Abstract
Objective
Previous aggregate analyses of the effect of police on crime show that increases in police staffing are especially effective at preventing homicide. This conflicts with evidence that suggests standard police methods should be more effective at preventing robbery, auto theft, and other property crimes. My objective is to reconcile the two.
Methods
Regression of crime rates on uniformed police staffing and other economic and demographic covariates, for a panel of 59 US cities for the period 1970–2013.
Results
Lagged crime rates are strong and statistically significant predictors of both policing staffing and crime rates, particularly homicide. When lags are included in the specification, the apparent effect of police on homicide drops by more than 70 %; there is little change in the effect of police on other crimes. Findings are robust with respect to specification and method.
Conclusions
Previous studies omitted lags and overstated the effectiveness of police on homicide. Because murder accounts for almost 40 % of all costs of crime in US cities, it is no longer clear whether increasing police force size is a cost-effective way to cut crime. Improving police tactics is more likely to work and less expensive.
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Notes
Not all did so. Eck and Maguire (2000) identify 14 studies conducted between 1971 and 1996 that relied on IVs to deal with simultaneity, including Levitt’s (1997) original study, since super seded by McCrary’s (2002) reanalysis. Although the other 13 studies were a substantial methodological advance over other studies of the time, none would be regarded as persuasive today: All relied on cross-sectional data; all used instruments (such as property tax revenues and average income) that may be directly correlated with crime rates; none conducted overidentification tests to demonstrate that the instruments were not so correlated.
At a presentation to the National Institute of Justice, Sherman (2010) summarized this line of thinking in a PowerPoint slide: “less prison + more policing = less crime.” Sherman’s point was that both prisons and police should be focused on high-risk people and places, and he in fact stated that “Just adding police is not predicted to cause less crime or harm” (slide 44). Unfortunately, it’s likely that more people read the title slide than listened to the presentation.
Of 6681 homicides reported in 2013 where the relationship between the victim and the offender is known, 2605 (39 %) were committed by the victim’s friends or family members, and 2795 (42 %) were committed by neighbors and acquaintances. Only 1281 (19 %) were committed by strangers. Federal Bureau of Investigation, (2013/2014), Expanded Homicide Data Table 10.
About 57 % of homicides are committed in residences; another 5 % are committed in bars, hotels, offices, and other buildings where police do not typically patrol; another 3 % are committed in fields, woods, and other outside locations where police presence is unlikely. The pattern is similar for nonfatal assaults. In contrast, the vast majority of robbery and property crimes are committed at least partially on the streets, in parks, parking lots, gas stations, or other places where police presence is likely. Federal Bureau of Investigation, (2013/2014), NIBRS data tables.
Clearance rates for robbery and larceny have increased steadily (if only slightly) since the mid-1990s; they have remained stagnant for aggravated assault, burglary, and auto theft, and actually declined substantially for forcible rape. Homicide rates declined from the 1960s until about 1995 (Cronin et al. 2007, at 12), but have remained relatively stable since then. Federal Bureau of Investigation, (2013/2014), Table 25.
Those arrested for murder are less likely to have prior arrest or conviction records than those arrested for nonfatal assaults, robbery, and property crimes, at least in large urban counties. Those arrested for murder are also less likely to have multiple arrests than those arrested for property crimes and no more likely to have multiple arrests than those arrested for nonfatal assaults or robbery; they are less likely to have multiple convictions than those arrested for nonfatal assaults or property crimes, and no more likely to have multiple convictions than those arrested for robbery (Reaves 2013, Tables 7, 8, and 9).
This estimate assumes that crimes are reported to police at the rates estimated by the National Crime Victimization Survey (Truman and Langton 2014), and that costs accrue to victims and society as estimated by McCollister et al. (2010). Although imperfect, this is a commonly used approach (e.g., Aos and Drake 2014; Heaton 2010; Levitt 1997).
The estimates are based on Levitt’s (1998) Table II (based on a cross-section of National Crime Victimization Survey results for 26 cities) and Table III, col (4) (a time-series of nationwide NCVS data from 1973 to 1991). Table II included one result for each of seven crime types; Table III included a single, average result. A third analysis was based on the same data set as Levitt’s (1997) analysis of the effects of police on crime, and appears to suffer from the case-weighting error identified by McCrary (2002). For eight usable estimates, Cochrane’s Q = 12.600, p(χ2) = .082. Thus we cannot reject the hypothesis of homogeneity among crime types.
Others have. See Chalfin and McCrary (2012).
An early version of this data set was also used by Marvell and Moody (1996) in a study that did not use instruments.
Levitt eliminated five cities from his original data set because they did not directly elect a mayor. This restriction ensured applicability of a potential instrumental variable to predict sworn officer rates and identify the crime equation. The data set used includes corrections by McCrary (2002) which strengthen the relationship between Levitt’s instruments and police staffing. Thirteen cities did not report crime levels for 1 year (usually 1988); crime levels were interpolated for these years using a geometric mean. Columbus failed to report crime levels for 2012 and 2013; these cases were eliminated from the analysis. One city (Tucson) reported levels of larceny for the period 2004–2012 that were not accepted by the FBI; another city (Toledo) did not report larceny levels at all for 2009–2013. These cities were omitted from the theft equations, but remain in the auto theft equations. The FBI also refused to accept Chicago’s forcible rape reports for 1986–2013; rape rates for 1970–2013 were not counted in the nonfatal assaults total for Chicago. Six cities did not report police staffing levels for one year, and two failed to report for multiple years (2 years in one case, three in the other). Sworn staffing levels were interpolated for these cases, again using a geometric mean. Excluding the cases with interpolated values has no appreciable effect on results.
Some previous analysts weighted cases by city population, on the theory that residual variance would be systematically lower for the largest cities. This is appropriate when crime rates are uncorrelated with population and the predictive model is sufficiently complete that Poisson errors make up a large share of the residual variance. If the model is incomplete or improperly specified, and particularly if crimes are committed often enough that random variation is a relatively minor issue, population may have little correlation with residual variance. On the other hand, population weights reduce the external validity of the results by focusing undue attention on a few, large cities. In this sample, for example, New York would receive 33 times the weight of Akron, Ohio. There is only one New York, but dozens of cities about the size of Akron that are not in the sample.
A fourth variable, state sales tax rates, was found to be an effective instrument in a study conducted at the state level (Lin 2009). It was not an effective instrument in this study. Although positively associated with police, t was <1.0 in all specifications.
Preliminary analysis showed that the first-stage coefficients on mayor and governor were almost identical, but that the F value of the instruments as a whole was improved by combining the two.
The annual survey from which the firefighter data were taken may be prone to random measurement errors. Chalfin and McCrary (2012, Table 4) compared the effects on crime of two measures of police staffing: the FBI’s Uniform Crime Reports and the Census Bureau’s Annual Survey of Governments. In all 20 cases, coefficients on the ASG measures were closer to zero than those on the UCR measures, a pattern consistent with measurement error. In the ASG firefighter data, I found 24 cases (1 % of the total of 2419) where an otherwise-steady series was broken by one year where the reported level was 20 % or more higher or lower than adjacent levels. Replacing these anomalies with a geometric mean substantially increased the correlation between fire and police without increasing the overidentification statistic. The smoothed version of fire is used in all analyses described below.
This is a conservative assumption. If crimes are actually committed according to a contagious distribution, such as a negative binomial, random fluctuations will be larger. Barnett (1981), relying on evidence of multiple-victim murders, finds that σ2 = 1.04λ. Thus the error attributed in Table IV to random commission is slightly understated, even for the case of a Poisson process.
For λ > 6 or so, we can use a Taylor series expansion of ln(λ − x − λ) to calculate the variance of ln(x it ) = σ 2 x /λ2, which equals 1/λ for a Poisson process. If E(y) = λp, the expected number of crimes reported, the commission variance can be expressed as p/E(y). Similarly, the reporting variance of ln(y it ) = σ 2 y /(λp)2 = λp(1 − p)/(λp)2 = (1 − p)/E(y) and the variance due to both sources is simply p/E(y) + (1 − p)/E(y) = 1/E(y). The variance of the difference of two independent and identically distributed random variables is the sum of the variances, here 2/E(y); the sum of squares due to random processes is approximately \(2\Sigma _{it} 1/E(y_{it} ).\)
Adding covariates to the y (crime) equations has no material effect on the results. NCVS data begin in 1973; values of p for 1970–1972 were extrapolated using a log-linear trend line. Since the sum of the two sources of random variation does not include p, improved estimates of p would only affect the relative importance of random commission and reporting processes, not the total.
Due to the small sample sizes, it is difficult to prove this assertion. Panel unit-root and stationarity tests are not especially helpful; for all crime types, we can be virtually certain that some cities are not stationary; for all violent crime types, we can be virtually certain that some are not unit-root. When unit-root and stationarity tests are conducted individually on ln(murder) for the 54 cities without structural breaks, 32 cities are clearly nonstationary (Dickey–Fuller GLS test not significant but KPSS stationarity test is significant), 8 are clearly not unit-root (Dickey–Fuller test significant, KPSS test not significant), and 14 are uncertain (neither test significant or both tests significant). Other crime types and police are clearer: 39–52 cities are clearly nonstationary, 0–3 cities are clearly not unit-root, the rest are uncertain. In only one city (Minneapolis) are two variables stationary; the other variables appear to be unit-root there. The best characterization of the sample as a whole is that all these variables are nearly unit-root.
Consider two variables, x and y, defined as x t = r x x t–1 + (1 − r) Φ where Φ is the standard Normal distribution and similarly for y t . Set r x = +.833 (like police) and r y = +.816 (like murder) and estimate 10,000 sets of T = 40 cases each. In the absence of spurious correlation, 500 of the 10,000 cases would be correlated at |r| > .299, with p(r) ≤ .05. Instead, 3660 sets had correlations this large or larger. That is, we would obtain 7.2–7.4 times as many significant correlations as we would have in the absence of serial correlation among the two variables. The problem is, of course, worse for the other crime types because their serial correlations are larger. For r y = +.887 (like nonfatal), 4066 sets appear to be significantly correlated; for r y = +.911 (like auto), 4212 sets appear to be significant correlated.
Similarly, a Poisson regression which accounts for random variation in the dependent variable but not in the lagged dependent variables produced a lag sum of .894 with standard error .004. Another test is less robust, but simpler. When murder rates are aggregated over the 59 cities in the sample (thus reducing the effect of measurement errors in any given city), murder rose and fell over time with the other crimes. The average correlation between aggregate murder rates and aggregate rates for other crimes over the 1970–2013 time-series was .75; only robbery was more closely correlated with rates of other crimes (r = .80). The highest inter-crime correlation was between murder and robbery rates, at r = .94. Similar results were obtained for aggregate annual percentage changes. Murder behaved over time just like the other crimes did.
Any time-series with a single significant autocorrelation at lag 1 can be represented by either a moving average model with one parameter (that is, MA1) or by an autoregressive model with several parameters. If we were only trying to obtain i.i.d. residuals, the MA1 model would of course be more parsimonious.
Suppose the murder rate increases by a standard deviation in year t. Then the Granger analysis shows that, all else equal, police rates will increase by .092 standard deviations in year t + 1, by .082 standard deviations in year t + 2, and so on, for a total change of Σ k=5 γ k = +.318 standard deviations. In general, the sum of the lags is the appropriate measure of the eventual effect of a 1-year change in either crime or police.
There are at least three other justifications for omitting lags. First, independent and identically distributed residuals are no longer needed to obtain consistent standard errors. Nonspherical residuals bias standard errors, but most of these studies were conducted since heteroskedasticity- and autocorrelation-consistent (HAC) standard errors became readily available. Second, lagged dependent variables imply that all independent variables have dynamic effects on crime (e.g., the well-known Koyck model). Thus each coefficient β shows the short-run effect only; the long-run equilibrium effect is β/(1 − Σ k φ k ), where φ k is the coefficient on the kth lagged dependent variable. Although dynamic effects can be easily explained, there is no theoretical reason to expect them in advance. Finally, the coefficients on the lagged dependent variables themselves will be biased in panel data, as will be the coefficients on any covariates that are correlated with the lagged dependent variables (Nickell 1981). For panels of this size, however, the bias on the lag coefficients is small (about 6 % of the true value), and the bias on associated covariates will be smaller still (2–3 % of true value; Judson and Owen 1999). As shown below, these biases are small compared to the biases associated with omitting the lags.
On this issue, at least, we have some direct evidence. Evans and Owens (2007, p 190) found that high-crime cities were more likely to obtain COPS grants than low-crime cities.
Clustering on msa also accounts for any spatial correlation among cities in the same metropolitan area. Standard errors clustered on city and state was in all cases almost identical to those shown, suggesting that spatial correlation was not an important issue for these data.
Hausman tests were conducted of the differences between the OLS and 2SLS equations for all crime types. The test covered all lagged crime rates and all covariates except for police. The largest test result, obtained for the nonfatal equations, was \(\upchi_{15}^{2}\) = 2.856, p(χ2) > .999. Diagnostic tests also returned similar results with the exception of heteroskedasticity, which was statistically significant in the theft OLS equation (F = 1.549, p = .044). Except for the coefficient on police, the OLS and 2SLS equations are functionally identical.
The rule of thumb that F > 10 only applies for just-identified equations with a single instrument. These instruments also meet the Stock-Yogo (2005) standards for equations with three instruments: Bias is <5 % of the OLS bias; size for a p < .05 test is <.10. In analysis of a data set very similar to this one, Kovandzic, et al. (2015) found mayor, governor, and fire—the original instruments used by Levitt (1997, 2002)—to be inadequate, with F ≈ 3 or 4. I obtained similar results, which is why mayor and governor have been combined and fire has been smoothed before differencing. This study also spans a longer period and includes more covariates, some of which are excellent predictors of crime.
Although the sum of the lag coefficients is large, the murder equations (and all equations) are stationary. The test for stationarity is to estimate the roots of the characteristic equation, 1 − Σφ t x t = 0 where φ t is the coefficient on the tth lag of the dependent variable. If all of the roots lie outside the unit circle – that is, for all real roots z, |z| > 1 and for all complex roots a + bi, a 2 + b 2 > 1—then the equation is stationary. The real root of the murder equation is −1.781 and all complex roots likewise lie outside the unit circle. Similar results were obtained for all other crime types. More generally, large negative distributed lags produce a sawtooth pattern, strongly mean-reverting but highly negatively serially correlated. If the lag coefficients are large enough, the series continues to revert to the mean but individual cases become further from zero in an alternating positive/negative pattern—the sawtooth gets bigger and bigger. These coefficients are nowhere near that large.
The F values differ among equations because each included a different set of lagged dependent variables.
The median regression minimizes the sum of absolute deviations, not squared deviations, and is robust in the face of outliers (Cameron and Travedi 2005). Per Amemiya (1982), median regression results were obtained for each second-stage equation using OLS first-stage predictions. Standard errors were bootstrapped. M-estimator regressions (not shown) are also robust with regard to outliers and produced very similar results to the median regressions. The S-estimator relies on a robust covariance matrix developed by Freue et al. (2013); efficiency was improved by trimming outliers and high-leverage cases (Desbordes and Verardi 2012). MM-estimators are robust to both outliers and leverage (Yohai 1987). This MM-estimator was obtained through an iterative process. A standard MM-estimator was developed to predict police, then predictions of this estimator were used in a second-stage MM-estimated regression. Case weights from the second stage were then used to produce an updated first stage through weighted least-squares, predictions of which were used to update MM-weights. The process continued until further iterations had no effect on the first six decimal places of the second-stage coefficients. Convergence typically required three to eight iterations.
Comparison of βs across crime types is appropriate if the large coefficients on lagged murder are due to random measurement errors in murder, not differences in dynamic effects across crime types. This is consistent with the results shown on Table 4. Estimating such differences, or even verifying the existence of any dynamic effects, is beyond the scope of this paper.
A negative binomial regression on murder rates on fixed city and year effects shows an overdispersion parameter of α = .066. Thus the standard deviation of annual fluctuations would be \(\sqrt {(M +\upalpha\,M^{2} )} ,\) where M is the average number of murders committed yearly.
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Spelman, W. The Murder Mystery: Police Effectiveness and Homicide. J Quant Criminol 33, 859–886 (2017). https://doi.org/10.1007/s10940-016-9315-8
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DOI: https://doi.org/10.1007/s10940-016-9315-8