ABSTRACT
For nearly every crime, there is a victim. However, the vast majority of studies in the economics of crime have focused on the causal determinants of criminality. We present novel evidence on the causal determinants of victimization, focusing on legal access to alcohol. The social costs of alcohol use and abuse are sizable and well documented. We find criminal victimization—for both violent and property crimes—increases noticeably at age 21. Effects are not present at other birthdays and do not appear to be driven by a “birthday celebration effect.” The effects are particularly large for sexual assaults, especially those that occur in nonresidential locations. Our results suggest prior research that has focused on criminality has understated the true social costs associated with increased access to alcohol.
I. Introduction
For nearly every crime committed, there is both an offender and a victim. Yet, due to both data constraints and disciplinary norms, economics research on crime dating back to Becker (1968) has focused primarily on policy levers that modify the behavior of potential offenders (Nagin 2013; Chalfin and McCrary 2017). Perhaps this is natural because the chief policy levers at the disposal of a social planner, namely police (which change the certainty of punishment) and prisons (which change the severity of punishment), are intended to influence the actions of the agents committing crimes. Given that, by offending, offenders violate society’s explicit social norms, this perspective is largely consistent with the normative views of the general public, which does not wish to blame the victim for having been victimized (Crawford 1977; Eigenberg and Garland 2008).
We agree with this view—that victims are not blamed when a crime occurs—and note that, since markets require the voluntary transfer of property rights, there can be neither a market nor a price for victimization. (Carnis 2004). At the same time, victim behavior can be an important input into the cost function of potential offenders. As such, providing information can be a critical means through which social planners can empower victims while also tailoring public safety interventions to be maximally disruptive to potential offenders (Cozens et al. 2005; MacDonald 2015; Branas et al. 2016), and in so doing, reducing the overall cost of crime control (Ben-Shahar and Harel 1995). In this work we provide some of the first evidence on the causal determinants of victimization, focusing on abrupt change in legal access to alcohol at age 21 in the United States.
Identifying the determinants of victimization is both important and promising for several reasons. First, recent literature has found that becoming a crime victim has a wide range of impacts and includes effects as diverse as mental well-being (Cornaglia, Feldman, and Leigh 2014; Dustmann and Fasani 2015), labor market earnings and benefits receipt (Bindler and Ketel 2019), and health outcomes for newborn infants (Currie, Mueller-Smith, and Rossin-Slater 2022). Accordingly, the costs of victimization are likely to be large and especially concentrated among the most vulnerable members of society (Papachristos et al. 2015).
Second, for many crimes, especially those that have low clearance rates, abating crime through deterrence-based strategies is costly. This is especially true of family violence, which typically occurs indoors and thus may be less sensitive to traditional law enforcement inputs than other interventions, such as mandatory reporting laws (Rodriguez et al. 2001; Iyengar 2009), the provision of social services (Davis, Weisburd, and Taylor 2008; Iyengar and Sabik 2009), or divorce laws (Stevenson and Wolfers 2006; Brassiolo 2016). Instead, victimization-oriented strategies might reduce crime at lower cost. While the normative implications of this hypothesis are potentially controversial, given the high collateral costs of the criminal justice system (Aizer and Doyle 2015; Dobbie, Goldin, and Yang 2018), this policy option may be worth further exploration.
Third, victims often have relatively little information about their probability of being victimized, as well as the effectiveness of private investments in crime control. Indeed, given that research has yet to offer much evidence on the causal effect of actions or policies on victimization, we might expect that individuals will have difficulty accurately forecasting this on their own. Therefore, it stands to reason that victims might not optimally invest in precaution in a wide variety of situations.1
Finally, while programmatic interventions typically have high variable costs, we note that informational interventions often have low marginal costs and, as such, are easier to scale. Because of this, there may be considerable promise in providing information to victims, as well as law enforcement.
Studying the determinants of victimization has proven elusive for at least two reasons. First, it is difficult to identify policies that affect the probability of victimization without also affecting the supply side of the market. Second, victimization research is hampered by the extremely limited availability of microdata, especially U.S. microdata at the subnational level (Gutierrez and Kirk 2017). While a large research literature in criminology identifies some demographic and situational correlates of victimization (Gottfredson 1986), finding exogenous variation upon which a causal claim may be made about an actionable policy lever has proven elusive.
We study one prominent policy lever that plausibly has an outsize influence on victimization: legal access to alcohol. A large body of research has found evidence of significant social costs associated with legal and low-cost access to alcohol (Grossman and Markowitz 1999; Markowitz 2000; Carpenter 2005, 2007; Carpenter and Dobkin 2009, 2011, 2015, 2017; Cook and Durrance 2013; Heaton 2012; Kilmer et al. 2013; Anderson, Crost, and Rees 2017).2 These papers utilize both age-based discontinuities in access to alcohol and geographic variation in state or local policy. The consensus reached in this literature suggests that legal access to or lower prices for alcohol are associated with increased traffic fatalities, suicides, violent behavior, and injuries, including intentionally inflicted injuries among male victims (Carpenter and Dobkin 2017). Despite the substantial body of evidence documenting the negative public health impacts of alcohol use and abuse, these impacts might be even larger if alcohol use also increases the risk of of becoming a victim of a crime more broadly, which none of the previous studies have been able to address. In particular, one of the most intriguing possibilities is that legal access to alcohol might be an important driver of sexual assaults, a relationship that has received wide speculation in the literature in criminology and public health (Kantor and Straus 1989; Dembo et al. 1992; Miller, Downs, and Testa 1993; Abbey et al. 2001; Abbey 2002; Champion et al. 2004; Felson and Burchfield 2004). These studies, while suggestive, are largely correlational and lack credible research designs, though recent and more credible research has intriguingly linked sexual assaults to local culture of drinking and alcohol abuse, or “college party culture” (Lindo, Siminski, and Swensen 2018).
The primary empirical challenge involved in identifying a causal impact of alcohol use on crime is that using alcohol, particularly to excess, is an endogenous choice. As a result, there are many reasons why a correlation between alcohol use and victimization might exist either among individuals or, for a given individual, over time. We study a related research question—and one that pairs naturally with a potential policy lever—and estimate the extent to which legal access to alcohol causes a discrete change in victimization. By focusing on legal access to alcohol, we study a bundle of related interventions, including the amount of alcohol that individuals consume, as well as the venue where drinking occurs. Our empirical analysis considers the mechanisms underlying the effects we observe and points to evidence that the venue of consumption is an important driver of the effects of legal access to alcohol.
In order to identify a causal effect of legal access to alcohol on victimization, we utilize the fact that legal access in the United States changes discretely at age 21 and, using a sharp regression discontinuity (RD) design, estimate the likelihood that an individual is victimized just after their 21st birthday relative to the period before their 21st birthday. In order to estimate the model, we build a unique administrative data set that contains the exact date of birth for all crime victims known to law enforcement in eight large U.S. cities and find strong evidence that certain types of victimization—sexual assault and burglary for women, assault and robbery for men, and larceny for both genders—increase considerably at age 21. This effect is found only at age 21 (and not on prior or subsequent birthdays) and is unlikely to be driven by celebrating one’s 21st birthday itself.
On the whole, our estimates suggest that legal access to alcohol changes the landscape of victimization considerably and that a sizable share of serious crime could be abated by policies that change legal access to alcohol or modify the parameters of public intoxication. In particular, our findings suggest that victimization rises to the greatest extent among venues outside of one’s home, suggesting that it is not merely the volume of alcohol consumed but also where it is consumed that drives victimization risk. Our findings also provide additional insights into the complex and controversial relationship between alcohol and sexual assault (Lindo, Siminski, and Swensen 2018). In particular, while both Carpenter and Dobkin (2015) and Hansen and Waddell (2018) fail to find evidence that arrests or criminal charges for rape increase at age 21, we find sexual assault victimization at age 21 increases by nearly 25 percent in our preferred specifications.3 Taken together, these findings are more consistent with a model of crime in which perpetrators of sexual assault seek out vulnerable populations than with a model where sexual assault perpetrators lose control due to increased alcohol use.4
The remainder of this paper proceeds as follows. Section II provides a brief institutional history of the minimum legal drinking age and its effects on alcohol consumption. Section III provides detail on the unique administrative data set collected for this study. Section IV provides an overview of the econometric models. Section V presents results, and Section VI concludes.
II. Background
A. Private Actions and Victimization
There are many ways through which potential victims can reduce their likelihood of becoming the victim of a crime. With respect to property crimes, these include investments in traditional target- hardening strategies (for example, locks and deadbolts) and technology (for example, surveillance cameras and security systems), as well as labor inputs, such as private security services. In the case of violent crimes, which drive an outsize share of the social costs of offending (Chalfin 2015), private precautions are, to a greater extent, driven by behavioral modifications by potential victims—modifications that are perceived to change an individual’s probability of victimization. Such behavioral modifications might include avoiding leaving one’s home at night, hailing a taxi instead of walking while in a high-crime area, carrying fewer valuables on one’s person, or maintaining a generally higher level of vigilance or situational awareness. Each of these actions has the potential to make crime less profitable to a potential offender.
While investments in private precaution are costly with often unknown benefits to potential victims, they are potentially attractive to a social planner for a number of reasons. First, an individual victim may have more information about how to successfully abate their risk of being victimized than law enforcement, which must devise crime control strategies on the basis of typical patterns of victim and offender behavior that cannot easily tailor these strategies to a given individual’s needs (Ben-Shahar and Harel 1995; Felson and Clarke 1995). Second, in most cities in the United States, there is approximately one sworn police officer for every 250 residents, so there are natural limits to the ability of law enforcement to deter offending (Chalfin and McCrary 2018). Finally, investments in private precaution may raise search costs for offenders, thus making crime less attractive overall (Shavell 1991). Thus, private precautions, even when observable to potential offenders, may generate positive spillovers to society.
Taken as a whole, the theory suggests that it may be possible for potential victims to abate crime more efficiently than can the government—at least at the margin. Consider, for instance, crimes such as larceny or burglary, which often involve belongings left unattended or homes that were unlocked at the time of the crime, both of which are extremely common and could be abated through low-cost changes in behavior among potential victims. These crimes are only marginally responsive to police staffing (Chalfin and McCrary 2018). Yet, for a variety of reasons—because individuals do not fully internalize the cost of victimization (Clotfelter 1978; Ayres and Levitt 1998), because public spending on crime control may be treated as a subsidy (Guha and Guha 2012), or because individuals are myopic or misinformed—victims may underinvest in precaution relative to what is socially optimal.5 This raises the possibility that there may yet be low hanging fruit to pick with respect to addressing crime through private victim action.
B. Alcohol Use and Victimization
Literature outside of economics has linked alcohol abuse and victimization, either as a correlate of victimization risk (Champion et al. 2004; Felson and Burchfield 2004) or as a predictor of subsequent victimization (Kantor and Straus 1989; Widom 2001), particularly in the context of domestic violence and sexual assault (Abbey 2002). However, none of these studies use exogenous variation to identify a causal effect of substance use. Within economics, prior research has found that emergency department visits for injuries inflicted by others increase at age 21 (Carpenter and Dobkin 2017) and that sexual assault victimization rises during college football game days (Lindo, Siminski, and Swensen 2018), an effect which is credibly due to an increase in alcohol consumption. While the evidence is predominantly correlational, there are a number of reasons why alcohol use and crime victimization might be causally related. First, there is evidence that the use and, particularly, abuse of alcohol causes individuals to exhibit fewer inhibitions (Mulvihill, Skilling, and Vogel-Sprott 1997; Easdon and Vogel-Sprott 2000; Fillmore and Vogel-Sprott 2000), which may lead them to take on risks that they otherwise would not have taken (Ryb et al. 2006). Thus, victimization might rise with alcohol abuse due to a change in the risk tolerance of potential victims. Second, intoxication may affect an individual’s situational awareness and therefore increase the ease with which a motivated offender can identify and approach a victim. For instance, an intoxicated victim might be less likely to notice a risky situation (Parks and Miller 1997) or take actions to mitigate that risk.
Third, a large literature establishes that intoxication increases aggression (Giancola and Zeichner 1995; Graham et al. 2006), which itself is a predictor of victimization, especially for assaults. We note, for example, that the difference between an assault victim and the perpetrator of an assault can simply be which party strikes the first blow (Chalfin, Danagoulian, and Deza 2019). Finally, intoxicated victims may be less able to defend themselves effectively, thus reducing the cost to a potential offender.
C. The Minimum Legal Drinking Age and Alcohol Consumption
In the United States, the minimum legal drinking age (MLDA)—the age at which individuals are legally allowed to purchase alcohol—has historically oscillated between 18 and 21 years of age. Many states initially lowered their MLDAs only to raise them again later in the 1980s. Currently, essentially every state implements a MLDA of 21.6 While the law does not prevent minors from securing access to alcohol (Freisthler et al. 2003), there is ample evidence that legal access to alcohol nevertheless increases drinking and, in particular, problematic drinking. First and most directly, research uses information from National Health Interview Survey to show that drinking increases at both the extensive and intensive margins when individuals turn 21 (Carpenter and Dobkin 2009). Second, prior research shows that traffic fatalities (Carpenter and Dobkin 2009, 2011; Francesconi and James 2019) and drunk driving arrests (Carpenter and Dobkin 2015; Hansen and Waddell 2018) increase with legal access to alcohol due to the MLDA. Third, related evidence shows that it is precisely the most problematic types of drinking that increase at age 21—for example, binge drinking—as opposed to moderate levels of drinking (Carpenter, Dobkin, and Warman 2016). This research and other related studies on youth zero tolerance laws (Carpenter 2007) suggest that alcohol use, including consumption patterns consistent with alcohol abuse, increases with legal access to alcohol. Finally, we note that the MLDA may also shift the venue of alcohol consumption. While underage individuals can obtain alcohol from bars and restaurants either using fake identification or because waitstaff do not ask for proof of legal age, research suggests that individuals who consume alcohol prior to reaching the age of legal majority generally obtain alcohol at convenience stores, supermarkets, or at house parties (Gosselt et al. 2007; Fabian et al. 2008).
III. Data
This research considers whether individuals who have legal access to alcohol are more likely to become crime victims. As national microdata on crime victims are unavailable, we construct a unique data set on crime victimization, using administrative microdata obtained from eight municipal police departments in the United States. The eight police departments are the municipal law enforcement agencies for the following cities: Charlotte, NC (Charlotte–Mecklenburg); Dallas, TX; Denver, CO; Houston, TX; Kansas City, MO; Milwaukee, WI; San Diego, CA; and St. Louis, MO.7 These departments cover a population of approximately eight million residents, represent a number of different U.S. regions, and include three of the ten largest cities in the United States—Houston, Dallas, and San Diego.8 Table 1 explores the extent to which the cities in our analytic sample differ from other U.S. cities and the population as a whole with respect to their crime rates. The cities in our sample have higher than average crime rates, approximately 50 percent higher than other large cities, depending on the crime type. St. Louis, in particular, has an extremely high crime rate and had the highest homicide rate in the United States in 2016.
Crime Rates in the Study Sample (2016)
In each city, the data contain information on the type of crime, the date of victimization, and the victim’s exact date of birth and gender. To protect victim anonymity, we do not have victim identifiers. We focus on crimes that, with a few exceptions, largely correspond to the Federal Bureau of Investigation’s list of “index crimes,” which are collected annually and reported in the FBI’s Uniform Crime Reports. Specifically, we focus on the following crimes: assault,9 burglary, homicide, larceny, motor vehicle theft, robbery, and sex-related crimes (an aggregate of rape and other sexually related offenses), in cities for which they are available.10 Overall, data cover the years 2007–2018, though exact years of data availability vary by department.11 In all subsequent analyses, we aggregate the data from our eight cities in order to generate a national estimate of the effect of legal exposure to alcohol on crime.
We supplement our administrative data with microdata from urban respondents to the U.S. National Crime Victimization Survey (NCVS), a survey of a random sample of between 49,000 and 77,000 U.S. residents, collected by the U.S. Bureau of Justice Statistics (BJS) since 1977. The NCVS is the principal national data set on victimization in the United States (Gutierrez and Kirk 2017) and allows us to ensure that the reporting of crimes to law enforcement does not change discontinuously at age 21, a critical falsification check for our analysis. In the NCVS, respondents are asked to indicate whether they have been the victim of a crime during the past six months. Critically respondents are also asked whether they reported that crime to law enforcement. We use the NCVS to explore whether crime reporting changes at the age of 21, a story that might be true if intoxicated victims who are under the MLDA are less likely to report a crime to law enforcement. If true, this could lead us to conclude that victimization increases at age 21 even though this effect might merely be an artifact of differential crime reporting. In Section V.B.1, we consider whether crime reporting changes discontinuously at age 21 and conclude that, for most types of crimes, there is little evidence of differential crime reporting at the MLDA.
Prior to describing our empirical models and results, we pause here to present a brief descriptive analysis of the age-victimization profile in our administrative data. In Figure 1, we present the share of victimizations by age, using a local polynomial smoother. Panel A presents violent crimes; Panel B presents property crimes. For both crime types, we present results separately for males (using a black line) and females (using a gray line). Consistent with a long-standing empirical regularity that has been documented by scholars of victimization, crime victimization generally rises throughout childhood, peaking between the ages of 20 and 30 and falling steeply thereafter (Stafford and Galle 1984). Several exceptions are worth noting. First, there are important gender differences with respect to the victimization age profile of sexual assault. Among males, sexual assaults are most prevalent in childhood, and the risk declines substantially thereafter. Among females, sexual assault risk peaks just prior to age 20. Second, while homicide risk peaks for both genders in the early 20s, the peak is especially large for men, reflecting the ubiquity of gang violence and “vendetta-like antagonisms,” often referred to colloquially as “beefs” (Kennedy 1996). The opposite pattern holds for assaults, with women experiencing an especially high degree of vulnerability in their early 20s while men’s victimization risk declines more slowly throughout their life span.
Age Profile of Victimization
Notes: This figure presents local polynomial regressions of age on the share of victimizations in the data. Each observation is the share of all victimizations within crime type and gender that occur at a given age.
Referring to Online Appendix Figure A1, readers can contrast patterns in our data, derived from crime reports, with survey data from urban respondents to to the NCVS.12 Violent victimization patterns are, on the whole, extremely similar to those derived from our administrative data.13 However, there are some notable differences with respect to property crime victimization. In contrast to the law enforcement data from our eight cities, in the NCVS, the age–crime profile for burglary and larceny suggests that crime victimization drops off less dramatically after age 30. Notably, both the NCVS and our administrative data highlight that the age period affected by the MLDA, the early 20s, is an important period for policy given high victimization rates for nearly all crimes.
IV. Methods
We estimate the causal effect of legal access to alcohol on victimization using a regression discontinuity design, leveraging the discrete change in legal alcohol access at age 21. The primary identifying assumption is that individuals who are just below age 21 and individuals who are just above age 21 are interchangeable—that is, they do not differ, on average, with respect to both observable and unobservable characteristics. The design likewise assumes that other features of the social environment that affect crime do not change discontinuously at age 21. While age is a common running variable in empirical applications in applied microeconomics—see, for example, Lemieux and Milligan (2008); Smith (2009); McCrary and Royer (2011)—we discuss potential violations of this assumption in Section V.B.3.
Because all individuals are subject to the treatment age, 21, without exception, we estimate treatment effects using a “sharp” RD design. In keeping with standard empirical practice, we estimate treatment effects using the following general specification operationalized using Poisson regression:
1
Yi ∼ Poisson(γi) is the count of victimizations occurring at relative age i (measured as days relative to age 21), (Xi – c) is the number of days relative to a given crime victim’s 21st birthday, and Di is an indicator variable for whether or not the criminal incident occurred prior to or after the victim’s 21st birthday.14 The coefficient on Di, τ, identifies the causal effect of legal access to alcohol. Because the evolution of victimization over the life cycle may be nonlinear in age relative to 21, in practice, we specify a model that also includes (Xi – c)j and the product of this term and Di for polynomials of order j = 2 and 3. These nonlinearities allow us to account for numerous factors that may affect victimization, such as criminality, which is known to vary over the life course (Loeber and Farrington 2014), an age gradient to alcohol consumption or the likelihood that an individual lives alone. We also estimate RD models using the optimal bandwidth calculation of Calonico, Cattaneo, and Titiunik (2014).
Equation 1 is estimated for a given bandwidth, h, so that the regression is estimated for those observations within c − h ≤ Xi ≤ c + h. Our primary models use a bandwidth of two years. All models are estimated using robust standard errors, which accommodate the possibility that there is heteroskedasticity among the individual error terms within age bins. In Section V.D, we describe a number of additional robustness checks that test the sensitivity of the results to alternative modeling strategies.
In addition to estimating the effect of reaching the MLDA, we also estimate a “birthday effect”—that is, the change in victimization risk on a victim’s birthday itself or on the following weekend when an individual might celebrate their birthday. Estimating this effect is important for two reasons. First, controlling for a victim’s birthday helps to ensure that our estimates of the causal effect of alcohol access are not merely due to birthday celebration effects. Second, birthday celebration effects are interesting in their own right. We estimate—and control for—birthday celebration effects by adding a dummy variable to Equation 1 that indicates whether date i was the victim’s birthday or whether the victim’s birthday occurred on the subsequent weekend.
V. Results
A. Main Results
We study the effect of the reaching the legal drinking age separately for violent crimes (murder, robbery, sexual assault, and other assaults) and property crimes (burglary, larceny, and motor vehicle theft). We also estimate models separately by gender. Tables 2 and 3 present Poisson regression estimates of the effect of legal access to alcohol on victimization for males and females, respectively. In each cell, we report the incidence rate ratio (IRR) from the Poisson regression model and the robust standard error around the estimate. The first column reports coefficient estimates for the regression outlined in Equation 1 using an order-one polynomial in age. Columns 2 and 3 include a second- order polynomial and a third-order polynomial in age, respectively. In Column 4, we focus on the quadratic specification and add a dummy variable for whether an individual is victimized on their birthday in order to distinguish legal access to alcohol from birthday celebration effects. Recognizing that birthdays are not always celebrated on an individual’s exact birthday, in Column 5, we include the birth date itself and the three following days. In Column 6, we include the entire week around the individual’s birthday.15
Poisson Male RD Effects
Poisson Female Regression Discontinuity Effects
For males, legal access to alcohol leads to a 7 percent increase in both violent and property victimization. Effects are especially large for sex offenses (12–120 percent; 74 percent in our preferred model), though these are not precisely estimated as sexual assaults with male victims are relatively uncommon in the data. Effects are also meaningful and significant at conventional levels for robbery (8 percent), nonsexual assault (7 percent), larceny (8 percent), and motor vehicle theft (12 percent). Effects for burglary are close to zero in all specifications. For females, legal access to alcohol does not, in general, increase the likelihood of a violent victimization. This is consistent with Carpenter and Dobkin (2017), who find female hospitalizations and emergency department visits do not increase for injuries intentionally caused by others. Their measure, like overall violent crime, is a composite of many different types of injuries.16 Disaggregating crimes into finer categories reveals substantial heterogeneity across crime types. While assaults do not increase generally for female victims, sexual assaults increase considerably—by approximately 24 percent. Property crimes likewise increase—by approximately 12 percent for burglary and larceny. Unlike for males, we find little evidence that motor vehicle theft victimization is sensitive to the MLDA for women. We further note that the estimated effects, for the most part, are not sensitive to our choice of polynomial and persist regardless of how we account for birthday effects. Figures 2 and 3 present the estimated effects for males, and Figures 4 and 5 present the equivalent effects for females. In each set of figures, we fit a local quadratic regression through the data.
Effect of MLDA on Male Victimization
Notes: This figure contains fitted Poisson estimates and average victimization counts in 14-day bins for violent crimes. Poisson estimates include a second-order polynomial in age fully interacted with an indicator for age over 21 and no birthday controls. 95 percent confidence intervals included. All regressions use a two-year bandwidth.
Effect of MLDA on Male Victimization Property Victimizations
Notes: This figure contains fitted Poisson estimates and average victimization counts in 14-day bins for property crimes. Poisson estimates include a second-order polynomial in age fully interacted with an indicator for age over 21 and no birthday controls. 95 percent confidence intervals included. All regressions use a two-year bandwidth.
Effect of MLDA on Female Victimization Violent Victimizations
Notes: This figure contains fitted Poisson estimates and average victimization counts in 14-day bins for violent crimes. Poisson estimates include a second-order polynomial in age fully interacted with an indicator for age over 21 and no birthday controls. 95 percent confidence intervals included. All regressions use a two-year bandwidth.
Effect of MLDA on Female Victimization Property Victimizations
Notes: This figure contains fitted Poisson estimates and average victimization counts in 14-day bins for property crimes. Poisson estimates include a second-order polynomial in age fully interacted with an indicator for age over 21 and no birthday controls. 95 percent confidence intervals included. All regressions use a two-year bandwidth.
B. Robustness
The results presented in Section V.A suggest that the probability of crime victimization changes discontinuously at age 21, an effect that we attribute to the MLDA. In this section, we subject these results to greater scrutiny in order to establish that the change in victimization that we observe is the result of legal access to alcohol and not another feature of the social world.
1. Differential reporting behavior
A natural concern in ascribing a causal interpretation to the results reported in Section V.A is that these estimates could be an artifact of differential crime reporting among individuals who have reached the MLDA. This might be the case, for instance, if underage victims are less inclined to report a crime to law enforcement due to concerns about being arrested or detained as a result of their own illegal use of alcohol. Such a story is especially worrisome insofar as it could rationalize our principal finding—that victimization increases at age 21.
The differential reporting story is not possible to rule out using our administrative data because these data include only crimes that are known to law enforcement. In order to investigate whether there is differential crime reporting by age, we turn to survey data and focus our attention on 18–35-year-old, urban respondents to the 2006–2016 waves of the National Crime Victimization Survey, the principal source of national data on crime reporting behavior (Lauritsen, Heimer, and Lynch 2009; Gutierrez and Kirk 2017). Leveraging the fact that the NCVS captures whether an individual was victimized as well as whether or not they reported a given crime to law enforcement, we observe the extent to which reporting rates change discretely at age 21.
Figure 6 presents the age-path of the reporting rate separately by gender among urban respondents to the NCVS. We do so by regressing a dummy variable for whether a crime is reported on a series of age dummies, conditional upon interacted crime type by survey year fixed effects. We focus on reporting rates for the violent and property crime aggregates, as reporting rates for individual crime types are noisy due to small numbers of victims in the NCVS.17 There is little evidence of a discrete change in the reporting of violent crimes at 21. Likewise, for property crimes, there are no clear reporting trends among women aged 19–23—the slight jump in crime reporting at 21 (approximately eight percentage points) is small and statistically insignificant. Among men, there is a secular increase in crime reporting with age, and there is some evidence that property crime reporting increases discretely at age 21. However, the estimated difference is small (approximately 3.5 percentage points) and not statistically significant at conventional levels. We note that even if the estimated reporting difference is taken at face value, it is unlikely to be large enough to explain the magnitude of our point estimate.
Reported Victimization by Age, Urban Victimizations
Notes: This figure presents estimates of βk from 
, where i is individual, k is age in years at time of survey, and t crime type. Reportikt is an indicator variable that is one if an individual reported their victimization to the police and zero otherwise. Age Indik is an indicator variable that is one if individual i was age k at the time of survey wave w. 95 percent confidence intervals included based on robust standard errors. Only victimizations where an individual was victimized in their home county and for whom the home county is urban are included. Estimates are based on the 2006–2016 waves of the National Crime Victimization Survey and relative to age 20.
One caveat in using the NCVS is that the survey records a respondent’s age at the time that the survey was administered, not the respondent’s age at this time they were victimized. As a result, there are likely to be a number of instances in which the victim’s age is mislabeled with respect to when the victimization occurred. In Online Appendix Figure A2 we subtract one from each respondent’s age to account for the possibility that a respondent’s calendar age does not reflect their age at the time of victimization. Patterns are qualitatively similar to those in Figure 6 but provide even less compelling evidence for a discontinuous change in crime reporting at 21. Overall, the evidence provides support for our claim that the changes in victimization that we observe at the MLDA are driven primarily by legal access to alcohol and are unlikely to be an artifact of age-graded reporting patterns among crime victims.
2. Bandwidth selection
In order to test the sensitivity of our preferred estimates to bandwidth selection, we reestimate our primary outcome model for a range of bandwidths between 180 and 730 days, in ten-day increments. Figure 7 presents the results of this exercise for violent crimes, and Figure 8 presents results for property crimes. The figures demonstrate that a strategic choice of bandwidth is not likely to be driving our our principal estimates. With the exception of motor vehicle theft, the estimates are, if anything, more conservative at our preferred bandwidth of two years than they are at smaller bandwidths. We also reestimate results using the optimal bandwidth calculation of Calonico, Cattaneo, and Titiunik (2014); these results are presented in Online Appendix Table A1 (using a uniform kernel) and Online Appendix Table A2 (using a triangle kernel) and are substantively similar to our preferred estimates.
Bandwidth Sensitivity: MLDA Effect Violent Victimizations
Notes: This figure presents estimates of the sensitivity of the RD estimates presented in Tables 2 and 3 to the choice of bandwidth for violent crimes. In the figures, the bandwidth is plotted on the x-axis; incident rate ratios are reported on the y-axis. In each case, regressions include a second-order polynomial in age fully interacted with an indicator for age over 21 and no birthday controls.
Bandwidth Sensitivity: MLDA Effect Property Victimizations
Notes: This figure presents estimates of the sensitivity of the RD estimates presented in Tables 2 and 3 to the choice of bandwidth for property crimes. In the figures, the bandwidth is plotted on the x-axis; incident rate ratios are reported on the y-axis. In each case, regressions include a second-order polynomial in age fully interacted with an indicator for age over 21 and no birthday controls.
3. Sample selection
While our administrative data set provides incredibly granular data on the timing of victimization, an inherent limitation is that we observe only those individuals who are victimized by a crime. As such, our estimates could potentially be compromised by sample selection bias—that is, differential selection into the sample local to the MLDA. Given that the data we use to draw inferences are victimization counts by relative age, the most pressing concern is that sample selection bias changes the risk of entering our sample as a function of the running variable. In particular, we note the possibility that, upon reaching the MLDA, individuals who live in outlying areas become differentially likely to travel to the cities in our sample—for instance, to consume alcohol in bars or nightclubs in the closest large city. To the extent that this is true, there would be more 21-year-olds than 20-year-olds available to victimize in municipal law enforcement data, and, as such, we could observe increased victimization after age 21 that is an artifact of geographic selection rather than a genuine change in the vulnerability of potential victims at age 21. Some of our prior analyses are inconsistent with this notion, as several categories of common crimes do not show increases. For instance, we do not find that general assaults increase for females. In this section, we offer a more formal test for geographic sorting at the MLDA.
Leveraging national data from the NCVS and additional detail in our microdata from Dallas, we offer three different tests for geographic sorting at the MLDA. First, using NCVS data, we assess the extent to which the share of victimizations that occurred in a crime victim’s county of residence changes as a function of age. A decrease in the share of home county victimizations would be consistent with geographic sorting effects. As discussed in Section V.B.1, a limitation to the NCVS is that exact dates of birth and victimization are not provided. Accordingly, victimizations that occur at age 21 will apply to individuals who are both age 21 and age 22 at the time they were surveyed by the NCVS. These data are plotted in Figure 9. Overall, while there is evidence for a secular rise in the share of home county violent crime victims with age, there is little evidence that the share of victimizations in a victim’s home county decreases between the ages of 19 and 23.
Home County Victimization by Age, Urban Respondents
Notes: This figure presents estimates of βk from 
where i is individual, k is age in years at time of survey minus one year, and t crime type. Home_Countyikt is an indicator variable that is one if an individual was victimized in their county of residence and zero otherwise. Age Indik is an indicator variable that is one if individual i was age k at the time of survey wave w. 95 percent confidence intervals included based on robust standard errors. Estimates are based on urban respondents of the 2006–2016 waves of the National Crime Victimization Survey and relative to age 20.
Next, in Dallas, we observe each crime victim’s home municipality, allowing us to discern whether the crime victim is a Dallas resident or not. We use these data to construct two additional tests for geographic sorting. First, given that sample selection will be predominantly driven by selection into our sample among nonresidents, we begin by focusing our attention on crime victims who are local residents. The assumption is that, among local residents, we would not expect the number of potential victims to change discontinuously at the threshold of the running variable. We also present estimates for nonresidents for reference. While an effect of the MLDA on victimization among the resident subsample provides evidence that sample selection is not driving our main results, we note that to the extent that local residents and nonresidents themselves differ with respect to victimization risk, there is, of course, no requirement that the results of this analysis should mirror our main estimates.
We present RD estimates for local residents in Dallas in Table 4. For each model, an IRR above one indicates that, among local residents, who are less subject to geographic sorting concerns, victimization rises at the MLDA. Referring to the table, there is clear evidence for an increase in property victimization among both male and female Dallas residents. For violent offenses, the evidence is less compelling. In particular, we do not see clear evidence for the increase in violent victimization for men that we reported in Table 2 or the increase in sexual assault victimization reported in Table 3. That said, the estimates use data from a single city and, as such, are imprecise. There is, therefore, little evidence against the estimates reported in Tables 2 and 3. For example, among male Dallas residents, point estimates suggest an increase in robbery victimization of 5 percent and an increase in assault victimization of 4 percent. These estimates are extremely similar to those reported in Column 6 of Table 2, where we estimate that robbery and assault victimizations rise among men by 8 percent and 7 percent, respectively. For sexual assaults with female victims, our point estimate suggests that, if anything, these decline at the MLDA among Dallas residents. However, the standard error (0.258) is large, and, accordingly, the estimate is not inconsistent with the 25 percent increase reported in Table 3.
Poisson Regression Discontinuity Effects, Dallas Subsample
To provide further clarity, we present a third test of geographic sorting and consider whether the share of crime victims who are local residents changes discontinuously at age 21. To the extent that this share falls at age 21, this might constitute evidence of geographic sorting. Because some crime types are rare in the data, there are relative ages, measured in days, in which there are zero crimes in the data. Accordingly, the share of local residents, the dependent variable in this specification, is undefined in some bins. To address this issue, we collapse our data into monthly bins, and, given that there are a relatively small number of data points to fit, we fit a local linear regression to the data. Figures 10 and 11 present these results. With the exception of overall property crimes for males, one test out of 13, there is little evidence of a discontinuous increase in the share of victims who are local residents at age 21 for any of our crime types or for the crime aggregates. Taken as a whole, our reading of the evidence, both from Dallas and the NCVS, is that the effect of the MLDA on victimization is unlikely to be an artifact of geographic sorting.
Sample Selection Test: Male Victims, Dallas Subsample
Notes: This figure contains local quadratic regressions of relative age (14 day bins) on the share of male victims who are local to Dallas. 95 percent confidence intervals are included. Burglary is not included as visitors to Dallas cannot be burglarized. Homicide and sex crimes are not included do to a large number (26 and 71, respectively) of undefined bins. All regressions use a two-year bandwidth.
Sample Selection Test: Female Victims, Dallas Subsample
Notes: This figure contains local quadratic regressions of relative age (14 day bins) on the share of female victims who are local to Dallas. 95 percent confidence intervals are included. Burglary is not included as visitors to Dallas cannot be burglarized. Homicide is not included do to a large number (89) of undefined bins. All regressions use a two-year bandwidth.
4. Other robustness checks
We conduct several additional robustness tests. First, we consider the possibility that the results reported in Section V.A might be driven disproportionately by one of the eight cities in our sample and thus might be sensitive to the removal of any one of these cities from the data. In Online Appendix Tables A3 and A4, we reestimate our preferred models, those that use a quadratic polynomial and are reported in Column 2 of Tables 2 and 3, dropping one city at a time from our data. In all cases, estimates are remarkably insensitive to the exclusion of any one of our eight cities. This analysis is also helpful in addressing the possibility that legal access to recreational marijuana in Denver or medical marijuana in San Diego, both of which occur at the age of 21, is confounding our results. Dropping either (or both) of these cities from the analysis has no substantive impact on point estimates for any of the crimes we study. Given the link between crime and access to gambling (Gazel, Rickman, and Thompson 2001; Grinols and Mustard 2006), we also consider whether our results might be an artifact of the fact that, in most states, the minimum legal age to gamble at a casino is 21. To address this, we focus on Milwaukee and San Diego, the two cities in our sample in which the legal age to gamble in a casino is below the age of 21. We report estimates for this subsample in Online Appendix Table A5. While the estimates are less precise given that the sample is smaller, they are substantively similar to our preferred estimates.
Next, we show that the increase in victimization that we observe at age 21 is unique and is not present at other ages that are, to first order, unaffected by the MLDA. Figures 12 and 13 present RD treatment effects graphically for each age between 19 and 35, using an order-two polynomial. In the figure, age is plotted on the x-axis, and the IRR bounded by a 95 percent confidence interval is plotted on the y-axis. Graphs are presented for estimates that were significant at conventional levels in Tables 2 and 3. In each graph, the treatment effects cluster around an IRR of one, indicating that there is no average treatment effect of legal access to alcohol at ages other than 21. Critically, in all cases, the treatment effect at age 21 is the largest among all of the ages estimated, which indicates that the RD effect at age 21 is unusual and therefore provides key support for the prior estimates.
Placebo Test of Regression Discontinuity Effect on Male Victimization
Notes: This figure contains IRR estimates for the RD effect of the MLDA on male victimization for each age from 19 to 35. Regressions include a second-order polynomial in age fully interacted with an indicator for age over the cutoff age, as well as an indicator for the exact birthday of the cutoff age. All regressions use a two-year bandwidth.
Placebo Test of Regression Discontinuity Effect on Female Victimization
Notes: This figure contains IRR estimates for the RD effect of the MLDA on female victimization for each age from 19 to 35. Regressions include a second-order polynomial in age fully interacted with an indicator for age over the cutoff age, as well as an indicator for the exact birthday of the cutoff age. All regressions use a two-year bandwidth.
Finally, we test for whether our estimates are robust to different functional forms. We begin by reestimating results using least squares regression (Online Appendix Tables A6 and A7) and negative binomial regression (Online Appendix Table A8). Next, we note that our primary estimates aggregate victimizations by relative age across our entire sample of cities. In Online Appendix Tables A9 and A10, we instead aggregate by the city × relative age bin, including city fixed effects in the model and clustering standard errors by relative age.18,19
C. Extensions
Having considered the robustness of our main results, we next consider two extensions that provide further context for these results. First, we consider the potential mechanisms through which legal access to alcohol increases crime victimization. Next, we consider the extent to which crime victimization rises, in general, around an individual’s birthday—whether that birthday is an individual’s 21st or not.
1. Location of victimization
There are two primary mechanisms through which legal access to alcohol might affect victimization: exposure and vulnerability. By exposure, we are referring to the change in alcohol access that occurs at age 21, understanding that even though minors regularly access alcohol before reaching the MLDA, the ease through which alcohol can be accessed changes at age 21 (Carpenter and Dobkin 2009). By vulnerability, we are referring to the change in the ways in which alcohol is consumed at the MLDA, independent of any change in exposure. In particular, does legal access to alcohol increase victimization by shifting the location of problematic drinking (for example, drinking in bars of nightclubs), or does legal alcohol access operate primarily by increasing alcohol use?
To better understand the mechanisms through which the MLDA affects victimization, we estimate treatment effects separately for crimes that occur in residential versus nonresidential locations. Location information was shared by the following five police departments in our subsample: Dallas, TX; Denver, CO; Houston, TX; Milwaukee, WI; and St. Louis, MO.20 In Table 5, we report effects for residential and nonresidential crimes, both with (Columns 3 and 4) and without (Columns 1 and 2) a control variable for the birthday celebration effect. As in previous analyses, we further disaggregate results by crime type and gender. For males, effects on violent victimization are, on the whole, driven by crimes that occur in nonresidential locations. This is especially true for assaults and also, to a lesser extent, for robberies.21 Effects on property victimization vary less by location type. For females, the large effects for sex offenses are likewise driven by nonresidential locations, while effects for larceny are equally large in both location types. Taken as a whole, the data suggest that increases in victimization are, at least to an extent, driven by the fact that alcohol use is more likely to occur in nonresidential settings after individuals have reached the legal drinking age.
Poisson Regression Discontinuity Effects—Residential versus Nonresidential
More broadly, some types of crimes, for instance burglary, might largely capture the exposure effect. While the effect of the MLDA is large and significant for burglary, this point estimate is considerably smaller than the point estimate for the most social costly crimes. This suggests that while exposure could account for some of the impacts on sexual assaults, it likely would not account for the majority of the estimated impacts.22
2. Birthday celebration effects
A large literature in public health establishes that individuals are more likely to consume alcohol in both public and private on their birthdays—especially at age 21 (Neighbors et al. 2005; Brister, Wetherill, and Fromme 2010). Until this point, we have conditioned on the period of time just around a victim’s birthday in order to identify the effect of the MLDA more reliably. In this section, we investigate whether there are “birthday effects,” that is, a general increase in victimization on or around an individual’s birthday, independent of an intercept shift in the incidence of victimization that occurs at age 21 and endures in the ensuing weeks and months.
We estimate birthday effects by adding three different sets of birthday-related indicators to our main RD models—an indicator for an individual’s birthday, an indicator for an individual’s birthday and the following three days, and an indicator for the week around an individual’s birthday.23 Table 6 presents Poisson estimates of the change in the likelihood of victimization on or around an individual’s birthday; these estimates are derived from the same model used to estimate effects of the MLDA in Tables 2 and 3 in which we controlled for birthday effects.24 The first three columns present estimates for males, the next three columns for females. Each column corresponds to a different definition of the birthday celebration window. Birthday celebration effects are very large—overall, men are nearly 30 percent more likely to suffer a violent victimization and 10 percent more likely to suffer a property victimization on or around their birthdays. Effects are similar for women. Both genders are more likely to be assaulted. For women, sexual assault effects are particularly large, with a 60 percent increase in the likelihood of suffering a sexual assault on one’s birthday.25
Poisson Birthday Effects
VI. Conclusion
A large body of research has explored the causal determinants of criminality. While victimization is an equally important side of the same coin, due to data constraints, this topic has received far less attention in the literature. Given that recent media attention and research related to criminal justice highlight the high social costs of overpolicing (Fagan et al. 2016) and the widespread application of harsh prison sentences (Aizer and Doyle 2015), there is increasing appeal to understanding whether other policies can affect crime while potentially imposing fewer costs.
We study one prominent policy lever that operates through private precaution and that could plausibly have an outsize influence on victimization: legal access to alcohol. We construct a novel administrative data set that contains the exact date of birth and date of victimization for crime victims in eight large cities in the United States and use a regression discontinuity design to estimate the change in victimization that occurs at age 21, the MLDA in the United States. We find evidence that victimization increases at age 21 for both males and females, though in subtly different ways. Males experience a greater number of assaults and robberies; females experience a large increase in the risk of a sexual assault. Victims of both genders experience a modest increase in the incidence of property crimes. Results are robust to empirical specification, bandwidth selection, and controls for birthday celebration effects.
The likely mechanisms behind these increases in victimization are varied and include differences in the amount of alcohol that is consumed after reaching the legal drinking age and differences in the environment in which alcohol is consumed. Given that effects are largest in nonresidential locations, there is some evidence for the latter of these two mechanisms. Effects do not appear to be an artifact of increased reporting of crimes at age 21.26
This research provides some of the first causal evidence that alcohol increases crime victimization. Our findings suggest that prior estimates based on arrests (Carpenter and Dobkin 2015) or criminal charges (Hansen and Waddell 2018) likely underestimate the effect of alcohol on total crime. Our findings can also potentially reconcile the reason why regression discontinuity based estimates of arrests using the MLDA are typically smaller than recent differences-in-difference estimates (Anderson, Crost, and Rees 2017). The local average treatment effect (LATE) of the former is based on criminality, and the LATE of the latter is based on the combination of victimization and criminality. Our LATE identifies the impact of the MLDA on victimization alone. Finally, these findings provide additional insights into the complex and controversial relationship between alcohol and sexual assault (Lindo, Siminski, and Swensen 2018). In particular, while both Carpenter and Dobkin (2015) and Hansen and Waddell (2018) fail to find evidence that arrests or criminal charges for rape increase at age 21, we find sexual assault victimization at age 21 increases by nearly 25 percent. Moreover, while Carpenter and Dobkin (2017) find injuries caused by others do not increase for females, their measure is an aggregation of both assaults and sexual assaults. Given the victimization data reveal assaults are many times more common than sexual assaults, it is entirely possible medical visits for sexual assaults might have increased in their sample, but that this increase was nullified by a lack of increase in other assaults. Taken together, these findings are more consistent with a model of crime in which perpetrators of sexual assault seek out vulnerable populations than with a model where sexual assault perpetrators lose their self-control due to increased alcohol use.
More generally, this research highlights the possibility that information interventions that educate the public about its increased risk of victimization and encourage individuals to invest in private precautions to prevent victimization may help mitigate the effects of alcohol access on criminal victimization. Behavioral changes, such as remaining cautious of one’s surroundings, avoiding walking home alone or taking a taxi instead of walking, avoiding violence when faced with conflict, locking one’s door immediately after returning home, and being particular about the degree to which one associates with strangers while drinking, all have the potential to reduce criminal victimization. Ultimately, the degree to which information provision leads to a reduction in victimization will depend on the ability of offenders to substitute an intoxicated for a nonintoxicated victim. While it is possible that motivated offenders might easily identify alternative victims to prey upon, it seems likely that the cost of searching for an alternative victim are higher for sexual assault than they are for common street crimes, such as robbery or motor vehicle theft. To be clear, we are not suggesting a campaign of victim-blaming. On the contrary, information is a means of empowering potential victims to better protect themselves. It is also a means through which public safety interventions can be optimally tailored to achieve maximum impact on social welfare.
The possibility of raising the drinking age to reduce the social cost of alcohol use is a strategy that should be taken with caution as it is unclear whether the United States’ unique cultural relationship with alcohol is a by-product of its drinking age being 21.27 As it stands, our estimates suggest that the increased consumption of alcohol at age 21 is met with additional costs previously not considered. Moreover, there are a number of other policies worth considering that may interact with both exposure and alcohol consumption mechanisms that shift at age 21. These include zoning and licensing, operating hours restrictions, and alcohol taxes.
Moreover, the choices and precautions of individuals could carry externalities to others. As an individual engages in precautions, this has a small effect on the returns and costs of engaging in crime for potential offenders. Aggregated, this would suggest the private supply precautions would be undersupplied relative to what is socially optimal, even if we assumed individuals were privately optimizing. Thus, private precautions like locks, private security cameras, alarms, or GPS antitheft trackers might merit subsidies. Moreover, this is further justification for taxes on alcohol, which have remained largely unchanged in nominal value since the 1990s and whose externality offsetting effects have likely been eroded by inflation (Cook and Durrance 2013). Future research could investigate whether other alcohol control policies, such as taxes, are also effective in reducing victimization.
Footnotes
The authors thank Amanda Agan, Mark Anderson, Monica Deza, Carlos Dobkin, Rhiannon Jerch, Hae Nim Lee, Lars Lefgren, Jason Lindo, Vikram Maheshri, Daniel Rees, and Emily Weisburst for helpful comments that greatly improved earlier versions of this manuscript. They also appreciate helpful comments from seminar participants at the University of Maryland, College Park, and American University, as well as conference attendees at the Economics of Risky Behavior Conference in Bologna, Italy. The authors have nothing to disclose. Interested researchers may inquire about accessing the data via these channels: Charlotte (https://www.charlottemi.org/serviceadministration/city-clerk/freedom-of-information-act-requests/), Dallas (openrecordunit{at}dpd.ci.dallas.tx.us), Denver (DPDRecords{at}denvergov.org), Houston (OpenRecords{at}houstonpolice.org), Milwaukee (mpdopenrecords{at}milwaukee.gov), Kansas City (https://kcmo.mycusthelp.com/WEBAPP/_rs/(S(o33oxgsz04hqrr0yhlsxmu2h))/supporthome.aspx), San Diego (https://sandiego.nextrequest.com/requests/new), and St. Louis (https://stlouismo.govqa.us/WEBAPP/_rs/(S(iotvuue4edqpflp1l0f0kjdq))/SupportHome.aspx).
Supplementary materials are available online at: https://jhr.uwpress.org/.
↵1. We further note that individual choices may result in externalities to others as investments in precaution may change the relative returns of crime to potential offenders.
↵2. A notable exception is a paper by Lindo, Siminski, and Yerokhin (2016), who find no evidence of an effect of legal access to alcohol on motor vehicle accidents in Australia.
↵3. Furthermore, while Carpenter and Dobkin (2017) study emergency department visits and hospitalizations, those data limit them to studying intentional injuries caused by others. This measure is a composite of sexual assault and assault and is likely underpowered to detect increases driven by sexual assaults alone, given the relative frequency of each type of crime. In our data, assaults are roughly 15 percent more common than sexual assaults for female victims. This difference might be larger in medical utilization data. This difference might be larger in medical utilization data, as Sugar, Fine, and Eckert (2004) find while body injury is common in sexual assault, admission to emergency or surgical services happened only in 5 percent of the cases they studied.
↵4. It is important to note that we are unable to identify the subset of victimizations that are cleared by an arrest. It is entirely possible that, in keeping with the literature on offending, there is no significant change in these victimizations after the 21st birthday. This is especially likely if there is an increase in victimizations that involve alcohol at the MLDA. See Spohn and Tellis (2012) for more information.
↵5. Some of the earliest thinking about the role of private precaution in the crime production function can be found in the seminal work of Ehrlich (1973, 1981), who conceive of the “derived demand” for crime as the willingness of market participants to invest in private precautions.
↵6. There are a few very limited exceptions. For instance, some states, such as Wisconsin, permit alcohol use with one’s parents at restaurants.
↵7. Note that not every crime has a person-victim—for example, crimes against businesses. We focus on crimes with a person-victim.
↵8. In total, we successfully reached out to 22 police departments. We received no reply from municipal law enforcement agencies in the following cities: Cincinnati, OH; Cleveland, OH; Detroit, MI; Memphis, TN; Nashville, TN; Washington DC; Atlanta, GA; Sacramento, CA; Tuscon, AZ; Cambridge MA; Baton Rouge, LA; Seattle, WA; and Las Vegas, NV. The following departments declined our request for data: Baltimore, MD; Miami, FL; Orlando, FL; Philadelphia, PA; Boston, MA; Columbus, OH; Portland, OR; Phoenix, AZ; and Newark, NJ. We used data from every city that supplied us with data and did not exclude data from the analysis for any reason.
↵9. In a deviation from the index crime designation, this category includes both aggravated and simple assaults, but not sexual assaults.
↵10. While specific offense types vary by city, we include the following offenses in our sexual assault aggregate: fondling, rape, sexual assault or battery, and sodomy. See Online Appendix C for the universe of sex offenses by police department.
↵11. See Online Appendix D for department-specific date ranges.
↵12. Homicide is not included in this figure as all victims are deceased and are therefore unavailable to complete the survey.
↵13. Note that the age profile of male sex crime victimization follows an unusual distribution. This is because there were so few male urban respondents to the NCVS who reported being a victim of a sex crime (54 total respondents over the ten years of the survey).
↵14. Following a persuasive argument put forth in Osgood (2000), our default model is Poisson regression as it makes assumptions about error distributions that are consistent with the nature of event counts. Sometimes crime counts are modeled using negative binomial regression models due to concerns about overdispersion in the data. We prefer Poisson regression for two reasons. First, tests for overdispersion do not distinguish between overdispersion and misspecification—see Berk and MacDonald (2008) and Blackburn (2015). Consequently, it is a priori unclear when overdispersion actually exists and is consequently an issue. Second, Poisson regression is first-order equivalent to negative binomial regression when robust standard errors are used—as we do Wooldridge (2010).
↵15. We also estimate our models including an interaction between our birthday effect variables and the indicator for age over 21. Results are unchanged.
↵16. Indeed if we study sexual assault and assault aggregated together, we estimate a 1 percent increase in this combined crime category, which is similar in size and precision to their estimates.
↵17. We report the number of survey respondents in each crime type by age by gender bin in Online Appendix F.
↵18. Similar robustness checks for birthday celebration effects can be found in Online Appendix Tables A11 and A12.
↵19. We also reestimate our RD models using local linear regressions, which we present in Online Appendix Tables A1 and Table A2. In all cases, estimates are quantitatively and qualitatively similar to our preferred estimates.
↵20. Online Appendix E contains the department-specific location tags that we consider to be “residential.”
↵21. The same is true for sex offenses though sparse data means that the results are estimated with only limited precision.
↵22. In Online Appendix Table A13, we consider whether effects vary according to whether local universities are in session. This could be a potentially important source of heterogeneity in our estimates if college students are especially likely to be inframarginal actors with respect to the MLDA. While we cannot perfectly disambiguate between the availability of college students and seasonality more generally, the table provides little evidence that effects vary along this dimension.
↵23. All birthday effects are estimated with a quadratic polynomial in age interacted with an indicator for being 21 or older at the time of victimization.
↵24. Online Appendix Table A11 reports log-linear estimates of the birthday effect.
↵25. In order to investigate whether the birthday celebration effect is unique to age 21, we reestimate birthday celebration effects (using the exact birthday) for all ages between 19 and 35. These estimates are presented in Online Appendix Figures A3 and A4, which plots incidence rate ratios on the y-axis against the victim’s birthday in years on the x-axis. These figures support the idea that birthday celebration effects are not unique to age 21 and are instead universal, persisting throughout an individual’s life.
↵26. The effects of legal access to alcohol that we report here are qualitatively large and empirically important. However, these estimates potentially point to an even larger role of alcohol use in crime victimization. To see this, consider that the reduced form estimates reported in this paper can be seen as intent-to-treat estimates of the effect of alcohol use, understanding that alcohol will tend to change discontinuously, albeit imperfectly, with legal access to alcohol. The magnitude of the effect of alcohol use on victimization will thus depend on the first-stage relationship between the MLDA and alcohol use. Thus, subject to an assumption that the MLDA affects victimization only through the increased use of alcohol, our results can be seen a conservative estimate of the aggregate impact of problematic alcohol use on crime victimization.
↵27. If this is the case, a policy that raises the drinking age might have a negative general equilibrium impact on the binge-drinking culture that is common in the United States.
- Received July 2020.
- Accepted April 2021.
