Allocating Resources Among Prisons and Preschool: An Analysis of the New Evidence

Abstract

Twenty-five years ago, we argued that it would be possible to reduce incarceration and use the resultant savings for investments in preschool education, which would further lower the crime rate. In this article, we revisit that line of thinking, surveying recent literature on the cost and efficacy of prisons and preschool education for crime reduction. We find that the new evidence strengthens our earlier conclusion about the feasibility of this thought experiment. The costs (in real dollars) of prison are higher than 25 years ago, and prisons are slightly less effective at reducing or preventing crime. In addition, the evidence shows broader and stronger effects of preschool on crime and in programs operating at a much larger scale than the programs we previously evaluated.

Keywords

crime prevention early childhood education preschool Head Start social costs of incarceration elasticity of incarceration public policy

The aggregate social costs of crime victimization are enormous, and every affluent society expends considerable resources to reduce these costs. More than 25 years ago, we conducted a broad investigation into the substantial growth of incarceration in the United States, accounting for its costs and also its effectiveness at reducing crime. As a part of that project, we posed a thought experiment: Could the U.S. be more effective at reducing crime not by increasing incarceration, but rather by directing resources otherwise earmarked for prisons toward preschool enrichment programs? At the time, evidence from small pilot programs in preschool enrichment had shown that they could generate substantial decreases in crime (Donohue and Siegelman 1998). Our evaluation of the costs and benefits of both prisons and preschool led to the conclusion that, under specified assumptions, preschool programs could be as effective in stopping crime as further substantial increases in incarceration.

Since that article was published, additional research has clarified elements of the costs and benefits of both potential options. In this article, we revisit our 25-year-old thought experiment. First, we summarize relevant new findings on the costs of incarceration and on the elasticity of crime with respect to incarceration. We go on to examine the latest evidence on the cost and crime-reducing efficacy of preschool programs. We conclude that the evidence from our earlier work is, if anything, stronger today: Prisons carry more social costs and are less effective at crime reduction than we had estimated in 1998, and existing preschool programs that are far larger than the early pilot projects that we previously examined appear to generate substantial crime-reduction benefits.

The Costs of Incarceration

In the 1990s, we estimated the annual per-inmate cost of incarceration to be $65,100 (Donohue and Siegelman 1998). Donohue (2009) later offered a wider range of about $33,500 to $102,400 (all in 2020 dollars), which reflects the substantial uncertainty about the various factors that contribute to the overall costs to society. Several recent studies have explored these factors, especially those regarding the indirect social costs of incarceration. A large body of economic literature now details the impacts—both negative and sometimes positive—of incarceration on labor market outcomes, recidivism, children’s well-being, and some broader social impacts.

Table 1 summarizes three sets of estimates of these costs (all expressed in 2020 dollars), from our initial 1998 paper, the second article by Donohue in 2009, and our current best estimate of the annual per-inmate cost of incarceration. Our current estimate ranges from $57,500 (somewhat below our earlier estimates) to $110,400; the median value of $83,950 yields a substantially higher cost of incarceration than what we found in the two earlier studies (and roughly 29 percent higher than our initial paper in 1998). The rest of this section spells out the details of these estimates.

Table 1

Annual Costs of Incarceration per Inmate (2020 Dollars)

	New Update	Donohue and Siegelman (1998)	Donohue (2009)
Operational costs	$38,500	Not decomposed	$33,500
Capital costs	$0 to $3,900	Not decomposed	$0 to $3,900 (depending on current prison capacity)
Direct lost productivity	$9,000 to $28,000	Not decomposed	$0 to $32,500
Other indirect social costs	$10,000 to $40,000	Not addressed	$0 to $32,500
Total annual cost per inmate	$57,500 to $110,400 Mean value: $83,950 (but only $82,000 saved if reducing incarceration below prison capacity)	$65,100	$33,500 to $102,400 Mean value: $67,950

Operational and capital costs of prisons

Prison expenditures are compiled by the Bureau of Justice Statistics, which include staff wages, inmates’ medical care, food, utilities, the cost of building new correctional facilities, and other costs of running prisons. In 2017, the total corrections expenditures at all governmental levels were about $89 billion, of which $51 billion were at the state level, $30 billion at the local level, and $8 billion at the federal level—a 42 percent real increase from their 1997 level (Buehler 2021).

States incarcerated about 1.3 million prisoners in 2017 (Bronson and Carson 2019). Matching that figure to expenditures, the operational cost per state inmate per year was about $38,500 (in 2020 dollars). That figure is consistent with the federal level of $40,000 per year per inmate.

Using the direct cost per bed of a prison construction project in Connecticut and assuming a prison lifetime of 40 years, Donohue (2009) estimated the capital costs of building new prisons and renovating current ones at $3,900 per inmate. That estimate is likely an overestimate since a more recent prison construction project in Colorado generates a capital cost per inmate of only $2,256.¹ That said, if a state were to expand prison capacity, it would necessarily incur this cost, but if it reduces the level of incarceration below capacity, it would not save this per-inmate capital expense.

Social costs of incarceration

Absent incarceration, many inmates would be working in the legitimate economy, so the decline in their productive activities imposes a social burden (Donohue 2009). Several recent studies have tried to estimate other impacts of incarceration on inmates and their families, both during and after the period of incarceration.² Being incarcerated may impair subsequent employment prospects and increase the likelihood of recidivism, thus generating further lost productivity and increasing future crime-associated costs. Incarceration may also impact inmates’ families in potentially conflicting ways.³ We rely on this new research to improve on the previous estimates of Donohue and Siegelman (1998) and Donohue (2009).

Lost productivity during incarceration

Lost productivity during the period of incarceration is an immediate and direct cost (Donohue 2009). We generate a wage rate that an average inmate would have earned if not incarcerated, noting that the average inmate is a 39-year-old male with only 10.6 years of education (for the full profile of prison inmates from the Bureau of Justice Statistics, see Beatty and Snell 2021). Based on this full education profile and U.S. Bureau of Labor Statistics (2022) earnings data, we estimate that, absent incarceration, the average inmate could have earned about $37,000 per year. If we assume that one-fourth of those inmates would have been unemployed if free, the average lost productivity is about $28,000 per year. This figure is somewhat lower than Donohue’s (2009) estimate, which had assumed that the average inmate had a high school diploma.

One might adjust this estimate downward if one found that incarceration enabled the inmate to avoid the disutility of work (a social benefit) as well as other expenses (such as housing, clothing, and so on that become an operational prison cost). Donohue (2009) offers a lower bound estimate of lost productivity at about one-third of the lost wage, about $9,000 in our case. This gives a final bound of $9,000 to $28,000 per inmate per year of lost productivity.

Impaired productivity after release from prison

Released inmates may find that incarceration has negatively impacted their earnings prospects, either because employers may be reluctant to hire them or because the period in prison can diminish human capital. Kling (2006) finds no evidence of a significant effect of incarceration on postrelease labor market outcomes, using a “judge leniency design.”⁴ Mueller-Smith (2015), however, concludes that there is a significant and sizable negative impact of incarceration on postrelease employment.

Mueller-Smith (2015) uses a more comprehensive panel of randomly assigned courtrooms in Harris County, Texas, from 1980 to 2009, estimating that each year of incarceration reduces postrelease employment by 3.6 percentage points, and that individuals with stable precharge employment suffer a 24 percent reemployment drop in the years following their release. The same study shows that past inmates become more likely to request either direct cash welfare or food stamps. Discounting to present values with a 5 percent rate, Mueller-Smith (2015) estimates that a one-year sentence generates about $41,000 to $55,000 (in 2020 dollars) of social costs due to postrelease criminal behavior and economic impact, with the labor market channel taking up the bulk of these costs.

Garin et al. (2025) supports the Mueller-Smith view that incarceration imposes significant employment damage, although the Garin et al. estimate is smaller. Garin et al. (2025) find that inmates suffer a 13 percent drop in cumulative earnings over the five years following their sentence, but they are no longer harmed on this dimension beyond five years. Based on data from North Carolina and Ohio in 1991–2017, Garin et al. (2025) estimate that a one-year sentence decreases cumulative earnings by only $2,914.⁵

Impact of incarceration on recidivism

Incarceration could be damaging in ways that would generate further costs years after release but could also deter future criminal conduct or improve the inmate’s human capital if it aided in overcoming substance abuse or developing beneficial job or life skills. Loeffler and Nagin (2022) conclude from their recent literature review that no consensus points to which of these effects dominate.

The studies using the judge-leniency design find primarily that incarceration and pretrial detention either have no effect on recidivism (Dobbie et al. 2018; Loeffler 2013; Nagin and Snodgrass 2013) or are criminogenic (Gupta et al. 2016; Leslie and Pope 2017; Mueller-Smith 2015). One potential bias in these analyses could arise if past inmates were subject to increased surveillance and punishment, thereby elevating the observed crime behavior relative to total crime behavior and making incarceration appear worse than it is (Harding et al. 2017).

A second strand of the literature uses regression discontinuity designs, exploiting thresholds in judicial scoring systems. These studies tend to find that incarceration has a deterrent effect on recidivism (Hjalmarsson 2009; Rhodes et al. 2018; Rose and Shem-Tov 2021). Loeffler and Nagin (2022) try to reconcile these conflicting results by suggesting that outcomes may be influenced by local rehabilitation policies: Jurisdictions that emphasized rehabilitation policies would generate less recidivism from incarceration, while those without rehabilitation measures generate more harmful consequences. Some conflict appears in these results, but those who find the judge-leniency designs more credible than regression discontinuity studies would lean toward the conclusion that incarceration increases recidivism.

Impact on the families of inmates

Incarceration may impact inmates’ families, who may either suffer or benefit from the imprisonment of a spouse or parent. Mueller-Smith (2015) notes that older inmates experience an elevated risk of divorce during or after their sentence and that younger inmates are less likely to marry during and after their time in prison.

Donohue (2009) speculated that the incarceration of a parent would damage the life path of any children, but two recent studies instead find that the benefits of incarcerating a troubled parent may exceed the costs. Norris et al. (2021) addressed this issue using public Ohio court cases data from 1991 and private juvenile court records from 1995 to 2017. The authors linked this data to birth records in 1972 onward, as well as schooling data, to find the children of defendants and siblings of juvenile defendants. Using a standard judge instrumental variables (IV) design, the authors concluded that parental incarceration reduced the likelihood of children’s incarceration by 4.9 percentage points and improved their adult neighborhood. (At the same time, Norris et al. [2021] found this incarceration had no impact on children’s education and teen parenthood, so the benefits operated through some other channel.) Additional research will probably be necessary before a consensus emerges on whether parental incarceration is damaging or beneficial to the relevant families.

Estimating these social costs of incarceration

Our goal here is to provide a plausible range for the estimated monetary value of these numerous indirect social costs that improves on the Donohue (2009) estimate of $32,500 per year per inmate (in 2020 dollars). This point estimate is within the range given by the lower bound of Garin et al. (2025) and the higher bound of Mueller-Smith (2015). An impressionistic Bayesian updating of Donohue (2009) based on the newer literature might suggest a range of $10,000 to $40,000 of indirect social costs per year per inmate.

Overall cost of an added inmate

Donohue and Siegelman (1998) had estimated the overall marginal cost of locking up an additional inmate at $65,100, while Donohue (2009) provided a range of $33,500 to $102,400 (based on the components indicated in Table 1), with a higher mean value of $67,950. Our latest estimates based on our review of 25 years of additional research show that both the lower and higher bound are now higher, with a range from $57,500 to $110,400 and a mean value of $83,950. Since at this point, the allocational decision presumably involves shrinking the prison population to free up resources, this decline in the number of inmates does not save capital costs, so the saved resources from a marginal reduction in incarceration would be $82,000 (in 2020 dollars). This figure is roughly 26 percent higher than we had estimated in 1998.

The Elasticity of Crime with Respect to Incarceration

Donohue and Siegelman (1998) and Donohue (2009) both extensively discussed the literature estimating the elasticity of crime with respect to incarceration: X/Y, where X is the percent change in crime induced from a Y percent increase in incarceration. The 1998 paper stated: “Our view is that the elasticity probably falls in the range of .15–.20, but it could be as low as .10 or as high as .30” (Donohue and Siegelman 1998, 31). To be clear, this range implies a negative elasticity: As incarceration increases, crime is predicted to fall. A decade later, Donohue (2009, 283) noted the continuing uncertainty surrounding the estimates of this elasticity and concluded, “it is perhaps most likely to be between -0.10 and -0.15, but it is conceivably within the broader interval between -0.05 and -0.40.”

These figures implicitly assumed a constant elasticity of incarceration with respect to crime. For any given estimate, say -0.15, this assumption would imply that increasing incarceration by 100 percent would reduce crime by 15 percent. Since the U.S. over the past 50 years increased its incarceration rate from roughly 100 per 100,000 to 500 per 100,000, we more than doubled our prison population twice over the period. With a constant elasticity of -.15, the first doubling would have reduced crime by about 15 percent and the second doubling by another 15 percent; the final increase in the prison population (from 400 to 500 per 100,000) would only have reduced crime by one-fourth of a 15 percent crime drop (or 3.75 percent).

Even with the assumed constant elasticity, there was an enormous decline in the efficiency of increasing incarceration. The first jump from 100 to 200 per 100,000 cost only half as much as the second doubling from 200 to 400 per 100,000, so the costs of massively increasing incarceration have been large and growing. Indeed, the added increment from 400 to 500 per 100,000 (a 25 percent increase in incarceration) cost as much as the first doubling, which led to a 15 percent crime reduction but only generated a crime reduction of 3.75 percent. Of course, if this elasticity is not constant but rather falls as incarceration rises and impacts increasingly less socially harmful offenders (“diminishing returns”),⁶ then the benefits would fall even faster than in this hypothetical.

Tables A1–A3 in online Appendix A summarize some major estimates over the past 15 years of the elasticity of crime with respect to incarceration for violent crime, homicide, and property crime, respectively. Appendix B discusses a variety of econometric estimates of the elasticity of crime with respect to incarceration based on U.S. data.

Updating Prior Elasticity Estimates for the U.S.

Chalfin and McCrary (2017) summarize a large body of research for the Journal of Economic Literature in concluding that -0.1 to -0.7 is a plausible range for the elasticity of crime with respect to incarceration. Noting that “most recent estimates fall in the low end of that range,” they state that their best guess is an elasticity of -0.2 (Chalfin and McCrary 2017, 26). Kaplan and Chalfin (2019, 172) comment that the elasticity of crime with respect to incarceration is “at most, approximately -0.1 to -0.2.” These two studies, then, are quite comparable to our 1998 elasticity estimates, as well as that of Donohue (2009). We provide more details in online Appendix B, but more recent studies typically, albeit not uniformly, tend to show smaller but still negative elasticities. We estimate the elasticity of crime relevant to movements from today’s level of incarceration is probably in the range from -0.05 to -0.15, which is modestly lower than we estimated previously.

Preschool and Crime Since 1999

Our original paper focused on evaluations of a small number of model preschool interventions, including Perry Preschool (Berrueta-Clement et al. 1984), that linked preschool exposure to subsequent adult criminal behavior. Since 1999, however, dozens of papers have examined the crime-preventing effects of both small-scale model programs and larger-scale programs such as Head Start.⁷

Table 2 summarizes the relevant literature through 2024. Three themes emerge. First, dozens of rigorous evaluations, using a range of techniques that pay careful attention to econometric identification issues, now generally confirm a key conclusion of our 1998 paper that preschool interventions can meaningfully reduce crime. Recent work even finds effects of preschool on the second generation—the children of those who originally attended—including on crime. Not only does the literature suggest the existence of a causal relationship between preschool and subsequent criminality, scholars have made some progress in uncovering the mechanisms by which this effect occurs (see Algan et al. 2022; Baulos et al. 2024; Heckman et al. 2013; Johnson and Jackson 2019).

Table 2

Summary of Studies of Early Childhood Education (ECE) and Crime

Authors	Data & N	Method	Conclusion
Model/Small-Scale ECE Programs (Perry, etc.)
M. Anderson (2008)	Perry Preschool Project and Abecedarian Project	Augmented statistical comparison of treatment and controls in initial randomized controlled trial (RCT), adjusting for multiple hypothesis tests.	Correcting for multiple inferences suggests modest effects of these programs for females and little or no effect for males. At age 27, Perry women’s likelihood of criminal record dropped from 0.35 to 0.20 (43%); lifetime arrests fell from 2.27 to 0.32 (85%). Only the second is significant after statistical corrections. Perry men’s likelihood of criminal record dropped from 0.72 to 0.70 (2.7%); lifetime arrests dropped from 6.1 to 3.8 (38%); neither statistically significant after corrections. At age 21, the Abecedarian program showed large (40–80%) drops for women in convictions, ever jailed, and marijuana use, but none statistically significant after corrections. Men experienced 25–45% drops in convictions, felonies, ever-jailed and marijuana, but none were significant after corrections.
Campbell et al. (2012)	Abecedarian Project: 111 boys and girls in 1972 (101 at age 30)	RCT	Treated and control groups were virtually identical with respect to criminal conviction at age 30: 27% and 29%, respectively.
Heckman et al. (2013)	Perry	RCT	Exposure to preschool program had significant effects at age 40, via changes in personality traits, such as increased motivation, socialization, and emotional control (even if no increase in measured IQ).
Heckman et al. (2024)	Perry	Augmented statistical comparison of treatment and controls in initial RCT, adjusting for multiple hypothesis tests.	Statistically significant effects of Perry Preschool on a number of outcomes, including criminal activity for males and females at age 40. For males, nonjuvenile arrests fell 36%, total crime costs by 45%, total criminal charges by 33%, and nonvictimless charges by 52%. Most are statistically significant even after imposing corrections for multiple inferences in small samples with imperfect randomization.
Heckman and Karapakula (2019, online appendix)	Survey of second generation (children) of Perry participants and controls, N of 70–80	Augmented statistical comparison of (children of) treated and control groups in initial RCT.	Children of treated participants have—among other things—lower levels of participation in crime, compared with the children of controls, especially for male participants. While 40% of the children of controls were never suspended from school, addicted, or arrested, that number is 62% for the children of treated subjects, more than 50% higher. The mechanism seems to be improved childhood home environments. Siblings of participants, especially male siblings, also experienced substantial positive effects.
Algan et al. (2022)	250 boys deemed disruptive at age 6 in 1984: 69 treated, 181 in control. Admin. data used at follow-up for criminal record.	RCT	Psychological intervention to improve the social skills and self-control of at-risk kindergarten boys in Montreal in the 1980s. Treated group had higher trust and self-control as adolescents; increased social group membership, education, and reduced criminality as young adults, and increased marriage and employment as adults. No cognitive effects. Crimes at age 24 reduced from 2.15 in control to 1.13 in treated group (47%), but with p of 0.17. [This is ITT because some in both groups refused to participate in study.]
Head Start (HSt)
Family Fixed Effects (FFE) Estimates
Garces et al. (2002)	Panel Study of Income Dynamics (PSID), retrospective information about HSt participation for 554 to 3,200 adults age 18+ in 1995 (mid-60s through mid-70s); crime data are self-reports. Smaller Ns when fixed effects used.	Regressions with controls and maternal fixed effects, so estimates based on sibling differences.	9.5% of those not in HSt report being booked or charged with a crime at age 27. Controlling for maternal fixed effects (Table 2, Col. 4), HSt reduced that fraction by 5.3 ppt, or roughly 56%, though the effect was not statistically significant.
Deming (2009)	3,698 HSt attendees in the 1980s, based on Children of the National Longitudinal Survey of Youth (CNLSY) and self-reported crime.	Regressions with controls and maternal fixed effects.	Small (2 ppt) and insignificant positive effect on crime, but large positive long-run effect on index of social outcomes (which includes crime with negative weight).
Pages et al. (2020)	Replication and extension of Deming (2009), adding 10 additional cohorts.	Regressions with controls and family fixed effects.	Effects range from -5 ppt in some samples to +2.5 ppt in others, but none are statistically significant.
Miller et al. (2023)	PSID & CNLSY. N = 1,247 to 4,258.	Reweighting on observables to correct for the fact that families with fewer children are less likely to have one or more treated and one or more untreated children, which would bias the FFE estimator.	HSt does not have a meaningful effect on the probability of committing a crime. No quantitative estimates provided (but in these data, effects were weak before any correction applied).
Difference-in-Differences (DID) Estimates
Johnson and Jackson (2019)	4,536 individuals born between 1950 and 1976 (followed through 2015 using PSID) who were exposed to different levels of HSt funding when they were 4 years old. Crime data are self-reports.	DID estimates based on differences in long-run outcomes across birth cohorts from the same childhood county that experienced larger increases in HSt spending at age 4 to the differences in outcomes across the same birth cohorts within other childhood counties that experienced smaller increases in spending.	Exogenous changes in post-HSt funding compliment HSt to produce adult effects, so effect of HSt is nonlinear. At average post-HSt spending levels, a $1,000 (25%) increase in HSt spending per poor child lowers incarceration by 2 to 8 ppts. No baseline data provided.
Bailey et al. (2021)	22.48 million children born from 1950 to 1980	DID estimates comparing cohorts who were age eligible when HSt launched (age 5 and younger) to those born in the same county who were age ineligible (6 and older).	Small, insignificant effects of HSt on incarceration after adjusting for pretrends. But “currently incarcerated” is not comparable to other studies that measured “ever arrested” or “ever incarcerated.”
Barr and Gibbs (2022)	Data on HSt availability + HSt grant-writing assistance + CNLSY. N = 1,978. “Crime” is self-report of any engagement with criminal justice system by age 18.	DID specification comparing difference in outcomes between children of women born too early for HSt exposure (before 1961) and children of women born later (1961–1964), across counties receiving and not receiving HSt grant-writing assistance.	Mother’s exposure to HSt reduces child’s criminal engagement (arrest, conviction, or probation) by 12.5 ppts from a baseline of 27% (46%), with range between 6 ppt and 13 ppts. Measurement errors might make this 30–50% smaller. Larger effects for males.
Anders et al. (2023)	Administrative crime data (including county of birth) for convictions 1972–2018, plus HSt and “Smart Start” rollout data by county in N. Carolina. N ≈ 1.5 million.	DID regression based on county-year-cohort exposure to program.	HSt availability (ITT measure) lowers likelihood of serious conviction by age 35 by 1.3 ppts (vs. 4.6% baseline, a 28% drop), but only in high-poverty counties. Smart Start availability lowers likelihood of serious criminal conviction by 0.6 ppts (12%) overall by age 24.*
Regression Discontinuity Estimates
Carneiro and Ginja (2014)	2,833 male children born 1977–1996, followed through 2008. Crime data are self-reports.	Regression discontinuity design, based on income eligibility thresholds that depend on year, state, family size, and family structure. Careful attention to alternative care arrangements and to selective attrition.	For males 16–17, HSt lowers arrest/conviction rate from 0.136 to 0.118 (13%, but not statistically significant with conservative test). For males 20–21, HSt lowers arrest/conviction rate from 0.284 to 0.170 (a drop of 40%, statistically significant). Both are marginal effects, based on ITT estimates.
Gray-Lobe et al. (2023)	Test scores and other outcomes for cohorts of 4-year-olds in Boston’s public preschool program. N = 4,000.	Comparison of students who were randomly lotteried in or out of public preschool in 7 admissions cohorts.	No crime data, but preschool enrollment improves high school disciplinary outcomes by a large and statistically significant 0.17 standard deviations.

Crime reduction is 7× larger than effect on test scores × conditional correlation between test scores and crime.

NOTE: ITT = intent to treat; ppt = percentage point.

Second, while our earlier work was skeptical about the crime-reducing effects of Head Start, subsequent evidence suggests we were too pessimistic. Head Start participation probably does lower the likelihood that participants will ever engage in criminality. Finally, several of the studies directly or indirectly confront a key implementation issue we identified in our original paper: whether program effectiveness is sustainable at larger scale than the model interventions we focused on. The evidence suggests that it is.⁸

Model programs

Overall, Table 2 suggests that small-scale preschool interventions can reduce subsequent criminal behavior. The Perry Preschool experiment is the leading example of an early childhood intervention whose effects have been monitored for a long follow-up period; North Carolina’s Abecedarian program (Ramey et al. 1976) is another.

Depending on how criminality is measured, M. Anderson’s (2008) reevaluation of the Perry data shows the program led to large (40–80 percent) drops in criminality for women, but smaller (3–38 percent) declines for men. But Heckman et al. (2024) find much larger effects, especially for men: Women’s nonjuvenile arrests, total charges, and nonvictimless charges fell by 51–87 percent; men’s fell by 32–51 percent. Moreover, Heckman et al.’s careful correction for multiple hypothesis testing (as well as for imperfect randomization) generated p-values between 0.07 and 0.32 for women and 0.04 to 0.14 for men—statistically significant (or close) at conventional levels.

M. Anderson (2008) also looked at the Abecedarian program, as did Campbell et al. (2012). While M. Anderson (2008, 1492) characterizes the results as showing “no significant reduction in conviction or incarceration rates by age 21,” it seems more accurate to say that the dampening effects were substantial (71 percent for conviction, 42 percent for incarceration for women; 26 percent for conviction, and 45 percent for incarceration for men), but not statistically significant. On the other hand, Campbell et al. (2012) reexamined the Abecedarian data when subjects were 30 years old and concluded that the treated and control groups were “virtually identical” with respect to criminal convictions (27 percent versus 28 percent).

A more recent model program is the Montréal Longitudinal-Experimental Study (Algan et al. 2022). This was a two-year initiative targeting high-risk boys at age six that focused on social skills and self-control training. As with the Perry and earlier Abecedarian studies, the authors find a large (47 percent) drop in crimes at age 24, but the small sample size meant the effect was not statistically significant (p = 0.17). However, the program did have parallel positive effects on other outcomes at age 30, including employment, income, and marriage.

Large-scale interventions: Head Start

Moving from small-scale randomized experiments to large-scale studies using observational data entails some obvious tradeoffs. When participation in the program is not determined randomly, correcting for selection effects becomes crucial (Heckman 2020). Nonetheless, the ability to use larger samples, more recent data, and national-level interventions are obvious advantages for policy analysis. We discuss studies by method.

Family fixed effects

Selection problems are an obvious concern in evaluating any program based on observational data. Looking at raw data, one study found that 11 percent of children enrolled in Head Start were charged with a crime by age 27 versus 9.5 percent for those not enrolled in the program, making it appear as though participation increased criminality (Garces et al. 2002). Given that Head Start targeted families whose children would be at high risk for future criminality even if they did not participate in the program, this result is unsurprising; controlling for observable variables such as family income eliminated Head Start’s “crime-enhancing” effect (Garces et al. 2002).

But since participation in Head Start was voluntary, one concern is that because families who chose to enroll in the program might have placed a greater emphasis on human capital accumulation, it might look as though the program were responsible for effects that should properly be attributed to family background. That is, there may be unobservable cross-family differences that bias the comparison between participants and nonparticipants.

The family fixed effects (FFE) specification addresses this problem by estimating the effects of Head Start using only data from families where one sibling attended the program and another did not. This approach ensures that Head Start’s effects on criminality are identified exclusively from within-family differences in children’s participation, thus eliminating bias from unobserved cross-family differences. But FFE estimates have some significant tradeoffs, which have been widely acknowledged (see, e.g., Cascio 2021).

The four studies summarized in Table 2 that use the FFE model find an inconsistent pattern of program effects. Garces et al. (2002) found that 9.5 percent of those not exposed to Head Start reported being charged with a crime and that participation in the program lowered this fraction to 4.2 percentage points, a drop of roughly 56 percent. The effect was not statistically significant, however. Deming (2009) estimated that Head Start led to a 2 percentage-point (though statistically nonsignificant) increase in crime. But Deming (2009) also found overall positive effects on an index of prosocial outcomes (of which crime was an element). Pages et al. (2020) reanalyzed the FFE model using 10 additional cohorts of data (from 1990 to 2000) and with reweighting on observables to correct for the “selection-into-identification” problem identified by Miller et al. (2023). They conclude that Head Start’s lasting effects were generally “elusive” and that its effects on crime ranged from -5 percentage points to +2.5 percentage points, depending on the specification; none of these was statistically significant, however.

Difference-in-differences

An alternative method for evaluating Head Start is to compare groups with greater or lesser “exposure” to the program, before and after their exposure. For example, suppose Head Start was available in location j in year t and became available in location j’ only in year t’ ( j’ ≠ j; t’ > t). The first difference compares the subsequent criminality of those who were four years old at time t in location j with those who were four years old at time t-1 in the same location. But a better measure uses the alternative location (j’) as an additional control. That would mean comparing the change in criminality between time t and t-1 in location j with the change in criminality between time t and t-1 in location j’ (where the program had not yet been introduced).

Several studies adopt variants of this technique. Instead of estimating the effects of enrollment in Head Start, Johnson and Jackson (2019) look at the effect of Head Start spending at the local level.⁹ To do so, they “compare the differences in long-run outcomes across birth cohorts from the same childhood county that experienced large increases in Head Start spending at age four to the differences in outcomes across the same birth cohorts within other childhood counties that experienced small (or no) increases in Head Start spending at age four” (Johnson and Jackson 2019, 323–324).¹⁰ They conclude that having access to the average Head Start program (at the average level of subsequent K–12 spending) lowered the adult probability of incarceration for poor children by 2.4 to 8 percentage points, with p-values of 0.09 and 0.06, respectively. Given that the poor children in their sample had a lifetime probability of incarceration of 8 percent, the effect is equivalent to a 25 percent to 100 percent reduction in incarceration probability.

Bailey et al. (2021) exploit a huge dataset based on census and Social Security records that indicate each child’s date and place of birth. They identify the effects of Head Start based on (“chaotic”) time-series and cross-sectional variation in county-level rollout of Head Start programs between 1965 and 1980, rather than funding levels. Although they lack data on family background or Head Start participation, they can use an intent-to-treat (ITT) estimator to measure the effect of exposure to Head Start. They find substantial positive effects on a range of outcomes, but no effect on incarceration (their only criminality measure). But they caution that they can only measure whether someone was incarcerated as of 2018 (rather than lifetime incarceration risk), which greatly reduces their power to detect any Head Start effects.

Barr and Gibbs (2022) studied second-generation effects on the children of those who enrolled in Head Start during the 1961–1964 period, again with a difference-in-differences specification that compares outcomes across children of mothers born too early for exposure (before 1961) with those of mothers born later (1961–1964), across counties receiving and not receiving Head Start funding.¹¹ In their full sample, 27 percent had an arrest, were convicted, or served probation. They estimate that the availability of Head Start for a mother lowered the subsequent criminality of her children by between 6 and 12 percentage points (or 22 percent and 44 percent, depending on sample definitions).¹²

Anders et al. (2023) look intensively at the experience of North Carolina, allowing them to link data on Head Start availability across counties with the complete administrative data on individuals’ subsequent criminal records by county of birth. (They lack individual data on Head Start enrollment, so they use exposure to Head Start as their explanatory variable.) As with other studies, they leverage geographic and chronological variation in Head Start rollout to compare children who were eligible versus ineligible in counties where Head Start was available versus unavailable (plus additional controls). They find that Head Start availability lowers the likelihood of serious conviction by age 35 in high-poverty counties by 1.3 percentage points (compared to a 4.6 percent baseline), for a 28 percent drop (p = .028), although they find no such effect in low-poverty counties. The authors found that a second program, Smart Start, which replicated and extended Head Start in more recent decades, had very similar effects on crime.

Regression discontinuity

The regression discontinuity design identifies the effect of program participation by comparing those who just met the eligibility criteria (for example, had a family income just under the threshold to qualify for participation) with those who were just ineligible. Carneiro and Ginja (2014) use this method to compare the subsequent criminality of boys who just fell short of the eligibility requirement for Head Start (based on income, family size, etc.) with those who were just eligible. Using an ITT specification that does not rely on whether an individual participated in Head Start, but rather on whether they were eligible to have done so, they conclude that the program had a small and statistically nonsignificant effect on the subsequent criminality of male youths aged 16–17. But for men aged 20–21, they conclude that the program lowered criminality (arrest or conviction) by 11 percentage points. From a baseline rate of 28 percent, this represented a statistically significant drop of 40 percent.¹³

Costs and Efficacy of Preschool Programs

Given the lack of research on Head Start and crime as of the late 1990s, our original paper focused on small, high-cost model programs such as Perry Preschool. We assessed the cost per student (for the full, two-year Perry program) to be $14,800 in 1998 dollars, the equivalent of roughly $28,500 in 2024. As of 2021, official data indicate that Head Start spent $10.3 billion on an enrolled student population of 839,116 (Office of Head Start 2021)—roughly $14,200 per student in 2024 dollars. Since Head Start is only half as expensive as Perry, it needs to be only half as effective as Perry at lowering crime to generate the same crime-reducing benefit per dollar spent.

It is difficult to compare the crime-reduction estimates in Table 2 across studies. They use a variety of crime measures (ever-incarcerated, currently incarcerated, total arrests or convictions at various ages, with different crime definitions), crime data (administrative records, self-reports), and econometric estimates (ITT versus treatment on the treated). To account for legitimate concerns that the Perry program might be difficult to scale, our earlier analysis applied a conservative 50 percent discount to the program’s effects. Head Start’s crime-reducing effects need no discount for scale-up problems, since the program is already so large.

With respect to preschool education and its effects on crime, we assess that the scholarly research since our 1998 paper has:

(1) Largely confirmed our initial assessment that at least some of the model preschool programs have durable crime-reducing effects;

(2) Demonstrated that Head Start and related large-scale programs such as North Carolina’s Smart Start also likely have crime-reducing effects, about which we were initially skeptical; and

(3) Shown that, beyond crime, both small-scale programs and Head Start have a variety of other “prosocial” effects on a range of other important outcomes, including adult smoking (K. Anderson et al. 2010), marriage, employment and earnings (Akee and Clark 2024; Ludwig and Miller 2007), and adult mental health (Lacey 2023). These positive consequences are consistent with the crime-reducing effects on which we focused.

Conclusion

In our previous exploration of the effects of incarceration and preschool on crime, we concluded that “given precise targeting, and if a broadly implemented preschool program could generate half the crime-reduction benefits achieved in the pilot studies [of these programs], then cutting spending on prisons and using the savings to fund intensive pre-school education would reduce crime” (Donohue and Siegelman 1998, 1). The research since 1998 buttresses this conclusion in two ways. First, we now have evidence that large-scale preschool programs do have the capacity to deliver at least half the crime-reducing benefits observed in the enriched pilot programs. The efficacy of Perry Preschool at reducing crime has not changed (and indeed, there appear to be crime-reducing effects for the children of those who attended).

Second, the social science literature we have reviewed indicates that the social costs of incarceration are roughly 25 percent greater than we estimated in 1998 and that the crime-reducing benefit of incarceration is somewhat lower than we estimated at that time. Our 1998 paper estimated that the cost of adding an additional inmate was $65,100 per year in today’s dollars, while our accounting based on the recent literature puts that figure at $82,000 (even with prisons now below capacity). We also concluded that the elasticity of crime with respect to incarceration was about -0.1 to -0.2, while newer estimates seem to suggest a slightly lower range of -0.05 to -0.15. Altogether, these findings mean that imprisonment is likely less cost-effective than we assessed 25 years ago.¹⁴

The implication here is that preschool interventions can meet the threshold of efficacy that we indicated was necessary for cost-effective shifting of resources from prisons to preschool enrichment programs. This is particularly true since our estimated costs of incarceration are higher and the benefits of incarceration somewhat lower than we estimated 25 years ago. Indeed, policymakers may have realized this, because we see prison populations have been declining for a decade and preschool enrichment programs have been rising. Our bottom line is that the case for shifting resources from prisons to preschool is at least as strong as—and probably stronger than—it was in our earlier article.

Supplemental Material

sj-docx-1-ann-10.1177_00027162251342885 – Supplemental material for Allocating Resources Among Prisons and Preschool: An Analysis of the New Evidence

Supplemental material, sj-docx-1-ann-10.1177_00027162251342885 for Allocating Resources Among Prisons and Preschool: An Analysis of the New Evidence by John J. Donohue and Peter Siegelman in The ANNALS of the American Academy of Political and Social Science

Footnotes

Notes: We are grateful to Brandon Welsh and two referees for helpful comments and to Eric Baldwin, Matthew Benavides, Alex Oktay, and Amy Zhang for outstanding research assistance.

Supplemental Material

Supplemental material for this article is available online.

Notes

John J. Donohue is C. Wendell and Edith M. Carlsmith Professor of Law at Stanford Law School, a research associate at the National Bureau of Economic Research, and a senior fellow at the Stanford Institute for Economic Policy Research. He has written extensively on issues relating to crime and criminal justice.

Peter Siegelman is Philip I. Blumberg Professor of Law at the University of Connecticut School of Law.

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