1 Heavy Alcohol Use and Crime: Evidence from Underage Drunk Driving Laws Christopher Carpenter Assistant Professor of Economics/Public Policy UC Irvine Graduate School of Management This paper provides new evidence on the causal relationship between heavy episodic alcohol use and crime by using variation induced by adoption of very strict underage drunk driving laws. Carpenter (2004) shows that these Zero Tolerance (ZT) laws significantly reduced binge drinking (5 or more drinks at one sitting) by males age 18-20, with no effect for slightly older males age I use age-specific arrest data for police agencies in MSAs to estimate the effect of ZT laws on crime, controlling for both year and police-agency fixed effects. I find that ZT laws which lowered the BAC threshold at which underage youth are deemed to be driving under the influence significantly increased the fraction of adult male DUI arrests attributable to year olds. I also find that ZT laws decreased the fraction of nuisance crime and property crime arrests attributable to year olds by about 3-4 percent, with no effects on violent crime. These results are validated by important null findings: ZT laws did not affect arrests in any crime category for slightly older males age In fact, the estimated reductions in property crime by single year of age exhibit a discontinuity around the predicted age threshold. These results suggest that heavy episodic alcohol use does cause the commission of property crime. Though the overall magnitude of the property crime reduction from ZT laws is small, the implied economic savings (i.e. the dollar value of goods damaged or stolen) equals $150 million annually. I thank Alan Auerbach, Ken Chay, Phil Cook, Isaac Ehrlich, Bill Evans, Justin McCrary, Heather Royer, Emmanuel Saez, and seminar participants at UC Berkeley, Washington University School of Social Work, Emory University, RAND, UC Irvine Graduate School of Management, UC San Diego, Simon Fraser University, University of Virginia, UC Riverside, SAMHSA, Mathematica, Yale School of Public Health, University of Michigan School of Public Health, and the annual Robert Wood Johnson research meetings for very helpful comments. Feng Pan and Tracy Finlayson provided helpful research assistance. I am particularly grateful to Officer Rob Schneider of the Ann Arbor Police Department for answering many questions. This project was generously supported by the Robert Wood Johnson Foundation, though results do not imply their endorsement. All errors and omissions are my own.
2 Heavy Alcohol Use and Crime p. 1 INTRODUCTION There is extensive evidence documenting a strong relationship between alcohol use and crime. The Bureau of Justice Statistics (BJS) reports that over a third of convicted offenders in 1996 were drinking at the time of their offense (1998). Data on victims perceptions indicate that almost 3 million violent crimes occur each year in which victims are certain that the offender had been drinking (BJS, 1998). Finally, some crimes such as driving under the influence (DUI) are explicitly linked to alcohol use. The evidence is less clear, however, that heavy alcohol use causes individuals to commit crime, for example by increasing aggression, lowering inhibition, or altering one s perceptions of acceptable behavior. Indeed, it could be that some unobserved third factor such as risk preference causes individuals both to consume alcohol and to commit crime. Alternatively, individuals who plan to commit crime might drink alcohol in order to get up the nerve. In each of these latter cases one might observe a positive relationship between alcohol use and crime that does not reflect a true causal role for alcohol use. A key difficulty in identifying a compelling research design that would credibly estimate the causal effect of alcohol use on crime is finding a mechanism that generates arguably exogenous variation in alcohol consumption. A handful of previous studies have used state variation in beer and alcohol taxes to estimate crime effects, with most of these papers finding that higher beer taxes are associated with significantly lower rates of several types of crime and self-reports of violent behavior. There are, however, a number of limitations to using state beer taxes in this context, including: disagreement in the economics literature as to the existence and robustness of an inverse relationship between
3 Heavy Alcohol Use and Crime p. 2 beer taxes and alcohol consumption (Dee 1999 and others); questions about whether such tax changes meet the requirements for natural experiments (Kubik and Moran 2001); and the lack of a credible within-state control group for identifying beer tax effects. In this paper, I use adoption of tougher drunk driving laws aimed at youth under age 21 to estimate the effect of heavy episodic alcohol use on crime. These Zero Tolerance (ZT) laws were enacted by every state over the past two decades and substantially lowered the legal blood alcohol content (BAC) limit for underage drivers. Specifically, underage youth in the pre-zt regime were subject to the same BAC threshold as adults over age 21 generally in the range After ZT laws were put into effect, this legal limit for youth fell to.00,.01, or.02, depending on the state. ZT laws require states to revoke the license of any underage driver whose BAC exceeds the new lower legal limit. Research indicates these drunk driving laws generated very sharp differences in heavy alcohol use for individuals very close in age. Carpenter (2003, forthcoming) shows that ZT laws reduced the likelihood of binge drinking behavior five or more drinks at one sitting by about 13 percent among young males age 18-20, with no effects for slightly older youth age In the context of identifying effects of alcohol use on crime, ZT laws are particularly attractive because 1) adoption of tougher drunk driving policies is arguably uncorrelated with omitted determinants of crime; 2) there is substantial variation across states in the timing of policy adoption; and 3) the laws create sharp predictions about which age groups should have been affected. To examine whether ZT laws reduced crime committed by underage individuals, I use data on male arrests by single year of age for police agencies in Metropolitan
4 Heavy Alcohol Use and Crime p. 3 Statistical Areas (MSAs) from the FBI Uniform Crime Reports for the period (Chilton and Weber 2000). I estimate reduced form models of the effect of ZT laws on the proportion of adult male arrests attributable to (22-24) year olds, controlling for other state alcohol restrictions, state demographics, and macroeconomic conditions. The models also include police agency and year fixed effects; as such, ZT effects are estimated from within-agency deviations in age-specific crime coincident with the timing of ZT adoption. To preview, I find that ZT laws changed the age structure of DUI arrests within police agencies: the proportion of adult male arrests attributable to year old males (but not year old males) rose significantly in conjunction with ZT implementation. Since ZT laws substantially lowered the threshold at which year old impaired drivers were liable for arrest for driving under the influence, this result is not surprising and suggests that ZT laws were actively enforced. Moreover, these DUI arrest increases were most salient in states where virtually the entire population drives (as opposed to using public transportation). I also find that ZT laws and by implication reductions in heavy alcohol use reduced the fraction of public drunkenness and disorderly conduct arrests attributable to year olds (but not year olds), and the same pattern holds for vandalism. With respect to the major types of crime, I find strong evidence that ZT laws were associated with significant decreases in property crimes attributable to young men in the targeted age group, age 18-20, on the order of 3.4 percent. The property crime reductions are validated by an important null finding: ZT laws had no statistically or economically significant effect on property crime arrests for slightly older males age I find no
5 Heavy Alcohol Use and Crime p. 4 economically or statistically significant effects for violent crime for either age group. Finally, I show that observable measures of enforcement (per capita police and police expenditure) were not responsive to adoption of ZT laws, suggesting the property and nuisance crime reductions are real. I interpret the results as evidence in favor of a causal role for heavy episodic alcohol use on the commission of nuisance and property crime. This research is important for several reasons. First, I focus on a group of young men who are disproportionately represented in the criminal justice system: year old males account for 15 (30) percent of all (adult) male arrests for property crime in MSAs (see Figure 1). Understanding the causal determinants of crime among these youths may therefore be particularly useful in crafting effective crime policy. 1 Second, this paper employs a new policy tool tough drunk driving laws for detecting the effect of heavy alcohol use on crime. Most previous studies have used state excise taxes on beer which have limitations in the context of youth alcohol consumption. Third, this paper examines the relationship between alcohol and crime in the presence of both year and police agency fixed effects which unambiguously purge the ZT estimates from secular year effects and time-invariant unobserved agency-level heterogeneity, respectively. This two-way fixed effects model has become the standard framework in the economics and policy evaluation literature but has generally not been used in research on alcohol and crime. Fourth, these results help isolate the specific types of alcohol use in this case heavy episodic drinking that are causally related to criminal activity in this context. Understanding whether drinking participation or heavy episodic drinking (or both) is the core determinant of 1 I am aware of only two published papers (Joksch and Jones 1993 and Saffer 2001) that specifically examine the relationship between alcohol use and crime among young adults. Markowitz (2001) considers high school students, but focuses on weapon carrying and self-reported violence as opposed to crime.
6 Heavy Alcohol Use and Crime p. 5 criminal behavior is key for design of effective public policy. Finally, the results suggest that failure to consider the unintended positive externalities associated with these laws may lead to inefficient under provision of this type of alcohol control. The paper proceeds as follows: Section I briefly reviews the relevant economics literature on alcohol use and crime. Section II describes the data and empirical approach, and Section III presents the results. Section IV offers a discussion, and Section V concludes. I. PREVIOUS LITERATURE: ALCOHOL AND CRIME The economics literature attempting to disentangle the causal relationships between alcohol and crime has used different sets of policy experiments to address the potential endogeneity of alcohol use and criminal behavior. Miron (1999) considers state and federal prohibitions on alcohol use over the past century and finds that alcohol prohibition substantially raised the homicide rate in the United States, consistent with the idea that prohibition created violent black markets. Joksch and Jones (1993) use variation in alcohol availability induced by increases in states Minimum Legal Drinking Age (MLDA) in the 1980s and find that higher MLDAs were associated with a lower incidence of vandalism and disorderly conduct (on the order of 10 percent) among the treated age groups relative to those unaffected by the more restrictive alcohol policy. 2 Most of the papers in the alcohol and crime literature, however, have focused on the money price of alcohol usually the state excise tax on beer as the key variable of Similarly, Grossman and Markowitz (2001) focus on the link between alcohol use and behavioral problems such as fighting among college students. 2 There is substantial evidence that movements toward higher MLDAs were associated with sharp reductions in alcohol use by individuals in the targeted age groups. See, for example, Dee (1999).
7 Heavy Alcohol Use and Crime p. 6 interest. Studies using individual-level data have found that beer taxes are negatively related to self-reports of child abuse committed by mothers (Markowitz and Grossman 2000a) and wife abuse committed by husbands (Markowitz and Grossman 2000b). Markowitz (2001) uses alcohol taxes in an instrumental variables framework and finds that drinking and binge behavior both increase the likelihood that a student reports he engaged in physical violence. Finally, Saffer (2001) uses data on individuals age 12 and older from the 1991 cross section of the National Household Survey on Drug Abuse and finds that beer taxes reduce the likelihood of self-reported arrest, property crime, and property damage. Studies using aggregate level FBI data have also used variation in the level of the state beer tax to estimate reduced form models of crime. Cook and Moore (1993) find that higher beer taxes reduce arrests for robbery and rape, with no effect on assault or homicide. 3 II. RESEARCH DESIGN AND DATA DESCRIPTION In this paper I make use of a set of drunk driving laws aimed at underage individuals that have been adopted at different times by all 50 states. These Zero Tolerance (ZT) laws were motivated by the fact that the nationwide MLDA is 21. As such, it may be 3 This class of papers using variation in beer excise taxes (either across states at a point in time or within states over time) has generally not focused on the effects for crime committed by youths and young adults. One notable exception is Saffer (2001), as mentioned above. Because that study only included one cross section, however, it could not address sensitivity of the estimates to inclusion of state fixed effects. Indeed, this issue has become a source of debate in the economics literature, as some economists have called into question the existence of a robust first stage relationship between beer taxes and alcohol consumption among youth. Dee (1999), for example, used Monitoring the Future (MTF) data to show that the strong negative relationship between teen drinking patterns and state beer taxes becomes small and statistically insignificant once controls for unrestricted state and year fixed effects are included. Others have similarly argued that beer taxes are not robust in this context (see, for example, DiNardo and Lemieux 2001, Young and Likens 2000, and Mast, Benson, and Rasmussen 1999). There is, however, a very large literature that finds large and statistically important reductions in heavy drinking associated with beer taxes, some of which do include controls for state fixed effects (see, for example, Cook and Tauschen 1982, Cook and
8 Heavy Alcohol Use and Crime p. 7 reasonable to expect that any driver under age 21 should not have measurable amounts of alcohol in his blood. Indeed, these laws require states to suspend the license of any underage driver who has a blood alcohol content (BAC) above.02 or.00, depending on the state. Maine was the first state to enact such a law in 1983, and all states adopted ZT laws by July of The 1995 National Highway Systems Designation Act threatened states with the loss of federal highway funding if they did not adopt a ZT law. Several published studies have shown these laws to have been effective at reducing underage highway fatalities likely to have involved alcohol. 4 Carpenter (2003a) shows that one way these laws worked was to moderate heavy alcohol use among underage males age by about 13 percent, with no effect for slightly older males age This research design exploits two key observations: (1) ZT laws are robust policy levers with respect to heavy episodic drinking among young males; and (2) adoption of these tougher drunk driving laws is arguably unrelated to omitted determinants of agespecific crime. While offenses such as driving under the influence (DUI) and vehicular homicide are clearly policy targets of drunk driving laws, the same is not true of other types of crimes. Indeed, qualitative evidence overwhelmingly indicates that traffic fatality reductions and highway safety were the key reasons states passed ZT laws. Reductions in, say, rape or larceny were not arguments heard in the debates over enacting these policies. 5 Furthermore, as noted above states were compelled to adopt these Moore 1994, Coate and Grossman 1988, Cook and Moore 2001, and others). In this paper, I explicitly focus attention on Zero Tolerance laws. 4 These papers range from descriptive comparisons of states with and without ZT laws to more sophisticated policy analyses that include state and year fixed effects and a variety of state level demographic and economic controls. Estimates in the literature range from 6-17% reductions in highway fatalities attributable to ZT laws. See, for example, Eisenberg (2003). 5 It is, of course, entirely plausible that adoption of ZT laws is correlated with changes in police enforcement and aggressiveness in reducing all types of crime following ZT adoption. It is likely, however, that these biases would affect both crime committed by both year olds and year olds
9 Heavy Alcohol Use and Crime p. 8 policies under federal mandate. As such, these drunk driving laws may be plausibly exogenous with respect to crime rates other than DUI. 6 To estimate the effect of ZT laws on crime, I use data on arrests by single year of age for police agencies in Metropolitan Statistical Areas (MSAs) from the FBI Uniform Crime Reports. 7 These administrative data cover agencies in MSAs and span the time period ( ) over which most ZT laws were adopted by states. 8 The data were compiled and cleaned by two criminologists and include counts of arrests for 43 major types of crime (Chilton and Weber, 2000). 9 I aggregate offenses into different groups standard in the criminology literature, focusing on violent crimes (murder, rape, robbery, and aggravated assault) and property crimes (burglary, larceny, and motor vehicle theft). I also consider the offense most since it is difficult to differentiate a priori between individuals in these age groups. As such, differences in crime associated with ZT adoption by age-based treatment and control groups should reflect true ZT effects. 6 Beer taxes are arguably more susceptible to endogeneity concerns such as those highlighted by Kubik and Moran (2001). If, for example, states earmark funds raised by beer tax increases for funding crime reduction programs, this could contribute to a negative relationship between beer taxes and crime rates. 7 Existing individual level data sources are inadequate for the current purposes. The NLSY does ask about lifetime criminal history in the 1980 survey, but these young men came of age too soon relative to ZT adoption. The National Criminal Victimization Surveys (NCVS) offer repeated cross sections at the individual level on self-reports of criminal victimization, but state identifiers are not available. Another source of individual level data on crime is now being collected by the FBI through an effort called NIBRS, the National Incident Based Reporting System. However, states only began collecting this data in the past half decade, and the first few years contain only a handful of states. The National Household Survey of Drug Abuse (NHSDA) contains information on self-reports of criminal activity for year olds but state identifiers are not available. Similarly, data on juvenile crime (those age 17 or younger) from the FBI is not rich enough to answer the current question. One reason is that the juvenile justice system carries very different procedures, incentives, and sanctions than the adult corrections system (Levitt 1998). Also, data on juvenile crime and custody rates is much less complete than the associated data for adults. 8 The Chilton and Weber crime files do not contain information on arrests by single year of age for agencies outside MSAs, in part because arrests of males in this tight age group in more rural areas are extremely rare for certain types of crime. Police agencies in MSAs are also more likely to report reliable arrest counts throughout the panel. The police agency is the lowest level at which one can obtain arrest data by single year of age. Previous research and reports by the Bureau of Justice Statistics highlight numerous problems related to missing data and imputation associated with the fact that police agencies are not required by law to report arrest counts to the FBI (BJS 1999). A key problem is that the imputation scheme for agencies reporting fewer than 12 months of data changed in 1994, right in the middle of the analysis period. 9 Previous studies have also used the Chilton and Weber arrest files. See, for example, Harris et. al
10 Heavy Alcohol Use and Crime p. 9 likely to be affected by the law changes: driving under the influence. Finally, to provide a point of comparison with previous studies, I consider arrests for public drunkenness, disorderly conduct, and vandalism. As is common the criminology literature, I use all observations where the police agency reported arrest data for at least a six month period, and I inflate arrest counts by relevant factors for those agencies who reported less than twelve months of data. To capture the age-specific nature of ZT laws, I create a dependent variable that similarly reflects the age structure of crime within a police agency. Specifically, I construct an age-specific arrest ratio, R pt, by dividing the number of arrests of (22-24) year old males by the total number of arrests of adult males in a police agency. This class of dependent variable has been used previously by both economists and criminologists (see, for example, Joksch and Jones 1993 and Conlin, Dickert-Conlin, and Pepper 2002). 10 The benchmark model for estimating the reduced form effect of ZT laws is given by: (1) R pt = β 0 + β 1 Z st + β 2 (Zero Tolerance) st + β 3 P + β 4 T + ε st where R pt is the age-specific arrest ratio for agency p in year t, as described above. I estimate separate regressions for males in each age group for DUI, public drunkenness and disorderly conduct, vandalism, property crime, and violent crime. Z is a vector of state variables that may be correlated with the key variables of interest or that have been shown in previous work to be empirically important determinants of crime. These 10 This arrest ratio also has the advantage that it avoids the problem of questionable reliability of population counts by single year of age at either the state or MSA level. It also has drawbacks, however. For example, by including year olds in the denominator, one would expect an upward bias for the estimated effect of ZT laws on the year old arrest ratio (if ZT laws truly reduce crime committed by year olds). Table 10 shows that the key results are robust to using arrests of all adults 25 years old and older as an alternative denominator.
11 Heavy Alcohol Use and Crime p. 10 include: the real value of the federal and state excise tax on beer (in 2001 dollars), fraction of population age 15-19, fraction black, share of population below the federal poverty level, per capita income (in 2001 dollars), a variable indicating the Minimum Legal Drinking Age is 21, and the presence of each of three drunk driving policies aimed at adults. 11 Zero Tolerance is a variable that equals the fraction of the year for which the state ZT policy is in place, and the coefficient of interest, β 2, captures the effects of the ZT policies on crime. Dummy variables for each police agency control for time-invariant agency-specific factors and are captured by P. Dummy variables for each survey year control for period-specific shocks common to all police agencies in any given year and are captured by T. All regressions are weighted by the population reported by the police agency, and standard errors are clustered at the state level. The intuition in this paper is straightforward: a causal role for alcohol use in crime should be characterized by a reduction in arrests when ZT laws are adopted. Moreover, these reductions should be age-specific, since the changes in alcohol use associated with ZT laws were themselves age-specific. Therefore, if alcohol use causes crime, then one should observe reductions in the year old arrest ratio, but not the year old arrest ratio. Put differently, the year old males provide an important counterfactual for what would have happened to the criminal activity of year olds in the absence 11 Information on drunk driving and drinking age policies comes from various years of the Digest of State Alcohol Related Legislation, as well as from personal correspondence with the National Highway Transportation and Safety Administration (NHTSA). The number of states that adopted ZT laws is in Appendix Table 1. Data on beer taxes come from various years of the Brewer s Almanac. State unemployment rates come from BLS published statistics. I use the Statistical Abstract of the United States, various years, to obtain per capita income (transformed to 2001 dollars), percent of the state population below the federal poverty level, the share of the population that is black, and the share of the population age Means for key variables used in the analysis are reported in Table 2. The adult drunk driving policies are discussed at length elsewhere (see, for example, Dee 2001) and include lower legal limits for adults (at.08 blood alcohol content and.10 blood alcohol content) and administrative license revocation
12 Heavy Alcohol Use and Crime p. 11 of ZT policies (and, by implication, heavy alcohol use). As such, arrests of year olds account for contemporaneous changes in criminality that may be spuriously associated with ZT laws but that are not due to the reductions in heavy alcohol use. III. MAIN RESULTS Descriptive statistics on the age-specific arrest ratios in the pre-zt period for the various types of crime considered in this paper are provided in Table 2. I note that the fraction of crime attributable to year olds is larger than that attributable to year olds for every type of crime considered, except for DUI. Moreover, the level of the year old arrest ratio indicates that young men in this tight age range are responsible for a disproportionately large share of arrests for different types of crime, particularly property crime. These results that the age-crime profile peaks at about age 18 have been noted previously by other researchers (e.g. Donohue and Levitt 2002). I begin by presenting evidence of the effect of ZT laws on the age composition of DUI arrests. Figure 2 depicts the graphical relationships between theoretical BAC levels and DUI arrests before and after ZT laws, showing both the old level applicable to adults and youth in the pre-zt regime, as well as the new lower level applicable to youth once ZT laws are passed. Given some BAC level at which individuals exhibit driving impairment (and are thus pulled over by police), Figure 2 illustrates why DUI arrests of underage youth should increase with ZT laws. Underage drivers in the pre-zt regime who were impaired (and thus pulled over by the police) but below the state s legal limit for adults (Group 2) were generally not subject to a DUI arrest; in the post-zt regime, laws. Carpenter (2003a) showed these laws not to be important predictors of youth alcohol consumption. They are also not systematically related to youth arrests. I include them here for completeness only.
13 Heavy Alcohol Use and Crime p. 12 these same drivers (Group 5) would be in violation of DUI law. 12 Therefore, if there were no change in drinking patterns associated with policy adoption, ZT laws should by construction increase the year old arrest ratio for driving under the influence (DUI). Moreover, as long as the behavioral consumption response was not complete (i.e. as long as it is not true that all underage drivers in Groups 1 and 2 moved to groups 6 and 7 in the post-zt regime), one should still expect an increase in DUI arrests for year olds. Put differently, an increase in DUI arrests for year old males associated with ZT adoption indicates that the laws were being actively enforced (i.e. they were not simply on the books ). Indeed, Table 2 indicates an important finding that ZT laws had a positive, significant, and direct effect on arrests of year olds for driving under the influence (DUI), even after controlling for all the variables described above, including police agency and year fixed effects. This suggests that another way ZT laws reduced fatalities was by removing dangerous underage drivers from the nation s highways. 13 Relative to its pre-reform mean, the top panel of Table 2 suggests that ZT laws reduced the DUI arrest ratio over the decade by about 5 percent. I find no significant effect of ZT laws on the year old arrest ratio for DUI. For completeness and comparison to the previous literature, I also report the effect of the (log of the) real value of the state and federal beer tax in 2001 dollars. I find no beer tax effects on either DUI arrest ratio. 12 Note that it is likely that underage drivers who had driven above the state s legal limit for adults in the pre-zt regime (Group 1) would be unlikely to significantly reduce alcohol consumption after ZT laws are passed (i.e. move to Groups 6 or 7) since their behavior in the pre-zt regime reveals non-responsiveness to DUI law. 13 Note that this result need not imply increased enforcement or police activity. Indeed, it is unlikely that police officers can visually differentiate between 20 and 22 year olds when they decide to pull over an impaired driver. Later I show that ZT laws appear unrelated to observable measures of police enforcement.
14 Heavy Alcohol Use and Crime p. 13 Table 3 explores these DUI effects further by exploiting variation across MSAs in the extent of public transportation. The intuition is that policies imposing harsher sanctions on drunk driving should be relatively unimportant in areas with extensive public transportation systems (e.g. New York City and Washington DC) compared to similarly sized cities where essentially everyone drives (e.g. Detroit). While the degree of mass transit is almost surely not randomly assigned in the population, it provides a useful descriptive margin for identifying patterns that one should observe in the presence of a true ZT effect. To implement this strategy, I separate MSAs by the fraction of the working age population that reported using public transportation as a means to get to work in the 2000 Census. 14 I then performed OLS estimation of equation (1) separately on each of three groups: areas with relatively low (<2%), medium (2-6%), and high (>6%) rates of public transit use. 15 Indeed, the top row of Table 3 reports the fraction of adult male arrests of year olds for DUI, property crime, and violent crime that are for DUI and reflects the expected pattern: DUI arrests as a fraction of the total are decreasing in public transit use, as expected. Table 3 reveals that the DUI arrest increases associated with ZT laws of year olds also follow the predicted pattern: areas with the lowest rates of public transit exhibited the largest and strongest responsiveness of year old DUI arrests to ZT laws. Specifically, the DUI arrest rate for these high-driving areas increased by about ten percent relative to its pre-reform mean: this is about twice the size of the effect in the full 14 A small fraction of police agencies in the Chilton and Weber crime files could not be matched to public transit measures. These observations were dropped from the analysis in Table The overall pattern of DUI arrests is robust to reasonable alternative choices of these thresholds.
15 Heavy Alcohol Use and Crime p. 14 sample (Table 2). 16 In contrast, areas with more developed mass transit had smaller and statistically insignificant ZT induced increases. 17 While crimes such as DUI are explicitly linked to alcohol use, there are other sets of crimes that are commonly thought to be associated with alcohol use in less direct ways. Often termed nuisance crimes, these offenses are generally characterized by large social costs relative to direct economic costs. I use anecdotal evidence that when arresting individuals for the negative effects of heavy alcohol consumption, police officers typically choose either public drunkenness or disorderly conduct. Considering arrests for these two crime categories, I find in the top panel of Table 4 that ZT laws reduced year old arrest ratio for these two crimes on the order of 5 percent relative to its pre-reform mean. Notably, the year old arrest ratio for these crimes was unaffected by ZT laws, and neither ratio is significantly responsive to state beer taxes. This is consistent with the idea that ZT laws moderated heavy alcohol use by year old males but not year old males. The bottom panel of Table 4 considers the reduced form effect of ZT laws on the nuisance crime of vandalism. I consider vandalism separately because previous research suggests that increases in the MLDA induced large reductions in vandalism arrests (Joksch and Jones 1993). The results in Table 4 are consistent with the effects found by previous studies and suggest that ZT laws reduced the year old arrest ratio for 16 Estimates for year olds in this DUI exercise by the degree of public transit revealed no statistically significant ZT effects. 17 This overall pattern remains if one considers an alternative dependent variable capturing the fraction of year old male arrests for DUI, property and violent crime that are attributable to DUI. That is, low public transit areas saw relatively more important increases in this alternative arrest ratio than did high public transit areas.
16 Heavy Alcohol Use and Crime p. 15 vandalism by about 4.5 percent relative to the pre-reform mean. 18 Again, there are no ZT effects for year olds, and there are no beer tax effects for either model. Table 5 presents the key crime results of interest and focuses on the two major classifications considered by economists and criminologists: violent and property crimes. The top panel of Table 5 provides no evidence that ZT laws and by implication reductions in heavy alcohol use reduced violent crimes (murder, rape, robbery, and aggravated assault) committed by young men in the targeted age group. The coefficient estimate, while negative, is not statistically significant and very small in magnitude (suggesting an effect of.2% relative to the pre-reform mean of the year old violent crime arrest ratio). In fact, the 95% confidence interval for the ZT coefficient is such that it excludes reductions larger than about 5.2 percent of the associated pre-reform mean. The lower panel of Table 5, in contrast, provides evidence that ZT laws were effective at reducing the fraction of adult male property crime arrests attributable to year olds, the targeted group. Specifically, I estimate that ZT laws significantly reduced the year old property crime arrest ratio by 3.4 percent relative to its prereform mean, controlling for police agency and year fixed effects, other alcohol control policies, and state demographic controls. Both the property and violent crime models are validated by an important null finding for year old males, whose alcohol consumption behavior was unaffected by the tougher ZT laws: the ZT effects for this slightly older age group are small and statistically indistinguishable from zero. 18 Appendix Table 2 provides replication of the qualitative results in Joksch and Jones (1993) that changes in the MLDA over the period reduced vandalism and disorderly conduct arrests of year olds. While their empirical approach and data differ slightly from those considered here, I am able to reproduce their main result that nationwide increases in the MLDA (to age 21) were associated with significant reductions in both vandalism and disorderly conduct. Specifically, the estimates in Appendix Table 2 indicate that, relative to the pre-reform mean of the year old arrest ratio, an MLDA of 21
17 Heavy Alcohol Use and Crime p. 16 There are a handful of other estimates in Table 5 that merit mention. First, the reduced form models explain a large fraction of the variation in age-specific arrest ratios for property crime on the order of 56 percent. Not surprisingly, police agency fixed effects by removing time-invariant agency-specific heterogeneity account for the bulk of this explanatory variation (results not shown). Second, the effects of the (log) beer tax on the age-specific arrest ratios for violent and property crime in Tables 4 and 5 are not systematically negative and are never statistically significant. This highlights an important advancement of the current research design relative to those that rely on variation in beer taxes: ZT laws create natural within-state treatment and control groups based on single year of age. The same is not true of beer taxes, since everyone essentially pays the same money price for beer. As such, it is not surprising that there appears to be no systematic relationship between beer taxes and the age-specific arrest ratios considered here. The estimates in Table 5 suggest an important role for ZT laws and by implication reductions in heavy alcohol use in the reduction of property crime. Table 6 investigates these property crime reductions further by separating the dependent variable into finer ratios by single year of age. Each column represents a different OLS estimation, and all models include all the control variables in equation (1). The results in Table 6 show that the property crime reductions associated with ZT laws conform predictably to the specific ages treated by ZT laws. Specifically, the estimated effects of ZT laws in Table 6 exhibit a predictable discontinuity in age just after age 20, as shown reduced vandalism arrests by 3.2 percent and disorderly conduct arrests by 3.4 percent, both significant at the 10 percent level.
18 Heavy Alcohol Use and Crime p. 17 in Figure Table 6, then, suggests that the property crime effects associated with ZT laws reflect age-specific reductions that would be expected in the presence of a causal link between heavy alcohol use and property crime. Table 7 investigates the property crime effects by specific offense type for the year old arrest ratio. Recall that property crimes include arrests for burglary, larceny, and motor vehicle theft. As with the previous tables, all models include all the control variables described above, including unrestricted two-way fixed effects. The estimates in Table 7 indicate that ZT laws had the largest and strongest effects on reductions in larceny, or theft. The reduced form estimate indicates that ZT laws reduced the year old arrest ratio for larceny by about 4.7 percent relative to the pre-reform mean. Estimates for burglary and motor vehicle theft, while both negative, are not significant. Table 8 examines the role of city size in the property crime reductions. The Chilton and Weber crime files allow one to separately identify police agencies in cities and counties of various population sizes. While there is no strong a priori theoretical prediction on the importance of ZT laws by city size, it does offer an interesting descriptive margin. Each column of Table 8 represents a separate OLS estimation of equation (1) for four various city sizes: more than 100,000 residents, between 25,000 and 100,000 residents, between 10,000 and 25,000 residents, and less than 10,000 residents. Interestingly, the property crime reductions appear approximately evenly distributed across medium and small sized cities. Estimates of the ZT effect for the three city sizes below 100,000 residents are all statistically significant and very similar in magnitude to 19 Results for 21 year olds are not reported in Table 6 but are plotted in Figure 3. I exclude 21 year olds throughout the analysis for comparability to the binge drinking estimates in Carpenter (2003). Those consumption models excluded 21 year old men due to an inability to precisely assign treatment status based on lack of birthdate information.
19 Heavy Alcohol Use and Crime p. 18 the baseline estimates (about a 4-5 percent reduction off the pre-reform mean). 20 Property crimes attributable to year olds for police agencies in the very large cities exhibit smaller responsiveness to ZT laws, and the coefficient estimate is not statistically significant. 21 Table 9 investigates whether ZT laws affected criminal activity for college and university police agencies. An interesting feature of FBI crime data is that areas with no permanent residents (such as university police) can be separately identified because they report zero population. This allows the researcher to consider the subsample of fullservice college and university police departments, who generally have the same authority as other police agencies to make arrests for different types of crime. Because the disproportionate majority of college students are in the age groups targeted by ZT laws, one might expect particularly strong effects for this subgroup. Moreover, a high rate of problem alcohol use in universities has been well documented and is widely portrayed in the popular media as a causal factor in rape on college campuses. However, college and university students may be less likely to have or need car access than their similarly-aged peers who are not in college; as such, it is unclear whether drunk driving laws should 20 Estimates for year olds by city size revealed no statistically significant ZT effects. It is also worth nothing that separating the analysis by city size allows an examination of the degree to which the zeros problem might be contributing to the results. This is because cities of at least 10,000 residents have almost no police agencies characterized by zero arrests of year olds for property crime. As such, the arrest ratio does a better job in those agencies at capturing the true age structure of crime. That the property crime reductions associated with ZT laws in cities of, say, 25,000 to 99,999 residents (where essentially all police agencies have strictly positive arrests of year olds for property crime) are very similar to the full sample estimates suggests that the ZT effects are, indeed, real. 21 One possible explanation for the smaller property crime reductions in the very large cities is that city size may be correlated with the presence of mass transit which itself should affect the degree to which ZT laws reduce alcohol consumption. I investigated this directly by performing the same public transit exercise for property crime arrests as was done in Table 3 for DUI arrests. I found property crime reductions associated with ZT laws for the lowest public transportation areas that were marginally significant at the 10 percent level and that were similar in size to the full sample estimates about 3.5 percent. Somewhat surprisingly, the areas with the highest rates of public transit also experienced marginally significant reductions in property crime attributable to year old males.
20 Heavy Alcohol Use and Crime p. 19 have affected their drinking behaviors. Also, university crime as measured by arrests reported by university police departments is much rarer than crime away from universities. Prior to ZT adoption, for example, university police arrested only 7 males age per year on average for property crime compared with 31 male arrests of year olds in the balance of the sample. The same pattern exists for violent crime as well: university police arrested less than 2 men age on average per year for violent crime, while the same figure for other agencies was 13.6 arrests. Thus, it is not clear whether one should expect ZT laws to have affected age-specific crime at colleges and universities. Table 9 reports the associated ZT effects for year old arrest ratios for DUI, property crime, and violent crime for the sample of colleges and universities. 22 Notably, the pattern of the observed coefficient estimates on the ZT indicator is very similar to the main sample estimates: ZT laws are estimated to reduce property crime for these agencies by a marginally significant 10 percent. The estimate for the DUI arrest ratio, while not statistically significant, indicates a large increase of about 14 percent, while the violent crime effect in Column 3 is essentially zero. 23 Table 10 presents a variety of robustness checks on the baseline property crime results for year olds for the main sample. Each column of Table 10 represents a different model, and all include the control variables described above in equation (1). 22 Note that because these agencies report zero population, the models are unweighted. In models where I weight the arrest ratios by age-specific arrest counts, the overall qualitative pattern remains, though the property crime reduction is no longer statistically significant. 23 Note that this does not rule out a causal role for alcohol use in campus violent crime such as rape. In particular, one alternative explanation (of several) that cannot be tested with arrest data is that heavy episodic use increases the likelihood of rape victimization but not the commission of rape (i.e. drunk people are easier targets). I am investigating this possibility in future research. Also, the Bureau of Justice Statistics reports that the overwhelming majority (85% in 1995) of violent victimizations of college
Does Federal Financial Aid Affect College Enrollment? Evidence from Drug Offenders and the Higher Education Act of 1998 Michael F. Lovenheim 1 Emily G. Owens 2 June 2013 Abstract In 2001, amendments to
The Effects of Merit-Based Financial Aid on Drinking in College Benjamin W. Cowan and Dustin R. White February 25, 2015 Abstract We study the effect of state-level merit aid programs (such as Georgia s
Does Strengthening Self-Defense Law Deter Crime or Escalate Violence? Evidence from Expansions to Castle Doctrine Cheng Cheng Texas A&M University Mark Hoekstra Texas A&M University and NBER Forthcoming
The Labor Market Impact of Employer Health Benefit Mandates: Evidence from San Francisco s Health Care Security Ordinance July 6, 2011 Carrie H. Colla *, William H. Dow, Arindrajit Dube Abstract: A key
Do Harsher Prison Conditions Reduce Recidivism? A Discontinuity-based Approach M. Keith Chen, Yale University and Cowles Foundation, and Jesse M. Shapiro, University of Chicago and NBER We estimate the
CRIME RATES AND LOCAL LABOR MARKET OPPORTUNITIES IN THE UNITED STATES: 1979 1997 Eric D. Gould, Bruce A. Weinberg, and David B. Mustard* Abstract The labor market prospects of young, unskilled men fell
EI @ Haas WP 238 Commercial and Industrial Demand Response Under Mandatory Time-of-Use Electricity Pricing Katrina Jessoe and David Rapson February 2013 Energy Institute at Haas working papers are circulated
This article was published in an Elsevier journal. The attached copy is furnished to the author for non-commercial research and education use, including for instruction at the author s institution, sharing
Do Retiree Health Benefits Cause Early Retirement? David M. Linsenmeier Princeton University November 2002 I would like to thank Orley Ashenfelter, Linda Bilheimer, David Blau, Melissa Clark, Henry Farber,
FEDERAL RESERVE BANK OF SAN FRANCISCO WORKING PAPER SERIES The Effect of an Employer Health Insurance Mandate on Health Insurance Coverage and the Demand for Labor: Evidence from Hawaii Thomas C. Buchmueller
This work is distributed as a Discussion Paper by the STANFORD INSTITUTE FOR ECONOMIC POLICY RESEARCH SIEPR Discussion Paper No. 12-007 The RAND Health Insurance Experiment, Three Decades Later by Aviva
The Effect of Health Insurance Coverage on the Use of Medical Services * Michael Anderson Carlos Dobkin Tal Gross UC Berkeley UC Santa Cruz & NBER Columbia University firstname.lastname@example.org email@example.com
WORKING P A P E R The Impact of Nearly Universal Insurance Coverage on Health Care Utilization and Health Evidence from Medicare DAVID CARD, CARLOS DOBKIN, NICOLE MAESTAS WR-197 October 2004 This product
Does Risk Adjustment Reduce Selection in the Private Health Insurance Market? New Evidence from the Medicare Advantage Program November 2010 Preliminary and Incomplete Jason Brown U.S. Department of the
NBER WORKING PAPER SERIES DO CIGARETTE TAXES MAKE SMOKERS HAPPIER? Jonathan Gruber Sendhil Mullainathan Working Paper 8872 http://www.nber.org/papers/w8872 NATIONAL BUREAU OF ECONOMIC RESEARCH 1050 Massachusetts
THE PRISON BOOM & THE LACK OF BLACK PROGRESS AFTER SMITH & WELCH DEREK NEAL UNIVERSITY OF CHICAGO DEPARTMENT OF ECONOMICS, COE, AND NBER & ARMIN RICK UNIVERSITY OF CHICAGO DEPARTMENT OF ECONOMICS Abstract.
Working Paper The Effect of Montana's 24/7 Sobriety Program on DUI Re-arrest Insights from a Natural Experiment with Limited Administrative Data Gregory Midgette and Beau Kilmer RAND Justice, Infrastructure,
TRANSFER PAYMENTS AND THE MACROECONOMY: THE EFFECTS OF SOCIAL SECURITY BENEFIT INCREASES, 1952 1991 Christina D. Romer David H. Romer University of California, Berkeley December 2014 We are grateful to
DISCUSSION PAPER SERIES IZA DP No. 5026 Ranking Up by Moving Out: The Effect of the Texas Top 10% Plan on Property Values Kalena E. Cortes Andrew I. Friedson June 2010 Forschungsinstitut zur Zukunft der
Does Microfinance Really Help the Poor? New Evidence from Flagship Programs in Bangladesh Jonathan Morduch Department of Economics and HIID Harvard University and Hoover Institution Stanford University