The Lasting Effects of Early-Childhood Education on Promoting the Skills and Social Mobility of Disadvantaged African Americans and Their Children

Abstract

This paper demonstrates the long-term intragenerational and intergenerational benefits of the HighScope Perry Preschool Project, which targeted disadvantaged African-American children. We use newly collected data on the original participants through late middle age and on their children into their mid-twenties. We document long-lasting improvements in the original participants’ skills, marriage stability, earnings, criminal behavior, and health. Beneficial program impacts through the childrearing years translate into better family environments for their children leading to intergenerational gains. Children of the original participants have higher levels of education and employment, lower levels of criminal activity, and better health than children of the controls.

1. Introduction

This paper analyzes newly collected life-cycle panel data on the original participants of the pioneering HighScope Perry Preschool Project (PPP) social experiment through late midlife and on their children into their mid-twenties. We use longitudinal data based on multiple surveys and administrative criminal records. PPP aims to promote the social mobility of disadvantaged African-American children and it is successful. It also has substantial beneficial intergenerational effects. Gains in cognition are sustained through late midlife, contradicting claims about cognitive fadeout of PPP and other early childhood programs. Enriched early childhood education programs are promising vehicles for promoting social mobility within and across lifetimes.

A program created sixty years ago is relevant today because it influences the design of current and proposed early childhood education programs. The populations it was designed to serve are still substantial. At least 30% of current Head Start programs are based on it (Elango et al., 2016). About 10% of African-American children born in the 2010s satisfy the eligibility criteria for PPP.¹ Commonalities over time and across cultures and ethnic groups in the process of child development make our conclusions relevant to other contexts.² Our study provides general lessons for policies that foster child development.

It is well-documented that PPP improved the life-cycle outcomes of its original participants through age 40 (e.g., Elango et al., 2016; Heckman and Karapakula, 2021; Heckman et al., 2010b). We show that positive impacts on the original participants persist through their childrearing years. These gains led to better environments for their children, who are more likely than children of the first generation of control participants to grow up in stable two-parent households. Their parents have higher average earnings, less engagement with the criminal-justice system, and better executive functioning (cognition), socio-emotional skills, and health.

PPP did not directly treat the children of the original participants. Nonetheless, it generated positive intergenerational externalities. Children of treated participants are 17 percentage points less likely to have been suspended from school during their K-12 years compared to children of control participants. They are also 9 percentage points more likely to be in good health through young adulthood, 26 percentage points more likely to be employed, and 8 percentage points less likely to be divorced. There are pronounced impacts by sex. Children of male treated participants are 18 percentage points less likely to have been arrested through young adulthood compared to children of male control participants. Our estimates are statistically significant and robust when we use multiple estimation strategies and inferential procedures designed to address methodological challenges inherent in PPP and many other social experiments (Bruhn and McKenzie, 2009). We apply rigorous small-sample inferential methods in recognition of PPP’s sample size and to counter the undocumented but often repeated claim that “Perry’s samples are too small.”

This paper proceeds in the following way. Section 2 briefly describes the literature related to our study. It clarifies our contribution relative to other work on the intergenerational impact of early childhood education and relative to recent studies of PPP. Section 3 describes the program, our data, and our methodology. Section 4 presents impacts on the original participants of PPP, which include improvements in the environments in which their children were raised. Section 5 presents our intergenerational estimates. Section 6 concludes.

2. Related Literature

Little is known about the intergenerational impacts of early childhood education. Barr and Gibbs (2022) and Rossin-Slater and Wüst (2020) are exceptions. The latter paper exploits differential timing in preschool availability in Denmark during the period 1933-1960 and studies its intergenerational impact on educational attainment at age 25. Barr and Gibbs (2022) study the intergenerational impact of Head Start programs available in the 1970s using a similar design. They analyze education, teenage pregnancy, and youth criminality. Both studies find beneficial intergenerational impacts.

Our study breaks new ground because it is based on experimental data and collects detailed information about the long-term life-cycle outcomes of the original participants and the outcomes of their children. We study intergenerational outcomes of the children across the life cycle from early life (e.g., special education and school suspension) to young adulthood (e.g., employment and marriage stability).

2.1. Recent Studies of the HighScope Perry Preschool Project

A companion paper, García et al. (2021), monetizes the treatment effects of the program we study through age 54. It reports a benefit-cost ratio of 6.0 after adjusting for the distortion generated by the taxes required to fund the program. That paper focuses on the cost-benefit analysis of the program. It does not analyze the life-cycle patterns we document in this paper. It does not analyze in detail the age-54 outcomes of the original participants discussed in this paper, especially those related to newly collected measures of skills. Its analysis includes a crude monetization of some of the intergenerational treatment effects in this paper. It does not present treatment effects on the newly collected intergenerational outcomes. Heckman et al. (2010b) and Heckman and Karapakula (2021) study the impact of PPP on its original participants through age 40. Both studies develop identification, estimation, and inference methods especially suited for tackling the challenges inherent to PPP’s design and implementation.

Heckman and Karapakula (2019b) is the working-paper version of Heckman and Karapakula (2021). We use some of the methods developed and tested in that paper. Heckman et al. (2010a) and Heckman et al. (2013) are related studies. Heckman et al. (2010a) provide estimates of the internal rate of return of PPP using extrapolations informed by original-participant data through age 40. Heckman et al. (2013) develop and apply a mediation framework to document that the short-term impact of PPP on socio-emotional skills largely explains the long-term impacts on age-40 outcomes such as employment and crime. Conti et al. (2016) report treatment effects on health outcomes of the original participants at ages 27 and 40. They build on the framework of Heckman et al. (2013) to provide dynamic mediation analyses of these health outcomes. None of these studies use the intergenerational data studied in this paper.

3. Program, Data, and Methods

3.1. The HighScope Perry Preschool Project

The HighScope Perry Preschool Project was a high-quality early childhood education program.³ Its participants were born in the late 1950s and early 1960s. Its curriculum was designed to foster development of cognitive and socio-emotional skills. Children were active learners who planned, executed, and reflected on activities guided by teachers. Children made choices and solved problems. Teachers gave them feedback (Schweinhart et al., 1993), a form of reinforcement learning (Dehaene, 2021).⁴

Participants lived in the catchment area served by the Perry Elementary School in Ypsilanti, Michigan. In-school surveys, referrals, and canvassing identified an initial pool of participants. Eligibility criteria were based on IQ scores and socio-economic status. A pool of 123 disadvantaged African-American children was randomized into the program (treatment group) or not (control group). Treatment-group children received two years of 2.5-hour preschool sessions during weekdays starting at age three. They also received weekly teacher home visits during the two-year treatment period. Control-group children did not receive any treatment because there were no treatment substitutes available in the area where they lived. The program was implemented before Head Start and indeed influenced its design and creation. Comparing the treatment and control groups allows us to identify program impacts compared to no treatment in any other program. For early childhood programs implemented later, control-group parents enroll their children in alternative preschools of varying quality. Identification of clearly defined treatment effects thus requires additional assumptions to control for choices of other options (García et al., 2018; Heckman et al., 2000; Kline and Walters, 2016).

Weikart et al. (1978) report that every family that received an offer to participate in PPP accepted it. We thus estimate the average treatment effect for program eligibles. Heckman et al. (2010b) report that 15% of African-American females and 17% of African-American males satisfied PPP’s eligibility criteria at the time of its implementation. After participants were randomized, the status of a few participants was swapped. This reassignment potentially compromised the randomization protocol and resulted in an imbalance of baseline characteristics (see Table 1). Failure in implementation of randomization protocols is not rare in social experiments. This failure can have sizable empirical consequences (Bruhn and McKenzie, 2009). We are upfront about these issues and adjust our estimates accordingly.⁵

Table 1.

Original Participants, Sample Sizes and Unadjusted Mean Differences

	Pooled		Male		Female
	C	(T-C)	C	(T-C)	C	(T-C)
Panel a. Baseline, Age 3
IQ	78.54	1.03	77.85	1.37	79.58	0.46
Socioeconomic Index	8.62	0.17	8.65	0.24	8.57	0.09
Mother Works	0.31	−0.22	0.28	−0.22	0.35	−0.23
Mother’s Age	28.66	0.92	28.63	0.84	28.71	1.01
Sample Size	65	−7	39	−6	26	−1
Panel b. Age-54 Follow-Up
Sample Size, Observed	50	2	30	−1	20	3
with Children	41	−1	22	−2	19	1
Total Children	104	6	56	−4	48	10
Child’s Age	28.11	0.18	25.75	1.42	30.85	−1.58
Sample Size, Not Observed
Deceased	9	−3	4	0	5	−3
Other Reasons	6	−6	5	−5	1	−1
Panel c. Fertility, Age 54
No Children	0.07	0.03	0.10	0.03	0.02	0.02
Children	2.08	0.04	1.87	−0.07	2.40	0.12
>5 Children	0.04	0.04	0.03	0.04	0.05	0.04
Age when Child Born	21.80	1.25	22.82	1.98	20.63	0.67
Panel d. Parenting
Not Out of Wedlock when Child Born	0.20	0.03	0.23	0.07	0.16	−0.01
No Cohabitation with New Partner while Child Grew Up	0.39	0.11	0.41	0.09	0.37	0.13
Fraction of Years Married through Child’s Age 10	0.13	0.19	0.09	0.21	0.18	0.16
Read Daily to Child	0.13	0.13	0.14	0.11	0.11	0.14
Panel e. Skills and Health (Latent Variables*), Age 54
Executive Functioning	−0.14	0.36	−0.21	0.56	−0.05	0.14
Positive Personality	−0.20	0.42	−0.22	0.37	−0.19	0.46
Grit	−0.08	0.16	−0.17	0.15	0.01	0.15
Openness to Experiences	−0.24	0.32	−0.23	0.25	−0.26	0.39
Health	−0.14	0.15	−0.13	0.15	−0.15	0.16
Panel f. Education at Age 54
High School Graduation	0.46	0.31	0.55	0.15	0.37	0.48
College Graduation	0.20	−0.15	0.14	−0.04	0.26	−0.26
Panel g. Average Employment and Earnings of Parents through Child’s Age 10
Fraction of Years Employed	0.44	0.16	0.47	0.16	0.40	0.17
Earnings (1,000s of 2017 dollars)	18.39	8.58	22.55	11.53	13.57	6.65
Panel h. Crime, Age 54
Days in Jail	71.15	−35.52	119.18	−73.83	15.53	10.37
Misdemeanor Arrests	0.90	−0.60	1.45	−0.95	0.26	−0.16
Felony Arrests	0.80	−0.60	1.40	−1.00	0.11	−0.11

Note: Panel a. summarizes basic variables and the sample size at baseline of the original participants. Panel b. summarizes the sample size of the original participants observed and not observed in the age-54 follow-up. The first part of Panel c. summarizes fertility variables for all the original participants observed in the age-54 follow-up. The second part of Panel c. and Panels d. to h. summarize variables at the original participant level for those observed in the age-54 follow-up who report having children, using information on up to their five eldest children. C for sample size rows: number of observations in the control group. C for outcome rows: control-group mean for variables at the original-participant level—Panel a., first part of Panel c., Panel d., and Panels f. and h; and control-group mean in the within original-participant average across up to their five eldest children for variables at the child-of-original-participant level—second part of Panel c. and Panels d. and g. The columns (T-C) are constructed analogously to the columns (C) for treatment-control differences. We bold (T-C) entries for outcome rows when their permutation p-values are less than 0.10. The null hypothesis for each difference is that it is less than or equal to 0 for all outcomes except for crime outcomes. For crime outcomes, the null hypothesis for each difference is that it is greater than or equal to 0. Appendix Table A.1 presents variable definition and construction details. Standard errors and alternative estimates for the mean differences in this table are in Table 2.

^*Latent variables are constructed using the method described in Section 3.4 and the measures in Appendix Table A.1.

3.2. Age-54 Follow-up

Panel a. of Table 1 gives the sample size and baseline characteristics of the study. Original or first-generation participants were followed in multiple rounds of data collection through age 54. In this paper, we use data from the age-54 follow-up, in which information on their adult children was collected.⁶ We supplement these data with earlier waves to form panel observations. Panel b. of Table 1 provides the sample size of original participants in the age-54 follow-up: 83% of the 123 original participants were surveyed; 12% were not surveyed because they were deceased, and 5% were not surveyed for other reasons. Combining survey questions with criminal (police and court) administrative records, we observe marriage, earnings, and criminal histories from enrollment to age 54.⁷

The first part of Panel c. of Table 1 summarizes fertility information of the 102 participants surveyed in the age-54 follow-up. Eighty one of these participants report having children. The treatment-control difference in the number of children is small and statistically insignificant. This evidence rules out experimentally induced fertility as an important consideration. The program had minimal impacts on childbearing. The original participants are only asked about their first five children. This does not result in a major loss of information because only a small fraction of first-generation participants report having more than five children. Information losses due to not observing children yet to be born are also a minor issue in the age-54 follow-up, as the vast majority of the original participants are likely to have completed childbearing and adoption.

Appendix Table A.2 compares the sample of participants with children in the age-54 follow-up with the sample of participants without children. No consistent statistical differences are found between the two samples, although this comparison is not precise because the sample of those without children is very small (9 control-group and 12 treatment group participants).

3.3. Analysis Sample

Our main analysis sample includes 41 first-generation control and 40 first-generation treatment participants. The sample includes original treatment and control participants who report having children in the age-54 follow-up. They have 104 and 110 children, respectively, who constitute the sample of children that we use to assess intergenerational impacts. We conduct analyses at the first-generation participant level because only first-generation participants were randomized. Accordingly, when we analyze the child sample, we need to account for its origin.⁸

We construct intergenerational outcomes as follows. Let I index first-generation participants and 𝒥 index outcomes. Define $Y_{i,j}^{c(i)}$ as the outcome j ∈ 𝒥 of child c(i) of first-generation participant i ∈ I. The mean outcome j for the children of i is

$${\overline{Y}}_{i,j}^c≔\frac{1}{\#{𝒞}_i}\sum _{c\in {𝒞}_i}{Y}_{i,j}^{c(i)},$$ (1)

where 𝒞_i indexes the children of first-generation participant i.⁹ We define ${\overline{Y}}_{i,j}^c$ as outcome j for each first-generation participant. ${\overline{Y}}_{i,j}^c$ is the outcome for the “average child” of i.

3.4. Measurement Framework

Let $Y_{i,j}^1$ denote outcome Y_i,j when first-generation participant i ∈ I is assigned to treatment status (D_i := 1) and $Y_{i,j}^0$ when they are assigned to control status (D_i := 0). The observed outcome is thus $Y_{i,j}=Y_{i,j}^1{D}_i+Y_{i,j}^0(1-D_i)$.¹⁰ When analyzing child outcomes, we treat average child outcomes as treatment and control outcomes for the original participants, dropping the c(i) and c superscripts for notational simplicity.

For outcome j ∈ 𝒥, we consider three estimators of the average treatment effect $\mathbb{E}\left[Y_{i,j}^1-Y_{i,j}^0\right]$. The first is the (unadjusted) treatment-control mean difference. We pool first-generation treatment and control participants and estimate the coefficients in the model

$$Y_{i,j}={\gamma }_j+{\delta }_j{D}_i+{\epsilon }_{i,j},$$ (2)

where ε_i,j is an error term with $\mathbb{E}\left[{\epsilon }_{i,j}\mid D_i=d_i\right]=0$. γ_j is an estimator of the control mean and δ_j is the mean-difference estimator. δ_j identifies the average treatment effect assuming that treatment is randomized without compromises and that attrition is random.

A second estimator—regression-adjusted mean difference (OLS)—is used to address the randomization compromises and attrition patterns described in Section 3. We construct this estimator including the baseline variables in Panel a. of Table 1 in addition to first-generation participant sex as covariates in Equation (2). We know the qualitative features of the randomization failure, but not details about individual participants. We know that baseline variables are only partially balanced across the treatment and control groups. OLS identifies the average treatment effect under the assumption of conditional random assignment to treatment and attrition conditional on baseline covariates.

Our third estimator is a more general mean-difference adjustment used in Heckman and Karapakula (2021). It is an augmented inverse-probability weighting estimator (AIPW) adapted to the sampling protocol of PPP. It weights Equation (2) by the inverse probability of being treated and having attrited (recall that the reasons for attrition are being dead, not being interviewed in the age-54 follow-up, or not having children). AIPW imputes (missing) counterfactual outcomes for each first-generation participant based on the same baseline variables used as covariates when computing the OLS estimates. AIPW is useful for its double-robustness property. It provides a consistent estimator of the average treatment effect if either the weighting scheme or the (imputed) Equation (2) is correctly specified.¹¹

We also present Lee (2009) bounds for average treatment effects, a supplementary set of results accounting for compromises in randomization. This method is appropriate for contexts with (conditional) randomized assignment to treatment and sample selection generated by attrition. We refer readers to the source paper for details. Lee’s bounds require two assumptions: (i) (conditional) randomized assignment to treatment; and (ii) treatment affects attrition uniformly across the sample (i.e., the probability of being attrited should either increase or decrease as a function of treatment status for all individuals). The first assumption is plausible in our context, as we condition on variables unbalanced due to the compromises in the randomization protocol. The evidence in Panel b. of Table 1 is consistent with the second assumption. First-generation treatment-group participants were more likely to be followed-up at age 54 (either because of death or other reasons).

Creating Factor Variables.

We observe sets of survey items designed to measure different skills. For each set of skill measurements, we use factor analysis to create a one-dimensional, interpretable aggregate of each set of items. Factor analysis summarizes the covariability among the observed items.¹² It reduces the dimension of the data by creating one latent factor variable from multiple items in each category. It accounts for measurement error. Appendix Table A.1 lists the items that we use for estimation. Following standard practice (Gorsuch, 1983; Thompson, 2004), we assume that each item is associated with at most one skill.¹³ For estimation, we assume that the measurement system is the same across treatments and controls. This hypothesis is tested and not rejected in Heckman et al. (2013). We standardize each latent factor variable to have an in-sample mean 0 and standard deviation 1. We use the same procedure to produce a health latent variable.

Inference.

Outcomes are reported so that a positive point estimate indicates a beneficial treatment effect. Crime outcomes of the original participants are an exception. For “positive outcomes” we test if the treatment effect is less than or equal to 0, outcome by outcome. For the crime outcomes of the original participants, we test if the treatment effect is greater than or equal to 0. We report one-sided tests because most outcomes of Perry are beneficial in this and other studies. For our baseline AIPW estimator, we present several p-values. Our baseline p-value is permutation-based because it is especially suited for analyzing small samples like ours. We also present bootstrap standard errors for all of the estimators considered. All of our inference is clustered at the first-generation participant level.¹⁴

4. Impact on the Original Participants

PPP had an impact on the socio-emotional skills of the original treatment participants. Heckman et al. (2013) document that this impact translated into improvements in labor-market, crime, and health outcomes through age 40.¹⁵ In this section, we update that analysis. This motivates the source of the intergenerational externalities that we report below.¹⁶ We show that the impact on the skills, marriage, earnings, crime, and health outcomes of the original participants persists through their childrearing years up to their late midlife years. Their improved outcomes produce better home environments for their children.

We start by describing the treatment-control mean differences for the original participants in Table 1 and Figure 1. We then discuss robustness of our estimates to multiple estimation strategies and inferential procedures. Panel e. of Table 1 summarizes newly collected data at age 54 on skills of the original participants. It shows that PPP has a long-lasting impact on both cognitive and socio-emotional skills. PPP increases the skills of the pooled group of male and female original participants by 0.2 to 0.4 standard deviations. Male original participants drive this impact. However, the average treatment-control differences are positive for all skills for both males and females.

Figure 1. Original-Participant Marriage, Earnings, and Crime by their Age and by their Children’s Age.

Note: Panel (a) displays the control-group and treatment-group unadjusted means of a married-status indicator by age of the original participants who reported having children. We mark the treatment-group mean when the unadjusted treatment-control mean difference has a permutation p-value less than 0.10. The null hypothesis for the difference is that it is less than or equal to 0. Panel (b) is analogous in format to Panel (a) for annual earnings in 1,000s of 2017 USD. Panel (c) is analogous in format to Panel (a) for cumulative violent misdemeanor and felony arrests. For Panel (c) the null hypothesis for the difference is that it is greater than or equal to 0. Panels (d) to (f) are analogous in format to Panels (a) to (c), but they are plotted by age of the children of original participants. For Panels (d) to (f) the outcomes are first averaged within original participants across up to five eldest children before constructing control and treatment means.

Ours is the first paper to document the impact of high-quality early education on skills at late midlife. The long-lasting impact on executive functioning challenges the often-repeated claim of “fadeout” in the treatment effects on skills, specifically on cognition. Previous research claims that the impact of early childhood education on cognitive-test scores disappears (fades out) shortly after the endpoints of interventions (Bailey et al., 2020; Hojman, 2016; Protzko, 2015). Some authors argue that the fadeout in cognition (and also socio-emotional skills) is real, and not only a measurement artifact (Bailey et al., 2017, 2020). These studies are all based on short-run follow-ups. Our estimates dispute this claim. Our measure of executive functioning is based on well-established tests that measure cognition (Raven and Stroop tests).

Panel e. of Table 1 also describes another relevant life-cycle outcome: health. We summarize health using a latent factor (see Section 3.4). Examples of items underlying this factor include waist-to-hip ratio, high total cholesterol, and chronic severe pain (see Appendix Table A.1 for a complete list of items). These items are part of the newly collected data at age 54. The mean difference of the latent variable is not precisely estimated. However, Appendix Figures A.3a shows estimates of the treatment and control distributions of the health latent variable. Treatment shifts the distribution rightward. Treatment-group participants are 15 percentage points more likely to be healthier than 80% of individuals in the pooled treatment and control sample (permutation p-value = 0.06). Appendix Table A.3 presents treatment effects on the individual items forming the health latent variable. Other studies document impacts on adult health of early childhood education up to age 30 or 40 (Campbell et al., 2014; Conti et al., 2016). Our analysis confirms that health impacts persist up to age 54. This finding is new. Positive forecasts of the long-term health impact of early childhood education are thus justified.¹⁷

Panels (a) to (c) of Figure 1 display the average evolution of life-cycle outcomes of the original participants who reported having children in the age-54 follow-up. The improvements in marriage stability, earnings, and criminal behavior of the original treatment participants are substantial. At age 30, they are more than 10 percentage points more likely to be married, have 10,000 dollars higher average annual earnings, and accumulate approximately one fewer average arrest.¹⁸ Panels (d) to (f) show the means of the same variables by child treatment status and age.¹⁹ The improvements of the original treatment participants imply that their children are more than 15 percentage points more likely to be born to married parents than children of control-group participants. They are also born to parents who, on average, make almost 10,000 dollars per year more and have a lower average of cumulative arrests. The advantage of children of the original treatment participants builds up years before they are born. It persists throughout their childhoods.

Panels d. to h. of Table 1 reinforce the evidence in Figure 1. They show that, on average, children of the original treatment group were more likely to grow up in two-parent stable environments compared to children of the original controls. They were read to more often while growing up.²⁰ Their parents had greater skills, were employed a larger fraction of time, had more education and earnings, and engaged less in criminal behavior when they were growing up.

Table 2 reports robustness checks for the estimates presented in Table 1. Column (1) replicates the mean-difference estimates in Table 1 for reference. It provides the corresponding bootstrapped standard errors. We then show the OLS estimates of the treatment effect and the Lee (2009) bounds. The OLS estimates align with the mean differences. The bounds are tight. Panel b. of Table 2 presents AIPW estimates, which most comprehensively addresses the randomization compromises described in Section 3.1. We also provide alternative p-values. The several checks verify that the treatment-control differences are robust to different estimation strategies and remain statistically significant under several inferential procedures. Table 2 also provides estimates and inference for two summary measures of the outcomes in Figure 1—fraction of years married and earnings between ages 21 and 40, which are the ages in which the original participants do most of their parenting. The results confirm substantial and significant treatment-control differences. Treatment increased the parenting and economic resources that the original participants provided to their children.²¹

Table 2.

Robustness of Estimated Treatment Effects and Standard Errors for the Original Participants

Panel a. Basic Estimates
	(1) Mean Difference		(2) Adjusted Mean- Difference (OLS)		(3) Lee (2009) Bounds
	Estimate	S.E.	Estimate	S.E.	Lower	Upper
Age when Child Born	1.245	(1.150)	1.332	(1.282)	0.959	1.423
Not Out of Wedlock when Child Born	0.030	(0.094)	−0.040	(0.100)	0.013	0.035
No Cohabitation with New Partner while Child Grew Up	0.110	(0.110)	0.061	(0.115)	0.099	0.121
Fraction of Years Married through Child’s Age 10	0.188	(0.077)	0.159	(0.086)	0.174	0.195
Fraction of Years Married, Ages 21 to 40	0.156	(0.069)	0.156	(0.080)	0.135	0.164
Read Daily to Child	0.125	(0.086)	0.107	(0.089)	0.107	0.131
Executive Functioning	0.356	(0.193)	0.348	(0.197)	0.320	0.401
Positive Personality	0.418	(0.174)	0.369	(0.203)	0.418	0.471
Grit	0.158	(0.197)	0.165	(0.241)	0.113	0.158
Openness to Experiences	0.321	(0.194)	0.284	(0.183)	0.271	0.351
Health	0.153	(0.219)	0.153	(0.274)	0.133	0.153
High School Graduation	0.312	(0.103)	0.334	(0.110)	0.307	0.329
College Graduation	−0.145	(0.071)	−0.146	(0.075)	−0.166	−0.144
Fraction of Years Employed through Child’s Age 10	0.162	(0.074)	0.156	(0.079)	0.154	0.174
Average Earnings (1,000s of 2017 dollars) through Child’s Age 10	8.584	(4.615)	8.170	(4.798)	7.018	9.145
Average Earnings (1,000s of 2017 dollars), Ages 21 to 40	8.624	(4.031)	8.241	(4.417)	6.464	9.327
Days in Jail	−35.521	(27.267)	−31.652	(27.360)	−42.790	−34.735
Misdemeanor Arrests	−0.602	(0.272)	−0.735	(0.330)	−0.640	−0.596
Felony Arrests	−0.599	(0.281)	−0.601	(0.275)	−0.599	−0.594
Panel b. Estimates of Preferred Estimator: AIPW
			p-values
					Bootstrap
	Estimate	S.E.	Analytic	Permutation	Simple	Studentized
Age when Child Born	1.482	(1.335)	[0.103]	[0.096]	[0.101]	[0.112]
Not Out of Wedlock when Child Born	−0.066	(0.107)	[0.793]	[0.739]	[0.684]	[0.853]
No Cohabitation with New Partner while Child Grew Up	0.049	(0.129)	[0.309]	[0.359]	[0.307]	[0.331]
Fraction of Years Married through Child’s Age 10	0.141	(0.091)	[0.023]	[0.052]	[0.054]	[0.056]
Fraction of Years Married, Ages 21 to 40	0.138	(0.092)	[0.016]	[0.044]	[0.048]	[0.053]
Read Daily to Child	0.089	(0.091)	[0.114]	[0.197]	[0.152]	[0.116]
Executive Functioning	0.354	(0.215)	[0.031]	[0.043]	[0.030]	[0.029]
Positive Personality	0.461	(0.207)	[0.003]	[0.010]	[0.032]	[0.010]
Grit	0.096	(0.262)	[0.325]	[0.330]	[0.362]	[0.325]
Openness to Experiences	0.204	(0.215)	[0.100]	[0.164]	[0.143]	[0.135]
Health	0.121	(0.312)	[0.291]	[0.299]	[0.330]	[0.337]
High School Graduation	0.333	(0.125)	[0.000]	[0.004]	[0.008]	[0.008]
College Graduation	−0.130	(0.091)	[0.970]	[0.942]	[0.953]	[0.970]
Fraction of Years Employed through Child’s Age 10	0.145	(0.089)	[0.024]	[0.039]	[0.076]	[0.022]
Average Earnings (1,000s of 2017 dollars) through Child’s Age 10	8.879	(5.561)	[0.024]	[0.041]	[0.078]	[0.027]
Average Earnings (1,000s of 2017 dollars), Ages 21 to 40	8.462	(5.258)	[0.019]	[0.020]	[0.081]	[0.030]
Days in Jail	−33.219	(28.841)	[0.083]	[0.120]	[0.154]	[0.035]
Misdemeanor Arrests	−0.803	(0.340)	[0.002]	[0.006]	[0.017]	[0.003]
Felony Arrests	−0.611	(0.314)	[0.008]	[0.005]	[0.032]	[0.005]

Note: Panel a. presents treatment-effect estimates and standard errors of the average treatment effect for the first-generation participant outcomes summarized in Table 1 using the mean-difference and the adjusted mean-difference OLS estimators explained in Section 3.4. It also presents the Lee (2009) bounds. We include treatment-effect estimates for a summary variable for the marriage and earnings longitudinal outcomes (the average between ages 21 and 40). Panel b. presents treatment-effect estimates, standard errors, and p-values based on our preferred estimator (AIPW) for the outcomes in Panel a. The AIPW estimator and p-values are explained in Section 3.4. The standard errors are bootstrapped and clustered at the first-generation participant level. The null hypothesis for each treatment effect is that it is less than or equal to 0 for all outcomes except for the crime outcomes. For the crime outcomes, the null hypothesis for each treatment effect is that it is greater than or equal to 0.

5. Intergenerational Outcomes

We now turn to the outcomes of the children of the original participants. We analyze the eight outcomes displayed in Figure 2.²² These are outcomes for the average child, constructed using the formula in Equation (1). We analyze children of all ages when examining school suspension, special education, arrests, and health. We only consider children age 19 or older when analyzing teenage parenthood. For years of education, employment, and divorce, we consider children 23 and older. The children of the original participants are, on average, 28 years old when information on them is reported at the age-54 follow-up. Most of them satisfy all of the age cutoffs imposed. All first-generation participants who report having children have at least one child satisfying all of the age cutoffs except for two.²³

Figure 2. Outcomes of the Second Generation (Children) by Sex of the First Generation (Original-Participant Parents).

Note: Panel (a) displays the unadjusted mean for never suspended, never in special education, and years of education for the children of the original participants (intergenerational outcomes). To simplify the figure, we display years of education as the number of years after the twelfth year of education. The unadjusted means are displayed by treatment status of the original participants. On top of each bar, we display the corresponding treatment-control unadjusted mean difference (Δ). We mark the difference when its corresponding treatment-effect estimate using our preferred AIPW estimator explained in Section 5.1 has a permutation p-value less than 0.10. The null hypothesis for the treatment effect is that it is less than or equal to 0. The outcomes are defined as within original-participant averages across up to five eldest children, as explained in Section 3.3. The unadjusted means by treatment status are then calculated. Panels (b) and (c) are analogous in format to Panel (a) for the outcomes labeled.

5.1. Adjusted Mean Differences

Figure 2 displays unadjusted treatment-control mean differences. They are sizable. The children of the original treatment participants are more likely to never have been suspended from school, be employed, never have been arrested, be in good health, and never have been divorced. They also accumulate more years of education. We adjust these differences and provide inference in Column (1) of Table 3. Given the robustness of the estimates in Section 4, we focus our discussion on results based on AIPW and permutation-based inference, which most comprehensively address randomization compromises and small sample size.²⁴ AIPW also accounts for factors preventing us from observing second-generation outcomes. These factors include death and any other reason for not observing first-generation participants in the age-54 follow-up. They also include not observing second-generation outcomes for first-generation participants who do not have children.

Table 3.

Intergenerational Treatment Effects by Sex of the Original Participants and their Children

	(1)	(2)	(3)	(4)	(5)	(6)	(7)	(8)	(9)
First Generation:	Pooled			Male			Female
Second Generation:	Pooled	Male	Female	Pooled	Male	Female	Pooled	Male	Female
Never Suspended from School	0.169 [0.029]	0.196 [0.064]	0.119 [0.170]	0.224 [0.041]	0.114 [0.276]	0.163 [0.125]	0.092 [0.251]	0.311 [0.032]	0.057 [0.398]
Never in Special Education	−0.051 [0.758]	0.050 [0.347]	−0.100 [0.880]	−0.068 [0.721]	−0.093 [0.731]	−0.058 [0.646]	−0.028 [0.621]	0.251 [0.075]	−0.160 [0.988]
Years of Education	0.084 [0.409]	0.704 [0.045]	0.093 [0.423]	−0.165 [0.619]	0.331 [0.250]	−0.131 [0.534]	0.436 [0.190]	1.231 [0.029]	0.410 [0.270]
Employed	0.258 [0.006]	0.228 [0.072]	0.217 [0.056]	0.299 [0.022]	0.280 [0.113]	0.365 [0.033]	0.200 [0.079]	0.155 [0.241]	0.007 [0.482]
Never Arrested	0.088 [0.129]	0.082 [0.240]	−0.015 [0.560]	0.176 [0.032]	0.214 [0.114]	−0.005 [0.519]	−0.036 [0.607]	−0.104 [0.739]	−0.029 [0.576]
In Good Health	0.092 [0.090]	0.170 [0.054]	0.135 [0.053]	0.102 [0.047]	0.202 [0.038]	0.088 [0.156]	0.077 [0.264]	0.124 [0.239]	0.203 [0.079]
Never Teen Parent	−0.061 [0.758]	−0.045 [0.653]	−0.083 [0.758]	−0.026 [0.570]	−0.060 [0.618]	−0.066 [0.640]	−0.111 [0.836]	−0.025 [0.586]	−0.107 [0.758]
Never Divorced	0.076 [0.074]	0.088 [0.051]	0.044 [0.275]	0.042 [0.325]	0.074 [0.012]	−0.037 [0.639]	0.123 [0.016]	0.108 [0.165]	0.159 [0.035]

Note: This table presents treatment-effect estimates for our eight second-generation outcomes by sex of the first-generation participant (parent) and second-generation participant (child) using our AIPW estimator. In brackets, we present each estimate’s permutation p-value. We bold the treatment-effect estimates when their permutation p-values are less than 0.10. The null hypothesis for each treatment effect is that it is less than or equal to 0.

PPP has a beneficial intergenerational impact that is consistent with its impact on the first generation. High-quality early childhood education programs like PPP improve the early-life socio-emotional skills of children. This translates into long-term impacts on labor-market, crime, and health outcomes.²⁵ School suspension is an indirect measure of early-life socio-emotional skills and PPP has a sizable impact on them for the second generation. The impact on health through young adulthood and longer-term outcomes as employment and relationship stability (never have been divorced) are also sizable. For crime, the impact is much stronger for men and we discuss it in Section 5.2.

We examine “employment” to further interpret our estimates. We compare the second-generation impacts with the first-generation impacts of PPP and Head Start (a federal early childhood education program targeted toward disadvantaged families like PPP, and founded in its wake).²⁶ We estimate that PPP increases the second-generation probability of employment by 25.8 (s.e. 11.5) percentage points. Table 3 shows that the treatment-effect estimate is similar for second-generation male and female participants. Heckman and Karapakula (2021) report an age-40 first-generation impact of PPP on employment of 26.6 percentage points for men (p-value = 0.02) and −1.6 percentage points for women (p-value = 0.50). Our results indicate that the first-generation impacts of PPP spillover into the second generation. The first-generation impact spillovers to male and female second-generation participants. The intergenerational impact of PPP on employment is also larger than the first-generation impact of Head Start on the probability of not being idle during young adulthood—7.1 (s.e. 3.8) percentage points (Deming, 2009). PPP has a larger second-generation impact than the first-generation impact of Head Start.

Column (1) of Table 3 shows that, while not all estimates are statistically significant at the 10% level, there is a general pattern of positive treatment effects. At the 10% level, we detect significant treatment effects on four out of the eight outcomes we study when analyzing the pooled sample of male and female second-generation participants. Appendix Table A.8 shows that this conclusion holds when using alternative inferential procedures. For two reasons, these results are unlikely to be a consequence of cherry picking. First, we analyze all of the second-generation outcomes observed. If all eight treatment effects were 0, we would reject the null hypothesis of no treatment effect for 10% of outcomes by chance using a 10% significance level. The F-statistic for the joint null hypothesis of no treatment effect for the eight outcomes is 2.21 (p-value = 0.04). Second, our outcomes are interpretable categories of independent interest. Correcting p-values for multiple hypothesis testing for such diverse categories of treatment effects would lump together very different outcomes and would lack any behavioral justification.

5.2. Gender Differences

Impacts of early childhood education on long term outcomes are usually found to be greater for boys than for girls (Elango et al., 2016). Educational outcomes are the exception to this rule.²⁷ The first-generation impact of PPP is consistent with these findings. Table 3 shows a greater intergenerational impact on second-generation male children than on second-generation female children. For instance, we reject the null hypothesis that the treatment effect is less than or equal to 0 using a significance level of 10% for five out of the eight outcomes. For second-generation female participants, we only reject the null for two out of eight outcomes.

For crime, we find a substantial, positive impact on never being arrested for children of first-generation male participants. The impact on second-generation male children drives this result. PPP reduced criminal activity of first-generation male participants. The intergenerational impact on their sons is consistent with recent studies in economics and sociology finding that parental incarceration (most incarcerated individuals are men) leads to a significant intergenerational increase in behavior issues and teen crime (Dobbie et al., 2018; Haskins, 2014; Murray et al., 2014; Turney and Haskins, 2014). These results are primarily for disadvantaged individuals, making the comparison to our study relevant. The second-generation crime impact is also consistent with studies in other fields documenting that early-life environments determine young-adult criminal activity (Belsky et al., 2020; Henry et al., 1999; Piquero and Moffitt, 2005; Wright et al., 1999). Section 5.3 discusses further the intergenerational transmission of criminal outcomes in the sample.

5.3. Contextualization of Intergenerational Treatment Effects

Though scarce, the literature on the intergenerational impact of high-quality preschool summarized in Panel a. of Table 4 allows us to contextualize our estimates. Rossin-Slater and Wüst (2020) study the intergenerational impact of high-quality preschool in Denmark. They exploit availability for children born between 1935 and 1957 to women who were born between 1955 and 1987. They argue that most beneficiaries were disadvantaged. They estimate the intent-to-treat or reduced-form effect of preschool availability in the municipality where the mothers resided when they were between three and seven years old. They find an intergenerational impact on years of education of 0.06 (p-value < 0.01), from a control-group mean of 12.13. Our estimate for the full sample is 0.08 (p-value = 0.41), from a control-group mean of 12.99. While their estimate is an intent-to-treat and our estimate is an average treatment effect, the alignment may be due to large take-up among disadvantaged populations. We find a large impact of 0.70 (p-value = 0.05) for male children and a smaller and insignificant impact of 0.093 (p-value = 0.42) for female children. Rossin-Slater and Wüst (2020) do not report results by gender.

Table 4.

Comparison to Other Causal Intergenerational Estimates and to Intergenerational Relationship Estimates

	(1)	(2)	(3)	(4)
Panel a. Intergenerational Treatment Effects of Preschool
	Years of Education, Age 25 Rossin-Slater and Wüst (2020)	Years of Education, Mid Twenties This study	Ever Arrested, Convicted, or Put on Probation, Twenty or Older Barr and Gibbs (2022)	Ever Arrested, Mid Twenties This study
Pooled	0.06 {12.13}†	0.08 {12.99}	−0.13 {0.28}	−0.09 {0.37}
Males	N/A	0.70 {12.08}	−0.23 {0.40}	−0.08 {0.59}
Females	N/A	0.09 {13.52}	−0.03 {0.17}	0.02 {0.21}
Parameter	Intent-to-Treat	Average treatment effect	Intent-to-Treat	Average treatment effect
Relevant Population	Children of disadvantaged Danish women. Women were born between 1935 and 1957. Children were born between 1955 and 1987.	Children of disadvantaged African-American individuals born in Ypsilanti, Michigan. One parent of each child participated in PPP and was born between 1957 and 1962. Children were born between 1973 and 1992.	Children of mothers whose mother had less than high school education. Mothers were born between 1960 and 1964.	Children of disadvantaged African-American individuals born in Ypsilanti, Michigan. One parent of each child participated in PPP and was born between 1957 and 1962. Children were born between 1973 and 2008.
Empirical Design	High-quality preschool available in municipality where mother resided when she was between three and seven years old.	One parent randomly assigned to high-quality preschool (PPP).	Head Start available in mother’s birth county when she was 4 or 5 years old.	One parent randomly assigned to high-quality preschool (PPP).
Panel b. Intergenerational Relationship of Crime Outcomes: Children’s Criminal Outcomes on Parents’ Criminal Outcomes
	Dobbie et al. (2018) Correlation	Dobbie et al. (2018) Causal	This Study, Control Group Correlation	This Study, Treatment Group Correlation
	0.04 {0.09}	0.184 {0.237}	0.32 {0.57}	−0.06 {0.40}
Children Population	Children born between 1980 and 1984 in the US (National Longitudinal Survey of the Young 1997).	Socioeconomically disadvantaged children residing in Sweden whose parents were involved in a criminal trial between 1997 and 2004.	Male children of disadvantaged African-American males born in Ypsilanti, Michigan. Male parents were control participants of PPP and were born between 1957 and 1962. Male children were born between 1973 and 2008.	Same as previous column for male children of male treatment participants of PPP.
Estimand	Coefficient from a regression of an indicator of criminal conviction of child between ages 15 and 17 on an indicator of parental incarceration before child turns 16. Regression is estimated in sample of parent-child pairs.	Same as previous column, except that parental incarceration is instrumented using a judge-leniency instrument.	Coefficient from a regression of an indicator of child ever being arrested up to the mid twenties on an indicator of whether parent was arrested up to age 22. Regression is estimated in sample of pairs of fathers and average male children.	Same as previous column.

Note: Column (1) of Panel a. displays the intergenerational treatment effect of high-quality preschool for children of disadvantaged women in Denmark on years of education at age 25, taken from Column (1) of Table A6 in Rossin-Slater and Wüst (2020). Column (2) displays the closest estimates from our study, taken from Table 3. Column (3) displays the intergenerational treatment effect of Head Start for children of disadvantaged women in the US on an indicator of ever arrested, convicted, or put on probation at age 20 or after, taken from Tables 2 (pooled) and 3 (males and females) of Barr and Gibbs (2022). Column (4) displays the closest estimates from our study, taken from Table 3. Column (1) of Panel b. displays OLS estimates from a regression of an indicator of children’s criminal outcomes (conviction between ages 15 and 17) on their parents’ criminal outcomes (incarceration before own child turns 16). Column (2) displays estimates of the same regressions as Column (1), based on Swedish administrative records and instrumenting parental incarceration using a judge-leniency instrument. Column (3) displays the closest estimate to Column (1) based on the data used throughout this paper. We limit the sample to the control original male participants with male children. Columns (4) is analogous in format to Column (3) when limiting the sample to the original treatment participants.

^†:In Columns (1), (2), and (4) of Panel a., we display the mean of the control group in curly brackets. In Column (3), we display the full-sample mean in curly brackets. In Panel b., we display the mean of the children’s dependent variable for children whose parents had any incarceration or arrest in curly brackets. In Column (2), the mean reported is for the full sample, as opposed to the sample of the socioeconomically disadvantaged.

Barr and Gibbs (2022) estimate the intergenerational impact of Head Start, using a similar approach to that of Rossin-Slater and Wüst (2020). They exploit availability of Head Start in a mother’s county of birth when she was 4 or 5 years old to estimate an intent-to-treat or reduced-form effect. Mothers were born between 1960 and 1964. Barr and Gibbs (2022) provide estimates for disadvantaged mothers, whose take-up may also have been high. They find a negative impact of −0.23 (p-value < 0.01) on ever being arrested, convicted, or put on probation at age twenty or after for male children, from a mean of 0.40. For female children, the impact is small and insignificant. Our estimates are also driven by male children. They are smaller in magnitude than theirs. For male children, we find an impact of −0.08 (p-value = 0.24) from a mean of 0.59. Crime is an activity mainly performed by men. When limiting the sample to male children of original male participants, our estimate is −0.21 (p-value = 0.11). Our estimates thus quantitatively and qualitatively align with those of the other studies in the literature aiming to identify causal intergenerational impacts of high-quality preschool. Our study solidifies previous evidence given the advantages already discussed.

A major result in this and previous studies of PPP is its effectiveness in reducing the criminal activity of its original participants. We investigate the intergenerational relationship of this outcome in Panel b. of Table 4. We report the slope estimate of a regression of an indicator of a child ever being arrested up to the mid-twenties (analyzed in this section) on an indicator of parental arrest. We provide estimates by treatment status and limit the sample to male children of the original male participants, given that crime is primarily a male activity.²⁸ The estimate of 0.32 for the control group indicates an expected positive correlation. This estimate is larger than the closest estimate in the literature of 0.04 reported by Dobbie et al. (2018). Our larger correlation in the control group is sensible given that these authors analyze a US representative sample pooling advantaged and disadvantaged parent-child pairs and including males and females, whereas we use a sample selected to be disadvantaged. The estimate for the treatment group is −0.06.²⁹ Although the correlations do not have a causal interpretation, their difference across experimental groups suggests that PPP is effective at breaking the intergenerational transmission of criminal activity.

The control-group estimate in Panel b. of Table 4 provides an estimate of the male-male intergenerational transmission of the probability of being arrested for disadvantaged individuals. This relationship can be estimated in non-experimental settings.³⁰ Treatment decreases the probability of being arrested for treatment parents by 24 percentage points. If the relationship estimated in the control group were causal, the predicted intergenerational impact of treatment on the probability of being arrested would be −0.24 × 0.32 = −0.08. We also consider an alternative calculation based on a causal estimate of the intergenerational transmission for disadvantaged individuals reported in Dobbie et al. (2018) and described in Panel b. of Table 4.³¹ This would yield a predicted intergenerational impact of −0.24 × 0.18 = −0.04. Either prediction provides a lower bound for the actual estimate of the intergenerational impact of PPP(−0.21, see Table 3). Our intergenerational estimate is larger than the predictions likely because, as documented in Section 4, treatment not only decreases the probability of being arrested for original treatments but also improves their skills, labor-market prospects, and marriage stability. The impacts on these multiple mediators suggest a greater intergenerational impact than that predicted by the one-to-one intergenerational transmission of the probability of being arrested.

6. Summary

The HighScope Perry Preschool Project was a pioneering early childhood education program designed to promote the social mobility of disadvantaged African-American children. The foundational principles of the program guide current practice and are incorporated in at least 30% of current Head Start programs (Elango et al., 2016). Using newly collected data, we examine its impact on the original participants through age 54 and on their adult children. We find substantial and lasting positive effects for the original treatment-group participants on cognition and beneficial personality traits contradicting claims on fadeout that are based on relatively short-term follow-ups. We also document long-lasting impacts on health using a rich set of measures that include overall health and cardiovascular indicators. The first-generation treatment-group participants have more stable adult home lives in terms of marriage and divorce and higher earnings in the childrearing years.

These benefits promote intergenerational mobility for their children. The children of treatment-group participants are less likely to be enrolled in special education programs and have fewer school suspensions than the children of control-group participants. They are more likely to be employed and in good health. They are much less likely to engage in crime. We find important differences in impacts by gender. The male children of the original male treatment-group participants receive the greatest benefits, consistent with a literature on the adverse effects of disadvantaged environments on boys (Autor et al., 2019). García and Heckman (2022) estimate that application of Perry to the currently eligible disadvantaged African-American children would reduce the black-white prime-age earnings gap by 42%. Given the commonality of the process of child development around the world, our findings generalize broadly.