Are Drug-Free School Zones Effective? Evidence From Matching Schools and School-like Entities

Abstract

Using a combination of spatial and statistical analysis, this paper focuses on analyzing the effectiveness of drug-free school zones (DFSZ) around K-12 schools in Los Angeles County. A propensity score matching model is employed to match schools and school-like entities to compare the amount of drug crimes in two distinct 1000-foot buffers surrounding them. The model is then compared to a coarsened exact matching model. The average treatment effects (ATE) and average treatment effects on the treated (ATT) are estimated. Our results indicate that there are 2.7 and 1.7 fewer drug crimes and non–marijuana-related drug crimes respectively near schools, as a result of the policy. The total effect of the policy is estimated to reduce drug crime near schools by between 1065 to 1643 fewer incidences per year. Furthermore, we find no significant differences in gang-related drug crimes, gang-related violent crimes, or property crimes as a result of the policy.

Introduction

America has a long history of medicinal and recreational drug use dating back to its inception. Many of today’s illicit drugs were often used to treat common health issues. For example, cocaine was commonly used to treat toothaches and heroin was used for asthma. The first drug control law in the United States dates back to the late 1800s, known as The San Francisco Den Ordinance of 1875, which was passed to stop the spread of opium dens (Drew, 2015; Editors, n.d.). Not long after, the first federal regulations of drugs began in the early 1900s, with the passage of The Pure Food and Drug Act in 1906 and The Smoking Opium Exclusion Act in 1909. However, it was not until the perceived debauchery of the 1960s, an era of recreational drug use that encouraged experimentation with newer drugs like lysergic acid diethylamide (LSD), marijuana, and cocaine, that set off the drastic increase in drug regulation (Berridge & Bourne, 2005).

The War on Drugs officially began in the early 1970s when President Nixon declared drug abuse to be “public enemy number one” and, in response, increased funding for drug-control agencies, created the Drug Enforcement Administration (DEA), and proposed mandatory minimum sentencing laws for drug crimes. The Reagan administration in the 1980s followed suit by reinforcing and expanding on The War on Drugs initiative. One such contribution was the passing the Anti-Drug Abuse Act of 1986, which created mandatory minimum prison sentences on certain drug offenses and established the “schoolyard” law making it a federal offense to distribute drugs within 1000 feet of a school (Editors, n.d.).

Gradually, all 50 states adopted some form of drug-free school zone (DFSZ) laws, though they differ in the zone size, covered locations, covered offenses, and penalties. For example, Alabama has the largest DFSZ setting a boundary of 15,460 feet (approximately three miles) from all schools, colleges, and public housing projects. This has led to 73% of the entire state being covered by drug-free school zones (Fractl, 2020). Massachusetts has the smallest drug-free zoning size of 100 feet around parks and 300 feet around schools and preschools. However, a majority of states have kept the standard size for these zones at 1000 feet. The type of locations or entities that are protected by the zones also vary greatly across states and include places such as schools, school buses, parks, churches, day care centers, movie theaters, libraries, ball parks, youth centers, public pools, arcades, public housing, mental health facilities, etc. The type of offenses covered under these laws are typically for the sale, distribution, manufacturing, or possession of certain illicit drugs, and many of the penalties include enhanced fines and/or increased minimum mandatory sentencing terms as well as limits on parole eligibility (Porter & Clemons, 2013). The main objective of drug-free school zone laws is to reduce drug crimes where children are present in order to protect them from being exposed or involved in drug-related activities and secondly, to reduce drug use overall.

Unintended Consequences

Though the intention of the DFSZ laws to protect children is a good one, adverse consequences of these laws have been called into question over the last two decades. Conversations regarding the extent of coverage of zones and racial disparities in who receives the harsher penalties are commonplace and have encouraged lawmakers to reevaluate specifications of DFSZ laws that may be problematic. One study that has inspired these conversations, performed by Ciarmella and Krisia with The Ready Foundation, employs spatial analysis to analyze the DFSZ in Tennessee. They demonstrate that the geographic proximity of protected entities created a blanket of coverage much larger than intended. The result is only a small amount of cumulative space where the DFSZ laws do not apply. The authors highlight the point that “States created drug-free school zones thinking that the threat of Draconian prison sentences would keep dealers away from schools. But the very size of these zones undercuts the premise” (Ciaramella & Krisai, 2017, p. 23). Furthermore, since the implementation of DFSZ laws, many states have applied protections that expand beyond just K-12 schools to include places like parks, churches, daycare centers, etc. The problem with expanding these laws, and setting arbitrary zone sizes across entire states, is that they can create expansive areas of coverage where the DFSZ laws apply. This no longer separates out the immediate vicinity around schools as “special areas” to deter criminals away from, making the real-world impact of these laws out of line with their original intent.

The issue of geographic coverage is exacerbated in dense urban areas where protected entities are much closer together and entire cities may be nearly covered by DFSZ laws, essentially making them “zoned out” for drug crime. An example of this comes from a case study done in 2004 which analyzed Drug-Free Zones in three large cities in Massachusetts, where at the time the zone parameters for DFSZ were set at 1000 feet (Brownsberger, Aromaa, Brownsberger, & Brownsberge, 2004). The study showed that the zones “cover 29% of the areas of the study cities and 56% of the high-poverty areas within the cities. Although less than 1% of the drug-dealing cases involved sales to minors, approximately 80% of cases occurred within school zones, apparently because of the density of schools in high-poverty/high-drug-dealing areas” (Brownsberger et al., 2004, p. 1). This study along with increased drug incarceration rates, costs, and racial disparities led policymakers in Massachusetts to reevaluate the DFSZ laws and by 2012 passed legislation to reduce the zone size to 300 feet around protected entities.

The prevalence of DFSZ in dense urban areas can also lead to further racial disparities in the justice system, since minorities are more likely to live in dense urban areas compared to Whites who are more likely to live in suburban or rural areas where the zones are less prevalent (Ciaramella & Krisai, 2017; Greene, Pranis, & Ziedenberg, 2006; Parker et al., 2018). New Jersey, for example, has one of the highest proportion of prisoners incarcerated for drug offenses where an alarming 96% of them are Black or Hispanic (Greene et al., 2006). The increased use of imprisonment for drug offenders comes with large fiscal impacts to not only the state, but also to the communities of color that are disproportionately impacted by the laws. Interestingly, New Jersey did not experience less drug use compared to states with a more moderate use of incarceration for drug offenses (Schiraldi & Ziedenberg, 2003).

Another issue with having expansive drug-free school zones is that it makes it increasingly difficult for offenders to distinguish where drug-free zones end. This is especially true in dense urban areas with many overlapping boundaries or when houses or other structures obstruct the direct line of sight to the school. Without clearly marked signage indicating the area is within a school zone, many offenders are not aware that committing a crime, even when blocks away from a school, has greater penalties attached. For this reason, critics of the drug-free school zone laws argue that smaller school zones which are more easily estimated by potential offenders would be more effective in deterring drug crimes away from the zoned areas and better serve the intended purpose of the law (Ciaramella & Krisai, 2017; Greene et al., 2006).

From a sociology perspective, the DFSZ laws can be problematic as some criminal sentencing from the law can be considered unreasonably harsh. For example, many of the laws dictate mandatory minimum sentencing ranging 3–5 years and revoked possibility of parole. This can perpetuate other issues in the criminal justice system such as prison overcrowding, skewed effects on economically disadvantaged offenders, higher recidivism, hasher punishments for minorities, and hindering rehabilitation efforts (Greene et al., 2006; Schiraldi & Ziedenberg, 2003; The Illinois Disproportionate Impact Study Commission, 2010). One example that powerfully illustrates the distorted consequences of the DFSZ laws is the case of Jordan Peters, who was only 20 at the time of his conviction after he was arrested for selling mushrooms to a police informant:

“Peters had no prior criminal history, but because the $80 drug transaction happened 587 feet from an elementary school, he received a mandatory 15 years in state prison. He will not be released until 2027” (Ciaramella & Krisai, 2017, p. 39).

Not only did Peters not have a criminal history, but he was purposefully lured into selling the drugs to an informant, which has resulted in him spending much of his youth behind bars. This supports the final argument of critics who claim that the DFSZ laws do not work as intended and are grossly misused by law enforcement (Ciaramella & Krisai, 2017; Greene et al., 2006). Police officers have been known to use undercover tactics posing as interested drug buyers near schools in order to get mandatory or increased punishments for the perpetrators provided by the zones, which is in direct conflict with what the laws are meant to deter—exposure to children of drug-dealing near schools (Ciaramella & Krisai, 2017). Drug-free school zone laws are also widely used as effective leverage tools, threatening increased mandatory jail time, to coerce offenders into accepting terms of a plea bargain prior to being proven guilty in a court of law. Analysis of court outcomes in Connecticut revealed that 90% of those arrested on mandatory drug charges, a majority of which were in urban school zones, were convicted on a lesser charge (Kajstura, 2014). The court outcome data in the report for Connecticut further showed a lack of deterrence as the number of arrests for mandatory minimum drug offenses increased between 2000–2004 (Greene et al., 2006; Kajstura, 2014). These plea agreements and the pattern of justice served do not accomplish the goals that the DFSZ laws intend to promote and skew the understanding of reasonable consequence.

Contribution

There seems to be a consensus in research literature that unintended adverse consequences of DFSZ laws exist and are measurably large. However, from a cost-benefit perspective, it is equally important to analyze whether or not these laws are effective at achieving their primary goal. If these laws do provide deterrence of drug crime nears schools, then policy makers need to compare the social benefits to the social costs of these laws to determine if they need revision or elimination. Currently, however there is a lack of research focused on measuring the effectiveness of these laws and any benefits they provide.

Thus, an essential question to answer in furthering the debate on the revision of the DFSZ laws is do these policies reduce crime near schools at the current and most common 1000-foot regulated zone, and if yes, by how much? Examining this question will provide a better understanding of the benefits provided by the current DFSZ policies and is the focus of this paper. We attempt to answer this research question by analyzing the effectiveness of a specific drug-free school zone law through a combination of geospatial analysis and statistical matching techniques. Thus far, there is limited spatial research on the topic of drug-free school zones. Most of the spatial analyses that have been done focus on mapping drug-free school zones in order to calculate the percentage of land mass they cover or use crimes counts in entire census tracts (Brownsberger et al., 2004; Ciaramella & Krisai, 2017; Greene et al., 2006), our analysis is superior in that we measure crime counts within the exact area covered by the DFSZ policy and the area directly outside of it.

This study focuses on Los Angeles County, California which offers a wide range of demographics and a sizable population. The DFSZ law for California falls under the California Health and Safety Code 11,353.6 and is formally known as the Juvenile Drug Trafficking and Schoolyard Act of 1988. It mandates adult defendants (18+ years old) have additional penalties of 3–5 years for offenses that occur within 1000 feet of any K-12 public or private school during school hours where children are expected to be present. The law applies to offenses for possession with intent, delivery, sale, or manufacture of certain drugs including cocaine base, stimulants that impact the central nervous system, and opium derivatives. The enhanced penalties of the DFSZ law does not apply to marijuana offenses.

Method

To identify the potential deterrent effect of the DFSZ law on crime in Los Angeles County, we compare the amount of crime that occurs near schools to the amount of crime that occurs near entities resembling school-settings where children are commonly present, but where the DFSZ laws do not apply, which we refer to as non-schools. Non-school entities include places such as after school tutoring centers, YMCAs, libraries, recreation and community centers with youth programming, and head-start/preschool programs not located on a K-12 school campus. Our basic strategy is to count the number of crimes that occur near each school and non-school and then match schools to similar non-schools to determine if the DFSZ law generates a difference.

Formally, let $y_{i r}^{S}$ be the number of crimes that occurs within a radius of r of location i. Here, S is a binary variable that equals one for schools and zero for non-schools. If we are interested in the effect of the DFSZ law if it were applied to all entities, we are interested in the average treatment effect (ATE). Using the potential outcomes framework, ATE is

ATE = E (y_{i r}^{S = 1} - y_{i r}^{S = 0}) .

(1)

However, if we are interested in the effect of the policy on the amount of crime near schools, we are interested in the average treatment effect on the treated (ATT), which is

ATT = E (y_{i r}^{S = 1} - y_{i r}^{S = 0} | S_{i} = 1) .

(2)

Unfortunately, we only observe either $y_{i r}^{S = 1}$ or $y_{i r}^{S = 0}$ for a given entity i, known as the fundamental problem of causal inference. As a result, the observed amount of crime is

y_{i r} = S_{i} y_{i r}^{S = 1} + (1 - S_{i}) y_{i r}^{S = 0} .

(3)

The issue is that schools and non-schools may be systematically different. Therefore, we cannot simply compare the average amount of crime near schools to the average amount of crime near non-schools.

To determine the effect of the policy we must employ a method for specifying an appropriate comparison, or control, group for schools. That is, we must determine what the number of crimes would have been absent the policy. To do so, we use non-schools that are otherwise similar based on a rich set of observable characteristics, X. In other words, we must compute the ATE and ATT using data that are balanced based on observable factors. Specifically, we employ propensity score matching. Under the assumptions of strong ignorability, $(y_{i r}^{S = 1}, y_{i r}^{S = 0}) ⊥ S_{i} | X_{i}$ , and non-zero probability of treatment, $0 < \Pr (S_{i} = 1 | X_{i}) < 1$ , Rosenbaum and Rubin (1983) showed that treatment assignment is also strongly ignorable conditional on the propensity score $e_{i} \equiv \Pr (S_{i} = 1 | X_{i})$ , $(y_{i r}^{S = 1}, y_{i r}^{S = 0}) ⊥ S_{i} | e_{i}$ . As a result, matching treated and untreated observations based on the propensity score leads to unbiased estimates of the ATE and ATT. In practice, we estimate the propensity score using logistic regression

\ln [\frac{\Pr (S_{i} = 1 | X_{i})}{1 - \Pr (S_{i} = 1 | X_{i})}] = X_{i}^{'} β .

(4)

We then match non-schools to schools based on the predicted probabilities, or propensity scores. Finally, the calculations of the ATE and ATT are made using the matched sample. Specifically, we use nearest neighbor matching. The estimation of the ATE requires the potential outcome for each observation, school and non-school; thus, we match every school with the non-school that has the closest estimated propensity score and we match every non-school with the school that has the closest propensity score. The estimation of the ATT only requires the potential outcomes for schools; therefore, we only match each school to the non-school with the closest propensity score.

While propensity score matching is a very common method for causal inference in many disciplines, some scholars suggest there are better methods for creating covariate balance, and that propensity score matching may actually increase imbalance (King & Nielsen, 2019). One commonly suggested alternative is to use coarsened exact matching (Iacus, King, & Porro, 2012). Ideally, one would like to create exact matches between treated and untreated observations based on the covariates, called exact matching. However, this is very implausible, especially with continuous covariates, as we have in our data. Rather than trying to reduce the covariate space to a single measure, like in propensity score matching, we can initially make our variables coarser, or create bins, then exactly match based on the coarsened data. In practice, we coarsen the data and create strata based on the coarsened covariates. We then drop any observations that lie in strata without at least one school and one non-school. The remaining data are the matched sample. However, recent research suggests that coarsened exact matching, while achieving good covariate balance, may discard too many observations, leading to bias and less precise estimates (Black, Lalkiya, & Lerner, 2020; Ripollone, Huybrechts, Rothman, Ferguson, & Franklin, 2020). As a result, we focus our discussion on the results from propensity score matching and present coarsened exact matching results for comparison.

The applicability of any matching method depends on the assumption of strong ignorability, see above. Another way to state the assumption is that treatment assignment is not affected by any unmeasured variables, sometimes referred to as the no unmeasured confounders assumption. In our case, we must assume that there are no unobservable differences between schools and non-schools that affect the amount of drug-related crime. In other words, non-schools are an appropriate comparison, or control group, conditional on the observed covariates. That is, the amount of crime occurring near non-schools is a measure for the amount of crime that would occur near schools with similar levels of the covariates absent the DFSZ policy. As a result, the covariates we consider are population density, population counts by sex and age, education level, race, poverty, renter/owner-occupied housing, unemployment, female-headed households, and single-parent households. These are described in more detail in the Data section below. Furthermore, matching methods require overlap in the raw data. Since observations are matched based on observed covariates, there must be a degree of overlap between schools and non-schools for matches to be made. We examine the degree of overlap in the raw data in the Results section.

Data

The study area points of interest include all public and private K-12 schools as well as non-schools in Los Angeles County. All points of interest data were obtained from the Los Angeles County ArcGIS Hub. Crime data across 5 years (2012–2016) for the county was collected from the Los Angeles County Sheriff Department GIS Data Portal as public crime data records. The data portal disclaimed that for privacy and protection purposes actual crime locations have been slightly moved but remain within the same block. The schools and non-school entities are compared to each other for analysis within two buffer zones: 0–1000 feet, where the DFSZ laws apply only to schools, and 1000–2000 feet where no DFSZ laws apply.

Crime data for the county was sorted into six categories: (1) all drug crimes, (2) drug crimes for which the DFSZ law applies (namely, those excluding marijuana offenses), (3) gang-related drug crimes, (4) gang-related violent crimes, (5) violent crimes, and (6) property crimes. Violent crime is comprised of the following four offenses: aggravated assault, homicide, forcible rape, and robbery. Property crime is comprised of burglary, larceny theft, motor vehicle theft, and arson.

The first two crime categories are used to determine if there is in fact a difference in drug crime near schools. Category 3 is included due to the correlations that often exist between gangs and drug activity, especially in Los Angeles County (Howell, Decker, & U.S. Department of Justice Office of Justice Programs, Office of Juvenile Justice Delinquency Prevention, 1999). It allows us to determine whether or not differences in drug crimes between schools and non-schools are gang related. We include categories 4 and 5 due to the relationship between drug crimes and violent crime (Decker, Katz, & Webb, 2008; Duke, Smith, Oberleitner, Westphal, & McKee, 2018; Martínez, Rosenfeld, & Mares, 2008). The hypothesis is that if there are differences in drug crimes, we expect to also observe differences in violent crimes. More specifically, we would expect to see smaller differences in violent crime compared to drug crime. For example, if there are differences in drug crimes and gang-related drug crimes, we would expect differences in violent crime and gang-related violent crime, respectively. Similarly, if there are no differences in drug crime, we would expect no differences in violent crime, as the policy targets drug crime. Lastly, we use category 6 to determine whether there are any overall differences in crime between schools and non-schools. For example, if the policy is ineffective, but crime in general is different between schools and non-schools, we would see differences in drug crimes that are not the result of the policy. As a result, if the policy is effective, we would observe less drug crimes near schools and a significantly smaller impact, or no impact, on property crime.

Crime points in the six categories were summed within each of the two buffer zones for all schools and non-schools. Demographic and covariate data was collected at the block group level from the US Census Bureau through the ESRI Online ArcGIS and Simply Analytics platforms. There are a total of 3012 schools and 990 non-schools in the data. Table 1 displays descriptive statistics for the sample . All of our covariates are measured as proportions of the population, with the exception of the following three variables: population, population density, which is persons per square mile, and median household income. For our poverty measure, we use the proportion of the population with income levels below the poverty threshold over the last 12 months.

Table 1.

Descriptive Statistics.

Variables	Full sample	Schools	Non-schools
Drug crimes (0–1000 ft)	9.965 (24.34)	9.063 (22.00)	12.71 (30.20)
Drug crimes (no marijuana) (0–1000 ft)	6.732 (17.69)	6.027 (15.99)	8.875 (21.95)
Violent crimes (0–1000 ft)	7.681 (20.71)	6.967 (18.39)	9.853 (26.43)
Gang-related drug crimes (0–1000 ft)	.706 (2.503)	.649 (2.433)	.879 (2.700)
Gang-related violent crimes (0–1000 ft)	1.199 (3.787)	1.094 (3.550)	1.520 (4.416)
Property crimes (0–1000 ft)	29.86 (64.42)	28.83 (59.70)	33.00 (76.98)
Drug crimes (1000–2000 ft)	29.21 (60.60)	27.16 (58.90)	35.47 (65.12)
Drug crimes (no marijuana) (1000–2000 ft)	21.02 (44.75)	19.38 (43.14)	26.02 (49.01)
Violent crimes (1000–2000 ft)	23.00 (52.75)	21.90 (52.76)	26.35 (52.58)
Gang-related drug crimes (1000–2000 ft)	2.262 (6.399)	2.130 (6.335)	2.664 (6.575)
Gang-related violent crimes (1000–2000 ft)	3.636 (9.776)	3.449 (9.729)	4.205 (9.902)
Property crimes (1000–2000 ft)	87.21 (157.8)	85.97 (155.0)	90.96 (166.3)
Population	1746 (882.4)	1754 (904.7)	1722 (810.9)
Population density	11,586 (8,829)	10,946 (8,389)	13,534 (9799)
Less than HS	.252 (.197)	.232 (.192)	.313 (.200)
HS	.198 (.0911)	.195 (.0912)	.208 (.0902)
Bachelor’s	.180 (.128)	.190 (.129)	.149 (.120)
Black	.0933 (.149)	.0904 (.148)	.102 (.153)
Asian	.139 (.162)	.142 (.161)	.131 (.165)
White	.504 (.197)	.517 (.200)	.463 (.184)
Hispanic	.491 (.299)	.466 (.297)	.569 (.292)
Female poverty	.102 (.0698)	.0947 (.0665)	.125 (.0744)
Male poverty	.0869 (.0630)	.0807 (.0604)	.106 (.0667)
Median household income	68,988 (37,020)	72,844 (37,945)	57,255 (31,266)
Males	.490 (.0306)	.490 (.0271)	.493 (.0395)
Owner occupied	.486 (.275)	.513 (.273)	.402 (.262)
Males unemployed	.127 (.0669)	.124 (.0642)	.134 (.0739)
Females unemployed	.126 (.0683)	.121 (.0647)	.139 (.0765)
Single parents w/child	.201 (.100)	.192 (.0963)	.230 (.107)
Female households no husband	.245 (.0956)	.236 (.0925)	.271 (.0998)
18–24 year olds	.106 (.0528)	.104 (.0472)	.114 (.0666)
25–34 year olds	.147 (.0520)	.144 (.0524)	.154 (.0502)
Males 15–24 years old	.0700 (.0400)	.0689 (.0386)	.0731 (.0438)
Observations	4002	3012	990

Note. Means with standard deviations in parentheses.

The average number of drug-related crimes occurring within 1000 feet of a location is 9.97 and displays great variability with a SD of 24.3. Non-schools average more drug crimes in the 0–1000-foot radius, 9.1 crimes for schools and 12.7 for non-schools. A similar pattern holds for our other five specified crime counts. On average, there is more crime that occurs within the 1000–2000-foot area. The overall average number of drug crimes is 29.2 and is 27.2 for schools and 35.5 for non-schools. Again, a similar pattern holds for the other included crime counts. We discuss further differences in the sample in the next section when we compare the raw data to the matched sample.

Results

We begin by presenting evidence regarding the overlap of observed covariates in the sample. Figure 1 presents density plots for the estimated propensity scores for schools and non-schools. In the left pane of Figure 1, it is clear that there is substantial overlap between schools and non-schools, in the raw data. While the peak of the distribution is at a higher propensity score for schools, as would be expected, the two distributions overlap to a great deal.

Next, we assess the balance created from our propensity score matching method. Balance in the observed covariates between schools and non-schools in the matched sample depends on the joint distributions of the covariates for schools and non-schools. However, since we have several covariates, we follow common practice and analyze lower-dimensional measures focusing primarily on the marginal distributions of the covariates (Ho, Imai, King, & Stuart, 2007). A simple first examination of balance is to assess the similarity in the distributions of the propensity scores between schools and non-schools in the matched sample. Figure 1 displays the density plot for the propensity scores in the matched sample. It is clear that the distributions are extremely similar. However, as noted by Austin (2009b), analyzing the distributions of the propensity scores may be misleading. Thus, we turn our attention to the baseline covariates themselves.

We first look at the baseline covariates’ standardized differences in the raw and matched samples (Rosenbaum & Rubin, 1985), presented in Table 2. All of the standardized differences in the matched sample are below the suggested threshold of 0.10 (Austin, 2009a; Normand et al., 2001; Stuart, Lee & Leacy, 2013), with the largest standardized difference begin 0.072. Next, we examine the variance of each covariate for schools and non-schools. A perfectly matched sample would have equal variances for each of the covariates for schools and non-schools. As a result, we examine the variance ratios for each covariate in the raw and matched samples (Austin 2009a; Imai, King, & Stuart, 2008), also reported in Table 2. The variance ratios are all very close to one, except for three of the covariates, which all have ratios closer to one than in the raw data. Finally, we present density plots for each covariate for schools and non-schools in the raw and matched samples. The results are displayed in Figures 2 –6. The graphical results suggest the nearest neighbor matching on the propensity scores has balanced the observable covariates.

Table 2.

Standardized Differences and Variance Ratios.

Variables	Standardized differences		Variance ratios
Variables	Raw	Matched	Raw	Matched
Population	.037	.072	1.245	1.180
Population density	−.284	.047	.733	1.007
Less than HS	−.417	.016	.918	1.021
HS	−.144	−.010	1.021	.942
Bachelor’s	.330	.005	1.145	1.059
Black	−.079	−.009	.929	.994
Asian	.068	−.020	.943	.907
White	.280	.017	1.178	.966
Hispanic	−.350	.001	1.035	.979
Female poverty	−.436	.005	.800	.981
Male poverty	−.390	.004	.822	.949
Median household income	.448	−.022	1.473	.901
Males	−.080	.007	.471	.614
Owner occupied	.413	−.024	1.086	.978
Males unemployed	−.146	−.033	.755	.859
Females unemployed	−.252	−.017	.717	.866
Single parents w/child	−.374	.016	.804	.926
Female households No husband	−.368	.000	.859	.936
18–24 year olds	−.178	−.010	.502	.523
25–34 year olds	−.202	.025	1.087	.986
Males 15–24 ears old	−.102	−.024	.779	.796

Coarsened exact matching allows us to analyze a different measure of balance. Since the covariates are coarsened, examining the joint distributions in the raw and matched samples is possible. In practice, we can examine the multidimensional histogram for the covariates since we have reduced the dimensions of the histogram from coarsening the data. The measure of balance is the L₁ statistic (Iacus, King & Porro, 2011). The L₁ measure, which is bound between 0 (perfect balance) and 1 (complete imbalance), is not informative in and of itself. Rather it is useful to compare measures between treatment groups to determine if matching has improved overall balance (Blackwell, Iacus, King & Porro, 2009). The L₁ measure for our raw data is 0.796. Following coarsened exact matching, the L₁ measure is $3.67 \times 10^{- 15}$ , which represents a substantial improvement in overall balance.

Our propensity score matching results are reported in Table 3 for the 1000-foot radius that the DFSZ law applies to. The results show significant differences in both drug crimes and drug crimes for which the policy applies (no marijuana-related crimes) between schools and non-schools. If all sites were schools, we would expect a decrease of 2.8 drug crimes and 1.9 non-marijuana-related drug crimes near each site, the ATE. We observe 2.7 and 1.7 fewer drug crimes and non-marijuana-related drug crimes respectively near schools, as a result of the policy, ATT.

Table 3.

Propensity Score Matching Results 0–1000 Feet.

Effect	Drug crimes	Drug crimes (no marijuana)	Violent crimes	Gang-related drug crimes	Gang-related violent crimes	Property crimes
ATE	−2.819*** (1.016)	−1.896*** (.670)	−1.984** (.911)	−0.154 (.0982)	−0.220 (0.138)	−4.489 (3.041)
ATT	−2.727** (1.104)	−1.747** (.700)	−1.745* (.984)	−0.126 (.0899)	−0.166 (0.144)	−4.001 (3.374)

Note. (Abadie & Imbens, 2016) standard errors in parentheses. The matched sample size is 4002 for the ATE and 3012 for the ATT. *** p < .01, ** p < .05, * p < .1.

As mentioned in the Data section, we can further evaluate the policy by examining our other dependent variables. To begin, since we find there are fewer drug crimes near schools, we expect to see fewer violent crimes near schools as well. Table 3 shows that we do find a significant difference in violent crime between schools and non-schools. The ATE and ATT for violent crimes are −1.9 and −1.7 respectively. Next, there are no differences in gang-related drug crimes. As a result, we expect to see no differences in gang-related violent crime, which is what we observe. Lastly, there are no differences in property crime either, suggesting there are no general differences in crime between schools and comparable school-like entities. However, the results presented in Table 3 are difficult to compare across crime categories. As a result, we present standardized effects in Figure 7. The results are consistent with the policy having its intended effect, differences in drug crime, smaller differences in violent crime, and even smaller difference on the other categories. In total, we find differences in drug crime and smaller differences in violent crime. Furthermore, we find no differences in gang-related drug crime, gang-related violent crime or property crime. Thus, we conclude the policy is effective at reducing drug-related crime near schools.

Table 4 reports our coarsened exact matching results for the 1000-foot radius around schools and non-schools. As noted above, the coarsened exact matching method discards many observations, leaving only 625 schools and 537 non-schools in the matched sample. The estimated ATT is −1.8 for drug crimes and −0.9 for non-marijuana drug crimes. While the results are smaller than for our propensity score method, the general conclusion remains that there is less drug-related crime near schools compared to similar non-schools.^1,2

Table 4.

Coarsened Exact Matching Results 0–1000 Feet.

Effect	Drug crimes	Drug crimes (no marijuana)	Violent crimes	Gang-related Drug crimes	Gang-related violent crimes	Property crimes
ATT	−1.768** (0.840)	−0.867 (0.583)	−1.286 (1.031)	−0.0952 (0.0800)	−0.0968 (0.125)	−2.433 (2.473)

Note. Standard errors clustered at the strata level in parentheses, as suggested by Abadie and Spiess (2021). Sample size is 1162; there were 537 non-schools matched in strata with 625 schools. *** p<0.01, ** p<0.05, * p<0.1.

Using our estimated ATT, we can calculate the total effect of the policy on drug crime near schools. There are between 5325 and 8214 less drug crimes near schools over the 5-year period, or 1065 to 1643 fewer per year. Furthermore, we can calculate the ATE on the untreated using our propensity score results, which is −3.1. Therefore, we estimate that if the policy applied to non-school locations there would be a decrease of 3069 drug crimes near these locations for a 5-year period, or 614 fewer per year.

Next, we examine the area from 1000 feet to 2000 feet from schools and non-schools. Propensity score estimates are in Table 5. We find similar results to the 1000-foot radius. There are significant differences in drug crimes and non-marijuana drug crime, ATEs of −3.9 and −3.1 respectively and ATTs of −3.5 and −2.8 respectively. We also find no effects on either gang-related drug crime or gang-related violent crime. However, we have conflicting information from our coarsened exact matching method. The estimated ATTs, reported in Table 6, are all positive and none are statistically different from zero. As a result, we are confident in the conclusion that the policy reduces drug crime near schools; however, the effect may not extend beyond the 1000-foot radius.

Table 5.

Propensity Score Matching Results 1000–2000 Feet.

Effect	Drug crimes	Drug crimes (no marijuana)	Violent crimes	Gang-related drug crimes	Gang-related violent crimes	Property crimes
ATE	−3.860* (2.181)	−3.111* (1.608)	−1.233 (1.692)	−.328 (.224)	−.234 (.337)	−4.762 (5.825)
ATT	−3.525 (2.207)	−2.750* (1.642)	−0.893 (1.773)	−.288 (.242)	−.207 (.350)	−3.054 (6.332)

Note. Abadie and Imbens (2016) standard errors in parentheses. The matched sample size is 4002 for the ATE and 3012 for the ATT. *** p < .01, ** p < .05, * p < .1.

Table 6.

Coarsened Exact Matching Results 1000–2000 Feet.

Effect	Drug crimes	Drug crimes (no marijuana)	Violent crimes	Gang-related drug crimes	Gang-related violent crimes	Property crimes
ATT	2.442 (2.313)	.677 (1.575)	.785 (.934)	.0121 (.182)	.115 (.254)	5.880 (4.099)

The results presented thus far measure crime in counts. However, a useful sensitivity test for our conclusions is to analyze drug crime rates. Therefore, we use drug crimes per 1000 members of the population. Table 7 displays results for all drug crimes and non-marijuana drug crimes. The results are similar to our results using drug crime counts. There is significantly less drug crime near schools, and the results are larger, in absolute terms, for all drug crimes. Also, we see the same conflicting results for the area from 1000 feet to 2000 feet from schools and non-schools between propensity score matching and coarsened exact matching.

Table 7.

Matching Results Using Crime Rates (per 1000 Member of Population).

Effect	0–1000 Feet				1000–2000 feet
	Drug crimes		Drug crimes (no marijuana)		Drug crimes		Drug crimes (no marijuana)
	PSM	CEM	PSM	CEM	PSM	CEM	PSM	CEM
ATE	−2.309*** (.894)		−1.491** (.654)		−3.231* (1.856)		−2.768** (1.327)
ATT	−2.249** (1.002)	−1.083* (.603)	−1.370* (.737)	−.563 (.436)	−2.925 (1.966)	1.740 (1.655)	−2.571* (1.376)	.362 (1.102)

Note. Abadie and Imbens, (2016) standard errors in parentheses for propensity score matching (PSM). Standard errors clustered at the strata level in parentheses, as suggested by Abadie and Spiess, (2021), for coarsened exact matching (CEM). The PSM matched sample size is 4002 for the ATE and 3012 for the ATT. For CEM, the sample size is 1162; there were 537 non-schools matched in strata with 625 schools. *** p < .01, ** p < .05, * p < .1.

Timing of Crime

One concern with our results is that they may be coming from fewer crimes being committed when more people are present. During school hours, there are many people congregated in a single place. As a result, criminals may avoid committing crimes near schools during school hours simply because of the number of people present. If this were the case, we would see fewer crimes near schools; however, not as a result of the policy. Therefore, we present evidence about the number of drug crimes committed throughout the day, within the 1000-foot radius.

Figure 8 displays the number of drug crimes that are committed throughout the day. We round the time of the crime to the nearest 30-minute increment. As an example, a crime committed at 11:10a.m. is included with all crimes committed between 10:45a.m. and 11:14a.m. Similar to a study of over 840,000 police incidents in 10 major cities, we find that crime steadily rises throughout the day from a low at around 6:00a.m. (The Sleep Judge, 2020). However, we are truly interested in any differences between schools and non-schools, and during school hours.

Figure 9 displays the average crime near locations for schools and non-schools for weekdays. We see that both location types exhibit very similar patterns in crime on weekdays. Furthermore, there is always more crime near non-schools, compared to schools. Even during off-school hours, shown on the graph as before 7:00a.m. and after 4:00p.m., there is more crime near non-schools. Figure 10 displays the average crime near locations for schools and non-schools on weekends. If our results are not driven by the policy, we would expect to see no difference between schools and non-schools on weekends, or even perhaps more crime near schools, as non-school locations may be busier on weekends. However, similar to the results for weekdays, both location types follow similar patterns throughout the day on weekends and there is always more crime near non-schools. Taken together, the two figures suggest crime is not displaced from schools due to the concentration of people, patterns for schools and non-schools are very similar and differences in crime remains even during off-school hours.

Conclusion

In analyzing the effectiveness of DFSZ laws, our findings indicate that the 1000-foot protected zone around K-12 public and private schools do provide some level of deterrence for drug crimes, which extends even outside normal school hours when the law is enforceable. We estimate that the policy leads to 1065 to 1643 fewer drug crimes per year near schools, a measurable benefit of the policy. The conflicting estimated ATTs results between our propensity score and coarsened exact matching methods in the 1000–2000-foot buffer zone suggests that the benefits of the policy may not extend beyond the 1000-foot radius, lending support to critics who argue extremely large DFSZ boundaries provide no additional benefit.

An interesting finding in the data was that there is no measurable difference in gang-related drug crimes and gang-related violent crimes between schools and non-schools. This suggests that the DFSZ policy has no deterrent effect on gang-related criminal activity. One reason for this may be that the law is only enforced on adults age 18 + and recent research on youth gangs show that most members join before 18 years old (SafeYouth, n.d.). The implication is that either the policy should be amended to charge increased penalties to adolescents or other policies are needed in conjunction with this policy to deter gang-related criminal activities away from schools.

The main policy implications of this study are twofold. First, the results provide support that the DFSZ laws in Los Angeles County, CA do deter drug crimes near schools within the 1000-foot radius covered by the law. An additional benefit to the current policy is that the DFSZ law appears to deter not only the specific drug crimes outlined in the law, but all drug crimes including marijuana offenses. A reasonable explanation for this may be that individuals are not familiar with the exact drugs covered by the law and assume any drug offense will carry higher penalties near a school. Since many factors can affect criminal behavior, the results found here may only apply to Los Angeles County or very similar areas. Therefore, it would be important for policymakers in other territories to conduct similar studies to accurately measure the benefits of the DFSZ law in that area based on the size of their protected zones and types of protected entities.

Secondly, the results presented in this paper help determine the benefits, measured by the number of crimes deterred, provided by a DFSZ law that uses the standard 1000-foot protected radius. As outlined in the introduction, the debate about whether the current size of protected zones covered by the DFSZ laws are too large mainly focuses on the cost impacts of the zones and largely ignores measurements of the benefits. To determine if these DFSZ laws and the size of their protected zones are efficient, one must measure both the costs and benefits provided by the policy. On the benefits side, it is important for policymakers to not only consider the number of drug crimes deterred near schools, but also what the impact of that deterrence is on children. For example, did the absence of these crimes prevent any children from trying or using drugs, becoming addicted, dropping out of high school, having lowered future lifetime productivity and income levels, etc.? Admittedly, these valuations may be very hard or even impossible to measure and are beyond the of this paper, but nonetheless are important points to consider in the debate about the effectiveness and efficiency of DFSZ laws.

There are some limitations of the study that should be noted. First, the study area focused on Los Angeles County, CA. Though this is a large and diverse geographic area, the effects of the DFSZ law shown here may not be the same in other territories. Therefore, the results may only be attributable to Los Angeles County or other very similar territories. Secondly, though we use a rich set of covariates, it is possible that certain omitted variables exist that may make a difference in the results. Two variables where data was unavailable for our study were the zoning distributions for percentage of residential or commercial use at the block group level and the number of liquor stores present. Since empirical literature has shown the prominence of liquor stores to have an effect on crime, particularly violent crime, exclusion of this variable may impact the results (Britt, Carlin, Toomey, & Wagenaar, 2005; Franklin, LaVeist, Webster, & Pan, 2010). Lastly, our analysis provides evidence that DFSZ laws are effective at the most common 1000-foot protected zone size, however, it does not address whether or not this is the optimal size for such zones which is beyond the scope of this paper.

Future research should focus on measuring the deterrence of drug crimes at various proximities from schools to determine if there is an optimal DFSZ size that maximizes deterrence benefits while also minimizing the unintended consequences and costs associated with large DFSZ. Also, without a monetary valuation of the benefit to society of deterred crimes near schools and of the unintended consequences and enforcement costs related to the policy, we cannot perform a cost-benefit analysis. Future research should focus on these valuations to analyze the efficiency of DFSZ policies against its comparative alternatives. Lastly, more studies in various geographic locations are needed to determine if the results shown here are generalizable to the population at large.

Footnotes

Declaration of Conflicting Interests

The author(s) declared no potential conflicts of interest with respect to the research, authorship, and/or publication of this article.

Funding

The author(s) received no financial support for the research, authorship, and/or publication of this article.

ORCID iD

Erica Freer

Notes

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