THE EFFECTS OF LOCAL LAW ENFORCEMENT BLOCK GRANTS ON SERIOUS CRIME

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THE EFFECTS OF LOCAL LAWENFORCEMENT BLOCK GRANTS ONSERIOUS CRIME*

JOHN L. WORRALLThe University of Texas at Dallas

Keywords: Local Law Enforcement Block Grants, crime rate, UniversalHiring Program, endogenous, police levels

Research SummaryThe Local Law Enforcement Block Grants (LLEBG) Program wassecond only to the Community-Oriented Policing Services (COPS)Program in its funding levels. Some $3 billion was dispensed to localjurisdictions to reduce crime and improve public safety; yet the effectsof LLEBG funding on crime have been all but ignored. Accordingly,panel data from more than 5,000 cities covering a 12-year period(1990–2001) were collected, and index crime rates were regressed onLLEBG funding and appropriate demographic controls. Additionalcontrols for police levels and other federal grants were also introduced,proper checks for endogeneity of grants (and police levels) were per-formed, and the models were subjected to an array of robustnesschecks. A consistent message emerged: LLEBG Program funding wasassociated with significant reductions in serious crime.

Policy ImplicationsAlthough LLEBG funding seemed to reduce serious crime, the resultsalso revealed that the decrease did not occur through the hiring of addi-tional police officers, even though many funds were used for thatpurpose. Other mechanisms were thus at work, but the data did notprovide insights into what these mechanisms were. In any case, every $1in LLEBG funding per capita was associated with approximately 59fewer index crimes per 100,000 people. When combined with the find-ings from recent studies of the effects of community policing grants oncrime, this study suggests additional federal support for local law-enforcement agencies should be considered.

* The author would like to thank Tom Jessor and the Government AccountabilityOffice for valuable assistance in data collection and suggestions for the analysis. Directcorrespondence to John L. Worall, Program in Criminology, The University of Texas atDallas, 800 West Campbell Road, GR 31, Richardson, TX 75080-3021 (e-mail:[email protected]).

CRIMINOLOGY & Public PolicyVolume 7 Number 3 Copyright 2008 American Society of Criminology

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Recently, researchers have expressed interest in the effects on crime offederal assistance to local criminal justice agencies. For example, Zhao,Scheider, and Thurman (2002) found that grants from the Office ofCommunity-Oriented Policing Services (COPS Office) in the U.S. JusticeDepartment led to significant city-level reductions in violent and propertycrime.1 Others (e.g., Evans and Owens, 2007; Government AccountabilityOffice [GAO], 2005) have found that significant reductions in seriouscrime could be attributed to COPS grants, particularly those under the so-called Universal Hiring Program (UHP). Whereas Zhao et al. (2002) con-sidered the direct effects on crime of COPS grants, Evans and Owens(2007) and the GAO (2005) treated grants as instruments for police levelsand thus were concerned with the indirect effects of COPS on crime.

These studies have most likely focused on federal grants because of thefunding amounts involved. Between 1995 and 2000 alone, some $8.8 bil-lion in grants were awarded to local law-enforcement agencies throughoutthe United States (e.g., GAO, 2005). Such significant funding levels makeit such that their effects on crime could be “picked up” in standard signifi-cance tests. COPS, however, is not the only federal program that hasawarded large amounts of money to criminal justice. The Local LawEnforcement Block Grants (LLEBG) Program, which was launched in fis-cal year (FY) 1996, was second only to the COPS Program in the funds itawarded to local agencies—and in its costs to taxpayers. Although the pro-gram is now defunct,2 roughly $3 billion in LLEBG funds were dispersedto police departments, local governments, and allied entities for crime con-trol and promotion of public safety.

National evaluations of the LLEBG Program have been conducted andpublished (Cosmos Corporation, 2005; Yin, Pate, Kim, Sheppard, andWarner, 2001), but whether the LLEBG Program served its intended pur-pose remains largely unknown. That is, the question of whether LLEBGshave reduced crime remains mostly unanswered. In a study of the effectsof policing on crime, the GAO (2005) used LLEBG as instruments forpolice levels in an effort to gauge the effect of policing on crime, but directassociations between LLEBG and crime were not of particular interest.The current study attempts to fill this gap. It does so using panel data froma large sample of U.S. cities. Results suggest that LLEBG significantlyreduced a variety of index offenses in cities of various sizes.

1. Worrall and Kovandzic (2007) disputed this finding.2. A similar program has emerged in its place. It is called the Justice Assistance

Grant Program.


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Federal Assistance to Local Law EnforcementThe Law Enforcement Assistance Act (LEAA) of 1965 marked the first

significant federal government effort to fund local criminal justice pro-grams. The enabling legislation called for $7 million in appropriations,which is an amount that pales in comparison with funding levels of late.When the LEAA Program was discontinued, federal funding levels dwin-dled, but during the late 1980s, they once again became a priority. One ofthe largest programs launched at the time was the Edward Byrne Memo-rial State and Local Law Enforcement Assistance Formula Grant Program(hereinafter the Byrne program). Under this program, which was createdin 1988, the Bureau of Justice Assistance awarded grants to states for useby state and local governments to improve their criminal justice system.Grants could be used for everything from enforcing laws, hiring personnel,and purchasing equipment, to providing training and technical assistance(Dunworth, Haynes, and Saiger, 1997).

The next significant federal effort of note was the so-called COPS Pro-gram, which was created pursuant to the Violent Crime Control and LawEnforcement Act of 1994 (see Worrall and Kovandzic, 2007; Zhao et al.,2002). The program’s mandate has been to improve community policingthroughout the United States, and various programs have been imple-mented for this purpose. The most prominent is the so-called UHP. Otherprograms include Making Officer Redeployment Effect (MORE), whichwas a technology acquisitions program; Accelerated Hiring, Education,and Deployment; Funding Accelerated for Smaller Towns; the Youth Fire-arms Violence Initiative; the Anti-Gang Initiative; the CommunityPolicing to Combat Domestic Violence Initiative; and several others. Mostprograms require a local match. Since the COPS Program’s inception,nearly $10 billion has been awarded to local law-enforcement agenciesthroughout the United States.

Operation Weed and Seed is another noteworthy federal program(Dunworth and Mills, 1999). It has awarded grants for the purpose of first“weeding out” criminals and then “seeding” communities with neededservices, prevention programs, and neighborhood revitalization. Vio-lence Against Women Act grants have been awarded as well. This pro-gram, which was launched in 1996, provides funding for training law-enforcement officials and prosecutors, which creates special domesticviolence prosecution units and implements new procedures in the name ofdomestic violence prevention. More recently, federal funding has takenaim at terrorism, errors of justice, and reentry through such programs asthe State and Local Terrorism Prevention Training and Technical Assis-tance Program, the Solving Cold Cases with DNA Program, the Paul


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Coverdell Forensic Science Improvement Grants Program, and the Pris-oner Reentry Initiative.

Local Law Enforcement Block Grants

The LLEBG Program was launched in 1996 to provide local govern-ment agencies (not just police departments) with funding to reduce crimeand improve public safety. Grants decisions were based on the number ofstate and jurisdiction-level Part I violent crimes (Bauer, 2004; see belowfor more details). In FY 1996, the program awarded more than $400 mil-lion to local governments. Funding peaked at nearly $500 million in FY1998, but dropped to just over $100 million in FY 2004 (Bauer, 2004).Unfortunately, the program has since been discontinued. Nevertheless,some $3 billion was awarded to local law enforcement, and at one point,the program accounted for about 20% of all federal funding for local crim-inal justice efforts (Yin et al., 2001).

The LLEBG Program was born after an amendment to the ViolentCrime Control and Law Enforcement Act of 1994.3 Unlike COPS grants,however, LLEBG funds could be awarded to local units of government,not just to police organizations. The program was also distinctive becauseit placed few restrictions on local governments, and it was less burdensomethan, say, the COPS Program because it required only a 10% match at thelocal level.

According to a Bureau of Justice Assistance publication (Gist, 2000),nearly 60% of grants went to equipment and technology purchases. Therest went, in descending order, to law-enforcement hiring and overtime(22.7%), crime prevention (10.5%), adjudication of violent offenders(3.1%), drug courts (2.7%), school security (2.3%), and multijurisdictionaltask forces (0.2%) (Gist, 2000). As for grant recipients, a national evalua-tion of the LLEBG Program found that roughly two thirds of the primarycontacts on the grants were in law enforcement, and roughly threequarters of grant funds went directly to law enforcement, specifically tohiring, overtime, and equipment (Yin et al., 2001:4–6). Finally, nearly 3,000jurisdictions proposed hiring new officers with their funds.4

Effects of Law-Enforcement Grants on CrimeAn exploration of the association between LLEBG funding and crime is

limited in the sense that it sacrifices detail. In other words, a measure offunding does not adequately capture the many distinct uses for the funds.

3. Public Law 104-034.4. This value includes county-level agencies. The analyses reported in this article

were city level.



Hiring of an additional officer may not (or may) lead to the same reduc-tions in crime that could be witnessed through implementation of amultijurisdictional task force. Likewise, funding police officers’ overtimemay not yield the same returns as launching a drug court, the latter ofwhich the literature supports enthusiastically (e.g., Belenko, 2001). Theseissues notwithstanding, it is still critical to explore, at a macro level,whether billions of dollars in taxpayer funds have been well spent. Indeed,it is all but impossible to evaluate such programs on a national scale with-out a focus on spending amounts.

Plenty of precedents for the research are reported here. Those research-ers interested in the relationship between police and crime, for instance,have sometimes used funding levels in lieu of actual officer counts (e.g.,Deutsch, Simon, and Spiegel, 1990; Ehrlich, 1973; Fox, 1979; Friedman,Hakim, and Spiegel, 1989; Greenwood and Wadycki, 1973; Hakim, 1980;Jacob and Rich, 1981; Jones, 1974; Land and Felson, 1976; Liu and Bee,1983; McPheters and Stonge, 1974; Swimmer, 1974a, 1974b; Wellford,1974). Other researchers have focused squarely on federal grant programs,especially the COPS Program (GAO, 2003, 2005; Muhlhausen, 2001; Zhaoand Thurman, 2001; Zhao et al., 2002). For example, Zhao et al. (2002:7)concluded:

Our analyses suggest that COPS hiring and innovative grant programshave resulted in significant reductions in local crime rates in citieswith populations greater than 10,000 for both violent and nonviolentoffenses. Multivariate analysis shows that in cities with populationsgreater than 10,000, an increase in one dollar of hiring grant fundingper resident contributed to a corresponding decline of 5.26 violentcrimes and 21.63 property crimes per 100,000 residents.

Most recently, researchers have used federal law-enforcement grants tohelp identify the police-crime relationship (e.g., Evans and Owens, 2007;GAO, 2005). The problem is that although police may reduce crime, crimemay lead to increases in the number of police officers, which biases anypresumed relationship between both variables toward zero. No shortage ofresearch has been published in response to this problem (e.g., Levitt, 1997,2002), but the recent approach has been to use grants as instrumentsbecause some grants, particularly hiring grants, can be expected to affectpolice levels but not directly affect (or be affected by) crime. In otherwords, grants may, through hiring, boost police forces and thereby reducecrime. This line of research presents some fairly convincing evidence thateither police levels, federal spending on local criminal justice priorities, orboth, reduce crime.

Moving away from policing, other researchers have explored the effectsof funding levels on crime at a macro level. For example, Worrall (2004)


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explored the effects on juvenile arrests of a delinquency prevention pro-gram in California. His main measure of the program was county-levelfunding allocations. Other researchers have explored associations betweenwelfare spending and serious crime at the aggregate level (e.g., Hannonand DeFronzo, 1998a, 1998b). These efforts complement qualitative stud-ies and site-specific evaluations, offering an assessment of whetherspending for local criminal justice initiatives reduces crime, arrests, andother outcomes of interest. The research reported here continues in thisvein by filling a significant void in the literature.5

MethodsThis article presents the results of a macro-level assessment of the

effects of LLEBG spending on serious crime. Associations between fund-ing levels and crime rates were explored at the city level. The followingsections discuss data, variables, measurement, and estimation proceduresused for the analyses.

Data, Variables, and Measurement

Panel data from a sample of 5,199 cities, which covered the years 1990to 2001, were gathered by the GAO and supplied to the author pursuant toa Freedom of Information Act request. Sources of the data were theOffice of Justice Programs Financial Data, the Uniform Crime Reports(UCR), the Bureau of Economic Analysis in the Commerce Department,the National Center for Health Statistics, and Law Enforcement AgencyIdentifiers Crosswalk in the Bureau of Justice Statistics. The latter file pro-vided geographic identification information for each unit and facilitatedmerging of the various data sources.

The financial data from the Office of Justice Programs contained bothobligations (grant awards) and draw-downs (annual amounts spent bygrant recipients). This research used draw-down amounts, which avoidedthe need to estimate spending patterns (e.g., Evans and Owens, 2007;Zhao et al., 2002).

Data on annual expenditures from several grant programs wereincluded in the master file. These programs included, first and foremost,the LLEBG Program, followed by COPS grants (UHP, MORE, innova-tive COPS grants, and other COPS grants), Byrne program grants, andother federal grant programs (a catchall category for all other non-COPSfederal grants to local law-enforcement agencies and units of government

5. Incidentally, only one study (Cosmos Corporation, 2005) made any effort toperform site-specific evaluations of LLEBG programs, but the effects on crime wereignored.



during the analysis period). All grants data were per capita and lagged byone year to allow for delays between receipt of funds and reductions incrime (Evans and Owens, 2007; Worrall and Kovandzic, 2007; Zhao et al.,2002; and others have taken this approach).

UCR data contained the necessary crime and officer counts. These datawere converted to index crimes (homicide, rape, robbery, assault, bur-glary, larceny, and motor vehicle theft) per 100,000 persons and officersper 10,000 persons. As discussed, roughly 25% of LLEBG Program fundsdid not go directly to law enforcement; however, proper controls for thesize of a city’s police force were necessary because 75% of LLEBG Pro-gram funds did go to police agencies. Additionally, controls for policepresence were also essential because failure to do so could have resulted inspurious associations between grant spending and serious crime.

Data collected from the Bureau of Economic Analysis and the NationalCenter for Health Statistics included population counts used to constructthe aforementioned rates and demographic data, which included per cap-ita income, percent nonwhite, percent 18 to 24 years old, and percentemployed.6 These data were measured at the county level and, as such,were annual estimates. The data in the years between the decennial U.S.Census did not need to be estimated or interpolated. These four variableswere included in regression models for control purposes. The need to con-trol for racial composition finds support in the literature (e.g., Holmes,2000; McNulty and Holloway, 2000). Income and employment controlsalso find support, particularly in the social disorganization literature (e.g.,Bursik, 1988; Sampson, 1985; Shaw and McKay, 1972). Finally, criminal-career research supports the controls for young males (e.g., Blumstein,Cohen, Roth, and Visher, 1986:66). Summary statistics are reported inTable 1.

Estimation Procedure

The author estimated a series of fixed-effects regression and instrumen-tal variables (IV) regression models using the Generalized Method ofMoments (GMM) (Wooldridge, 2001).7 GMM is ideal, as it allows forheteroskedasticity and autocorrelation that are of unknown form. As

6. Percent employed may not be as ideal as percent unemployed, but the percentunemployed was not available in the data received from the GAO.

7. These models were implemented in Stata (StataCorp, College Station, Tex.)with the user-written command –xtivreg2– (xtivreg2 can also be used with exogenousregressors). The IV regressions were estimated when one right-hand-side variable wasconsidered endogenous. Since dedicated fixed effects commands were used, unit dum-mies were not added because they were conditioned out of the estimation process, thussaving thousands of degrees of freedom (an easy explanation can be found here: stata.com/support/faqs/stat/xtreg2.html). Year dummies were added to each specification.


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Table 1. Summary StatisticsObserved Mean S.D. Minimum Maximum

Dependent VariablesHomicides per 100,000 45,621 4.62 7.66 0 162.05Rapes per 100,000 45,614 29.09 30.39 0 824.87Robberies per 100,000 45,619 98.98 169.71 0 2,321.27Assaults per 100,000 45,625 276.99 338.90 0 5,579.04Burglaries per 100,000 45,625 822.25 610.11 0 9,895.44Larcenies per 100,000 45,625 2,542.82 1,864.77 0 29,416.10MV thefts per 100,000 45,625 326.52 399.69 0 5,875.57

Police VariablesLLEBGa 45,625 0.40 1.90 0 129.31Police levelsb 45,624 17.13 11.54 0 457.02UHP 45,625 0.75 2.02 0 67.25COPS MORE 45,625 0.17 1.64 0 190.00COPS innovative 45,625 0.04 0.39 0 16.97COPS miscellaneous 45,625 0.002 0.04 0 3.50Byrne program 45,625 0.02 0.36 0 27.54Other federal 45,625 0.09 1.37 0 122.89

Other CovariatesPer capita income 45,483 23,305.06 7,490.103 5,479 87,098Percent nonwhite 45,483 0.14 0.13 0.0002 0.86Percent 18–24 years old 45,483 0.14 0.03 0.07 0.50Percent employed 45,483 55.93 0.51 0.18 34.80

Notes: MV = motor vehicle; S.D. = standard deviation.a This and all other grant variables, besides police levels, are in (US$) draw-down amountsper capita during the calendar year. Approximately 1,600 of the 5,199 cities received noLLEBG funding during the period covered by this analysis.b Sworn officers per 10,000 people.

Kovandzic, Schaffer, and Kleck (2005:18) observed, “This robustness toarbitrary violations of homoskedasticity and independence is appealing toempirical researchers, not least because it means obtaining valid estima-tion results that does [sic] not require a researcher to model theseviolations explicitly or correctly.” GMM is also advantageous because itnests several familiar estimators, like ordinary least squares, two-stageleast squares, and instrumental variables, within a single framework.

Tests for skew, heteroskedasticity, and autocorrelation in preliminarymodels affirmed that each problem existed in the data. Accordingly, to besafe, models also were estimated with robust standard errors (Huber,1967; White, 1980; Williams, 2000), and they took state-level clusteringinto account through proper adjustments to the standard errors (see Froot,1989; Rogers, 1993).8 The results reported below should thus be consid-ered robust to heteroskedasticity, autocorrelation, and arbitrary

Finally, the data were stationary in levels per the augmented Dickey–Fuller test andHausman tests called for fixed effects in lieu of random effects.

8. The “robust cluster” option was used after –xtivreg2–.



covariance across observations within each state. Lastly, all data were inlevels, which was consistent with Evans and Owens (2007), Worrall andKovandzic (2007), GAO (2005), and Zhao et al. (2002), but robustnesschecks adopted alternative specifications.

ResultsThe first models considered the direct effects of LLEBG on crime. Sub-

sequent models introduced other important controls, which includedpolice levels (officers per 10,000) and other federal grants, to the equa-tions. Next, LLEBGs were treated as endogenous, and then indirectassociations between grants and crime were explored. Finally, numerousrobustness checks were performed.

Direct Effects of LLEBG Funding on Crime

Table 2 presents the results of models analyzing the direct effects ofLLEBG funding on the seven index crimes. This approach was taken byZhao et al. (2002), who estimated the direct effects on crime of variousCOPS grants. The inverse associations between LLEBG funds and crimesuggest that the money led to significant reductions in all index crimesduring the analysis period.9 This interpretation is at least somewhat prob-lematic because grants could easily be correlated with omitted variables,such as police levels and other federal grants. As a first step, however,these estimates offer some preliminary evidence that LLEBG funding mayhave served its intended purpose.

The negative and significant associations between nonwhite and all butthe homicide and assault outcomes were unexpected. Because the intra-unit variation in this variable is minimal, it may have reflected the sameheterogeneity the fixed-effects procedure seeks to estimate. That is, it mayhave been correlated with the unit effects, which introduced the “sign-flipping” (see, e.g., Plumper and Troeger, 2007).10

Effects of LLEBG Funding on Crime, Controlling for Police Levels

Zhao et al. (2002) were criticized by Worrall and Kovandzic (2007) fortheir failure to introduce proper controls for police levels into their modelsof COPS grants and crime. In the current case, it was critical to control for

9. This finding may suggest that cities that experience higher-than-usual crimerates in the past will have lower future crime rates, not that funding reduced crime.Robustness checks that account for past crime growth/decline address this issue. SeeTable 8 and the accompanying discussion.

10. This regressor was also less refined than separate ones for different racial cate-gories, which also could have contributed to the unexpected results. Unfortunately, amore refined measure of race was not available.


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Table 2. Effects of LLEBG Funding on CrimeHomicide Rape Robbery Assault Burglary Larceny MV Theft

LLEBG –0.191 –0.587 –6.472 –14.224 –14.693 –17.995 –7.627(3.56)** (2.18)* (2.88)** (2.51)* (2.45)* (2.23)* (4.23)**

Income 0.000 0.000 –0.001 –0.001 –0.003 –0.026 –0.005(1.37) (0.37) (1.41) (0.57) (0.76) (3.42)** (1.53)

Nonwhite –4.306 –93.099 –441.822 –277.696 –2,199.530 –6,274.531 –1,453.593(0.62) (5.85)** (2.94)** (1.43) (3.55)** (3.99)** (2.65)*

Percent 18–24years old –2.913 71.502 104.611 219.042 –1,276.271 –5,293.537 1,500.905

(0.18) (0.81) (0.48) (0.38) (0.81) (1.52) (1.89)Employment 0.579 3.859 8.003 9.924 31.080 –12.419 66.679

(1.77) (2.06)* (0.79) (1.00) (1.25) (0.09) (1.37)

Observations 38692 38687 38690 38696 38696 38696 38696Units 4377 4377 4377 4377 4377 4377 4377

Notes: Robust t statistics are in parentheses. All test statistics are robust to heteroskedasticity andclustering. MV = motor vehicle.*p < .05. **p < .01.

police levels, first, because 75% of the cities sampled saw their grants godirectly to municipal police departments and, second, because studies ofthis nature need at least some controls for other criminal justice prioritiesand preferences. Related to this latter point, omitted variable bias couldbe a problem if there is a correlation between police levels and LLEBGand police levels and crime. Accordingly, officers per 10,000 were intro-duced into the models reported in the previous section. The results arepresented in Table 3.

The author’s initial expectation was that LLEBG effects would bewashed out by the introduction of police controls. This expectation did notpan out. More interesting still, the only significant police coefficients werein the positive direction. This observation is likely symptomatic of theendogeneity of police levels. If, for example, the effect of crime on policeis more pronounced than the effect of police on crime, a positive associa-tion may be revealed. Steps to address this endogeneity problem, and thepossible endogeneity of LLEBG funding, were thus taken. The resultsfrom these models are reported below.

Effects of LLEBG Funding on Crime, Controlling for Police Levelsand Other Federal Grants

Even with proper controls for police levels, the association betweenLLEBG funding and crime could be spurious because of omission of fund-ing levels from other federal grant programs. In other words, an agencythat received LLEBG may have also secured other grants, which couldhave been themselves inversely associated with crime. Table 4 thuspresents the results of models in which controls were introduced for bothpolice levels (per 10,000) and per-capita spending in other federal grant



Table 3. Effects of LLEBG Funding on Crime, Controlling for PoliceLevels

Homicide Rape Robbery Assault Burglary Larceny MV Theft

LLEBG –0.204 –0.672 –6.341 –14.169 –17.306 –22.472 –7.098(3.74)** (2.49)* (3.42)** (3.19)** (2.73)** (2.87)** (3.64)**

Police levels 0.011 0.277 0.395 1.376 3.967 18.585 1.471(0.73) (4.49)** (1.96) (2.98)** (3.78)** (5.15)** (2.66)*

Income 0.000 0.000 –0.001 –0.001 –0.003 –0.024 –0.006(1.53) (0.30) (1.48) (0.52) (0.77) (2.99)** (1.64)

Nonwhite 2.072 –85.701 –345.654 –328.623 –2,123.573 –5,309.901 –1,252.235(0.38) (5.31)** (2.64)* (2.21)* (4.00)** (4.04)** (2.30)*

Percent 18–24years old 1.171 102.889 169.279 627.733 –247.070 –2,307.844 2,206.071

(0.09) (1.48) (0.86) (1.52) (0.21) (0.88) (2.89)**Employment 0.708 4.435 12.156 10.611 51.849 30.760 90.914

(1.73) (1.91) (0.83) (0.86) (1.39) (0.18) (1.36)

Observations 47,620 47,612 47,618 47,624 47,624 47,624 47,624Units 5,054 5,054 5,054 5,054 5,054 5,054 5,054


programs. Spending levels from these programs were captured in six vari-ables: UHP spending, COPS MORE spending, innovative COPS grantsspending, miscellaneous COPS grant spending, Byrne program grantspending, and an additive measure of all other federal grant spending.Once again, these data were draw-downs, the actual amounts spent at themunicipal level during each calendar year.

The inverse associations between LLEBG spending and serious crimestood up with these controls.11 This finding is important on two levels.First, failure to control for other federal grant programs could have led tospurious associations between LLEBG funding and crime. Second, thegrant amounts could also serve as proxies for other unmeasured variables,such as agency “progressiveness” that would otherwise have been left outof the main models. There is no way of knowing this of course, but anagency (or city) that receives more grants than its neighbor could be moreserious about crime prevention, which is something that may not havebeen captured by a single grant measure.

The Functionally Exogenous Nature of LLEBG

It is conceivable that whereas LLEBG funding could have reducedcrime, crime rates may have encouraged local jurisdictions to seekLLEBG. Indeed, the LLEBG funding process required exactly this type of

11. Per a reviewer’s recommendation, the author also ran models with all non-LLEBGs summed into a single variable. The results were not altered. They are availa-ble upon request.


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Table 4. Effects of LLEBG Funding on Crime, Controlling for PoliceLevels and Other Federal Grant Programs


LLEBG –0.194 –0.597 –6.569 –14.323 –15.060 –18.655 –8.173(3.52)** (2.06)* (3.04)** (2.49)* (2.66)* (2.30)* (5.52)**

Police levels –0.007 0.227 0.165 0.599 2.399 13.943 0.852(0.65) (4.16)** (0.84) (1.22) (2.55)* (4.23)** (1.43)

UHP –0.047 –0.206 –2.499 –4.109 –10.279 –14.254 –3.232(1.59) (1.55) (3.40)** (5.55)** (8.50)** (2.49)* (1.52)

COPS MORE 0.019 –0.039 –0.170 –0.437 –2.359 –6.330 –1.381(0.70) (0.84) (1.07) (0.77) (3.51)** (2.33)* (2.45)*

COPSinnovative –0.153 –0.468 –6.615 –8.615 –26.366 –62.817 –13.393

(1.69) (1.06) (3.85)** (2.26)* (5.22)** (3.80)** (2.94)**COPSmiscellaneous 0.283 –2.843 –39.094 –32.210 –104.460 –566.781 –5.229

(0.30) (0.66) (2.69)** (2.03)* (4.04)** (2.55)* (0.14)Byrneprogram 0.103 –0.454 2.054 2.408 –2.408 17.303 –3.342

(0.73) (1.27) (0.66) (0.53) (0.30) (1.11) (0.53)Other federal 0.034 –0.023 1.430 1.674 4.515 3.718 3.771

(1.25) (0.22) (1.34) (1.40) (1.11) (0.66) (2.02)*Income 0.000 0.000 –0.001 –0.001 –0.003 –0.024 –0.005

(1.34) (0.55) (1.40) (0.53) (0.70) (3.29)** (1.52)Nonwhite –3.880 –90.714 –416.264 –236.903 –2,087.547 –6,077.160 –1,406.996

(0.56) (5.52)** (2.90)** (1.27) (3.53)** (4.04)** (2.63)*Percent 18–24years old –3.222 74.702 96.472 213.187 –1,278.002 –5,080.215 1,496.729

(0.20) (0.86) (0.43) (0.38) (0.83) (1.51) (1.90)Employment 0.570 3.755 7.406 8.943 28.100 –21.939 65.361

(1.73) (2.13)* (0.72) (0.88) (1.16) (0.18) (1.36)



action. The formula for grant distribution followed a two-step procedure.First, states received funds based on their three-year average number ofPart I violent crimes compared with the same for all other states that sub-mitted data to the FBI (see Bauer, 2004:2). Second, individual agenciesreceived funds following the same procedure, except allocations werebased on each agency’s three-year average of Part I violent crimes dividedby the state total. Thus, because grant allocations were to be based onprior crime, endogeneity would seem to be a problem.

Researchers rarely have the luxury of understanding the precise mech-anics of a simultaneous relationship between two variables. In literaturethat examines police level-crime relationships, for example, researchershave generally speculated that crime boosts police levels in the same waypolice levels reduce (or increase) crime. Here, however, the LLEBG Pro-gram funding protocol specified, a priori, a two-way relationship with an



elaborate explanation for precisely how crime was to affect grants. Thismechanism permitted easy testing to check whether, in fact, past crimewas significantly associated with LLEBG. The author thus regressedLLEBG on the three-year average of each agency’s Part I violent crimerate divided by its respective state’s Part I violent crime rate.12

Table 5. Effects of Past Crime on LLEBG FundingFull Model Model 2 Model 3 Model 4 LLEBG > 0

3-years pastcrime –53.704 –51.963 –58.594 –57.771 37.712

(1.65) (1.61) (1.89) (1.87) (0.80)Police levels 0.028 — — — –0.017

(3.56)** — — — (0.38)UHP 0.046 0.052 — — 0.007

(3.73)** (3.88)** — — (0.53)COPS MORE 0.019 0.019 — — 0.012

(1.57) (1.57) — — (0.84)COPSinnovative 0.084 0.084 — — –0.090

(2.74)** (2.67)* — — (2.85)**COPSmiscellaneous 0.069 0.074 — — –0.087

(0.33) (0.36) — — (0.42)Byrneprogram –0.519 –0.535 — — –0.012

(1.71) (1.70) — — (0.12)Other federal 0.381 0.388 — — 0.412

(1.85) (1.86) — — (1.46)Income –0.000 –0.000 –0.000 — –0.000

(2.64)* (2.76)** (2.30)* — (0.60)Nonwhite 5.601 5.504 6.064 — –3.635

(1.89) (1.83) (1.88) — (0.69)Percent 18–24years old –4.289 –4.798 –3.366 — –5.189

(0.75) (0.83) (0.55) — (0.78)Employment –0.152 –0.142 –0.151 — –0.579

(1.40) (1.29) (1.29) — (0.43)

Observations 38694 38695 40531 40658 7955Units 4377 4377 4403 4417 2143

Notes: Robust t statistics are in parentheses. All test statistics are robust to heteroskedasticityand clustering.† p < .10. *p < .05. **p < .01.

The results of various models are reported in Table 5. Because pastcrime failed to achieve significance at conventional levels, LLEBGs weretreated as functionally exogenous in the models reported throughout this

12. This estimation roughly approximated the LLEBG award process while keep-ing the analysis in rates.


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article. Because this finding directly contradicts the LLEBG fundingformula, some explanation is in order. Recall that funding decisions werebased on numbers of Part I violent crimes, not on rates. That is, the fund-ing decisions did not take into account agency size, city population, andthe like. The variables constructed for the analyses reported in this article,however, were rates.

Some associations between past crime rates and LLEBG nearlyachieved significance in Table 5. Had the author declared significance atthe .10 level, these inverse associations may have biased the reported asso-ciation between LLEBG and crime in Tables 2–4, 7, and 8. In other words,if LLEBG reduced crime, and crime in turn reduced LLEBG, then theLLEBG coefficients may have overstated the inverse association betweenLLEBG and crime. To guard against this possibility, the author alsoregressed the crime variables on endogenous LLEBG, exogenous policelevels, and the controls. LLEBGs were instrumented with the second andthird lags on non-LLEBG. The instruments passed applicable relevanceand validity tests, and the inverse association between LLEBG and crimeremained strong. These results are available from the author upon request.

Indirect Associations between LLEBG and Crime

The GAO (2005) and Evans and Owens (2007) were the first to treatfederal law-enforcement spending as an instrument for police levels.Evans and Owens instrumented police levels with what they called “paidofficers granted” (2007:188), which is a sum of grant totals from two pro-grams: UHP and the COPS Distressed Neighborhood Program. Theirlogic for doing so was that hiring grants increased police levels but couldnot be expected to affect crime directly, except through police levels.13

The GAO took a similar approach, but it instrumented police levels withseveral federal grant programs, which are the same ones also considered inthis study.

When police levels are instrumented with federal grants, the relation-ship between grants and crime effectively becomes indirect. Better stated,the federal grant variables effectively “replace” police levels in the maininstrumental variables equations. One can estimate “reduced form”regressions to observe how this replacement is so. In such models, thedependent variable of interest is regressed on all instruments and exoge-nous regressors (see, e.g., Evans and Owens, 2007:195, Table 5).

To state that an association between grants and crime is “indirect” maynot be the technically correct description, but it is at least nearly accurate:

13. Recall that the two requirements for a “good” instrument are correlation withthe endogenous regressor (relevance) and independence from the error term in themain equation(s) (validity).



Hiring grants may boost police forces and thereby affect crime. That is,hiring grants may not affect crime except through the police. At least thislogic is offered up in previous studies (Evans and Owens, 2007; GAO,2005). The possibility remains, of course, that hiring grants may be corre-lated with other unobservables, but because the police level-crimeconnection was of secondary concern in this article (i.e., not the key sub-stantive concern), any instrument limitations should be taken in stride.Readers are invited to consult Evans and Owens (2007) and GAO (2005)for additional defense of using COPS grants as instruments for policelevels.

If, as previous research suggests, COPS hiring grants can be expected toaffect crime through police levels, then it stands to reason that the sameshould apply in the LLEBG context. Recall that roughly 75% of LLEBGfunding went to law-enforcement agencies, and several agencies used thefunding to hire more officers. Thus, it is realistic to expect that LLEBGmay have affected crime indirectly through additional hiring. To be sure,such an effect could have been tempered by direct linkages betweenLLEBG funding and crime. The alternative is that LLEBG funding didnothing to alter appreciably the ratio of sworn officers per 10,000 people.Both possibilities were explored, and the results are presented in Table 6.

Table 6 contains the results of regressions of police levels on LLEBGfunding and on funding from the other six federal grant programs alreadymentioned.14 The individual coefficients reveal that only UHP was signifi-cantly associated with police levels. LLEBG, in contrast (along with theother federal programs), did not alter police levels. The significance ofUHP has interesting implications for some results already presented. Hir-ing was significant in Table 5, which is not problematic because it isreasonable to expect that dedicated hiring grants increased police forcesizes. The significance of hiring may also explain the significant and posi-tive associations between police levels and crime found in Tables 3 and 4.The positive associations between police levels and crime in those tableswere most certainly symptomatic of endogeneity. Accordingly, additionalmodels were estimated in which police levels were treated as endogenousand instrumented with UHP. All other variables, which include LLEBG,were treated as exogenous. Results are presented in Table 7.

Two interesting findings emerge from the results reported in Table 7.First, LLEBG funding retained its significant and inverse association withall seven index crime rates. Second, the positive associations betweenpolice levels and crime (see Tables 3 and 4) disappeared. Indeed, the coef-ficients became negative and significant for robbery, assault, and burglary.

14. To use instrumental or two-stage least-squares terminology, these are “firststage” regressions.


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Table 6. Effects of LLEBG Funding and Other Federal Grants onPolice LevelsLLEBG 0.057 — — — — — — 0.015

(1.56) — — — — — — (0.35)UHP — 0.152 — — — — — 0.152

— (3.79)** — — — — — (3.86)**COPS MORE — — 0.011 — — — — 0.002

— — (0.55) — — — — (0.11)COPSinnovative — — — 0.003 — — — –0.047

— — — (0.04) — — — (0.80)COPSmiscellaneous — — — — –0.027 — — –0.462

— — — — (0.06) — — (1.15)Byrneprogram — — — — — –0.562 — –0.636

— — — — — (1.17) — (1.35)*Other federal — — — — — — 0.152 0.160

— — — — — — (1.54) (1.68)Income –0.000 –0.000 –0.000 –0.000 –0.000 –0.000 –0.000 –0.000

(2.33)* (2.21)* (2.33)* (2.31)* (2.31)* (2.35)* (2.39)* (2.37)*Nonwhite –3.455 –4.278 –3.228 –3.194 –3.192 –3.216 –3.004 –4.155

(0.56) (0.68) (0.52) (0.51) (0.51) (0.51) (0.49) (0.67)Percent 18–24years old –16.428 –15.976 –16.610 –16.593 –16.593 –16.953 –17.007 –16.775

(1.74) (1.72) (1.75) (1.75) (1.75) (1.77) (1.79) (1.80)Employment 0.626 0.630 0.620 0.619 0.618 0.628 0.614 0.636

(0.81) (0.81) (0.80) (0.80) (0.80) (0.81) (0.80) (0.83)

Observations 38,696 38,696 38,696 38,696 38,696 38,696 38,696 38,696Units 4,377 4,377 4,377 4,377 4,377 4,377 4,377 4,377

Notes: Robust t statistics are in parentheses. All test statistics are robust to heteroskedasticity andclustering.*p < .05. **p < .01.

Of all the models estimated and whose results have been reported thus far,the Table 7 models are arguably most appropriate. They accounted forendogeneity of police levels and treated LLEBG and other federal fund-ing as exogenous.

The coefficients reported in Table 7 can be interpreted as follows: Forevery $1 per capita of LLEBG funding, the homicide rate declined by 0.19per 100,000. So, if a city of 100,000 people received a $200,000 grant, itcould expect 0.38 fewer homicides per 100,000 people.15 This reductionmay not seem drastic, but with an average homicide rate of 4.62 per100,000 people (see Table 1), this translates into roughly an 8% reduction.These findings are fairly consistent with previous research (see GAO,2005, Appendix VI, Table 17).

15. Estimates near the end of Table 8 can be interpreted similarly (e.g., 20.963fewer violent crimes per 100,000 for each dollar of LLEBG spending).



Table 7. Effects of LLEBG Funding on Crime with Endogenous PoliceLevels (UHP Instrument)


LLEBG –0.190 –0.566 –6.317 –13.893 –13.941 –16.580 –7.816(3.60)** (2.29)* (3.63)** (2.68)** (3.40)** (2.65)* (6.06)**

Police levels –0.317 –0.996 –16.145 –26.036 –63.724 –71.611 –19.883(1.43) (1.08) (2.28)* (2.95)** (4.03)** (1.65) (1.21)

COPS MORE 0.019 –0.033 –0.133 –0.373 –2.187 –5.962 –1.326(0.87) (0.67) (0.33) (0.39) (1.38) (1.78) (1.72)

COPSinnovative –0.167 –0.521 –7.377 –9.854 –29.425 –66.560 –14.351

(1.81) (1.11) (4.12)** (2.39)* (4.76)** (3.75)** (3.34)**COPSmiscellaneous 0.134 –3.274 –46.527 –44.159 –133.576 –597.942 –14.300

(0.13) (0.74) (2.77)** (1.95) (3.57)** (2.39)* (0.49)Byrneprogram –0.095 –1.211 –8.299 –14.468 –44.219 –35.788 –16.444

(0.33) (1.11) (0.78) (0.85) (1.10) (0.72) (0.86)Other federal 0.083 0.180 4.042 5.949 15.157 17.842 7.112

(1.32) (0.78) (1.42) (1.57) (1.46) (1.29) (1.47)Income 0.000 –0.000 –0.003 –0.003 –0.009 –0.032 –0.007

(0.39) (0.17) (2.58)* (2.00) (1.66) (3.39)** (1.62)Nonwhite –5.162 –95.686 –483.957 –347.481 –2,361.841 –6,427.398 –1,492.980

(0.75) (6.04)** (2.35)* (1.37) (2.82)** (3.59)** (2.34)*Percent 18–24years old –8.419 53.936 –177.390 –234.190 –2,389.535 –6,530.084 1,148.076

(0.47) (0.61) (0.65) (0.34) (1.41) (1.83) (1.49)Employment 0.771 4.467 17.711 25.713 69.474 28.772 78.307

(1.40) (1.69) (0.80) (1.33) (1.01) (0.15) (1.19)



Robustness Checks

Table 8 presents the results of various robustness checks. LLEBG coef-ficients and t statistics are reported. Additionally, the “base” model foreach row in Table 8 was the regression of the appropriate crime rate onLLEBG, endogenous police, other federal grant programs, and relevantsociodemographic controls.

Researchers rarely complain when samples achieve the size of thoseused in the analyses reported here. But the large sample surely maskedvariations in the effects of LLEBG on crime that could have been attrib-uted to jurisdictional size. In response to this concern, four additional setsof models were estimated with subsamples, which range in size from 625cities to almost 2,500 and correspond to different population sizes (seeTable 8 for the breakdown). For the most part, the LLEBG coefficients


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Table 8. Robustness Checks (LLEBG Coefficients and Associated tStatistics Reported)


Population 0–25,000a –0.090 –0.306 –2.855 –9.524 –9.081 –11.825 –3.348(2.28)* (1.37) (2.34)* (2.03)* (1.90) (1.40) (2.90)**

Population25,001–50,000b –0.257 –1.161 –15.182 –43.334 –33.026 –56.645 –11.135

(1.95) (2.28)* (3.82)** (8.48)** (3.55)** (2.27)* (1.42)Population50,001–100,000c –0.528 –1.243 –17.511 –26.800 –39.928 –36.695 –24.553

(6.18)** (4.14)** (6.46)** (5.26)** (5.82)** (2.67)* (3.22)**Population more than100,000 –0.389 –1.536 –14.022 –27.634 –24.480 –17.988 –10.367

(3.75)** (4.30)** (3.80)** (5.99)** (3.26)** (1.20) (1.57)Log-level –0.014 –0.010 –0.014 –0.018 –0.002 –0.001 –0.003

(3.05)** (3.07)** (3.68)** (3.05)** (0.71) (1.27) (0.91)Log-log –0.101 –0.010 –0.096 0.000 –0.051 0.023 –0.001

(8.62)** (1.19) (2.07)* (2.14)* (2.66)* (2.69)** (0.03)No controls –0.196 –0.593 –6.740 –14.267 –15.073 –18.458 –8.053

(3.49)** (2.16)* (2.77)** (2.50)* (2.40)* (2.09)* (4.21)**No lags –0.193 –0.700 –6.274 –14.272 –16.658 –20.987 –7.163

(3.28)** (2.53)* (3.92)** (3.21)** (2.91)** (3.06)** (4.65)**Two lags on LLEBG –0.164 –0.593 –6.380 –13.744 –16.037 –21.420 –7.946

(3.02)** (2.21)* (2.88)** (2.07)* (2.49)* (2.22)* (7.30)**No clustered standarderrors –0.190 –0.566 –6.317 –13.893 –13.941 –16.580 –7.816

(5.08)** (4.22)** (5.34)** (5.43)** (4.25)** (3.76)** (5.38)**No robust standarderrors –0.190 –0.566 –6.317 –13.893 –13.941 –16.580 –7.816

(3.60)** (2.29)* (3.63)** (2.68)** (3.40)** (2.65)* (6.06)**No robust/clusterstandard errors –0.190 –0.566 –6.317 –13.893 –13.941 –16.580 –7.816

(10.32)** (8.40)** (23.70)** (22.15)** (12.15)** (7.33)** (13.86)**Heterogeneous yeareffects –0.148 –0.376 –4.612 –10.821 –6.137 5.871 –2.983

(2.97)** (1.82) (2.43)* (2.24)* (1.61) (2.55)* (2.75)**Crime growth cells –0.150 –0.336 –4.443 –10.391 –5.194 8.103 –3.189

(2.79)** (1.78) (2.78)** (2.21)* (1.82) (2.77)** (3.47)**Violent and propertycrime –20.963 –38.336

(2.95)** (3.69)**Aggregate crime –59.263

(3.54)**

Notes: Robust t statistics are in parentheses. All test statistics are robust to heteroskedasticity and clustering.Unless otherwise specified, models estimated were the same as those reported in Table 7. MV = motor vehicle.a Sample consisted of 2,485 units.b Sample consisted of 1,308 units.c Sample consisted of 695 units.*p < .05. **p < .01.

remained negative and significant. The effects were minimal in the smallercities but were pronounced in the largest cities.

Next, to ensure the models were not sensitive to a linear specification,log-level and log-log models were estimated. The first of these modelsregressed logged crime rates on levels of the other variables. The secondmodel regressed logs on logs. Clearly the results were not altered to a



significant extent. Additional models with no controls, no lags of spend-ing,16 two lags of spending,17 and no adjustments for either clustering,heteroskedasticity, or both, were also estimated. The LLEBG coefficientsretained their significance levels for the most part.

Dummy variables for each year were included in the regressions sum-marized in Tables 2–7. These dummies captured year-to-year shocks thatcould have affected all cities simultaneously and thus could have yieldedspurious associations between LLEBG funding and crime were they notincluded in the models. The problem is that year dummies cannot ade-quately capture preexisting trends in either LLEBG funding and/or policelevels. If, for example, LLEBG funding was distributed during a timewhen police forces were expanding (clearly the case as a result of theUHP), then any association between LLEBG and crime could have alsobeen spurious. Alternatively, if a particular jurisdiction was experiencing asignificant decline in crime during the observed period, then year dummieswould not have captured the trend.

In response to these concerns, models with heterogeneous year effectswere also estimated. These effects were calculated by (1) regressing policelevels in the pre-LLEBG period on a linear time trend for each unit; (2)doing the same for the aggregate crime rate; (3) organizing the coefficientsfrom each regression into quartiles; and (4) interacting the resulting cellswith year dummies, for a total of 192 (4 × 4 × 12 = 192) separate yeareffects. Similar approaches were taken in Evans and Owens (2007) andGAO (2005). These “growth cells” replaced the year dummies. LLEBGsignificance levels were not appreciably altered. Models were also esti-mated with only crime growth cells (4 × 12 = 48). The results stayed thesame.

Finally, models of violent, property, and total crime rates were esti-mated. LLEBG funding was significantly and inversely associated witheach of these offense categories. All told, the results presented in Table 8,coupled with those from the earlier tables, provide some fairly convincingevidence that LLEBG funding led to reductions in serious crime through-out the United States during the analysis period. Interestingly, the effectswere considerably more pronounced than those between COPS grants andcrime (e.g., Zhao et al., 2002). It seems, then, that the LLEBG Programmay have given more bang for its buck. The last rows of Table 8 suggest

16. These models checked whether there was a contemporaneous effect ofLLEBG spending on crime.

17. These models checked whether there was a two-year delay between LLEBGspending and its effect on crime. They assumed that it took two years instead of one toput new technologies in the field, hire new officers, and otherwise spend LLEBG fundsbefore the effects on crime could be realized.


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that every $1 in LLEBG funding per capita was associated with 59.263fewer index crimes per 100,000 people.

Discussion and ConclusionsResearchers have become increasingly interested in the effects on crime

of federal support for local law enforcement (e.g., Evans and Owens, 2007;GAO, 2005; Worrall and Kovandzic, 2007; Zhao et al., 2002). Most of theirattention, however, has been limited to the Justice Department’s COPSProgram. It is more than a little surprising that the LLEBG Program hasbeen effectively ignored in this literature despite the fact that LLEBGfunding was second only to the COPS Program and once accounted forsome 20% of federal support for local law enforcement (Yin et al., 2001).The research reported here marks the first effort to assess the direct (andindirect)18 effects on serious crime of the LLEBG Program on a nationalscale.

The results of the analyses provide fairly convincing evidence thatLLEBG funding led to reductions in serious crime throughout the UnitedStates. The author began with regressions of index crime rates on LLEBGfunding and appropriate controls. Then several alternative specificationswere adopted. These specifications (1) controlled for police levels; (2) con-trolled for other federal support, including COPS grants; (3) checked forendogeneity of LLEBG funding; (4) explored indirect associationsbetween LLEBG and crime; (4) estimated models with various city popu-lation subsamples; and (5) tested the robustness through several otherspecifications. Across the board, LLEBG funding retained its inverse asso-ciation with serious crime.

The main measure of support to local law enforcement in this study waslagged spending, but it was not without limitations. A one-period lag mayhave failed to pick up contemporaneous effects and/or distant laggedeffects. Robustness checks addressed these limitations, but the possibilityremained that the panel models estimated were not optimal, despite themany different specifications presented.

Implications

The fairly robust inverse association between LLEBG funding andcrime complements another recent body of research, that concerned withthe connection between COPS grants and crime (examples include Evansand Owens, 2007; GAO, 2005; Zhao et al., 2002). Several researchers

18. Recall that GAO (2005) was also concerned with indirect effects, that is, of theeffect of LLEBG funding as an instrument for police levels in a study of the policelevels-crime connection.



(Muhlhausen, 2001; Worrall and Kovandzic, 2007) have found that federalsupport to local law-enforcement agencies for the purposes of increasingtheir community policing activities has reduced crime. Findings fromGranger causality tests (Kovandzic and Sloan, 2002; Marvell and Moody,1996) and the most recent time-series designs (DiTella and Schargrodsky,2004; Klick and Tabarrok, 2005) complement this research. A fairly consis-tent message has developed: Criminal justice spending and crime ratesseem to go hand in hand. The problem is that federal support seems to bedwindling. COPS Program funding continues to be cut, and the LLEBGProgram is no more.

For years, researchers have debated whether successful crime-preventionprograms achieve their results through deterrence or incapacitation. Thedominant assumption in the policing-crime literature is that if an enhancedpolice presence leads to less crime, then deterrence is responsible (e.g.,Pratt and Cullen, 2005:415–417). Another plausible explanation, however,is that crime-prevention programs increase the ability of police to appre-hend law breakers; in which case, subsequent reductions are caused by an“incapacitative” rather than a deterrent effect (e.g., Kessler and Levitt,1999)—assuming sufficient jail space is available. To the extent LLEBGfunding did not significantly reduce crime through additional police hiring,then perhaps incapacitation was responsible. Unfortunately, the limita-tions of the data analyzed do not support a decisive answer.

Thus, only two conclusions can be drawn. One conclusion is that federalsupport for local law enforcement seems to reduce crime. Another conclu-sion is that “generic” crime-prevention funding programs are preferred.Concerning this latter point, whereas LLEBG funding was based on pastcrime, the program’s requirement that jurisdictions simply use their fundsto “improve public safety” may have represented an improvement overother grant programs (e.g., COPS), which mandate that grant funds beused for specific purposes.

Complex systems theory (Henry and Milovanovic, 1991; Milovanovic,1997; Walker, 2007) may offer some additional insight. If we assume localcrime is a system, then inputs into it come in the form of feedback. Feed-back, in this case grants, can be negative (moving the system to lesscomplexity), positive (moving it to more complexity), or nonlinear (posi-tive when needed, negative when needed) (Walker, 2007). An example ofnegative feedback may be allowing grant recipients to undertake initia-tives that they regard as best, in contrast to being forced to follow top-down, one-size-fits-all initiatives, such as UHP. This method could reducecomplexity and thus yield a reduction in crime. In contrast, giving a systemwhat it does not need or want (e.g., more officers for all, as in the case ofUHP) could yield opposite results: A neighborhood could “react badly


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to increased police patrols—in effect, the residents could believe theneighborhood is lost—which could exacerbate the problem and push theneighborhood to a higher level of disorder” (Walker, 2007:575). Thisexplanation may describe why researchers have not been enthusiasticallysupportive of the COPS Program (see, e.g., Worrall and Kovandzic, 2007).But more LLEBG evaluations are needed before we can know for sure, asthis is but a single one.

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350 WORRALL

Zhao, Jihong and Quint C. Thurman2001 A National Evaluation of the Effect of COPS Grants on Crime from 1994

to 1999. Washington, D.C.: U.S. Department of Justice.

John L. Worrall is professor of criminology at the University of Texas at Dallas. Hisinterests are policing, courts, and panel data models. He is co-editor of a forthcomingSUNY Press book, The Changing Role of the American Prosecutor, and editor of thejournal Police Quarterly. He received his Ph.D. in political science from WashingtonState University in 1999.

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THE EFFECTS OF LOCAL LAW ENFORCEMENT BLOCK GRANTS ON SERIOUS CRIME