Article Review

Opening the Door for More: Assessing the Impact of Sentencing Reforms on Commitments to Prison Over Time

Mark G. Harmon1

Received: 21 January 2015 /Accepted: 22 April 2015 / Published online: 8 May 2015 # Southern Criminal Justice Association 2015

Abstract Since the early 1970s, U.S. states have adopted a series of sentencing reforms that have substantially altered sentencing and release policies by limiting discretion of judges, parole boards, and/or prison administrators. The current study assesses shifts in year-to-year changes in new commitments and parolees returned to prison within all 50 states from the years 1972 to 2008. The study tests the theory that sentencing reforms resulted in increased commitments to prison due to changes in the structures of sentencing and not due to increased crime. Data was analyzed using panel regression with robust standard errors, fixed effects, and conditional change scores. By treating six main sentencing reforms as dynamically interacting, the results suggest that certain combinations of sentencing reforms significantly increase new commitments while the number of parolees returned to prison was not meaningfully affected. The analysis further indicates that the combinations that the reforms appear in at the state- level influence the magnitude of the impacts of reforms.

Keywords Sentencing reforms . Net widening . Imprisonment . Panel models

Introduction

Up through the mid-1970s, the United States universally employed the rehabilitation model of imprisonment across all 50 states and at the federal level (Tonry, 2009). Under this model, judges would sentence convicted individuals to relatively wide-ranging prison terms (e.g., 5 to 25 years). Then, after a specified period of time, parole boards would often determine when the prisoner was properly rehabilitated and ready for

Am J Crim Just (2016) 41:296–320 DOI 10.1007/s12103-015-9296-4

* Mark G. Harmon [email protected]

1 Mark O. Hatfield School of Government, Division of Criminology and Criminal Justice, Portland State University, PO Box 751, Portland, OR 97207-0751, USA

release. The model reflected a criminal-centered approach designed to pattern punish- ment after the offender’s rehabilitation needs (Irwin & Austin, 1997).

Beginning in the 1960s, a host of individuals and organizations including politicians, criminal justice practitioners, social science researchers, and the media started to criticize the indeterminate model and demanded new approaches. The criticisms included complaints about the apparent arbitrary nature of sentencing, perceived ineffectiveness of treatment and reform programs, belief that correctional facilities were too cozy, and perceived ineffectiveness of the system in curbing recidivism. Specific to sentencing, critics argued that there was far too much variability in sentencing types and time served (Blumstein, 1983; Tonry, 2009). The criticisms aided in the adoption of a series of extensive criminal justice reforms often labeled the Bget tough on crime^ or Blaw and order^ movement. As part of this Blaw and order^ movement, legislators and/or voters passed a series of discretion-limiting sentencing reforms in 39 states and at the federal level (Bureau of Justice Assistance, 1996; Tonry, 2009).

One of the byproducts of the law and order movement was that in the early 1970s an unprecedented rise in the prison population began. Over the next 40 years imprison- ment nationwide increased over 500 % (Irwin & Austin, 1997). Over the last few decades, criminal justice scholars have endeavored to understand the role that sentenc- ing reforms passed during the law and order era played in America’s imprisonment boom. The research has produced a number of competing findings, with some scholars indicating a connection between the reforms and increased imprisonment (e.g. Harmon, 2013; Stemen, Rengifo, & Wilson, 2006), while others have shown no relationship or even a reduction in imprisonment (e.g. D’Alessio & Stolzenberg, 1995; Marvell, 1995; Zhang, Maxwell, & Vaughn, 2009).

With no clear consensus in the literature, a number of questions related to the impact of sentencing reforms are still unresolved. One question of note is whether the increases and/ or decreases in imprisonment were the result of changes in the number of individuals going to prison, or changes in the length of sentences, or both. Zhang and colleagues’ (2009), study was one of the handful of studies that systematically assesses both admis- sions to prison and sentencing length in the context of sentencing reforms and the only study to incorporate reforms in a similar fashion as in this analysis presented in this study.

The analysis in this study focuses on the effects of sentencing reforms on prison admissions, both new commitments to prison and parole violators returned. No prior research could be found that specifically assessed both of these areas of prison commitments nor has commitments (including new commitments) been assessed with the models utilized in this analysis. The goal of this analysis is to measure the changes in the trends of new commitments and parolees who returned to prison as a result of the adoption of sentencing reforms across all states from 1972 to 2008.

This study models the impact that six main sentencing reforms had on commitments to state prisons in the U.S. The reforms included are sentencing guidelines (divided into presumptive and voluntary), statutory presumptive sentencing, determinate sentencing (abolishment of discretionary parole boards), truth in sentencing, and three strikes laws, all of which represent significant changes to sentencing policies. The dates and in which states these reforms were adopted is outlined in Table 1. It indicates that sentencing reform states now outnumber non-reform states. Thirty-nine states have at least one reform, with most states having two or more (Frase, 2005; Stemen et al., 2006; Tonry, 2009).

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Table 1 Distribution of sentencing types across the United States as of 2008

Presum. Guide. Vol Guide. Stat. Presum. Deter. Sent. Truth in Sent. Three Strikes

Alabama – 2006 – – – –

Alaska – – 1980 – – –

Arizona – – 1978 1994 1994 –

Arkansas – 1994 – – – 1995

California – – 1976 1976 1994 1994

Colorado – – 1979 79–85 – 1994

Connecticut – – – 81–90 1995 1994

Delaware – 1987 – 1990 1990 –

Florida 1994 1983–93 – 1983 1995 1995

Georgia – – – – 1995 1995

Hawaii – – – – – –

Idaho – – – – – –

Illinois – – – 1978 – –

Indiana – – 1977 1977 – 1994

Iowa – – – – 1996 –

Kansas 1993 – – – 1993 1994

Kentucky – – – – – –

Louisiana – 1987 – – – 1994

Maine – – – 1976 1995 –

Maryland – 1983 – – – 1994

Massachusetts – – – – – –

Michigan 1999 1984–98 – – 1994 –

Minnesota 1980 – – 1982 1993 –

Mississippi – – – 1995 1995 –

Missouri – 1997 – – 1994 –

Montana – – – – – 1995

Nebraska – – – – – –

Nevada – – – – – 1995

New Hampshire – – – – – –

New Jersey – – 1977 – – 1995

New Mexico – – 1977 1977 – 1994

New York – – – – 1995 –

North Carolina 1995 – – 1981 1994 1994

North Dakota – – – – 1995 1995

Ohio 1996 – – 1996 1996 –

Oklahoma – – – – – –

Oregon 1989 – – 1989 1995 –

Pennsylvania 1982 – – – 1991 1995

Rhode Is. – – 1981 – – –

South Carolina – – – – – 1995

South Dakota – – – – 1996 –

Tennessee 1989 – – – 1995 1995

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Literature Review

The birth of the law and order movement is often linked to the decade of the 1960s. During this time, increased urban unrest that resulted in riots, radical youth and black power movements, assassinations of top political figures, and increased crime rates impacted American’s sensibilities about crime and justice (Beckett, 1997; Clear & Frost, 2009; LaFree, 1998). These sensibilities interacted with and were enhanced by media coverage (Scheingold, 1991; Simon, 2007), public concerns (Clear & Frost, 2009; Warr, 1995), and the political responses to these problems (Beckett, 1997; Hagan, 2010). Scholars noted that these interactions created a perfect storm that cultivated increased focus on crime and a demand for more punitive sanctions. America thus declared a war on crime and a war on drugs whose mantra was tough on crime and tough on offenders. Among the many weapons of these wars was sentencing reforms.

At the national level, the movement translated into substantial policy changes and investment in justice initiatives (Tonry, 2009). Over 40 laws were passed at the federal level including the Omnibus Crime Control and Safe Streets Act of 1968, which (among other things) created the Law Enforcement Assistance Administration (LEAA). The LEAA provided funds to law enforcement agencies to modernize and professionalize their operations. The bail reform act (United States Code, Title 18, Sections 3141-3150) and sentencing reform act (as part of the Comprehensive Crime Control Act of 1984) were both passed in 1984 creating the federal sentencing guidelines. The Reagan administration alone signed into law 23 crime and justice related bills, significantly more than his immediate predecessors. New reform bills continued into the 1990s. For example, in 1994 the federal government passed the Violent Crime Control and Law Enforcement Act (1994 Omnibus Crime Bill). The law allocated billions of dollars to states as long as they adopted truth in sentencing laws,

Table 1 (continued)

Presum. Guide. Vol Guide. Stat. Presum. Deter. Sent. Truth in Sent. Three Strikes

Texas – – – – – –

Utah – 1985 – – 1985 1995

Vermont – – – – – 1995

Virginia – 1995 – 1995 1995 1994

Washington 1984 – – 1984 1984 1993

West Virginia – – – – – –

Wisconsin – 85–94 & 99 – – 1999 1994

Wyoming – – – – – –

Total 10 11 8 18 24 24

Table 1 represents the current sentencing type used by each state as of 2008. Presum. Guide. presumptive sentencing guidelines. Vol. Guide. voluntary sentencing guidelines. Stat. Presum. statutory presumptive sentencing. Deter. Sent. determinate sentencing. Truth in Sent. truth in sentencing. Three Strikes three strikes laws. All other states utilize indeterminate sentencing

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which mandated 85 % of the original sentence being served. The law also supplied money for more police officers and other crime control programs (Hagan, 2010).

At the state level, 39 states and the District of Columbia passed some type of sentencing reform (Bureau of Justice Assistance, 1996; Tonry, 2009). These reforms represented a movement toward a justice model of punishment that was in line with the Bget tough on crime^ mantra. The movement focused on making criminals pay and deterring those who might commit future crimes. In a sense, sentencing reforms took to heart the three tenets of deterrence theory; that punishment must be swift, certain, and severe. Because the Supreme Court’s Bdue process^ emphasis made it difficult to increase the swiftness of punishment, reforms were most successful in instituting the latter two tenets. They pushed sentencing towards what the designers of the policies dubbed was an appropriate and certain response to crime. Additionally, the reforms were designed to be severe enough (at least more severe than before the reforms) to deter crime and/or at least incapacitate the offender. By the mid-1970s, the sentencing reform movement began to have concrete effects on legislation, with the adoption of several reforms at the state-level (Bohm, 2006; Garland, 2001; Tonry, 1995). By the late 1990s, two-thirds of the states had passed at least one reform, with most of them passing more than one (Bureau of Justice Assistance, 1996; Frase, 2005).

Criminal justice scholars have long been interested in assessing the impact of sentencing reforms. The results of the previous studies are inconsistent and at times quite contradictory. Some scholars have pointed to increased imprisonment as a result of sentencing reform. Other scholars have suggested the opposite, indicating no additional increase or even a reduction in prison growth (Harmon, 2013; Stemen et al., 2006). As a result of these inconsistent and contradictory findings, no consensus has emerged as to the true impacts of sentencing reforms.

For example, a recent study by Zhang and colleagues (2009) tested a Weberian theory of legal rationality on state-level reforms categorized in a similar way as the reforms in this study. They found that across all 50 states and the District of Columbia that states with sentencing reforms were generally not associated with larger changes in both new commitments to prison and time-served than non-reform states. They did find that voluntary sentencing guidelines (definition found in Table 2) significantly in- creased new commitments, while three strikes laws significantly reduced new commit- ments. However, in both cases the impact was relatively small and outweighed by a number of other factors. Furthermore, they found no relationship between reforms and increased time served. In a study authored by Sorensen and Stemen (2002) that assessed reforms in a similar way also found that changes in sentencing policies largely did not impact imprisonment or admissions. Their study indicates that only presump- tive sentencing guidelines were consistently related to either admissions or imprisonment.

Conversely, D’Alessio and Stolzenberg (1995) found that after the passage of sentencing guidelines jail populations rose in Minnesota, but that the impact was lessened when prison overcrowding was considered. Stemen and associates (2006) measured the impacts of the same six sentencing reforms presented in this study1 and reported a number of competing findings in their large National Institute of Justice

1 There are slight differences in the way Stemen and colleagues categorize the reforms from the way they are categorized in this study.

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study of state imprisonment policies. As an illustration, they found that the combination of determinate sentencing and voluntary sentencing guidelines increased state impris- onment. On the other hand, their study also indicated that the combination of determi- nate sentencing and presumptive sentencing guidelines lowered imprisonment rates, though not significantly.

Generally, the results of the studies that assessed states-level changes in imprison- ment over time (e.g., Harmon, 2013; Marvell, 1995; Nicholson-Crotty, 2004; Sorensen & Stemen, 2002; Spelman, 2009; Stemen et al., 2006; Zhang et al., 2009) have suggested that the elimination of discretionary parole release (e.g., determinate sen- tencing) and the adoption of truth in sentencing were more likely to be associated with changes in imprisonment, though some studies indicated these reforms increased imprisonment while others suggested they decreased it. For example, Stemen and Rengifo (2010) found that back-end sentencing reforms that constrain release decisions are more impactful than front-end reforms that constrain sentencing discretion. They generally found that these back-end reforms lowered imprisonment more than in- creased it. It is important to note that this finding is not universally supported across all of the studies.

Marvell (1995), in findings similar to Stemen and colleagues’ (2006) study, found that when prison capacity was specifically taken into consideration while adopting sentencing guidelines, prison growth slowed between 1974 and 1990. Although Marvell (1995) study was methodologically robust, it possessed some limitations, including an analysis restricted to nine presumptive sentencing guideline states. Spelman (2009), Stemen and colleagues (2006), and Zhang and colleagues (2009) all analyzed similar reforms (to each other and to this study) with panel data from all 50 states. Like the analysis in this study, they included data that covered a relatively long period of time. The results of these three studies generally indicated that reforms more often reduced, rather than increased, imprisonment and prison admissions or were not

Table 2 The six reforms included in analysis

Reform Description

Presumptive Sentencing Guidelinesa

Consists of a matrix of possible sentences with a more narrow sentencing range defined by an offender’s prior offenses and the severity of the offense. The sentence is enforced through appellate review.

Voluntary Sentencing Guidelinesa

Treat guidelines as formal recommendation, but does not legally mandate they be followed by the judge. That is, while judges generally follow them, the prosecution nor the defense may appeal deviations from the matrix

Statutory Presumptive Sentencinga

Acts less like a sentencing rubric than sentencing guidelines. It represents an attempt to create uniformity within similarly situated crimes by specifying an appropriate or Bnormal^ sentence for each offense.

Determinate Sentencingb Refers to a system without discretionary parole boards.

Truth in Sentencingb Requires offenders serve a statutorily defined minimum amount of time. Only states meeting the 1994 Federal Omnibus Crime Bill minimum of 85 % time- served of original sentence are considered in this analysis.

Three Strikes Lawsc A habitual offender law focused on three-time felony offenders. It generally suggests a severe sentence for a third felony offense.

a Front-End Reforms b Back-End Reforms c Sentencing Enhancement

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significantly related to changes in imprisonment. Conversely, Spelman (2009) found that truth in sentencing laws, especially those passed after the 1994 Omnibus Crime Bill, resulted in a 13 % increase in state imprisonment. Spelman (2009) contends that the increase in imprisonment is more of a reflection of the funds made available through the federal crime bills and the ability of a state to spend more on justice due to growths in state revenues between the 1960s and 1990s. Whatever the reason, the study did indicate a significant, positive effect of truth in sentencing laws. Similarly, Harmon (2013) found that sentencing reforms were in some cases related to increased growth in imprisonment, especially when multiple reforms were present. Harmon’s study found that the interactions between the sentencing reforms are an important consideration, especially the interaction of the back-end reforms. The study did show that reforms in some cases slowed prison growth but that was less common.

While some prior research has shown a relationship between sentencing reforms and changes in imprisonment, one of the key questions not fully explained is whether this change was a result of longer sentences or because more individuals were entering the system. As stated before, Zhang and associates (2009) is one of the only studies to date that specifically explored new commitments to prison in a context similar to this study. While the goals of this study and Zhang and colleagues’ (2009) study were similar and incorporated similar data, there are some important differences. First, Zhang and colleagues’ (2009) study a hierarchical linear model as opposed to the panel model implemented in this study. Second, their study covers less years of analysis. Third, this study included interaction effects between the reforms that Zhang and colleagues’ (2009) did not include.

It’s possible that sentencing reforms increased admittance to prison. For example, the general increased punitiveness of sentencing reforms may result in a process that increased the number of individuals Bcaught-up^ by a new policy. That is, the reforms increased the number of people brought into the system through changes in criminal justice policy or practices itself, and not through increased criminal activity (McMahon, 1990). For example, Schwartz, Steffensmeier, and Feldmeyer (2009) found that in the 1990s, women were arrested at increasingly higher rates for assault in spite of evidence that showed that women were not actually committing substantially more assaults. They concluded that changes in criminal justice policies and practice, and not changes in criminal behavior, were the main determinate of the increased arrests. Similarly, the analysis presented below considers whether sentencing reforms increased the number of new commitments to prison and parole violators returned to prison, regardless of criminal activity or other determinates. In other words, the reforms themselves, simply through their application, brought in more individuals.

Some scholars (Marvell, 1995; Steffensmeier & Demuth, 2006; Stemen et al., 2006) have suggested that there are three possible ways that sentencing reforms could have led to increased prison admittance. First, some convicted criminals of relatively small crimes may not have gone to prison prior to sentencing reforms. Generally, inmates only go to prison if they are sentenced to more than 1 year, where a person with a lesser sentence would be serving time in county or local jail. It is plausible that under sentencing reforms, relatively minor crimes that did not result in a prison term under previous sentencing structures now carry a prison term. This would directly impact new commitments to prison. Second, more criminals could be sentenced to serve time in prison rather than on probation (or other non-confinement means), resulting again in an

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increased in those who go to prison as new commitments. Third, sentencing reforms often mandate that prisoners being released be placed under supervised (sometimes intensive) parole, rather than unconditional release or other more passive forms of parole. This could lead to higher rates of recorded parole violations, resulting in a direct increase in parole violators returning to prison.

Following from the assertions made by previous scholars, this study tests two distinct hypotheses. The first hypothesis is that states that adopted sentencing reforms had higher rates of new commitments to prison than states that did not adopt reforms. The second hypothesis is that states that adopted sentencing reforms had higher rates of parolees return to prison than states that did not adopt reforms. While this study focuses on admittance to prison, it should be noted that it does not exclude the possibility that reforms increased time served.

It is worth noting that some of the reforms assessed seem more directly connected to admittance to prison than others. For example, the front-end reforms of sentencing guidelines and statutory presumptive sentencing, due to their focus on sentencing before an inmate enters prison, seems more directly connected to new commitments to prison. On the other hand, determinate sentencing and truth in sentencing laws seem to be less directly connected to new commitments. These back-end reforms are more explicitly connected to release than admissions. The inclusion of these back-end reforms in the analysis of new commitments is vital because states adopted multiple reforms in different combinations and at different times (see Table 1). This suggests that the effects of reforms should be treated as being both interactive and dynamically changing. Fortunately, the regression analysis incorporated in this study allowed for the modeling of the reforms likely dynamic and interactive nature (Jaccard & Turrisi, 2003).

Method

This study utilized state level data covering all 50 states for each year between 1972 and 2008. The effects of sentencing reforms were modeled using panel regression analysis to assess the impacts of sentencing reforms on new commitments to prison and parolees returned. These are the two mechanisms where individuals enter prison and both represent areas where reforms could have an impact. In the analysis both cross- sections in the form of states as well as time in the form of years were modeled. This model, by simultaneously modeling cross-sectional and time-series effects, resulted in 1850 (50 states * 37 years) possible observations. This Bpooling^ of the time-series and cross-sectional data greatly improves the statistical power of the models (Hsiao, 2003; Wooldridge, 1997).

The Bureau of Justice Statistics through their yearly report, prisoners,2 1999 (or corresponding year) supplied the main dependent variables. The remaining variables were compiled from 14 different sources. The specific source location of each variable is discussed below. The models in the analysis allowed for the assessment of the changes in both new commitments and parolees returned to prison due to the adoption of sentencing reforms over time and across all 50 states simultaneously.

2 Note that the report changes names three times over the years under analysis.

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Dependent Variables

To assess the impacts of sentencing reforms on the two distinct areas under investiga- tion, the analysis included two different dependent variables. The first measured the number of new commitments per 100,000 to state prisons. This includes anybody admitted to prison for the first time for a new crime, including first-time offenders, previously incarcerated individuals admitted for a new offense, and probation violators remanded to prison for the first time. The second measured the number of parolee violators returned to prison per 100,000. Data for both dependent variables was obtained from the Bureau of Justice Statistics (BJS) (1972, 1984, 1999) year-end reports on state-by-state prison populations, which includes admissions (known, be- ginning in 1999, as Prisoners, 1999 (through 2008)). The BJS published these reports yearly. The variables were measured at the state-level (including all 50 states) over time from 1972 to 2008. There were a 140 missing cases in the new commitments data and a 153 in the parolee data.3 This missing data was not overly clustered in one region of the country or within a small number of states suggesting the missing data does not significantly undermine the analysis.

A Dickey-Fuller test of new commits (Z(t)=−3.74) and of parolees returned (Z(t)=− 3.08) (suggested the presence of a unit root in both dependent variables. This means that this year’s data is likely related to the previous year’s data. This is an unsurprising finding given that when the dependent variables are measured as a rate there are substantive reasons to believe that a previous year’s rates of those entering the system are highly associated with the current year’s level (Spelman, 2008). This year to year relationship is called serial correlation and because it is likely present, the dependent variables were transformed into percent change (ΔY=((Yit/Yit−1)−1)*100). Regression models utilizing this type of dependent variable are sometimes referred to as a change- score (as percent change) model (Finkel, 1995; Halaby, 2004).

Between 1972 and 2008, imprisonment trended up almost 550 %. In this context, reforms would likely appear to increase new commitments and parolees returned to prison simply because they are clustered on the more recent end of the time-series where the rate of those entering prison was the highest. This is a common time-series specification problem that must be corrected. One of the advantages of incorporating the percent change transformation into the analysis is that it also corrects for this problem. Unlike the rate models (models with unchanged dependent variables), the change-score models no longer fail the Dickey-Fuller tests for both dependent vari- ables. This allows for assessment of state-level changes for those entering prison over time due to changes in state-level covariates.

Sentencing Reform Variables

Table 2 outlines the six key independent variables representing sentencing reforms and how they differ from one another. While most previous research is in agreement on the general goals of the reforms, it differs considerably in how to characterize the design and application of the reforms and there is little consensus about how to classify them

3 In some isolated cases data was missing for a specific state by year data points of the independent variables. In these cases a three-year moving average extrapolation technique was used to input the missing data.

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into appropriate groups (Frase, 2005; Stemen et al., 2006). This analysis largely follows a classification system of reforms that focus on the loci of impact (on the front-end of sentencing or the back-end of release) and on important legal distinctions. They were compiled from four different sources that included a report from the Bureau of Justice Assistance (1996), a study by Frase (2005), a study by Zhang and colleagues (2009), and a report by the Vera Institute (Stemen et al., 2006). Each of the reforms was represented by a dummy variable that represented the year the reform went into effect.

There are a few key points about the reforms that should be noted. First, all six reforms represented a shift from the indeterminate-rehabilitation model to a more punitive model with a discretion-limiting sentencing or release structure. Second, presumptive sentencing guidelines, voluntary sentencing guidelines, and statutory presumptive sentencing are considered mutually exclusive front-end reforms and may not, at any given time, coexist with either each other or indeterminate sentencing. Third, the back-end reforms limiting or eliminating discretionary release (truth in sentencing or determinate sentencing) are considered separate because their focus on release allowed operation alongside the front-end reforms. Finally, because three strikes laws work more as a sentencing enhancement, they are allowed to occur alongside both the front-end and back-end reforms (Frase, 2005; Stemen et al., 2006).

The complexity of state sentencing reforms provided a challenge in assessing their impact. These six reforms rarely operated alone, and when they did operate alone it was not for long, as states most often adopted another reform soon after. For example, nine of the 10 presumptive sentencing guideline states adopted at least two other reforms, and all 10 have adopted truth in sentencing laws. Six of the 11 voluntary guideline states adopted determinate sentencing, which was ultimately adopted in 18 states. It is further complicated by the fact that when states did adopt different reforms, they most often instituted them in different years (see Table 1). For example, Pennsylvania adopted presumptive sentencing guidelines in 1982, truth in sentencing in 1991, and then adopted three strikes in 1995. In all there are 27 distinct combinations of reforms. The variability in the timing of reform adoption within states, as well as the sheer number of combinations in which they can exist, makes analysis difficult, but not impossible. It does suggest that a flexible and dynamic model is most appropriate, even if this means the model must sacrifice parsimony. To account for this complexity, the analysis incorporated first-order interactions between all of the reforms in some of the models.

Control Variables

The control variables were organized into three areas of influence. The groupings and the descriptive statistics for the 11 control variables are presented in Table 3. Two crime variables, one for arrests for violent crimes 4 and one for arrests for drug crimes, comprised the first area of influence. The arrest data was acquired through the FBI’s publically available Uniform Crime Report (UCR) Age, Sex, and Race files (1972– 2008). The variables were then transformed into state-specific rates using census data (1970a, 1970b–2008) (both centennially census data and intra-census interpolations as

4 Violent crime arrests represent UCR indexed crimes and include the offenses of murder, forcible rape, robbery, and aggravated assault.

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supplied by the Bureau of the Census) and then further transformed into a percent change score (ΔX=((Xit/Xit−1)−1)*100) to avoid any issues due to trends in arrests. The crime variables represented a theory that arrests had a direct effect, meaning that states with more crime had larger increases in prison admissions. This dictates that the crime variables be lagged, as changes in arrest rates were not likely to have an instant effect. Those arrested will undoubtedly take time to be processed through the system. Non-lagged crime variables would suggest a simultaneous effect. While possible – for example, if higher crime created social pressure to Bdo something about it^ – it was less likely (DeFina & Arvanites, 2002).

The second grouping of controls contained five social and economic variables including percent Black, percent Hispanic, unemployment rate, poverty rate, and percent urban. The U.S. Census (1970a, 1970b) 5 supplied data for percent Black, percent Hispanic, and percent urban. The census data was also used to construct all rate variables. This census data included both 10-year census figures and population estimates calculated by the Census Bureau. Percent Black and Hispanic were simply the percent of the population in a state that is Black and Hispanic respectively. Percent urban is the percentage of the states population that lives in an urban area (urban was defined by the census). Percent urban, percent Black, and percent Hispanic did not change considerably over time (though they vary considerably from state-to-state); high percent states remained relatively high while low percent states remained relatively low. Because of the stability of these variables, the variables were not transformed. The U.S. Bureau of Labor Statistics (1972) and U.S. Bureau of the Census (2008) supplied the last two demographic variables: percent unemployed (unemployment rate) and percent of the population under the poverty line (percent poor). These variables were also not transformed, as they also did not trend substantially over time.

5 Data from the census was compiled from both census data and population estimates.

Table 3 Descriptive statistics of the control variables

Mean St. Dev. 25th percentile 75th percentile

Crime & Justice

Violent Crime* 3.11 27.15 −4.60 7.53 Drug Crime* 23.50 28.20 −2.33 20.45

Social & Economic

Percent Black 10.54 8.91 3.44 15.19

Percent Hispanic 6.24 8.38 1.29 7.33

Unemployment Rate 5.59 2.15 4.20 6.80

Poverty Rate 12.75 3.96 9.80 15.10

Percent Urban 6.32 42.99 −17.29 22.87 Political

Republican State House −0.76 2.46 −3.01 1.97 Republican Governor** – – – –

* Percent Change

** Indicates a dummy variable

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Finally, the analysis incorporates two measures of partisan political affiliation that represent the third area of control variable influence. Republican governorship was measured through a simple dummy code supplied by Hershey (2007). The influence of partisan politics in the state legislatures was measured through a relatively new technique developed by Harmon (2011, 2013) with data supplied by Dubin (2007). In this measure, positive scores represent Republican control, while negative scores represent Democratic control. The measure also takes into account the diminishing returns of increased party concentration. Some research has indicated that while both parties were supportive of the law and order movement, Republicans may have been more stalwart in their support (Helms & Jacobs, 2002; Jacobs & Carmichael, 2001).

Statistical Modeling

The panel (time-series cross-section) regression technique employed utilized robust standard errors. While robust standard errors help correct for some of the potential issues in panel models, it does not solve all issues associated with the complicated analysis (Hsiao, 2003). One of the key considerations is the possibility that the models suffer from Omitted Variable Bias. This occurs when state-level variables that were not included in the analysis and are stable over time and/or time variant variables that do not vary across states are correlated with the error term of the dependent variable. Omitted variable bias can make point estimates inconsistent, leading to biased coeffi- cients. Therefore, to properly specify the model, Omitted Variable Bias must either not be present in the random effects model (Y=β0+β1X1it…βnit+υi+ςi+εit)

6 or it must be corrected for by incorporating fixed effects (Halaby, 2004; Murtazashvili & Wooldridge, 2008).

A Hausman Test (x2=56.31,p<.001) comparing a full fixed-effects model (which controls for both time-specific and unit-specific omitted variable bias) to a random- effects model (which does not correct for omitted variable bias) suggested that Omitted Variable Bias was affecting the consistency of the new commitment model. A second Hausman Test (x2=44.13,p<.05) of parolees returned to prison also suggested Omitted Variable Bias was present in the full model. Therefore, in the analysis of both variables, a full fixed-effects model was utilized: Y=β0+β1X1it…βnit+i1…in−1+t1…tn−1+εit. This model controls for any omitted variable bias present by incorporating dummy codes for both units (i1…in−1) and time (t1…tn−1), which Bwashes-out^ υi and ςt, the unit-specific error and the time-specific error respectively (which are biasing the results) of the random effects model, making the coefficients unbiased.

Change scores (as percent or in other forms), such as the dependent variables in this analysis, are not without their limitations. Biased results can occur if the impact of the explanatory variables is related to the initial values of the dependent variables. Incorporating an unchanged and lagged (one-year) term of the dependent variables as a control variable can correct this specification problem. A model of this type is often referred to as the static-score or conditional change-score model and Bframes the analysis in the following fashion: do the independent X variables [both X or ΔX]

6 Where υi is the unobserved time-invariant variation, is the unobserved case-invariant variation and εit is the idiosyncratic error term. εit is assumed to be uncorrelated with X1it…Xnit and with υi and where υi and are not correlated with X1it…Xnit.

Am J Crim Just (2016) 41:296–320 307

influence changes in Y (e.g., ΔY ) for fixed levels of Yt-1, that is, taking into account the negative effect of initial values of Y (represented by βn+1Yit−1) on subsequent change^ (Finkel, 1995, p. 9).

One of the main advantages of the conditional change score model is that it accounts for differences in overall imprisonment from state to state. For example, Louisiana has the highest imprisonment rates in 2008 at 867 inmates per 100,000, while Maine had the lowest at 148. In the unconditional change-score model (no lagged dependent variable in the equation) a 10 inmate per 100,000 increase in Louisiana is treated the same as a 10 inmate increase in Maine. This would not accurately represent the relative impact in each state, as a 10-inmate increase in Louisiana is a 1.1 % increase, while a 10 inmates in Maine accounts for a 6.8 % increase. The conditional change-score model accounts for these base differences in imprisonment. This means that states with high overall rates of imprisonment will not get less impact than states with low initial imprisonment. The structure of the final model, ΔY=β0+β1itX1it…βnit+βn+1Yit−1+i1 …in−1+t1…tn−1+εit , likely supplied consistent and efficient point estimates that are statistically robust and substantively meaningful.

Results

Table 4 presents the results for both the effects of reforms on new commit- ments to prison and parolees returned to prison. A total of four models are presented with Models 1 and 2 assessing new commits and Models 3 and 4 assessing parolees. Models 1 and 3 include only the six reform and the control variables. These models assume that the effects of the reforms are independent of each other and that no interactions are present. Models 2 and 4 include first order interactions for all of the reforms. Keeping with convention, non- significant interaction coefficients were left in the models because significant interactions were expected (Jaccard & Turrisi, 2003).

New Commitments to Prison

Model 1 of Table 4 indicates that only two of the reforms (statutory presumptive sentencing and truth in sentencing) are statistically significant. Both of these reforms resulted in a yearly increase in prison growth over indeterminate sentencing. The effect for statutory presumptive sentencing is moderately large, indicating that these states have 15.2 % growth in new commitments per year. While at first glance it seems that these two reforms increased new commitments, care should be taken when interpreting these results. First, rarely did a state pass only truth in sentencing laws or statutory presumptive sentencing. In fact, in the 24 states that have passed a truth in sentencing law, only three states – Iowa, New York, and South Dakota – passed truth in sentencing without any other reforms. Similarly, of the eight states that have adopted statutory presumptive sentencing, only Alaska did not subsequently pass an additional reform. Second, as Model 2 of Table 4 indicates, the reforms had a high level of interaction. The different combinations had exceedingly different effects. This suggested that the effects of the reforms should not be treated as being independent from each other, making the interpretation of coefficients in Model 1 tenuous and likely inappropriate.

308 Am J Crim Just (2016) 41:296–320

T ab

le 4

T he

ef fe ct s of

se nt en ci ng

re fo rm

s on

pe rc en t ch an ge

in pr is on

ad m is si on s o ve r ti m e: 19 7 2 – 2 00 7

N ew

A dm

it s

P ar ol ee s R et ur ne d

M od el 1

S E

M o de l 2

S E

M od el 3

S E

M od el 4

S E

S en te n ci n g R ef or m s

P re s. S en t. G ui de li ne s

−2 .1 4

(7 .2 2)

7. 93 *

(3 .8 4)

−2 .3 3

(5 .6 6 )

1. 04

(4 .7 6 )

V ol un ta ry

S en t. G u id el in es

4 .5 9

(5 .1 4)

6. 61

(6 .2 7)

−3 .5 1

(3 .8 6 )

−2 .8 9

(4 .2 2 )

S ta tu to ry

P re su m pt iv e S en t.

15 .1 6 **

(4 .9 4)

19 .3 2* *

(5 .5 6)

4. 39

(4 .6 5 )

4. 73

(5 .6 9 )

D et er m in at e S en te nc in g

3 .9 6

(3 .7 3)

14 .0 1* *

(4 .0 5)

−0 .3 4

(2 .7 0 )

−0 .0 6

(3 .3 5 )

T ru th

in S en te nc in g .

7 .9 6 *

(3 .5 7)

16 .6 7* *

(4 .8 8)

3. 62

(3 .8 8 )

6. 63

(4 .8 8 )

T hr ee

S tr ik es

6 .6 9

(3 .7 5)

16 .2 8*

(6 .9 7)

3. 61

(3 .5 9 )

7. 42

(5 .1 7 )

In te ra ct io n T er m s

P re s. G ui de

* D et er m . S en t.

– –

−2 8. 16 *

(1 2. 41 )

– –

−1 1. 63

(1 1 .5 1 )

P re s. G ui de

* T ru th

in S en t.

– –

4. 19

(9 .9 0)

– –

5. 37

(9 .0 9 )

P re s. G ui de

* T hr ee

S tr ik es

– –

−3 .6 4*

(1 .7 8)

– –

−4 .2 4

(1 0. 6 5)

V ol . G ui de

* D et er m . S en t.

– –

7. 53

(9 .0 9)

– –

19 .8 0* *

(6 .3 1 )

V ol . G ui de

* T ru th

in S en t.

– –

−9 .3 9

(9 .8 3)

– –

−9 .4 9

(6 .5 5 )

V ol . G ui de

* T hr ee

S tr ik es

– –

−8 .7 4

(8 .3 7)

– –

−7 .5 3

(6 .0 8 )

S ta t. P re s. * D et er m . S en t.

– –

−1 5. 42 *

(6 .6 5)

– –

0. 35

(5 .9 3 )

S ta t. P re s. * T ru th

in S en t.

– –

−1 2. 73 *

(5 .7 9)

– –

−1 0. 62

(8 .5 5 )

S ta t. P re s. * T hr ee

S tr ik es

– –

−6 .2 1

(8 .8 6)

– –

−1 .4 2

(8 .0 9 )

D et . S en t. * T ru th

in S en t.

– –

−9 .1 3*

(4 .5 4)

– –

−2 .4 5

(8 .2 1 )

D et . S en t. * T h re e S tr ik es

– –

−4 .4 4

(6 .5 9)

– –

−3 .8 3

(6 .5 7 )

T ru th

* T hr ee

S tr ik es

– –

−9 .5 4

(8 .3 5)

– –

−1 .0 6

(6 .1 4 )

Am J Crim Just (2016) 41:296–320 309

T ab

le 4

(c on ti nu ed )

N ew

A dm

it s

P ar ol ee s R et ur ne d

M od el 1

S E

M o de l 2

S E

M od el 3

S E

M od el 4

S E

C ri m e C on

tr ol s

V io le nt

C ri m e A rr es ts

0 .0 0 16

(0 .0 09 4)

0. 00 1 5

(0 .0 10 )

0. 00 6 4

(0 .0 0 97 )

0. 00 5 9

(0 .0 1 0)

D ru g C ri m e A rr es ts

0 .0 0 50 * *

(0 .0 01 6)

0. 00 5 7* *

(0 .0 01 )

0. 00 2 9*

(0 .0 0 14 )

0. 00 2 8*

(0 .0 0 14 )

D em

o gr ap hi c C on tr ol s

P er ce n t B la ck

0 .8 2 *

(0 .3 3)

0. 82 * *

(0 .2 9)

0. 54 *

(0 .2 3 )

0. 57 *

(0 .2 3 )

P er ce n t H is pa ni c

1 .3 4 *

(0 .5 4)

1. 71 * *

(0 .5 7)

−0 .5 3

(0 .3 2 )

−0 .4 8

(0 .2 9 )

P er ce n t U ne m p lo y m en t

−0 .9 5

(0 .4 9)

−0 .8 6

(0 .4 9)

−0 .9 2*

(0 .4 5 )

−0 .9 1*

(0 .4 5 )

P er ce n t P oo r

−0 .9 4 *

(0 .4 1)

−0 .7 5

(0 .4 0)

−0 .2 2

(0 .3 1 )

−0 .2 0

(0 .2 9 )

P er ce n t U rb an

0 .0 8

(0 .0 5)

0. 07

(0 .0 5)

0. 11 *

(0 .0 5 )

0. 10 *

(0 .0 5 )

P ol it ic al C on tr ol s

R ep u bl ic an

S ta te H o us e

3 .3 5 **

(1 .1 3)

3. 14 *

(1 .1 8)

2. 50 *

(1 .0 2 )

2. 12 *

(1 .0 1 )

R ep u bl ic an

G ov er no r

1 .2 2

(2 .8 7)

0. 25

(3 .0 6)

−1 .3 7

(2 .4 7 )

−1 .2 4

(2 .5 8 )

C o ns ta nt

19 .6 9 **

(5 .8 6)

18 .8 9*

(7 .1 3)

7. 32

(7 .0 0 )

5. 38

(6 .4 7 )

O bs er v at io ns

17 1 0

17 10

1 69 7

1 65 9

R -S q (w

it h F ix ed

E ff ec ts )

0 .3 4

0. 39

0. 17

0. 19

R -S q (w

it ho ut

F ix ed

E ff ec ts )

0 .1 1

0. 14

0. 05

0. 08

S ta nd ar d er ro rs in

pa re nt h es es

** * p < 0. 00 1,

** p < 0 .0 1 , * p < 0 .0 5

310 Am J Crim Just (2016) 41:296–320

Model 2 of Table 4 adds in first-order interaction terms for the reforms. Because interaction effects can be arduous to interpret in regression analysis, Table 5 was constructed to ease interpretation. The coefficients in Table 5 (and Table 6) were calculated using Stata’s margins command. The margins command produces coeffi- cients estimating the combined effects of the interaction terms and their main effect by taking the numerical derivative of the mean expected value of the specific combination of sentencing reforms (∂y/∂x=bj+b12Xki). The effects were calculated while holding the control variables at their means (other reforms not included in the calculation were set to 0 and the dummy variable for Republican governor was set to 1). Thus, Table 5 represents the average effect of the specific combination being considered for the average state with a Republican governor. The margins command also calculates standard errors of the estimated marginal effects and tests if the effect is significantly larger than zero. The significance of the coefficients does not indicate if the effect was significantly larger than non-reform states or other reform states per se, but it does indicate if the combination is significantly impacting year-to-year changes in impris- onment. The calculated effects can also be compared to the average yearly change of indeterminate sentencing (non-reform states), which is 6.6 %.

As Model 2 highlights the interaction terms can have a significant effect. In most cases the interaction term was negative. This means the interaction term served as a moderating effect. This can be understood as indicating that when the reforms are interacting the impact is not a simple additive effect. To illustrate consider the impact of both presumptive sentencing guidelines and three strikes. The independent main effect of the each reform is 7.9 and 16.3 respectively. If the reforms were treated as being additive (as opposed to interactive) in a non-interactive way the combined impact would be 24.2 (24 % higher prison admissions in those states). Because the interaction term between presumptive sentencing guidelines and truth in sentencing is −3.6 the additive effect of 24.2 is an overestimation. The impact including the interaction term is only 20.6, suggesting these two reforms resulted in about a 20 % increase in prison admissions. By using the margins command in Table 5, the combined effects of the reforms accounted for while also holding the control variables at their means. This means the impact of the coefficients in Table 5 can be interpreted to mean the impact of the reforms, singular and in combination for the Baverage^ state (which accounts for the difference between 20.6 calculated above and the 17.2 calculated in Table 5).

It should be noted that the interpretation of any one coefficient in Table 5 (and in Table 6) should be done with care. In many cases only a handful of states at any given time had the specific combination of reforms represented by the coefficient. The dynamic nature of the full interaction model allows the analysis to leverage every time a specific reform was present in a state for any given year and in any combination. This allows the model to be more efficient and generate significant results even when a specific combination of reforms occurred in relatively few states (Jaccard & Turrisi, 2003). It is best to consider the overall trends than to interpret any one coefficient. Additionally, because they are average effects, it is important not to apply the findings to any one state that may have that combination.

The results did indicate that in the majority of the cases, reforms (both singularly or in combination) significantly increased changes in new commitments to prison. Of the 32 coefficients calculated in Table 5, 27 were significant with 26 increasing new commitments more. In the majority of the cases the effects were at least 50 % higher

Am J Crim Just (2016) 41:296–320 311

T ab

le 5

E st im

at ed

ag gr eg at e pe rc en t ch an ge

in ne w

co m m it m en ts to

p ri so n

D et er m in at e

S en te nc in g

T ru th

in S en te n ci n g

T h re e

S tr ik es

D et er m in at e S en te nc in g

& tr ut h in

se nt en ci ng

T ru th

in S en te n ci n g &

T hr ee

S tr ik es

D et er m in at e S en te n ci ng

& T h re e S tr ik es

T ru th

in S en t. , D et er m in at e

S en t. , &

T h re e S tr ik es

P re su m . S en t. G ui d e.

4. 60 *

−9 .5 5

25 .4 5 *

1 7. 2 3*

11 .3 0

38 .0 9 ** *

3. 0 8

23 .9 3*

(2 .4 6 )

(9 .4 0)

(1 2. 1 6)

(8 .5 6)

(9 .8 5)

(9 .9 1)

(1 4. 4 8)

(1 0 .3 1 )

V ol un ta ry

S en t. G u id e.

2. 79

24 .3 3* *

10 .0 6

1 0. 3 3*

3 1. 6 0* * *

17 .6 0 *

31 .8 7* **

39 .1 4* * *

(6 .3 2 )

(9 .2 1)

(7 .8 4 )

(5 .1 3)

(8 .2 1)

(8 .9 1)

(7 .3 4 )

(8 .5 7)

S ta tu to ry

P re su m p.

S en t.

16 .4 2 **

15 .0 1* **

20 .3 6 *

2 6. 5 0* * *

1 8. 9 5*

30 .4 4 **

25 .0 8* **

29 .0 3* *

(5 .5 0 )

(4 .2 1)

(1 0. 1 0)

(6 .8 2)

(8 .7 2)

(9 .6 2)

(7 .2 8 )

(8 .8 7)

D et er m in at e S en te nc in g

11 .7 8* *

19 .3 1 **

2 3. 6 2*

21 .6 2 **

(4 .4 4 )

(6 .6 0 )

(9 .4 5)

(7 .3 2)

T ru th

in S en te nc in g

14 .4 4 **

2 1. 1 8*

(4 .6 9 )

(9 .7 7)

T hr ee

S tr ik es

14 .0 5*

(6 .3 9 )

In d et er m in at e S en t.

6. 61 * **

(1 .0 1 )

T h e co ef fi ci en ts re pr es en t th e av er ag e p er ce n t ch an g e o v er

ti m e fo r n ew

co m m it m en t ra te p er

10 0, 00 0 st at e po pu la ti on s co nt ro ll in g fo r th e va ri ab le s pr es en te d in

M od el 2 o f T ab le 3 .

S ta nd ar d er ro r in

pa re nt he se s. ** * p < 0. 0 01 , **

p < 0 .0 1 , * p < 0 .0 5 . P re di ct ed

sc or es

an d st an da rd

er ro rs w er e ca lc u la te d us in g S T A T A ’s m ar gi n s co m m an d

312 Am J Crim Just (2016) 41:296–320

T ab

le 6

E st im

at ed

ag gr eg at e pe rc en t ch an ge

in pa ro le es

re tu rn ed

to pr is on

D et er m in at e

S en te n ci n g

T ru th

in S en te nc in g

T hr ee

S tr ik es

D et er m in at e S en te nc in g

& T ru th

in S en te nc in g

T ru th

in S en te nc in g

& T hr ee

S tr ik es

D et er m in at e

S en te nc in g

& T h re e S tr ik es

T ru th

in S en t. ,

D et er m in at e S en t. ,

an d T hr ee

S tr ik es

P re su m pt iv e S en t. G ui de .

8. 18

−2 2 .3 2

2 9. 0 4

20 .4 1

−1 .4 6

26 .2 1*

−5 .1 5

1 5. 7 0

(5 .4 7)

(2 2. 38 )

(3 8 .1 7)

(3 8 .7 0 )

(2 2. 46 )

(1 2. 5 9)

(4 5. 0 8)

(1 8 .5 2 )

V ol un ta ry

S en t. G u id e.

2 6. 8 0* * *

9. 73

2 3. 8 4*

22 .4 3* *

6. 77

19 .4 7

5. 3 5

2 .4 0

(6 .8 8)

(1 0. 21 )

(9 .2 9)

(6 .8 6)

(1 2. 73 )

(1 1 .9 8)

(1 0. 0 1)

(1 4 .6 9 )

S ta tu to ry

P re su m p.

S en t.

−3 .6 5

9. 46

−1 7. 0 8

1. 6 6

−3 .9 7

−1 1. 7 6

14 .7 8

1 .3 4

(2 0. 74 )

(9 .7 7)

(3 9 .1 5)

(1 7 .5 7 )

(2 7. 05 )

(3 0. 4 6)

(1 6. 5 4)

(2 0 .6 5 )

D et er m in at e S en te nc in g

2 6. 7 0* *

3 0. 8 0*

29 .7 4*

31 .0 1*

(1 0. 10 )

(1 4 .9 9)

(1 4 .0 5 )

(1 5. 6 2)

T ru th

in S en te nc in g

2 7. 1 7*

12 .0 2

(1 1. 9 2)

(1 1. 78 )

T hr ee

S tr ik es

21 .0 2

(1 0. 85 )

In d et er m in at e S en t.

7 .4 8 ** *

(1 .2 5)

T h e co ef fi ci en ts re pr es en t th e av er ag e pe rc en t ch an g e ov er ti m e in th e ra te o f pa ro le es

re tu rn ed

p er 1 00 ,0 00

co nt ro ll in g fo r th e va ri ab le s pr es en te d in M od el 4 of

T ab le 3 .S

ta nd ar d er ro r

in p ar en th es es . * **

p < 0 .0 0 1,

* * p < 0. 01 , * p < 0. 05 . P re di ct ed

sc or es

an d st an d ar d er ro rs w er e ca lc ul at ed

u si n g S T A T A ’s m ar gi ns

co m m an d

Am J Crim Just (2016) 41:296–320 313

than in non-reform states and in some cases as much as 5 times larger. For example, states with presumptive sentencing guidelines and truth in sentencing laws had yearly changes of just over 25 %. This is almost 4 times higher than non-reform states whose growth was, on average, about 6.6 %.

In the 26 significant cases where growth was higher than non-reform states, the growth was generally 0.5 to 3 times as big when they adopted only one or two reforms. States that adopted two to four reforms generally increased their prison growth in new commitments at higher rates, closer to 2.5 to 5 times larger. Another important observation from Table 5 was the powerful impact of the Bback-end^ reforms. In general, as a state added additional back-end reforms, new commitments tended to grow at higher percentages. While there were a few cases in which adding additional back-end reforms actually lowered the number of new commitments, this was rather limited. Policymakers may want to take note of this important observation. It indicates that if a state already had a front-end reform, adding additional back-end reforms results in anywhere from one-third to doubling the yearly growth in new commitments to prison.

Overall Table 5 indicates that a limited number of the reform combinations resulted in lower changes. For example, in the 15 different combinations (in which 12 were significant) that truth in sentencing laws appears, in only one case (the combination of voluntary sentencing guidelines, truth in sentencing, and three strikes) did it reduce new commitments and this effect was not significant (see Table 5). Overall, in only four cases did the reform combination result in lower growth of new commitments than in non-reform states.

There are a couple of important effects in the control variables of note. First, in both Model 1 and 2 of Table 4 violent crime arrests did not significantly increase the change in new commitments, but drug crime arrests did. It was a relatively small but mean- ingful effect. States at the 75th percentile of percent change in drug arrests sent about 1.8 % more new commitments to prison. States at the 25th percentile sent about 1 % fewer new commitments to prison. This finding was not unexpected given the effect the war on drugs had and continues to have on imprisonment in the U.S. (Engen & Steen, 2000). Of the remaining control variables, both percent Black and percent Hispanic significantly increased new commitments, suggesting that higher percentages of people of color led to higher growth in new commitments. Finally, the analysis suggests that when Republicans controlled a state’s House of Representatives (also called the assembly in some states), the state sent more new commitments to prison.

Parolees Returned to Prison

The analysis of parolees returned to prison produced results in notable contrast to the analysis of new commitments. First, the analysis was less stable. While the percentage of new commitments generally trended up over the period observed, percent change in parolees returned was much less consistent and often switched between positive and negative percent change in conjoining years. This may help explain why the models explain half as much variation as the new commitment models (r-squared of .19 compared to .39).

The results of the full interaction model (Model 4 in Table 4) indicated very few significant results. Only one interaction term was significant. Given this lack of

314 Am J Crim Just (2016) 41:296–320

significant results, it is not surprising that Table 6 (which presents coefficients in the same way that Table 5 does for new commitments) produced fewer significant coeffi- cients. Only nine of the 32 combinations were significant. In most of the cases when a combination was significant, either truth in sentencing or three strikes was present. In some ways this finding is expected; the back-end reforms focus more heavily on parole than the front-end reforms. This is certainly true of determinate sentencing and truth in sentencing laws, which tremendously changed discretionary parole decisions. It is important to note that it is extremely rare to find only these back-end combinations; thus, support for the hypotheses is only found in those rare cases. In fact, for the entirety of the period observed, in only two states do back-end reforms exist without other reforms. When the rarity of the events are considered, the analysis essentially found no substantial evidence that reforms increased the rate of parolees returned to prison over non-reform states.

Finally, the analysis suggested that drug arrests significantly affected parolees returned to prison. The significant positive impact of drug crimes again suggests that the war on drugs played a role in sending more people to prison, with similar effects on both parolees and new commitments. Additionally, percent Black was significant while percent Hispanic was not. This is in contrast to the new commitment analysis, which showed a significant effect of both percent Black and percent Hispanic. Percent urban increased parolees returned while percent unemployment led to lower rates of returned parolees. Finally, the results again indicate that Republican control of the state house resulted in significantly larger parolees returned to prison.

Discussion

Much of the prior discussion in the literature has focused on the impact of reforms on imprisonment in general, with some research suggesting they are associated to in- creased imprisonment (e.g. Harmon, 2013; Stemen et al., 2006), while others have shown no effect or a decrease (e.g. Marvell, 1995; Nicholson-Crotty, 2004; Zhang et al., 2009). Few studies specifically separated out the effects on time served versus commitments to prison. Savelsberg (1992) noted that imprisonment rates are made-up of three distinct components: those who are entering prison, plus those who were already there, minus those who have left. The previous research on sentencing reforms has almost exclusively focused on total imprisonment rates, which does not distinguish whether reforms impacted those already in prison (time served) versus those entering prison (commitments) versus those who exited (either paroled or unconditionally released). The analysis presented here helps to disentangle the specific impact of sentencing reforms by focusing on the understudied area of the impact of sentencing reforms on commitments to prison. Future research should continue to disentangle the loci of impact, especially focusing on time-served.

The analysis of this study lends some credence to their assertion that states with certain combinations of sentencing reforms are sending more inmates to prison for minor crimes that would have otherwise resulted in a jail sentence and/or more inmates are getting prison sentences instead of probation. The analysis cannot distinguish between these two loci of effect, but the results do support the general hypothesis that sentencing reforms increased new commitments to prison. On the other hand, the

Am J Crim Just (2016) 41:296–320 315

results do not support the suggested third area where reforms could increase commit- ments to prison-parolees returned.

In respects to the impacts of new commitments to prison, the findings of this study are in contrast to the findings of the other major study (Zhang et al., 2009) that looks at the impacts of sentencing reforms on commitments. It is important to highlight both the differences in model specification and data between the two studies as it may explain the divergent findings. First, Zhang and colleagues’ (2009) study incorporated a hierarchical linear model as opposed to the panel model implemented here. Second, the Zhang and colleagues’ (2009) study ran from 1973 to 1998. The analysis in this study includes 10 additional years of data up through 2008 (as well as one additional year in 1972). Third, and perhaps most importantly, this study includes interaction effects between the reforms that the Zhang and colleagues’ (2009) study did not include. As highlighted in Tables 5 and 6, the interaction effects appear to be highly impactful.

The analysis underscores the importance of considering reforms as operating in combination and not independently of each other within states, as the impacts differ substantially when different combinations are considered. This is evident in the impact of the interaction terms presented in Table 4, but Tables 5 and 6 better illustrates it. Models of the impacts of sentencing reforms without considering their interactive nature are much simpler to interpret, but as the findings highlight treating reforms as independently impacting prison admissions miss-specifies their true effects. For exam- ple, Model 1 allowed us to consider only 6 coefficients for each of the reforms (and not the additional 12 interaction terms) and there is no need for post hoc calculations (as found in Tables 5 and 6). The model suggested that truth in sentencing, independent of other reforms, increased new commits by 8.0 % per year. There are substantive reasons to question this. First, truth in sentencing focus on time served and conceivable should have little to no impact on prison admits. Second, rarely did the reform operate in a state alone further questioning the impact of this reform without considering its interaction with other reforms. Additionally, as the results of Model 2 indicated it is important to not treat reforms as independent. The interaction terms highlight the highly interactive and dynamically changing nature of sentencing reforms working in tandem. When you consider the substantial impact of the interactions between the reforms and the fact that truth in sentencing only operated alone in 3 of the 24 states that adopted the it, it helps to explain why it is significant in Model 1 when intuitively it should not. It is likely that the coefficient for truth in sentencing Bpicked up^ the impacts of the other reforms and thus does not accurately represent the impact of the reform. This further reinforces the conclusion that the results from Model 1 can’t be trusted and that an interaction model is more appropriate.

There are a couple of observations related to the impacts of the reform combinations worthy of further examination. First, the effects of the reforms were quite different in the models without interaction terms compared to the ones with them. For example, Model 1 (new commitments to prison), which did not include interaction terms, only statutory presumptive sentencing and truth in sentencing were significant. In Model 2, which added interaction terms to Model 1, the effects were quite different. First, in the main effects, only voluntary sentencing guidelines were not significant. Second, the interaction terms demonstrated that the combinations of reforms were not purely additive in their relationships. For example, the impact of a state with statutory

316 Am J Crim Just (2016) 41:296–320

presumptive sentencing and truth in sentencing on new commitments is not merely the sum of the two coefficients in Model 1. The analysis shows that reforms are working in tandem and should not be treated as independent of each other when they are both in effect in a state.

Future research may want to see if specific combinations are working to create certain groupings that function as one regime, as opposed to effects interacting together. To illustrate, consider the following hypothetical example. One state adopts sentencing guidelines, truth in sentencing, and three strikes because they follow a specific model of justice (perhaps a Bjust desserts^ model). Another state adopted sentencing guidelines and determinate sentencing, because of concerns of prison growth (perhaps an Badministrative^ model of justice). It then may be possible to distinguish these two Bregime types^ from each other on more substantive grounds than this analysis can. Future research should also focus on simultaneously assessing commitments (new com- mitments and parolees returned) and time served (perhaps prison releases too). Since one of the primary focuses of the law and order movement was on longer prison terms, it is quite possible reforms had a substantial impact on length of sentence, but this analysis is not able to make a definitive conclusion on that matter and further exploration is needed.

Conclusions

When significant, the effects of sentencing reforms on new commitments are strong. The analysis suggests that new commitments increased at a rate of 6.6 % per year in non-reform states (indeterminate sentencing states). Adopting a sentencing reform typically doubled to tripled growth in new commitments. Even at the lowest level of additional growth in new commitments, reforms add 10 to 15 % more inmates a year. In 1 year an additional 10 % might be manageable, but compounded over an extended period the additional inmates could be very difficult to absorb into an already over- crowded system (Irwin & Austin, 1997). For example, when three strikes laws were hastily passed in the 1990s, the U.S. was sending about 600,000 new commitments a year to prison (Schneider, 2006). In a state that already passed statutory presumptive sentencing, three strikes would add an additional 10 % yearly to the number of new commitments to prison. By the mid-2000s, this would result in an additional 815,000 inmates sent to prison above the levels in the early 1990s. If one adds in the adoption of statutory presumptive sentencing, which sent nearly a million new inmates to prison, the combined effects of these two reforms was vast.

The analysis generally suggests that as additional reforms were adopted, states sent even more new commitments to prison. This is an important consideration for policymakers. It suggests that the reforms are directly impacting those who are entering the system. The passage of sentencing reforms may be more likely in states that are generally more punitive. In this scenario, reforms symbolically represented punitive criminal justice attitudes in practice. If a state was generally more punitive, the logic follows that they would be more likely to pass symbolic representations of their punitiveness, but here the analysis suggests that reforms are more than simply symbolic representations as the reforms have a tangible impact.

Overall, the analysis can conclude that sentencing reforms impacted new commit- ments in about 85 % of the combinations of sentencing reforms. The same cannot be

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said for parolees, for whom the effects were limited to back-end combinations that only exist in a handful of cases. It should be noted that no study to date could be located that looked specifically at the impact of sentencing reforms on parolees returned to prison. The analysis of this study does not support the hypothesis that sentencing reforms were sending more parolees back to prison. While the results of Table 6 do indicate that combinations of sentencing reforms that include back-end reforms are affecting parolees returned, these results are in many respects uncon- vincing. As previously noted, only two states have passed sentencing reforms where the significant combinations are observed. The general lack of significant effects on the front-end and the limited effects on the back-end allow us to conclude that the effects of sentencing reforms on parolees are generally not present, and thus not substantively meaningful. This finding is a little surprising because the rhetoric of the law and order movement has included considerable focus on repeat offenders and often accused states of having ineffective parole systems (Gottschalk, 2006; Simon, 2007).

While the analysis does not support the hypothesis that reforms increased parolees returned to prison, it does suggests that some combinations of reforms are sending more new commitments to prison. This is the central finding of this investigation. The results indicate that some sentencing reforms significantly impacted changes in new commitments over time, indicating they led to larger aggregate changes under most conditions. For example, as highlighted in Table 5, the presence of statutory presumptive sentencing, truth in sentencing, or three strikes, though not without exception, tended to increase the change more. It is important to note that the significant and largely higher growth in new commitments to prison was observed while controlling for arrests for violent and drug crimes. This means that the higher rates of new commitments in reform states cannot be explained simply by higher arrests rates. The impact of sentencing reforms is especially notable given the inclusion of drug arrests. While research has shown that drug arrests and convictions played the largest role in rising imprisonment across the U.S. over the last 40 years, reforms are again increasing new commitments to prison above and beyond the effects of crime, even drug arrests.

Because the analysis suggests that there was indeed an increase in new commitments, it raises a number of important questions surrounding these policies. As we move further and further away from the height of the law and order movement, it is important to ask if these reforms were good policy. The costs of incarceration continues to climb and prison beds are currently in extreme shortage in a number of states (Clear & Frost, 2009; Shane-DuBow, 1998). The overall costs of imprisonment growth to individual states can be high. While variation from state to state exists, the average cost per inmate across all states in 2008 was $30,600. The costs are even higher when capital costs of building new jails and prisons are added to the equation (Boerner & Lieb, 2001). Additionally, increased imprisonment places resource pressures on public defenders and the courts. Rapid increases in prison populations can be devastating to a system that is often slow to respond (Kruttschnitt, 2005). With falling state revenues it may be time to consider alternatives that are more cost effective and more just.

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Mark G. Harmon is an Assistant Professor in the Division of Criminology and Criminal Justice in the Hatfield School of Government at Portland State University. He studies the interconnection between race, politics, and the criminal justice system. His recent research has focused on the effects of state-level sentencing reforms on various components of sentencing including the impacts on people of color. Dr. Harmon has also worked on developing more robust quantitative methods in criminal justice research.

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