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Author's personal copy Social Science Research 39 (2010) 506–516
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Police levels and crime rates: An instrumental variables approach q John L. Worrall *, Tomislav V. Kovandzic The University of Texas at Dallas, Program in Criminology, GR31, 800 W. Campbell Rd., Richardson, TX 75080, USA
a r t i c l e
i n f o
Article history: Available online 10 February 2010 Keywords: Police levels Crime rates GMM Instrumental variables Reverse causality
a b s t r a c t While police levels may affect crime, governments may react to crime by increasing police levels. The instrumental variables (IV) approach to this problem has proven difficult due to the problem of locating instruments for police levels. Using panel data from over 5000 cities (1990–2001), we instrumented police levels with two types of federal law enforcement grants, thus yielding over-identified models. We also subjected our instruments to both relevance and validity testing, a step authors of similar studies have yet to take. We found fairly robust inverse associations between police levels and four index crime rates (homicide, robbery, assault, and burglary), but mainly in large cities. Ó 2010 Elsevier Inc. All rights reserved.
1. Introduction Since Becker’s (1968) seminal economic model of crime, dozens of researchers have examined the relationship between police levels (usually measured as officers per 1000 or 10,000 people) and crime. As this literature has matured, questions about the potential endogeneity of policing in crime models have arisen.1 For example, if more police cause less crime, then do governments alter police levels in response to crime? Most researchers appear convinced the answer is yes. This has led to three separate strains of research, each of which attempts to address—or circumvent—the reverse causality problem. First, some researchers have circumvented the simultaneity issue by conducting Granger causality tests, to determine, for instance, whether lags of police levels predict current crime (e.g., Marvell and Moody, 1996; Kovandzic and Sloan, 2002). This approach is advantageous in two respects. First, it helps determine the extent to which police may ‘‘Granger cause” crime and vice-versa. Second, from a policymaking standpoint, Granger models may be more appropriate because it is more likely that police affect crime with a lag, rather than contemporaneously. But therein lies one of the most significant limitation of the Granger causality test; it cannot detect same-period relationships.2 Time series models, often including lags of police levels, have also been estimated.3 Most recently, these researchers have exploited ‘‘natural experiments” (see Angrist and Krueger, 2001, p. 73). For example, Klick and Tabarrok (2005) and DiTella and q An earlier version of this paper was presented at the 2007 Crime and Population Dynamics Summer Workshop in Queenstown, Maryland. We thank Patrick Brandt (UT Dallas), Chetan Dave (UT Dallas), Bill Evans (University of Notre Dame), Bill Jessor (GAO), Mark Schaffer (Heriot-Watt University), and workshop participants for helpful comments. * Corresponding author. E-mail address:
[email protected] (J.L. Worrall). 1 Studies that have ignored this issue, some of which are recent, include Carr-Hill and Stern (1973), Hakim (1980), Hakim et al. (1978), Levine (1975), Phillips and Votey (1975), Wellford (1974), Zhao and Thurman (2001), and Zhao et al. (2002). Other authors have used lags of police to skirt simultaneity on the assumption that police affect crime with a delay and/or presented models in which the cross-influences of crime and police on one another are instantaneous (e.g., Bayley, 1985; Fox, 1979; Greenberg and Kessler, 1982; Greenberg et al., 1983; Greenwood and Wadycki, 1973; Jones, 1974). As Marvell and Moody (1996, p. 617) observe, however, ‘‘. . .current-year crime can affect lagged police levels through common correlation with lagged crime, which is not in the regression and, thus, is in the error term” (also see Fisher and Nagin, 1978, pp. 373–374). 2 Other limitations occur if the functional form is not right and/or there is selection on unobservables. 3 For examples see Corman and Mocan (2000), Corman and Joyce (1990), Corman et al. (1987), Fox (1979), Fujii and Mak (1980), Jacob and Rich (1981), Land and Felson (1976), Liu and Bee (1983), Loftin and McDowall (1982), and Wolpin (1978).
0049-089X/$ - see front matter Ó 2010 Elsevier Inc. All rights reserved. doi:10.1016/j.ssresearch.2010.02.001
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Schargrodsky (2004) examined the effects on crime over time of terror alert levels and actual terrorist attacks, respectively. These approaches were creative because both phenomena constituted exogenous shocks to the police presence (though not necessarily the size of the force), providing an opportunity to detect increases or decreases in crime. The problem, however, is twofold. First, the designs these researchers employed were limited to single jurisdictions and thus the findings were not generalizable. Second, opportunities to commit crime may have decreased during terrorist incidents or alerts (see, e.g., Evans and Owens, 2007, p. 183, n. 4). Finally, a number of researchers have explored the prospect of a simultaneous relationship between policing and crime. The most commonly-employed modeling strategy has instrumental variables (IV) regression. Some of the more prominent examples include Evans and Owens (2007), Government Accountability Office (2005), Levitt (1997, 2002). As is well-known, the primary problem associated with the instrumental variables approach is locating proper instruments, variables which are plausibly correlated with police levels but are uncorrelated with the error terms in the crime equations. Much work remains to be done with the IV approach. First, the search for instruments is not over. Second, nearly all models employing IV methodology have been just-identified,4 meaning ex post instrument validity testing was not possible.5 For those authors who did estimate over-identified models, we have yet to find any reporting of the results of instrument validity tests. This paper seeks to improve on previous IV studies of the police levels–crime (hereafter PL-C) relationship by presenting the results of over-identified models that were estimated with demonstrably relevant and valid instruments. 2. Previous research6 We limit our attention, for the reasons just discussed, to those studies that have used IV regression to estimate PL-C models, and we organize the literature into two categories: (1) studies that have used federal grant spending instruments to estimate PL-C models and (2) all others. We do this in order to draw more attention to the grant instruments, as we draw on law enforcement grants data for our instruments. We begin with the studies that have predated the grants instrument approach. 2.1. Police instruments other than federal law enforcement spending Working from most recently-published to most-distantly published, we begin with Levitt (2002), who instrumented police levels with municipal firefighters. Presumably, firefighter and police levels are associated, but firefighters will not directly affect crime. This assumption is certainly plausible, but Levitt could not test it because his model was justidentified. Indeed, Levitt (2002) pointed out a possible weakness: The number of firefighters might positively covary with the unobserved factors increasing crime. For instance, if for political reasons, increases in police also tend to trigger increases in firefighters, [this could lead] the estimates to understate the true impact of police on crime. On the other hand, with a fixed municipal budget, an exogenous increase in crime may lead to more police and fewer firefighters (p. 1245). Levitt selected the firefighters instrument in response to criticism of his earlier (1997) decision to use electoral cycles (see McCrary, 2002). In his 1997 study, Levitt found growth in police force size during mayoral and gubernatorial elections, thus addressing instrument relevance.7 The reasoning is straightforward; given the saliency of crime as a social issue, persons running for mayor or governor will have incentives to manipulate police forces (or at least promise to do so), leading to an increase in police. The problem is whether campaign timing is correlated with a variable left out of the main crime equation, a realistic possibility. For example, mayors may engage in other crime reduction strategies besides hiring more police. Next, Cornwell and Trumbull (1994) instrumented police levels with two variables. Their model was just-identified, however, because two variables in the main crime equations (police levels and probability of arrest) were considered endogenous. The instruments were (1) an offense ratio of face-to-face crimes (e.g., robbery) to non-face-to-face crimes (e.g., burglary) and (2) tax revenues per capita. Probability of arrest was instrumented with the offense ratio because, presumably, there would more likely be an arrest in a face-to-face crime, but it is doubtful this arrest ratio would directly affect crime. Tax revenues were used to instrument police levels, but this is problematic because while more tax revenues may lead to more police, they could just as well directly affect crime through other channels. Prior to the 1980s, simultaneous models were estimated to study the PL-C relationship, starting primarily with Ehrlich (1973). A problem is that many of these studies relied on questionable instruments. Almost across the board, they excluded demographic variables, such as population density, from the main crime equations (e.g., Bahl et al., 1978; Furlong and Mehay, 1981; Huff and Stahura, 1980; McPheters and Stronge, 1974). This is problematic because such variables are known predictors of crime (both theoretically and empirically). Some researchers also excluded various combinations of other crimes from their individual offense models. Hakim and his colleagues (1984) explained it this way: ‘‘From each crime supply equation, variables controlling for the average return on other crimes in the other crime supply equations are excluded” (p. 728). Howsen and Jarrell (1987) also included a vector 4 5 6 7
That is, the number of instruments has not exceeded the number of endogenous regressors. Instrument validity testing is also called testing for over-identification restrictions. We have deliberately ignored the theory underlying the substantive issue at hand, focusing instead on methodological issues for our submission to JQC. Specifically, the results from first-stage regressions were reported.
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of crime variables other than the crime variable of interests in their police models (see p. 446). These approaches are roughly similar to Cornwell and Trumbull (1994) in the sense they relied on ‘‘internal” instruments, those constructed from the available data. 2.2. Instrumenting police with federal law enforcement spending The notion of instrumenting police levels with federal law enforcement spending, while recent, is not without precedent. Some early police–crime studies instrumented police levels with some variation on either actual police spending or community preferences for additional criminal justice-related spending. For example, Bahl et al. (1978), who estimated three structural equations—a police compensation equation, a police employment equation, and a crime equation—modeled police employment (officers per 1000) using the price of a police employee, along with other factors (p. 70). Swimmer (1974a, 1974b), like Cornwell and Trumbull (1994), used tax revenues, but he included it in a model of the ‘‘demand for police” in a system of two equations: ‘‘As the budget increases across cities, more public services, including police, are bought” (p. 620).8 Fast-forwarding to the present, two recent studies seeking to specify the police–crime relationship have also exploited spending data for identification purposes. This work began when Evans and Owens (2004) drafted a working paper, ‘‘Flypaper cops.”9 The Government Accountability Office (2005) found the paper and emulated it in evaluation of the federal COPS program.10 Evans and Owens went on to revise their paper, which was eventually published in the Journal of Public Economics in 2007. We will not continue to reference the 2005 work, but mentioning it here gives Evans and Owens (2007) due credit for their role in the GAO (2005) report. Unfortunately, the GAO did not completely emulate the Evans and Owens approach, which, as we argue shortly, was problematic. 2.2.1. The Evans and Owens (2007) approach Evans and Owens (2007—hereafter E-O) were interested, like the many researchers whose work we referenced above, in the PL-C relationship. In an effort to identify the relationship, they instrumented police levels with what they called ‘‘paid officers granted” (p. 188). Paid officers granted was modeled as the sum of two federal community policing grant awards to local law enforcement agencies: (1) Universal Hiring Program (UHP) grants and (2) Distressed Neighborhood Program (DNP) grants. The Universal Hiring Program, by far the largest source of COPS grants, has provided billions of dollars of grants to local police agencies for additional policing hiring. The program provides ‘‘matched” grants where the federal government provides up to 75 percent of the cost of hiring a new officer, up to $75,000 per officer over three years, leaving it to recipients to pick up the tab at the end of three years. DNP refers to the Distressed Neighborhood Program. It provides full funding for the hiring of an officer, but awards are for one year. Only 18 sites around the country received DNP grants. The E-O equation used to create the paid officers grant variable was as follows: ‘‘paid officers granted = 0.75UHP hires + DNP hires” (Evans and Owens, 2007, p. 188). First-stage regressions revealed strong associations between lagged paid officers granted and current-year police levels. That is, COPS grants significantly increased the sizes of the police departments included in their sample, although not to the degree the authors expected. The E-O approach to instrumenting police levels is based on the simple premise that hiring grants boost the size of police forces. Hiring is also unlikely to directly affect crime, except through police levels. The possibility remains, however, that some omitted variable is associated with hiring grants and crime (an example may be ‘‘progressiveness”), but this is less likely when the focus is limited to hiring grants, as opposed to other grants intended to support novel programs. Because the E-O model was just-identified (as they noted in the paper), they could not respond to possible criticisms of this sort by testing their identification restrictions. Again, an over-identified model was necessary. 2.2.2. The GAO approach As we already indicated, the GAO (2005) emulated the E-O approach to instrumenting police levels. It did not, however, follow it to the letter. Police levels were instrumented with several federal grant programs, including UHP, Making Officer Redeployment Effective (MORE) grants, COPS innovative grants, other COPS grants,11 Byrne program discretionary grants,12 Local Law Enforcement Block Grants (LLEBG),13 and other non-COPS federal grants (GAO, 2005, Appendix VI, p. 76). All told, 8
Also see Chapman (1976), Greenwood and Wadycki (1973), and Pogue (1975). The paper can still be accessed at: http://www.bsos.umd.edu/econ/evans/wpapers/Flypaper%20COPS.pdf. 10 ‘‘COPS program” refers to the Office of Community-Oriented Policing Services in the U.S. Justice Department. It was created as a result of provisions in the Violent Crime Control Act of 1994 that authorized appropriations of nearly $10 billion for local police departments to hire additional officers, pursue community policing priorities, and implement innovative programs (Public Safety Partnership and Community Policing Act of 1994, Title 1 of the Violent Crime Control and Law Enforcement Act of 1994, P.L. 103-322 [1994], 42 U.S.C. Section 3769dd). 11 MORE, COPS innovative grants, and other COPS grants include all other federal funding from the COPS program besides Universal Hiring. Importantly, most of the grants awarded under these programs were not for hiring. 12 The Byrne program (short for the Edward Byrne Memorial State and Local Law Enforcement Assistance Grant Program) awards both formula and discretionary grants. Formula grants are passed through state-level entities to local agencies and were excluded from the GAO analysis (and ours) because they cannot readily be tracked. Discretionary grants are those awarded, on a discretionary basis, directly from federal to local authorities. 13 Local Law Enforcement Block Grants, according to the U.S. Justice Department, provide ‘‘funds to units of local government to underwrite projects that reduce crime and improve public safety.” Several such grants are used for hiring. 9
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seven separate instruments of police levels were used. Like E-O, the GAO found that UHP grants were positively and significantly associated with police levels (GAO, 2005, Appendix VI, p. 83). Many of the other grants were not associated with police levels, however, yet they appeared in the main crime regressions. 3. Unfinished business Assuming police levels are endogenous, then one or more suitable instruments for police levels must be sought. The foregoing sections looked more at the instruments selected than the requirements for what constitute ‘‘good” instruments. There are two requirements. First, instruments must satisfy the relevance test, that is, be plausibly correlated with the endogenous regressor they are (or it is) replacing. The GAO, E-O, and some of the other authors whose work we have cited have satisfied (or at least tried to do so) the relevance test by reporting first-stage regression results. First stage models regresses police levels on the instruments and all other exogenous variables. Significant coefficients on the instruments suggest instrument relevance. Significance tests alone are not sufficient. This is because when instruments are only weakly correlated with the endogenous regressor, IV estimates of parameters will be biased in the same direction as OLS and estimated standard error will be unreliable. Specifically, standard errors will be too small and the null will be rejected too often (Bound et al., 1995; Staiger and Stock, 1997). Staiger and Stock (1997) recommend conducting an F-test on the instruments in the first-stage regression; an F-statistic of at least 10, in their view, is indicative of relevance. Of course, if the first-stage regression indicates one instrument is irrelevant (i.e., not individually significant) the researcher should consider dropping the instrument as efficiency is not improved by its use (Hall and Peixe, 2003). While the search for relevant instruments is by no means over, the most unfinished business lies in the area of instrument validity. This refers to the requirement that an instrument be uncorrelated with (or orthogonal to) the error term in the crime equation(s). Near as we can tell, none of the studies cited have conducted ex post specification testing to demonstrate instrument validity. Rather, authors have relied solely on theoretical arguments as to why their chosen instruments were unlikely to be correlated with the error term in the crime equations. The lone exception appears to be Evans and Owens’ (2007) study, where they showed no significant association between pre-COPS crime and paid officers granted (p. 189).14 It would be preferable, though, to formally test for instrument validity (Godfrey, 1988, p. 145). In order to assess instrument validity, a model must be over-identified.15 If the researcher has only one instrument the model is just-identified and the validity of the instruments cannot be tested. Most of the IV studies we cited instrumented police levels with a single variable, making for just-identified models. Levitt’s (2002) measure of firefighters, for instance, while relevant, may not have been valid, and it was impossible to assess whether it was. Likewise, E-O combined two hiring grant programs (UHP and DNP) into a single measure of paid officers granted, again yielding a just-identified model. The instruments may still have been invalid. Over-identification restrictions are most often tested using the well-known J-statistic of Hansen (1982). These and other test statistics are easily calculated via the Generalized Method of Moments (GMM) framework (Wooldridge, 2001), which we adopted for the analyses presented in this paper. We now turn to the methods used in our analysis, then we demonstrate in the results section the relevance and validity of our instruments.16 4. Methods This study used the same dataset generated by the GAO for study of the relationship between police levels, COPS grants, and crime rates (see GAO, 2005). The data consisted of yearly observations on 5199 cities throughout the United States, from 1990 to 2001. The dependent variables used in our analyses were the rates per 100,000 of seven index crimes.17 Police variables were officers per 10,000 and ‘‘draw-downs”18 per capita in two grant programs: Hiring and ‘‘other” non-COPS grants (these were our instruments). Hiring grants included funding for hiring under three COPS grants programs: Universal hiring, the Distressed Neighborhoods Program, and COPS in Schools. Importantly, each of these hiring grants are theoretically meaningful as instruments because they could not have affected crime directly, except through police hiring. The ‘‘other” non-COPS grants included all federal grants to local law enforcement agencies excluding those under the following programs: MORE grants, innovative COPS grants, miscellaneous COPS grants, and Byrne grants.19 Other covariates in each of the models were per capita income, percent nonwhite, percent between 18 and 24, and percent employed. Summary statistics appear in Table 1. 14
Even this approach may be limited without introducing controls for current crime. As one reviewer of an early draft observed, in randomized controlled trials, the instrument is assignment to treatment. Instrument validity in this case can be ascertained by examining balance in pre-determined characteristics by treatment assignment. 16 A concern is that high-crime cities may seek more grants than lower crime cities, thus creating a possibility that grants are not exogenous to crime. Worrall and Zhao (2003), however, found no such relationship. Crime rates were not associated with grant getting. 17 These data were cleaned per the procedure described in GAO (2005, Appendix I, pp. 31–32). 18 Draw-downs capture actual spending patterns. Thus we avoided the need to ‘‘model” spending patterns (e.g., Evans and Owens, 2007; Zhao et al., 2002). 19 For more on the details of each program, see GAO (2005). We did not instrument police levels with these other grant programs because preliminary models suggested they could not be properly excluded from the main crime equations. We did, however, include them as controls in models appearing in the robustness check section. 15
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Table 1 Summary statistics. Obs.
Mean
Std. Dev.
Min.
Max.
Dependent variable Homicides per 100,000 Rapes per 100,000 Robberies per 100,000 Assaults per 100,000 Burglaries per 100,000 Larcenies per 100,000 MV thefts per 100,000
47,897 47,889 47,895 47,901 47,901 47,901 47,901
4.57 28.82 96.60 276.47 813.27 2517.74 320.72
7.62 30.20 166.97 340.24 607.31 1860.67 393.87
0 0 0 0 0 0 0
162.05 824.87 2321.27 5579.04 9895.44 29,416.10 5875.57
Police variables Police levels Police officers per 10,000
47,901
17.17
11.68
0
457.02
Instruments for police levels Hiring $ per 10,000 Non-COPS $ per 10,000
47,901 47,901
0.82 0.10
2.16 1.44
0 0
67.25 122.89
Other grantsa MORE $ per 10,000 Innovative $ per 10,000 Misc. COPS $ per 10,000 Byrne $ per 10,000
47,901 47,901 47,901 47,901
0.17 0.04 0.002 0.02
1.62 0.39 0.04 0.35
0 0 0 0
190.00 16.97 3.50 27.54
47,755 47,755 47,755 47,755
23,416 14.06 13.97 56.13
7545.13 12.81 3.24 68.22
5479 0.00 6.76 18.00
87,098 86.07 50.33 72.02
Controls Per capita income Pct. nonwhite Pct. 18 to 24 Pct. employed a
These other grants were introduced as controls in alternative specifications. See Table 5.
Table 1 begins with the dependent variables. Police variables are summarized in three categories. Police officers per 10,000 appear first, followed by our instruments. The category of ‘‘other grants” consists of additional grant programs that were treated as controls in alternative specifications to mitigate against the possibility of a spurious association between police levels and crime. Finally, controls appear near the bottom of the table. 4.1. Approach to estimation We estimated a series of fixed effects instrumental variable models using the Generalized Method of Moments (GMM).20 The GMM estimator, as opposed to the traditional IV estimator, has become increasingly popular in recent years to empirical researchers addressing problems where endogeneity and instrument validity are of paramount concern, as is the case here. Another benefit of the GMM estimator is that the standard errors of the parameter estimates will be robust to arbitrary violations of heteroscedasticity and independence and researchers need not model these violations explicitly or appropriately (Kovandzic et al., 2005).21 Finally, all crime models were estimated with data in their original levels, as opposed to first-differences, to be consistent with Evans and Owens (2007), Worrall and Kovandzic (2007), GAO (2005), Zhao et al. (2002), and other recent studies on the PL-C relationship.22 5. Results We first treated police levels as exogenous. Then we regressed police levels on our instruments and the other variables mentioned above, to demonstrate relevance. Third, we treated police levels as endogenous and instrumented with the grant variables discussed above. Finally, we adopted various alternative specifications to check whether our findings were sensitive to any particular set of models. 5.1. Exogenous police Table 2 contains the results of models where police levels were treated as exogenous. That is, we assumed a unidirectional relationship between police and crime, ignoring the possibility that crime could affect police. These models were 20 These models were implemented in Stata with the user-written command –xtivreg2–. Unit and year dummies were included. Hausman tests called for fixed effects in lieu of random effects. All models were estimated with robust standard errors and took into account state-level clustering (e.g., Froot, 1989; Huber, 1967; Rogers, 1993; White, 1980; Williams, 2000). 21 Many of the same corrections can be made to just-identified IV models. 22 We did not formally test for stationarity, but we estimate models below that account for preexisting trends in the data.
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J.L. Worrall, T.V. Kovandzic / Social Science Research 39 (2010) 506–516 Table 2 Effects of exogenous police levels on crime rates. Homicide
Rape
Robbery
Assault
Burglary
Larceny
MV theft
Police levels
0.005 (0.38)
0.258 (4.43)**
0.219 (0.93)
0.982 (2.31)*
3.486 (3.17)**
17.961 (4.89)**
1.274 (2.22)*
Per capita income
0.000 (1.65)
0.000 (0.44)
0.001 (1.18)
0.000 (0.22)
0.003 (0.63)
0.024 (2.86)**
0.006 (1.54)
Pct. nonwhite
0.860 (0.15)
89.680 (5.78)**
383.252 (2.69)**
412.597 (2.36)*
2226.136 (4.12)**
5443.081 (4.15)**
1294.301 (2.35)*
Pct. 18 to 24
1.784 (0.13)
104.904 (1.47)
188.460 (0.92)
670.219 (1.46)
195.179 (0.16)
2240.463 (0.84)
2227.354 (2.91)**
Pct. employed
0.744 (1.75)
4.554 (1.94)
13.273 (0.88)
13.111 (1.03)
54.902 (1.42)
34.725 (0.20)
92.166 (1.37)
Obs. R-squared
47,620 0.02
47,612 0.02
47,618 0.07
47,624 0.04
47,624 0.23
47,624 0.14
47,624 0.08
Robust t-statistics in parentheses. All test statistics are robust to heteroskedasticity and clustering. Police levels per 10,000. Crime rates per 100,000. * p < 0.10. ** p < 0.05.
Table 3 First stage results (police levels regressed on exogenous variables). Hiring instrument
0.238 (6.57)**
— —
0.234 (6.28)**
Other grant instrument
— —
0.198 (2.10)*
0.187 (2.08)*
Per capita income
0.000 (2.39)*
0.000 (2.57)*
0.000 (2.47)*
Pct. nonwhite
3.869 (0.61)
2.382 (0.38)
3.674 (0.58)
Pct. 18–24
8.597 (1.00)
10.546 (1.19)
9.387 (1.10)
Pct. employed
0.787 (0.85)
0.779 (0.84)
0.783 (0.85)
Obs. R-squared
47,624 0.06
47,624 0.05
47,624 0.06
Robust t-statistics in parentheses. All test statistics are robust to heteroskedasticity and clustering. Instruments per 10,000. Police levels per 10,000. * p < 0.10. ** p < 0.05.
estimated for illustrative purposes only, and as something of a baseline against which to compare the results from subsequent models. Two features of Table 2 are interesting. First, none of the police levels coefficients were negative. Second, five of seven were both positive and significant. This, we submit, is evidence of the endogeneity of police levels. Indeed, if police levels reduce crime and crime positively affects police levels, then the police coefficients will be biased downward—and possibly in the positive direction (e.g., Levitt, 1997). 5.2. Endogenous police Table 3 presents the results of first stage models where we instrumented police levels with hiring grants and ‘‘other grants.” Recall that ‘‘other” referred to non-COPS grants and also excluded grants under three additional COPS programs and the Byrne program. ‘‘Other” was basically a catchall category for a broad range of miscellaneous grant programs. Returning to the table, it is clear that both instruments were relevant in the sense that they were individually and jointly associated with police levels. We present the F-test results in Table 4, to which we now turn. Table 4 presents the results from over-identified models of the PL-C relationship. Police levels were inversely associated with homicide, robbery, assault, and burglary.23 These results are roughly consistent with Evans and Owens (2007), GAO 23
Scatterplots revealed that this relationship was monotonic.
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Table 4 Effects of endogenous police levels on crime rates.
Police levels Log per capita income Pct. nonwhite Pct. 18–24 Pct. employed Reduced form hiring First stage hiring 1993 crime rate Implied elasticity F-stat., excl. instruments p-Value Anderson Canon corr. p-Value Hansen’s J p-Value Obs.
Homicide
Rape
Robbery
Assault
Burglary
Larceny
MV theft
0.257 (2.91)** 0.000 (0.84) 0.186 (0.03) 0.767 (0.05) 0.950 (1.49) 0.058 0.234 5.28 0.76 29.08 .0000 819.900 .0000 0.025 0.8755 47,620
0.081 (0.22) 0.000 (0.19) 90.536 (6.12)** 101.602 (1.44) 4.819 (1.81) 0.034 0.234 28.16 0.08 29.05 .0000 819.526 .0000 1.513 0.2186 47,612
6.157 (2.61)* 0.002 (1.87) 399.595 (2.41)* 126.415 (0.61) 18.261 (0.89) 1.535 0.234 110.30 0.98 29.10 .0000 820.299 .0000 0.174 0.6762 47,618
8.155 (2.73)** 0.001 (0.78) 436.033 (2.29)* 581.304 (1.21) 20.268 (1.51) 1.691 0.234 889.42 0.14 29.09 .0000 820.25 .0000 0.399 0.5277 47,624
21.125 (2.77)** 0.005 (1.07) 2289.260 (3.71)** 434.665 (0.36) 74.180 (1.27) 5.689 0.234 2583.71 0.36 29.09 .0000 820.25 .0000 0.508 0.4759 47,624
11.842 (0.72) 0.027 (3.15)** 5519.522 (3.96)** 2530.475 (0.95) 58.069 (0.29) 4.456 0.234 344.06 0.11 29.09 .0000 820.25 .0000 1.421 0.2332 47,624
5.956 (0.85) 0.006 (1.64) 1312.846 (2.23)* 2156.994 (2.88)** 97.829 (1.30) 2.071 0.234 305.06 0.44 29.09 .0000 820.25 .0000 1.077 0.2993 47,624
Robust t-statistics in parentheses. All test statistics are robust to heteroskedasticity and clustering. Police levels instrumented with hiring grants and other grants. Crime rates per 100,000. Police levels and instruments per 10,000. ‘‘Reduced form hiring” is hiring coefficient from reduced form model. First stage hiring is hiring coefficient from last column of Table 3. Implied elasticity interpreted as one percent increase in hiring leads to an X percent reduction in the applicable crime rate. 1993 police levels were 16.17 per 10,000. * p < 0.10. ** p < 0.05.
(2005), and Levitt (1997, 2002). We also scaled the parameters so as to turn them into elasticities.24 These are reported in the middle of Table 4. So, for example, a one percent increase in hiring was associated with a 0.76 percent reduction in homicide. The elasticities in Table 4 are also remarkably similar (save, possibly, for assault) with those estimated by other researchers (e.g., Evans and Owens, 2007; GAO, 2005; Levitt, 1997, 2002). The bottom portion of Table 4 contains a number of important statistics. First, the F-statistic for the instrument set tests whether the instruments are jointly significantly different from zero. Clearly they were, as evidenced by the p-values. In general, F-statistics of less than 10 are worrisome and likely indicative of weak instruments (Baum et al., 2003; Staiger and Stock, 1997, p. 557). Note that F-statistics in Table 4 all over around 29, suggesting clear instrument relevance. Another test of instrument relevance is also reported in Table 4. The Anderson canonical correlation test is a likelihood ratio test of whether the equation is identified. In other words, it is a test of whether the excluded instruments are correlated with the endogenous regressor. Next, the Hansen’s-J-statistic tests over-identifying restrictions (e.g., Sargan, 1958; also see Wooldridge, 2002, p. 123). The joint null hypothesis is that the instruments are valid, that is, uncorrelated with the error term and that the instruments are properly excluded from the crime equation. The statistic is distributed chi-squared, and significance beyond p = 0.05 suggests that one or more instruments cannot be excluded from the main crime equation. The J-statistic was not significant in any of the Table 4 models. This is important because it suggests our instruments were properly excluded from the main structural equations. It bears mentioning that the percent nonwhite variable was negative and significant for several models reported in Table 4. This is counterintuitive, especially in light of recent studies examining the relationship between race and crime (e.g., Krivo et al., 2009), but we feel it may be an artifact of the panel data. Worrall (2008a, 2008b) found, for example, that racial composition, particularly at the city level, is both invariant and slow-moving, leading to possible collinearity with unit dummy variables. A classic symptom of such collinearity is flipping signs on regression coefficients. 5.2.1. A note about the power of validity tests Our decision to instrument police levels with two federal grant programs requires careful attention to instrument validity. As such, it is critical to understand when these tests will have the power to detect that instruments that cannot be considered exogenous. Assume, as we have here, that we have a model with one endogenous regressor and that the endogenous regressor has been instrumented with two variables. If none of the instruments are valid, the J-statistic for the full set of instruments can, but might not have, any power. 24 This was done using the same formula as Evans and Owens (2007) and GAO (2005), namely (reduced form hiring coefficient/first stage hiring coefficient from full first stage model) (police levels in 1993/crime rate in 1993). Consistent with Evans and Owens (2007) and GAO (2005), we focus on the hiring coefficients. The 1993 crime rate was used in the calculation because there were no hiring grants prior to 1994.
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More technically, consider the simple case of a single endogenous regressor, no exogenous regressors, two excluded instruments ZA (i.e., hiring grants) and ZB (i.e., non-hiring grants), and assume conditional homoskedasticity. Then the J-sta^0 using both Z and Z as instruments with the tistic is numerically equal to a Hausman test that contrasts the IV estimator b A B ^A using just Z (Hayashi, 2000, pp. 233–234).25 Since b is scalar, the Hausman statistic takes this form: IV estimator b A 0 0
0 ^A b ^A b ^0 V ^0 ¼ ^ 1 b H¼N b 0 D 0
^0 ^A b b 0
2
r^ 2 P pr1 o^x2 P pr1 o^^x2 i
i
where one ^ denotes the fitted value of prox regressed on the single instrument ZA, and two ^s denotes the fitted value from a regression on the two instruments ZA and ZB. H is distributed as v2(1), and is simply an alternative and numerically equiv^A . ^0 and b alent expression for the J-statistic. It is easy to see that the test statistic gets its power from the contrast between b 0 Assuming both ZA and ZB are invalid instruments, the test will still have the power to detect that both ZA and ZB are in^0 ) is asymptotically large. This is possible if b ^A and b ^0 converge asymptotically to different biased ^A b valid, but only if (b 0 0 estimators (see White, 1994, p. 274). If, however, ZA and ZB are invalid ‘‘in the same way”, meaning that they introduce ^A and b ^0 will converge asymptotically to the same biased estimator, the same asymptotic bias into estimates of b0, b 0 A ^ ^ (b0 b0 ) will be asymptotically small, and the test will not have the power to detect that both instruments are invalid and hence that both estimators are wrong. It follows, then, that the more unrelated the instruments are to each other, the more credible is a failure to reject the null that the instruments are exogenous, since a failure to reject would require that two unrelated instruments generate the same ^0 . Our instruments are fairly unrelated in the sense that one is hiring grant and the other consists of varasymptotic bias in b ious non-hiring grants (we discuss the implications of an absence of non-grant instruments later). This, coupled with the findings from our validity tests, we feel strongly refutes claims that one or both of our instruments may have been correlated with the error terms in the crime equations. 5.3. Alternative specifications Table 5 presents the police levels coefficients from models where we employed alternative specifications. LLEBG coefficients and t-statistics are reported. Additionally, the ‘‘base” model for each row in Table 5 was the regression of the appropriate crime rate on endogenous police levels, those presented in Table 4. First, the large sample may have masked variations in the effects of police levels on crime that could have been attributed to jurisdictional size. In response to this concern, four additional sets of models were estimated with subsamples corresponding to different population sizes. Police levels were not significantly associated with crime rates in cities below 100,000. This finding is not without precedent. For example, Zhao et al. (2002) found associations between COPS grants and crime in larger cities. Next, to address the possibility that police levels do not exert a contemporaneous effect on crime, we lagged the instruments by one period. The results were almost identical to those presented in Table 4. Additional models with no controls, no year dummies, and no controls and year dummies were also estimated. The police levels coefficients retained their significance levels for the most part. Dummy variables for each year were included in the regressions summarized in Tables 4 and 2, as is conventional with two-way fixed effects models. These captured year to year shocks that could have affected all cities simultaneously and thus could have yielded spurious associations between police levels and crime were they not included in the models. The problem is that year dummies cannot adequately capture preexisting trends in either crime rates and/or police levels. If, for example, our instruments, particularly hiring grants, were distributed during a time when police forces were expanding, then any association between them and crime could have also been spurious. Alternatively, if a particular jurisdiction was experiencing a significant decline in crime during the observed period, then year dummies would not have captured the trend. In response to these concerns, models with heterogeneous year effects were also estimated. These effects were calculated by (1) regressing police levels in the pre-grant period on a linear time trend for each unit; (2) doing the same for the aggregate crime rate; (3) organizing the coefficients from each regression into quartiles; and (4) interacting the resulting cells with year dummies, for a total of 192 (4 4 12 = 192) separate year effects. Similar approaches were taken in Evans and Owens (2007) and GAO (2005). These ‘‘growth cells” replaced the year dummies. LLEBG significance levels were not appreciably altered. Models were also estimated with only crime growth cells (4 12 = 48). The crime growth cell results appear first in Table 5, followed by the results from models with the heterogeneous year effects. The final set of results from Table 5 controlled for other grant programs, notably those listed as ‘‘other grants” in Table 1 and discussed earlier. This step was taken to address the possibility that such grants were correlated with our instruments and crime, thus possibly leading us to overstate the PL-C relationship. As the coefficients in the last row of Table 5 show, the effect of police levels on crime remained more or less intact. 25 Numerical equality also requires that the estimate of the variance of e from the efficient IV regression is used in the estimates of the variances of both IV estimators.
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Table 5 Alternative specifications.
Pop. 0–25,000 Pop. 25,001–50,000 Pop. 50,001–100,000 Pop. 100,000 & over Lagged instruments No controls No year dummies No controls/year dummies Crime growth cells Heterogeneous year effects Other fed. grant controls
Homicide
Rape
Robbery
Assault
Burglary
Larceny
MV theft
0.127 (1.07) 0.200 (2.11)* 0.539 (2.63)* 0.779 (3.14)** 0.371 (2.23)* 0.271 (2.86)** 0.361 (3.52)** 0.581 (4.47)** 0.207 (1.99)* 0.310 (2.34)* 0.238 (2.78)**
0.183 (0.41) 0.367 (0.49) 0.829 (0.72) 0.856 (1.47) 1.356 (1.84) 0.154 (0.40) 0.232 (0.76) 0.872 (2.40)* 0.035 (0.10) 0.089 (0.22) 0.032 (0.09)
2.646 (1.95) 8.806 (1.71) 17.344 (1.33) 29.221 (3.03)** 15.083 (2.45)* 7.569 (2.56)* 6.795 (2.96)** 12.102 (3.48)** 5.022 (2.30)* 5.695 (2.44)* 5.571 (2.42)*
6.940 (1.45) 13.298 (1.53) 15.271 (1.73) 13.907 (1.10) 28.177 (4.83)** 8.964 (2.85)** 10.849 (3.63)** 21.639 (5.03)** 5.280 (1.56) 5.436 (1.13) 7.297 (2.50)*
16.543 (2.03)* 26.303 (1.69) 64.721 (2.20)* 49.889 (3.94)** 51.833 (2.87)** 23.742 (2.78)** 29.167 (3.68)** 81.215 (5.51)** 14.142 (2.40)* 9.329 (1.34) 18.275 (2.52)*
27.886 (1.63) 41.124 (0.82) 7.463 (0.30) 18.606 (0.74) 60.231 (1.61) 15.586 (0.90) 19.476 (1.31) 112.377 (3.81)** 9.539 (0.71) 12.365 (0.82) 8.101 (0.50)
0.086 (0.03) 9.371 (0.61) 23.215 (0.97) 62.751 (2.34)* 14.271 (1.15) 7.781 (1.01) 7.025 (1.07) 25.200 (2.54)* 2.066 (0.32) 2.624 (0.40) 4.844 (0.70)
Police levels coefficients reported. Robust t-statistics in parentheses. All test statistics are robust to heteroskedasticity and clustering. Police levels instrumented with hiring grants and other grants. Crime rates per 100,000. Police levels and instruments per 10,000. Baseline model same as Table 4. * p < 0.10. ** p < 0.05.
5.4. Local average treatment effects It would have been naïve for us to assume that the treatment we evaluated (police levels) was homogeneous across units. Under the more realistic assumption of treatment heterogeneity, the PL-C effect we estimated was the average treatment effect among units that varied their treatment status in response to the instruments. In other words, police levels were not distributed randomly but rather were affected by innumerable considerations—many of which were not captured in the instruments. Imbens and Angrist (1994) call this the local average treatment effect (LATE). Most of the LATE literature (e.g., Angrist and Imbens, 1995; Heckman and Vytlacil, 2005; Heckman et al., 2006) has employed individual-level data (e.g., Kane and Rouse, 1995). For example, in a model of labor market returns, Card (1995) instrumented community college attendance with the student’s proximity to a college. A problem is that, like police levels, proximity to a college is not randomly distributed. The LATE approach has yet to be applied in criminological studies of localities (or to macro-level units in general, even outside of criminology). It is still fashionable to assume parameter homogeneity in instrumental variables estimation, particularly with countries as the units of analysis (e.g., Acemoglu et al., 2001). Nevertheless, we feel time is right to think about local average treatment effects in the type of estimation reported here. As mentioned, a possible problem with our choice of instruments is that police levels may be altered by a number of factors. Examples include public referendum, budget cuts, and mayoral turnover. Our instruments failed to capture these, hence our findings were local to federal grants. While this limitation was insurmountable, we submit that it is a telling limitation nevertheless, as it suggests federal support for local law enforcement is a policy worth pursuing. Such support has been on the decline in recent years, yet this and other recent studies (GAO, 2005; Worrall, 2008a, 2008b) suggest it should perhaps be increased. What’s more, since our instruments captured very different categories of federal support (hiring grants and non-hiring grants), we were able to show that this strengthened the instrument validity test we employed. It also appears there is no single variety of federal support that should be pursued over the other.
6. Summary and conclusion The PL-C relationship has been explored at great length, but the jury is still out on the direction and nature of the relationship. Nowhere is this more apparent than in the literature concerned with a simultaneous association between police levels and crime. The problem is that police may reduce crime, but crime may increase police.26 Numerous studies have thus sought out, selected, and defended the use of creative instruments for police levels. Nearly all these studies have ignored instrument validity, and none have formally tested for it. Instrument validity testing is critical because without doing so, the most a 26
There are also other problems of measurement error and omitted variable bias, to name two.
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researcher can do is use theory to deflect critics’ arguments that the instruments selected should appear in the main equation (or equations) of interest. Most recently, federal policing grant amounts have been selected as instruments. Most of these, especially hiring grants, appear to be associated with police levels and not directly related to crime. Evans and Owens (2007) instrumented police levels with the sum of two hiring grants, those from the Universal Hiring and Distressed Neighborhoods program. The result was a just-identified model of the PL-C relationship. We sought to improve this approach by estimating over-identified models that permitted us to check both instrument relevance and validity. The one issue we have not given much attention to thus far is whether there is a clear PL-C relationship. 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