COPS Princeton Study

More COPS, Less Crime∗
Steven Mello
Princeton University
Industrial Relations Section
Firestone Library A-16-H-2
Princeton, NJ 08544
[email protected]
January 3, 2017
Abstract
I exploit a unique natural experiment to estimate the causal effect of police on crime. The American
Recovery and Reinvestment Act increased funding for the COPS hiring grant program from $20
million in 2008 to $1 billion in 2009 and over $150 million annually in 2010-2013. During this period,
grant applications were scored and funding was allocated according to a fuzzy cutoff rule. I leverage
quasi-random variation in grant receipt by comparing the change over time in police and crimes for
cities above and below the score threshold. Relative to low-scoring applicants, cities above the cutoff
experience increases in police levels of about 3.6% and decreases in violent and property crimes of
about 4.8% and 3%, respectively. The effects are driven by large and statistically significant effects
of police on robbery, larceny, and auto theft. I also find evidence that police reduce murders, with the
point estimate implying that one life can be saved by hiring eleven officers. Arrest rates do not increase
with police force expansions, suggesting a deterrence mechanism underlying the crime reductions. The
program passes a cost-benefit test under some assumptions but not others. The results highlight that
police hiring grants may offer higher benefit-cost ratios than other stimulus spending.
JEL Classification: K42, H76.
Keywords: Police, crime, deterrence.

∗

I am grateful to Ilyana Kuziemko and Alex Mas, who provided considerable advice and encouragement on this project. I
thank Jessica Brown, John Donohue, and Felipe Goncalves, who read earlier drafts and offered valuable insights and criticisms.
Mingyu Chen, David Cho, Janet Currie, Will Dobbie, Hank Farber, Andrew Langan, Chris Neilson, and participants of
the Princeton Public Finance Working Group provided helpful comments. An Online Data Appendix, which describes the
processing of the data in detail, is available at www.princeton.edu/∼smello/papers/CopsDataAppendix.pdf. I acknowledge
financial support from a Princeton University Graduate Fellowship. Any errors are my own.

1

Introduction

In February 2009, President Obama signed into law the American Recovery and Reinvestment Act (ARRA),
which provided for over $490 billion in stimulus spending between 2009 and 2011. The Recovery Act allocated
about $2 billion to the Department of Justice (DOJ), the majority of which was used to finance a reinvigoration
of the DOJ’s police hiring grant program. The Community Oriented Policing Services (COPS) hiring
program, which covers the salary cost of new police hires for local law enforcement agencies, was a cornerstone
of President Clinton’s Violent Crime Control and Law Enforcement Act of 1994. Between 1995 and 2005, the
COPS hiring program spent almost $5 billion to help local police departments hire about 64,000 officers (Evans
and Owens 2007). Allocations for the program fell from over $1 billion per year in the late 1990’s to almost
zero in the years 2005–2008. The injection of Recovery Act funding restored the COPS hiring program budget
to $1 billion in FY 2009, and allocations for the program remained above $150 million annually through 2013.
I rely on variation in police levels generated by the program’s rebirth, termed COPS 2.0, to estimate
the effect of police on crime.1 Crime is estimated to cost Americans over $200 billion per year, and local
government expenditures on police protection exceed $87 billion annually (Chalfin 2016). Given that provision
of public safety is a key responsibility of local governments, and that hiring additional police is the main policy
instrument for crime prevention, the causal effect of expanding police forces on crime rates is a parameter
of substantial interest. In practice, estimating this effect is made difficult by the fact that police hiring
decisions are endogenous to local crime conditions, which introduces simultaneity bias in OLS estimates.2
Beginning with Levitt (1997), researchers have tried to overcome endogeneity issues by relying on quasiexperimental research designs. Instruments used in the literature include mayoral election years (Levitt 1997,
McCrary 2002), firefighter hiring (Levitt 2002), federal policing grants (Evans and Owens 2007, Worrall and
Kovandzic 2010), terror alert levels (Klick and Tabarrok 2005), and state sales tax rates (Lin 2009). Quasiexperimental studies have consistently documented that police reduce crime, although estimated magnitudes
vary widely across papers.3 Further, these instruments are not without potential flaws. Binary instruments,
such as election years, discard most of the variation in police rates and are often weak by conventional
standards. Federal grant instruments suffer from the the possibility that these grants are targeted where they
1

To the best of my knowledge, the term was coined by David Muhlhausen in a report for the Heritage Foundation titled
Why Would COPS 2.0 Succeed when COPS 1.0 Failed?
2
See, e.g., Klick and Tabarrok (2010) for further discussion.
3
For a more complete summary of the existing literature on the police-crime relationship, see reviews by Levitt and Miles
(2006), Klick and Tabarrok (2010), and Chalfin and McCrary (2016b).

1

are most needed or most likely to succeed, either of which would violate the exclusion restriction. Papers
using sharp micro-time series variation in police presence generated by terror alert systems or terrorist attacks,
including Klick and Tabarrok (2005), Draca, Machin and Witt (2011), and Di Tella and Schargrodsky (2004),
provide convincing evidence that police deter property crimes. However, these studies estimate treatment
effects specific to single jurisdictions, raising questions of external validity (Klick and Tabarrok 2010).
In this paper, I exploit a unique natural experiment generated by the scale up the COPS grant program.
Beginning in 2009, hiring grants were awarded based on an open solicitation application process. Local
law enforcement agencies applied for funding, and the COPS office scored the applications and distributed
funds. A fuzzy cutoff rule was used in selecting winners, with the probability of grant receipt jumping
discontinuously at a state by year-specific application score threshold. I leverage this feature of the program
for identification. My primary empirical strategy, which is similar to the dynamic regression discontinuity
approach implemented in Cellini, Ferreira and Rothstein (2010), is to compare the change over time in
police and crimes for cities with scores exceeding the threshold with those below. The approach exploits
the discontinuous allocation rule while still allowing the inclusion of police agency fixed effects to account
for level differences across cities. I control independently for the effect of the application score on the time
path of police and crimes by including interactions between the score and a set of event time (i.e. years
since application) indicators in the regressions. Further, I construct year fixed effects that vary by city size
and pre-program crime trends, so that estimates are identified by comparing cities above the threshold
with cities below that are of similar size and followed similar trends in the years prior to grant application.
I show that high and low scoring cities follow similar trends in police and crime prior to the application
year. Compared with cities just below, however, police rates increase by about 3.6% in the years following
the program application for cities above the threshold, while violent crimes and property crimes fall by about
4.8% and 3% respectively. To estimate a single police-crime elasticity for each crime category, I instrument
the police rate with an interaction between an indicator for the post-application period and an indicator
for whether the score exceeded the threshold in 2SLS regressions where the crime rate is the dependent
variable. The estimates imply crime-police elasticities of -1.36 for violent crime and -0.84 for property crime.
Estimates obtained with a conventional Regression Discontinuity Design approach are almost identical. An
analysis of individual crime types reveals that police reduce murders, robberies, larcenies, and auto thefts.
The estimated elasticities for murder and robbery are particularly large relative to existing studies. The
2

point estimate in my primary murder specification implies that one life can be saved by hiring eleven police
officers. I find little evidence, however, that arrests increased following the program-induced police force
expansions, which suggests a deterrence mechanism underlying the estimated crime effects.
While mine is not the first paper to study the effect of police on crime, this study contributes to the
existing literature in several important ways. The discontinuous allocation rule used in distributing grant
funding allows for a cleaner identification strategy than has been used in past studies. While the majority of
existing literature has focused on large cities or state-level data because of data quality concerns, I rigorously
clean the FBI crime data and examine all cities with populations above 1,000 that applied for COPS funding
between 2009–2013. My results, therefore, may be relevant to a larger share of local governments than
prior estimates. Finally, several of the most-cited papers on the topic have studied the high crime periods
of the 1980’s and 1990’s. I study a period with low and falling crime rates and show that additional police
still have a meaningful impact in this very different environment.
The rest of the paper is organized as follows. Section 2 provides background on the COPS hiring program.
I describe the data in Section 3 and my empirical strategy in Section 4. Section 5 presents the results. I
conduct a cost-benefit analysis in Section 6 and conclude in Section 7.
2

Background on the COPS Hiring Program

2.1

Program History

In September 1994, President Bill Clinton signed into law the Violent Crime Control and Law Enforcement
Act, the largest federal crime bill to date. The bill authorized $8.8B in spending on grants for state and local
law enforcement agencies between 1994 and 2000 and established the office of Community Oriented Policing
Services (COPS) to administer the new grant programs. A key tenet of the crime bill was the creation
of the COPS Universal Hiring Program (CHP), which covered 75% of the cost of new police hires for grant
recipients. The stated goal of the hiring grant program was to put 100,000 new police officers on the street.4
CHP funding exceeded $1B in fiscal years 1995–1999, but appropriations fell considerably in the early
2000’s. Less than $200M was allocated for the hiring program in 2003–2004, and less $20M was appropriated
in each year 2005–2008 (James 2013). The program was defunded due both to the retreat of crime as a
central policy issue and to questions over the program’s effectiveness (Evans and Owens 2007). Reports
4

See http://www.justice.gov/archive/opa/pr/Pre_96/October94/590.txt.html.

3

produced by the Heritage Foundation in 2001 and 2006, for example, argued that hiring grants did not
reduce crime because grants were used to supplant other expenditures rather than to expand police forces.5
Funding for the hiring program saw a dramatic resurgence in 2009 with President Obama’s signing of the
American Recovery and Reinvestment Act. The Recovery Act provided $2B in new funds to the Department of
Justice, with $1B earmarked specifically for the COPS hiring program. The funding was seen both as a precautionary measure for keeping crime rates low in the face of a worsening economy and as a means to create or preserve as many as 5,000 police officer jobs across the country. Following the injection of ARRA funds in FY2009,
congressional appropriations exceeded $140M annually between 2010 and 2013, a large increase from the 2004–
2008 funding levels.6 Hiring grants awarded in FY’s 2009–2011 were also more generous than in previous years,
covering 100%, rather than 75%, of entry-level salary and fringe benefits for hires or rehires for three years.7
2.2

Details of COPS 2.0

Hiring grants were distributed based on an open solicitation application process – any state, local, or
tribal agency with primary law enforcement responsibility was eligible to apply for funding. As part of the
application, agencies were required to submit an array of statistical information, including indicators of fiscal
health, local unemployment rates, local poverty rates, and local crime rates. Indicators of municipality fiscal
health included police agency operating budget, local government operating budget, and locally generated
revenue for the current and prior two fiscal years, as well as details about local government employee layoffs.
Applicants were also required to submit an essay on their community policing strategy and request a specific
number of police officers for which they required funding.8
Using the submitted information, the COPS office assigned each applicant a fiscal need score and a crime
score. COPS office documentation indicates these scores were generated by ranking applicants in the same
state and population group (smaller or larger than 150,000) against each other on each application question,
then weighting each question to obtain an aggregate ranking for each agency. I was unable to replicate
the reported application scores by following this approach, most likely due to my inability to observe a large
share of the application material. Municipal level employment and financial data, for example, are publicly
available on an annual basis for only a small fraction of cities. As such, I proceed treating the function
5

See, e.g., http://www.heritage.org/research/reports/2008/04/why-would-cops-20-succeed-when-cops-10-failed.
See (James 2013) for a detailed history of COPS funding.
7
The program reverted to covering 75% of salary and benefits beginning in 2012.
8
See http://www.cops.usdoj.gov/pdf/CHP/e05105273-CHP.pdf.
6

4

mapping application data to scores as unknown. The two component scores were added together to create an
aggregate application score, and funding was allocated according to the within-state score ranking. Data on
hiring grant awards strongly suggest that a de facto cutoff strategy was used, which can be seen in Figure 1.
Applicants were eligible to receive a grant of up to 5% of current force size, capped at a maximum. For
example, a department employing 100 sworn officers at the time of application was eligible to receive a grant
of 5 officers from COPS. The maximum grant size was 50 in 2009, 25 in 2010–2012, and 15 in 2013. These
maximums were binding for only a small share of applicants. In my sample of 4,374 cities, only 9 departments
employed over 1,000 officers and only 55 employed over 300. Two final rules governed grant allocations. First,
the COPS office was required to distribute at least 1.5% of total hiring program funding to each state. Second,
they were required to distribute at least 50% of all funding to jurisdictions with populations exceeding 150,000.
2.3

Research on the COPS Program

Although this paper is, to my knowledge, the first to examine COPS 2.0, several papers have studied the
first iteration of the COPS hiring program. The most noteworthy paper on the topic is the careful and
well-regarded study by Evans and Owens (2007). Papers by the GAO (2005) and Worrall and Kovandzic
(2010) also study the original COPS program and employ similar research designs.
In the first part of the paper, Evans and Owens (2007) examine whether COPS grants increased police
forces. Using a twelve-year (1990-2001) panel of 2074 cities, they regress sworn officers per 10,000 residents
on the lagged number of officers granted by the COPS office per 10,000 residents in panel data models,
finding that local police forces increased by 0.7 sworn officers for each granted officer. In the second part
of the paper, the authors instrument the police rate with the lagged grant rate in 2SLS regressions where
the crime rate is the outcome of interest, finding that increases in police are associated with statistically
significant declines in robberies, assaults, burglaries, and auto thefts.
Relative to Evans and Owens (2007), my contribution is twofold. First, I improve on their identification
strategy. I observe data on grant applications, which they do not, and am able to infer a discontinuity-based allocation rule from these data. This allows the use of cities who applied for but were not offered hiring grants as
a control group for grant winners. I argue that the set of applicants denied funding is a superior control group
to the broader set of cities who report crimes to the FBI. Applicants may differ from non-applicants in their
beliefs about future crime, for example. Further, the use of the discontinuous allocation rule helps circumvent
5

the possible endogeneity of grant take-up. In my setting, some cities with scores above the threshold are not observed as winning grants, which may reflect cities denying grant offers or the COPS office specifically rejecting
applicants on the basis of private information. My identification strategy considers these cities as treated, however, alleviating concerns about unobservable differences across cities that do and do not receive hiring grants.
Second, I study a different era of the program. Evans and Owens (2007) examine the introduction of
the COPS program in the mid 1990’s, when crime rates were high and crime in general was a central policy
issue. The stated goal of the program was to induce large increases in police forces across the country. My
focus is the reinvigoration of the program following the injection of ARRA funding. The goal of COPS
2.0 was to preserve law enforcement jobs and prevent a rise in crime due to worsening economic conditions.
The poor fiscal health of many cities during this period, combined with a lower program budget than during
the original COPS period, generated a highly competitive application process. The different context, various
program changes, and the availability of a cleaner identification strategy warrant a new evaluation. Further,
this paper contributes to a broader literature on the effectiveness of the Recovery Act and offers insights
on the relative benefits of including law enforcement funding in stimulus packages.
3

Data

3.1

COPS Program Data

I obtained data on applications for COPS hiring grants for the years 2009–2013 from the COPS office website.9
These data provide FBI ORI codes and application scores for the universe of applicants in each year.10 The
application score scale varies across years, and I standardize the scores to have mean zero and variance one
for each year individually so that score “distance” has the same interpretation across program years. The
COPS office also provides information on grant recipients for each year beginning in 2008. A small number of
hiring grants were awarded in 2008, and since I do not have application information for 2008, I discard these
data. The grants data include name of agency, number of officers granted, and dollar value associated with
the grant, for all CHP awards in each year. I collected data on award winners from 2009–2013 and merged
them with the application information using a name-matching algorithm, with a match rate of 97.7%.
The application score cutoffs were computed as follows. The COPS office documentation indicates that
9

For example, 2009 application scores are at http://www.cops.usdoj.gov/pdf/Applicant_Rankings2.pdf.
An ORI code is the unique identifier given to each agency that reports crimes to the FBI through the Uniform Crime
Reporting Data System.
10

6

applicants from the same state and population group (greater or smaller than 150,000) were ranked against
each other. I divided the applicants into state × size × program year groups g accordingly. Note that while
I use only municipal agencies with populations above 1,000 in the regression analysis, I use all the applicants
to compute the score thresholds. Within each group, I follow the strategy in Hoekstra (2009) to infer the
cutoffs. That is, at each score s in group g, I estimate the regression
1[Win Granti]=α+β1[si ≥s]+i
using only group g observations and identify the value of sg that maximizes the R-squared of this regression.
In several cases, the selected sg value is a non-negligible margin above the next highest score. In these cases,
setting the cutoff at sg may overstate the true “closeness” to the cutoff of the city at sg . For this reason, I
compute the threshold in group g as the average of the regression-selected sg and the next highest score.
In the analysis, I discard applications from groups without a competitive application process. Group
g is deemed noncompetitive if it meets any of three conditions: (1) group g has no winners; (2) group g
has no losers; (3) the coefficient from a regression of a grant win dummy on the application score, using
only observations in group g, is negative.
The results of the cutoff computations can be seen in Figure 1. The figure pools all program years
together and plots the probability of winning a hiring grant as a function of the application relative to
the cutoff. There is a clear discontinuity in the probability of grant receipt at the threshold. In a regression
of a grant win indicator on the relative score and an indicator for whether the score exceeds the threshold,
the coefficient (standard error) on the high score indicator is 0.89 (.0088). A more formal RD estimate
(see Table 3) yields a coefficient of 0.69 (0.03).
3.2

FBI Data

Data on police employees and crimes reported at the agency level are from the FBI’s Uniform Crime
Reporting Data System (UCR), which are compiled by and available for download from the NACJD. The
UCR provides monthly counts of index I crimes for all reporting agencies in the Offenses Known file. Index
I crimes include the core violent (murder, rape, robbery, aggravated assault) and property (burglary, larceny,
motor vehicle theft) crimes. The number of sworn officers employed by each agency in each year is reported in
the UCR Law Enforcement Officers Killed in Action (LEOKA) file. Because police officer counts are reported
only once yearly, and many agencies report their full-year crime counts once rather than report monthly,
7

I aggregate these counts to the agency-year level. I collected UCR data for 2005–2014, the most recent year
currently available. For city population, I use a smoothed version of the measure reported in the UCR files.11
The UCR data requires thorough cleaning before use. I implement a regression-based approach similar to
that of Evans and Owens (2007) to identify record errors and extreme outliers. Using data from 1990–2014, I
fit the time series of police and crime rates to a quartic time trend for each agency individually. Observations
were then identified as errors if the percent difference between the observed and predicted values differed by
more than a pre-determined city size group × crime type threshold. Observations flagged as errors are recoded
as missing in the dataset. The data-cleaning procedure is described in more detail in the Data Appendix.
3.3

Other Data Sources

The COPS and UCR data are supplemented with basic demographic variables measured at the county level.
I use county-level data because most demographic measures are not available at the city level on an annual
basis. I computed percent black, percent hispanic, and percent aged 15-24 from county population estimates
obtained from the SEER program at the NIH for the period 2005–2014. County-level per-capita income
was obtained from the Bureau of Economic Analysis (BEA), and county-level unemployment rates were
obtained from the BLS Local Area Unemployment Statistics data files. I use percent black, percent Hispanic,
percent aged 15-24, log per capita income, and unemployment rate as controls in the crime regressions.
3.4

Sample Construction

Using the 2000, 2005, and 2012 Law Enforcement Agency Identifiers Crosswalks, which are compiled by
the NACJD, I identified the universe of municipal police agencies that report crimes to the FBI. 9,949 police
agencies meet this requirement. I drop cities with population below 1,000, which reduces the number of
agencies to 9,162, because per-capita measures are much noisier, and often orders of magnitude higher,
below this threshold.12 I also require cities to have five (out of ten possible) years of valid population, police,
violent crime, and property crime observations. 8,917 cities survive this restriction. From this sample, I
drop cities with any observations in the top and bottom 1% of the distribution of sworn officers per capita,
which leaves 8,034 police agencies. Of these, 4,374 applied for COPS program funding between 2009 and
2013 and were in a competitive application group. This list of 4,374 cities comprises the main sample.
11

Chalfin and McCrary (2016a) note that the UCR population measure tends to jump discontinuously around census
years. For this reason, I follow their procedure and smooth the population measure using local linear regression. For more
detail, see the Online Data Appendix.
12
See Figure 3 in the Online Data Appendix.

8

3.5

Sample Characteristics

As described in more detail below, the unit of analysis in this study is an application, indexed by a city
and program year. Table 1 illustrates the distribution of applications across city size groups and program
years. The sample is heavily weighted towards smaller cities, with 49% of cities having populations between
5,000 and 25,000. Only 10% of cities are above the 50,000 resident threshold. The average city applies
twice. About 34% apply only once, while about 56% apply either twice or three times. The rest apply
four or more times. The applications under study are distributed across program years as follows: 43%
in 2009, 25% in 2010, 13% in 2011, 7.5% in 2012, and 11% in 2013.
Table 2 presents summary statistics for each of the 8,804 city × applications in the year prior to application.
The average city has about 25,000 residents, 21 sworn officers per 10,000, 35 violent crimes per 10,000, and
314 property crimes per 10,000. Breaking down the applications by high (above the threshold) and low
scores reveals some disparities in the types of cities. High-scoring cities are about twice as large on average
and have about 2.5 more police per 10,000 residents. Violent (property) crime rates are about 80% (50%)
higher in cities with applications above the threshold.
Figure 2 illustrates the relationship between the application score and characteristics of the city ×
application observations. The first panel plots the frequency of the relative application score. The lack of
excess mass just above the cutoff suggests no systematic manipulation by cities into eligibility. The estimated
discontinuity (standard error) from the McCrary (2008) test is -.072 (.076), implying that smoothness in
the density function cannot be rejected. The second panel plots the average covariate index by score bins of
width 0.25 in the year prior to application. The covariate index is the predicted crime rate from a regression
of total crimes per 10,000 residents on controls (see above) and year fixed effects (to account for the fact
that applications were submitted in different calendar years). Cities above the cutoff have higher covariate
indices on average, but the difference does not appear to be discontinuous. Similarly, it appears that in
the year prior to application, high scoring cities have higher police and crime rates, but cities exceeding
the threshold do not differ discontinuously on these measures.13
13

This is confirmed statistically in Table A-1, which presents RD estimates using local linear regression and Imbens and
Kalyanaraman (2012) bandwidths where the pre-application covariate index, police rate, and crime rate are the outcomes
of interest. None of the estimated discontinuities is statistically significant.

9

4

Empirical Strategy

The goal of the empirical analysis is to leverage quasi-random variation in police rates induced by COPS
program allocation rules to estimate the causal effect of police on crime. As discussed above and pictured
in Figure 1, a fuzzy cutoff rule in the application score was used in allocating grants among applicants. Less
than 10% of applicants with scores just below the threshold received grants, while over 80% of applicants
just above were funded. Such an allocation rule lends itself naturally to a regression discontinuity approach,
which would compare cities just above the threshold with cities just below with the underlying assumption
that exceeding the cutoff is random.
To begin, I consider a standard regression discontinuity design. Let i index cities and denote si for city
i’s application score. City i faces a cutoff score s∗i and I let
hi =1[si ≥s∗i ]
be a high score indicator. A standard RD specification in this context is
∆yi =θhi +f(˜
si)+i
where ˜s = s−s∗, f(·), and ∆yi is the change in some outcome y. In the main specification, I consider
the change between one year prior to one year after the program application as the change of interest. A
complication is the fact that cities need not apply only once. In the RD setup, I treat each city × application
as its own observation – a single city appears in the dataset once for each submitted application. In the
estimation, I approximate f with local linear regression and select the application score bandwidth as the
optimal bandwidth from Imbens and Kalyanaraman (2012). The coefficient of interest, θ, measures the
extent to which the change in y differed for cities above and below the threshold.
In practice, the standard RD estimates are imprecisely estimated. To address this, I instead implement a
dynamic, difference-in-differences version of the regression discontinuity design. My strategy is based closely
on that used by Cellini et al. (2010), who study the effect of passing bonds for school facility investments
on housing prices. The setup is as follows. Suppose that city i applies for funding in year ˜t and receives the
application score si. The cutoff score faced by city i in year ˜t is s∗i and let ht be an indicator for exceeding the
threshold. Let τ =t−˜t be the year relative to the application, or the event time year. Assuming cities vary in
their application years, one could examine the effect over time of crossing the threshold at τ =0 by estimating
10

yitτ =ατ +θτ hi ×ατ +φi +κt +t

(1)

where ατ is an event time fixed effect, φ is a city fixed effect, and κ is a year fixed effect. Equation (1) is an
event study regression where the event is a grant application and the event time coefficients are allowed to
vary by whether the application score is above or below the threshold.
Again, an important complication is that cities need not apply only once. Indeed, in my sample of 4,374 applicant cities, 2,867 apply multiple times. Considering a single application for each city would require taking a
stand on which is the focal application. Further, it would reduce the number of events to be analyzed from 8,804
to 4,374. Instead, I follow the stacking approach for dealing with multiple events detailed in Lafortune, Rothstein and Schanzenbach (2016) and Cellini et al. (2010). The time series for each city is copied once for each application that city submits. That is, one observation in the dataset is a city × application year × calendar year.
The analogue to (1) with stacked data is
yiatτ =ατ +θτ hia ×ατ +φia +κt +t

(2)

where hia is an indicator for whether the application score in year a is above the cutoff and φia is city ×
application fixed effect. While the city fixed effects are replaced with city × application fixed effects, I
cluster the standard errors at the city level. Because of the stacked data, cities with more applications
receive more weight in estimates of (2). To account for the relative overrepresentation of cities that apply
more often, I weight cities by one over the number of applications when estimating regressions of this form.
Underlying equation (2) is an assumption that whether sia exceeds the threshold is random. This
assumption is plausible for application scores very close to the cutoff but less believable in cases where the
score is far from the threshold. Rather than discard city × applications outside an arbitrary bandwidth
of the threshold, I make two adjustments to the estimating equation to improve the plausibility of this
assumption. First, I add interactions between the score in year a and the event time dummies. These
interactions capture the effect of the score on the time path of y independent of whether the score exceeds
the threshold. Second, instead of controlling only for year fixed effects, I group cities according to their
size and pre-program trends and construct year effects that vary by these groups. Using this technique,
cities with scores above the threshold are not compared with all cities below, but instead with cities below
11

the threshold that are of similar size and followed similar pre-program trends.
The pre-program cell by year effects, also used in Evans and Owens (2007), are constructed as follows. First,
cities are grouped into six size categories according to their population: 1,000-2,500; 2,500-5,000; 5,000-10,000;
10,000-25,000; 25,000-50,000; 50,000+.14 Cities that fall in multiple categories during the sample period are
placed in the group they appear most often. Then, for each city, I estimate a linear time trend in the police
rate and crime rate for the period 2005-2008. Cities are then grouped according to the size category by
(within size category) quartile of police pre-trend by (within size category) quartile of crime pre-trend. That
is, a city falls into one of 6×4×4=96 groups, and regressions include year effects that vary by these groups.
Note that this approach is done separately for each crime type, so that in regressions where, for example,
robbery is the dependent variable, cities are grouped according to their pre-program robbery trends.15
The main estimating equation is then
yiatτ =ατ +θτ hia ×ατ +λτ sia ×ατ +γXit +φia +κt +iatτ

(3)

where λτ is the coefficient on an interaction between the event time fixed effect and the application score
associated with applicant ia and κt is a pre-program cell by year fixed effect. The coefficients of interest
are the θτ ’s, which trace out the effect of crossing the threshold in event time. The pre-period (τ <0) θτ ’s
provide a specification check for whether the pre-program trends differ among high and low-scoring cities.
The post-period θτ ’s are intent-to-treat estimates of the effect of hiring grants on y.
Estimates of (3) where y is police officers per 10,000 residents and crimes per 10,000 residents can be
thought of as the first stage and reduced form components of an instrumental variables estimate of the
causal effect of police on crime, generating one estimate for each event time year. To estimate a single
average effect, I estimate the equation
Crimeiatτ =θP oliceiatτ +βP ostiatτ +ατ +λτ sia ×ατ +γXit +φia +κt +iatτ
14

(4)

50,000 residents is a lower than desirable cutoff for the largest city size group. However, there are only 123 cities
with populations > 100,000. This results in a very small number of cities in each pre-program cell bin. Hence, I pool the
50,000-100,000 and 100,000+ groups together when creating the groups.
15
I present a test of whether grouping cities accordingly, as well as controlling for event time × application score interactions,
improves the plausibility of the randomness assumption in Table A-4. Using data from the year prior to application, I regress
an indicator for whether the score exceeded the threshold on a set of city characteristics. When the full sample is used and
cities are ungrouped (Column 1), the F-statistic from a joint significance test of the observable characteristics is 129.25. Adding
pre-program cell fixed effects reduces the F-stat to 94.25 (column 2), and controlling linearly for the score further reduces it
to 22.4 (Column 3). It is important to note that level differences in observables across cities above and below the threshold are,
in practice, irrelevant because such differences are absorbed by the city × application fixed effects in (2). This exercise simply
demonstrates that above-threshold cities are compared with more similar below-threshold ones after making these adjustments.

12

where P ost=1[τ ≥0] and P ostiatτ ×hia instruments for police. This specification is a standard difference-indifferences IV estimating equation except that the event time indicators and event time × application score
interactions are included.
5

Results

5.1

Regression Discontinuity Evidence

Figure 3 plots binned averages of the two-year change in police rates by the application score. The unit of
observation is a city × application and I focus on city × applications within one point of the cutoff. Bin widths
are selected to have equal mass. The squares plot this change as of one year prior to application (i.e. the change
from three years prior to one year prior), which is a placebo test. The circles plot this change as of one year after
the application (i.e. the change from one year prior to one year after), which captures the short term effects of
the program. Although the binned averages are noisy, the figure suggests that changes prior to the program are
relatively continuous through the score distribution, while changes after the program increase discontinuously
at the score threshold. Police rates increase slightly for cities above the threshold, who become eligible for
funding, while police rates fall by between 0.5 and 1 sworn officer per 10,000 for cities below the cutoff. The
differences at the threshold suggest that COPS grants were associated with relative increases in police levels.
Figure 4 presents identical plots where the two-year change in crimes per 10,000 residents is the outcome
of interest. Again, the average changes are relatively noisy, but the plots suggest that cities above and
below the threshold experienced similar changes in violent and property crimes prior to program application.
Cities above the cutoff, however, appear to experience larger declines in crime than cities below following
program application. The disparity in crime changes at the threshold suggests that (relative) police increases
induced by the program caused a (relative) drop in crime.
Table 3 presents the RD estimates. All regressions use the optimal IK bandwidth and control for the
score with local linear regression. Robust standard errors from Calonico, Cattaneo and Titiunik (2014) in
parentheses. Columns 1-2 show that crossing the threshold is associated with an increase in the probability
of grant receipt of 0.69 percentage points and an increase in active grant funding of about $61,000.16 Column
3 indicates that police forces increase by 0.63 sworn officers at the threshold. Columns 4 and 5 suggest
that crossing that threshold was associated with relative declines of 1.68 violent crimes and 10.46 property
16

Active Funding is my estimate of grant dollars spent on a given city in a given year. This is computed by summing total
funding over the prior three years (because grants cover three years of salary) then dividing by three (to annualize the amount).

13

crimes. Evaluating at pre-period means, these results imply crime-police elasticities of -1.24 for violent crime
and -0.86 for property crime. The reduced form crime estimates are not statistically signifiant, however.17
5.2

Event Time Evidence

Figure 5 plots the θτ ’s from estimates of (3) where sworn officers per 10,000 residents is the dependent
variable. One year prior to the application is the excluded year, so the differences between high and low
scoring cities are normalized to that year. Cities with scores above and below the threshold follow similar
trends in the years prior to application. Beginning with the application year, however, the cities diverge,
with police increasing among cities above the threshold relative to those below. Note that given the timing
of program events and police measurement, it is reasonable to expect hiring grants to have an impact in the
application year. Grant funding is distributed in the summer, while police levels are measured in October.
Further, anecdotal evidence suggests that many COPS 2.0 awards were used to avoid scheduled layoffs,
and such an effect would be seen more quickly than actually hiring and training new officers.
The corresponding estimates for violent crimes are presented in Figure 6. As with police, violent crime
rates follow similar trends in high and low scoring cities during the pre-period, but diverge beginning with
the application year. The coefficients in years 0 through 2 are all statistically distinguishable from zero.
The high score coefficients are noisy for murder, but do turn more negative in the post period, with the
coefficient at τ =1 statistically significant. For robbery, above cutoff cities appear to follow a slight upward
trend relative to those below in the pre-period. Compared with low-scorers, however, high-scoring cities
experience statistically significant declines following the application year. The assault coefficients follow
a pattern similar to those for aggregate violent crime, turning from zero in the pre-period to negative in
the post-period before returning to zero. None of the post-period coefficients are significant, however.
An analogous pattern emerges for property crimes, as depicted in Figure 7. For aggregate property crime,
larceny, and auto theft, exceeding the threshold at time zero is unrelated with changes in the crime rate
in years prior, but is associated with statistically signifiant declines in the post period. Coefficients also
turn negative following the application year for burglary, albeit more slowly.
The point estimates underlying the event study figures for police and aggregate violent and property crimes
are presented in Table 4. The estimates indicate that on a base of 22.54, exceeding the threshold is associated
with about a 3.6% increase in the police rate. Similarly, cities with high scores experience a relative decline
17

Regression discontinuity plots and estimates for individual crime types are presented in Figure A-2 and Table A-2.

14

in violent crime of about 4.8%, which suggests an elasticity of violent crime with respect to police of about
-1.33. Property crimes decline by about 3% following the application year for grant eligible cities, suggesting
an elasticity of about -0.8. The analogous estimates for the individual crime types are shown in Table A-3.
5.3

IV Results

The differences-in-differences IV strategy outlined in Section 4 suggests a straightforward way to estimate
the effect of grants on police. Column 1 of Table 5 presents coefficients on Post and Post × High from
a regression where active grant funding per 10,000 residents is the dependent variable.18 The coefficient
on Post × High suggests that relative to cities below the threshold, grant funding increases by about $51,000
dollars per 10,000 residents following the application. Column 2 shows that police forces increases by about
0.75. A simple Wald estimate of the effect of grant funding on police is then 0.75/$51,000, which implies
that one officer-year is added for every $68,000 in grant funding awarded.
Columns 3 and 4 present IV estimates of the effect of police on violent and property crime based on
equation 4, that is using Post × High as an instrument for the police rate. The F-statistic corresponding
to the instrument is in the range of 30, confirming that this instrument satisfies the relevance condition.
The estimates suggest that an additional officer is associated with 2.9 fewer violent crimes and 16.23 fewer
property crimes. To convert the coefficients to elasticities, I multiply the point estimates by the ratio of
the mean police and crime rate.19 The results imply crime-police elasticities of -1.36 for violent crime and
-0.84 for property crime. Worth noting is the fact that these elasticities are nearly identical to those obtained
via the standard RD specification, which lends credence to the dynamic RD identification strategy.
Table 6 presents the corresponding estimates for individual crime types. The results suggest that police
force increases generate statistically significant declines in murders, robberies, larcenies, and auto thefts.
Estimated coefficients imply that an additional officer leads to 0.09 fewer murders, 1.4 fewer robberies, 8.6
fewer larcenies, and 3.5 fewer auto thefts. The implied elasticities are -4.8, -2.9, -0.62, and -2.18 respectively.
Worth noting is the fact the event time estimates also suggested an effect on assault and that the p-values
for the assault and burglary coefficients in Table 6 are 0.275 and 0.156, respectively.
The magnitude of the estimated murder effect warrants further discussion. The point estimate of -0.0896
18

Active funding is computed as the sum of grants received over the previous four years divided by four. Grants cover
three years of salary but the event study estimates suggest that year zero and year four are partially treated.
19
The means are for 2005 and for cities within 1 point of the score threshold. These means were selected because the
instrumental variables estimates are local to cities near the cutoff.

15

implies that one life can be saved by hiring eleven additional police officers. At a value of a statistical life
(VSL) of $7M and an annual cost per officer of $130,000 (Chalfin and McCrary 2016a), the benefits of
this proposition outweigh the costs by a wide margin of $5.6M. The lower bound of the 90% confidence
interval around the point estimate (-0.019) implies one life saved for every 53 officers hired, which still passes
a cost-benefit test by over $100,000.
5.4

Comparison with Existing Studies

A common finding in the existing literature is that crime-police elasticities are larger for violent than property
crime. My results confirm this finding, as I estimate a violent crime elasticity of -1.36 and a property
crime elasticity of -0.84. Evans and Owens (2007) find a similar violent crime elasticity of -1.34. Their
estimated property crime elasticity of -0.26, however, is about one third the size of my estimate. Lin (2009),
who studies state-level data, also finds a similar violent crime elasticity of -1.13, but a considerably larger
property crime elasticity of -2.18. Chalfin and McCrary (2016a) find smaller elasticities of -0.34 and -0.17,
but these disparities could be due to differing samples – their study examines only large cities.
Estimates for individual crime types vary widely across existing papers. Murder-police elasticities range
from -0.24 (Marvell and Moody 1996) to -3.03 (Levitt 1997). My point estimate implies a quite large
elasticity of -4.8, but the 95% confidence interval includes elasticities as small as -0.35. Consistent with
existing work, I find little statistical evidence that police reduce rapes but strong evidence of an effect on
robbery. My estimate of the robbery-police elasticity of -2.93, however, is larger than most existing estimates.
For example, Lin (2009) and Evans and Owens (2007), whose estimates are at the larger end of the current
literature, find statistically significant elasticities of -1.86 and -1.34.
Past studies have diverged on whether police reduce aggravated assaults. Evans and Owens (2007) find
a large and statistically significant elasticity of -0.96, while the corresponding figure in Chalfin and McCrary
(2016a) is a small and insignificant -0.1. The implied elasticity in Table 6, -0.77, is on the larger end of
existing estimates. Although the coefficient is not statistically significant, the event time coefficients in
Figure 6 appear to suggest an effect. Several studies have found that police reduce burglaries, with most
estimated elasticities between -0.3 (Klick and Tabarrok 2005) and -0.59 (Evans and Owens 2007). My
estimate, -0.64, is similar in magnitude but not significant.
Existing estimates for larceny also vary widely. Many studies have found essentially no effect, while
16

my results suggest a statistically significant larceny-police elasticity of about -0.62. On the other hand,
prior studies have commonly found large and robust effects of police on auto thefts. Estimates range from
-0.44 (Worrall and Kovandzic 2010) to -0.85 (Klick and Tabarrok 2005) to as large as -4.14 (Lin 2009). My
estimate of -2.18 is on the larger end of estimates in the literature.
5.5

Robustness

In this section, I probe the robustness of the crime-specific estimates discussed above. Figure 8 illustrates
the first stage and reduced form estimates underlying the crime regressions when varying bandwidths are
used – that is, when only city × applications within a certain distance of the application score threshold are
used in the estimation. A bandwidth of 4 includes 99% of the data and 4.5 includes all city × applications
used in the primary regressions.
The police panel indicates that the first stage effects are stable regardless of the bandwidth used. The
reduced form murder effect is similar in magnitude for bandwidths larger than 0.1 and statistically significant
for bandwidths larger than 1.5. The point estimate shrinks slightly, however, when only applications within
0.5 points are used. The rape estimates hover around zero and are never distinguishable from zero. For
robbery, the reduced form effects are statistically significant at the 95% level regardless of the bandwidth,
although the point estimate is slightly smaller when using only closer applications. Coefficients for assault and
burglary are never significant and reveal no clear pattern in terms of the relationship between the bandwidth
and effect size. The magnitude of the estimated larceny effect is consistent across bandwidth sizes and most
estimates are significant at the 90% level, as was the case in Table 6. The results for auto theft reveal that
although estimated effect size for bandwidths greater than one are similar and always significant, the effect
is smaller and significant only at the 90% level when only the closest applications are used in the analysis.
I present additional robustness checks in Table 7, which repeats the estimates in Table 6 using alternative
specifications. In the second row, I repeat the estimation using only cities with ten years of valid data for
that crime type. The effects are similar, and if anything, larger than in the main specification. In the third
row, I conduct the estimation using “balanced panels” – that is, for each city × application, only years
between four years prior and two years after the application year are used. I also drop 2013 applications,
so that all cities used in the estimation are observed over the four years prior to two years after range.
These regressions test whether the estimated effects are driven by changes in years well after treatment. The
17

murder and robbery estimates shrink, although the robbery estimate is still highly significant. The estimated
assault effect is notably larger and marginally significant, implying an elasticity of about -1.15. The larceny
and auto theft estimates are similar in magnitude and statistical significance to the main specification.
In the fourth row, I restrict the analysis to cities with population greater than 10,000.20 This sample criterion
is the same as that used in Evans and Owens (2007) and is meant to ensure that the estimated effects are
not merely a result of noisiness in the crime data for very small cities. Relative to the main specification, the
effects for robbery, assault, larceny, and auto theft grow, with the robbery and auto theft estimates remaining
significant. The estimated murder and assault remain large but not statistically distinguishable from zero.
In the fifth row, I augment the main specification by replacing the event time × application score
interactions with event time × relative score (score minus the threshold) interactions that vary by whether
the score exceeds the threshold, similar to a standard regression discontinuity design specification that
controls linearly for the running variable and allows the slope of the line to vary on either side of the
threshold. Relative to the first row, this approach strengthens the murder effect but weakens the robbery,
larceny, and auto theft effects. In the sixth row, I repeat the specification from the fifth row using only
city × applications within one point of the cutoff. This specification, which is the most demanding in Table
7, yields results very similar in magnitude and significance to those in the main specification.
As an additional robustness check, I explore the sensitivity of the results to varying the definition of the
treatment. COPS hiring grants cover a police officer salary for three years (or 75% of that salary for grants
in 2012 and 2013). In the main specification, however, assumes that cities above the cutoff at year t are
treated through the end of the sample. Cities above the cutoff in 2009 are coded as treated 4-5 years after
the application, for example. To test the extent to which this coding scheme is relevant for the estimated
effects, I repeat the first stage and reduced form evidence under varying treatment length specifications.
That is, I create P ostk =1[0<=τ <=k] and P ostk ×High and estimate
Crimeiatτ =βP ostkiatτ +θP ostkiatτ ×Highia +ατ +λτ sia ×ατ +γXit +φia +κt +iatτ
and examine how θ varies across values of k.
The results of this exercise are shown in Figure 9. Note that k = 5 includes all post-application years
in the data and therefore corresponds to the main specification. Setting k =2 or k =3 would capture the
20

To be precise, cities whose population exceeds 10,000 in at least five years.

18

program “letter of the law” and revert cities to “untreated” at the conclusion of the grant period. An
immediate takeaway is that the first stage is increasing in the specification of the treatment length. The
coefficient is roughly twice as large when all post period years are indicated as treated as when only the
application year and the year after are included. The estimates for robbery, burglary, larceny, and auto
theft follow an inverse pattern, with effects smallest when the shortest period is used and largest when
using the longest period. The inverted relationship is comforting in the sense that implied Wald estimates
(the reduced form divided by the first stage) appear to be relatively stable across the treatment length
specifications. For murder, the reduced form is quite small and insignificant when k <4, but grows when
k is 4-5 and is only significant when k =5, which may shed doubt on the robustness of the estimated murder
effect. This result seems to be at odds with the event time estimates, however, as we observed in Figure
6 that high scoring cities experienced large drops in murder at τ =1 relative to those below the threshold.
Further, the estimated murder effect survived the majority of specification tests in Table 7.
5.6

Mechanisms

As with other crime control policies, police hiring may reduce crime through two channels – deterrence
or incapacitation. Standard economic models of crime, such as Becker (1968), predict that police increases
deter crime by raising the expected cost associated with criminal behavior. Cost increases elicit a behavioral
response, with fewer potential offenders choosing to engage in crime. However, police may also increase the
number of individuals detained or incarcerated, which reduces crime by incapacitating potential offenders.
By which mechanism police reduce crime is of considerable interest because incapacitation is associated
with incarceration costs in addition to the police wage bill.
In practice, my estimates almost surely identify a combination of deterrence and incapacitation effects
(Chalfin and McCrary 2016b). To get a sense of the relative importance of the two mechanisms, I examine
whether COPS-induced police force expansions were associated with increases in arrest rates. As highlighted
in Owens (2012), the intuition behind this test is that if police deter crime, increased police presence will
reduce crime without necessarily increasing the number of offenders actually apprehended. On the other
hand, for police to have an incapacitation effect, hiring police must increase the number of arrested, and
therefore incapacitated, potential offenders.
For this exercise, I rely on data from the UCR Arrests file, which reports yearly arrest counts by offense
19

category at the agency level. Not all agencies that report crimes to the FBI also submit arrest data. The
sample for the arrest rate analysis includes 3,519 cities (out of 4,374) and 7,138 city × applications out
of (8,804). The arrest data were cleaned and processed using the same method as the crimes data which
is described in the Data Appendix. Figure 10 plots the event time × high score interaction coefficients from
regressions where arrests per 10,000 residents is the outcome of interest.21 The figures suggest that exceeding
the threshold is associated with a decline in murder and robbery arrests. There is little evidence, however, that
arrest rates changed for any other crime types. In Table 8, I repeat the IV estimates from Table 6 for arrest
rates. For reference, I show the coefficient from an identical-sample regression of crimes (instead of arrests)
on police in the table. The estimates suggest that police increases were associated with a decline in robbery
arrests of similar magnitude to the actual decline in robberies (elasticity of -2.6), which suggests that the
estimated robbery reductions were accomplished through deterrence. Past work has also shown that robbery
may be a particularly deterrable crime type. Abrams (2012), for example, finds that sentence enhancements
for gun crimes enacted in the 1970’s and 1980’s were associated with large and statistically significant
declines in gun robberies. The arrest rates coefficients for no other crime type are statistically significant,
and the coefficients are negative for all crime types except assault and burglary. In line with the argument in
Owens (2012), I take these results as evidence that police deter murders, robberies, larcenies, and auto thefts.
6

Cost-Benefit Analysis

Given that police added by the program reduced crime, a natural question is whether the COPS hiring
program passes a cost-benefit test. The first-stage estimates in Table 5 imply that police forces increased
by one for each $68,000 in grant funding. Just over $900M was allocated to cities in my sample, implying
that grants awarded between 2009-2013 added 13,393 officer-years for these cities.22 After accounting for
deadweight loss associated with raising government funds, the federal cost is in the range of $1.2B. Most
estimates in the literature suggest that the annual cost of a fully-equipped police officer is around $130,000,
which implies that local governments spent an additional $830M on the estimated police increases. Hence,
a reasonable estimate of the program’s total cost is about $2B.
I use victimization cost estimates common in the literature to convert crime reduction into social value
dollars. The estimates I use are taken from Cohen and Piquero (2009) and Chalfin and McCrary (2016a)
21
22

For comparability, the police and crime event study plots specifically for the arrests sample are shown in Figure A-5.
$910,764,901/68,000=13,393.

20

and are shown in Table 9. The social benefit associated with an additional police officer is the sum of the
police coefficients for the individual crime types, with each coefficient weighted by the social cost associated
with that particular crime type. Obviously this computation is sensitive to the choice of coefficients. To
be conservative, I use the smallest (in absolute value) coefficient for each crime type in Table 6, which yields
an estimated social value per officer of $417,456. Under this assumption, the total benefit generated by
the program is 13,393 × $417,456 ≈ $5.6B, which suggests the program easily passes a cost-benefit test.
As noted in existing studies, whether additional police are cost-effective depends particularly on whether
they reduce murder. The sensitivity of cost-benefit analysis to the estimated murder effect is, of course, due
to the fact that murder is the most costly crime type by a factor of 50.23 Using the same set of coefficients
as above but setting the murder effect to zero gives a total benefit estimate of about $900M, approximately
equal to the federal spending on grants but well below the program’s total costs. On the other hand, if an
additional police officer prevents at least 0.0214 murders annually, the program is cost effective even if police
have no effect on all other crime types.24 A police-murder effect of -0.0214 is within the 90% confidence
interval of the estimate in my preferred specification (−0.0896±0.07) and smaller (in absolute value) than
the point estimate in all specifications in Table 7.
As a component of the American Recovery and Reinvestment Act, the increase in COPS program funding
was intended, at least in part, to create or save police officer jobs. Hence, it is useful to compare the costs and
benefits associated with the COPS program to those associated with other stimulus spending under the heading
of job creation. The degree to which ARRA spending increased employment has been the subject of much
debate. The academic literature has focused on estimating the cost per job created (or saved) by the Recovery
Act, relying on cross-state variation in the generosity of transfers received from the federal government.
Despite apparently similar methodologies, existing estimates vary widely. Chodorow-Reich, Feiveson, Liscow
and Woolston (2012) estimate a cost per job-year of $26,000, with most job-creation in the private sector.
Conley and Dupor (2013) find that most jobs created were in government and estimate a cost per job-year of
$200,000. My analysis implies a cost per police officer job-year of $68,000, which is squarely in the range of the
existing estimates. Depending on the crime coefficients used, my estimate of the social benefit per officer-year
is between $25,000 and $418,000. Given the relatively modest cost per job-year, and potentially large positive
23

Although murder is rare, its costliness outweighs its rarity. For example, while robberies are about 275 times more
common than murders, one murder is 550 times more costly when using a VSL of $7M.
24
13,393 officer years × 0.0213 fewer murders per officer-year × $7M (social cost per murder) = $2B (total program cost).

21

crime reduction externalities, the benefit-cost ratio associated with police hiring grants may compare favorably
with other forms of stimulus spending. Such programs may be more politically feasible, as well, since spending
under the heading of crime reduction is more likely to gain bipartisan support than many federal programs.25
7

Conclusion

In this paper, I exploit quasi-random variation in police levels induced by COPS program allocation rules
to circumvent the endogeneity of police hiring and estimate the casual effect of police on crime. My
identification strategy relies on the fact that grant funding was awarded as a discontinuous function of
cities’ application scores. I compare the change over time in police and crime for cities above and below the
application score threshold with the underlying premise that cities below are a valid control group for cities
above. Studying the dynamics non-parametrically, I show that police and crimes follow similar trends in high
and low scoring cities prior to the application year, but the trends diverge as the high scoring cities become
eligible for funding. The corresponding instrumental variables estimates demonstrate that an additional
officer prevents 2.9 violent crimes and 16.23 property crimes, with implied elasticities of -1.36 and -0.84.
An examination of individual crime types reveals that the results are driven by large effects of police
on robbery, larceny and auto theft. My estimates suggests that an additional officer is associated with 1.39
fewer robberies, 9.6 fewer larcenies, and 3.5 fewer auto thefts. I also find evidence of a sizable effect of police
on murder – the coefficient in the main specification is statistically significant and implies that one murder
per year can be prevented by hiring eleven officers. The magnitudes of the murder, robbery, larceny, and
auto theft estimates are generally robust to specification checks and the effects remain when examining
only cities close to the application score thresholds. Further, I show that program-induced police increases
were not coupled with increases in arrest rates, which suggests that crime reductions were achieved through
deterrence rather than incapacitation.
The conclusion of a cost-benefit analysis of the program hinges on whether police reduce murder. Assuming
no effect of police on murder, I estimate a total social benefit attributable to the program approximately
equal to federal spending on hiring grants but well below my best estimate of the program’s total cost.
On the other hand, if an additional police officer prevents at least .0214 murders annually, the social value
associated with murder reduction alone is enough to justify the program’s cost. A police-murder effect of
25

See, e.g. Bipartisan House group seeks to bolster nation’s police forces with COPS bill, Mike Lillis for the thehill.com,
5/14/2011.

22

-.0214 is within the 90% confidence interval of the point estimate in my preferred specification (-.089), and
I estimate effects of at least this magnitude in all specifications. Regardless of the cost-benefit conclusion,
however, the results highlight that programs to increase police officer employment may offer higher returns
than other stimulus spending because of the associated crime reduction externality. I estimate that one
officer-year was added for every $68,000 spent by the federal government, and that the social benefit of
the ensuing crime reduction is at the very least $25,000 but quite possibly as large as $400,000.
My analysis raises several questions for future work. The fact that police increases were, on average,
associated with large crime reductions suggests that police levels were not set optimally ex ante. This
conclusion is also reached in a recent paper by Chalfin and McCrary (2016a), who argue that the average
U.S. city is underpoliced. Understanding what frictions prevent the efficient allocation of local government
resources for crime prevention might prove an interesting avenue for new research. Additionally, the treatment
effect of police on crime is almost certainly heterogeneous. A careful examination of this heterogeneity,
which is beyond the scope of this paper, may reveal the optimal allocation of police across cities and assist
the COPS program in targeting future grants.

23

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24

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26

Figure 1: Discontinuity in Probability of Grant Receipt

1

Share Winning Grants

.8

.6

.4

.2

0
-4

-2

0

2

4

Score Relative to Cutoff

Notes: A unit is a city × application. Bin width equals 0.25. Figure shows share of applications in each bin that resulted in
grants.

Figure 2: Characteristics of Applicants by Application Score

Frequency of Running Variable

Pre-Application Covariate Index
450

800

400

600

350

400

300

200

250

0
-4

-2

0

2

4

-4

-3

Score Relative to Cutoff

-2

-1

0

1

2

3

4

3

4

Score Relative to Cutoff

Pre-Application Police Rate

Pre-Application Crime Rate

28

800

26
600

24
22

400

20
200

18
-4

-3

-2

-1

0

1

2

3

4

-4

Score Relative to Cutoff

-3

-2

-1

0

1

2

Score Relative to Cutoff

Notes: An observation is a city × application. Bin width equals 0.25. Covariate index is the predicted crime rate from a
regression of crimes per 10,000 residents on controls and year fixed effects. Covariate index, police rate, and crime rate are
plotted for one year prior to the application.

27

Figure 3: Two-Year Change in Police by Application Score

.5

0

-.5

1 Year Prior
1 Year After

-1
-1

-.5

0

.5

1

Score Relative to Cutoff

Notes: An observation is a city × application. Bin width selected to have equal mass. Plot shows the mean two-year change
(i.e. change from t−2 to t) in police per 10,000 residents for one year prior and one year after the application year. Cities are
weighted by one over the number of applications.

Figure 4: Two-Year Change in Crime by Application Score

Violent Crime

Property Crime
0

5

-10

0
-20

-30
-5

-40

-10

-50
-1

-.5

0

.5

1

-1

Score Relative to Cutoff

-.5

0

.5

1

Score Relative to Cutoff

Notes: See Figure 3 for legend. An observation is a city × application. Bin width selected to have equal mass. Plot shows the
mean two-year change (i.e. change from t−2 to t) in crimes per 10,000 residents for one year prior and one year after the
application year. Cities are weighted by one over the number of applications.

28

Figure 5: Effect of Exceeding the Threshold on Police

1.5

Sworn Officers per 10,000

1

.5

0

-.5
-3

-2

-1

0

1

2

3

Year Around Application

Notes: Dependent variable is sworn officers per 10,000 residents. 95% confidence bands from standard errors clustered at the
city level. Figure plots coefficients on interaction between an event time indicator and a high score indicator. Regression
includes controls, event time fixed effects, event time fixed effects interacted with the application score, city × application fixed
effects and pre-program cell × year fixed effects. Cities are weighted by one over the number of applications. Regressions also
include event time coefficients (and high score interactions) for 4+ years prior and 4+ years after. Corresponding coefficients
shown in Table 4.

Figure 6: Effect of Exceeding the Threshold on Violent Crime

All Violent

Murder
.05

Crimes per 10,000

Crimes per 10,000

2
0
-2
-4

0
-.05
-.1
-.15

-6

-.2
-3

-2

-1

0

1

2

3

-3

Year Around Application

-2

-1

0

1

2

3

Year Around Application

Robbery

Assault

0

Crimes per 10,000

Crimes per 10,000

2

-.5
-1
-1.5
-2

1
0
-1
-2
-3

-3

-2

-1

0

1

2

3

-3

Year Around Application

-2

-1

0

1

2

3

Year Around Application

Notes: Dependent variable is crimes per 10,000 residents. 95% confidence bands from standard errors clustered at the city level.
Figures plots coefficients on interactions between an event time indicator and a high score indicator. Regression includes
controls, event time fixed effects, event time fixed effects interacted with the application score, city × application fixed effects
and pre-program cell × year fixed effects. Cities are weighted by one over the number of applications. Regressions also include
event time coefficients (and high score interactions) for 4+ years prior and 4+ years after. Corresponding coefficients shown in
Table 4 and A-3.

29

Figure 7: Effect of Exceeding the Threshold on Property Crime

All Property

Burglary
4

Crimes per 10,000

Crimes per 10,000

10
0
-10
-20
-30

2
0
-2
-4
-6

-3

-2

-1

0

1

2

3

-3

Year Around Application

-2

Larceny

0

1

2

3

Auto Theft
2

Crimes per 10,000

5

Crimes per 10,000

-1

Year Around Application

0
-5
-10
-15
-20

0

-2

-4
-3

-2

-1

0

1

2

3

-3

Year Around Application

-2

-1

0

1

2

3

Year Around Application

Notes: Dependent variable is crimes per 10,000 residents. 95% confidence bands from standard errors clustered at the city level.
Figures plots coefficients on interactions between an event time indicator and a high score indicator. Regression includes
controls, event time fixed effects, event time fixed effects interacted with the application score, city × application fixed effects
and pre-program cell × year fixed effects. Cities are weighted by one over the number of applications. Regressions also include
event time coefficients (and high score interactions) for 4+ years prior and 4+ years after. Corresponding coefficients shown in
Table 4 and A-3.

30

Figure 8: Sensitivity of First Stage and Reduced Form Estimates to Varying the Bandwidth

Sworn Officers

Murder

1.2

Rape

.05

.4
.2

1

0

.8

-.05

0

.6

-.1

-.2

.4

-.15
0

1

2

3

4

5

-.4
0

1

2

Bandwidth

3

4

5

0

1

Bandwidth

Robbery

Assault

0
-.5

2

3

4

5

4

5

Bandwidth

Burglary

1

2

0

0

-1
-1

-2

-2

-1.5

-4

-3
0

1

2

3

4

5

0

1

Bandwidth

2

3

4

5

Bandwidth

Larceny

0

1

2

3

Bandwidth

Auto Theft

5

0

0

-1

-5

-2

-10

-3

-15

-4
0

1

2

3

Bandwidth

4

5

0

1

2

3

4

5

Bandwidth

Notes: Each figure plots the coefficients on Post × High from regressions where police (crimes) per 10,000 residents is the
dependent variable and only applications with scores within the indicated bandwidth of the cutoff are used. 95% confidence
bands are from standard errors clustered at the city level. All regressions includes controls, city × application fixed effects,
event time fixed effects, event time fixed effects interacted with the application score, and year × pre-program cell fixed effects.
Cities are weighted by one over the number of applications.

31

Figure 9: First Stage and Reduced Form Estimates by Varying Definitions of Post

Sworn Officers

Murder

1

Rape

.05

.4

0

.2

.8
.6

0

-.05

.4

-.2
-.1

.2
1

2

3

4

-.4

5

1

Treatment Length

2

3

4

5

1

Treatment Length

Robbery

2

Assault

0

1

-.5

0

-1

-1

3

4

5

Treatment Length

Burglary
4
2
0
-2

-2

-1.5
1

2

3

4

5

-4
1

Treatment Length

2

3

4

5

Treatment Length

Larceny

1

2

3

4

5

Treatment Length

Auto Theft

5

0

0

-1

-5

-2

-10

-3

-15

-4
1

2

3

4

Treatment Length

5

1

2

3

4

5

Treatment Length

Notes: Each figure plots the coefficients on Post × High from regressions where police (crimes) per 10,000 residents is the
dependent variable and only applications with scores within the indicated bandwidth of the cutoff are used. 95% confidence
bands are from standard errors clustered at the city level. All regressions includes controls, city × application fixed effects,
event time fixed effects, event time fixed effects interacted with the application score, and year × pre-program cell fixed effects.
Cities are weighted by one over the number of applications.

32

Figure 10: Effect of Exceeding the Threshold on Arrests

Murder

Rape

.1

Robbery

.2

0

0

-.1

-.2

-.2

.5
0
-.5

-.4

-.3

-1

-.6
-3

-2

-1

0

1

2

3

-3

Year Around Application

-2

-1

0

1

2

3

Assault

1
0
-1
-1

0

1

2

3

Year Around Application

-1

0

1

2

3

Larceny

1.5
1
.5
0
-.5
-1
-2

-2

Year Around Application

Burglary

2

-3

-3

Year Around Application

5

0

-5
-3

-2

-1

0

1

2

Year Around Application

3

-3

-2

-1

0

1

2

3

Year Around Application

Auto Theft
.5

0

-.5
-3

-2

-1

0

1

2

3

Year Around Application

Notes: Dependent variable is arrests per 10,000 residents. 95% confidence bands from standard errors clustered at the city level.
Figures plots coefficients on interactions between an event time indicator and a high score indicator. Regression includes
controls, event time fixed effects, event time fixed effects interacted with the application score, city × application fixed effects
and pre-program cell × year fixed effects. Cities are weighted by one over the number of applications.

33

Table 1: Breakdown of Sample by City Size and Application Year

Size Group

Unique Cities

2009

Applications
2010 2011 2012

1,000-2,500

475

421

241

79

45

53

2,500-5,000

687

587

340

145

77

104

5,000-10,000

941

804

477

221

130

195

10,000-25,000

1204

1032

652

331

199

309

25,000-50,000

594

528

304

173

111

167

50,000-100,000

350

312

169

153

76

105

100,000+

123

99

48

45

23

49

Total

4374

3783

2231

1147

661

982

2013

Notes: Cities observed in multiple categories are placed in the group they appear in most often. The groups indicated are those
used to construct the pre-program cell × year fixed effects except that the 50,000-100,000 and 100,000+ groups are pooled
together.

34

Table 2: Summary Statistics for Applicant Cities
High Score
3.992
(10.76)

Low Score
2.058
(4.503)

Total
2.438
(6.297)

Per Capita Income

3.704
(1.041)

4.027
(1.171)

3.963
(1.154)

Unemployment Rate

7.558
(2.977)

7.504
(2.689)

7.515
(2.748)

Percent Black

0.133
(0.151)

0.101
(0.111)

0.108
(0.120)

Percent Hispanic

0.121
(0.153)

0.108
(0.129)

0.111
(0.134)

Percent Age 15-24

0.140
(0.0288)

0.138
(0.0316)

0.139
(0.0311)

Sworn Officer Rate

23.71
(9.160)

20.66
(8.684)

21.26
(8.862)

Violent Crime Rate

66.36
(48.77)

27.37
(28.41)

35.04
(36.82)

Property Crime Rate

475.0
(222.0)

274.9
(167.4)

314.2
(196.3)

Population

Notes: Standard deviations in parentheses. An observation is a city × application. Number of observations by group: 1,371
(High Score); 7,433 (Low Score); 8,804 (Total). There are 4,374 unique cities and cities are weighted by one over the number of
applications. Characteristics reported as of the year prior to application.

35

Table 3: Regression Discontinuity Estimates

Above Threshold
Mean
IK Bandwidth
Cities
Observations

Pr(Win)
0.69***
(0.03)
.15
.39
1343
1766

Grant Funding
50998***
(4977)
16703
.78
2223
3371

Police
0.633***
(0.201)
21.85
.93
2510
3947

Violent
-1.678
(1.64)
46.32
.72
2098
2887

Property
-10.456
(7.3)
425.48
.79
2245
3198

Notes: Robust standard errors from Calonico et al. (2014) in parentheses. Bandwidth choice is the optimal bandwidth from
Imbens and Kalyanaraman (2012). Dependent variable in Column 1 is an indicator for grant receipt. Dependent variable in
Columns 2-5 is the change in y per 10,000 residents between one year prior and one year after program application. Application
score is controlled for via local linear regression with a triangular kernel.

36

Table 4: Effect of Exceeding the Threshold on Police and Crime

Police
0.0328
(0.117)

Violent Crime
-0.280
(0.971)

Property Crime
-2.321
(4.130)

3 Years Prior

-0.0391
(0.115)

-0.173
(0.900)

-0.0973
(3.774)

2 Years Prior

-0.110
(0.101)

-0.330
(0.785)

-0.180
(3.488)

Application Year

0.345***
(0.109)

-1.711**
(0.805)

-4.823
(3.211)

1 Year After

0.943***
(0.128)

-2.518***
(0.919)

-10.77**
(4.273)

2 Years After

0.783***
(0.165)

-2.896***
(1.087)

-14.13***
(4.756)

3 Years After

0.678***
(0.183)

-1.382
(1.197)

-12.65**
(5.349)

4+ Years After

0.882***
(0.201)
22.54
4201
8459
84590

-2.497*
(1.331)
48.05
4201
8459
78993

-16.62**
(7.105)
433.58
4201
8459
80587

4+ Years Prior

Mean
Cities
City x Applications
Observations

Notes: Standard errors clustered at the city level in parentheses. Dependent variable is police (crimes) per 10,000 residents.
Table displays coefficient on event time indicators interacted with an indicator for whether the application score at time zero
exceeds the threshold. Each regression includes controls, city × application fixed effects, event time fixed effects, event time
fixed effects interacted with the application score, and year × pre-program cell fixed effects. Cities are weighted by one over
the number of applications.

37

Table 5: Effects of Grants on Police and Crime

Post

Post x High

Grant Funding
-2298.4***
(659.1)

Police
0.226
(0.166)

50926.6***
(1552.9)

0.748***
(0.129)

Police
Mean
Elasticitiy
F-Stat
Cities
City x Applications
Observations

4201
8459
84590

22.54
4201
8459
84590

Violent Crime
0.525
(1.114)

Property Crime
3.509
(6.039)

-2.904**
(1.244)
48.05
-1.36
31.19
4201
8459
78993

-16.23**
(6.412)
433.58
-.84
29.76
4201
8459
80587

Notes: Standard errors clustered at the city level in parentheses. Table presents IV estimates corresponding to equation (4).
Each regression includes controls, city × application fixed effects, event time fixed effects, event time fixed effects interacted
with the application score, and year × pre-program cell fixed effects. Cities are weighted by one over the number of applications.

38

Table 6: IV Estimates of the Effect of Police on Individual Crime Types

Police
Mean
Elasticitiy
F-Stat
Cities
City x Applications
Observations

Murder
-0.0896**
(0.0420)
.42
-4.8
28.52
4205
8473
79850

Rape
-0.138
(0.179)
4.08
-.76
28.32
4203
8465
78462

Robbery
-1.390***
(0.383)
10.69
-2.93
31.77
4203
8468
78981

Assault
-1.127
(1.032)
33.16
-.77
26.77
4090
8258
77141

Burglary
-2.464
(1.738)
86.8
-.64
29.4
4109
8297
78190

Larceny
-8.579*
(4.778)
311.12
-.62
28.74
4109
8290
79286

Auto Theft
-3.536***
(0.979)
36.52
-2.18
31.66
4110
8297
77404

Notes: Standard errors clustered at the city level in parentheses. Table presents IV estimates corresponding to equation (4).
Each regression includes controls, city × application fixed effects, event time fixed effects, event time fixed effects interacted
with the application score, and year × pre-program cell fixed effects. Cities are weighted by one over the number of applications.

39

Table 7: Robustness Checks

Murder

Rape

Robbery

Assault

Burglary

Larceny

Auto Theft

Same as Table 6

-.09**
(.04)
[28.52]

-.14
(.18)
[28.32]

-1.39***
(.38)
[31.77]

-1.13
(1.03)
[26.77]

-2.46
(1.74)
[29.4]

-8.58*
(4.78)
[28.74]

-3.54***
(.98)
[31.66]

Balanced Samples

-.09**
(.04)
[11.98]

-.05
(.21)
[11.8]

-2.25**
(.89)
[9.550]

-.9
(1.35)
[12.53]

-2.51
(1.92)
[23.46]

-14.5**
(6.95)
[16.55]

-4.46***
(1.65)
[14.05]

Balanced Panels

-.05
(.05)
[32.22]

-.13
(.16)
[34.54]

-1.38***
(.36)
[36.07]

-1.72*
(1.02)
[32.99]

-1.4
(1.69)
[32.01]

-8.70*
(4.53)
[31.91]

-3.59***
(.93)
[35.25]

Pop >10,000 Only

-.07
(.05)
[13.57]

-.25
(.28)
[14.09]

-1.76**
(.74)
[17.1]

-2.41
(1.88)
[11.91]

-.9
(3.01)
[14.19]

-9.52
(8.359)
[12.9]

-5.33**
(2.08)
[16.65]

Flexible Score Controls

-.11*
(.06)
[15.63]

-.28
(.23)
[15.85]

-.88*
(.51)
[15.95]

-1.81
(1.69)
[13.18]

-3.15
(2.8)
[13.4]

-7.71
(6.53)
[16.24]

-1.81
(1.23)
[16.77]

Flexible + Close

-.12*
(.07)
[14.49]

-.24
(.25)
[15.4]

-1.16**
(.58)
[14.36]

-2.74
(1.81)
[12.88]

-3.94
(3.09)
[12.92]

-8.43
(6.29)
[18.06]

-2.6*
(1.36)
[15.64]

Notes: Each coefficient is from a separate IV regression. Standard errors clustered at the city level in parentheses. First-stage
F-statistic for the corresponding regression in brackets. All regressions include controls, city × application fixed effects, event
time fixed effects, event time fixed effects interacted with the application score, and year × pre-program cell fixed effects.
Cities are weighted by one over the number of applications. Balanced Samples uses only cities with valid data for that crime
type in all years. Balanced Panels drops 2013 applications and uses only data between 4 years prior and 2 years after the
application. Flexible Score Controls allows the event time × score effect to vary by whether the score exceeds the threshold.
Flexible + Close repeats this specification using only applications within 1 point of the threshold.

40

Table 8: IV Estimates of the Effect of Police on Arrests

Police
Mean
Elasticitiy
F-Stat
Crime Effect
Cities
City x Applications
Observations

Murder
-0.0686
(0.0424)
.24
-6.04
21.48
-.05
3507
7110
67172

Rape
-0.00820
(0.105)
.9
-.19
22.59
-.22
3506
7105
66365

Robbery
-0.326*
(0.168)
2.68
-2.57
28.42
-.97
3506
7108
66452

Assault
0.445
(0.615)
14.53
.65
23.03
-.3
3488
7078
65925

Burglary
0.490
(0.483)
10.22
1.01
22.74
-2.6
3496
7094
65857

Larceny
-0.538
(2.204)
48.85
-.23
23.14
-8.43
3496
7087
66041

Auto Theft
-0.0890
(0.177)
3.54
-.53
24.91
-3.22
3497
7094
65692

Notes: Same as Table 6 except that the dependent variable is arrests per 10,000 residents. Crime Effect reports the coefficient
on police from a regression where crimes per 10,000 residents is the dependent variable and the sample is the same as that used
to estimate the arrest effect. The crime estimates for robbery, larceny, and auto theft are statistically significant. The p-values
for the crime estimates (in order) are 0.224, 0.269, 0.006, 0.778, 0.165, 0.089, and 0.001.

Table 9: Victimization Costs of Crime Types
Crime Type

Victimization Cost
$7,000,000

Murder
Rape

$142,020

Robbery

$12,624

Assault

$38,924

Burglary

$2,104

Larceny

$473
$5,786

Auto Theft

Notes: Costs of non-murder crime victimization taken from Cohen and Piquero (2009). Cost of murder taken from standard
VSL estimates in the literature. $7m is the dollar value used in (Chalfin and McCrary 2016a).

41

Appendix For Online Publication
Figure A-1: Yearly Appropriations for COPS Hiring Program, FY 1995-2013

Dollars (Millions)

1500

1000

500

0
1995

2000

2005

2010

2015

Year

Notes: Appropriations data from James (2013). Dashed line denotes 2005, my first year of data used in the regressions.

Figure A-2: Simple RD Plots for Individual Crime Types
Murder

Rape

.2
.1
0
-.1
-.2
-.3

Robbery

.5

2

0

0

-.5

-2

-1
-1

-.5

0

.5

1

-4
-1

Score Relative to Cutoff

-.5

0

.5

1

Assault

0

.5

0

0

-10

-5

-20

1

0

.5

1

Larceny

5

-10
-.5

-.5

Score Relative to Cutoff

Burglary

4
2
0
-2
-4
-6
-1

-1

Score Relative to Cutoff

-30
-1

Score Relative to Cutoff

-.5

0

.5

1

Score Relative to Cutoff

-1

-.5

0

.5

1

Score Relative to Cutoff

Auto Theft
-2
-4
-6
-8
-10
-1

-.5

0

.5

1

Score Relative to Cutoff

Notes: See Figure 3 for legend. An observation is a city × application. Bin width selected to have equal mass. Plot shows the
mean two-year change (i.e. change from t−2 to t) in crimes per 10,000 residents for one year prior and one year after the
application year. Cities are weighted by one over the number of applications.

42

Figure A-3: Effect of Exceeding the Threshold on Future Program Activity
Apply

High Score

.2

1
.8

0

.6
.4

-.2

.2
0

-.4
-1

0

1

2

3

4+

-1

Year Around Application

0

1

2

3

4+

Year Around Application

Receive Grant
1
.8
.6
.4
.2
0
-1

0

1

2

3

4+

Year Around Application

Notes: Figure plots coefficients on event time indicators interacted with whether the time zero application exceeded the
threshold. Each regression includes controls, city × event fixed effects, event time fixed effects, and city size × year fixed effects.

Figure A-4: First Stage and Reduced Form Estimates without Score Controls, Varying Bandwidths

Sworn Officers

Murder

1

Rape

.05

.8

0

.6

-.05

.4

-.1

.2

-.15
0

1

2

3

4

5

.2
0
-.2
-.4
0

1

2

Bandwidth

3

4

5

0

Robbery

Assault
0

-1

-1

-2

-1.5

-2

-4

-2

-3

-6

-2.5

-4
2

3

4

5

1

Bandwidth

2

3

4

5

Bandwidth

Larceny
-5

-2

-10

-4

-15
-6

-20
0

1

2

3

Bandwidth

4

5

0

1

2

3

4

Bandwidth

Notes: Same as Figure 6 except without event time × score interactions.

43

0

1

2

3

Bandwidth

Auto Theft
0

4

5

4

5

-8
0

0

3

Burglary

0

1

2

Bandwidth

-.5

0

1

Bandwidth

5

Figure A-5: Police and Crime Event Study Plots for Arrests Sample

Sworn Officers

Murder

1.5

Rape
.4
.2
0
-.2
-.4
-.6

.05
0
-.05
-.1
-.15
-.2

1
.5
0
-.5
-3

-2

-1

0

1

2

3

-3

Year Around Application

-2

-1

0

1

2

3

Robbery
4

0

2

-2
-2

-1

0

1

2

3

-3

Year Around Application

0

1

2

3

Burglary

0

-1

-1

4
2
0
-2
-4
-6

-.5

-1.5

-2

Year Around Application

Assault

.5

-3

-3

Year Around Application

-2

-1

0

1

2

3

Year Around Application

Larceny

-3

-2

-1

0

1

2

3

Year Around Application

Auto Theft
2
1
0
-1
-2
-3

5
0
-5
-10
-15
-20
-3

-2

-1

0

1

2

3

Year Around Application

-3

-2

-1

0

1

2

3

Year Around Application

Notes: Each figure plots the coefficients on Post × High from regressions where police (crimes) per 10,000 residents is the
dependent variable and only applications with scores within the indicated bandwidth of the cutoff are used. 95% confidence
bands are from standard errors clustered at the city level. All regressions includes controls, city × application fixed effects,
event time fixed effects, event time fixed effects interacted with the application score, and year × pre-program cell fixed effects.
Cities are weighted by one over the number of applications.

44

Table A-1: Regression Discontinuity Specification Checks

Above Threshold
Mean
IK Bandwidth
Observations

McCrary Test
-0.072
(0.076)
.67
2927

Cov Index
-1.66
(5.16)
357.87
.86
3686

Police
0.37
(0.54)
21.58
1.21
4948

Violent
2.9
(2.84)
44.83
.83
3405

Property
16.9
(12.2)
378.93
1
4078

Notes: Column 1 reports coefficient (standard error) from the McCrary (2008) test for discontinuity in density. Columns 2-5
report RD estimates where y, measured one year prior to application, is the dependent variable. Robust standard errors from
Calonico et al. (2014) in parentheses. Bandwidth choice is the optimal bandwidth from Imbens and Kalyanaraman (2012).
Application score is controlled for via local linear regression with a triangular kernel.

Table A-2: Regression Discontinuity Estimates for Individual Crime Types

Above Threshold
Mean
IK Bandwidth
Cities
Observations

Murder
-0.007
(0.072)
.39
.87
2377
3314

Rape
-0.241
(0.335)
3.98
.63
1931
2477

Robbery
-0.327
(0.446)
10.46
.87
2377
3366

Assault
-1.944
(1.43)
31.74
.77
2199
3022

Burglary
-1.19
(2.3)
84.92
.8
2262
3179

Larceny
-7.398
(5.66)
304.93
.79
2245
3204

Auto Theft
-0.331
(1.617)
36.7
.77
2199
2973

Notes: Robust standard errors from Calonico et al. (2014) in parentheses. Bandwidth choice is the optimal bandwidth from
Imbens and Kalyanaraman (2012). Dependent variable is the change in crimes per 10,000 residents between one year prior and
one year after program application. Application score is controlled for via local linear regression with a triangular kernel.

45

Table A-3: Effect of Exceeding the Threshold on Individual Crime Types

Murder
-0.0477
(0.0401)

Rape
-0.188
(0.144)

Robbery
-0.170
(0.287)

Assault
-0.233
(0.747)

Burglary
-0.970
(1.237)

Larceny
-4.017
(3.279)

Auto Theft
1.139*
(0.650)

3 Years Prior

-0.0421
(0.0464)

0.0117
(0.167)

-0.519*
(0.271)

0.0329
(0.759)

-0.0444
(1.365)

-1.350
(3.032)

0.394
(0.551)

2 Years Prior

-0.0662
(0.0426)

-0.0323
(0.172)

-0.254
(0.249)

-0.219
(0.695)

0.466
(1.287)

-1.881
(2.780)

0.663
(0.469)

Application Year

-0.0436
(0.0432)

-0.203
(0.160)

-0.720***
(0.277)

-0.969
(0.702)

0.687
(1.231)

-4.440*
(2.648)

-1.214***
(0.452)

1 Year After

-0.120***
(0.0391)

-0.0987
(0.168)

-1.143***
(0.289)

-1.274
(0.776)

-0.712
(1.547)

-7.791**
(3.303)

-1.622***
(0.542)

2 Years After

-0.0804
(0.0521)

-0.0187
(0.184)

-1.509***
(0.296)

-0.948
(0.946)

-1.909
(1.576)

-12.08***
(3.809)

-1.804***
(0.601)

3 Years After

-0.0685
(0.0514)

-0.0347
(0.215)

-1.301***
(0.314)

-0.0371
(1.054)

-2.240
(1.709)

-8.056*
(4.262)

-2.069***
(0.658)

4+ Years After

-0.168***
(0.0546)
.42
4199
8457
79711

-0.437*
(0.246)
4.08
4197
8449
78329

-1.365***
(0.337)
10.69
4197
8452
78851

-0.948
(1.133)
33.16
4085
8247
77046

-5.475**
(2.131)
86.82
4103
8281
78063

-7.069
(5.655)
311.12
4106
8283
79225

-2.628***
(0.740)
36.52
4105
8283
77288

4+ Years Prior

Mean
Cities
City x Applications
Observations

Notes: Standard errors clustered at the city level in parentheses. Dependent variable is police (crimes) per 10,000 residents.
Table displays coefficient on event time indicators interacted with an indicator for whether the application score at time zero
exceeds the threshold. Each regression includes controls, city × application fixed effects, event time fixed effects, event time
fixed effects interacted with the application score, and year × pre-program cell fixed effects. Cities are weighted by one over
the number of applications.

46

Table A-4: Balance Check

Log Population

High Score
0.0396***
(0.00559)

High Score
0.0650***
(0.0173)

High Score
0.0440***
(0.0158)

Log Per Capita
Income

-0.0972***
(0.0219)

-0.0767***
(0.0225)

0.00477
(0.0189)

Unemployment Rate

-0.00832***
(0.00198)

-0.00831***
(0.00196)

-0.0149***
(0.00174)

Percent Age 15-24

-0.411***
(0.147)

-0.392***
(0.149)

-0.220
(0.137)

Percent Black

-0.0914*
(0.0470)

-0.0808*
(0.0472)

-0.111***
(0.0406)

Percent Hispanic

0.0364
(0.0393)

0.0196
(0.0397)

-0.0545*
(0.0330)

Per Capita Sworn
Officers

2.305
(6.817)

-0.356
(6.827)

-3.531
(5.782)

Per Capita Violent
Crimes

29.79***
(2.251)

29.06***
(2.236)

12.46***
(1.760)

Per Capita Property
Crimes

4.394***
(0.408)

4.431***
(0.414)

1.304***
(0.342)

94.26
Yes
7984

0.218***
(0.00608)
24.22
Yes
7984

Application Score
Joint F-Stat
Group FE
Observations

129.25
No
7984

Notes: Robust standard errors in parentheses.

47