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The minimum wage and cross-community crime disparities

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Abstract

This study examines the heterogeneous impacts of minimum wages, which could affect low-income workers’ earnings and employment opportunities, on crime rates across neighboring communities. Using geo-tagged reported crime incident data from 18 major U.S. cities, we find that minimum wage increases reduce violent crime rates notably more in low-income communities than in high-income ones. On average, a one-dollar real minimum wage increase narrows the disparity in quarterly violent crime rates between low- and high-income communities by 12%. The impact varies considerably across different types of cities. The income effect resulting from raising the minimum wage is the main contributing factor.

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Notes

  1. See, DiNardo et al. (1996), Lee (1999), Card and DiNardo (2002), Autor et al. (2016), and Bárány (2016).

  2. Considerable research has documented the state and trend of crime gap across communities (e.g., Morenoff et al. 2001; Hannon 2005; Bernasco and Block 2009; Papachristos et al. 2018; Krivo et al. 2021; Wheeler et al. 2021).

  3. Using 1990–2000 annual data on the largest 239 U.S. cities, Fernandez et al. (2014) find that minimum wage increases are associated with reductions in property and violent crimes. More recently, Agan and Makowsky (2021) examine the prison release records across 43 states in the United States from 2000–2014 and find that minimum wage increases are associated with a decline in recidivism, primarily by reducing property and drug crimes. By contrast, some studies document a positive relationship between minimum wages and crime. Beauchamp and Chan (2014) exploit changes in state and federal minimum wage laws from 1997 to 2010 and find a positive effect of minimum wage increases on crime for people employed at a binding wage. Fone et al. (2023) assess the impact of minimum wages on crime using data from multiple sources and find that minimum wage increases do not reduce crime and rather increase property crime arrests among those aged 16–24. Specifically, Braun (2019) uses a search-theoretic framework and shows a U-shaped relationship between the aggregate crime rate and the minimum wage.

  4. The analysis has been done at the levels of city-year (Fernandez et al. 2014), county-year (Fone et al. 2023), police force area-year (Hansen and Machin 2002), and individual (Beauchamp and Chan 2014; Agan and Makowsky 2021; Fone et al. 2023).

  5. While Dube et al. (2010), Harasztosi and Lindner (2019) and Cengiz et al. (2019) show the disemployment effect is small, Sabia et al. (2012), Meer and West (2016), Jardim et al. (2018), and Clemens and Wither (2019) reveal a large disemployment effect. By contrast, Card (1992) and Giuliano (2013) document a positive employment effect. With regard to household income, Neumark and Wascher (2002) and Burkhauser et al. (2023) suggest that rising minimum wage might reduce household income of lower-skilled workers via its disemployment effect. However, Aaronson et al. (2012) and Dube (2019) demonstrate that an increase in minimum wage raises household income.

  6. For example, Card (1992) and Neumark and Wascher (2003) find that raising the minimum wage reduces school enrollment, whereas Campolieti et al. (2005) show that such an increase has no significant effect on teenagers’ school enrollment rate. Pacheco and Cruickshank (2007) document that increasing the minimum wage has a statistically significant negative effect on teenagers’ school enrollment rate, but they find no significant impact on the enrollment rate of 20–24-year-olds.

  7. The 18 cities are Detroit, Baltimore, Milwaukee, Chicago, Portland, Memphis, Philadelphia, Indianapolis, Nashville, San Francisco, Denver, Seattle, Boston, New York, Los Angeles, Austin, Dallas, and Las Vegas.

  8. We download the shape boundary files of the 2010 census tracts and the cities from https://www2.census.gov/geo/tiger/TIGER2010DP1/, accessed on July 25, 2020.

  9. The ACS 5-year estimates at the tract level are downloaded from https://factfinder.census.gov/, accessed in November 2019.

  10. We confirm that using the 74% of the tracts that did not change income status from the 2006–2010 ACS to the 2014–2018 ACS does not alter our conclusions.

  11. While the 2005–2009 ACS uses the 2000 census boundary, the next ten waves of ACS use the 2010 census boundary. Because the boundaries of some tracts might change between census years, the 2000 census tracts may not be matched with the 2010 census tracts. Hence, we decide to use data from the 2006–2010 ACS to define the tract income status.

  12. The crime rates based on this population size would overestimate the crime rates of tracts with faster population growth after 2010. We show in Section 5.3 that using quarterly numbers of crimes generates results comparable to those derived from using quarterly crime rates.

  13. The anonymization process varies by city. For example, in Detroit, “The anonymization process systematically takes the point of the original XY coordinates and places them randomly within 180 feet along the street from the original point.” In Chicago, “The location (where the incident occurred) is shifted from the actual location for partial redaction but falls on the same block.”

  14. The CPI-U-RS, all items, 1977–2019, is downloaded from https://www.bls.gov/cpi/research-series/home.htm, accessed on June 25, 2020.

  15. In Online Appendix Table A4, we show that our main conclusions are robust to including the observations in which the federal and state minimum wages are not binding in the analysis, and using the highest of federal, state, and substate minimum wages as the measure of the binding minimum wage. Nevertheless, the magnitude of the estimate declines considerably, which could be attributed to the fact that other unobserved changes in local conditions are correlated with both substate minimum wages and crime rates. We notice that cities with substate minimum wages tend to have a higher income level than those without.

  16. Tracts within a city are not necessarily in the same county. However, for the 18 sample cities, the city minimum wage rather than the county minimum wage is invariably binding when the substate minimum wage is binding for the sample periods.

  17. To see whether the crime rates are accurately measured, we use the neighboring sample and plot the crime trends by tract income status for each city in Online Appendix Fig. A1. For Indianapolis, Las Vegas, and Dallas, we spot striking and unexpected fluctuations in crime rates. We cannot find any explanations for such changes in the police department reports. However, excluding these cities generates results consistent with the baseline estimates. See Section 5.3 for more details.

  18. Crime statistics from 2010 are publicly available for 10 out of the 18 cities we are analyzing, Austin, Chicago, Detroit, Indianapolis, Los Angeles, Milwaukee, New York, Philadelphia, San Francisco, and Seattle.

  19. As specification tests, we use the raw minimum wage and the logarithm of the real minimum wage for \(MW_{st}\), and use the quarterly number of crimes for \({crime\,rate}_{rt}\). The results are robust. See Section 5.3 for further details. We thank an anonymous reviewer for pointing out that minimum wage changes may affect crime reporting behaviors. For example, due to minimum wage increases, people may come to the conclusion that the benefits of reporting a crime are insufficient to justify the associated costs. However, because a considerable proportion of crime complaints are reported by 911 calls, we expect that minimum wage changes should have a minimal impact on the reporting. Direct evidence on the reporting of crimes awaits future research.

  20. Callaway et al. (2021) emphasize the need for a stronger common trends assumption for identification when dealing with continuous treatments, particularly in analyses comparing units with higher and lower doses. In our context, since minimum wages are continuous and uniformly applied within a city—meaning all tracts face the same minimum wage in any given period—we avoid comparisons between higher- and lower-dose units. Instead, we compare low- and high-income tracts within the same city. We thank an anonymous reviewer for raising this issue.

  21. In the neighboring sample, since we only include low- and high-income neighboring tracts, the common trends assumption implies that the neighboring tracts in one city have the same crime trends in the absence of minimum wage changes.

  22. For example, we account for any correlation between a low-income tract and a high-income tract in the same city in a given year-quarter. We also account for any correlation between a tract in New York and a tract in Chicago in a given year-quarter. In addition, we report the p-values for the standard errors clustered at the state-low-income and year-quarter levels for the baseline estimates.

  23. To obtain a general understanding of the relationship between minimum wages and the rates of specific crime types for low- and high-income tracts, we also use Eq. (1) for estimation and report the results in Online Appendix Table A5.

  24. To ensure they do not confound our main effects, we construct variables for these small events, beforeEARLY, EARLY, PRE, POST, afterPOST. Here beforeEARLY, EARLY, PRE, POST, and afterPOST capture the number of small increases if \( j \le -6\), \(-5\le j \le -4\), \(-3 \le j \le -1\), \(0 \le j \le 3\), or \(j\ge 4\), respectively. In Eq. (3), \(Small_{st}\) represents these five variables for small events and their interactions with the indicator of low-income tracts. In Eq. (4), since the city-year-quarter fixed effects are controlled for, \(Small_{st}\) represents the interactions of the small events measures and the indicator of low-income tracts.

  25. We also use the full sample for estimation and plot the estimates in Fig. A2 in Online Appendix. The patterns are generally in line with those from the neighboring sample.

  26. The two-way fixed effects estimate is a weighted sum of the average treatment effect (ATE) in each treated cell. In our context, a treated cell is a tract in a year-quarter after a minimum wage adjustment. The weights attached to the ATEs sum to one, but some may be negative. Consequently, the fixed effects estimate of \(\gamma \) could be negative even when all the ATEs are positive but heterogeneous across tracts or time. In Online Appendix A1, we use the method proposed by de Chaisemartin and D’Haultfœuille (2020) to assess this issue in our study and find that it is not a serious concern.

  27. From the data spanning from 2000q1 to 2023q1, we identify a total of 95 such prominent events and create 106 event-city-specific datasets. However, 10 of these are subsequently excluded due to the non-binding nature of the federal and state minimum wages in those cases.

  28. The 2006–2010 ACS 5-year data at the city level are downloaded from https://data.census.gov, accessed on April 3, 2023.

  29. To gain insights into whether the narrowing of the crime disparity could be attributed to a steeper decline or a slower rise in crime rates within low-income communities, we also present the findings from Eq. (1) in Online Appendix Table A7.

  30. We examine the robustness of the mechanism analysis results using alternative ACS 5-year estimates at the tract level. First, we use the 2005–2009 ACS 5-year estimates at the tract level, the earliest publicly available tract-level ACS data, instead of the data from the 2006–2010 ACS to classify low-income tracts. Second, we construct a balanced sample of tracts using the ACS 5-year estimates from 2005–2009 to 2017–2021, and merge the tract characteristics for the estimate period of \([t, t+4]\) instead of \([t-4, t]\) with the minimum wages in t. The results of the two robustness checks are reported in Online Appendix Tables A9 and A10, respectively. Despite the substantial differences in the sample composition, these results align with those in Tables 5 and 6, particularly regarding the reduction in the income gap between low- and high-income tracts in response to the minimum wage increases.

  31. In Online Appendix A2, we perform back-of-the-envelope calculations, assuming the income effect of minimum wage changes as the sole channel through which the minimum wage influences the violent crime rate. Our estimation reveals that a one-dollar increase in total annual household income is associated with a reduction of $0.14 in total violent crime cost.

  32. The poverty thresholds in 2010 are downloaded from https://www.census.gov/data/tables/time-series/demo/income-poverty/historical-poverty-thresholds.html, accessed on May 9, 2022.

  33. The mean number of earners per household among the lowest fifth income quintile is obtained from the Current Population Survey (CPS) Annual Social and Economic (ASEC) Supplement - Household Income in 2010, https://www.census.gov/data/tables/time-series/demo/income-poverty/cps-hinc/hinc-05.2010.html, accessed on April 5, 2022.

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Acknowledgements

We thank editor Shuaizhang Feng and two anonymous reviewers for very helpful comments and suggestions.

Funding

Li Li received support from the National Natural Science Foundation of China (72103065).

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  1. School of Public Management, Faculty of Economics and Management, East China Normal University, 3663 Zhongshan North Road, Shanghai, China, 200062

    Li Li

  2. Department of Economics, National University of Singapore, 1 Arts Link, Singapore, 117570, Singapore

    Haoming Liu

  3. IZA Institute of Labor Economics, Bonn, Germany

    Haoming Liu

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Li, L., Liu, H. The minimum wage and cross-community crime disparities. J Popul Econ 37, 44 (2024). https://doi.org/10.1007/s00148-024-01023-w

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