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Racial Bias in Criminal Records

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Abstract

Objectives

Government officials use criminal records as proxies for past conduct to decide who and how to investigate, arrest, charge, and punish. But those records may be racially biased measures of individual behavior. This paper develops a theoretical definition of bias in criminal records in terms of measurement error. It then seeks to provide empirical estimates of racial bias in official arrest records for a broad swath of offenses.

Method

I use official arrest and self-reported crime data from the Pathways to Desistance study to estimate Black-to-white and Hispanic-to-white crime ratios conditional on arrest. I also develop a novel, theory-based empirical test of differential reporting across racial and ethnic groups.

Results

Compared to white subjects with the same number of arrests, I estimate that Black subjects committed 53, 30, 23, and 56% fewer property, violent, drug, and DUI offenses, respectively, and that Hispanic subjects committed 19 and 46% fewer drug and DUI offenses. The analysis finds relatively little evidence of differential reporting that would bias my estimates upwards, with the possible exception of drug trafficking offenses.

Conclusion

The results provide evidence that Pathways subjects’ arrest records are racially biased measures of their past criminal behavior, which could bias decisions of criminal justice officials and risk assessment algorithms that are based on arrest records.

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Notes

  1. I use the term “Hispanic” because it is used by the Pathways data.

  2. For a more thorough discussion of the challenges of linking distinct criminal justice records associated with the same person, see Tahamont et al. (2021).

  3. I am grateful to an anonymous reviewer for this point.

  4. As Appendix Fig. 9 shows, the only exception is DUI, in which Black subjects have fewer arrests than white subjects with a similar number of offenses. The estimates for DUI, however, are highly imprecise and statistically insignificant and, as shown in Appendix Tables 2 and 3, these offenses represent a tiny fraction of all arrests.

  5. The NCVS, for example, may undercount white perpetrators if, due to false stereotypes about race and ethnicity, victims are systematically biased towards perceiving a perpetrator is Black or Hispanic. In contrast, police databases that populate the UCR may significantly overcount white (and undercount Hispanic) arrestees, just as administrative correctional records overcount white prisoners (Carson 2018: 7).

  6. While the NCVS is nationally representative, only 75% of the population lives in jurisdictions covered by the UCR (FBI 2018), and the missing jurisdictions are disproportionately less populous (Snyder 2011).

  7. Several other papers (e.g., Weaver et al. 2019; Blumstein et al. 2010) study the relationship between self-reported offenses and self-reported arrests (or a combination of self-reported and official arrests), but, for a variety of reasons, measures of self-reported arrests differ substantially from official records (Junger-Tas and Marshall 1999; Pollock et al. 2015) and are thus less suited for a study of measurement error in official arrest records. Another set of papers, not relevant to the current study, examine the relationship between official and self-reported arrests (e.g., Piquero, Schubert and Brame 2014; Krohn et al. 2013).

  8. One study measures the proportion of all subjects who reported committing at least one crime who also were arrested at least once, but due to very small sample sizes the estimates are heavily underpowered (Huizinga and Elliot, 1987). A second study, by Piquero and Brame (2008: 12), uses the baseline survey wave of the Pathways study to assess a different question: “whether the racial and ethnic groups in [the] sample … exhibit important differences in prior self-reported delinquency or prior arrests.” The paper primarily tests for differences in the mean and median number of self-reported offenses across racial and ethnic groups, as well as differences in the mean and median number of arrests. One table does, however, report a regression of arrests on race, ethnicity and total number of self-reported offenses. The race and ethnicity coefficients are statistically insignificant, but, in part because the dependent variable is the number of arrests rather than the number of crimes, it’s difficult to translate these results into crime ratios conditional on arrest. Furthermore, the estimates are statistically imprecise because they rely on just one wave of data, the only one available at the time. The current paper addresses this imprecision by using ten additional waves of survey data that have more recently become available.

  9. The unconditional estimator, which is biased, examines the proportion of all subjects of a given racial group who both fail to disclose their drug use and test positive on a urinalysis test. The conditional estimator, which is unbiased, measures the proportion of subjects who do not disclose their drug use among the subset that tested positive.

  10. A few other studies, not relevant here, test for evidence that members of different racial or ethnic groups report past arrests at different rates (e.g., Hirschi 1969; Krohn et al. 2013).

  11. All datasets used in the study are available through ICPSR at https://www.icpsr.umich.edu/web/NAHDAP/series/260.

  12. Due to small sample sizes, I cannot disaggregate Hispanic subjects into more specific ethnic categories.

  13. Subjects who reported using a specific drug were asked to choose one of the following options to describe the frequency: 1–2 times, 3–5 times, 6–11 times, once per month, two to three times per month, four to five times per month, and everyday. To estimate the number of uses in a given wave, I assume the subject used the minimum value for each category and, when appropriate, multiplied that value by the length of the relevant recall period. To compute an aggregate estimate of drug-use frequency at the person-wave level, I summed the frequency of use for seven drugs: cocaine, opiates, ecstasy, amphetamines, hallucinogens, marijuana, and amyl nitrates.

  14. It is possible the data is missing some arrests due to record sealing but the number is probably very low. Arizona did not seal criminal records during the study period. While Pennsylvania allowed individuals to petition the court to seal, uptake was likely rare (Prescott and Starr 2020) and petitioners typically had to wait a significant period to become eligible. In contrast, Pathways appears to have obtained arrest information quickly. The study website notes: “Agreements with both the juvenile and adult court systems in Phoenix permit data transfer on a daily (juvenile court) or monthly (adult court) basis. In addition, we obtain FBI records…on a yearly basis.” https://www.pathwaysstudy.pitt.edu/codebook/official-record-information.html.

  15. The unclassified arrests are highly heterogeneous, but some of the most common charges are failure to appear, non-DUI driving violations, and illegal weapon carrying.

  16. Almost 75% of the ambiguous violent arrests are for low-level simple assaults, kidnap**, false imprisonment, or broadly defined sexual offenses. Roughly 65% of the ambiguous property arrests are for forgery, trespass and fraud.

  17. As an alternative approach, Appendix Table 5 reports the results of an OLS regression where the dependent variable is the number of self-reported offenses and the independent variables are race and ethnicity interacted with number of arrests. The estimates are similar to Fig. 1; though, they are sometimes statistically imprecise due to small sample sizes and the need to estimate two parameters for each racial or ethnic group—both slope and level parameters. The regressions are also not easily interpretable because racial bias in criminal records could be reflected either in a negative coefficient on the level parameter for Black or Hispanic subjects or in a negative coefficient on the slope parameter for those groups. Moreover, interpreting the magnitude of racial bias depends on a combination of these two coefficients together.

  18. The results are unchanged if I include the binned category.

  19. The sampling distribution is asymmetric because if the number of crimes reported by Black (or Hispanic) subjects is higher than the number reported by white subjects, the crime ratio can go from 1 to infinity, while if the number of crimes reported by white subjects is higher, the estimate can only go from 0 to 1. My results are virtually identical if I use the percentile confidence interval. The confidence intervals are much larger if I use the normal or basic confidence interval because they incorrectly assume a symmetric sampling distribution.

  20. I do not use the fifth month before survey collection in the first six waves or the eleventh month before survey collection in the last four waves because the reporting period for a substantial fraction of the corresponding person-waves contain only five or eleven months, respectively and the first month in every wave is reserved as the post-period for the previous wave.

  21. When a survey was conducted in the second half of a month, the recall period included the month in which the survey took place. For example, if the survey was conducted on July 20th, the subject was asked to report crimes from January through July. The upshot is that self-reported offense data for subjects interviewed in the second half of the month may be incomplete for that month.

  22. I dropped rows corresponding to months falling outside the 7-year study period for each subject and rows associated with missed waves. I also dropped rows to ensure each event has a full pre- and post-period. First, I dropped the first month in each subject’s first wave because these months represent a post-period without any corresponding pre-period. Second, I dropped all but the first month in each of the subjects’ final wave because they represent a pre-period without any corresponding post-period. Third, I drop all pre- and post-period months associated with a small number of events in which—due to a gap in data collection—more than one month elapsed between the last month of the previous wave and the first month of the next wave. Fourth, in the first six waves of the study, I dropped all rows corresponding with pre-period months that were more than four months away from the event and in waves 7 to 9, I dropped all rows corresponding with pre-period months that were more than ten months away from the event. Finally, I dropped the entire pre- and post-period for every event missing at least one month during the pre- or post-period.

  23. The results are similar from a Poisson regression (see Appendix Table 7); though, I omit fixed effects for calendar month-year because the regressions appear unable to estimate standard errors for them in this context.

  24. The results are substantively similar from a Poisson regression (see Appendix Table 9); though, I omit fixed effects for calendar month-year because the regressions appear unable to estimate standard errors for them in this context.

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    Ben Grunwald

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I would like to thank Brandon Garrett, Lisa Griffin, Aziz Huq, Sandra Mayson, John Rappaport, Megan Stevenson, and three anonymous reviewers for helpful comments and feedback.

Appendix

Appendix

See Figs. 6, 7, 8, 9, 10, and 11, and Tables 2, 3, 4, 5, 6, 7, 8, and 9.

Fig. 6
figure 6

Self-reported crime conditional on arrest, Philadelphia only. Notes +p < 0.10, *p < 0.05, **p < 0.01

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Fig. 7
figure 7

Self-reported crime conditional on arrest, Phoenix only. Notes +p < 0.10, *p < 0.05, ** p < 0.01

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Fig. 8
figure 8

Serious self-reported crime conditional on arrest. Notes +p < 0.10, *p < 0.05, ** p < 0.01. DUI is omitted because it consists of one item and cannot be disaggregated further

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Fig. 9
figure 9

Self-reported drug possession offenses conditional on arrest. Notes +p < 0.10, *p < 0.05, ** p < 0.01

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Fig. 10
figure 10

Mean self-reported offenses by period and race, waves 1–6

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Fig. 11
figure 11

Average number of arrests conditional on number of self-reported offenses

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Table 2 Descriptive statistics for self-reported offenses and official arrests, waves 1–6 (6-month waves)
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Table 3 Descriptive statistics for self-reported offenses and official arrests, waves 7–10 (12-month waves)
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Table 4 Self-reported offenses conditional on arrest, crime ratios conditional on arrest, and weighted average of crime ratios
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Table 5 OLS regressions of arrests and race on self-reported offenses
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Table 6 Crime ratios conditional on arrest, by person-wave level caps on self-reported offenses
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Table 7 Poisson regression on self-reported offense variety scores, waves 7–9
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Table 8 OLS regression on self-reported offense variety scores, waves 1–6
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Table 9 Poisson regression on self-reported offense variety scores, waves 1–6
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Grunwald, B. Racial Bias in Criminal Records. J Quant Criminol (2023). https://doi.org/10.1007/s10940-023-09575-y

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