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New York Economic Review Volume 49, Fall 2018

The Thin Blue Line:

Police Militarization and Violent Crime1

J. Britton Haynes Jr.2 Alexander F. McQuoid3

ABSTRACT

Recent events such as the riots in Ferguson, Missouri, have highlighted the increased militarization of police forces in

the United States. This paper utilizes a new dataset that covers all military equipment transfers between the Defense

Logistics Agency and local police forces from 1990 to 2014 to consider the effect of increased militarization on crime.

These transactions were conducted under the Department of Defense's 1033 Program and constitute a major transfer

of capital resources to local police departments with nearly two billion dollars transferred in the form of surplus military

equipment. To deal with concerns of identification, we instrument for participation in the 1033 program using state-level

exposure to the military through federal military spending set by Congress. We find that increased capital transfers to

states embodied in military equipment reduces total violent crime and violent crime subcategories. The effect is large

for overtly militaristic equipment such as assault rifles, but also for less militaristic transfers such as communication

equipment, implying that both enhanced capabilities as well as power projection are important drivers of violent crime

reduction. In addition, we find no evidence of a labor input response through additional hiring of sworn police officers,

indicating that the program resulted in a more capital-intensive police force. Further, we find that increased police

militarization results in lower incarceration rates even after controlling for reduced crime rates, suggesting a broader

law and order impact beyond just enhanced capabilities. The results make clear that increased police militarization in

the United States has played a meaningful role in the reduction in violent crime observed over the last twenty-five years.

JEL classification: H56; H7; H72; H76;

1 The views expressed in this paper are those of the authors and should not be attributed to the United States Naval

Academy or Department of Defense. We thank Amit Khandelwal, John Huston, Jonathan Dingel, David Grad, Joao

Salles, Paul Landefeld as well as seminar participants at Florida International University, Eastern Economic Association

Annual Conference, Western Economic Association Annual Conference, and the Congressional Budget Office for

feedback and comments. All errors are our own.

2 Ensign, United States Navy ([email protected])

3 Economics Department, United States Naval Academy, 589 McNair Road, Annapolis, MD 21402 ([email protected])

mailto:[email protected]

New York Economic Review Volume 49, Fall 2018

1 INTRODUCTION

On the night of November 24th, 2014, men patrolled the streets armed with M-4s adorned in body armor and

camouflage fatigues, while shielding their faces with gas masks. This scene seemed reminiscent of a patrol in Iraq,

Afghanistan, or some other foreign war-zone. However, these heavily armed men were not soldiers, but police

officers in Ferguson, Missouri. The police presence in Ferguson put a spotlight on the growing trend of police forces

across the United States employing military grade equipment.

Much, if not all, of this equipment is loaned to police departments across the country through the Department of

Defense (DoD) Excess Property Program 1033. 1033 has transferred nearly $2 billion worth of military equipment to

law enforcement agencies since its roots were formed in the National Defense Authorization Act for Fiscal Years 1990

and 1991. This militarization of United States police departments has raised serious questions about the practical need

and implications for police forces to have access to military equipment such as Mine Resistant Ambush Protected

(MRAP) vehicles and military style uniforms. Supporters state that police may operate more effectively with access to

military grade equipment and tactics, while detractors argue policing is fundamentally distinct from, and antithetical to,

military operations. While many Americans found the militaristic police images in Ferguson startling and uncomfortable,

only limited empirical work has been done to understand the implications of this massive militarization of local police

forces.

In this paper, we utilize data for all 50 U.S. States since the introduction of the 1033 program in 1997 to study the

impact on crime rates through 2013. The amount of military equipment transferred to local police departments varies

wildly across states and over time. We exploit this information to identify the impact of increased militarization on violent

and property crime rates, as well as additional aspects of law and order.

To preview our results, we find that after accounting for state heterogeneity, national secular crime trends, and

selection into the 1033 program, increased police militarization does meaningfully reduce violent crime rates. In

addition, we find no effect of the program on sworn police offer rates, which suggests the program works primarily

through enhancing the capital-intensity of police officers. We find evidence for both a capabilities enhancement effect

and a "projection of power" effect on reducing violent crime rates. Finally, we find that incarceration rates are lower in

areas with more militaristic police forces, even after controlling for declines in crime rates, suggesting a broader impact

on law and order. Based on these results, we conclude that increased police militarization in the United States has

played a meaningful role in the reduction in violent crime observed over the last twenty-five years.

The primary identification issue is that military transfers are not randomly distributed across states, but may

respond to current crime or expectations about future crime. For example, if those areas with the most crime or those

with appropriate expectations about future crime are the localities requesting more militarization, the estimated impact

of militarization will capture both the true effect of increased militarization as well as the selection bias. Since both the

sign of the effect and the selection bias are unknown, this could lead to a variety of inferential mistakes about the true

impact of police force militarization.

To address this concern, we deploy an instrumental variables approach based on state exposure to militarization

through federal military spending. Federal military spending differs across states and over time, and is driven by

historical and international military needs that are unlikely to be directly related to current state crime levels. Federal

military spending is controlled by Congress and mostly set in advance, making it unresponsive to local crime.

New York Economic Review Volume 49, Fall 2018

However, the presence of federal military spending provides state exposure to military culture, language,

personnel, and equipment. While federal military spending is not directly correlated with local crime, exposure through

increased interaction with military customs and personnel influences awareness and interest in military equipment.

Federal military spending is therefore a viable instrument for militarization of the local police force through the 1033

program.

Using a naive bivariate approach, we find no effect of increased police militarization on violent crime rates when

only police militarization is included in the empirical specification. The estimated effect is essentially zero. This

observation, however, conceals important features in the data. First, the inclusion of time trends is significant as the

US as a whole has experienced a secular decline in crime rates. Second, states differ dramatically in their exposure to

crime, and failing to account for these differences results in misleading inferences about the impact of increased

militarization. When both state fixed effects and control variables identified in the previous literature as significant

determinants of crime are included, the estimated effect of militarization is negative, but small. One might be tempted

to conclude that the massive resources transferred via the 1033 program were thus wasted.

However, even after controlling for observables, there is a lingering concern that selection into the 1033 program

has not been adequately accounted for in the analysis. In particular, it seems likely that high crime areas might be more

interested and willing to seek out additional resources, including military equipment transfers through the 1033 program.

This would create a positive correlation between militarization and crime rates, and result in a biased estimated

coefficient compared to the true causal effect.

These concerns are born out when militarization is instrumented for using federal military spending. The IV

specification results in estimates vastly more negative, suggesting that selection into the 1033 program is a significant

factor that needed to be accounted for in the analysis. As a result, the true estimated effect of militarization is quite

large and statistically significant for total violent crime as well as disaggregated violent crime categories such as murder,

forcible rape, aggravated assault, and robbery. We find no robust, statistically significant effects on total property crime

or property crime categories. Our results are robust to alternative specifications, sample periods, manpower

instruments, and assumptions on error terms.

The plan for the rest of the paper is as follows. Section 2 provides a review of the relevant literature, while Section

3 provides a brief description of the history and evolution of the 1033 program. Section 4 introduces the data and

descriptive statistics. Section 5 presents the empirical approach and results. Section 6 concludes.

2 Related Literature

Despite the controversial nature of the 1033 program, there has been only limited empirical

evaluations of the program, or the more general impact of police militarization on crime. The historical

evolution of police militarization has been documented in Balko (2006), Paul and Birzer (2008) and Hall and

Coyne (2012), with a more extensive treatment found in Balko (2013). Starting with Becker (1968),

economists have long considered the interactions between policing, punishment, and crime. While theory

has helped to develop a better understanding of the possible channels through which policing and

punishment might impact crime, the economic literature has predominantly focused on empirical analysis

(see DiIulio (1996) and Cameron (1988)).

The best empirical work has shown that the 1033 program has had a significant and important impact

on crime. The two foundational papers in the literature are Harris et al. (2017) and Bove and Gavrilova

New York Economic Review Volume 49, Fall 2018

(2017). Harris et al. (2017) look at the impact of the 1033 program on local interactions between police

officers and citizens, and find that the program reduced the number of citizen complaints, assaults on police

officers, and increased drug arrests. Bove and Gavrilova (2017) find that overall crime rates are reduced,

although there is no effect on arrest rates. Further exploration of mechanisms leads them to conclude that

military equipment works by improving the capabilities of law enforcement to deter crime. Our approach

here is similar to Bove and Gavrilova (2017), although we consider a longer period of analysis and use a

related, but distinct instrumental approach.

As we treat 1033 as a transfer of capital, parallels arise between it and other programs designed to

provide additional resources to police forces, such as the Community Oriented Policing Services (COPS)

program that was established with the Violent Crime Control and Law Enforcement Act of 1994. Two of the

main components of the COPS program were the Universal Hiring Program (UHP) and the Making Officer

Redeployment Effective (MORE) grants. COPS began at a similar time as 1033 (at the time, the program

was known as Program 1208 as discussed in the next section) due to high levels of crime at the time. 1033

and COPS are similar in that they both work via transfers of resources to Law Enforcement Agencies

(LEAs). While 1033 is a direct equipment transfer, COPS provides grants for hiring more officers through

UHP and grants for purchasing equipment through MORE. Both resource transfer programs were designed

in order to improve the functioning of police forces and ultimately reduce crime. COPS focused on

manpower and common capital equipment, while 1033 introduces restricted military grade equipment.

The COPS program has been analyzed in depth in Evans and Owens (2007). Utilizing the COPS

program as an instrument to test whether shocks in the number of police officers has any effect on crime

rates, they find that the COPS program increased the size of police forces and that there is a negative

relationship with COPS UHP grants and four crime categories: auto theft, robbery, burglary, and aggravated

assault. The authors also found that MORE grants had a negative relationship with the previous four crime

rates as well as larceny rates. This finding suggests that 1033 may also have a negative relationship with

crime rates since both 1033 and the MORE grant portion of the COPS program were designed to enhance

police capabilities via equipment.

There is a long tradition of trying to estimate the effect of more police on crime. Cornwell and Trumbull

(1994) were an early attempt to use a panel data approach to control for unobserved heterogeneity when

they estimated a model of crime using counties in North Carolina. However, even after accounting for time-

invariant heterogeneity and common trends, dealing with selection bias has been the key challenge in this

literature (see Marvell and Moody (1996)). Solving the selection bias inherent in understanding the effect

of police resources on crime has proven challenging, spurring innovative solutions. Levitt (1997) uses

election cycles to instrument for police hiring with the identifying assumption being that politicians up for an

election have an incentive ”to be tough on crime” by hiring more police officers independent of the actual

crime dynamics, although questions have been raised about the approach (see McCrary (2002), Levitt

(2002), and Worrall and Kovandzic (2010)). Fisher and Nagin (1978) argues there are more fundamental

endogeneity concerns when studying police force size and crime determination.

New York Economic Review Volume 49, Fall 2018

More recently, researchers have used features of terrorism (and institutional responses to terrorism)

as instruments for police resources. Klick and Tabarrok (2005) use terror alert levels to instrument for police

levels in DC to tease out the effect of police on crime. They find that higher levels of alerts, during which

DC police are more highly mobilized, are associated with lower crime levels. Di Tella and Schargrodsky

(2004) utilize the allocation of police forces after a terrorist attack in Buenos Aires to study the effect on

motor vehicle theft under the assumption that police force allocation in response to a terrorist attack is

unrelated to crime dynamics. They find that the deterrence effect of police is large, but highly local. Draca

et al. (2011) follow a similar approach in the aftermath of the 2005 terrorist attacks in London, and find

similar results.

There is further debate about determinants of crime beyond police resources. Levitt (2004) and

Shoesmith (2010) provide an overview of the literature on the determinants of crime, and in particular, the

decline starting in the 1990s. There is some consensus on appropriate demographic and employment

factors. Ethnic and racial disparities in crime and the criminal justice system are discussed in Sampson and

Lauritsen (1997), Howson and Jarrell (1987), and Resignato (2000). Macroeconomic cycles have been

identified as important by Raphael and Winter-Ebmer (2001) while measures of income have been studied

by Doyle et al. (1999). The role of the age distribution and its impact on violent crime has been documented

in Perkins (1997), while Levitt (1998) focused on juvenile crime and punishment. Howsen and Jarrell (1987)

discusses determinants of property crime, and shows that violent and property crime are influenced by

different factors.

Prison populations are thought to have a negative relationship with crime as suggested by Marvell and

Moody Jr (1994) among others. Incarceration is thought to work through two specific channels, an

incapacitation effect (”criminals off the street”) and a deterrence effect through the increased threat of

punishment. Levitt (1996) uses prison overcrowding and institutional features as a natural experiment to

identify the causal effects of prison population growth on crime. Kuziemko and Levitt (2004) study the

impact of imprisoning drug offenders specifically on the determination of crime.

Our identification strategy is reminiscent of Nakamura and Steinsson (2014) (see also Hooker and

Knetter (1997)), who use the differential impact of military procurement at the state level to identify fiscal

multipliers, and Barro and Redlick (2011) who use military spending changes related to wars to identify the

effects of government spending and taxes on output fluctuations. In a cross-country context, Creasey et al.

(2012) use variation in military foreign aid to study national building and growth. The political economy of

military spending is highly political, as documented by Mintz (2002). This is particularly useful for our

identification strategy for two reasons. First, national military spending is driven by geopolitical events rather

than local crime dynamics. Second, there is significant variation in state exposure to military spending, and

this is related to historical circumstances that are unlikely to respond to local crime changes (see Braddon

(1995)). These two observations suggest that the exclusion restriction is valid, and as we show in the

analysis below, federal military spending is highly correlated with intensity of participation in the 1033

program, making this a valid instrument for police force militarization.

New York Economic Review Volume 49, Fall 2018

Having surveyed the related literature, we turn next to the specific characteristics of the 1033 program.

3 Background: 1033 Program

With the National Defense Authorization Act for Fiscal Years 1990 and 1991, Congress set the

foundation for what would later become the 1033 program. This act allowed the DoD to transfer surplus

equipment to state and federal agencies to help fight the War on Drugs through the 1208 Program. The

1208 Program was operated directly from the Pentagon through the Regional Law Enforcement Support

Offices. These offices facilitated the transfer of surplus military equipment from the DoD to state and federal

law enforcement. In October of 1995 the Defense Logistics Agency (DLA), the primary supply agency of

the Department of Defense, took control of the program. The National Defense Authorization Act for Fiscal

Year 1997 expanded 1208 and re-branded it as the 1033 Program.

The transition from 1208 to 1033 greatly increased the size of the DoD transfer program. This expansion

allowed for all law enforcement agencies to acquire property for bona fide law enforcement purposes that

assist in their arrest and apprehension mission. Under 1033, the requirement for equipment to be used to

support the War on Drugs was dropped, yet requests for materials to support counter drug operations still

received priority. Following the transition to 1033, between 1997 and 1999 a National Program Office was

created at DLA in order to oversee the entire program. In 2009 oversight of the program was transitioned

to the newly founded DLA Disposition Services Law Enforcement Support Office (LESO) headquartered at

Battle Creek, Michigan. This transition created an office dedicated to the execution and support of the 1033

program.

To become a beneficiary of the 1033 program a state must create a Memorandum of Agreement (MOA)

with the DLA. Once an MOA is formed, the governor of the state must appoint a DLA State Coordinator

who is charged with the oversight of the program within the state to include accountability and proper use

of transferred equipment. Once a State Coordinator is assigned Law Enforcement Agencies (LEAs) may

apply to participate in 1033. Currently, DLA has an MOA with all 50 states, D.C., and the territories of Puerto

Rico, Guam, and the Virgin Islands. Once approved by the State Coordinator and DLA LESO, a

representative from an LEA may visit a DLA Disposition Services Site or visit the DLA's online webpage to

see what equipment is available for transfer. After visiting a DLA Site, a LEA may prepare a request for

equipment accompanied by a justification for why the LEA needs said equipment. Equipment requests are

then sent to the State Coordinator and then DLA LESO, who has the final say, for approval. If approved, a

LEA may take charge of the property and is required to cover all costs associated with the transportation

of the property.

Since the creation of the 1208-1033 program, nearly $2 billion worth of equipment has been transferred

from the DoD to state and federal law enforcement. Figure 1 displays the yearly evolution of program

transfers. These transfers take the form of a regulated loan of capital with the potential for later ownership.

Once 1033 property has been transferred, LEAs are required to utilize the equipment within one year, and

New York Economic Review Volume 49, Fall 2018

must use the equipment for one year. After this initial year, LEAs are required to submit proof of possession

in the form of pictures, descriptions, and serial numbers of all equipment transferred.

LEAs are only required to submit proof of possession annually for equipment valued over $20,000 or

equipment that requires special demilitarization when it is no longer of use. Equipment that does not meet

this criteria is assigned a DLA demilitarization (DEMIL) code of A. DEMIL Code A equipment does not need

to be reported following the initial year of ownership, and LEAs are free to dispose of this equipment as

they see fit after the initial year. 4 LEAs never receive de jure ownership of equipment valued over $20,000,

or equipment that requires special demilitarization. LEAs that have been loaned these types of equipment

must send them back to the DLA when they are deemed no longer useful by the LEA or by the State

Coordinator. For items that are of low value and do not require demilitarization, LEAs take full ownership of

the equipment after one year and are free to use and dispose of it as they see fit.

Accountability of property is a key feature of the 1033 program. Due to the nature of the items transferred,

it is essential for states and the DLA to keep records of all DoD equipment in LEAs hands. To facilitate

accountability and transparency, the DLA provides a roster of all equipment transferred from the DoD to

LEAs from 1990 up to the present. The dataset is organized by state (or territory), and includes information

on which specific agencies received items, what equipment was transferred, quantity received, value of

transferred equipment (when purchased by DoD), date of transfer, and whether or not it requires special

demilitarization or return to DLA.

For example, the Baltimore County Police Department received 275 M16A1 assault rifles (national stock

number 1005-00-073-9421) with a total value of $137,225 on July 31st, 2007, with the requirement that

they be returned to DLA for demilitarization. The rosters are not entirely military equipment though, as 1033

includes a large amount of Code A items. For example, the Washington County Police Department in

Washington, GA, received three guitar amplifiers (national stock number 7720-00-415-1343) with a value

of $583.50 each on February 26, 2014. This information forms the basis on the following analysis to study

the impact of police militarization on crime.

Of the $2 billion of equipment transferred to LEAs through 1033, only 17.3% of it is equipment that has

received a DEMIL code of A. Examples of these code A items include shredders, sleeping bags, cameras,

tools, and various other construction or office items. The vast majority of the equipment, 82.7%, must be

returned to the DLA for demilitarization. Examples of items with these codes include firearms, firearm

components, firearm optics, tactical vehicles, aircraft, boats, and night vision or infrared equipment. One of

the most expensive items in the code B-Q items is the “Mine Resistant Vehicle”. This nomenclature is

assigned to a variety of vehicles commonly referred to by the military as Mine-Resistant Ambush Protected

vehicles, or MRAPs. These vehicles were designed for the DoD to better protect service members in Iraq

and Afghanistan from the threat of IEDs, small arms fire, and land-mines. Since the beginning of 1208-

4 DEMIL codes are standardized and applied to all DLA equipment. Equipment that requires demilitarization

is assigned a DEMIL code of B, C, D, E, F, G, or Q.

New York Economic Review Volume 49, Fall 2018

1033, 559 of these vehicles have been transferred to LEAs, ranging in value from $412,000 per unit to

$1,309,299. Total MRAP transfers are valued at nearly $380 million, accounting for 22% of all code B-Q

transfers and 18.3% of the entire program - more than all code A items combined.

Each locality participating in the 1033 program is in control of how much equipment they request from

the DLA. Figure 2 displays the total value of transfers from 1990-2013 for each state via the 1033 program.

Every state has received some form of transfer, although participation in the program varied widely. Florida

is a clear outlier, with almost $300 million worth of transfers from 1990 to 2014. On the other end of the

spectrum are the Virgin Islands (not depicted) and Alaska with $164,000 and $990,000 respectively.

Summary statistics of total value of military transfers are provided in Table 1 below. Geographically,

Southern states (including Washington D.C.) occupy seven of the top 10 states in terms of military transfers,

with four in the top five: Florida, Texas, Tennessee, and Virginia. 5 Summary statistics for crime and military

exposure are also reported in Table 1.

4 Data

The first step in the analysis is to define a measure of militarization of police forces. The source for

this information comes from a DLA roster of all items transferred from the DoD to law enforcement agencies

in all 50 states, DC, and three territories from 1990 to 2014. Our unit of militarization is the monetary value

of military equipment provided by the DLA to each state per year in US Dollars. This metric is not

representative of the total value of equipment provided to each state by the DLA, but only of equipment that

receives a DEMIL code of B, C, D, E, F, G, or Q. This equipment was chosen as the metric of militarization

due to the special demilitarization requirement that it be returned to the DLA.

Code A items are loaned to LEAs with the ability for them to have de jure ownership after one year,

and most items are readily available on the civilian market and thus not truly “military”. Code A items were

almost exclusively transferred from 2012-2014. The relatively short period for analyzing Code A items

makes it inappropriate for inclusion in the primary analysis, although results are robust to the inclusion of

these codes.

The remaining data is drawn from a variety of sources. The crime statistics for violent and property

crime rates come from the FBI's Uniform Crime Reporting program (UCR). This data includes rates of

crimes per 100,000 population for 50 states and Washington D.C. from the years 1990-2013. The data

includes disaggregated measures of crime such as murder and non-negligent manslaughter, forcible rape,

robbery, aggravated assault, burglary, larceny, and motor vehicle theft. The first four of these measures

are aggregated up into a measure of Violent Crime (VCR), while the last three are grouped together as

Property Crime (PCR). Of particular note is the great difference between the mean violent crime rate and

property crime rate, with property crime being nearly eight times as prevalent as violent crime. Both rates

5 Results are robust to the exclusion of these states, and therefore not driven by the states receiving the most military transfers.

New York Economic Review Volume 49, Fall 2018

vary widely across localities, which influences the decision to use a fixed effects model in order to account

for locality specific heterogeneity. Furthermore, during the time period under consideration, crime rates

have followed a secular decline nationally (see Figure 3), which motivates the inclusion of time trends in

the analysis so as not to wrongly attribute secular forces to militarization.

Demographic data including total population, percentage of the population between 18-24, and

percentage that is black comes from the U.S. Census. This data covers all 50 states and D.C. from 1990-

2013 for population, and all states and D.C. from 2003-2013 for young and black percentages.

Unemployment rates and median income data come from the Federal Reserve Economic Data (FRED) and

covers all 50 states and D.C. from 1990-2013. The portion of a state's GDP devoted to the federal military

comes from the Bureau of Economic Analysis (BEA) and covers all 50 states and D.C. from 1997-2013.

Prison population statistics come from the Bureau of Justice Statistics for the years 1990-2013. Manpower

data comes from Department of Defense personnel historical publications for 1997-2009, and is used for

alternative instrument robustness confirmation.

Due to the limited or lack of available data for Guam, Puerto Rico, and Virgin Islands, these localities

are not included in the analysis, while multiple sample periods are used due to limited availability of control

variables. Where possible, we show that sample period selection has no qualitative effects on the results.

Our primary model focuses on 1997-2013 and 2003-2013.

5 Empirical Analysis

The 1033 program allows for a unique analysis of the interaction between police and crime as it is

focused on the capital of policing as opposed to the more common focus on the labor of policing. In what

follows, we will first focus on model selection using the Violent Crime Rate, before turning to the Property

Crime Rate and the seven disaggregated measures of crime rates. Along the way, we will highlight key

aspects of the data that help to causally identify the effect of increased police militarization on crime.

We begin the analysis by conducting a simple bivariate regression between violent crime rates and

our measure of police militarization, the value of restricted military equipment transferred to the state in a

given year. Limitations in data force us to consider three different samples. First, we focus on all years

between 1990 and 2013, which includes periods prior to the implementation of the 1033 program when

procurement took place under the smaller and more drug-specific 1208 program. Compared to later years,

there were far fewer transfers in terms of quantity and value. Our second sample focuses on the 1033

program only, from 1997 until 2013. Finally, because of limitations with available controls, we also study a

more recent period between 2003 and 2013 when all relevant controls are available. One result of the paper

is that sample selection does not change the fundamental results, although the magnitudes of the point

estimates do differ.

Table 2 reports estimates for the three different samples. In column (1), we estimate a naive pooled

bivariate regression without exploiting the panel structure of the data. For all three samples, the point

estimate is positive, although the all year sample is not statistically significant. If we took this estimate

New York Economic Review Volume 49, Fall 2018

seriously, one would conclude that the increase in police militarization lead to an increase in the violent

crime rate in the US during the 1033 program. For every 1 million dollars of military equipment transferred

to local police departments in the US, violent crime increased by 1.3 to 1.8 crimes per 100,000 residents.

One concern is that at the same time that police militarization was on the rise, there were national

secular downward trends in all crimes, both violent and property, that were unrelated to militarization. Figure

3 shows both violent and property crime rates decreased dramatically from 1990 through 2013, and follow

very similar national trends. Crime rates in 2013 were nearly half of what they were in 1990. This national

decline in crime is a first order feature of the data, and important to account for if a true causal impact of

militarization is to be estimated. If the true effect of police militarization on crime is positive, national trends

towards lower crime might bias the estimates downward. In column (2) of Table 2 yearly time trends are

included. The estimated coefficients on police militarization increase, and all samples imply that for each

additional million dollars spent on military equipment for local police forces, violent crime increased by 3

offenses per 100,000 residents.

An additional concern, however, is that police militarization is not randomly assigned to police

departments, but rather requested based on characteristics of the police departments. That is, there is likely

a selection bias in the transfer of police departments. While the direction of the selection bias could go in

either direction, one plausible view is that areas with high crime or expected high crime are likely to seek

out more resources, including both labor and capital. This would create a positive correlation between

militarization and (expected) violent crime, which would bias the estimate and understate the true effect.

One simple approach to attempt to account for selection bias is to pull out state-specific factors that do not

vary over time using state fixed effects. This is done in Column (3) and Column (4), where the latter includes

both year and state fixed effects.

The estimated coefficient changes dramatically once differences across states are accounted for. The

implied effect is now negative rather than positive, suggesting that increased police militarization actually

reduces violent crime rather than exacerbates it. The switch in sign of the estimated effect is consistent

with a selection bias story whereby the areas with higher (expected) crime are also the areas which utilize

more resources including capital (military) equipment. Column (4) adds time fixed effects to the state fixed

effects, pushing the point estimates closer to 0, once again confirming that national trends in crime need to

be accounted for as well as state differences. The point estimate in Column (4) is highly significant at the

1% and 0.1% level depending on the sample period.

Table 2 encapsulates the challenges facing an empirical analysis of police militarization and crime

rates. Local police departments face very different situations across the country and over time, and

participation in the 1033 program is an active choice. To correctly identify the true causal effect running

from police militarization to crime rates requires a plausible strategy to eliminate the selection bias inherent

in the problem. Our next attempt to deal with the selection bias is through the use of control variables that

have been previously identified in the literature as relevant for understanding the dynamics of crime in the

US.

New York Economic Review Volume 49, Fall 2018

One limitation of the results thus far is the possibility of state and time-varying omitted variables.

Without the inclusion of control variables, it is impossible to determine the robustness and validity of the

previous estimates. The problem is that identifying correct control variables is not without debate. In an

attempt to establish robust estimates, control variables are added to the model accounting for economic

indicators as well as demographic indicators. These results are detailed in columns (1) through (6) of Table

To get a sense of the possible omitted variables problem, control variables are included one by one in

Columns (1) through (5), while Column (6) includes all control variables. In Column (1), the state

unemployment rate is included, which is negative and statistically significant. The point estimate on police

militarization is slightly smaller at -0.7 (compared to -0.9 without any controls) and is statistically significant

at the 1% level. Column (2) includes the median income of the state with no resulting change in the original

point estimate, or its statistical significance. Column (3) includes the prison population percentage, which

has been identified as an important determinant of crime in previous literature. The point estimate on police

militarization becomes more negative and is statistically significant at 0.1%. Column (4) includes the

percentage of the population that is black, while Column (5) includes the percentage of the population that

is between 18 and 24. In both cases the point estimate is similar to the original estimate and highly

significant at the 0.1% level. Finally, in Column (6), we include all controls variables at once. The net result

is that the estimated coefficient on police militarization is highly significant, and only slightly smaller than

the estimate that only include time and state fixed effects. The results imply that for each one million dollars

of military equipment transferred to local police departments, violent crime decreased by 0.72 offenses.

Police militarization, time and state effects, and control variables explain about 50% of the observed

variation in violent crime rates.

As discussed above, however, the addition of controls is ultimately an unsatisfactory exercise, as the

underlying selection issue is not directly addressed. Instead, our preferred approach looks to address the

selection issue head on through the use of instrumental variables. The key identifying assumption here is

that federal spending on military is set by Congress, often years in advance, and that spending differs

across states for historical reasons. That is, federal military spending in a state varies over time and across

states, but for reasons that have nothing to do with local crime in a given year. Instead, we hypothesize that

federal military spending influences access and use of the 1033 program through exposure to military

customs, personnel, and equipment, but does not directly influence local crime rates. Our preferred

specification is therefore:

𝐶𝑟𝑖𝑚𝑒𝑠𝑡 = 𝛼 + 𝛽𝑚𝑖𝑙𝑖𝑡𝑎𝑟𝑖𝑧𝑎𝑡𝑖𝑜𝑛 ∗ 𝑀𝑖𝑙𝑖𝑡𝑎𝑟𝑖𝑧𝑎𝑡𝑖𝑜𝑛𝑠𝑡 + 𝛽𝑧 ∗ 𝐶𝑜𝑛𝑡𝑟𝑜𝑙𝑠𝑠𝑡 + 𝑆𝑡𝑎𝑡𝑒𝑠 + 𝑌𝑒𝑎𝑟𝑡 + 𝜖𝑠𝑡

where the dependent variable is a crime rate variable, militarization is measured as the value of transferred

military equipment to a state in a given year, and controls are drawn from previous literature. Given

New York Economic Review Volume 49, Fall 2018

concerns over selection bias, we instrument for militarization using federal military spending, and focus

on 𝛽𝑚𝑖𝑙𝑖𝑡𝑎𝑟𝑖𝑧𝑎𝑡𝑖𝑜𝑛.

To understand the impact of the IV approach, we begin implementation of the IV using federal military

spending in a model with no control variables. Due to data limitations, the addition of the controls lowers

the number years of data that may be used. Starting first with no controls and the longer time series, Column

(1) of Table 5 replicates the regression from Table 2. In Column (2), using the IV, the estimated coefficient

on police militarization becomes much more negative and continues to be highly statistically significant.

Whereas the simple OLS specification estimates the effect to be a reduction of -1.7 violent offenses per

million dollars of military equipment, the IV estimates is nearly 15 times larger at -22.45. The IV estimates

tells a very different story than the OLS estimate. The IV estimates suggests that there is a very large and

meaningful reduction in violent crime as a result of the 1033 program and the resulting increased

militarization of local police forces.

To evaluate the viability of the instrument, we need to consider the first stage effect of federal military

spending in a state, and its impact on the 1033 program. The first stage (Table 4) finds a statistically

significant relationship between federal military spending at the state level and participation in the 1033

program. Furthermore, the first stage F statistics is 15, suggesting we are unlikely to have a weak

instruments problem. The first stage significance is capturing the fact that exposure to military personnel,

language and customs promotes awareness of the 1033 Program and the equipment available.

Furthermore, the changes in military spending at the state level are correlated with new investments in

military equipment. The product cycle of military equipment means that old equipment is now surplus to

requirements, and therefore available for procurement through the 1033 program.

Based on the assumed validity of the exclusion restriction and the strength of the first stage, this

suggests the instrument is appropriate and useful, and that the resulting IV estimates strongly suggest that

the 1033 program of increased police militarization has had an economically and statistically significant

effect on reducing violent crime in the US.

Without properly accounting for national trends in crime, state heterogeneity, or selection bias

associated with participation in the 1033 program, one would be likely to conclude that the 1033 program

has a positive or negligible negative effect on violent crime. The truth of the matter is much different. Once

properly considered, the 1033 program of transferring military equipment to local police departments has a

meaningful impact on the reduction of violent crime.

To confirm that this finding is robust, we next consider the effect on violent crime with controls and

instruments over the shorter sample. Columns (3) and (4) replicates results from Tables 2 and 3. Columns

(5) and (6) report results when police militarization is instrumented for using federal military spending by

state. While the magnitudes are smaller, the general result is confirmed. Failure to properly account for

selection severely understates the true effect of militarization on violent crime. The impact of increased

police militarization through transfers of military equipment lead to a 12.6 reduction in violent crime offenses

New York Economic Review Volume 49, Fall 2018

per 100,000 residents for each million dollars transferred. The effect is statistically significant at the 0.1%

level, with the model explaining 85% of observable variation in violent crime across US states over time.

To check the robustness of the results to alternative instruments, we next consider multiple

instruments based on the same underlying logic. We augment the federal military spending data with

information on military personnel and total Department of Defense personnel. The idea is that exposure to

DoD personnel, both civilian and military, has an effect on access to the 1033 program, but has no direct

effect on local crime.

Table 6 reports results using personnel data from 2003 to 2009. Column (1) reports a simple

multivariate regression over this shorter time horizon. The estimated effects are more negative, but also

more variable, and no longer statistically significant, likely due to the lack of data. However, when we

instrument using federal spending in Column (2), the coefficient is nearly 15 times as large as in Column

(1), and statistically significant at the 5% level. The difference between this estimate and that found in

column (6) of Table 5 is driven in part by differences in sample size due to data limitation on personnel

data, although given the standard errors we cannot statistically distinguish between the two estimates.

Column (3) of Table 6 extends the analysis by including military personnel along with federal military

spending, with no discernible effect on the estimation. Column (4) includes a third instrument of total DoD

personnel (both military and civilian), resulting is a slightly smaller point estimate of -24.47 and with greater

statistical significance.

Next, we consider the robustness of inference to alternative assumptions on the error term. Table 7

re-estimates the model of Column (6) in Table 5 under four different error term assumptions. Column (1)

uses a simple homoskedastic assumption, and concludes that the effect is statistically distinct from zero at

5% significance. Column (2) uses a heteroskedasticity-consistent standard error estimator, resulting in

smaller standard errors and significance at 0.1%. Column (3) clusters at the state level under the

assumption of correlated shocks within a state, resulting is slightly larger standard errors when compared

to the robust estimator, but still significant at 1%. Lastly, in Column (4), we allow for both spatial and

temporal dependence using a Driscoll-Kray estimator. Geographic regions in the U.S. tend to be similar in

their approach to 1033. The concern is that geographic interdependence is not properly accounted for using

alternative error assumptions. The standard errors are smallest under this assumption, resulting in

statistical significance at the 0.1% level. Regardless of the assumption on error terms, the inferential results

are unchanged. Police militarization has a statistically significant reduction in violent crime.

The lessons from analyzing aggregate violent crime and police militarization are clear and robust.

There is significant heterogeneity across states, and a national secular decline in violent crime, but

increased police militarization via equipment transfers through the 1033 program are associated with

significant (both statistically and economically) declines in violent crimes at the state level. While the

estimated effect appears to be small if only control variables are included, the effect is noticeably larger

once the selection issue is directly addressed using a valid IV approach. We find that increases in police

militarization lead to lower violent crime rates.

New York Economic Review Volume 49, Fall 2018

Having established this result, we next consider the impact of militarization on property crime. There

are good reasons to believe that while property crime and violent crime tend to move together over time,

the specific effect of militarization could deter violent crimes while at the same time, push criminals into less

confrontational crimes such as property crime. That is, militarization can alter the relative cost of committing

a violent crime compared to property crime, not just the overall cost of committing crime. On the other hand,

if a more militarized police force works primarily through a power projection effect, the impact on less

aggressive property crime may be limited.

The results of Table 8 suggest that the impact on property crime is less robust then for violent crime.

Columns (1) through (3) report simple bivariate regressions using the three different sample periods (as in

Table 2 for violent crime) as well as state and year effects. In all three cases, the estimated coefficient is

negative, although it decreases in magnitude as the sample size declines. In Column (3), which focuses on

the period 2003-2013, the estimated effect is not significant. When controls are added in Column (4), the

effect is reduced by 33\% and is statistically insignificant. As discussed above, controls do not directly

address concerns over selection. Columns (5) and (6) re-estimate the models in columns (3) and (4) using

an IV approach. The results are mixed. In both cases, the estimated coefficient is significantly more negative

after accounting for possible selection in the 1033 program, as was the case with violent crime. However,

statistical significance is far from robust. In column (5), with no additional covariate controls, the estimated

impact of police militarization is significant at conventional levels. Adding in socio-economic controls in

column (6) reduces the estimated coefficient, while increasing standard errors, resulting in a loss of

statistical significance. While the point estimates are always negative, fragile inference prevents drawing

strong conclusions about the impact of police militarization on aggregate property crime. However, the

evidence does not support the view that police militarization is reduces certain types of crime at the expense

of other types of crime.

While VCR and PCR are useful aggregates, the process of simple aggregation may be hiding

important information about the determinants of crime, and how they respond to increased police

militarization. To consider these potential differences, we separate VCR and PCR into their seven

component crime rates to determine what specific offenses militarization may be providing deterrence for,

or uncover any positive effects that may be hidden by focusing on the aggregate rate.

The results are displayed in Table 9. The violent crime rate is a simple aggregation of murder, forcible

rape, robbery, and aggravated assault crime rates. Aggregate property crime includes burglary, larceny

theft, and motor-vehicle theft. General patterns found at the aggregate level are confirmed when looking at

the disaggregated components. First, there are no hidden reversals at lower levels of aggregation once

selection is accounted for in the estimation. Second, the general estimation patterns uncovered for

aggregate crime rates hold at disaggregated levels as well. When time and state fixed effects are included

as well as controls, the estimated effects on police militarization are negligible even when they are

statistically significant. However, using an instrumental variable approach results in noticeably larger and

New York Economic Review Volume 49, Fall 2018

more negative estimated effects. The consistency of the patterns at both aggregate and disaggregate levels

is comforting.

All four violent crime categories are statistically significant, while all three property crime categories

are insignificant. While the point estimates for all seven categories are negative, the disaggregated category

results underscore that property crime effects are fragile while the police militarization impact on violent

crimes is robust. By considering the disaggregated categories, we both confirm the robustness of the results

(and the patterns of the results), and also discover the channels through which increased police

militarization operates.

While the 1033 program is effective in reducing violent crime, to more fully evaluate the effectiveness

of the program, we should consider whether it is the militarization that matters, or whether it is the additional

resources that matter. One interpretation of the program is that it transferred significant capital resources

to police departments in need of resources, and as such, one should expect a reduction in crime. An

alternative interpretation is that specific military resources were transferred, and these military resources

have specific effects on crime deterrence. Or put differently, was it the capital resources in general or the

military resources in particular that affected crime.

We can try to provide a preliminary answer to this question by disaggregating transfers based on the

National Stock Number (NSN). A NSN is a 13-digit code attached to each piece of equipment, broken up

into a 4-digit Federal Supply Classification (FSC) followed by a 9-digit item code. The FSC groups together

similar supply products. The first FSC of interest are codes in the 1000s, which include weapons and aircraft

and account for about 40% of the value of equipment transferred. The second FSC of interest are codes in

the 2000s, which includes marine and ground vehicles and accounts for another 40% of transfers. The third

FSC of interest are codes in the 5000s which include tools, hardware, scaffolding and prefabricated

structures, construction and building materials, and communication equipment. This third category

accounts for 10% of transfers.

The three categories we focus on are important because they make up the vast bulk of transfers and

are regularly transferred throughout the period under consideration, but also because they represent

different degrees of militarization. The FSC codes in the 1000s reflect high militarization resource transfers

in the sense that these are capital resources that have very specific military capabilities. The FSC codes in

the 2000s include equipment that has high military capabilities (such as MRAPs), but also less military

capabilities such as utility trucks and cars. The FSC codes in the 5000s include specialized and non-

specialized equipment that provides capital resources without the heavy military emphasis. By

disaggregating the data long measures of high and low militarization, we can try to estimate the relative

impact of specific military equipment compared to general capital equipment transfers.

Results are reported in Table 10. In columns (1)-(3), the baseline regression with state and year fixed

effects are reported with each of the three militarization variables included in the specification using the

different sub-samples under consideration. Regardless of the sample period, medium military transfers

have the largest (negative) impact on violent crime. Low military transfers have the next largest negative

New York Economic Review Volume 49, Fall 2018

effect, but the coefficient is not statistically significant. High military transfers have a consistently small

negative and statistically significant effect on crime. The addition of controls in Column (4) doesn't alter the

story noticeably. The impact on high and medium militarization is negligible, while the estimated coefficient

on low military turns positive (although still statistically insignificant). These results suggest that it is the

militarization of the equipment transfers that matters for violent crime reduction

The story changes, however, once selection concerns are addressed directly with instrumental

variables. We focus on high and low militarization categories, which have the sharpest contrast in military

capabilities. In columns (5)-(8), we instrument for the highlighted category only, both with and without

control variables. Comparing column (5) to column (7), we see that the estimated impact for low military

transfers is nearly 3 times as large as high military transfers, although both are large and significant.

Comparing columns (6) and (8), which include additional controls, the point estimates are very similar and

tell the same story. Low militarization equipment transfers have a noticeably larger effect on violent crime

than high military transfers, although both are economically meaningful and statistically significant.

The result suggest that militarization in and of itself does matter for violent crime deterrence, but that

local police departments would also benefit from additional capital transfers. In terms of a cost-benefit

analysis, this suggests that a brand new dollar of spending on capital resources would provide more bang

when transferred as low militarization equipment. However, given the nature of the 1033 program, which

transfers depreciated surplus military equipment, such a comparison is not completely appropriate. The

empirical evidence supports the view that surplus depreciated military capital equipment of all kinds does

reduce crime rates in the US, making the 1033 program quite successful in achieving the stated mission of

increased police effectiveness in deterring and reducing crime.

To further explore the channels through which the 1033 program impacts crime, we next consider the

impact of the 1033 program on the other major input to police production besides capital: labor. It is possible

that the additional resources transferred via the 1033 program are reducing crime because the program

frees up additional resources that can be used to hire more sworn police officers, or alternatively the value

of an additional police officer increases because of the increased capital stock. Although identification is

challenging, the general consensus is that increased police officers do reduce the amount of crime in an

area. It may be that the observed effects from the 1033 program are operating through a labor channel

rather than a specific militarization channel.

To address this possibility, we explore the impact of capital transfers on the sworn police officer rate

in the state (officers per 100,000 residents). In column (1) of Table 11 we find a positive correlation between

the value of military transfers and police officer rate in a state. In column (2), we include year dummies to

account for any national changes in police officer rates, increasing the estimated coefficient close to 1,

which literally implies that for each additional million dollars in transferred equipment, the state hired 1

additional police officer per 100,000 citizens. In column (3), state fixed effects are included and the

coefficient switches signs and loses statistical significance. This suggests that within states over time, states

New York Economic Review Volume 49, Fall 2018

that receive more military equipment through the 1033 program have fewer police officers per 100,000

citizens, but the effect is not statistically distinguishable from zero.

The inclusion of controls in column (4) confirms the lack of a relationship. To deal with the selection

concerns highlighted above, we again instrument for the intensity of participation in the 1033 program using

federal military spending, and while the estimated effect becomes larger in magnitude, it continues to be

negative and statistically insignificant. Column (6) includes controls along with the IV, and while the

estimated coefficient switches signs again, it is statistically insignificant. Taken together, these results

suggest that increased capital equipment through the 1033 program had no effect on labor inputs.

The lack of a labor input response supports the view that militarization itself is important for the

estimated reduction in crime. Police departments in the US are becoming more capital-intensive, and in

particular, more military-capital-intensive as a result of the 1033 program, resulting in reduced crime. To

confirm the lack of an effect from labor, column (7) includes the police officer rate as an additional

determinant of violent crime, with no statistically distinguishable effect. The coefficient on police

militarization is slightly more negative compared to the estimate when police officer rate is excluded (-15

vs. -16.3), although the two estimates are not statistically distinct.

Finally, we consider the interaction between police militarization and institutions of order via the

incarceration rate. Incarceration rates are thought to have a negative effect on crime rates through two

different channels. One is a deterrence effect through increased cost of punishment when caught, and the

other is an incapacitation effect by taking criminals off the street.

In Table 12, we explore the relationship between increased police militarization and incarceration

rates. In column (1), a simple bivariate relationship suggests that areas with higher police militarization also

have higher incarceration rates, which is weakly significant at the 10% level. The inclusion of year effects

in column (2) has a negligible effect, while the inclusion of state fixed effects resulted in a much smaller

point estimate that is no longer significant, but still positive. In columns (4) and columns (5), the total crime

rate and the lagged total crime rate are included to capture the relationship between crime and

incarceration. The estimates imply that crime in the previous year is associated with higher incarceration

rates in the current year, consistent with a lag in the judicial process. After controlling for the relationship

between crime and incarceration in a state, there is no significant different effect for areas with greater

police militarization.

Once we account for selection using our instrumental variables approach, we find that police

militarization has a negative effect on incarceration rates. This effect is significant at the 5% level. Even

after controlling for the relationship between crime rates and incarceration rates, police militarization results

in lower incarceration rates. Taken together with the earlier results, this suggests that areas with increased

police militarization have lower violent crime rates, and furthermore incarceration rates are lower even after

accounting for the fact that crime rates are also lower. This suggests that police militarization is working by

making police forces more productive, which lowers crime directly, but also changes the calculus of crime,

resulting in an additional reduction in incarceration rates. Given recent concerns about the social costs and

New York Economic Review Volume 49, Fall 2018

externalities of incarceration, it is particularly notable that a more military capital-intensive police force

reduces both violent crime and incarceration rates.

6 Conclusions

The 1033 program has come under greater scrutiny due to concerns over the impact of recent trends

of police militarization. Until recently, most of the rhetoric was driven without regard to empirical evidence.

In this paper, we find robust support for the view that increased police militarization does reduce violent

crime rates significantly, consistent with the emerging literature.

Furthermore, we find that both high military equipment (assault rifles, MRAPs, aircraft) and low military

equipment (communications equipment and specialized tools) reduce violent crime rates, with the

estimated effect somewhat larger for capital transfers that enhance capabilities independent of any power

projection and deterrence. In addition, increases in capital stock had no effect on sworn police offer rates,

suggesting that the program is working through increased (military-) capital-intensive police forces. That is,

police departments used the 1033 program to enhance the capital stock per officer rather than hire more

officers to utilize the additional equipment. This more capable police force has reduced violent crime, and

even after controlling for these reductions in crime, states with a more militarized police force also have

lower incarceration rates, suggesting a broader impact on law and order institutions beyond police

productivity.

Unlike previous results found in Bove and Gavrilova (2017), we do not find robust support for the view

that police militarization reduces property crimes. Although our point estimates are similar, we do not have

sufficient statistical support to conclude these effects are different from zero. Our approaches differ in a

number of dimensions, including of level of aggregation, length of time series, and identification strategy.

However, all of these differences are also true for our analysis of violent crime, for which we find much

more robust support for the view that police militarization reduces these types of crimes. Caution is

warranted in overstating the impact of police militarization on less violent types of crimes such as motor

vehicle theft and larceny, and deserves further investigation.

A potential issue with the present approach concerns heterogeneity within states. There are two

separate problems to consider. First, as discussed in Aneja et al. (2012), there are serious concerns about

the reliability of crime data at sub-state levels. Maltz and Targonski (2002) argue that because of concerns

over reporting, county-level crime statistics should not be used to evaluate the effects of policy changes.

Maltz and Targonski (2003) argue that the state-level crime data are less problematic than county-level

data due to the FBI's cleaning and imputation process.

The second issue concerns the spatial nature of crime and crime deterrence. Crime is highly local,

often affecting neighboring street blocks differently. The process of aggregation to the state level may be

missing important differences at lower levels. Pushing back on this concern is the fact that police equipment

can be deployed easily across local jurisdiction. Much of the equipment transferred was to county and state

New York Economic Review Volume 49, Fall 2018

LEAs that operate across multiple local jurisdictions. Furthermore, inter-agency cooperation would generate

additional spillovers of resources across LEAs.

The question ultimately becomes one of appropriate aggregation. Our view is that the state is the

appropriate level of analysis because of the nature of the 1033 program, which runs through a state

coordinator. Spillovers across jurisdictions within a state are likely to be large, while spillovers across states

relatively small. Concerns over measurement error at sub-state levels further support the decision to focus

on state outcomes. Compared to Bove and Gavrilova (2017), choice of aggregation does not seem to matter

for violent crime, but may matter for property crime, possibly because property crime is more substitutable

across space and more susceptible to measurement error.

While the stated objective of the 1033 Program is to provide capital resources to facilitate the mission

of crime deterrence and reduction of law enforcement agencies, there may be additional effects of the

program beyond crime reduction. In this paper, we focus solely on the effect on crime. However, additional

dimensions of social well-being beyond crime may be impacted by increased police militarization. If

increased police militarization increases social fracture, for example, the costs may exceed the benefits of

reduced violent and property crime estimated here. Insler et al. (2018) find that police militarization reduces

civic engagement (measured by charitable giving and volunteering) for black households, but has no impact

on white households.

Nonetheless, the findings of this paper are important for understanding the impact increased police

militarization has on crime rates. Without properly accounting for geographic heterogeneity, secular national

declines in crime, and selection into the 1033 program, one would conclude that increase militarization had

no effect or even increased crime. Once all of these factors are accounted for, however, it becomes clear

that the 1033 has played a meaningful role in the reduction of violent crime in the United States.

New York Economic Review Volume 49, Fall 2018

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Figures and Tables

Figure 1: Program 1208 / 1033 Annual Transfer Values, 1990-2013

New York Economic Review Volume 49, Fall 2018

Figure 2: Total Transfers by State, 1990-2013

New York Economic Review Volume 49, Fall 2018

Figure 3: Violent and Property Crime Rates, 1990-2013

New York Economic Review Volume 49, Fall 2018

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