Abstract

This study investigates the effects of welfare reform—a major policy shift in the United States that increased low-income mothers' employment and reliance on earnings instead of cash assistance—on the quality of the home environments mothers provide for their preschool-age children. Using empirical methods designed to identify plausibly causal effects, we estimate the effects of welfare reform on validated survey and observational measures of maternal behaviors that support children's cognitive skills and emotional adjustment and the material goods that parents purchase to stimulate their children's skill development. The results suggest that welfare reform did not affect the amount of time and material resources mothers devoted to cognitively stimulating activities with their young children. However, it significantly decreased emotional support provision scores, by approximately 0.3–0.4 standard deviations. The effects appear to be stronger for mothers with lower human capital. The findings provide evidence that welfare reform came at a cost to children in the form of lower quality parenting. They also underscore the importance of considering quality, and not just quantity, in assessing the effects of maternal work-incentive policies on parenting and children's home environments.

Introduction

In the decade leading up to the current millennium, the United States saw unprecedented increases in low-income unmarried mothers' employment rates. In 1992, before the 1990s welfare reforms (WRs), unmarried mothers aged 25–34 had a labor force participation rate of 66% and an employment rate of 58% (authors' calculations from the Annual Social and Economic Supplement [ASEC] of the Current Population Survey [CPS]). By 2000, when WR had been fully implemented, these figures increased to 80% and 75%, respectively (authors' calculations from the ASEC of the CPS). The reforms imposed time limits and work requirements as conditions for the receipt of cash assistance alongside other substantial expansions of work supports (most notably, the Earned Income Tax Credit [EITC]), contributing significantly to these trends (for WR, see Fang and Keane 2004; Johnson et al. 2012; Ziliak 2016; for EITC, see Bastian and Lochner 2022; Hoynes 2009). Although WR and the EITC have been fully implemented for decades, they remain in effect. Between 1992 and 2019 (the last pre-pandemic year), unmarried mothers' labor force participation rate increased by more than 10 percentage points, and their employment rate increased by 13 percentage points (authors' calculations from the ASEC of the CPS).

Despite clear labor supply effects, the 1990s work-incentive policies had heterogeneous effects on families' material circumstances. Hoynes and Patel (2018) found that the EITC improved economic circumstances among families with incomes at 75% to 200% of the federal poverty level but not among more disadvantaged families. WR positively affected earnings, income, and consumption in the early years (Ziliak 2016). However, after WR was fully implemented, it appeared to have mixed effects, with overall positive effects but also increases in deep poverty (Bollinger et al. 2009; Schoeni and Blank 2000; Shaefer and Edin 2018; Trisi and Sherman 2016). Han et al. (2021) found that WR increased consumption among unmarried mothers, particularly the most disadvantaged. Although some of these findings may seem inconsistent, work incentive–induced increases in earnings, income, and even consumption might not automatically translate to improvements in material circumstances. For example, employment can lead to increased expenses (e.g., on transportation, childcare, or prepared food) that might not always be offset by increased earnings.

Little is known about how policy-induced increases in women's employment have affected children's home environments. The quality of the home environment and the emotional support and learning opportunities that parents provide in that setting are key inputs into children's development and long-run success (Björklund and Salvanes 2011; Doepke et al. 2019). Aside from potential improvements in material well-being, a key pathway for the influence of work-incentive policies on children's home learning and developmental environments is through changes in the quantity and quality of parental time. Parental time and emotional investments are central to children's development, especially in children's first years of life, when they are most often in their parents' (generally mothers') care (Del Bono et al. 2016; Duncan et al. 2022; Kalil 2015).

Increased maternal employment may decrease mothers' time spent with children, resulting in poorer supervision or care and less time available to provide emotional support or foster children's involvement in enriching activities (Aizer 2004). However, studies have found that although working reduces the time mothers spend with children, mothers guard their quality time with children by cutting back the least on activities directly engaging children (Bianchi 2000; Hofferth and Sandberg 2001). In particular, a recent study using detailed time diary data found that EITC expansions led to reductions in maternal time spent with children in “passive” noninvestment activities (e.g., housework, errands, waiting, shopping, and relaxing) and volunteering and attending social events with their children. However, it did not reduce mothers' time spent reading, playing, and doing arts/crafts with their children; helping them with homework; and providing and consuming medical care (Bastian and Lochner 2022). Additionally, if maternal employment increases the use of high-quality childcare, it could favorably affect children's home learning and developmental environments. For example, Gelber and Isen (2013) used experimental data and found that low-income children's participation in Head Start increased parents' time investments in home learning activities, perhaps because parents acquired new information about the positive impacts of educational investments on children's skill development.

Nonetheless, for low-income families, increased employment could worsen parent–child interactions if work conditions (e.g., hours or shifts, tasks, dangers, commutes) are stressful or tiring, potentially compromising the quantity and quality of parental investments by depleting parents' attention or behavioral self-control (Gennetian and Shafir 2015). In the extreme, Paxson and Waldfogel (2003) found suggestive evidence that early WRs increased child maltreatment. However, greater labor market attachment could improve mothers' self-esteem and provide more structure, increasing positive parent–child interactions (Reichman and McLanahan 2001). Further, changes in parental stress or time use because of work-incentive policies need not arise exclusively from changes in parents' individual employment experiences (Morrill and Pabilonia 2015). For example, changes in fertility and living arrangements resulting from WR (Bitler et al. 2006) could affect parental stress or time use, although the expected direction of such an effect is ambiguous.

Few studies have investigated the plausibly causal effects of large-scale maternal work-incentive policies on the quantity or quality of parental time with children (one exception is Bastian and Lochner 2022, which focused on the EITC). A review of seven welfare demonstration experiments conducted in the early 1990s found little to no effect on parenting behaviors (e.g., exhibiting warmth, engaging in cognitive stimulation, and engaging in harsh parenting) or maternal depression or self-esteem (Chase-Lansdale and Pittman 2002). However, the experimental evidence is based on sparse findings from limited geographic areas and generally predated the post-1996 WR period. Thus, it is not clear how generalizable those findings are in the context of national WR as implemented by the Personal Responsibility and Work Opportunity Reconciliation Act of 1996 (PRWORA). In fact, Chase-Landsdale and Pittman concluded that much remains to be learned about connections between WR and parenting. In addition, a few quasi-experimental studies of maternal behavioral outcomes found that PRWORA led to decreases in low-income mothers' substance abuse and crime (Corman et al. 2013; Corman et al. 2014; Kaestner and Tarlov 2006), which may be relevant for the quality of young children's home environments.

In a related inquiry, Guldi et al. (forthcoming) estimated the effects of Supplemental Security Income benefits for low-income families with infants whose birth weight was below 1,200 grams relative to those whose infants had a slightly (up to 200 grams) heavier birth weight and who therefore were not eligible. The purpose of the study was to investigate the effects of gaining child benefits for this subset of very low birth weight infants. The authors found that the mothers whose children gained benefits were more likely to reduce their labor supply from full-time to part-time and to demonstrate higher quality parent–child interactions at 9 months, albeit not at 2 years. These results suggest that reduced maternal work led to better parenting during infancy. However, they may not be generalizable because only a small fraction of infants are born at such low weights, and those children often have significant health and developmental issues.

The present study adds to this limited body of work by investigating the effects of WR—a major policy shift that increased low-income mothers' employment and reliance on their earnings instead of cash assistance—on the quality of their children's home environments using empirical methods designed to identify plausibly causal effects. Our study is close in spirit to that of Bastian and Lochner (2022), but it focuses on a different work-incentive policy shift, uses a different nationally representative dataset, and focuses on the quality of children's home environments rather than using time diary data. Those environments were assessed using rich, well-validated survey and observational measures of maternal behaviors that support children's cognitive skills and emotional adjustment along with measures of the material goods that parents purchase to stimulate their children's skill development.

Our analysis begins by confirming that WR substantially increased employment among low-income mothers with young children. Next, we present estimates of the effects of WR on detailed, validated measures of the home environment collected in each survey year of the 1979 National Longitudinal Survey of Youth (NLSY). We focus on children aged 0–5 years because the strongest labor supply effects of WR were among mothers with young children (Fang and Keane 2004), and the early years are foundational for children's development. Our results suggest that WR did not significantly affect mothers' time and material resources devoted to cognitively stimulating activities with their young children. However, it significantly negatively affected mothers' provision of emotional support, and the effects appeared stronger for mothers with low human capital. The findings provide evidence that maternal work incentives under WR came at a cost to children in the form of lower quality parenting. Our results underscore the importance of considering quality in addition to quantity in assessing the effects of maternal work-incentive policies on parenting and children's home environments.

Welfare Reform in the United States

Enacted in 1996, PRWORA ended entitlement to welfare benefits under Aid to Families with Dependent Children (AFDC) and replaced it with Temporary Assistance for Needy Families (TANF) block grants to states. Key features of the legislation were time limits on cash assistance and work requirements as a condition for receiving benefits. States were granted considerable latitude in establishing eligibility and program rules subject to national guidelines under PRWORA that mandated work requirements and a five-year lifetime limit on the receipt of cash assistance.

Although WR is often dated to the PRWORA legislation, reforms began in the early 1990s, when the Clinton administration expanded the use of “welfare waivers” to allow states to make experimental changes to their AFDC programs. Many features of PRWORA, such as work requirements and time-limited welfare receipt, were integral to these earlier programs. Although not federally mandated, waivers were implemented in most states by the 1996 enactment of the federal PRWORA legislation. Specifically, major statewide waivers—defined in a 1997 report by the Council of Economic Advisors (CEA 1997) as those that substantially altered the nature of AFDC regarding work requirements and incentives, time limits, and family caps—were introduced in 29 states over 53 months, and TANF was implemented in all states over 17 months. Considering both waivers and TANF, states reformed their welfare programs over 64 months, from October 1992 through January 1998 (see Table A1; all tables and figures designated with an “A” are in the online appendix).

Methods

Data

We use restricted data from the 1979 cohort of the National Longitudinal Survey of Youth (NLSY79), which follows a nationally representative sample of more than 12,000 individuals aged 14–22 in 1979. The survey began that year and was conducted annually until 1994 and biennially thereafter (National Longitudinal Surveys 2022a). The observation period for our study, 1990 (a few years before any WRs were implemented) to 2006, allows all states to have fully implemented WR and avoids conflating our results with the effects of the Great Recession. The NLSY79 provides an observation period enveloping WR, has large sample sizes, and includes rich information on the home environment, maternal characteristics, and other relevant variables. To our knowledge, no available dataset is more appropriate for estimating the effects of WR on children's home environments using rigorous econometric techniques.

The NLSY79 includes demographic data on mothers (age, education, marital status, and employment) and their children (age, sex, race, and Hispanic ethnicity), as well as information on the number and ages of other children in the household, mothers' Air Force Qualifying Test (AFQT) scores, and state identifiers that we use to merge measures of WR implementation and other state policy and economic measures to the individual-level data.

We use an indicator for any WR (AFDC waiver or TANF) in a given month and year in the child's state of residence in childhood. Other state- and year-level variables included in the analyses are unemployment and poverty rates, personal income per capita, minimum wage, number of children receiving the National School Breakfast and Lunch Program benefits, population, number of Medicaid beneficiaries, and lagged welfare caseload. We also include two measures of state and year EITC generosity: (1) whether the state had a refundable EITC allowing filers to receive the full credit amount they are eligible for depending on their earnings and family composition, even if their owed taxes are below the EITC amount; and (2) a continuous measure of the state's EITC generosity, expressed as the state EITC rate as a percentage of the federal credit.1

All NLSY79 waves included the Home Observation Measurement of the Environment-Short Form (HOME-SF), and the data include overall scores and subscale scores for cognitive stimulation and emotional support (National Longitudinal Surveys 2022b). Overall, the HOME-SF assesses resources available in the home, as well as parental warmth and responsiveness, control and discipline, supervision, and cognitive stimulation—all of which are important dimensions of parenting (Chase-Lansdale and Pittman 2002). Thus, the HOME-SF scores characterize the quality of children's learning and developmental home environments.

The NLSY79 used separate age-appropriate scales for children aged 0–2 years (Table A2) and 3–5 years (Table A3), and both caregivers and in-home interviewers provided information. The NLSY created binary measures from the answers to each of the questions in each of these instruments. For children aged 0–2, the raw cognitive and emotional scores had a maximum of 9 points. For children ages 3–5, the maximum points were 14 for the raw cognitive score and 12 for the raw emotional scale. The NLSY calculated standardized measures of the overall and subscale scores based on the NLSY79 sample, with means of 100 and standard deviations of 15 for the entire sample. These validated and widely used measures of the cognitive stimulation and emotional support that parents provide in the home have been used in hundreds of research studies (Mott 2004).

Empirical Approach

Our analyses are based on a quasi-experimental difference-in-differences (DD) design that exploits variation in exposure to WR based on differential implementation timing across states. This approach is standard in the economics literature evaluating the effects of WR. The following reduced-form baseline DD specification relates changes in HOME-SF scores to the child's exposure to WR:

HOMEimst=π Welfarest-12+Ximstβ1+Vmstβ2+Zstβ3+αs+τt+[αst]+εismt.
(1)

The HOME-SF score (HOME) for the ith child born to mother m residing in state s and observed at time t is a function of WR (Welfare), measured here by an indicator for whether a given state had a major AFDC waiver (pre-TANF) in place or had implemented TANF for at least 12 months at the time of the assessment. We incorporate the 12-month lag (Welfarest-12) in our main analyses because the potential effects of WR on the quality of the home environment—operating through changes in maternal work, time, and resource constraints—may take time to materialize. In supplementary analyses, we explore effect dynamics more flexibly. The vector X denotes controls for child characteristics (age, sex, race, and ethnicity), and V denotes controls for the mother's characteristics (age, highest grade of schooling completed, and numbers of children of various ages). We estimate all models via ordinary least squares (OLS).

The validity of the DD approach hinges on the parallel trends assumption—in our case, that conditional outcomes for individuals in the control states are a valid counterfactual for the conditional outcomes for individuals in the treated states. That is, the assumption holds that trends in outcomes would have been similar in treated and control states in the absence of WR. Deviations from parallel trends would reflect unobserved time-varying factors differentially impacting the treated and control states. To account for potentially confounding policy shifts and other unobserved factors, we include the rich set of time-varying state factors (Zst) detailed earlier and in table notes, as well as fixed effects for the mother's state of residence (αs) and period (interview month and year; τt), which control for time-invariant state heterogeneity, national trends, and any seasonal variations in the demand for parenting inputs. We report state-clustered standard errors adjusted for arbitrary correlation in the error term (ε) across and within individuals in a given state and across survey waves. In supplementary analyses, we assess robustness across models that sequentially add sets of the control variables and when including state-specific linear time trends (αst) that allow all states (including early- and late-reform states) to have differential systematic trends over the entire sample period. However, we are careful in interpreting estimates from models that include state-specific linear time trends because those controls may capture part of the treatment effect in addition to the unobserved factors when the treatment response is dynamic (Wolfers 2006).

Given that the welfare caseload has primarily been low-educated, unmarried mothers (Bitler and Hoynes 2010), we limit our main sample to unmarried mothers with no more than a high school education. This group represents the population of interest—mothers at risk of relying on welfare—for whom effects of WR on employment, income, other household conditions, and behaviors should be strongest. The literature has shown weak or no effects of WR on marriage, suggesting that endogenous selection into our sample through marriage is not a concern. However, prior work found that WR reduced high school and college enrollment among disadvantaged adult women (Dave et al. 2012). To assess the importance of potential compositional selection effects for our sample, we estimate models of associations between WR and the transition from being unmarried in 1990 (pre-WR) to being married during our sample period and between WR and the transition from having low educational attainment (high school education or less) in 1990 to having more education. We find no evidence that WR is associated with subsequent marital status or educational attainment in our sample of mothers with very young children (not shown).

In additional analyses, we address substantively important questions and methodological issues. First, we assess heterogeneity in effects across children's ages (0–2 years vs. 3–5 years, as delineated by the NLSY) and sex, following the distinction between these two age periods in the child development literature (Kalil et al. 2012) and increasing evidence that the returns to parental inputs differ substantially by gender (Bertrand and Pan 2013). We also assess heterogeneity by pre-WR maternal human capital (proxied by educational attainment) and ability (proxied by AFQT scores), given prior research pointing to nonuniform effects of WR on women's material conditions depending on their initial level of disadvantage.

Second, an emerging literature has identified potential issues with a two-way fixed effects or DD setting with staggered adoption of the treatment—here, states implementing WR at different times (Callaway and Sant'Anna 2021; Goodman-Bacon 2021; Sun and Abraham 2021). In the presence of dynamic treatment effects, standard DD estimates could be biased because they may capture the true treatment effect plus additional terms reflecting deviations from parallel trends and bias due to treatment effect dynamics. The latter source of bias largely arises from using earlier treated units as a counterfactual for later treated units. Moreover, as Sun and Abraham (2021) showed through decomposition analyses, dynamic coefficients estimated within a standard event-study framework could also be biased in this setting.

To assess the importance of biases attributable to heterogeneous treatment effects within our staggered policy rollout, we implement a stacked DD estimator (Abouk et al. 2021; Baker et al. 2022; Cengiz et al. 2019). For each treated group, considering the state and period of initial treatment, we identify “clean” controls using not-yet-treated individuals from states that have not yet implemented WR. This technique avoids problematic comparisons revealed in the standard DD setting (i.e., including previously treated observations as controls) by construction and ensures that treatment effects are identified using only comparisons between treated individuals and individuals who have not yet been treated; individuals in a control state are dropped as counterfactuals when that state implements WR. Each stack in the stacked DD estimator represents a sample of individuals treated in a given treatment year (i.e., states that separately implemented reform in 1992, 1993, and so on) and their controls drawn from the not-yet-implemented states.2 We pool these stacks across all treatment years and estimate Eq. (1) for this pooled sample to identify the average policy impact; this estimation allows for stable state heterogeneity and overall trends to differ across treatment groups by further controlling for stack-specific state and period fixed effects.

We use the stacked DD approach instead of methods proposed by Sun and Abraham (2021) and Callaway and Sant'Anna (2021), which address limitations of the standard DD approach, for two main reasons. First, the stacked DD facilitates comparison with the standard DD approach because it is most similar and is transparent in its construction and use of counterfactuals for each treatment group–time cohort (observations treated in the same period). Second, the stacked DD approach is less computationally intensive than the other methods when using individual-level data with an extensive set of covariates and interactions.

To assess the validity of the parallel trends assumption, we further implement an event-study analysis for the stacked DD estimator, decomposing the treatment effect into separate leads and lags of the policy effect:

HOMEimst,k=j=J_J¯πjDst,kj+Ximst,kβ1+Vmst,kβ2+Zst,kβ3+αs,k+τt,k[+αs,kt]+εismt,k.
(2)

All subscripts and variables are defined as earlier, with k denoting the treatment group or stack, and αs,k and τt,k denoting the stack-specific state and period fixed effects. Dstj is a treatment indicator for an event (here, the state implementation of WR) occurring j years away from t. The vector π denotes the coefficients on the treatment effect, with the reference period being j – 1, the year of WR implementation.3 Finding that the estimates of π for the period [J_, j – 2] are equal to 0 would provide evidence supporting the parallel trends assumption. Moreover, the trajectory of the coefficients for the periods [0, J¯] informs any dynamics evident in the policy impact.

Finally, we assess patterns in the standard and stacked DD estimates across four samples: (1) unmarried mothers with low education (high school or less), who are at high risk of exposure to WR and represent our target group and main analysis sample; (2) unmarried mothers with more than a high school education, who are at relatively high risk of exposure to WR; (3) married mothers with low education, who are at moderate risk of exposure to WR; and (4) married mothers with high education (college degree or more), who are at very low risk of exposure to WR and thus represent a placebo group.4 Given that highly educated married mothers are generally ineligible for welfare, we would not expect statistically or substantively significant effects of WR for that group; significant effects would suggest spurious time-varying state trends.

Results

Table 1 shows mean weighted standardized scores on the overall HOME-SF scale and two subscales for the focal group of mothers with children aged 0–5 who were at high risk of relying on welfare (unmarried mothers with a high school education or less), as well as for all mothers, married mothers with a high school education or less, unmarried mothers with more than a high school education, and married mothers with at least a college education. The mothers in the high-risk group scored substantially below those in the other subgroups; lower educated married mothers scored above higher educated unmarried mothers, and college-educated married mothers scored the highest. All but the last group scored below the overall national and NLSY79 means of 100, which was expected because those groups represent a relatively disadvantaged subset of the population.

We start by confirming that WR significantly and substantially increased labor supply in our NLSY79 sample of low-educated, unmarried mothers with young children. Table 2 reports these results from both standard and stacked DD models, which identify plausibly causal effects. Estimates point to a substantial employment increase of approximately 9–13 percentage points (17% to 24% relative to the baseline mean) and a 30% to 52% increase in weeks worked, although the stacked DD estimates are imprecise and do not achieve statistical significance at conventional levels.5 That these estimates are higher than those documented in the literature6 is understandable. Other studies have focused on unmarried mothers regardless of educational level and did not estimate differences by their children's ages. By contrast, we focus on a target group of low-educated unmarried mothers who have young children, the group whose employment has been most strongly affected by WR.

We present our main estimates of the effects of WR on HOME-SF scores in Table 3, for both standard and stacked DD models. The standard DD estimates suggest that WR significantly reduced overall quality of the home environment—as reflected in a significant decrease in the standardized overall HOME-SF score—by 2.9 percentage points, an effect magnitude that represents approximately a 3.3% decrease (relative to baseline mean) or a 0.16-standard-deviation (SD) decline (relative to the SD for the treated sample; see Table 1). The next two columns indicate that virtually all the adverse impact is driven by a decrease in the emotional support component (a decrease of 4.95 percentage points, representing a 5.5% or 0.28-SD decrease); the estimated effect for cognitive support, albeit negative, is small and statistically insignificant. In the presence of dynamic treatment effect heterogeneity, these estimates could be biased. If the treatment effect for the states that had previously implemented WR grows over time (as the upcoming event-study analyses suggest may be the case), then using already-treated units as a counterfactual may lead to attenuation bias.

The stacked DD estimates reveal a similar pattern of results, although the effect magnitudes are markedly larger.7 These results indicate that WR lowered the overall quality of the home environment (by roughly 6.2%, or 0.29 SDs); again, most of this decrease is driven by the emotional component (7.3%, or 0.37 SDs), although the cognitive component shows a marginally significant decrease (by 3.9%, or 0.18 SD). Both the standard and stacked DD estimates are robust across models that sequentially add subsets of the control variables (Table A4).

The validity of the DD approach rests on unobservable factors trending similarly across treated and control states, in which case outcomes for similar mothers in states that had not yet implemented WR would be a plausible counterfactual for outcomes for the treated mothers in the states that had. We assess this assumption's validity in two ways. First, Table A5 displays estimates from supplementary analyses that parametrically control for state-specific trends. Our results remain robust with these additional trend controls in both the standard and the stacked DD models.

Second, Figure 1 displays the results of conditional event studies based on the stacked DD model, as specified in Eq. (2). The event-study framework permits a direct test for any differential pre-policy trends across treated and control states, providing a more explicit assessment of the parallel trends assumption. It also allows us to decompose the dynamics in the main stacked DD estimates (reported in Table 3), which represent an average effect over the post-policy window. Although decomposing time-specific effects this way can be a somewhat noisy endeavor, the event-study results underscore three main points.

First, the results are validating and speak to the quality of the natural experiment; the lead pre-policy effects are close to 0 and statistically insignificant in virtually all cases, indicating that trends in the outcomes between the treated and control units were parallel before WR implementation. Only for the cognitive component is there a slight indication of a pre-trend difference (i.e., the coefficient for the two-year lead is marginally significant). Figure A1 presents the results of event studies from stacked DD models that control for state-specific linear trends. These findings reveal that all lead policy effects are statistically insignificant and essentially 0. That is, the additional controls fully purge the minimal differential pre-policy trends seen in Figure 1.

Second, the marked decrease in the quality of the home environment for the treated mothers, relative to similar not-yet-treated mothers, materializes only after WR implementation. Third, we find indication, particularly when we control for state-specific trends (Figure A1), that the policy impact may strengthen as the post-policy window grows. Several potential channels could underlie this magnification. The WR-imposed work constraints likely operate and bind with a lag, thereby impacting a greater portion of current and potential welfare recipients in our sample of high-risk mothers over time. Thus, one would expect stronger policy effects over the medium term than in the short term. The dynamics could also reflect stronger effects due to growing cumulative exposure to WR among older children who were exposed at younger ages as time since implementation increases. Finally, the dynamics could reflect heterogeneity across early versus later state adoption of WR: in the stacked DD models, the short-term effects (e.g., one or two years post-WR) are identified from all or most treated states, whereas effects for 3–4 years post-policy implementation would be identified from only the earliest adopters.

Results reported in Tables 46 explore heterogeneity in the effects by child's age, maternal pre-WR human capital, and child's sex. Exposure to WR significantly lowered overall HOME-SF scores for infants and toddlers (aged 0–2 years) and preschool-age children (aged 3–5 years), with very similar estimates for the two age groups that were largely driven by the emotional subscale (Table 4).

We find some evidence that WR took a greater toll on the home environments of children whose mothers had lower levels of human capital (i.e., had less than a high school education or scored below the median on the AFQT), particularly for the emotional subscale and for AFQT scores (Table 5). Specifically, estimates from stacked DD models indicate a significant WR-associated decrease in scores on the overall HOME-SF scale (by 7.2%; 0.33 SD) and both cognitive (4.6%; 0.21 SD) and emotional (8.2%; 0.41 SD) subscales for children of mothers with below-median AFQT scores. Although the coefficients are negative for higher ability mothers, the magnitudes are much smaller and not statistically significant. When stratifying by child's sex, we find slightly larger effects for girls, particularly for the emotional subscale (Table 6). Overall, although the subgroup patterns suggest heterogeneity by maternal human capital and the child's sex, sample size constraints limit more precise comparisons and preclude stronger inferences.

Finally, we estimate the effects of WR on HOME-SF scores for unmarried mothers with more than a high school education (Table 7, panel A; the relatively high-risk group), married mothers with no more than a high school education (panel B; the moderate-risk group), and college-educated married mothers (panel C; the placebo group of mothers who are highly unlikely to be affected by WR). Across the 18 models and samples, virtually all estimates are statistically insignificant and close to 0.8 Thus, the effects of WR on HOME-SF scores are concentrated in the high-risk (target) group, for whom the corresponding estimates are shown in Table 3.

A related issue is that the samples of relatively and moderately disadvantaged mothers (panels A and B) are often used in studies of WR as an additional comparison group within a difference-in-difference-in-differences (DDD) framework. However, doing so imposes the additionally restrictive assumption that time-varying unobserved factors in any given state impact outcomes identically across groups. The large baseline differences call this assumption into question. Nevertheless, as a robustness check, DDD estimates can be derived by differencing out the DD effects in panels A and B of Table 7 from the corresponding DD estimates in Table 3 for our high-risk group. The estimated effects in panels A and B are statistically insignificant and small in magnitude, indicating that differences between DDD and our DD estimates would be small; if anything, the DDD estimates would be larger because some estimates in panels A and B are positive. Thus, in terms of both patterns and magnitudes, our estimates in Table 3 are insensitive to explicitly using the relatively and moderately high-risk groups as comparison groups within a DDD research design.

Discussion

This study investigated the effects of WR—a major policy shift in the United States that increased low-income mothers' employment and reliance on earnings instead of cash assistance through the welfare system—on the quality of the home environments of preschool-age children. The findings add to the small body of research exploring how large-scale work-incentive policies affect children's home environments, which are important inputs into children's development. Using a national sample and empirical methods designed to identify plausibly causal effects, we estimated the effects of WR on the quality of the home environment using widely validated survey and observational measures of maternal behaviors that support children's cognitive skills and emotional adjustment as well as material goods that stimulate their skill development. The results suggest that WR did not generally affect the time and material resources mothers devoted to cognitively stimulating activities with their young children but had significant and substantial negative effects on mothers' provision of emotional support. The effect sizes were substantial: on average, WR reduced the quality of mothers' emotional support by roughly one third of an SD, and we found suggestive evidence that the effects may be even larger for mothers with lower human capital.

The findings complement those of time-use studies. For example, Bastian and Lochner (2022) found that EITC expansions, another major work-incentive policy targeted to low-income families, reduced maternal time spent with children in passive, noninvestment activities but not time spent engaging in developmentally enriching activities with them. Our results also align with Bianchi's (2000) foundational finding that maternal employment was not associated with reductions in mothers' time spent with children because working mothers instead reduced their time on housework, their own leisure, and sleep. The findings are also broadly consistent with those from a previous study of older children (aged 10–14) that found adverse effects of WR on parent–child activities, children feeling close to their mothers, and mothers knowing their children's whereabouts, with effects generally concentrated among boys (Reichman et al. 2020). That study used data from the Monitoring the Future youth surveys, focused on a much older group of children, and considered different parenting-related outcomes than the current study.

Our finding that WR had significant and substantial negative effects on mothers' provision of emotional support is important because emotional sensitivity in parenting is associated with children's self-regulation, social functioning, and early cognitive skills (Eisenberg et al. 2001; Hane and Fox 2006; Kochanska 2002; Tamis-LeMonda et al. 2019). Further, numerous studies have found associations between corporal punishment, such as spanking, and adverse cognitive and socioemotional child outcomes (Gershoff and Grogan-Kaylor 2016).

Our results suggest that low-income mothers faced with stronger work demands were able to maintain the quantity of their investments in their children (i.e., reading to them or taking them on outings) but that the potential stressors or disruptions associated with mandated work requirements took a toll on the quality of those interactions in terms of emotional affection or positive approaches to discipline. We can only speculate about what such stressors might be, but research has established that many low-income mothers work nonstandard and irregular hours and that the transition from welfare to work can pose costly challenges for mothers seeking appropriate childcare and transportation (Carrillo et al. 2017; Gassman-Pines 2011).

This study's findings reveal the importance of considering both quantitative and qualitative aspects of parenting and the home environment in evaluating social policy change. Further, they raise the important question of whether the returns on parents' time investments to children's skills decline when parent–child interactions are of lesser quality. Findings from two recent studies, in conjunction with the findings from the current study, provide some indirect support for that scenario. Mullins (2022) simulated the combined effect of WR and EITC changes on children's skill acquisition and found that children whose mothers had strong employment skills benefited from the policies but that children whose mothers had weaker job skills lost ground in cognitive and behavioral skill development. Similarly, Agostinelli and Sorrenti (2021) found that the net effects of the EITC on reading, math, and behavioral outcomes were negative for low-wage parents but positive for parents with sufficiently high wages. Our suggestive findings of stronger adverse effects on home environments for mothers with lower human capital point to a potential pathway underlying the findings from those two studies. In concert with the stronger effects we found on the emotional subscale than the cognitive subscale, these findings suggest that the returns on parents' time investments may be lower when parent–child interactions are of lesser quality.

Another way to place our findings in context is to consider how easy or costly it is to improve home environments. Many parenting interventions for young children in low-income families aim to improve the quality of the home environment along both dimensions studied here. For example, a recent large-scale U.S. Health and Human Services–funded evaluation experimentally tested the impact of the leading nurse home visiting programs (Michalopoulos et al. 2019). These programs place intensive time demands on parents and are expensive—costing an average of approximately $6,600 per family for 44 weeks of services in 2012 dollars (Burwick et al. 2014)—but had only modest impacts on the quality of the home environment and only for select subscales. The Michalopoulos et al. (2019) study reported treatment impacts of .09 SDs on a measure of the home literacy environment but no impact on parental supportiveness (akin to the emotional support measure in our study). In addition, the well-known Early Head Start program achieved modest treatment impacts (of ∼.10 SD) on a wider range of measures of the home environment for children ages 2–3 but no impacts for the highest-risk mothers (i.e., those with the lowest human capital; Love et al. 2005). All told, it appears to be very hard for the leading interventions to improve the quality of the home environment for low-income families. The fact that WR substantially worsened home environments is thus a costly problem.

In terms of the broader literature on WR, our findings underscore the importance of studying the effects of social policies—particularly those focusing on low-income families—not only on the target population but also on the next generation. They also suggest a potential mechanism underlying recent findings from Dave et al. (2021) that WR led to increases in delinquent behaviors among teenage boys and substance use among both boys and girls, with larger effects for boys—decreased maternal provision of emotional support. The stronger effects for boys could reflect gender differences in noncognitive returns to parental inputs in the teenage years (Bertrand and Pan 2013). Although the Dave et al. findings suggest that WR placed children on compromised long-term human capital trajectories, the literature on longer term second-generation effects of WR is in its infancy and does not yet point to strong evidence-based conclusions.

Overall, this study's findings indicate that maternal work incentives as implemented by welfare reform came at a cost to children in the form of lower quality parenting and that the negative effects were substantially larger than the positive treatment impacts of any existing intervention to improve the quality of low-income children's home environments. Our findings also underscore the importance of considering quality, and not just quantity, in assessing the effects of maternal work-incentive policies on parenting and children's home environments and may at least partially explain very recent findings showing negative effects of work-incentive policies (WR and EITC expansion policies) on skill development for children whose mothers have limited human capital. Finally, although WR was first implemented more than 25 years ago, the same cash assistance framework is in place today, and learning about its effects can provide guidance to states contemplating changes to their TANF programs, inform future welfare reform efforts, and help anticipate effects of other current and proposed policies that impose time limits and tie program benefits to employment.

Acknowledgments

The authors are grateful to participants of the 2022 Society of Economics of the Household meeting, 2022 Southern Economic Association meeting, and 2023 NBER Summer Institute, Children section, for helpful comments. This research was conducted with restricted access to Bureau of Labor Statistics (BLS) data. The views expressed here are those of the authors and do not reflect the views of the BLS. This research was supported in part by the National Center for Advancing Translational Sciences, a component of the National Institutes of Health (NIH) under award UL1TR003017; the Department of Health and Human Services/Health Resources and Service Administration (HHS/HRSA) under award U3DMD32755; and the Robert Wood Johnson Foundation through its support of the Child Health Institute of New Jersey (grant 74260). The content is solely the responsibility of the authors and does not necessarily represent the official views of the NIH, HHS/HRSA, or the Robert Wood Johnson Foundation.

Notes

1

The national-level EITC was unchanged during our observation period except for one major expansion in 1993, and year indicators may account for that change. Nevertheless, supplemental analyses (not shown) confirm that the estimates are insensitive to including (1) the maximum federal EITC credit based on the mother’s number of children age 18 or younger in the household and the year in addition to all other covariates (including the two state EITC variables described in the main text), and (2) year × number of children fixed effects in addition to all other covariates (including the state EITC variables). The results from these supplementary analyses provide strong evidence that our estimated effects of WR are not confounded by the federal EITC.

2

The treatment effect in the stacked DD estimator reflects states that implemented AFDC waivers or TANF through 1996. The last batch of states to implement WR in 1997 cannot be considered as a treatment stack because no clean controls exist for individuals residing in these states: all states implemented WR (TANF or earlier AFDC waivers) by 1997, so there were no more not-yet-implemented states from which to draw. For comparison, we used the same sample period in stacked and standard DD models, although treatment effects in the former are never identified in observations from 1998 onward because everyone was treated in those years, and the later observations only help to account for variability in time-varying covariates (e.g., state policies and economic conditions, longer term national trends). Omitting data from 1998 onward produces very similar estimates in the stacked DD analysis (not shown), which is not surprising given that those years are not material to identifying the treatment effects. A related issue is that owing to the necessity of utilizing clean, not-yet-treated states as controls, the stacked DD estimation relies more on the states that were early adopters of WR for identification. We observe no statistically significant differences between waiver and nonwaiver states in the pre-WR (1990) poverty rate, minimum wage, fraction Democrat in the House of Representatives, fraction Democrat in the Senate, personal income per capita, unemployment rate, population percentage on Medicaid, EITC rate, or growth in welfare caseload change between 1980 and 1990 (not shown). Furthermore, in a probit model predicting early adoption of WR, none of these state characteristics are statistically significant predictors (not shown).

3

Because we are building in a 12-month lag for the policy impact (as described earlier), the period denoted by j = 0 represents the 12 months following the WR implementation.

4

Using 2006 data from both the American Community Survey and the ASEC of the CPS, we found that women we classified as being at high risk of exposure to WR (unmarried mothers with a high school education or less) were 4–5 times as likely to report receiving welfare in the past year as married mothers with a high school education or less, roughly 2 times as likely to report receiving welfare as unmarried mothers with more than high school, and 35–63 times as likely to report receiving welfare as college-educated married mothers (placebo group).

5

We also found significant increases in annual hours worked; as with weeks worked, these effects are driven by the extensive margin (increases in employment) rather than the intensive margin (increases in labor supply, conditional on the mother already being employed). We used an inverse hyperbolic sine (IHS) transformation for weeks and hours worked because the IHS approximates the natural log and is interpreted in a similar manner but has the advantage of retaining zeroes (almost 45% of mothers were not working at baseline and thus worked 0 weeks and 0 hours) (Bellemare and Wichman 2020). The reported baseline means in the tables are computed as the weighted means for all low-educated unmarried mothers.

6

For example, Grogger (2003) found that WR increased unmarried mothers’ employment by 3.7%. In supplementary analyses using the NLSY that were as comparable to that study as possible (from standard DD models for unmarried mothers with children aged 0–17), we found an estimated WR effect on employment of 3 percentage points (not statistically significant at conventional levels), or 4% of the baseline mean of 0.69 (not shown).

7

Table 2 shows the opposite pattern for employment (smaller stacked DD effect magnitudes for labor supply). Given the identification constraints in the stacked DD specification (no variation after 1998), we cannot capture longer term dynamics; even effects 3–4 years post-WR are identified from the earliest adopters only, which might partially explain the smaller labor supply estimates in the stacked DD models than in the standard models. We replicated those models using standard DD analyses (i.e., limiting the data through 1998 and thereby limiting the potential for longer term dynamics and relying on the early reform states for identification); the estimates diminished in magnitude (to a 6% increase in employment and a 20% increase in weeks worked), indirectly supporting this explanation. For the parenting outcomes, the larger stacked DD estimates relative to the standard DD estimates would suggest that longer term effects are less important for those outcomes than for labor supply or that the standard DD estimates are even more downwardly biased than the standard DD labor supply estimates. Many forces could be at play and reconciling these patterns is difficult. Moreover, our standard errors are not precise enough to draw firm empirical conclusions about statistically significant differences between the standard and stacked DD estimates.

8

For the two samples of higher educated mothers (panels A and C), the effect is marginally significant (at the 10% level) for the cognitive scale. This low significance rate among the 18 specifications is what we would expect as a result of a type I error.

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Supplementary data