Requires a petition by the child or a probation officer on behalf of the child: must wait three years since last adjudicated or was last seen in co urt; during this three year period child must not have been convicted of a felony or misdemeanor involving moral turpitude, and child must have been rehabilitated to satisfaction of the court. WHEN CHILD REACHE S 21: All records are automatically sealed (so me crimes are excepted). New Hampshire Citation: N.H. Rev. Stat. § 169 - B:35 Terminology: Closed Brief Summary: Once a delinquent reaches 21 years of age all records shall be closed and placed in an inactive file. New Jersey Citation: N.J.S.A. 2C:52 - 4.1 ( expunge); N.J.S.A. 2A:4A - 62 (seal) Terminology: Expunge, Seal Brief Summary: SEAL: have elapsed since final discharge or since last entry of the court n ot involving custody or supervision, no subsequent adjudications or convictions and no pending charges EXPUNGE: five years must have elapsed since final discharge or since last entry of the co urt not involving custody or supervision, no subsequent adjudic ations or convictions and no pending charges, certain offenses ineligible to be expunged, has never had previous offense expunged, did not complete any diversion program. 120 New Mexico Citation: N. M. S. A. § 32A - 2 - 26 Termi nology: Seal Brief Summary: Before age 18 requires motion by or on behalf of the person who has been the subject of the delinquency proceedings: two years must have elapsed since release of person from custody or since entry of judgment not involving legal custody or supervision, no subsequent felony or misdemeanor involving moral turpitude and no pending charges, must show good cause fo r sealing. Upon age 18 or at the expiration of disposition (whichever occurs later) records are sealed automatically. Ne w York Citation: Family Court Act § 375.2 Terminology: Seal Brief Summary: Requires motion of the respondent: motion may be filed at any time subsequent to the entering of finding of delinquency; motion may not be filed until the respondent is 16 years of age. North Carolina Citation: N.C.G.S.A. § 7B - 3 2 00 Terminology: Expunction Brief Summary: Requires a petition of the court: person must have reached 18 years of age if undisciplined or 16 years of age if delinquent, certain offenses ineligible to be expu nged, 18 months since person was released from juvenile court jurisdiction, no subsequent adjudications or convictions. North Dakota Citation: NDCC, 54 - 23.4 - 17 Terminology: Sealed Brief Summary: Juvenile or law enforcement records must be sealed at the co nclusion of proceedings. Sealed records are eventually destroyed pursuant to rules and policies established by the Supreme Court. Ohio Citation: R.C. § 2151.356 Terminology: Seal (sealed records can later be expunged) Brief Summary: Requires application months from date of either termination of order of the court, unconditional discharge of the person, or court order that the child is no longer a juvenile offe nder registrant; the court will order the record sealed if the person has been sufficiently rehabilitated. Oklahoma Citation: 10A Okl.St.Ann. § 2 - 6 - 108 Terminology: Seal Brief Summary: The court may order the records sealed if one of a number of condition s occur: one year has elapsed since the later of dismissal/closure of the case by the court or notice to the court of final discharge of supervision, the person has no subseq uent criminal offenses in either juvenile or adult proceedings, and no juvenile or criminal proceeding is pending; no adjudication occurred; completion of diversion program; completion of military mentor program. Oregon Citation: O.R.S. § 419A.262 Terminology: Expunction Brief Summary: wn motion: if the matter is contested the following must be true: five years must have elapsed since most recent termination, no subsequent convictions of any felony or Class A misdemeanor, n o pending criminal proceedings or investigations. 121 Table Pennsylvania Citation: 18 Pa.C.S.A. § 9123 Terminology: Expunge Brief Summary: individual completed informal adjustment, diversion p rogram, all terms and conditions of the sentence imposed following a conviction for a summary offense, all terms and conditions of the sentence imposed following a conviction for a violation; five years have elapsed since the final discharge of the person from commitment, placement, probation or any other disposition and referral ; no subsequent convictions or adjudications, no pending charges, individual is 18 years or older. Rhode Island Citation: Gen.Laws 1956, § 14 - 1 - 6.1 Terminology: Seal Brief Summary: A ll court records shall be sealed upon final disposition of the case in the event of a no information, dismissal or not guilty finding or upon the completion of any sentence, probation and/or parole imposed . South Carolina Citation: Code 1976 § 63 - 19 - 205 0 Terminology: Destruction Brief Summary: Requires petition by the person who committed the offense: certain offenses ineligible to be expunged, person must be at least 18 years of age, successfully completed any dispositional sentence imposed, and no subs equent criminal charges. South Dakota Citation: SDCL § 26 - 7A - 114 through SDCL § 26 - 7A - 116 Terminology: Seal Brief Summary: release of the child or the discharge of the child by the Department of Corrections (whichever is later), no subsequent adjudications, no pending proceedings involving felonies, sexual contact offenses, or misdemeanors involving moral turpitude, Tennessee Citation: T. C. A. § 37 - 1 - 153 Terminology: Expunction Brief Summary: Requires petition by someone who was tried and adjudicated: must be 18 years or older, at least one year removed from most recent delinquency adjudication, certain offenses ineligible to be expunged, maintained a consistent and exemplary pattern of responsible, productive and civic - minded conduct for one or more years immediately preceding the filing of th e expunction petition or has made such an adjustment of circumstances th at the court believes that expunction serves the best interest of the child and the community . Texas Citation: V.T.C.A., Family Code § 58.003 ; V.T.C.A., Family Code § 58.204 Terminology: Sealing Brief Sum mary: record can only be viewed by criminal justice agencies. Prior to age 21 requires application by the juvenile: two years must have passe d since the final discharge of the person, no subsequent adjudications or convictions, no pending charges; These rules are sl ightly different for certain classes of offenses. 122 Utah Citation: U.C.A. § 78A - 6 - 1105 Terminology: Expunge Brief Summary: Requires petition by person who has been adjudicated: must be 18 years or older, one year must have passed from in offenses ineligible to be expunged. Vermont Citation: 33 V.S.A. § 5119 Terminology: Seal Brief Summary: NOTE: Statute change in 1996 changed Vermont to automatic sealing: for adjudications occurring after July 1, 1996 records are automatically sealed t committed certain offenses or has not been sufficiently rehabilitated. For adjudications occurring before July 1, 1996: reco rd will be sealed if on app Virginia Citation: VA Code Ann . § 16.1 - 306 Terminology: Expunge Brief Summary: On January 2 of each year the clerk destroys all records connected with juvenile proceeding if the juvenile has attained age 19 and five years have elapsed since the date of the last hearing in any case of t he juvenile which is subject to this section (ie: this occurs automatically). Records for certain offenses are ineligible to be destroyed. Washington Citation: West's RCWA 13.50.050 Terminology: Seal Brief Summary: Requires a motion by the person who i s the subject of the complaint: Specifics of the process depend on the offense which is trying to be sealed ; those who have gone through diversion programs may request that the records be destroyed. West Virginia Citation: W. Va. Code, § 49 - 5 - 18 Terminol ogy: Marked Brief Summary: One year after the juvenile's eighteenth birthday, or one year after personal or juvenile jurisdiction has terminated, whichever is later, the records of a juvenile proceeding are automatically marked and moved to a separate secu re confid ential place; Marking the juvenile records to show they are to remain confidential has the legal effect of extinguishing the offense as if it never occurred. Wisconsin Citation: W.S.A. 938.355 (4m) Terminology: Expunge Brief Summary: Requires pe tition of court: person must have reached 17 years of age, person must have satisfactorily complied with the conditions of dispositional order and that the juvenile will benefit from and society will be harmed by expungement. Wyoming Citation: W.S.1977 § 14 - 6 - 241 Terminology: Expunge Brief Summary: Requires petition of the court: juvenile must have reached the age of majority, certain offenses ineligible to be expunged, no subsequent convictions, adjudications, or pending proceedings, rehabilitation of pet itioner must satisfy the court. Note: Automatic statutes are shaded in gray. While I include the primary citation for the pertinent statute, additional citations and explanations are available from the American Bar Association (2013). 123 Table G. 2 : Summary of Expungement Statutes Yes No Specific States Does the state have automatic expungement? 14 37 Automatic states: AK, AR, FL, HI, MT, ND, NH, NM, NV, RI, TX, VA, VT, WV After expungement did the event ever occur? 15 36 States that do not specify event never occurred: AK, AL, AZ, DE, HI, MD, MN, MS, ND, NH, NJ, NY, OH, RI, SD Can an expunged record be used if the offender recidivates? 37 14 States where statutes do not mention that record can be reopened conditional on recidivism: AZ, CA, CT, IA, ID, IN , KY, MD, OR, RI, SC, UT, VA, WY Source: State statutes detailed in Table G.1. Note: This table is designed to show some of the variation in expungement statutes. The first row summarizes the states that have automatic expungement. The second row refers to states where after expungement the underlying criminal action is deemed to never have occurred by statute. The final row details if the record can be used against the juvenile if he or she commits a future crime. 124 G.2: Conceptual Framework This appen dix develops the c onceptual framework completely. Figure G.1: Game Tree and Payoffs Payoffs: No expungement 1. C 1 = 0, C 2 = 0 : 2. C 1 = 0, C 2 = 1 : 3. C 1 = 1, C 2 = 0 : 4. C 1 = 1, C 2 = 1 : Automatic expungement 1. C 1 = 0, C 2 = 0 : 2. C 1 = 0, C 2 = 1 : 3. C 1 = 1, C 2 = 0 : 4. C 1 = 1, C 2 = 1 : A B 125 I make the following assumptions in solving this game. The discount rate between the two periods is e qual to one. Because is a probability it must be between 0 and 1. For simplicity I assume and are uncorrelated with , so all individuals are committing crimes with the same payoff and have the same probability of being caught. I also assume t hat is large enough to impact behavior, so . Therefore, I must assume is between ½ and 1. The lower bound for ensures that the assumption above remains within the bounds of , and the upper bound ensures that one does not give up mo re than his entire salary if caught committing a crime. Lastly, must be sufficiently larger than , so I assume . I begin by solving the game in the world with no expungement. Using the payoffs above I can use backwards induction to determine how many people in the population will choose each action. Define the following three points (note that is the indifference point between payoffs 1 and 2 and is the indifference point between payoffs 3 and 4) : I can show that and in this world individuals with choose C 1 = 1, C 2 = 1, while individuals with choose C 1 = 0, C 2 = 0. Proof of : 126 To prove t he result of the game I use a number of cases: Case 1 : Suppose . Then the individual always chooses C 1 = 1, C 2 = 1. Proof by contradiction: Because , it is trivial to see the individual will always choose C 2 = 1. Suppose the individual chooses C 1 = 0. This implies: But I can show: 127 This implies , a contradiction. So the individual always chooses C 1 = 1, C 2 = 1. Case 2 : Suppose . Then the individual chooses C 1 = 1, C 2 = 1. Proof by contradiction. Because the individual will choose C 2 = 1 if at node A in the game tree, and the individual will choose C 2 = 0 if at node B in the game tree. Suppose the individual chooses C 1 = 0. This implies: a contradiction. So the individual always chooses C 1 = 1, C 2 = 1. Case 3 : Suppose . Then the individual chooses C 1 = 0, C 2 = 0. Proof by contradiction. Because the individual will choose C 2 = 1 if at node A in the game tree, and the individual will choose C 2 = 0 if at node B in the game tree. Suppose the individual chooses C 1 = 1. This implies: 128 a contradiction. So the individual always chooses C 1 = 0, C 2 = 0. Case 4 : Suppose . Then the individual will always choose C 1 = 0, C 2 = 0. Proof by contradiction: Because , it is trivial to see the i ndividual will always choose C 2 = 0. Suppose the individual chooses C 1 = 1. This implies : But I can show: Th is implies , a contradiction. So the individual always chooses C 1 = 0, C 2 = 0. Next I solve the game in the world with automatic expungement. Using the payoffs above, I can use backwards induction to determine how many people in the population will choose each action. Define the following points (note that , which is also defined above, is the indifference point between payoffs 1 and 2 and the indifference point between payoffs 3 and 4 in this world) : 129 I can show that in this world individuals with choose C 1 = 1, C 2 = 1, individuals with choose C 1 = 1, C 2 = 0, and individuals with choose C 1 = 0, C 2 = 0. Proof of : It is trivial to s ee that because . I prove the result of the game using a number of cases: Case 1 : Suppose . Then the individual always chooses C 1 = 1, C 2 = 1. Proof by contradiction: Because , it is trivial to see the indiv idual will always choose C 2 = 1. Suppose the individual chooses C 1 = 0. This implies: This i mplies , a contradiction. So, the individual always chooses C 1 = 1, C 2 = 1. Case 2 : Suppose . Then the individual chooses C 1 = 1, C 2 = 0. Proof by contradiction. Because , it is trivial to see the individual will always choose C 2 = 0. Suppose the individual chooses C 1 = 0. This implies: 130 a contradiction. So the individual always chooses C 1 = 1, C 2 = 0. Cas e 3 : Suppose . Then the individual chooses C 1 = 0, C 2 = 0. Proof by contradiction. Because , it is trivial to see the individual will always choose C 2 = 0. Suppose the individual chooses C 1 = 1. This implies: a contradiction. So the individual always chooses C 1 = 0, C 2 = 0. Finally, to be able to compare across these policy regimes, I prove that : 131 G.3: Data and Descriptive Statistics This appendix focuses on descriptive statistics across each of my data sources. Table G.3: All Expungement Data Application States Automatic States Year Michigan Washington Colorado Texas Florida Virginia 1997 . 1289 . . . 27116 1998 . 1327 . 123 . 27553 1999 . 1277 . 309 . 27789 2000 . 1366 . 517 . 26037 2001 . 1268 . 516 . 24308 2002 . 1355 . 754 7961 21874 2003 . 1393 158 805 9736 19331 2004 . 1309 149 810 10607 15215 2005 . 1350 182 1114 10860 13638 2006 . 1331 185 890 11416 10889 2007 . 1561 202 1560 12053 8164 2008 . 1736 146 1446 13497 5421 2009 29 1679 183 1697 14491 2470 2010 34 1158 191 2045 16945 360 2011 40 713 174 1776 17796 40 2012 48 416 246 2041 18272 36 2013 99 53 243 . 12947 21 Source: Michigan: Criminal Justice Information Center, Michigan State Police (juvenile set a sides) Washington: Washington Administrative Office of the Courts (expungement filing numbers) Colorado: Annual Reports of the Judicial Branch of the State of Colorado, Table 19 (expungement case numbers) Texas: Crime Records Service of the Department o f Public Safety (expungements) Florida: Florida Department of Law Enforcement (Certificates of Eligibility needed in the expungement process) Virginia: Virginia Department of Juvenile Justice (expungements) Note: The numbers reported for Texas and Flori da reflect the number of expungements by application despite the fact that these states are automatic. Many automatic states allow for expungement by application before the automatic expungement occurs. The numbers reported for Virginia represent all aut omatic expungements in the state. These numbers decrease in recent years because the date associated with the statistic is the date of intake (or date of arrest), meaning that many recent cases are not yet eligible for automatic expungement. State offici als from Florida and Virginia confirmed that the rate of expungement for those who are eligible is one. 132 Table G.4: NLSY Descriptive Statistics Overall (N=7,469) Mean Std. Dev . Female 0.490 0.500 Black 0.153 0.360 Hispanic 0.128 0.334 Urban (1997) 0. 685 0.465 Age (1997) 14.271 1.489 Live with both biological parents (1997) 0.534 0.499 Live with only biological mother (1997) 0.238 0.426 Household size (1997) 4.459 1.426 Total under 18 in household (1997) 2.367 1.190 Automatic State (1997) 0.200 0 .400 HS Grad 0.806 0.395 Ever Attended College 0.594 0.491 Graduated College 0.299 0.458 Juvenile Arrest 0.164 0.371 Juvenile Charge 0.101 0.302 Juvenile Conviction 0.054 0.226 Juvenile Incarceration 0.021 0.144 Age (2008 ) 25.830 1.452 Average Inc ome ( 1,000s ) (2008 - 2010) 29.000 21.252 Note: These statistics reflect responses from 7,469 respondents in the NLSY97 weighted by 1997 sampling weights (cumulative cases method). I drop 1,515 observations of individuals who missed at least one of the first five waves. I am unable to identify if these individuals had an arrest as a juvenile. Graduated college is an indicator of highest 133 Table G.5: Descriptive Statistics by Crime Applic ation (N=36) Automatic States (N=13) Mean St d . Error Mean St d . Error p - value (difference) Disorderly Conduct 199.338 27.411 169.367 42.171 0.569 Drug Crimes 184.935 18.101 163.759 15.856 0.508 Larceny 371.805 31.340 360.697 44.275 0.851 Bu rglary 76.388 5.628 65.804 7.648 0.316 Aggravated Assault 52.374 5.294 42.817 6.553 0.328 Robbery 27.197 4.434 17.620 4.590 0.232 Rape 3.933 0.393 3.982 0.581 0.948 Murder 0.966 0.106 0.659 0.123 0.116 Note: Th below the criminal age of majority. This analysis covers the years 2006 to 2010. Florida and Washington D.C. are excluded due to poor data quality. 134 G.4: State Data Sources I use a number of different data sources to provide important covariates throughout my analysis. I describe those sources and the particular data elements I use in this appendix. The primary source of data on crime and arrest s at the state level are the Uniform Crime Reports (UCR) published by the Federal Bureau of Investigation. I use the total level of reported crime by state over 2006 to 2010 as the denominator of my proxy variable for the unobserved juvenile justice envir onment. I also use data from the UCR to calculate a number of the crime covariates included in Table A.1, and I use arrest rate s in my state analysis in Table G.5, Table G.6, and Table G.7. Lastly, the UCR provides information on employed police officers and state expenditures on the justice system. I include these measures, scaled by population, as covariates in many analyses. Another source of justice data I use is count data on the number of prisoners in custody. The Census of Juveniles in Residenti al Placement provides the number of juveniles in state custody over time. I use the average number of juveniles in residential placement between 2006 and 2010 as the numerator of my proxy variable for the unobserved juvenile justice environment. 87 The Bur eau of Justice statistics collects similar data for counts of adult prisoners that I present in Table A.1. The last source of justice data I use is the National Juvenile Court Data Archive (NJCDA). I use published data from the NJCDA on state and county juvenile court case counts to determine the number of petitioned delinquency case counts by state and year. I present these data as the denominator of the calculated expungement rate in Table A.2. 87 Note that data are only collected in 2006, 2007, and 2010 for this time period. 135 Lastly, I use data from a number of different sources for the other background covariates I include in my analyses. For example, I use population by age measures from the Surveillance, Epidemiology, and End Results (SEER) Program to standardize many of the covariates. I use data from the U.S. Census Bureau to determine the demographic indicators I include in Table A.1. I also use data from the Bureau of Labor Statistics to calculate the unemployment rate and fraction of the population working in blue collar jobs. Data on the number of Head Start participants by state come from the Kids Count Data Center. 136 G.5 : State Level Analysis This appendix focuses on anal yses of expungement using state level data sources. Table G.6: State Level Juvenile Crime Regressions (1 ) Disorderly Conduct (2 ) Drug Offenses (3 ) La rceny (4 ) Burglary (5 ) Aggravated Assault (6) Robbery (7) Rape (8) Murder Automatic - 23.503 - 50.963 - 82.627 - 13.353 - 9.356 - 1.646 - 0.326 - 0.265 (61.311) (32.235) (54.022) (11.385) (9.049) (6.963) (0.813) (0.185) log(officers) - 68.189 - 110.911 - 409.032* - 66.195* - 20.939 - 27.905 - 2.236 - 0.720 (173.317) (91.124) (152.713) (32.183) (25.580) (19.683) (2.297) (0.523) log(expenditures) - 37.228 71.870 + 75.376 29.235 + 38.970** 21.765* 1.372 0.300 (79.805) (41.959) (70.317) (14.819) (11.778) (9.063) (1.058) (0.241) Unemp Rate - 23.557 - 23.488* - 52.746** - 0.397 - 1.671 - 0.805 - 0.428 - 0.055 (20.921) (10.999) (18.434) (3.885) (3.088) (2.376) (0.277) (0.063) Fraction Black 1.442 0.951 - 0.714 1.493* 0.952 1.233** - 0.001 0.042** (3.884) (2.042) (3.422) (0.721) (0.573) (0.441) (0.051) (0.012) Fraction Hispanic 0.010 0.008 - 0.002 0.007 0.005 - 0.015 - 0.009 0.025 + (0.012) (0.017) (0.010) (0.009) (0.010) (0.012) (0.011) (0.015) Fraction Urban 2.353 1.677 4.027 + 0.247 0.708 + 1.062** 0.040 0.003 (2.429) (1.277) ( 2.140) (0.451) (0.358) (0.276) (0.032) (0.007) Observations 49 49 49 49 49 49 49 49 Note: This analysis uses average juvenile arrest rates from 2006 to 2010 for the listed crime among 49 states. The District of C olumbia and Florida are excluded due to poor data quality. Officers and expenditures are expressed in per capita terms. The dependent variable is the juveni le arrest rate per 100,000 population. Standard errors appear in parentheses. + P < .10; * P < . 05; ** P < .01. 137 Table G.7: State Level Adult Crime Regressions (1 ) Disorderly Conduct (2 ) Drug Offenses (3 ) Larceny (4 ) Burglary (5 ) Aggravated Assault (6) Robbery (7) Rape (8) Murder Automatic - 14.697 - 21.452 + - 8.519 - 2.011 - 2.146 0.118 - 0.035 - 0.034 (12.466) (11.082) (8.960) (2.101) (4.375) (0.889) (0.206) (0.107) log(officers) 30.838 - 13.245 - 32.175 - 2.480 1.273 - 2.328 - 0.728 - 0.274 (35.240) (31.328) (25.328) (5.938) (12.368) (2.514) (0.581) (0.303) log(expenditures) 2.432 5.405 10.391 3.883 18 .287** 1.851 0.599* 0.036 (16.226) (14.425) (11.662) (2.734) (5.695) (1.158) (0.268) (0.140) Unemp Rate 0.376 - 1.150 - 0.700 1.296 + 2.002 0.617* - 0.029 0.031 (4.254) (3.782) (3.057) (0.717) (1.493) (0.304) (0.070) (0.037) Fraction Black - 0.460 2.172** 0.960 + 0.365** 0.344 0.184** 0.015 0.034** (0.790) (0.702) (0.568) (0.133) (0.277) (0.056) (0.013) (0.007) Fraction Hispanic - 0.457 1.394* 0.281 0.195 + 0.450 + 0.015 - 0.001 0.016** (0.667) (0.593) (0.480) (0.112) (0.234) (0.048) (0.011) (0.006) Fract ion Urban - 0.075 0.030 0.065 - 0.097 - 0.133 0.089* 0.003 - 0.005 (0.494) (0.439) (0.355) (0.083) (0.173) (0.035) (0.008) (0.004) Observations 49 49 49 49 49 49 49 49 Note: This analysis uses average adult arrest r ates from 2006 to 2010 for the listed crime among 49 states, where adult is defined as being above the age of criminal majority. The District of Columbia and Florida are excluded due to poor data quality. Officers and expenditures ar e expressed in per ca pita terms. The dependent variable is the adult arrest rate per 100,000 population. Standard errors appear in parentheses. + P < .10; * P < .05; ** P < .01. 138 G.6 : Robustness and Full Output This appendix focuses on robustness of the primary results and presenting an example of full output. Table G.8: Long - Term Effects of Automatic Expungement : Proxy Variable Analysis (Unweighted) (1 ) Not Arrested After Age 20? (2 ) Attended College (3 ) Graduated College (4 ) log( Average Income ) Juvenile Convict Sampl e (N=403) Automatic Expunge 0.101 + 0.068 0.041 0.317* (0.055) (0.056) (0.030) (0.141) R 2 0.106 0.144 0.206 0.177 Juvenile Arrest Sample (N=859) Automatic Expunge - 0.015 - 0.005 0.016 - 0.009 (0.032) (0.049) (0.024) (0.094) R 2 0.072 0.1 86 0.152 0.181 Never Arrested Sample (N=6188) Automatic Expunge 0.009 0.003 - 0.009 - 0.029 (0.013) (0.017) (0.017) (0.040) R 2 0.063 0.135 0.176 0.115 Note: Each panel restricts the sample to one of three catego ries: those who are never arrested as a juvenile, those who are arrested but not convicted, and those who are convicted. Standard errors are clustered at the state level. Average income is calculated over 2008 to 2010. Addit ional covariates are the same as column (2) in Table A.4. Nineteen observations are lost in this analysis because expenditures are unavailable for the Distri ct of Columbia. An example of the full regression output appears in Table G.12. + P<0.10, * P<0.05, ** P<0.01 139 Table G.9: Lon g - Term Effects of Automatic Expungement : Difference - in - Differences Analysis (Unweighted) (1 ) Not Arrested After Age 20? (2 ) Attended College (3 ) Graduated College (4 ) log( Average Income ) Treatment: Convicted Control: Arrested, Not Convicted Juven ile Convict x Automatic Expunge 0.113* 0.077 0.019 0.237 (0.043) (0.049) (0.040) (0.143) Juvenile Convict - 0.130** - 0.122** - 0.023* - 0.314** (0.037) (0.035) (0.010) (0.082) R 2 0.096 0.182 0.173 0.182 Treatment: Convicted Control: Never Arre sted Juvenile Convict x Automatic Expunge 0.056 0.074 + 0.044 0.216* (0.046) (0.039) (0.041) (0.103) Juvenile Convict - 0.268** - 0.322** - 0.159** - 0.497** (0.037) (0.018) (0.011) (0.079) R 2 0.100 0.170 0.192 0.130 Treatment: Arrested, No t Convicted Control: Never Arrested Juvenile Arrest x Automatic Expunge - 0.048 - 0.003 0.028 0.029 (0.030) (0.047) (0.026) (0.102) Juvenile Arrest - 0.136** - 0.221** - 0.141** - 0.255** (0.015) (0.028) (0.011) (0.050) R 2 0.091 0.174 0.197 0.133 Note: Each panel specifies the assumed treatment and control group for this difference - in - differences analysis. Standard errors are clustered at the state level. Average income is calculated over 2008 to 2010. Additional covariates are the same as column (2). Nineteen observations are lost in this analysis because expenditures are unavailable for the District of Columbia. An example of the full regression output appears in Table G.12. + P<0.10, * P<0.05, ** P<0.01 . 140 Tabl e G.10: Long - Term Effects of Automatic Expungement : Proxy Variable Analysis (Non - clustered) (1 ) Not Arrested After Age 20? (2 ) Attended College (3 ) Graduated College (4 ) log( Average Income ) Juvenile Convict Sample (N=403) Automatic Expunge 0.143 + 0 .077 0.051 0.253 (0.076) (0.070) (0.043) (0.176) R 2 0.094 0.153 0.238 0.184 Juvenile Arrest Sample (N=859) Automatic Expunge - 0.000 0.017 - 0.003 0.030 (0.054) (0.050) (0.031) (0.111) R 2 0.070 0.203 0.178 0.177 Never Arrested Sample (N=6188) Automatic Expunge 0.010 - 0.021 - 0.028 - 0.001 (0.016) (0.021) (0.019) (0.041) R 2 0.056 0.142 0.182 0.107 Note: Each panel restricts the sample to one of three categories: those who are never arrested as a ju venile, those who are arrested but not convicted, and those who are convicted. All regressions are weighted using 1997 sampling weights (cumulative cases method). Average income is ca lculated over 2008 to 2010. Additional covariates are the same as colu mn (2) in Table A.4. Nineteen observations are lost in this analysis because expenditures are unavailable for the District of Columbia. An example of the full regression output appears in Table G.12. + P<0.10, * P<0.05, ** P<0.01 . 141 Table G.11: Long - Ter m Effects of Automatic Expungement : Difference - in - Differences Analysis (Non - clustered) (1 ) Not Arrested After Age 20? (2 ) Attended College (3 ) Graduated College (4 ) log( Average Income ) Treatment: Convicted Control: Arrested, Not Convicted Juvenil e Convict x Automatic Expunge 0.153* 0.053 0.045 0.276 + (0.073) (0.067) (0.047) (0.152) Juvenile Convict - 0.133** - 0.108** - 0.027 - 0.320** (0.038) (0.034) (0.020) (0.089) R 2 0.087 0.198 0.205 0.178 Treatment: Convicted Control: Never Arrest ed Juvenile Convict x Automatic Expunge 0.120* 0.086 0.055 0.225 + (0.060) (0.057) (0.044) (0.126) Juvenile Convict - 0.279** - 0.316** - 0.177** - 0.473** (0.032) (0.028) (0.018) (0.075) R 2 0.094 0.176 0.198 0.124 Treatment: Arrested, Not Convicted Control: Never Arrested Juvenile Arrest x Automatic Expunge - 0.031 0.026 0.012 0.003 (0.043) (0.043) (0.030) (0.090) Juvenile Arrest - 0.145** - 0.226** - 0.155** - 0.236** (0.021) (0.021) (0.016) (0.050) R 2 0.086 0.182 0.205 0.126 So Note: Each panel specifies the assumed treatment and control group for this difference - in - differences analysis. All regressions are weighted using 1997 sampling weights (cumulative cases method). Average income is calculated over 2008 to 2010. Additional covariates are the same as column (2). Nineteen observations are lost in this analysis because expenditures are unavailable for the District of Columbia. An example of the full regressi on output appears in Table G.12. + P<0 .10, * P<0.05, ** P<0.01 . 142 Table G.12: Effect on College Attendance for Juvenile Convicts (Full Output) (1) Attended College 0.031* (0.012) 0.010 (0.007) Parental Income (1997) 0.017 (0.010) Age (1997) - 0.0 00 (0.017) Urban - 0.082 (0.056) Black - 0.025 (0.069) Hispanic - 0.025 (0.107) Female 0.093 + (0.048) Biological Mom 0.003 (0.061) Other Household Composition - 0.137 + (0.071) Household Size (1997) - 0.005 (0.036) Household Under 18 (199 7) - 0.034 (0.036) Automatic Expunge 0.077 (0.060) Unemployment Rate 3.392 (3.381) log(Officers) 0.010 (0.081) log(Expenditures) - 0.070 (0.107) log(Median Income) 0.333 (0.241) log(Head Start) 0.086 (0.075) Household Under 6 (1997) 0.06 3 + (0.036) Parental Income Missing - 0.028 (0.068) 0.094 143 (0.135) 0.349* (0.132) Custody Measure 11.342 (9.622) Sentencing Measure - 0.533 + (0.300) Imprisonment Rate 0.012 (0.016) N 403 R 2 0.153 Note: The dependent variable is an indicator for ever attending college. The regression is weighted using 1997 sampling weights (cumulative cases method). The reference group for househo ld composition is living with both biological parents. Household under 18 reflects the number of household members under 18 at the time of interview in 1997. Standard errors are clustered at the state level. + P<0.10, * P<0.05, ** P<0.01 . 144 APPENDIX H Appendices f Did Graduat ed Driver Licensing Laws Drive a Reduction i n Crime? 145 H.1: GDL Implementation In this appendix I list the effective dates of GDL implementation I use in my analysis. Table H.1: Effective Dates of GDL Implementation State Effecti ve date of three tiered law Alabama October 1, 2002 Alaska January 1, 2005 Arizona June 30, 2008 Arkansas July 1, 2002 California July 1, 1998 Colorado July 1, 1999 Connecticut October 1, 2005 Delaware July 1, 1999 District of Columbia January 1, 2001 Florida July 1, 1996 Georgia July 1, 1997 Hawaii January 9, 2006 Idaho January 1, 2001 Illinois January 1, 1998 Indiana January 1, 1999 Iowa January 1, 1999 Kansas January 1, 2010 Kentucky April 1, 2007 Louisiana January 1, 1998 Maine Augus t 11, 2000 Maryland July 1, 1999 Massachusetts November 4, 1998 Michigan April 1, 1997 Minnesota August 1, 2008 Mississippi July 1, 2000 Missouri January 1, 2001 Montana July 1, 2006 Nebraska January 1, 1999 Nevada July 1, 2001 New Hampshire Janu ary 1, 1998 New Jersey January 1, 2001 New Mexico January 1, 2000 New York September 1, 2003 North Carolina December 1, 1997 North Dakota January 1, 2012 Ohio January 1, 1999 Oklahoma November 1, 2005 Oregon March 1, 2000 Pennsylvania December 22, 1999 Rhode Island January 1, 1999 South Carolina July 1, 1998 South Dakota January 1, 1999 Tennessee July 1, 2001 Texas January 1, 2002 Utah July 1, 1999 Vermont July 1, 2000 Virginia July 1, 2001 Washington July 1, 2001 West Virginia January 1, 2001 Wisconsin July 1, 2000 Wyoming September 16, 2005 Source: Insurance Institute for Highway Safety (2013), Dee et al. (2005), Lexis - Nexis searches. 146 H.2: Traffic Fatalities In this appendix I present analyses focusing on GDL restrictions and traff ic fatalities. Table H.2: Descriptive Statistics, Traffic Fatalities Note: The unit of observation is state*year between 1992 and 201 0. Median household income is in 2011 dollars. Variables Mean Std. Dev. Outcome Variables Pre - GDL: All Teenage Death 50.86 44.304 Pre - GDL: All Death with a Teenage Driver 62.09 54.560 Pre - GDL: All Teenage Driver Death 22.72 19.196 Covariates Speed Limit - 65 0.49 0.493 Speed Limit - 70+ 0.47 0.493 Seat Belt (Primary Enforcement ) 0.32 0.465 Seat Belt (Secondary Enforcement ) 0.64 0.475 B lood A lcohol C oncentration 0.08 0.57 0.485 Blood Al cohol Concentration 0.10 0.40 0.479 Admin License Revocation 0.86 0.349 Percent Black 0.12 0.117 Percent Less Than 15 Years Old 0.21 0.019 Percent 15 - 19 Years Old 0.07 0.006 Percent 20 - 24 Years Old 0.07 0.007 Percent 25 - 44 Years Old 0.29 0.026 Perce nt 45 - 64 Years Old 0.18 0.020 Percent 65 or Older 0.18 0.023 Percent Urban 0.72 0.150 Unemployment Rate 0.05 0.018 Med Household Income (thousands) 52.05 8.146 Zero Tolerance 0.86 0.339 1 47 Table H.3: Extension of Previous Results on GDL and Fatalities Specification (1) Dee et al. (2005) (2 ) Replication (3 ) Additional Years of Data (4) All Death Teen Driver (5 ) Teenage Driver Death Years 1992 - 2002 1992 - 2002 1992 - 2010 1992 - 2010 1992 - 2010 Dependent Variable All Teen Fatalities All Teen Fatalities All Teen Fatalities All Deaths with Teen Driver Teen Driver Fatalities GDL - 0.056* - 0.060* - 0.064** - 0.064** - 0.051 + (0.026) (0.026) (0.023) (0. 024) (0.030) Observations 528 528 912 912 912 Note: All regressions use conditional maximum likelihood of the Negative Binomial distribution and include binary indicators for the following driving policies: primary e nforcement of seat belt laws, secondary enforcement of seat belt laws, speed limit 65 miles per hour, speed limit 70 or more miles per hour, legal blood alcohol concentration of 0.08, legal blood alcohol concentration of 0.10, administrative license revoca tion law, and zero tolerance law. Regressions also include state and year fixed effects. The unit of observation is state*year. Standard errors (in parentheses) are adjusted for clus tering at the state level. Column (1) presents the preferred speci fica tion in Dee et al. (2005). + P<0.10, * P<0.05, ** P<0.01 . 148 APPENDIX I Appendices f o Interstate Differences i n Pension Vesting R ules, K - 12 Teacher Experience, a nd Teacher Exit 149 I.1: NLSY Data In this appendix we discuss the panel of teachers we use fr om the NLSY. To identify teachers we look at industry and occupation codes across all reported job lines in all years: we label on any job line within any year. Next, we build a balanced panel for those who report being a teacher between 2002 and 2010 (age falls between 18 and 31) using the responses from these teachers. Using their recall in the interviews, where they provide th eir employment status by week, we fill in the panel with the time they report working as a teacher. We calculate the number of weeks worked as a teacher in the calendar year as well as the number of weeks worked in the fall. We also separately calculate the total number of weeks worked in each school year (school year is defined between week 32 of one year and week 32 of the next year sometime around August 1). In the event of multiple employers within the same year, we choose the employer for the year w ith the most weeks worked . In the event that someone spent the same amount of time with two employers, we assume their employer for the year is the employer where they began working first. We use state of residence to determine pension parameters for the teacher, implying that state of residence is the same as state of employment. It is not possible to determine state of employment or any specific information about the employer other than a numerical identifier in the NLSY Geocode Data. In addition, if s tate of residence is missing in any given year but available in years before and after the missing observation, we assume the state of residence has not changed if state of residence is constant for the adjacent non - missing observations. If there is any d iscrepancy between the non - missing observations we keep state of residence missing. 150 The hazard of first exit from teaching goes from missing to zero once a teacher begins working -- we consider a teacher to have worked if they report working at least 12 week s in the school year. Once they exit teaching for the first time the variable becomes one for the remainder of the panel. If they change employers but do not exit teaching the binary variable remains equal to zero . This happens in 262 individual by year observations, roughly 3.7 percent of our observations. We merge a number of covariates with these data. The covariates include marital status, number of biological or unrelated children in the household, gender, age, race, ethnicity, ability score, censu s region, and family income. We generate indicators for female, black, Hispanic, and mixed race. We also generate indicators for married, single, and separated/divorced. To create these indicators we aggregated the number of months in each year that an individual reported being married, single, and separated/divorced. We consider them married for that year if they spent six or more months married. We consider them single or separated/divorced for the year if they spent more than six months single or se parated/divorced. Next, we add the specifics of the pension system using data from 2001 to 2011 in the Public Fund Survey. We supplement/update these data using NCTQ documents, National Education Association (2010) , and our own research into plan handbook s. We merge the fiscal year of the plan onto the same year in the NLSY data. 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