Estimate the relationship between race and arrest within co-offending partnerships using a quasi-experimental framework. More specifically, this study argues that when two offenders commit an offense together (i.e., co-offend), the characteristics of the offense and victim are the same and can be removed as possible confounding variables. In this way, co-offenders can serve as counterfactual observations to one another, allowing for quasi-experimental analysis of the effects of race on arrest likelihood.
The current study restructures data from the National Incident-Based Reporting System (NIBRS) into a multi-level format wherein level-1 information on offender demographics and arrest are nested within a level-2 file containing information on co-offending partnerships, offense characteristics, and victim characteristics. By restricting the data to co-offending partnerships and examining within-partnership differences in arrest, the analysis examines racial differences in arrest given that two offenders commit the same offense together against the exact same victim.
While a traditional logistic regression approach suggests that black offenders are less likely than white offenders to be arrested (OR = 0.749), the quasi-experimental analysis examining within-partnership differences suggests the opposite: black offenders are more likely than their white co-offending partners to be arrested for an offense (OR = 1.031).
These results have two implications. First, traditional regression analyses of the relationship between race and arrest may be subject to significant selection and omitted variable bias. Second, there is potential racial disparity in co-offender arrest: black co-offenders are more likely than their white partners to be arrested for the same violent offense.
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This research limits the sample to violent offenses for two reasons. First, violent and property offenses are theoretically different in function and form from each other, and a complete examination of all offenses in the NIBRS data is beyond the scope of a single paper. Therefore, we chose to limit the sample to the most serious offenses. Second, violent offenses are inherently interpersonal, while not all property offenses involve contact between the victim and offender. This means that there are much higher rates of offender demographic missing data for property offenses, compared to violent offenses, and these characteristics were important matching criteria in the facilitation of the analysis conducted in this research.
Because missing data is not allowable at level 2 for HLM analyses, incidents containing missing data at this level are removed from the sample (roughly 13% of incidents).
Only a very small number of offender and arrestee segments could not be matched (< .01%) because the demographic information in the offender file did not match the demographic information in the arrestee file in any way (i.e., a female was arrested when the offenders were reported as all male). These cases were removed from the final sample.
Research conducted by Addington (2015) supports the assumption that these cases do, in fact, represent the same offender. She noted that, in the early years of NIBRS data collection, there was an informal FBI practice of encouraging agencies to “overwrite and correct offender information using arrestee demographics” (p. 162). This practice is no longer encouraged, but many agencies continue the practice. These changes are not flagged in any identifiable way, and cannot be examined in the current analysis.
The current analysis elected not to also match offenders on age. While capitalizing on age would have greatly increased the number of offenders that could have been included in the analysis, there is significant variation in the amount of time between the offense data and arrest date for each incident, allowing offender age to change significantly between the offender and arrestee file. It is also markedly more difficult for victim(s)/observer(s) to accurately estimate age based on observation alone. As a result, it was determined that including age as a matching variable could significantly increase the potential for error in matching the offender and arrestee segments.
We did not perform the analysis at the individual offender level because to do so would violate the regression assumption of independence, or uncorrelated error terms, given that co-offenders are likely more similar in their outcomes than those who do not offend together.
It is worth noting that, because the sample includes all mixed race or mixed gender dyads, regardless of arrest outcome, resulting estimates might best be considered conservative. For most of these co-offending partnerships, none of the offenders are arrested (about 61% of incidents), or both of the offenders are arrested (about 27% of incidents). The estimates would likely be substantially larger if the sample was limited to only those cases wherein there is a difference in arrest outcomes (about 11% of incidents), but because that sample would not realistically represent the co-offending partnerships in the sample, and further limit the generalizability of these results, we chose to include all incidents involving mixed gender or mixed race partnerships, regardless of differences in arrest outcomes.
Sample size in multilevel modeling is determined by the total number of units at each level, so a low average number of level-one units per level-two grouping has no problematic influence on power for testing regression coefficients (Snijders 2005). Therefore, the examination of two offenders per higher-level unit is not problematic.
The NIBRS data include the use of “body parts” as a possible personal weapon. These offenses were coded as not involving a weapon because it can be assumed that all offenders have these potential weapons, and coding them as weapons would skew the data positively regarding the prevalence of weapon use (see Cunningham and Vandiver 2018 for a similar coding scheme).
One might argue that, in order to estimate the relationship between race and arrest, one must jointly consider the level-2 and level-1 race estimate. But, according to the counterfactual framework outlined here, the primary estimate of interest is actually the level-1 race estimate, controlling for the level-2 race effect. The level-2 race estimate captures incident-level racial differences in arrest likelihood, which I argue are subject to potential omitted variable bias due to incident differences. The level-1 estimate, on the other hand, estimates differences within-partnerships, reducing this potential bias. As such, the level-1 estimate is best considered the within-incident race difference, the level-2 estimate is best considered a control measure for the impact of co-offending partner race, and the two estimates are best not considered jointly.
While the point estimate for the within-partnership difference in race is relatively small, it is worth noting that this is in part a product of the research design. That is, the intention of analyzing within-partnership differences was to reduce the portion of the observed estimate that is spurious by also accounting for unmeasured offense and victim characteristics. As such, it should be expected that the point estimates would be smaller because, theoretically, they are a closer approximation of the true effect.
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The authors wish to thank Barry Ruback, Wayne Osgood, Holly Nguyen, Jeremy Staff, and Scott Gest for comments on this and earlier versions of this research.
This research was completed in part with funding from the Bureau of Justice Statistics (2015-R2-CX-K032). The views presented represent those of the author and do not necessarily represent those of the Bureau of Justice Statistics.
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Lantz, B., Wenger, M.R. The co-offender as counterfactual: a quasi-experimental within-partnership approach to the examination of the relationship between race and arrest. J Exp Criminol 16, 183–206 (2020). https://doi.org/10.1007/s11292-019-09362-5