The Imprisonment Race: Unintended Consequences of “Fixed” Sentencing on People of Color Over Time

Abstract

Sentencing reforms represent an important shift in the criminal justice system. Reforms' main purpose is the removal of judicial discretion by ensuring a relatively predetermined sentence. This study assesses the effects of reforms on shifts in the odds of imprisonment of Blacks and Hispanics within U.S. states from 1978 to 2005. The study has implications for both theory and policy. Theoretically, social chain theory suggests the law and order movement interacted with structural-procedural changes that led to an unintended consequence. Substantively, the results indicate significant increases in disparities for people of color, which is counter to the policies' stated goals.

KEYTERMS:

• Sentencing reforms
• race and ethnicity
• imprisonment disparities

Acknowledgments

This investigation is based upon work supported by the National Science Foundation under Grant No. SES-0921906.

Notes

1. Vermont was excluded from the analysis, as race-specific imprisonment data was not reported for most years.

2. The cross-sectional time-series analyses referred to here are studies that compare states (all 50) over a large section of time. These studies, like this study, utilize the state as the unit of analysis and analyze changes in imprisonment rate.

3. Savelsberg (1992) only assessed the effects of sentencing guidelines. In this study, his theoretical frame is extended to all reforms considered.

4. Prior research has shown the connection between race and crack cocaine and that it was one of the driving forces behind the rise in young Black males entering prison during the 1980s.

5. In this study, second order, unanticipated, unintended, or unrecognized consequences and latent effects will all be considered representing the general ideal of the laws of unintended consequences as defined by Merton (1936).

6. 1981 was the first year data for Hispanics was available, limiting analysis to three less years than the analysis of Black imprisonment.

7. Unfortunately, early in the time period of this analysis, states only collected data on White, Black, and other with a separate question assessing Hispanic heritage. This, of course, limits the analysis in those groups and a number of researchers have pointed to the limitation of the “other” category as a justifiable measure. Furthermore, when disaggregated data did become available, many states had little to no individuals from a specific racial and ethnic group in prison (largely a result of small numbers in the general population of that state), making analysis unstable (Beck & Katz, 1995; Halaby, 2004).

8. First, early in the data series, states did not record any racial groups beyond Whites, Blacks, and others and used a separate question to assess Hispanic origin. Second, in some states, other racial groups represent relatively small percent in the general public, often resulting in very few and sometimes zero individuals in prison. This makes the analysis difficult, as the coefficients are unstable.

9. Along with incomplete data, Washington DC stopped housing its own prisoners in 2001.

10. Data for the years of 1978 to 1983 are available in the yearly publication: Prisoners in State and Federal Institutions on December 31, 1972 (through 1983). Data for the years of 1984 to 1998 is available in the yearly publication: Correctional Populations in the United States, 1984 (through 1998). Data for the years of 1999 to 2005 is available in the yearly publication: Prisoners, 1999 (through 2005). All three publications are produced and printed by the U.S. Bureau of Justice Statistics (U.S., 1965–1983, 1984–1998, 1999–2008). Rates per 100,000 for each variable were computed by taking the raw number of prisoners for each state by year that was provided by the Bureau of Justice Statistics and dividing by state population per 100,000 as supplied by the Bureau of the Census (U.S., 1965–1969, 1971–1979, 1981–1989, 1991–1999, 2001–2008, 1970, 1980, 1990, 2000).

11. For example, larger coefficients for Blacks (for each of the variables) over both Whites and Hispanics and the larger coefficients for Hispanics over Whites were observed. This is at least partly a result of differences in the dependent variables. For example, Blacks are incarcerated at higher rates; if, therefore, voluntary guidelines resulted in a 10% increase in imprisonment rates for each racial group, the increase in the “effect” on Blacks would be greater than for the White rates and the coefficient associated with voluntary guidelines in the Black equation would be greater than for the coefficient in the analysis of the White imprisonment rates. This limitation necessitates the analysis presented in this article, which presents odds ratios of Black to White and Hispanic to White imprisonment. In addition, the analysis has the added benefit of getting at the heart of the theoretical argument that reforms will have an “unintended” consequence of increasing imprisonment rates for people of color more than Whites.

12. The “standardization” of percent Hispanic involved three steps. First, the most recent categorization system began in 1990 and these percents were left unchanged and used as the “base” to adjust the remaining years. Second, because the rates between 1980 and 1989 were collected under a different definition and coding scheme, these rates were adjusted. The 1980 to 1989 rates were first converted to state-specific change scores. These change scores were then matched to their respective state-specific 1990 percent by using the average change score from 1990 to 1992 as an estimate of the change from 1989 to 1990. Then taking the 1990 percent and multiplying it by the 3-year averaged change score from 1990 to 1992, a percent for 1989 was estimated. Third, the estimated 1989 state-specific percent was then used as the base rate to move backward in time to generate percents based on the actual 1980 to 1989 change scores. The same procedure was then implemented for data prior to 1980 using the estimated 1980 percent as the base.

13. Coding the reforms as dummy variables for adopted suggests imprisonment rates would be affected 100% by the new policy in the first year it was adopted. A logarithmic measure represents a more appropriate theoretically expected effect and should lead to more robust results.

14. Five years was chosen because the median sentence in the United States is close to 2.5 years.

15. Removes the potential for negative scores.

16. Data from the Uniform Crime Report (UCR) is available in print and online from the U.S. Department of Justice, Federal Bureau of Investigation and is produced and printed yearly (U.S., 1965–2008b).

17. Violent crime arrests represent the Uniform Crime Reports indexed crimes, which include the offenses of murder, forcible rape, robbery, and aggravated assault.

18. In this project “violent crime” and “drug crime” rates refer to violent crime and drug crime arrests rates recorded by the Uniform Crime Reports for each year.

19. Data from the census is available online at http://www.census.gov maintained by the U.S. Bureau of the Census and was compiled from both census data and population estimates (U.S., 1965–1969, 1971–1979, 1981–1989, 1991–1999, 2001–2008, 1970, 1980, 1990, 2000).

20. State House and Senate variables were constructed by centering the percent Republican around 50% so that Republican control represents positive deviations from 50%, while Democratic control represents negative deviations. The absolute values of the deviations were then logged with the negative sign returned to the Democrats to create a logarithmic scale with positive and negative deviation from zero to represent the diminishing returns of political party concentrations.

21. Several problems can arise in panel analysis. Parks (1967) developed a generalized least squared (GLS) regression procedure to solve some of the issues and numerous studies have adopted the method (Beck & Katz, 1995). Park's method, however, may understate the standard errors of regression coefficients by as much as 50% to 300%, seriously calling into question the use of this estimator. To counter this problem, Beck and Katz recommend an approach that uses the Prais-Winsten regression with panel corrected standard errors. Their method is a variant of ordinary least squared (OLS) regression and although regular OLS is not particularly useful in time-series cross-sectional, it can be correctly implemented when used in conjunction with panel corrected standard errors (an error correction that takes into consideration the tendency for panels (in this case the states) to be correlated) and corrections for autoregression (the tendency for year to year observations to be correlated with each other) if need be.

22. The Hausman test can be used to determine whether the random effects model, a model that allows for both tome variant and time invariant error to vary freely, is likely to suffer from omitted variable bias. Omitted variable bias is a likely and potentially critical miss-specification of the models where unobserved unit specific (in this case state-specific) variation is not accounted for. If this bias is present and unaccounted for, the coefficient will be unstable and biased. In this case, the Hausman test indicates omitted variable bias is likely in this analysis. In this case, because no additional variables can be added, the fixed effect models should be used.

23. In effect, fixed effects for panels exploits within group variation by holding constant unexplained between group variations. The estimates achieve an unbiased state even when the random effects assumptions are violated. In this analysis the unit fixed-effects model offer significant advantages over the random effects model (Halaby, 2004).

24. An important advantage in this analysis is that fixed effects for states will control for any regional differences that may be present. For example, research has shown that the South has higher rates of imprisonment and the analysis will control for this difference and remove its effect from the results (England, Kilbourne, Farkas, & Dou, 1988). However, if someone were interested in state-to-state differences this model would not be appropriate.

25. As long as the analysis includes controls for time variant bias, in which a significant number of controls can be included in the analysis (e.g., auto-regressive controls for autocorrelation or moving averages).

26. It is not wise to use a random effects model when the Hausman test of the random effects versus fixed effects model for panels indicates that the fixed effect model is preferred. In most time-series cross-sectional analysis issues of confounded errors that are likely in a full random effects model can often be addressed with the inclusion of fixed effects for panels and controls for serial correlation (e.g., autoregressive controls). With the inclusion of fixed effects, the remaining variation becomes a measure of within panel variation from each panel's mean. As this may be a measure that is of theoretical interest, fixed effects for time would not be warranted. To illustrate, when fixed effects for both units and time are included, the substantive interpretation of the coefficients become a measure of the panels’ deviation from time by unit-specific mean that is stable over time, completely removing any unexplained time varying and panel varying effects. This of course could be a measure of theoretical interest, but is substantively different from the “change over time” measure of the panel-only fixed effects model. Whether a researcher chooses to include fixed effects for time is one of substantive interest informed by the research question, while the choice of the inclusion of fixed effects for panels is one of availability of appropriate controls irrelevant of the research question (Halaby, 2004).

27. Y = ((BI/BP)/(WI/WP)) and ((HI/HP)/(WI/WP)) where BI = Black imprisonment rates, BP = Black population, HI = Hispanic imprisonment rates, HP = Hispanic population, WI = White imprisonment rates, and WP = White population.

28. Control variable coefficients can be found in Table 3b.

29. Or the natural log of e, which is 1.

30. Percent change from indeterminate sentencing was estimated by setting the control variables to their mean and all other reform variables to zero and then calculating the increase in the odds of imprisonment for Blacks (5.75) and Hispanics (2.13), respectively.

31. It should be noted that Stemen et al. (2006) and Zhang et al. (2009) did not actually test the racial composition of imprisonment and their research was intended to only highlight the effect on the total imprisonment rate.

32. The models assessed change in the odds of imprisonment both within a state and across state controlling for state-level differences and changes between and within states while controlling for state-level differences not included in the model.

33. Just as individuals are aggregated into state-level measure, it can be said that this type of analysis aggregates the separate micro-level process that change due to the adoption of sentencing reforms into a singular “reform effect.”

34. For example, influencing judicial departures or prosecutorial discretion.

35. For example it is possible that Blacks and Hispanics commit more street crimes, which are often considered more “dangerous” crimes, and thus they will be punished more severely than Whites.

36. This analysis is not intended to suggest that the war on drugs or any other place in the criminal justice system associated with increased racial and ethnic disparities is not increasing racial and ethnic disparities. The analysis here is simply designed to say that sentencing reforms are associated with an increase in disparities beyond other places where disparities can occur, likely operating alongside them.