Previous research has neglected to consider whether trends in immigration are related to changes in the nature of homicide. This is important because there is considerable variability in the temporal trends of homicide subtypes disaggregated by circumstance. In the current study, we address this issue by investigating whether within-city changes in immigration are related to temporal variations in rates of overall and circumstance-specific homicide for a sample of large US cities during the period between 1980 and 2010.
Fixed-effects negative binomial and two-stage least squares (2SLS) instrumental variable regression models are used to analyze data from 156 large US cities observed during the 1980–2010 period.
Findings from the analyses suggest that temporal change in overall homicide and drug homicide rates are significantly related to changes in immigration. Specifically, increases in immigration are associated with declining rates for each of the preceding outcome measures. Moreover, for several of the homicide types, findings suggest that the effects of changes in immigration vary across places, with the largest negative associations appearing in cities that had relatively high initial (i.e., 1970) immigration levels.
There is support for the thesis that changes in immigration in recent decades are related to changes in rates of lethal violence. However, it appears that the relationship is contingent and varied, not general.
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Because some cities have missing data for one particular time point but not others, the number of valid city-year observations (591) is somewhat less than the number of cities multiplied by the number of time points (i.e., N × T = 156 × 4 = 624).
The 2010 SHR data were the most recently available when our analyses were initially conducted.
Some prior research distinguishes between gang-affiliated and gang-related homicides (e.g., Rosenfeld et al. 1999). While we acknowledge that such a distinction may be relevant, unfortunately, the SHR data do not allow us to make such a distinction.
A measure of linguistic isolation, the percentage of persons who speak English “poorly” or “not at all,” also has appeared in some studies. We considered using this item in the current analysis. However, because the linguistic isolation question for the 2010 American Community Survey differs from that of the preceding Decennial Censuses, we decided against using it.
Partly reflecting the influence of the seminal study by Land, McCall, and Cohen (1990), the inclusion of the percent black in “disadvantage” indices has become common practice. Empirically, this practice is justified by the high correlations that exist between percent black and other indicators of socioeconomic disadvantage in geographic units, which is also the case in our data. However, based on conceptual grounds, some scholars suggest that the percent black should be kept separate from disadvantage index measures. We believe there is some merit to both of these positions, and while the analyses presented herein employ a disadvantage index that includes the percent black, we also estimated models in which percent black is included as a separate predictor. Results from those models are very similar and lead to identical substantive conclusions as those that we present below.
The linear time-trend variable is centered at 1990 (i.e., 1990 = 0).
To be clear, our analysis approach is distinct from studies that examine cross-sectional effects of structural covariates at multiple points in time (e.g., Land et al. 1990) as well as from analyses that pool time cross-sections together and obtain estimates via ordinary least squares or via random-effects models. Each of the preceding approaches produces effects that, to varying degrees, reflect between-unit (i.e., between-city) effects. Our approach removes between-unit variation, focusing only on variation within units over time.
If this assumption holds, the random effects model may be preferred due to greater statistical efficiency. Several tests that compare fixed-effects and random-effects models are available. We use the approach suggested by Allison (2005), which is based on comparing the coefficients associated with the within-unit and between-unit components of the same variables. If the assumptions of the random-effects model are valid, these coefficients should not be significantly different; if they are, the fixed-effects model is preferred. For each model we estimated, the test procedure supported fixed-effects over the random-effects estimator.
Stata software includes a fixed-effects model explicitly designed for panel data analysis, “xtnbreg, fe.” However, Allison and Waterman (2002) showed that the model fails to account for effects of time-stable omitted variables.
A caveat is that coefficients in unconditional negative binomial models may be subject to “incidental parameters” bias (see Allison 2005:95; Allison and Waterman 2002). However, a Monte Carlo simulation study of this issue suggests the dummy variable approach to fixed-effects negative binomial does not result in any substantial bias, even under circumstances that are most likely to produce it (see Allison and Waterman 2002). Nevertheless, according to Allison (2005) one alternative to obtaining fixed-effects estimates is the “hybrid model,” which decomposes independent variables into time-stable and time-varying components and includes both in a random-effects regression model. Because the hybrid approach does not require estimation of dummy variables for each panel unit, it should not be affected by incidental parameters bias (Allison 2012). Thus, as a supplemental analysis, we also estimated our models via the hybrid method. Results obtained are nearly identical to those obtained with the unconditional (dummy variable) estimator.
Because the models include the log of the population as an offset, the coefficient associated with the log of the city population variable is expressed relative to 1.0. Therefore, coefficients greater than one indicate a positive association while those below one indicate a negative association.
Felony and argument homicides contain cases that appear notably heterogeneous (see “Appendix 1”). Therefore, it is worth considering whether the effects of immigration differ across the types that fall within the felony or argument homicide categories. To address this issue, we estimated fixed-effects negative binomial models predicting the major subtypes of felony homicide and the major subtypes of argument homicide. As we report in “Appendix 3”, those results lead to a similar conclusion as the results reported in Table 2; in particular, immigration does not have a statistically discernible relationship with any of the felony or argument homicide subcategories.
We measure the preexisting immigration level by computing the immigration index scores using 1970 Census data. These data for 1970 were obtained as an extract from the National Historical Geographic Information System at the Minnesota Population Data Center (2011). The 1970 immigration index is useful because it captures between-city differences that existed prior to the period of within-city change that is observed in our analysis. A plausible alternative would have been to use the 1980 immigration level rather than the 1970 level. We preferred the former because it can be considered exogenous to the 1980 homicide rate. It is worth noting, however, that generally similar results are obtained if 1980 data are used to measure baseline immigration levels.
In the interest of space limitations and to reduce redundancy, we omitted the marginal effects plots of the interaction effects for each of the homicide subtype models.
For example, at one unit above the 1970 mean, the within-city immigration coefficient in both the felony-homicide and argument-homicide is estimated to be negative and significant.
We computed outlier diagnostics on the regression models presented. No observations were found to be influential outliers based on a combination of both a large studentized residual and a large leverage value. To be more conservative, we re-ran our models after excluding cases that had studentized residuals and leverage values that fell in the top five percent of the distribution. Results from these supplemental models closely mimic those discussed above. Thus, there is little evidence that our results are impacted by influential outlying observations.
The consistency of standard linear regression estimators, such as ordinary least squares (OLS), rely on the assumption that explanatory variables are uncorrelated with the equation error term, an assumption that is violated when explanatory variables are endogenous (Wooldridge 2002).
Although not shown in Table 4, we also estimated three additional instrumental variable models. Each of these models utilized the Arellano-Bond (1991) dynamic panel data estimator and included the lag of the homicide rate along with the immigration measure as endogenous explanatory variables. In the first of these two equations the excluded instruments were all of the available lags (in levels) of the preceding endogenous predictors. In the second equation we also added the aforementioned geographic dummy variables to the excluded instrument set. In the third model, we followed the suggestion of a reviewer and also accounted for potential endogeneity of the drug arrest rate and the police officer rate, using the available lags of each of those variables as instruments. Results from all three Arellano-Bond models are similar to those obtained via the other estimators. Most notably, the effect of immigration on homicide rates is significant and negative.
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The authors thank David Greenberg and Shawn Bushway for input on the modeling strategy.
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Ousey, G.C., Kubrin, C.E. Immigration and the Changing Nature of Homicide in US Cities, 1980–2010. J Quant Criminol 30, 453–483 (2014). https://doi.org/10.1007/s10940-013-9210-5
- Violent crime trends
- Fixed-effects models