Understanding Race Disparities in Criminal Court Outcomes

Conditioning Sets and Measured Disparities

In the analyses below, we often assume that prosecutors, judges, and other participants in courts have full information—that is, they see all the elements of X* and X^law. Further, in many cases, we assume that —that is, researchers see a subset of the information available to court officials. Since researchers can only condition on information they possess, the empirical literature on racial bias in court outcomes focuses on studies that test null hypotheses of the form:

For now, we proceed under the assumption that , since researchers who attempt to test whether defendants of different races receive equal treatment under the law often construct with this goal in mind.

Given this assumption, there are at least two reasons that researchers may reject condition 2. First, even if we are willing to assume that conditioning on is at least approximately equivalent to conditioning on X*, conditional case outcomes may differ by race because court officials harbor explicit or implicit animus toward minority defendants, and this animus may produce more severe punishments for minority defendants compared to White defendants who pose similar risks to public safety, face comparable prospects for rehabilitation, and face comparable charges.

Second, conditioning on may not be a good approximation for conditioning on X*. Here, court officials produce expected outcomes that vary with the race of defendants conditional on , even though these expected outcomes do not vary with race conditional on X*. For example, consider a judge who learns that a convicted defendant lives in an area controlled by a violent street gang. This information is potentially relevant for sentencing if we assume the judge can use the information to form a better estimate of the likelihood that the defendant will commit future crimes (that is, the information is part of X*); not measured by researchers (that is, the information is not part of ); and correlated with race. If our hypothetical judge weighs the defendant’s residence in a violent neighborhood as an aggravating factor when sentencing the defendant, the judge is statistically discriminating against the defendant on the basis of a factor that is both correlated with race and not identified in the law as a mitigating or aggravating factor.

The consequences of this type of statistical discrimination are not obvious. If the judge weighs this factor properly when making decisions, the practice creates racial differences in the treatment of defendants, given , but the judge is behaving optimally with respect to the welfare consequences of the decision. If the judge places improper weight on unmeasured factors that are correlated with race, the judge creates racial disparities in court outcomes that are socially harmful.⁷

It seems reasonable to expect that judges often possess relevant information that researchers can never recover from datasets. As a result, researchers who discover racial differences in average case outcomes given often offer conjectures concerning whether such differences would remain if they were able to condition on X*. Given this reality, some researchers argue that tests for racial bias should involve tests for racial differences in the distribution of future behaviors among defendants who face the same charges and receive the same verdict and sentence. The rationale behind these tests is straightforward. Consider a set of defendants who face the same charge, receive the same verdict, and receive the exact same sentence. If average future criminal justice outcomes among this set of defendants vary with the race of the defendant, then courts are assigning the same sentences to different groups of defendants who differ both by race and by their propensities to commit new crimes. To many, this pattern suggests that courts are making racially biased decisions. However, as we explain in the section “Outcome Tests,” researchers require strong assumptions in order to infer racial bias in judicial decision making from racial differences in post-sentencing outcomes among defendants who receive the same sentence.

Taken as a whole, existing research has shown that it is difficult to conduct compelling tests of the null hypothesis that comparable defendants receive comparable case outcomes regardless of their race. However, as we noted, even courts that treat all citizens equally under the law may produce racially biased outcomes for structural reasons. We have already mentioned Alexander (2011) and her treatment of differences in mandatory sentences for persons convicted of selling crack versus powder cocaine. In the section “Pretrial Custody,” we note that, as an institution, cash bail is likely a form of structural racism. Scant evidence links pretrial release decisions to the capacity and willingness of defendants to post bonds is an effective way to retain high-risk defendants or compel good behavior among released defendants, but linking pretrial release to cash bonds does generate disparate harm for groups who have been harmed economically by past discrimination.

In addition, structural racism exists when the overall structure of court practices, sentencing laws, and rules governing community supervision create environments where courts routinely impose overly punitive sentences on all offenders in many offense categories. Since minority citizens, especially Black citizens, are much more likely to face arrest for a broad range of offenses, they suffer disparate harm from the ubiquitous assignment of excessive punishment to defendants. In the section “Sentencing Rules and Guidelines,” we discuss how a wave of punitive sentencing reforms drove the prison boom that began around 1980, and in the section “Incarceration and Public Safety,” we argue that existing evidence suggests that these reforms likely went too far. At the margin, the social costs of such large prison populations likely exceed any social benefits for the public, and since Black citizens are arrested at much higher rates than other groups, they suffer disparate harm from the sentencing laws that produce large prison populations.

In the section “Community Supervision,” we discuss the common practice of allowing parole officers to initiate the re-incarceration of parolees who violate technical conditions of their supervision, such as moving to a new residence without prior approval. There is little evidence that this practice generates important improvements in public safety, and because minority citizens are much more likely to be under parole supervision, they suffer disparate harm from this practice.

In the section “Simulating the Impacts of Reforms,” we present the results of several simulation exercises that attempt to assess how much policymakers can reduce absolute racial disparities in incarceration rates by making the practices and policies that govern pretrial release, sentencing, and parole supervision more efficient. The results suggest that it may be possible to significantly reduce racial disparities in incarceration rates by simply improving the rules that guide and constrain the decisions of judges, parole boards, and parole officers.

Alternative Taxonomies

Some may point to incomplete information as a potential source of bias in court outcomes. If judges and prosecutors do not observe the full set of defendant and case characteristics that are either socially or legally relevant for filing charges, conducting trials, negotiating plea bargains, and assigning sentences—that is, court officials produce case outcomes without full knowledge of X*, we expect them to produce nonoptimal decisions, and since rates of criminal justice involvement are much higher in minority communities, these nonoptimal decisions may disparately impact these communities.

We do not disagree, but we note that the justice system in the US is adversarial. The job of defense attorneys is to present information to courts that increases the likelihood that courts will produce more favorable case outcomes for the defendants they represent. Thus, any racial disparities in case outcomes that arise because judges often do not possess relevant exculpatory or mitigating information or because judges are less likely to possess such information when defendants are Black or Hispanic are disparities that arise from structural racism. As an example, low funding levels for public defenders may represent a form structural racism because historic patterns of discrimination against Blacks imply that, on average, Black defendants have less financial capacity to fund their own defense.

We take a similar stance on the topic of implicit bias. A significant literature documents that actors in the judicial system implicitly associate negative personality traits with membership in racial minority groups. Scholars debate the meaning of these associations, but we have found no compelling evidence that implicit bias generates racial bias in actual judicial decisions. Further, if any study were to establish a link between implicit bias and racial bias in judicial outcomes, such a result would simply be evidence that the legal system is structurally flawed. We contend that decisions that are uninformed, ill-considered, or both are more likely to be either too punitive or too lenient relative to socially optimal benchmarks, and therefore legal systems should contain guardrails that prevent rushed and impulsive decisions.⁸

Conditional Disparities in Release Rates

A number of studies find racial disparities in pretrial release rates conditional on various sets of controls for case characteristics and the criminal history of the defendant. Stephen Demuth and Darrell Steffensmeier (2004) examine pretrial release decisions in the seventy-five counties covered by the State Courts Processing Statistics (SCPS) program in its 1990, 1992, 1994, and 1996 surveys. They find that Black and Hispanic defendants are much less likely than comparable White defendants to obtain pretrial release. However, this result appears to be driven by the inability of these defendants to post bail. Black defendants are no more likely to be denied bail than comparable White defendants, and among those not denied bail, bail amounts for Black defendants are comparable to those for White defendants. Hispanic defendants who are not denied bail face slightly higher bail amounts than other comparable defendants, but these differences could never account for the high pretrial detention rates that Demuth and Steffensmeier (2004) document among Hispanics. Whites are detained pretrial in 23.5 percent of cases. The corresponding rates for Blacks and Hispanics are 28.4 and 34.7 percent respectively, and the largest driver of these racial differences is the inability of Black and especially Hispanic defendants to post bail.

Using data from Detroit, Charles Katz and Cassia Spohn (1995) also find that Black defendants are less likely to obtain pretrial release than comparable non-Black defendants, but they find little evidence of racial differences in average bail amounts given case and defendant characteristics. It appears that Blacks in Detroit are more likely to remain in jail pretrial because they have less financial capacity to post bail.

Table 1 presents original results from the main felony bond court in Chicago, Illinois. We examine data from 2011 through the summer of 2017. We highlight racial differences in several bond court dispositions. First, we explore racial differences in the bail amounts set by bond court judges. For these analyses, we create a single bail index that assigns a bail amount to all cases, even those that do not involve bail explicitly. If the bond court judge releases the defendant without requiring the defendant to post bail, we code the bail amount as zero dollars. If the bond court judge denies bail, we code the bail amount as $500,000.¹⁰ Judges rarely assign bail greater than $1.5 million dollars, and over this period, judges in this bond court seldom deny bail. It appears that many judges use a $500,000 bail to signal that they want the defendant to remain in jail.

For male defendants, we run a median regression of bail amount on an indicator for Black, indicators for class of crime, an indicator for a charge involving a violent crime, an indicator for having a prior felony arraignment, and an indicator for time period that captures changes in the administration of bond court. We find a median conditional racial gap in bail of $5,000. We begin with median regression because these results are robust to the specific bail imputation rules we use for defendants who are either released with no bail or denied bail. When we run ordinary least squares OLS regressions of our bail index on defendant and case characteristics, we find that judges set bail almost $1,025 dollars higher for Black male defendants.

When we conduct similar analyses for female defendants, we find slightly different results. The conditional median Black versus non-Black gap is $0, and we find that, on average, Black female defendants face bail amounts that are almost $1,870 lower than comparable non-Black defendants.¹¹

To place these results in context, $5,000 is the default increment for bail decisions. Among the most common bail amounts in our data, the next lowest bail amount is $5,000 less, and the next highest is $5,000 more. Thus, among both men and women, both the mean and median gaps in conditional bail amounts are within one step on the schedule of the most common bail amounts we observe.

We also examine racial gaps in the likelihood that the court releases a defendant without requiring him to post any bail. Here, we see large Black versus non-Black gaps. In almost 19 percent of cases involving non-Black, male defendants, the court grants release without bail, and regression-adjusted release rates for Black males are almost 6 percentage points lower than the rates for comparable non-Black defendants. Among females, we see a non-Black release rate of 32 percentage points and regression-adjusted rates that are 4 percentage points lower than rates for comparable Blacks.

This disparity in direct-release rates appears to be a key source of racial inequality in historical data from Chicago’s main bond court. Among defendants who are not released without bail, we see no racial gap in conditional median bail amounts among men or women. Further, among this sample of defendants, Black men and women face bail amounts that are respectively $3,056 and $4,166 lower, on average, than the bail amounts facing comparable non-Black defendants.

Even though Black defendants do not face higher bail amounts than comparable White defendants who are also required to post bond as a condition of release, racial differences in the likelihood that defendants post bail in a timely manner are another key driver of overall racial differences in pretrial custody outcomes. Here, we examine racial differences in the number of days that defendants spend in jail between their bond court hearings and the dates that their cases are resolved, and we make these comparisons among defendants whom the court requires to post the same bail. The results show that racial differences in the likelihood that defendants post even modest bail amounts contribute significantly to racial differences in jail time served.

Figure 1 presents regression results for male defendants. We regress jail time on the controls in our bail regressions plus a quartic in the bail amount and a separate quartic interacted with an indicator for Black. We do not include cases where defendants were released without bail or denied bail, and we further restrict the sample to defendants facing a bail amount between $1,000 and $250,000.¹²

• Download figure
• Open in new tab
• Download powerpoint

Figure 1.

Days in Jail, Cook County, Men

Source: Clerk of Court of Cook County.

Note: This figure presents two sets of predicted values. Each observation in our data is a case in the main felony bond court in Chicago, Illinois. The cases cover 2011 through August of 2017. We restrict the sample to men who are assigned bail amounts between $1,000 and $250,000. We then regress time spent in jail on an indicator for Black, controls for the year of case assignment, an indicator for a charge involving a violent crime, indicators for the class of the most serious charge, an indicator prior felony charges, indicators for defendant age, a quartic in the bail amount set, and a complete set of interactions between this quartic and the indicator for Black. We define time spent in jail as the number of days spent in jail during the interval between the bond court hearing and the date a case is dropped, dismissed, or decided. Here, we plot the race-specific expected days in jail for a Black versus non-Black defendant who is comparable with respect to the controls other than bail amount set.

The figure presents two plots of predicted days spent in jail as a function of the bail set in bond court. These plots describe results for two hypothetical defendants. One is Black, and one is not, but they both are less than twenty years old, have no prior convictions, and face a similar charge. We plot results for all bail amounts that appear in our data at least two hundred times for both Black and non-Black males.¹³ The graph starts at $5,000 bail. Here, the Black versus non-Black gap in predicted jail time is less than four days, but the gap grows with bail. At $50,000, the gap is just over seventeen days. Among those facing a bail amount of $250,000 the gap is thirty-nine days.¹⁴

While the racial gaps in expected days spent in jail are small given low bail amounts, racial differences in the likelihood that a defendant leaves jail quickly are not trivial. When we examine conditional racial gaps in the probability that a defendant leaves jail within ten days of his bond court hearing, we find that, given a bond amount of $5,000, non-Black males are almost 19 percentage points (72.2 versus 53.5) more likely than comparable Black males to leave jail within ten days of their bond hearings. Note that defendants facing a $5,000 bail requirement must post only $500 to gain release. Thus, even modest posting requirements generate significant racial differences in the prevalence of prompt exits from jail.¹⁵

In Chicago, Black defendants are significantly less likely to gain pretrial release with no conditions in bond court than non-Black defendants who are observationally similar. However, in Detroit and SCPS counties, bond court judges typically make similar custody rulings for comparable defendants of different races. Nonetheless, in all three cases, we see that the practice of requiring defendants to post bonds to gain release creates racial disparities in pretrial release rates, even among defendants who receive the same bail disposition. We conjecture that racial disparities in the economic circumstances of defendants drive this pattern.

These patterns are consistent with the view that, as an institution, cash bail is a form of structural racism. Aurelie Ouss and Megan Stevenson (2023) examine a 2018 reform in Philadelphia that eliminated cash bail for defendants charged with a specific set of offenses. They compare defendants before and after the reform who are charged with offenses that were or were not affected by the 2018 reform, and they find no evidence that the monetary incentives created by cash bail reduce pretrial misconduct. Further, the literature contains no evidence that, if case characteristics and defendants’ criminal histories are held constant, the financial capacity of defendants is highly correlated with their propensity to avoid pretrial misconduct given release. Finally, in many jurisdictions, there is no reason to expect cash bail to work well as an incentive scheme. Economically disadvantaged defendants are often incapable of paying the court cost charges they already face, and they are also judgment proof. As a result, any bond that they can post may well be applied to their court costs even if they incur no violations, and if they do earn violations, the court may find it hard to collect the resulting financial penalties that the law requires.

In sum, there is little evidence that, if case and defendant characteristics are held constant, defendants with greater financial capacity are less risky. Further, cash bail systems often provide weak ex post incentives for better defendant behavior while increasing expected jail time among groups that are economically disadvantaged. These facts imply that cash bail systems are inefficient. Further, since many forms of historical discrimination have reduced the current financial capacity of minority defendants, the disparate harm they suffer from the use of cash bail is a form of structural racism.

Outcome Tests

Another literature looks for evidence of racial bias in bond courts by comparing racial differences in pretrial misconduct among those released before their cases are resolved. Ian Ayres and Joel Waldfogel (1993) find that, if bail amounts are held constant, third-party bail bondsmen in New Haven, Connecticut, charge lower co-pay rates to minority defendants, a finding the authors interpret as evidence that released Black defendants are less risky than released White defendants. Using data from Miami and Philadelphia, David Arnold and colleagues (2018) find that, among defendants released pretrial whom they infer to be marginal candidates for release, White defendants are significantly more likely to be rearrested than Black defendants. They interpret this result as evidence that, on average, judges hold Black defendants to a higher standard when making release decisions.

However, the conclusions that scholars draw from tests for racial discrimination in court decisions based on racial differences in post-adjudication outcomes typically rest on strong assumptions. Researchers have long understood that they cannot draw firm conclusions concerning whether judges set different standards for release depending on the race of defendants solely on the basis of average outcome differences by race among all defendants who are released. Standard models of discrimination make predictions about differences in outcomes among marginal defendants in different groups. Thus, researchers must isolate marginal cases to conduct valid outcome tests.¹⁸ In addition, recent work shows that even in settings where researchers can isolate marginal cases, more robust models of decision-making raise new concerns about the use of outcomes tests as tools for identifying racial bias in judicial decisions.

In a recent article, Ivan Canay and colleagues (2024) invite readers to consider bond court judges who make decisions using the following threshold rule: grant pretrial release if

where

For simplicity, we assume that all defendants are the same on dimensions that researchers measure—that is, the following results are conditional on .

The left-hand side is the expected cost of releasing the defendant, ∆ is the violation cost society incurs from releasing the defendant, r is the race of the defendant, v is a defendant or case characteristic that the judge observes that is not observed by researchers, and z indexes judges.

On the right-hand side, τ (z, r, v) is judge z’s cost of detaining the defendant. The function c(z, r, v) is judge z’s assessment of the social cost of detaining the defendant. For our purposes, λ(z, r, v) represents the mistake that judge z makes when she forecasts ∆, and β(z, r, v) represents judge z’s personal distaste for detaining the defendant.

In this framework, judge z makes racially unbiased decisions if τ (z, r, v) = τ (z, v) for all r and v, but Canay and colleagues (2024) demonstrate that, even when judges are unbiased, post-verdict data on defendant outcomes may contain significant racial differences in average post-sentencing outcomes among marginal defendants.¹⁹ Further, the logic of their argument holds when we assume that the distribution of v is independent of race.

We use a simple example to illustrate the key insight that drives the reasoning of Canay and colleagues (2024). Consider two defendants. The first defendant faces multiple charges, and if convicted, faces a mandatory two-year prison sentence. Further, the police have a high-quality video that clearly establishes the defendant’s guilt. The second defendant faces similar charges, but this defendant has no prior criminal record, and the state’s case is so weak that a trial judge will likely dismiss the case in the weeks to come. In the first case, each day that the defendant spends in jail awaiting trial earns him a credit for time served that reduces the time he will almost surely serve in prison. In the second case, each day in jail is likely just a day of lost liberty. Since the social costs of detaining the first defendant, τ (z, r, v), are lower, an optimal judge should be more reluctant to release him. Put differently, if detaining the defendant has little impact on the total expected punishment he receives, an optimal judge will only release him if E(∆|r, v), the expected violation cost associated with releasing the defendant, is small.

How does this observation impact how we think about the content of marginal outcome tests for racial bias in judicial decisions? Let v be an index of the expected time served for the defendant, and let z be an unbiased judge who makes socially optimal release decisions. Next, consider a set of cases decided by z and assume that the defendants in this set are identical on all traits that z observes except race and v. Next, recall that τ (z, v) is declining in v and assume that E(∆|r, v) is an increasing function of v for all defendants of all races. Further suppose that, for any fixed v, expected violation rates are lower for Black defendants. Since τ (z, v) is a decreasing function of v, the value v* that defines expected time served for the marginal defendant, that is, E(∆|r, v*) = τ (z, v*), will be greater in the sample of Black defendants, and the expected violation risk, E(∆|r, v*), will therefore be lower for marginal Black defendants than marginal non-Black defendants. In this example, average violation rates differ by race among marginal cases even when a court makes racially unbiased and socially optimal release decisions.

This is not a far-fetched scenario. If past discrimination by police inflates the criminal records of Black defendants relative to non-Black defendants who have engaged in the same illegal activities, it is reasonable to expect that, among defendants facing the same expected time served, Black defendants have lower expected violation rates given release. Further, this is just one of many plausible scenarios that raise concerns about marginal outcomes tests as tests for racial bias in release decisions. Any factor v that causes τ (z, v) to slope up or down is a potential source of another example.²⁰

Our second concern about the interpretation of outcome tests in this setting is less formal and focused more on the details of bond court operations. The current literature proceeds as if the bond court judge determines the release outcome. However, in many cases, bond court judges do not determine release outcomes. They set release conditions, and defendants either meet or do not meet these conditions by posting required bonds, arranging for housing that satisfies requirements for electronic monitoring, and so forth. If judges can perfectly predict how defendants will respond to the conditions they set, this distinction does not matter. However, if judges have limited information concerning how defendants are likely to respond to different potential release conditions, releases outcomes in bond court are typically not decisions that judges make but decisions that defendants make in response to constraints that judges choose.

Historically, many bond courts have required judges to make decisions on bond and other release conditions in settings that put clear pressure on these judges to make quick rulings without access to formal risk assessments or information about the financial capacity of defendants.²¹ In recent years, some jurisdictions have provided bond court judges with detailed risk assessments of each defendant as well as information about the financial capacity of defendants,²² but much research on pretrial release outcomes comes from bond courts that asked judges to set release conditions with scant information about each defendant’s violation risk or financial capacity. It is possible that, given these conditions, bond court judges adopt rules of thumb that assign higher bail amounts to defendants who face more serious charges and have longer criminal histories. If this is the case, racial differences in violation rates given release may tell us nothing about how racial bias impacts the decisions made by bond court judges. Rather, these differences may arise primarily because the institutional practice of asking bond court judges to set bail without knowing anything about the financial capacity of defendants leaves many defendants who are low risk but poor in jail pretrial, and the prevalence of these defendants may well differ by race.

Fairness Tests

While tests for conditional differences in mean release rates or differential violation rates given release are the most common tests for bias in bond court outcomes, some studies test alternative conditions that, given our framework, do not make sense as tests for racial bias. These studies test what many researchers call fairness conditions. These conditions typically take the following form:

where S is a risk score or some other metric that the court uses to assess how risky it would be to grant pretrial release to the defendant. D is the release decision, and Y (1) is a potential outcome. Y (1) = 1 implies that, if released, the defendant engages in misconduct before his case is resolved. Y (1) = 0 implies that, if released, the defendant does not violate the conditions of his pretrial release. For simplicity, we assume that defendants cannot generate violations while in custody. So, we set Y (0) = 0 for all defendants.²³

Conditions 3 and 4 state that, among defendants who share a common and would also earn violations if released, the expected risk score and the expected release outcome do not vary with race. Some analysts associate the concept of racial fairness with one or both of these conditions, and Arnold and colleagues (2022) construct a test for disparate impact around condition 4.

Tests of these conditions must overcome estimation challenges since Y (1) is never observed for defendants who are not released, (D = 0). However, we argue that, even in a hypothetical setting where researchers could magically observe Y (1) for all defendants, researchers should not use these conditions to test for racial bias in pretrial procedures. We use a simple example to illustrate this point.

Generating Data from an Optimal Bond Court

Imagine the following data-generating process for a bond court. When an arrested offender is charged, the offender is examined by a risk-assessment team. Above, we define S as a random variable that is the result of the assessment process. The assessment team observes the complete set of characteristics that determine violation risk–that is, , and we assume that, conditional on X*, the probability of misconduct given release is independent of race. We also assume that the assessment team weighs all factors in X* optimally. As a result, S(X*) = P (Y (1) = 1|X*) = P (Y (1) = 1|X*, R). This means that, for defendants of all races, the score produced by the assessment team equals the true probability that Y (1) = 1 given X*. Finally, we assume that the court uses a cutoff rule to make custody decisions—that is, let denote the relevant characteristics for defendant i, and let (). Then, the court releases defendant i iff . For simplicity, we assume that is a socially optimal cutoff rule that does not vary with defendant characteristics.²⁴

Our hypothetical bond court cannot know with certainty whether a given defendant will earn a violation if released pretrial, but the court does make color-blind decisions that are socially efficient. Nonetheless, as long as the distribution of S varies with race, the data that this optimal court produces will always violate the fairness conditions stated in equations 3 and 4 above.

This result is quite general, but we illustrate the result here with a parametric example. To further ease exposition, we suppress explicit conditioning on defendant characteristics. Consider two populations of defendants, r and r′. Among defendants of race r, S ~ U (p_l, p_h), where 0 < p_l < p_h < 1. Among defendants in r′, S ~ U (cp_l, cp_h), where c > 1 is a constant that shifts the distribution of scores to the right and also increases the spread in scores, while maintaining a region of overlap with the distribution of scores for group r.²⁵ We assume that falls in this region of overlap—that is, .

If these two populations of defendants appear before our optimal bond court, the court will generate optimal risk scores and optimal release decisions on the basis of these risk scores. Nonetheless, it is straightforward to show that, given these optimal decisions:

The expected risk score among the r′ defendants who fail given release, Y (1) = 1, is c times greater than the expected score among the parallel group of r defendants. Further, it is straightforward to show that among those with Y (1) = 1, the optimal bond court releases a smaller fraction of group r′.

If we start by assuming that it is not possible to perfectly predict defendant behavior given release, then if the distributions of recidivism risks differ by race, optimal scoring rules and optimal release rules that are free of racial bias will always generate data that fail the fairness tests presented in equations 3 and 4. It is also possible to create biased decision rules that produce outcomes that violate fairness conditions, but in any context where distributions of violation risks differ by race, all unbiased decision rules always produce outcomes that violate fairness. So, when researchers employ data from the US and conclude that a set of risk-assessment scores or bond court release decisions fail a fairness test, they have learned little about whether the assessment scores or the release decisions were contaminated by racial bias.²⁶

Fairness concerns may loom large in a scenario where health professionals employ a racially unbiased set of diagnostic tools to detect disease (for example, early stage cancers) and recommend early treatment on the basis of these test results. In this setting, an unbiased diagnostic test may generate lower treatment levels among patients in racial groups with below-average disease prevalence.²⁷ Since unbiased diagnostic tests may become more fair if they become more accurate,²⁸ violations of fairness criteria in medical testing motivate efforts to improve the accuracy of diagnostic tests. However, medical testing differs from bond court in one key dimension. Each tumor that a medical team tests is either malignant or benign before it is tested. So, perfect classification is possible in theory. In contrast, defendants who stands before a bond court judge are neither violators nor non-violators. They are human beings, and if released, they will exercise personal agency by responding to the challenges and opportunities that confront them after release. In our framework, optimal bond courts do not attempt to classify defendants as violators or non-violators. Optimal bond courts try to predict the expected future costs of releasing a defendant and weigh these costs against the social costs of detention.

In an influential recent paper, Arnold and colleagues (2022) propose a sophisticated test for disparate impact in New York City bond courts that is a variation on the fairness test presented in 4 above. In our notation, they define two forms of disparate impact:

and develop tests for disparate impact by estimating weighted sums of these components. However, we have already shown that, even if the New York City bond courts are free of racial bias, we do not expect ∆₁ = 0, and a similar argument holds for ∆₀.²⁹

In addition, according to our reading of the literature on disparate impact, we contend that, any plaintiff who tried to use the methods of Arnold and colleagues (2022) to convince a court that the New York City bond courts produce a disparate impact on Black defendants would fail. Historically, tests for disparate impact in employment cases have involved comparisons among applicants who, given the information available at the time of application, have the same expected productivity in a specific position. So, we anticipate that disparate impact cases concerning bond court outcomes would hinge on comparisons among defendants with the same expected violation risk and not defendants who share a common potential future outcome, Y (1) = 1 or Y (1) = 0. Further, the traditional disparate impact standard does not require that a bond court employ optimal methods to calculate expected violation risks. It simply states that the court cannot screen on metrics that do not bear a demonstrable relationship to true violation risk.

The test that Arnold and colleagues (2022) propose is novel and interesting, and other researchers may find fruitful uses for the methods they develop. Our concern is that, as a general rule, the fairness tests presented in equations 3 and 4 do not provide information that is relevant for debates about optimal pretrial procedures. Standard tests for disparate impact do not take this form, and our optimal bond court example demonstrates that researchers should expect the Arnold and colleagues’ (2022) method to detect racial differences in release rates given Y (1) = 1 or Y (1) = 0, even in settings where bond courts are making release decisions that are socially optimal and unbiased.

Recent Reform Efforts

Given the growing evidence that cash bail systems are inefficient and that minority defendants suffer disparate harm from their design flaws, several states, cities, and counties have enacted bail reform measures in the last decade, and many more are considering them. Isabella Jorgensen and Susan Smith (2021) document several bail reforms across the country. They highlight recent comprehensive reforms enacted by New Jersey in 2017 and Illinois in 2023. The New Jersey reform did not eliminate cash bail entirely, but it took substantial steps to establish a presumption of release and reduce reliance on financial conditions. This reform substantially reduced jail populations in New Jersey without an attendant increase in rates of failure to appear or pretrial misconduct (Grant 2019).

The Illinois reform is the first statewide law to flatly eliminate cash bail, though it retains supervised release via electronic monitoring and mechanisms for prosecutors to request that defendants be detained prior to trial. There is not yet sufficient follow-up data to study the effects of this new regime.

Other reforms are more local and hence more tenuous. The district attorney of Philadelphia stopped requesting cash bail in a wide range of cases beginning in 2018. Ouss and Stevenson (2023) evaluate this policy change and find limited impacts. Bail judges were still able to give cash bail even when the district attorney did not request it. Rates of cash bail did fall, but rates of pretrial detainment remained constant. This suggests that the main effect of the policy was to remove cash bail in cases where defendants would have otherwise still been able to pay. Ouss and Stevenson (2023) do not find any change in misconduct rates among these affected defendants.

On the other hand, both Georgia and Texas recently passed state laws that strengthen cash bail as an institution.³⁰ Further, Jorgensen and Smith (2021) note that all state legislatures have the power to adopt laws that prevent local courts from pursuing reform efforts.

As debates over bail reform proceed, we note that successful reforms may still become unpopular. Imagine a reform that eliminates cash bail, improves risk-scoring procedures, and enhances the quality of pretrial monitoring services. Now, suppose the reform reduces jail populations by one half while fostering a 10 percent increase in the total number of pretrial violations. Even if the social costs associated with this 10 percent increase in violations are small relative to the large reduction in incarceration costs, opponents of the reform can generate headlines in local media that read “bail reform leads to increase in crimes committed by defendants waiting for verdicts.” Further, since forty-five of the fifty states allow bail bondsmen to make money by providing loans to persons who do not have the funds required to post bail, there are firms in most states that have a financial interest in preserving cash bail systems.³¹

Charging Decisions and Plea Bargains

In the section “Charging Decision,” we discuss the screening procedures that determine whether charges filed by police evolve into cases that courts decide. Some charges do not withstand basic scrutiny, and some defendants are diverted into programs that offer rehabilitation services or special programs. However, among the cases that remain, prosecutors have considerable discretion over the specific charges they file against defendants and over the terms of plea bargains that they offer.

Charging decisions and plea bargains are intrinsically linked because the charges filed against a defendant determine both the likelihood that prosecutor will be able to secure a conviction if the case goes to trial and the severity of the expected sentence if the prosecutor does secure a conviction. Prosecutors realize that the vast majority of defendants are risk averse and are therefore able to use charges that carry mandatory prison sentences as leverage in negotiations over plea deals.

Since most criminal cases do not go to trial but end when the defendant accepts a plea agreement, researchers have explored the impacts of the practice of settling cases through plea bargains. Many findings support the idea that prosecutors leverage the risk aversion of defendants in plea bargaining negotiations, and in jurisdictions where the same group of prosecutors handle charging decisions and plea negotiations, initial charging decisions are an important component of these efforts.

Within our framework, two questions about plea bargaining are immediate. Do prosecutors file charges and negotiate plea deals in a manner that exhibits bias against minority defendants? Does the practice of settling so many cases through plea bargains rather than a mechanism like bench trials produce inefficient outcomes that create disparate impacts on minority defendants?

Marit Rehavi and Sonja Starr (2014) demonstrate how bias may operate through charging decisions. They examine data from federal courts and find noteworthy racial differences in the distribution of time served in prison among comparable defendants in the same initial arrest category. The median Black defendant can expect to receive a sentence that requires him to serve roughly 9 percent more time in prison than a similar White defendant, and Rehavi and Starr (2014) show that this result is driven almost entirely by the choices of prosecutors. Holding arrest records and defendant characteristics constant, these researchers find that prosecutors are much more likely to charge Black defendants with crimes linked to mandatory minimum prison sentences. Further, Rehavi and Starr (2014) conclude that, if federal prosecutors did not discriminate in this manner, the steady-state population of Black inmates in federal prison would be about 10 percent smaller.

It is logically possible that racial differences in the nature of actual crimes committed exist within the 134 arrest categories that Rehavi and Starr (2014) employ, and that these differences justify the resulting racial differences in sentence lengths, but we have no evidence to support this claim, and we do know that, if Rehavi and Starr (2014) had introduced controls for the final charges facing each defendant, they would have found insignificant racial disparities in case outcomes. Rehavi and Starr (2014) illustrate that including variables in that are chosen by court officials may produce misleading results concerning the existence of bias in the courts. Rehavi and Starr (2014) argue that conditioning on the charges filed by prosecutors is equivalent to conditioning on the mechanism that prosecutors employ to exercise racial bias.³²

David Mustard (2001) also finds significant racial disparities in the federal sentencing outcomes conditional on a significant set of controls. He concludes that a key driver of more punitive sentencing outcomes for racial minorities is that prosecutors are more willing to ask judges to sentence defendants below the relevant sentencing guidelines as a reward for cooperating with prosecutors when dealing with White defendants. Given the framework we develop in the section “Analytical Framework,” we are reluctant to offer a definitive interpretation of these results. Do Mustard’s findings demonstrate that federal prosecutors have racial animus toward non-White defendants or that they statistically discriminate against non-White defendants because they correctly or incorrectly judge that White defendants are less prone to re-offend than similar non-White defendants? Or do prosecutors find it easier to obtain valuable cooperation from White defendants, and if so, why?³³

Some readers may conclude on the basis of these results that reforms that would eliminate plea bargains and mandate bench trials as the default means of resolving cases may both reduce racial disparities in case outcomes and improve social welfare. However, Jordan (2024) points out that the welfare analysis of plea bargaining as an institution is complex. Plea bargains provide insurance for defendants, and existing evidence suggests that many defendants are quite risk averse and value this insurance. It is logically possible that restrictions on the use of plea bargains could reduce racial disparities in sentencing outcomes while harming defendants of all races.

Sentencing Convicted Offenders

A larger literature adopts a more reduced form approach and examines racial differences in sentences among either arraigned defendants or those who receive a guilty verdict. Cassia Spohn (2015) notes that, in the early twentieth century, there were well-documented cases where courts dealt with Black defendants in biased ways that almost certainly reflected racial animus on the part of court actors.³⁴ However, she also notes that many early regression studies of racial disparities in sentencing and case outcomes did not find large racial disparities conditional on controls for relevant case and defendant characteristics. Spohn (2015, 225) notes that the 1983 report by the National Research Council’s Panel on sentencing research concluded that racial disparities in sentencing outcomes were “due primarily to factors other than racial discrimination in sentencing.”

Jaeok Kim and André Kiesel (2018) use administrative data from New York City and New York state respectively to examine the relationships between distributions of types of arrests and distributions of sentencing outcomes while including controls for the criminal histories of defendants. They find that racial disparities in the nature of offenses and the extent of criminal histories at the time of arrest account for racial disparities in sentencing outcomes and that courts in New York City may actually produce smaller disparities in sentencing outcomes than researchers would expect given the racial disparities in arrest characteristics.

Greg Ridgeway and colleagues (2020) also study New York sentencing outcomes using data on convicted offenders. They find that Black convicted offenders were about 70 percent more likely to be sentenced to prison than White convicted offenders. However, given controls for criminal history and crime characteristics at the state level, this gap shrinks to roughly 7.5 percent. This study is one of many in the criminology literature that conclude that most of the Black-White gap in incarceration sentences given conviction can be attributed to Black-White differences in the distribution of case and defendant characteristics.

However, Ridgeway and colleagues (2020) also find that conditional racial disparities in sentencing varied significantly among counties within New York state. They find that Black defendants in one county faced a 36 percent higher chance of being sentenced to prison than comparable White defendants. Low average rates of racial disparities in sentencing at a state or national level do not rule out the possibility that courts in certain jurisdictions sentence comparable defendants of different races quite differently. On the other hand, the regression methods that researchers employ to measure conditional disparities may be less reliable when applied to data from one jurisdiction. Ridgeway and colleagues (2020) note that, in some counties, Black defendants with long criminal histories who face serious charges have few or no peers among the population of White defendants. In these scenarios, researchers cannot know whether courts treat comparable defendants the same regardless of race because some types of defendants exist only within one race group.

Chad Topaz and colleagues (2023) employ data from federal courts to examine racial disparities in the length of prison sentences. Racial differences in case characteristics account for almost 90 percent of the overall nineteen-month difference in sentence length between Black and White defendants, but once again, the sizes of the conditional racial disparities in sentence length vary significantly among district courts. In some districts, these conditional disparities are small and statistically insignificant. In others, they are quite noteworthy.

Sentencing Rules and Guidelines

Since racial disparities in sentencing outcomes shrink dramatically when researchers add controls for observed case and defendant characteristics, it is possible that, given more complete sets of controls, these disparities would be negligible. However, the key point is the following: given any reasonable conjecture about the exact magnitude of these disparities given X*, structural factors likely remain the key drivers of overall racial disparities in criminal justice outcomes. In this section, we discuss the structural role of sentencing laws and guidelines in creating absolute racial disparities in the punishments that convicted offenders receive. In the next section, we consider structural flaws in the design of parole and probation supervision.

We begin with some observations about the history of sentencing policies. Derek Neal and Armin Rick (forthcoming) note that from 1925 to 1975, the US incarceration rate remained roughly constant at around one hundred per one hundred thousand.³⁵ Over this period, criminal law maintained an indeterminate sentencing regime that gave judges considerable discretion when sentencing convicted offenders, and court actors viewed offender rehabilitation as an important goal of the criminal justice system. Just as judges enjoyed great discretion when sentencing offenders, parole boards enjoyed great influence over the time that offenders who received a given sentence actually spent in prison. Parole boards saw their discretion as a tool for encouraging good behavior and rehabilitation. However, rising crimes rates and growing doubts that existing practices worked as tools for promoting rehabilitation sparked a change in the laws that governed sentencing and parole, and over the period 1975 to 2007, the incarceration rate increased by more than a factor of five. The rate fell steadily through the 2010s, but in 2019, it remained more than four times greater than the rate of one hundred per one hundred thousand that prevailed for roughly half of the twentieth century.

Here, we stress several points about the era of mass incarceration that has existed since roughly 1985, when the incarceration rate per one hundred persons first hit two hundred. To begin, using a variety of methods, Steven Raphael and Michael Stoll (2013) and Neal and Rick (2016) demonstrate that broad changes in sentencing laws drove growth in state prison populations. For example, Neal and Rick (2016) employ data from the National Corrections Reporting Program (NCRP) to estimate the likelihood that offenders arrested for specific offenses in 1985 would serve prison terms of various lengths. They use the results to simulate what the incarceration rate would have been in 2005 if these probabilities had remained fixed among subsequent cohorts of arrested offenders, and they conclude that the incarceration rate would have grown by roughly 25 to 40 percent. However, the actual incarceration rate grew by almost 145 percent. They conclude that at least 71 percent and as much as 83 percent of the observed increase in incarceration rates between 1985 and 2005 must be attributed to changes in how courts punished persons arrested for particular offenses.

Raphael and Stoll (2013) employ data from 1984 and 2004. They conduct a similar simulation exercise, but they require the prison system to be in steady state in both years. They conclude that 91 percent of the growth in incarceration rates between these two dates must be attributed to changes in how courts deal with arrested offenders.

Both Neal and Rick (2016) and Raphael and Stoll (2013) conclude that a broad-based shift toward more punitive sentencing laws drove these changes in expected time served in prison given arrest. Both review numerous changes in sentencing rules and guidelines at the state level that likely played a role. Further, Neal and Rick (2016) show that increases in the likelihood that an offender arrested for a particular crime would serve prison time are evident in all crime categories. Overall, the likelihood of serving time in prison given arrest increased by 84 percent, and these rates more than doubled for drug crimes and various forms of theft. The likelihood of serving prison time given arrest for a violent crime rose less sharply, but here the expected length of prison spells given incarceration rose sharply. In all violent crime categories, the likelihood of serving at least five years in prison given arrest grew by at least 100 percent.³⁶

Both studies find no evidence that the increase in sentencing severity that drove the state prison boom involved a differential increase in severity within the crime categories where minority defendants are most overrepresented among those arrested. However, data on federal prison incarceration rates over the same period tell quite a different story. Here, rising incarceration rates for drug crimes, weapons offenses, and immigration violations drove federal prison growth between 1980 and 2010, and these trends disproportionately impacted incarceration rates for minorities. Alexander (2011) explains how the Anti-Drug Abuse Act of 1986 contained sentencing rules for offenses involving crack cocaine that were much more severe than the rules for offenses involving powder forms of cocaine. This policy appeared to target Black drug offenders directly, and the population of Black inmates in federal prisons grew much faster than the population of White inmates.

Michael Light (2022) notes that average difference in the length of federal sentences assigned to Black versus White defendants declined sharply between 2009 and 2018, and he discusses several factors that likely contributed to this development. The Fair Sentencing Act of 2010 made it more difficult to apply mandatory minimum sentences in crack cocaine cases. Further, changes in federal law enforcement strategy likely contributed to the large reduction in the annual number of crack cocaine cases filed over this period. However, Light argues that changes in how judges sentenced Black versus White offenders conditional on their criminal history, offense severity, and relevant mandatory minimum sentencing requirements played almost no role in the dramatic decline in the Black-White sentencing gap. Regarding federal incarceration rates among Black citizens, both the disproportionate increase during the prison boom and the subsequent excess decline during the 2010s appear to have been driven by changes in sentencing rules and guidelines and not by changes in the behavior of judges conditional on existing policies.³⁷

Incarceration and Public Safety

We have argued consistently that laws and practices that are excessively punitive are a form of structural racism. Black males are arrested at more than five times the rate that White males are arrested. So, when courts produce approximately color-blind outcomes that are nonetheless too punitive—that is, the social costs of punishing defendants exceed the expected value of any resulting improvements in public order and safety—the laws and practices that govern court operations represent a form of structural racism. Likewise, when courts produce outcomes that are too lenient, Black communities often suffer disparate harm because victimization rates have typically been higher in Black communities, and much crime is within race.³⁸

The prison boom involved a sharp increase in the severity of sentencing rules for both state and federal courts, but to support our contention that this increase was excessive, we need to say something about the public-safety benefits created by this shift in policy. In this section, we review the literature on the links between incarceration policies and public-safety outcomes. The sharp growth of prison populations during the 1980s, 1990s, and 2000s was a catalyst for research on the public-safety benefits of incarceration. Further, in some states, recent efforts to reduce prison populations have produced additional evidence about the relationship between incarceration policies and public safety.

We begin by discussing recent evidence concerning the relationships between incarceration sentences and future offending rates for individual offenders. We then discuss work on the relationships between crime rates and the willingness of society to use incarceration as a sanction for offenders. Studies that provide detailed information about the impacts of incarceration on the behaviors of individual defendants may tell us little about society-level relationships between incarceration rates and crime rates. Criminals who are not incarcerated may increase their criminal activities when other criminals are incarcerated, or potential criminals may be deterred from starting a criminal career when they see existing criminals sentenced to long spells in prison. Further, the treatment impacts of incarceration among the population of currently incarcerated persons may be quite different than the distribution of impacts that we would observe if courts drastically increased or decreased their use of incarceration sentences.

Individual Treatment Impacts of Incarceration

Over the past decade or more, several studies have produced estimates of the impacts of incarceration on future offending among individuals who are marginal candidates for sentences that require time in prison as opposed to community supervision. These studies do not address replacement effects—that is, the possibility that, when the state incapacitates one offender, different offenders may increase their criminal activity. Further, these studies do not address general deterrence effects—that is, the possibility that harsh punishment of existing defendants serves as a deterrent to future offending by others.

Before reviewing empirical results from these studies, we need to define terms. Here, we follow the framework presented in Jordan and colleagues (2023). When the state incarcerates an offender, two impacts on public safety are immediate. First, the offender cannot commit new offenses while in prison. Second, the offender ages while incarcerated, and much evidence suggests that aging directly lowers rates of offending. The first effect is a direct incapacitation effect. The second is an indirect but still unavoidable effect of incapacitating an offender. In addition to these two incapacitation effects, the experience of prison may impact the age-specific offending rates of inmates after their release from prison. Whether time in prison increases or decreases these age-specific offending rates may hinge on how prisons operate, for example, the quality of programs that offer skills training, substance abuse counseling, behavioral therapy, and so forth. Thus, the impacts of prison experiences on post-release, age-constant offending rates are not unavoidable effects linked to incapacitation per se but rather impacts linked to the specific experiences of inmates during incarceration. If these experiences increase age-specific offending rates, time served in prison is criminogenic. If these experiences decrease age-specific offending rates, time served deters crime in the future.

To make these ideas more concrete, consider a group of comparable defendants who are all age a when sentenced. Assume that the court randomly assigns half of these defendants to serve periods in prison and assigns the other half to probation, m = 0. Let τ be a random failure time that denotes the time of the first offense a defendant commits after sentencing, and define F (t|a, m) as the probability that a defendant sentenced at age a to serve m years in prison commits a new offense during the first t periods after sentencing— that is, the probability that τ ≤ t given a defendant sentenced to m periods in prison at age a.

Several things are immediate. To begin, F (t|a, m) = 0 for t ≤ m, since we assume that inmates cannot offend while incarcerated. In addition, if we assume that the experience of prison does not change age-constant rates of recidivism, the full impact of of incapacitation at horizon t is an absolute reduction in recidivism rates of periods

Put differently, if the experience of prison impacts post-release offending rates only because prisoners age while incarcerated, then prison reduces recidivism rates by reducing the time that defendants are exposed to recidivism risk from t to and by shifting initial exposure to age instead of a. The magnitude of both effects is determined by time-served, .

Jordan and colleagues (2023) present estimates of F (t|a, 0) for the complier set—that is, those who may or may not receive an incarceration sentence depending on the severity of the judge assigned to their case, and they find that F (t|a, 0) grows little with t over horizons greater than forty-eight months. They also find small impacts of a year of aging on future recidivism rates. Taken together, these results imply that, over horizons of five years and beyond, the direct impacts of short prison spells on recidivism rates should also be small. Reducing exposure to recidivism risk from five years to four years matters little, and one year of aging has a minor impact on recidivism rates. Since most defendants sentenced to prison serve less than two years and many serve only a few months, there is no reason to expect large direct impacts of incarceration on recidivism at long horizons.

However, both Jordan and colleagues (2023) and Manudeep Bhuller and colleagues (2020) do find lasting impacts of incarceration treatment on recidivism. Bhuller and colleagues (2020) examine data from Norway and find that incarceration treatment reduces recidivism rates by roughly 29 percentage points five years after sentencing. Jordan and colleagues (2023) examine data from Cook County, Illinois. They find that incarceration reduces five-year recidivism rates by just over 29 percentage points among defendants sentenced following their first felony charge. However, when they examine repeat offenders, they find no impact of incarceration on five-year recidivism rates. The Bhuller and colleagues (2020) results for all offenders and the Jordan and colleagues (2023) results for first offenders are difficult to reconcile with the view that prison simply reduces exposure to recidivism risk and shifts recidivism risk to older and less risky ages. These two effects are not large enough to generate large reductions in recidivism rates at long horizons.

Since repeat offenders are former first offenders who were not deterred by the punishment they received in previous cases, no one should be surprised to learn that incarceration impacts recidivism differently among first offenders versus repeat offenders.³⁹ Nonetheless, in the US, most defendants sentenced to prison are repeat offenders.

Further, Bhuller and colleagues (2020) argue that the positive impacts of prison on recidivism rates in Norway are likely the result of effective training programs that may have few parallels in US prisons.

Taken as a whole, the existing literature suggests that, in the US context, most incarceration sentences incapacitate offenders and do little else. Often researchers define recidivism events as new arrests, new convictions, or new incarcerations. However, most crimes do not result in an arrest. So, some researchers have attempted to measure the incapacitation channel through inmate interviews that ask defendants about their history of past offenses. Reviews of this research, much of it conducted during the 1970s, prior to the surge in US incarceration rates, suggest the typical inmate would have committed ten to twenty serious felony offenses in a given calendar year, if he had not been incarcerated and managed to avoid arrest.⁴⁰

These results describe inmates incarcerated during a period when US incarceration rates were quite low, and the stock of prison inmates likely contained a larger fraction of career criminals. Further, Raphael and Stoll (2013) reports that the average age of prison inmates was lower in this earlier period. Both these factors suggest that the benefits of incapacitating the representative inmate fell as prison populations grew during the 1980s, 1990s, and 2000s. In a more recent analysis of the criminal activity of adults convicted of felonies, Emily Owens (2009) finds that the crime-reduction value of incapacitating an additional inmate for one year is roughly one-fifth of the reduction implied by much of the earlier research.

Parole Boards

Parole supervision usually applies to people released from state prison.⁵⁰ For much of the twentieth century, prison sentences involved indeterminate sentences with minimum and maximum sentences set at trial, and parole boards determined effective time served, but beginning in the 1970s, many states adopted more determinate sentencing laws, and the vast majority adopted Truth in Sentencing statues in response to the financial incentives provided by the 1994 Violent Crime Control and Law Enforcement Act.⁵¹

Nonetheless, Kevin Reitz and Edward Rhine (2020) note that despite the move toward determinate sentences in sixteen particular states, parole board decisions still impact time served for nearly three quarters of those released from prison. Even when sentences are determinate, parole and prison authorities exercise discretion when awarding time-served credits for good behavior and program participation.⁵²

In a recent annual report, the California Committee on Revision of the Penal Code (CRPC 2021) analyzed the results of parole hearings occurring in the state during calendar years 2019 and 2020.⁵³ The state parole board controls the release date for a small fraction of inmates, but the report found no differences in the likelihood of being granted parole by race. Both the average grant rate and the average grant rate conditional on the number of recent rules violation reports did not vary by race.

There are few independent estimates of the effect of race on parole hearing outcomes. Beth Huebner and Timothy Bynum (2008) analyze parole release decisions by race and ethnicity for serious youthful offenders in an unnamed jurisdiction. The authors find that legally relevant factors, such as a parole guideline score and an indicator of institutional misconduct, predict the release decision. However, they also find that conditional on the controls they include in a hazard analysis, the time to release conditional on being eligible for parole is relatively longer for Black people and shorter for Hispanic people relative to White people. We should note, however, that the vector of controls used in the study is limited.⁵⁴ More granular controls might yield different findings. Again, the control set in this study may not be the full set of relevant controls. While the evidence pertaining to racial disparities in placement on community supervision is thin, stronger evidence indicates that community corrections supervision is unduly restrictive, revokes many people on probation and parole who would likely not have re-offended, and disparately impacts Black people. We turn to this evidence now.

Parole Supervision

As we have noted, in states where inmates are released from prison to parole supervision, parolees often face significant risk of returning to prison even if they commit no new crimes. In many states, parole officers frequently initiate proceedings that result in former inmates returning to prison because they have violated a rule that governs the conditions of their supervision. In 2021, roughly 27 percent of admissions to state prisons involved people on community supervision, and in many cases, these admissions were punishments for technical violations of supervision conditions.⁵⁵

The oversized impact of technical violations in generating prison admissions is readily observable in data on post-release returns to custody among people released from the Illinois Department of Corrections (IDOC). Persons released from IDOC are subjected to mandatory supervision terms (referred to as Mandatory Supervised Release [MSR]) of one, two, or three years, with lengthier terms associated with more serious offenses.⁵⁶ Like those in other parole systems across the country, people on MSR must check in with their parole officer and obey all predetermined restrictions and orders of the MSR officer. Failure to comply and a recommendation to revoke by the MSR officer results in a hearing before the Prisoner Review Board that is external to the criminal court system in Illinois.

Figure 2 presents sixty-day moving average estimates of the proportion of people on MSR supervision in Cook County, Illinois, who experience their first return to prison as a function of time since release from prison. The data come from the period 1990–2010. The figure follows releasees for five years and provides separate estimates for persons with terms of one, two, and three years.⁵⁷

• Download figure
• Open in new tab
• Download powerpoint

Figure 2.

Empirical Re-incarceration Hazards by Mandatory Supervised Release Spell Length

Source: Clerk of Court of Cook County, Illinois; Illinois Department of Corrections.

Note: Each line presents a sixty-day moving average of the daily re-incarceration hazard for offenders recently released from state prison in Illinois. The individuals in the sample are persons sentenced to prison between 1990 and 2010 in Chicago, Illinois. Circles indicate former inmates given one year of Mandatory Supervised Release (MSR). Diamonds indicate former inmates given two years of MSR. Squares indicate former inmates given three years of MSR. The first vertical line of each type marks the end of the MSR period. The second vertical line marks sixty days after the end of MSR.

The first line in each pair of vertical lines marks one year, two years, and three years from the date of prison release. The second line in each pair is sixty days later. Beyond each of these dates, one of the estimated hazard functions is no longer impacted by supervision-induced revocations.

There are several noteworthy patterns in figure 2. First, while noisy, the hazard rates are similar over much of the first year for those assigned to one versus two years of MSR, and these two categories account for most of the sample. Second, once MSR supervision ends, we see marked declines in the re-incarceration hazard. This occurs at one year for those with a one-year MSR term (circles), at two years for those with two-year MSR terms (diamonds), and at three years for those with three-year terms (squares). Finally, as each group is released from their respective MSR terms, the re-incarceration hazard aligns closely with those of groups whose terms previously expired after shorter periods of supervision.

Individuals who commit and are convicted of new felony offenses will be punished for the new offense regardless of whether they are under community corrections supervision, and readmissions to prison associated with new criminal charges vary little around these cutoffs. Thus, the patterns in the figure are driven almost entirely by the fact that, when supervision ends, returns to prison for technical violations end.

Luke Brinkman and colleagues (2025) analyze more recent data on parole supervision in Illinois. In December 2022, Illinois reduced the standard MSR term for class 3 and 4 offenders from twelve months to six months. Brinkman and colleagues (2025) employ several different estimation strategies, and they find that reducing supervision terms by six months reduces the one-year rate of return to prison by roughly 7–10 percentage points or roughly one-third to one-half of the pre-reform level. This drop in returns to prison is driven by a drop in technical revocations. One year after release, the reform had no impact on the rate of revocations linked to new charges.

Brinkman and colleagues (2025) find similar results for both Black and non-Black persons who exit prison to MSR. The reform therefore had a disparate impact on Black citizens, who are overrepresented in the Illinois prison system.

Data on parole-revocation-hearing outcomes are not as widely available as data on sentencing outcomes in court cases, and we are unaware of other articles that investigate differential parole revocation rates by race while conditioning on individual case and person characteristics. However, two recent evaluations of reforms to parole practices in California and Kansas provide evidence that, historically, revocations rates have likely been inefficiently high, and Black citizens have been adversely and disparately impacted by the policies that produced these high revocation rates.

As we note earlier, California drastically revamped its community corrections practices in 2011. The reform greatly restricted the use of technical violations as a tool for returning parolees to prison and transferred authority for people released on nonserious, nonviolent, nonsexual offenses to county probation departments.

Weekly prison admissions in the state fell from approximately 2,100 to 600, and within six months, the size of the state prison populations dropped by roughly 30 percent (Lofstrom and Raphael 2016).⁵⁸ The findings from several studies strongly indicate that, prior to this reform, California was using technical revocations to incapacitate parolees who did not pose significant risks to public safety. First, there is little evidence that the large reduction in the prison population generated by the decline in revocations increased crime rates. Magnus Lofstrom and Steven Raphael (2016) employ synthetic cohort analysis as well as analyses of cross-county variation in the impact of the reform within the state and find no evidence of an impact of the policy change on violent crime. They find evidence of a modest effect on property crime, but this is driven almost entirely by an increase in one crime category, motor vehicle theft.

Second, in an analysis of monthly release cohorts from the state’s prison system, Lofstrom and colleagues (2014) show that, even though parolees experienced a 30-percentage-point decline in the likelihood of being returned to prison custody within one year of the implementation of realignment, the re-arrest rate for parolees did not change. Further, the rate of conviction given rearrest rose by only 3.1 percentage points. These findings suggest that, in the pre-alignment period, parole officials were not using technical revocations to re-incarcerate parolees who were serious threats to public safety.

These results are important because the decline in the state prison population had a disparate impact on incarceration rates by race. Lofstrom and colleagues (2020) analyze the effects of a constellation of California reforms occurring through 2017 on racial disparities in arrest and incarceration rates in the state. As in all states in the US, Black people in California are much more likely to be stopped by the police, to be arrested, to be under community corrections supervision, and to be incarcerated. Lofstrom and colleagues (2020) use data from the American Community Survey to estimate the proportion of California adults eighteen to fifty-five years of age who are residing in noninstitutional group quarters when surveyed. In 2011, the percent of Black, Hispanic, and White men institutionalized in the state was 9.3, 2.4 and 1.5 percent, respectively. By 2014 the comparable figures declined to 7.8, 2.2, and 1.3 percent. Hence, while the percent institutionalized fell among all groups, the decline was greatest among Black men, and the Black-White gap fell from 7.8 to 6.5 percentage points.

Ryan Sakoda (2023) analyzes several reforms to the use of technical revocation for people under supervision in Kansas. In 2000, the state enacted legislation that eliminated supervision for people who were released from prison after entering prison because they violated a technical condition of probation supervision. In Kansas, the new law describes this change as eliminating probation supervision. However, for our purposes, the original Kansas program is a form of parole supervision because it governs the supervision of people after their release from prison.

The new law applied to a subset of offenders convicted of less serious offenses, and Sakoda (2023) treats the new law as a natural experiment that defines a treatment group and a control group convicted of similar crimes not included in the legislation. The author documents a 28.5-percentage-point decline in the rate of returning to custody against a baseline rate of 35 percentage points. Further, among the treated, there is no measurable increase in convictions for new crimes that result in a return to prison. Finally, Sakoda (2023) demonstrates that, among the treated, the change in policy eliminates the 17-percentage-point Black-White disparity in the likelihood of being returned to prison that existed prior to the reform.⁵⁹

Probation Supervision

As we have noted, courts legally sentence many convicted felons to incarceration but do not require them to enter prison. Probation sentences allow convicted offenders to technically serve prison sentences in their communities under the supervision of a probation officer. If they refrain from committing new crimes and comply with all conditions of their supervision, they earn release from community supervision without ever entering prison. However, as in the case of parole supervision, many states grant probation officers the discretion to initiate proceedings that can produce probation revocations and prison admissions simply because a probationer violated a technical condition of supervision. Further, the best evidence available suggests that granting this power to probation officers is just as problematic as granting similar powers to parole officers.

Probation supervision is often applied to people convicted of misdemeanors or less serious felonies. In misdemeanor cases, failure to comply with the conditions of supervision may result in jail time. In felony cases, revocations usually result in time served in a state prison. In some jurisdictions, a period of probation supervision is appended to short jail spells, again with the threat of being returned to custody for failure to comply (Phelps 2020). Many jurisdictions also use systems of graduated sanctions and various forms of swift-and-certain compliance schemes in an attempt to avoid the imposition of lengthy prison terms.⁶⁰

Evan Rose (2021) analyzes a 2011 North Carolina reform that reduced the punishment for certain technical violations of probation, such as failure to pay fees or failing drug tests, from revocation to prison to short jail stays and other non-incarceration sanctions. Using people on supervised probation as the treatment group and those on unsupervised probation as the control group, Rose first documents a 5.3-percentage-point relative decline in the likelihood of being revoked among those whose supervision conditions were altered by the policy. Among the treated, overall arrests increased by roughly 2 percentage points.

Among Black people on supervised probation, the decline in revocation rates is twice as large, while the increase in rearrest rates is only slightly larger than 2 percent. Thus, the new policy eliminated the Black-White gap in revocation rates while having almost no impact on the Black-White gap in rearrest rates.

Rose notes that under specific, testable assumptions concerning behavioral responses to the law change, it is possible to estimate the expected recidivism rate among persons whom probation officers would have revoked in the pre-reform period but are not allowed to revoke after the reform. Rose calls this rate a measure of probation officer accuracy. If it equals one, then probation officers are using their discretion to revoke persons who are certain to commit a new crime in the near future unless they are returned to prison. If it equals zero, probation officers are revoking persons who pose no threat to public order or safety.

While probation officers initiate technical revocations for persons with higher propensities to offend, probation officers do not possess crystal balls. Further, their accuracy rate is discreetly lower among Black probationers relative to non-Black probationers, roughly .33 versus .55 respectively. In addition, as a tag for recidivists, revocation due to technical violations fails to identify roughly 93 percent of Black and non-Black probationers who re-offend, yet falsely classifies 9 percent of Black compliers and 2.5 percent of non-Black compliers as recidivists. Finally, Rose (2021) also reports that, due to racial differences in revocation accuracy by race, the technical revocations applied to Black offenders in the pre-reform period are much less likely to have generated reductions in crime that justify the resulting increased costs of incarceration.

Rose (2021) also notes that his results do not necessarily imply that probation officers harbor racial animus against Black persons on probation. Probation officers may follow the same rules of thumb for recommending revocations regardless of the race of the person under their supervision, but members of different race groups may find it more costly, on average, to comply with the standard conditions of supervision, such as paying fines in a timely manner. If failure to comply with such conditions is more a signal of economic hardship than criminality, the Rose (2020) results may be expected.⁶¹

A Common Thread

Collectively, the results from reform efforts in Illinois, California, Kansas, and North Carolina indicate that parole and probation supervision are blunt instruments for controlling crime. There is some evidence that technical revocations reduce crime, but the overall correlation between recidivism risk and the incidence of revocation is weak. In all four states, new laws restricted the ability of officials involved in community corrections to incarcerate those under their supervision without going through the courts, and in all four instances, prison populations shrank. Further, in three of four cases, the population of Black prisoners shrank proportionally more than the population of non-Black prisoners.

The Rose (2021) results do provide direct evidence that probation officers are more likely to falsely tag Black probationers. Further, it is hard to imagine a data-generating process that could produce the Sakoda (2023) results that does not involve some form of racial bias during the pre-reform period.⁶² Yet, neither study provides direct evidence that community corrections officers treat Black persons under their supervision differently than others. The key point is that policies that require or allow community corrections officers to send persons under their supervision to prison as punishment for violating administrative rules of conduct create hundreds of thousands of incarceration events each year that appear to do little to improve public safety. It is possible that violations of these rules are weak signals of the propensity to commit crime. If so, these bad policies are forms of structural racism, even if they are enforced in a color-blind manner, because Black persons are grossly overrepresented among those under community supervision.

Three Simple Changes

We have argued that policymakers could replace cash bail systems with pretrial detention systems that produce less disparate harm for minority communities while sacrificing little in terms of public safety. Since cash bail rations pretrial release according to a defendant’s financial capacity rather than the risk the defendant poses to the community, it should be possible to lower jail populations without harming public safety by tying release decisions more closely to violation risks rather than the financial capacity of defendants.

Here, we provide a rough sense of the potential impacts of such reforms by considering the impacts of a policy that mandates pretrial release for all persons charged with nonviolent crimes who are not on probation or parole at the time of their arrest. Since this ban does not apply to violent offenders or those with recent convictions, this policy experiment provides some insight into the potential gains of linking pretrial detention outcomes to public-safety risks rather than the financial capacity of defendants.

We also simulate the elimination of technical parole revocations. To date, no empirical studies provide evidence that parole officers effectively target offenders who pose relatively high risks to public safety when they initiate technical parole revocations that result in parolees returning to prison. Further, Lofstrom and colleagues (2014) show that the elimination of technical revocations in California reduced prison populations without serious harms to public safety.

Finally, we simulate the impacts of reducing prison admission rates for nonviolent offenders by one-half. Neal and Rick (2016) show that, during the prison boom, the likelihood that persons arrested for nonviolent crimes would serve prison terms of short, medium, and long lengths rose sharply, often by a factor of two or more.⁶⁵ Further, in the section “Case Outcomes,” we provide considerable evidence that the crime reduction benefits of increasing incarceration rates diminish with the size of prison populations.⁶⁶

Before presenting the results of these three simulations and a fourth simulation that captures the simultaneous implementation of all three reforms, we note that none of these hypothetical reforms impact how courts respond to violent crime. These reforms address jail time and prison time for nonviolent offenses as well as returns to prison as punishment for behaviors that violate no criminal laws. Our goal is to determine how much policymakers can shrink prison and jail populations through reforms that may well have limited public safety costs. We conclude that policymakers could likely use such reforms to reduce the number of persons in jail or state prison by more than 40 percent.

Methods

We use steady-state simulation methods to evaluate the potential impacts of our three criminal justice reforms. The appendix details our methodology. Here, we provide an overview.

We define thirty-two states that a person may occupy. Three states involve persons who are neither facing a felony charge nor under a sentence for a felony conviction.⁶⁷ These persons may be under probation supervision, parole supervision, or no supervision. We next define twenty-four types of defendants who are facing felony charges that are being adjudicated. Twelve of these types are detained in jail while courts resolve their cases. The other twelve types are granted release. Each type within each set of twelve types is defined by the interaction of four charge categories and indicators for whether the defendant faces a charge while on probation, on parole, or under no community supervision.⁶⁸ Finally, we define five types of prison inmates: persons in prison as the result of technical violations of parole and persons in prison following convictions on charges specific to one of our four crime categories.⁶⁹

We employ data from the State Court Processing Statistics, the National Corrections Reporting Program, and other sources to calculate transition probabilities between these thirty-two states. We set many of the possible transition probabilities to zero to respect the legal rules that govern these transitions. For example, persons cannot go from the state of no community supervision to prison without first going through one of the twenty-four states that describes the operation of courts.⁷⁰

Given an estimate of the transition matrix that generates movements among our thirty-two states, we can calculate the steady-state fractions of the population that occupy each state. We then multiply these fractions by the total US population in 2019 to produce baseline estimates of the counts in each state. We calculate four alternative steady states that capture the results of implementing each of our three potential reforms in isolation as well as the results of implementing all three simultaneously. Table 2 presents four key steady-state populations for the four scenarios: those in jail on pretrial detention, on probation, on parole, and in prison. The table also presents five subpopulations of prison inmates defined by our four charge categories and the possibility of entering prison following a technical parole violation.

Results

Table 2 presents our results. Column 2 presents the steady-state stock levels implied by the transition matrix that we construct. These levels are often reasonably close to the actual values for 2019. We chose 2019 because the impacts of COVID likely moved the various stocks in the criminal justice system far away from steady-state values, and our counterfactual exercises involve comparing different steady states.

Column 3 presents the implied steady-state stocks if we set pretrial detention rates to zero for all nonviolent offenders who are not under probation or parole supervision while holding other transition rates constant. This change shrinks the stock of persons on pretrial detention by roughly 58 percent and also shrinks the stock of prisoners and persons under probation supervision by 4 percent and 7 percent respectively. These latter reductions reflect the fact that recent research indicates that conviction rates are lower when defendants are not detained pretrial.⁷¹

Column 4 presents the implied stocks if we set the rate of technical parole revocations to zero. This change shrinks the prison population by just over 150,000 persons or roughly 13 percent of baseline simulated stock for 2019. This change also increases the number of persons under parole supervision by roughly 75,000.

Column 5 presents the implied stocks if we cut prison admission rates in half for those convicted of nonviolent crimes. The new steady-state population in state prisons is more than 20 percent lower, and the number of persons under probation supervision grows by over 300,000.

In the final column, we implement all three potential reforms at once. While each reform generates modest impacts when implemented alone, the results of implementing all three at once are quite striking. In the simulated 2019 baseline, there are more than 1.8 million persons behind bars: 681 thousand in jail and more than 1.13 million in state prisons. In our final simulation, the total incarcerated population is less than 1.06 million. Put differently, these three reforms, when implemented simultaneously, could reduce the number of persons incarcerated in jails and state prisons by about 40 percent. Further, the total number of persons under community supervision changes little since the increase in probationers is more than offset by a decline in parolees.⁷²

We do not possess the data required to calculate steady-state populations by race, but if these reforms were adopted, there is no reason to believe that Black or Hispanic defendants would see smaller than average reductions in their incarceration rates. Given existing evidence on racial disparities in income and wealth, reducing the number of persons detained pretrial, often because they cannot pay relatively small cash bail amounts, may benefit minority defendants more than White defendants. Further, we know that some prior reforms to the use of technical revocations greatly narrowed racial disparities in prison admissions through this channel.⁷³

We have examined data from the NCRP to assess the impact of curtailing technical parole violations in California on racial disparities in prison admissions. From 2008 through 2011 (the four-year period mostly preceding the reform), we estimate average annual admissions per 100,000 for technical parole violations in California equal to 1,049 for Black people, 191 for Hispanic people, and 174 for White people. For the first four years following the realignment reform implemented in October 2011, the comparable average annual admission rates are 78 for Black people, 17 for Hispanic people, and 10 for White people. Hence, the Black-White differential in annual admissions of this type shrank from 875 per 100,000 to 68 per 100,000 (a 92 percent decrease).

Further, even if these reforms generated the same proportional reductions in incarceration rates for all racial groups, the absolute reductions would be greater for Black and Hispanic citizens than for Whites, and much greater for Black citizens. At the end of 2019, the number of White persons in prison was less than the number of Black inmates. However, the White population was more than five times greater than the Black population. Our results in column 6 imply that implementing all three reforms at once would reduce state prison populations by 32 percent. Given 2019 prison populations as a starting point, a 32 percent reduction in total incarceration rates for all race groups implies that more than 460 additional adults per 100,000 Black adult citizens would be living outside prison, but among Whites, the comparable figure is less than 85.⁷⁴

The difference between columns 2 and 6 in counts of persons in jail waiting for a verdict is larger than the difference in total state prison populations, even though the baseline pretrial detention population in column 2 is much smaller than the baseline state prison population. We have no reliable data on racial differences in pretrial detention rates, but the overall jail incarceration rate in 2019 among Blacks was more than three times greater than the rate among Whites.⁷⁵ The change in pretrial detention populations between columns 2 and 6 likely implies a drop in jail incarceration rates among Blacks that is more than 200 per 100,000, but the comparable figure among Whites is far less than 100.⁷⁶

States and Potential Transitions

The thirty-two states are listed in table A.1. There are three states for people who are not currently in a state prison and who are not felony defendants in an ongoing court case. These states are not on probation or parole, on probation, on parole. We define twenty-four states that characterize types of persons who are in the process of being adjudicated for a felony arrest. The second column lists the twelve types who are detained pretrial. The third column lists the twelve types who are released pretrial. The states in these two columns are defined by all the possible combinations of four offense categories (violent, property, drug, public order), three status categories (not on probation or parole, on probation, on parole), and two pretrial detention categories (detained pretrial, released pretrial). The sum of the populations in the second column gives the number of jail inmates who are being detained pretrial on a felony case. Finally, we define five prison states. These include categories that distinguish prisoners according to why they were admitted to prison. We divide new court commitments into convictions for violent, property, drug, or public-order crimes. The final category is technical parole revocations.

With thirty-two categories, the transition probability matrix that describes the likelihood of transitioning between any two states involves 1,024 probabilities. Many of these are zero by construction or by assumption. For example, among persons who are not felony defendants, not under supervision, and not incarcerated, there are positive transition probabilities to many states that involve facing charges, but no person can transition from freedom to prison or community supervision without going through the courts. As another example, those in prison cannot transition directly to court. They may stay in prison, exit prison directly, or transition to parole.

For all arrested defendants, we calculate the probability that they are detained pretrial or released. Then, for each custody state, we calculate the probability of various case outcomes. For felony defendants who are not on probation or parole at the time of arrest, we calculate, for each offense category, the probabilities of being acquitted, convicted and sentenced to probation, and convicted and sent to prison. For defendants on probation or parole at the time of arrest, we estimate the probabilities that defendants are convicted and admitted, convicted but not admitted, and neither convicted nor admitted to prison. We assume that pretrial defendants under community correction supervision at the time of a new arrest do not successfully exit supervision in the year of a new arrest. They can only transition either to prison or back to their original community corrections status.

Finally, people incarcerated in state prison can transition to being not on probation or parole (an unconditional release) or to being on parole (conditional release), or they can continue in prison. We again calculate these probabilities separately for each offense category.

Transitions into Court

From the BJS analysis of the 2009 SCPS data (Reaves 2013), we observe that among felony defendants in large urban counties, 24.9 percent were arrested for violent offenses, 29.1 percent were arrested for property offense, 32.6 percent were arrested for drug offenses, and 13.4 percent were arrested for public-order offenses. In 2019, there were 495,871 part 1 violent offenses.⁷⁸ Assuming that all part 1 violent arrests are for felony offenses, we use the percentages for 2009 felony defendants to impute total offenses for the other offense categories (that is, for property, drug, and public-order felony arrests).

We use tabulations from Brian Reaves (2013) pertaining to the proportion of arrests within the four offense categories involving persons with no criminal justice status, persons on parole, and persons on probation to apportion arrests across these categories. In addition, we use tabulations from Reaves (2013) pertaining to overall pretrial release rates by offense category and overall release rates by criminal justice status to impute pretrial release rates by offense and criminal justice status. These imputations permit us to generate estimates of the transition probabilities from each of the three states in first column of table A.1 to the twenty-four states listed in the second and third columns.

Transitions out of Court

From Reaves (2013) we also observe overall felony conviction rates by offense group as well as the difference in conviction rates between those detained pretrial and those released pretrial. We generate conviction rates for each of the twenty-four groups listed in the second and third columns of table A.1 assuming that the detained-released conviction ratio is the same within offense groups. We then apply these imputed conviction totals to arrests within groups defined by community correction status, arrests offense, and pretrial detention status. This step yields total convictions within each offense group. Among those who are not convicted, we assume that defendants transition back to their original state.

We apportion the convicted within each offense group into those transitioning into prison and those transitioning into community corrections in the following manner. Using the 2019 admissions data from the NCRP, we first estimate the distribution of new court commitment prison admission across the four offense categories. We then apply this distribution to total admissions in 2019 to generate new court commitments for violent, property, drug, and public-order offense.⁷⁹ The ratio of total imputed convictions by offense category to admissions by offense category provides the admissions rate conditional on conviction for each of the four offense groups. We use these results to generate prison admissions totals for each of the twenty-four groups listed in the second and third columns of table A.1. We assume that convicted persons who are not admitted to prison either transition to probation (if not on probation-parole at arrest or on probation at arrest) or to parole (if on parole at time of arrest).

Transitions out of Community Supervision

We rely on the BJS analysis provided in Barbara Oudekerk and Danielle Kaeble’s (2021) study to calculate values for the total probation population and the number of successful exits from probation. We assume that the remaining probation population (the overall population less the successful exits, less those that we impute being admitted to prison on a new court commitment) continues on probation into the next year.

For the parole population, we pull values for the overall population, the number of successful exits, and the number that are returned to prison from parole (Oudekerk and Kaeble 2021). From the total returned to prison, we subtract the numbers that we impute being admitted to prison on a new court commitment. The balance we treat as being admitted for a technical parole violation. We estimate that roughly 87 percent of admissions to prison from parole are the result of technical parole violations.⁸⁰

Transitions out of Prison

From Ann Carson (2021), we glean that 19.3 percent of people released from prison are released unconditionally, with the remainder presumably released to parole. We use the NCRP to estimate the distribution of releases by the following commitment offense categories: new commitment, violent; new commitment, property; new commitment, drug; new commitment, public order; and technical parole violations. We apply this distribution to total releases from state prison in 2019 to generate an estimate of each flow. We also use the 2019 NCRP to estimate the distribution of the incarcerated population across these same offense categories, and we apply this distribution to the total state prison population for that year to generate stocks. These flows plus the stock estimates provide transition probabilities from each of the five prison incarceration groupings to three possible states: free with no community corrections supervision, on parole, or still incarcerated.

Solving for the Steady-State Populations Shares

The imputations we have discussed generate estimates of the probability of transitioning between each of the thirty-two categories described in table A.1 over the course of year. We array these transition probabilities in a 32 x 32 matrix, T, where T_ij is the probability of transitioning from state i to state j over the course of a year. Note that each element in T is nonnegative and each row of T sums to one. Let T′ denote the transpose of T. An eigenvector, v, of T′ must satisfy:

where λ is the associated eigenvalue. Holder’s Inequality guarantees that the largest eigenvalue of T′ is always one. Therefore, v* contains the steady-state population shares of the system defined by the laws of motion coded in T′ if

and v* is the eigenvector associated with λ = 1 that is normalized so that shares sum to one. We multiply the elements v* by the US population in 2019. The aggregation of the twelve population estimates for the categories in column 2 of table A.1 gives the steady-state pretrial felony jail population. The sum of the estimates for the populations for the five prison groupings in the last column yields the estimated prison population.