Abstract
There is no scholarly consensus as to the proper functional form of the crime equation, particularly with regard to one critical, explanatory variable—prison population. The critical questions are whether crime and prison rates must be differenced, whether they are cointegrated, and whether they are simultaneously determined—whether crime and prison cause one another. To determine the proper specification, different researchers have applied unit-root, cointegration, and Granger tests to very similar data sets and obtained very different results. This has led to very different specifications and predictably different implications for public policy. These differences are more likely to be due to the methods used, rather than to real differences among the data sets. When the best available methods are used to identify the proper specification for a panel of U.S. states, results are fairly clear. Crime rates and prison populations are close to unit-root; crime and prison are not cointegrated; crime clearly affects subsequent prison populations. Thus the best specification of the crime equation must rely on differenced data and instrumental variables. Alternative specifications run a substantial risk of spurious results.
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Notes
Several studies reported results of several specifications. Table 1 reports results of that specification that produced the highest adjusted R 2 or lowest Bayesian information criterion. For the studies that did not use a log-log specification (e.g., Smith 2004), Table 1 shows the elasticity at average values of violent crime and prison. The figure reported for Marvell and Moody (2001) is the elasticity of homicide rate with regard to prison population; the figure reported for Liedka et al. (2006) is the elasticity of index crime rate with regard to prison population.
Three parts are missing. Reliable crime data were not available from New York until 1965; Alaska did not report prison statistics to the National Prisoner Statistics program until 1971; in 2001, the U.S. Bureau of Prisons took over the District of Columbia prison system, merging its prisoners with other federal prisoners. Prison data were missing from four other states (Arkansas and Rhode Island, 1968–1970; Delaware and North Carolina, 1968); but these gaps were filled with the geometric mean of the prison population. Rates were then calculated in the usual way. Thus 2,280 cases are available for prison, and 2,290 cases for violent and property crime.
An argument often used for restricting the crime series to 1971 and later is that the FBI’s definition of larceny changed to include thefts for which the dollar value was $50 or less. This increased the larceny rate considerably in some states. On the other hand, the point at which this change took place is known, and the increase can be dealt with effectively by including a dummy variable for the year of the change in all calculations. A 30% increase in the length of the series is well worth the additional trouble. In addition, a longer time-series is useful for two technical reasons. First, the number of states, N, is approximately the same as the number of years, T. Thus this data set better matches the assumptions of several statistical tests, which rely on asymptotic results based on the assumption that N and T both approach infinity at about the same rate. Second, particularly when N is small, estimates of serial correlation are biased toward zero (Kiviet 1995; Nickell 1981). The bias is caused by the fact that each y t−1 is dependent on a weighted average of previous values of the error term, which in a small sample will not generally sum to zero (Hurwicz 1950; Maeshiro 2000). Monte Carlo simulations (Judson and Owen 1999) show that the biases are relatively small for T > 30 (the law of large numbers takes care of the problem); the biases are also small when the coefficients of the lagged dependent variables are less than 0.2 (the weights on which y t−1 depends are themselves close to zero). Thus a longer time-series will both improve precision and reduce bias. The primary argument against a long time series is that the data-generating process (for example, the extent of serial correlation or the existence of cointegration) is more likely to shift over a longer time period. The simplest way to account for such changes over time is to model them explicitly.
If the underlying statistic is close to normal-distributed, then (N − 1)(S/σ)2 will be χ2-distributed with N −1 degrees of freedom (Snedecor and Cochrane 1980), where N is the number of cross-sectional units (here, states), S is the standard deviation of test statistics across states, and σ is the expected standard deviation if the null hypothesis were correct (and thus all states were identical).
For each variable y, the estimate shown is r(y t , y t−1). Consistent with prevailing practice, all variables are logged here, and in all ensuing analyses, to stabilize the variance over time and across states. Here and throughout the analysis, very similar results are obtained for unlogged variables.
Even statistically significant differences are not policy relevant for our purposes. For example, the range of coefficients on the lagged dependent variable for property is .93 to .97—hardly a substantively important difference. Note, incidentally, that each of the 11-year averages is less than the average serial correlation over the entire time series, as one would expect if short time series provide biased results.
A third approach is more direct, and draws on the emerging literature on long memory processes and fractional integration. Some series do not appear to be stationary in levels, but do not appear to be unit root, either. In these cases, it may be appropriate to “fractionally difference” the series, such that α (X t − X t−1)δ = u t , where δ can be any real number between 0 and 1. If δ = 0, no differencing is required; if 0 < δ < .5, the series exhibits “long memory” (the effect of the u t diminishes very slowly over time), but the series itself is stationary; if δ > .5, the series is no longer stationary and is liable to produce spurious results in a regression, even if we account for autocorrelation in the usual way. Because the fractional differencing equation leads to an infinite series in the left-hand side of the equation, this approach is inconvenient and remains on the frontier of econometrics (see Baillie 1996 for a review). Nevertheless, it is possible to estimate the value of δ and its standard error (Geweke and Porter-Hudak 1988; Hassler 1993); if δ > .5, and particularly if δ≈ 1.0, we can be sure that some action (perhaps fractional differencing, perhaps simple first differencing) is needed to avoid spurious results. Unfortunately, standard errors for δ are very large when the time-series is short; if the Geweke and Porter-Hudak method is used when t = 46, it is not difficult to show that the standard error is approximately 0.39—obviously too large to produce usable estimates. For what it’s worth, the mean values of δ across states were close to one for prison (mean δ = 0.962), violent (mean δ = 0.849), and property (mean δ = 1.066), suggesting that the basic conclusion—these variables are close to unit-root—is justified, on average at least.
Other unit-root tests are available, and there is some evidence that they are more powerful under some circumstances (Campbell and Perron 1991; Schwert 1989). Nevertheless, in this case at least, the statistic chosen has no appreciable effect on the results. Phillips–Perron tests and FGLS tests produced very similar results for each combination of state and variable, and led to identical conclusions. Because it is the standard test, appears to be robust in a wide variety of circumstances, and can easily be adjusted to account for cross-sectional dependence, only CADF test results are reported in the text.
Cross-sectional dependence is substantial for these data. All of the crime studies examined in Table 1 accounted for it in the same way, by controlling for year fixed effects in the specification. It is not difficult to show that this is more or less equal to including the national average of the dependent variable in the specification (it is exactly the same if cases are weighted by state population). Year fixed effects were always (collectively) statistically significant, and including them typically increases R 2 by more than adding any other variable. Perhaps more to the point, if cross-sectional dependence is not accounted for in the unit-root tests, test results across states have less variability than expected, if the unit-root hypothesis were correct and the only deviations were due to sampling errors.
This is the usual explanation of the KPSS test. A more complete explanation is that it decomposes the time series into a deterministic time trend, a stationary error term, and a random walk component (the cause of any nonstationarity). KPSS then tests the variance of the random walk component against a null hypothesis of zero. Effectively, then, KPSS assumes that ρ = 0.
A variety of other tests have been suggested, including a χ2 test of the state-by-state significance levels (Maddala and Wu 1989) and a Z test of the log of significance levels (Choi 2001). These tests are not reported here because state-by-state significance levels were based on Normal approximations to the KPSS and CADF distributions, and are thus not exact. When these tests are applied to approximate significance levels, panel-wide significance levels are very similar to those shown below, and they lead to identical conclusions.
This procedure was originally recommended by Kwiatkowski et al. (1992). It has been modified slightly to account for recent findings as to the lack of power of the KPSS test in the face of fractional integration (that is, non-zero δ) and large (but non-unit) values of ρ (Hassler and Wolters 1995; Muller 2005).
It may also arise if the series is fractionally integrated with .5 < δ < 1.
If the series is in fact fractionally integrated, then there is a substantial risk of spurious regression results, even if we account for autocorrelation in the residuals. The reason is that the autoregressive function in a long memory model decays much more slowly than in the usual autoregressive, “short memory” model. Thus estimated generalized least squares or Newey–West estimators of the covariance matrix will underadjust, and substantial autocorrelation will remain in the residuals. To some extent this can be dealt with by adjusting for a longer lag, but the usual procedures for lag selection (e.g., Andrews 1991) will systematically understate the number of lags required.
That is, if we were to rely on a single specification for all states, it must rely on differenced variables. An argument can be made for using two specifications, differencing the majority of states that appear to be unit-root and using FGLS or computing Newey–West standard errors for the rest. Since the two procedures produce unbiased estimates of the same coefficients, this would allow for more efficient estimation in the undifferenced states without changing the results. Given that all states appear to be at least near-integrated in all three variables, however, the efficiency gains would be minor, and are probably not worth the substantial logistical difficulties.
It may also be that violent and property crime rates are cointegrated with one another. Recall that prison was chosen as a normalizing variable on substantive, not statistical grounds. If our only interest were in finding some evidence of a cointegrating relationship of some kind, it would make more sense to normalize on violent or property, instead. Because the stationarity characteristics of the residuals of the cointegrating equation are liable to mirror those of the dependent variable, choosing a dependent variable that is closer to stationarity maximizes the chances of finding evidence of cointegration. When the procedures used in the text were duplicated with violent as the normalizing variable, there was clear evidence of a (usually positive) cointegrating relationship between violent and property in some states, and residuals were stationary in five states. Thus there appears to be a long-run equilibrium relationship between violent and property crime rates, in a few states, at least.
Some argue for including control variables in the Granger equations to further reduce the risk of omitted variable bias. In our context, Useem et al. (2001, pp. 7–8), have disputed Marvell and Moody’s (1994) Granger test results on these grounds. If the nature and functional form of the control variables were known for both the crime and prison equations, this would no doubt be good advice. However, if we are unsure as to which control variables should be included and how, adding any controls lends a false sense of conclusiveness to what is essentially a quick-and-dirty diagnostic device. For this data set, there is a more fundamental problem: The best, single predictor of state crime rates, unemployment rates, were not collected at the state level by the U.S. Department of Labor until the early 1970s. Rather than risk substantial omitted variable bias, it makes more sense to conduct the Granger test in the usual way and caveat the findings appropriately.
This follows from the finding that, in short time-series, the coefficient on the lagged dependent variable is biased toward zero. See footnote 3, above, for references.
It may not. Both the FGLS and Newey–West procedures require estimates of the serial correlation in the residuals, and if this estimate is in error it may lead to misleading standard errors. The usual advice is to ignore serial correlation unless |ρ| > .3 or so (Kennedy 2004, p. 145).
In the case of the Liedka et al. (2006) study, the problem may have been exacerbated by the use of total crime rates (that is, violent plus property crime rates) as the dependent variable. For the 1960–2004 sample, the correlation between ΔC t and ΔC t−1 is .362, slightly larger than the correlations for violent and property crimes taken separately. This correlation is positive in 49 of 51 states, and greater than .30 in 36 states. Results are almost identical for the period covered by the Liedka et al. study.
In a county-level data set, Spelman (2005) used local criminal justice system resources, local jail capacity, twice-lagged arrest rates, and conservative voting patterns as instruments for jail and prison populations. These instruments were effective predictors of prison (F = 72.8, ΔR 2 = .192) but not of crime (for violent crime, F = 0.37, ΔR 2 = .0016; for property crime, F = 0.93, ΔR 2 = .0035). Whether these instruments behave similarly in a state panel is an open question, but it would be premature to state that no effective instruments are available.
A third possibility was raised by Western (2006): Even if we cannot come up with an unbiased estimate of the effect of crime rates on prison populations, we may be able to use available information to bound that relationship. Western suggests an upper bound of +.15, and uses it to estimate a lower bound (that is, the most negative possible estimate) for the effect of prison on crime. Although this is an interesting proposal, it would be difficult to estimate a valid bound on either relationship without using an instrument of some kind.
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Spelman, W. Specifying the Relationship Between Crime and Prisons. J Quant Criminol 24, 149–178 (2008). https://doi.org/10.1007/s10940-008-9042-x
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DOI: https://doi.org/10.1007/s10940-008-9042-x