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Does Money Really Matter? Estimating Impacts of Family Income on Young Children's Achievement With Data From Random-Assignment Experiments [1]

['Greg J. Duncan', 'Pamela A. Morris', 'Chris Rodrigues']

Date: 2011-09-20

Abstract Social scientists do not agree on the size and nature of the causal impacts of parental income on children's achievement. We revisit this issue using a set of welfare and antipoverty experiments conducted in the 1990s. We utilize an instrumental variables strategy to leverage the variation in income and achievement that arises from random assignment to the treatment group to estimate the causal effect of income on child achievement. Our estimates suggest that a $1,000 increase in annual income increases young children's achievement by 5%–6% of a standard deviation. As such, our results suggest that family income has a policy-relevant, positive impact on the eventual school achievement of preschool children. Keywords: income, child achievement, causal estimates

Despite countless studies estimating the association between family income and child development, there is still a lively debate about how, and even whether, a policy-induced increase in family income would be spent in ways that would boost the achievement of children (Duncan & Brooks-Gunn, 1997; Magnuson & Votruba-Drzal, 2009; Mayer, 1997, 2002). The estimation problem is a familiar one: Most studies of income effects are based on nonexperimental data and are susceptible to biases from unmeasured parent and family characteristics, as well as from bidirectional influences of children on their parents. Yet, understanding how much, if any, of the association between parents’ income and children's achievement is causal is critical to advancing developmental theory as well as improving our understanding about whether interventions designed to increase income are likely to promote children's academic achievement (Gennetian, Magnuson, & Morris, 2008). We contribute to this field of study using data from 16 implementations of welfare-to-work experiments, all of which assigned low-income and welfare-recipient single parents at random to control groups or to various welfare and employment policy treatments. All policy treatments had components designed to increase employment and reduce welfare; some, but not all, were designed to increase parents’ income as well. We use the exogenous variation in family income generated by random assignment (as well as the variation across the experimental treatment sites) to identify the effects of income on the achievement of young children. In doing so, we contribute to prior research to generate an estimate for the effect of income on young children's achievement as they enter the elementary school years.

Procedures and Measures Data in each study were compiled from several sources. One, basic demographic information, including prior employment history, on all sample parents at the point of random assignment (baseline) to the program and control groups was completed by welfare and program office staff. Two, administrative records provided information on welfare receipt, employment, and program payments prior to random assignment and during the follow-up period. Three, a parent survey was conducted with each family 2–5 years after baseline, depending on the study. And four, in some studies, children were tested to determine academic achievement and/or elementary school teachers completed a survey about children's academic achievement 2–5 years after baseline. Participants volunteered for New Hope; in all other cases their application to the welfare system or receipt of welfare required participation in the random assignment and the administrative sources of data collection. Parents could opt to not respond to the evaluation surveys, but response rates in all studies were high—between 71% and 90%, and nonresponse bias analyses conducted as part of the original studies confirmed the equivalence of program and control groups in these respondent samples (D. Bloom et al., 2000, 2002; Bos et al., 1999; Freedman et al., 2000; Gennetian & Miller, 2000; Hamilton et al., 2001; McGroder, Zaslow, Moore, & LeMenestrel, 2000; Morris & Michalopoulos, 2000). Family income Our key endogenous variable was family income. For all sample members in the six U.S. studies, administrative records provided data on monthly cash assistance and Food Stamp benefits and any cash supplement payments provided by the earnings supplement programs, as well as quarterly earnings in jobs covered by the Unemployment Insurance system. For the Canadian SSP samples, administrative records provided information on receipt of Income Assistance and receipt of SSP supplement payments, while the parent survey collected data on earnings from employment. For each quarter following random assignment, we computed an average quarterly parent income based on the sum of earnings, AFDC/Temporary Assistance for Needy Families/Income Assistance and supplement payments, and Food Stamp payments. Note that this income measure omits self-employment and informal earnings (except in SSP), other public transfers, private transfers, and earnings from family members other than the sample member (although nearly the entire sample was composed of single parents). All income amounts have been inflation-adjusted to 2001 prices using the Consumer Price Index. Canadian dollars were converted to American dollars before being adjusted for inflation. From this information, average annual income (in $1,000s) and log average annual income were computed over the time between random assignment and the assessment of child achievement. School achievement Children's cognitive performance or school achievement was measured using parent or teacher report or test scores. The SSP, Connecticut, FTP, New Hope, MFIP, and LA-GAIN studies included parent reports of children's achievement on a 5-point rating of how well children were doing in school (n = 7,958; these are based on a single item measure; except in SSP, these are based on an average of children's reported functioning in three academic subjects). Teacher reports of achievement—collected in Connecticut, New Hope, and NEWWS (n = 2,074)—were based on items from the Academic Subscale of the Social Skills Rating System (Gresham & Elliot, 1990). On this 10-item measure, teachers compared children's performance with that of other students in the same classroom on reading skill, math skill, intellectual functioning, motivation, oral communication, classroom behavior, and parental encouragement (internal consistency α = .94). Test scores included the Peabody Picture Vocabulary Test (Dunn & Dunn, 1981) for children ages 4–7 at the 36-month follow-up in SSP (n = 1,039), a math skills test containing a subset of items from the Canadian Achievement Tests (2nd ed.) for children ages 8 and up at the 36-month follow-up in SSP (n = 573), the Bracken Basic Concept Scale (Bracken, 1984) for children in NEWWS at the 2-year follow-up (n = 2,867), and the Math (N = 2,078) and Reading (N = 2,078) scores from the Woodcock-Johnson Psycho-Educational Battery—Revised (Woodcock & Johnson, 1989–1990) for children in NEWWS at the 5-year follow-up, all well validated and reliable tests of children's cognitive performance. Consistent with the approach of Morris, Duncan, and Clark-Kauffman (2005) using these same data, to provide comparability in outcomes across studies, these achievement outcomes were standardized in our research by subtracting study-specific means and dividing by study-specific control-group standard deviations. A similar approach was utilized in other research involving multiple studies in which each study collected slightly differing measures of achievement (see Anderson, 2008). Combining across measures allowed us to test whether our results were robust across alternative measures of children's achievement. Parent and teacher reports of children's achievement in these data were modestly correlated (r = .37), whereas, not surprisingly, teacher reports and test scores were more highly associated (r = .49–.54 between teacher reports and ratings on the Woodcock Johnson tests of math and reading). Important for this analysis, tests of whether experimental impacts on child achievement varied by source of report could not reject the null hypothesis of equivalence. That is, we interacted source-of-report dummies with the experimental dummy in models predicting child achievement. We found no significant differences in the experimental impacts depending on the source of achievement report, F(2, 9112) = 0.33, p = .72. Also, when we estimated impacts on child achievement in the individual studies in which multiple measures were available, we did not find significant interactions between source-of-report dummies and the experimental assignment indicator. Proportion of quarters employed From our Unemployment Insurance quarterly earnings data we calculated parental employment for each quarter of the follow-up period. Sample members were coded as having been employed in a quarter if their earnings for that quarter were greater than zero. Because these studies had differing lengths of follow-up, we calculated the proportion of quarters employed over follow-up by counting the numbers of quarters employed and dividing by the number of quarters in follow-up. Employment hours For the SSP, Connecticut, NEWWS (2-year follow-up only), and LA-GAIN studies, employment in formation was collected via the parent surveys. For each job parents had between random assignment and the survey, parents were asked to report the month and year in which they started and ended each job. Additionally, parents were asked to report for each job the number of hours worked per week when they left the job (or currently if still working). Respondents were asked to report all jobs, including self-employment and any other employment that may have taken place informally or out of state. Average hours employed per quarter over the follow-up was computed using the employment information on all jobs listed in the parent survey. Welfare receipt Monthly or quarterly welfare receipt from public assistance records was collected for all years of the follow-up period for each study. Proportion of quarters receiving any welfare was computed for all years of the follow-up using these data. Sample members were coded as having received welfare in a quarter if their welfare payments for that quarter were greater than zero. Our welfare variable is the average welfare receipt rate across all quarters of the follow-up period. Other control variables Covariates included in the first- and second-stage models were baseline parental and family characteristics (no baseline data were collected on children's outcomes in these studies). Administrative data and baseline surveys taken just prior to random assignment provided the following information: comparable pre-random-assignment measures of child age, number of years of receipt of cash assistance prior to baseline, average earnings in the year prior to baseline and its square, measures of whether the parent was employed in the year prior to baseline, whether the parent had a high school degree or general equivalency diploma, age of the child, whether the parent was a teenager at the time of the child's birth, the marital status of the parent, the number of children in the family, the age of the youngest child in the family, and the race/ethnicity of the parent. We also included controls for length of follow-up and type of achievement assessment, as well as dummy variables representing site/study controls.

Analysis Strategy As with Ludwig and Kling (2007), we capitalized on program and site variation using an instrumental variables (IV) estimation strategy (for greater discussion of this approach, see Gennetian et al., 2008; Gennetian et al., 2005). IV estimation is designed to improve one's ability to draw causal inferences from nonexperi-mental data. The basic idea is simple: If one can isolate a portion of variation in family income that is unrelated to unmeasured confound variables and then use only that portion to estimate income effects, then the resulting estimates are likely to be free from omitted-variable bias. In effect, IV methods seek to approximate experiments by focusing only on “exogenous” variation in family income caused by some process that is completely beyond the control of the family. In our case, random assignment to treatment or control groups in the various welfare experiments was an excellent candidate for an IV variable because families had no say in whether they were assigned to the experimental or control group as a function of the lottery-like random assignment process. More formally, we used interactions between treatment group assignments (T) and site (S) as instrumental variables to isolate experimentally induced variations in income (Inc) and achievement (Ach) across program models (ε is the error term). With X denoting baseline covariates, the models are shown in the following equations: Inc = TSγ 1 + Sγ 2 + Xβ 1 + ε 1 (1) and Ach = I n ^ c λ 1 + S λ 2 + X β 2 + ε 2 . (2) In effect, Equation 1 estimates Inc on the basis of experimental assignment and controls by site, whereas Equation 2 regresses the predicted level of Inc taken from Equation 1 on child achievement. The inclusion of the same control variables in Equation 2 as in Equation 1 and, importantly, of site fixed effect dummies ensures that the only variation in Inc used in the estimation of Ach comes from the lottery-based assignment to treatment and control groups by site. The success of IV models such as those seen in Equations 1 and 2 depends on the strength of first-stage prediction of income on the basis of being randomly assigned to the program treatment groups. Our site-based instruments had relatively strong predictive power. In the case of prediction of parents’ annual income and log income, the F statistics for the instruments when using program components that interacted with treatment group assignment as instruments were 45.68 and 26.64, respectively, and the F statistics for the instruments when using the Site × Treatment Group interactions as instruments were 15.59 and 9.71, respectively. This is important because it has been shown that weak instruments can result in potentially biased IV estimates as well as large errors in the second stage of the procedure. In our case, the F statistics show that our instruments are close to or exceed recommended levels (Bound, Jaeger, & Baker, 1995). Exclusion restrictions required that our random-assignment instruments affect achievement only through their effect on income (Angrist, Imbens, & Rubin, 1996). There are several reasons why this assumption might not have been met in our studies. First, some programs provided child care subsidies and others mandated mothers’ participation in educational activities. Because both center-based child care (see e.g., National Institute of Child Health and Human Development Early Child Care Research Network & Duncan, 2002) and maternal schooling (see e.g., Magnuson, 2003) have been linked to child achievement, these program elements provide ways in which assignment to these programs could have influenced achievement independently of income. Because we could account for these effects of the treatment that occurred alongside the changes in income we observed for all the children in the sample, we estimated Models 1 and 2 for a reduced set of programs that provided neither child care subsidies nor education mandates (leaving us with NEWWS–LFA, LA-GAIN, SSP, and Connecticut for the analysis). These provided arguably our least biased estimates of the effects of income on child achievement. A second concern was that all of the intervention studies sought to increase maternal employment and reduce welfare use. Maternal employment could have an independent effect on children's achievement by altering parental time allocation and thus violate the exclusion restriction (see e.g., Brooks-Gunn, Han, & Waldfogel, 2002; Waldfogel, Han, & Brooks-Gunn, 2002). Prior research has also suggested that welfare receipt may itself have an independent effect on children because of the stigma associated with welfare receipt, although the evidence on this issue is mixed (see e.g., Levine & Zimmerman, 2005). To address this concern, we estimated a more complete version of Models 1 and 2 in which time spent in employment and welfare receipt were treated as additional endogenous variables.

Results Before estimating our model on our full pooled sample, we estimated the set of impacts on economic and child achievement measures, as shown in . The top panel pools studies by type of program (i.e., program components); the bottom panel shows study-specific results. In all models, baseline child, parental, and family characteristics are included as control variables.1 Table 3 Dependent variables IV model results Program type and study/site Prop. of quarters employed over follow-up Average annual income (in $l,000s) Log average annual income Prop. of quarters receiving any welfare over follow-up Child achievement Effects of income on child achievement Effects of log income on child achievement Program type (not mutually exclusive) Earnings supplements (n = 8,941) 0.086 (0.010)*** 1.468 (0.158)*** 0.137 (0.018)*** –0.035 (0.010)*** 0.076 (0.024)*** 0.052 (0.017)*** 0.554 (0.188)*** Work first (n = 9,957) 0.079 (0.010)*** 0.446 (0.156)*** 0.025 (0.021) –0.022 (0.010)** 0.040 (0.025) 0.089 (0.064) 1.627 (1.710) Education/training first (n = 6,017) 0.044 (0.014)*** 0.308 (0.196) 0.046 (0.025)* –0.003 (0.013) 0.027 (0.037) 0.089 (0.130) 0.596 (0.852) Time limits (n = 2,631) 0.061 (0.016)*** 0.505 (0.251)** 0.033 (0.035) –0.014 (0.015) 0.064 (0.041) 0.127 (0.105) 1.926 (2.461) Child care assistance programs (n = 4,084) 0.072 (0.013)*** 0.961 (0.244)*** 0.074 (0.031)** 0.001 (0.013) 0.050 (0.034) 0.052 (0.037) 0.681 (0.543) Study/site Self-Sufficiency Project (SSP) British Columbia (n = 2,131) 0.076 (0.023)*** 1.609 (0.327)*** 0.146 (0.031)*** –0.056 (0.020)*** 0.112 (0.050)** 0.070 (0.034)** 0.768 (0.375)** New Brunswick (n = 1,844) 0.135 (0.023)*** 1.916 (0.274)*** 0.192 (0.035)*** –0.142 (0.023)*** 0.125 (0.054)** 0.065 (0.030)** 0.648 (0.306)** SSP Plus–New Brunswick (n = 471) 0.116 (0.047)** 2.244 (0.455)*** 0.243 (0.071)*** –0.170 (0.043)*** 0.061 (0.113) 0.027 (0.052) 0.252 (0.491) Connecticut's Jobs First (n = 1,521) 0.053 (0.021)** 0.813 (0.362)** 0.074 (0.041)* 0.038 (0.020)* 0.032 (0.054) 0.040 (0.069) 0.436 (0.779) MFIP Urban Full (n = 1,101) 0.114 (0.022)*** 1.302 (0.409)*** 0.130 (0.057)** 0.071 (0.022)*** 0.045 (0.056) 0.035 (0.044) 0.345 (0.461) Urban Incentives Only (n = 988) 0.050 (0.024)** 0.914 (0.413)** 0.109 (0.063)* 0.105 (0.024)*** –0.016 (0.062) –0.018 (0.068) –0.150 (0.569) Rural Full (n = 378) 0.086 (0.041)** 1.630 (0.585)*** 0.158 (0.075)** 0.077 (0.039)** –0.013 (0.093) –0.008 (0.057) –0.081 (0.591) New Hope (n = 1,049) 0.065 (0.023)*** 1.630 (0.541)*** 0.125 (0.047)*** –0.023 (0.023) 0.034 (0.066) 0.021 (0.041) 0.272 (0.533) NEWWS Atlanta LFA (n = 2,324) 0.046 (0.023)** 0.317 (0.286) 0.043 (0.029) –0.020 (0.022) 0.074 (0.059) 0.232 (0.264) 1.705 (1.663) Atlanta HCD (n = 2,607) 0.020 (0.021) 0.398 (0.262) 0.055 (0.027)** –0.007 (0.019) 0.101 (0.056)* 0.255 (0.205) 1.835 (1.265) Grand Rapids LFA (n = 1,458) 0.104 (0.027)*** 0.072 (0.452) –0.045 (0.062) –0.074 (0.028)*** 0.030 (0.070) 0.414 (2.720) –0.667 (1.873) Grand Rapids HCD (n = 1,388) 0.026 (0.026) 0.004 (0.462) –0.007 (0.056) 0.011 (0.027) –0.050 (0.078) –12.823 (1,511.755) 7.043 (54.664) Riverside LFA (n = 1,896) 0.121 (0.028)*** 0.095 (0.497) –0.042 (0.077) –0.079 (0.029)*** 0.007 (0.070) 0.071 (0.801) –0.162 (1.732) Riverside HCD (n = 2,022) 0.099 (0.024)*** 0.557 (0.354) 0.072 (0.053) 0.007 (0.024) –0.036 (0.066) –0.065 (0.123) –0.505 (0.971) LA-GAIN (n = 169) –0.004 (0.062) –1.047 (0.884) –0.112 (0.096) 0.009 (0.045) 0.000 (0.157) 0.000 (0.150) –0.003 (1.405) FTP (n = 1,110) 0.069 (0.022)*** 0.137 (0.330) –0.019 (0.059) –0.084 (0.020)*** 0.112 (0.063)* 0.816 (2.041) –6.021 (19.141) Open in a separate window All types of programs boosted employment to roughly similar degrees, although the earnings supplement programs produced the largest impacts on family income, amounting to nearly $1,500 per year. Welfare use fell the most in the earnings supplement programs as well. Although the point estimates of impacts on achievement were positive for all program types, only in the case of the earnings supplement programs was the coefficient statistically significant. The effect size was small, however, amounting to less than one tenth of a standard deviation. The study-specific estimates were variable and often imprecise but generally conformed to the impact patterns of their program type. Program impacts on income ranged from –$1,000 to +$2,200 but were positive and statistically significant only for the earnings supplement programs. Program impacts on achievement were positive and statistically significant for only four of the 16 programs, two of which supplemented earnings and two of which did not. The final two columns of show preliminary IV estimates of the effects of annual and log income on child achievement when income was taken to be the only endogenous variable. These coefficients amount to the ratio of program impacts on child achievement to the program impacts on income. Coefficients in the top panel are all positive in sign, although only in the earnings supplement programs are they statistically significant. Site-specific IV estimates show that almost all coefficients are positive in sign, although many of these coefficients have large standard errors. Pooled IV Estimates The full power of our IV approach comes from pooling data across all studies. In effect, in any given study, IV estimation leveraged the variation in family income due to random assignment to either the control or experimental group within each program or site—thus ensuring that this variation was unrelated to personal characteristics of the program participants—to predict the relationship between income and child achievement. In the pooled model, we leveraged the variation in impacts on income and child achievement across the studies and sites. This variation is depicted graphically in (see Ludwig & Kling, 2007), where the distance between each point and the x-axis represents the deviation of the group's average income from the overall site's average income and where the distance of each point from the y-axis represents the difference between the group's average child achievement level and the overall site's achievement level. Open in a separate window If income mattered for child achievement, we would have expected that the treatment group/site combinations with the biggest positive income deviations would also have the biggest positive achievement deviations. When a trend line was fit through these 28 points, the slope of the line (.0599) was equal to the IV estimate of the effect of income on child achievement including only site dummies as covariates and using Site × Treatment Group inter actions as instruments.2 The interpretation of the slope is that each $1,000 increase in income was associated with a .06 standard deviation increase in child achievement. First-stage estimates of our IV models were virtually identical to the impacts shown in the second and third columns of (see ). This is as was expected because the two sets of estimating equations differed only in that the study-by-study estimates allowed for study-specific coefficients on control variables, whereas the pooled model constrained control coefficients to be identical across studies. Table 4 Dependent variables All studies Reduced set of studies Variables interacted with treatment (instruments) Average annual income (in $l,000s) Log average annual income Prop. of quarters receiving any welfare over follow-up Prop. of quarters employed over follow-up Average annual income (in $l,000s) Log average annual income Prop. of quarters receiving any welfare over follow-up Average hr employed per quarter Program type (not mutually exclusive) Earnings supplements 1.567 (0.117)*** 0.157 (0.015)*** –0.044 (0.007)*** 0.077 (0.008)*** 1.850 (0.134)*** 0.178 (0.016)*** –0.103 (0.009)*** 50.835 (4.417)*** Work first 0.150 (0.113) –0.002 (0.015) –0.030 (0.007)*** 0.075 (0.007)*** 0.096 (0.200) –0.004 (0.024) –0.047 (0.013)*** 38.937 (6.580)*** Education/training first 0.303 (0.121)** 0.047 (0.016)*** 0.001 (0.008) 0.043 (0.008)*** Time limits –0.557 (0.221)** –0.057 (0.029)** 0.022 (0.014) –0.054 (0.014)*** –1.171 (0.333)*** –0.108 (0.040)*** 0.182 (0.022)*** –67.197 (10.934)*** Child care assistance programs –0.100 (0.179) –0.020 (0.023) 0.044 (0.011)*** –0.011 (0.012) F (instruments) 45.68*** 26.64*** 12.72*** 56.42*** 67.10*** 42.03*** 50.69*** 58.85*** Model R2 0.259 0.134 0.234 0.274 0.269 0.147 0.168 0.236 Model F 202.96*** 89.77*** 177.43*** 219.28*** 113.67*** 53.24*** 62.30*** 95.69*** Sample size 18,667 18,667 18,667 18,667 8,073 8,073 8,073 8,073 Study/site Self-Sufficiency Project (SSP) British Columbia 1.577 (0.205)*** 0.141 (0.027*** –0.055 (0.013)*** 0.081 (0.013)*** 1.594 (0.194)*** 0.143 (0.023)*** –0.054 (0.013)*** 40.848 (6.353)*** New Brunswick 2.007 (0.207)*** 0.197 (0.027)*** –0.146 (0.013)*** 0.119 (0.014)*** 2.007 (0.196)*** 0.198 (0.024)*** –0.145 (0.013)*** 56.871 (6.421)*** SSP Plus–New Brunswick 2.405 (0.340)*** 0.263 (0.044)*** –0.161 (0.021)*** 0.178 (0.022)*** 2.438 (0.321)*** 0.265 (0.039)*** –0.160 (0.021)*** 74.042 (10.528)*** Connecticut's Jobs First 0.764 (0.242)*** 0.068 (0.031)** 0.034 (0.015)** 0.056 (0.016)*** 0.776 (0.229)*** 0.067 (0.028)** 0.032 (0.015)** 22.594 (7.507)*** NEWWS Atlanta LFA 0.299 (0.196) 0.040 (0.025) –0.019 (0.012) 0.043 (0.013)*** 0.166 (0.306) 0.035 (0.037) –0.024 (0.020) 7.911 (10.051) Atlanta HCD 0.296 (0.185) 0.050 (0.024)** –0.005 (0.012) 0.015 (0.012) Grand Rapids LFA 0.108 (0.247) –0.040 (0.032) –0.077 (0.015)*** 0.107 (0.016)*** 0.096 (0.433) –0.055 (0.052) –0.095 (0.028)*** 78.708 (14.188)*** Grand Rapids HCD 0.147 (0.254) 0.000 (0.033) –0.011 (0.016) 0.040 (0.017)** Riverside LFA 0.163 (0.233) –0.034 (0.030) –0.074 (0.014)*** 0.122 (0.015)*** 0.285 (0.383) 0.009 (0.046) –0.058 (0.025)** 68.730 (12.549)*** Riverside HCD 0.554 (0.220)** 0.088 (0.028*** –0.005 (0.014) 0.095 (0.014)*** LA–GAIN –0.846 (0.726) –0.113 (0.094) –0.002 (0.045) –0.003 (0.047) –0.860 (0.687) –0.108 (0.083) –0.001 (0.045) –1.253 (22.522) MFIP Urban Full 1.317 (0.284)*** 0.135 (0.037)*** 0.067 (0.018)*** 0.116 (0.019)*** Urban Incentives Only 1.105 (0.302)*** 0.120 (0.039)*** 0.099 (0.019)*** 0.056 (0.020)*** Rural Full 1.552 (0.486)*** 0.135 (0.063)** 0.066 (0.030)** 0.088 (0.032)*** New Hope 1.355 (0.292)*** 0.104 (0.038)*** –0.041 (0.018)** 0.049 (0.019)** FTP 0.037 (0.283) –0.039 (0.037) –0.083 (0.018)*** 0.068 (0.018)*** F (instruments) 15.59*** 9.70*** 18.30*** 22.66*** 26.10*** 17.15*** 23.32*** 26.35*** Model R2 0.259 0.135 0.243 0.277 0.269 0.148 0.171 0.239 Model F 151.61*** 67.36*** 138.89*** 165.64*** 95.61*** 45.04*** 53.53*** 81.63*** Sample size 18,667 18,667 18,667 18,667 8,073 8,073 8,073 8,073 Open in a separate window presents ordinary least squares (OLS) and second-stage IV estimates from a series of achievement models. These models all utilized the pooled data, which represented our preferred models in allowing us to estimate the unique effects of income. We first present the findings using all studies (which include some for which we could not fully control for all the other potential mediators of program impacts), and then we present the results from models using the subset of studies for which we could model key mediators of impacts alongside income (which arguably present our least biased estimates). Table 5 OLS Program type as instruments IV Sites as instruments IV Model and variable Log income Annual income Log income Annual income Log income Annual income All studies Model 1 Income 0.006 (0.002)*** 0.049 (0.016)*** 0.052 (0.016)*** Log income 0.025 (0.016) 0.453 (0.173)*** 0.438 (0.162)*** Model 2 Income 0.006 (0.002)** 0.029 (0.032) 0.042 (0.029) Log income 0.043 (0.021)** 0.216 (0.270) 0.291 (0.236) Average hr employed per quarter (in 100 hr) Proportion of quarters employed over follow-up 0.004 (0.040) 0.006 (0.041) 0.246 (0.530) 0.332 (0.481) –0.127 (0.420) 0.021 (0.365) Proportion of quarters receiving any welfare over follow-up –0.159 (0.034)*** –0.179 (0.037)*** –0.221 (0.945) –0.283 (0.941) –0.512 (0.290)* –0.559 (0.294)* Sample size 18,667 18,667 18,667 18,667 18,667 18,667 Reduced set of studies Model 1 Income 0.004 (0.003) 0.063 (0.019)*** 0.060 (0.019)*** Log income 0.000 (0.024) 0.649 (0.209)*** 0.611 (0.201)*** Model 2 Income 0.000 (0.003) 0.003 (0.043) 0.062 (0.035)* Log income –0.015 (0.028) 0.032 (0.411) 0.539 (0.316)* Average hr employed per quarter (in 100 hr) 0.019 (0.011)* 0.022 (0.011)* 0.180 (0.152) 0.181 (0.144) –0.029 (0.113) 0.014 (0.109) Proportion of quarters employed over follow-up Proportion of quarters receiving any welfare over follow-up –0.092 (0.050)* –0.077 (0.054) –0.193 (0.789) –0.190 (0.804) –0.128 (0.638) –0.065 (0.670) Sample size 8,073 8,073 8,073 8,073 8,073 8,073 Open in a separate window As seen in columns 1 and 2 of , OLS estimation revealed positive income effects for both linear and log income models, but only the linear model coefficient was statistically significant at conventional levels. Coefficient estimates were small, however, with an additional $1,000 of annual family income being associated with less than 1% of a standard deviation increase in child achievement.3 In the third through sixth columns of , we present the IV models utilizing all studies available, first using study components as instruments and then using study sites as instruments. When, in Model 1, income is the only endogenous variable, estimates suggest a .05 standard deviation increase in child achievement associated with every $1,000 increase in parents’ annual income and a .45 standard deviation increase in child achievement associated with a log-unit increase in parents’ income.4 Controls for parents’ employment and welfare income decreased the estimated income effect by about half and increased standard errors as well. The bottom half of presents our preferred estimates. In this case, IV estimates were based on the subset of studies that targeted employment, welfare receipt, and/or income but neither maternal education nor child care use. This reduced set of studies better conformed to the exclusion restriction and, with survey data on parents’ work hours, allowed us to substitute a conceptually more appropriate measure of work hours for quarters of employment. These analyses boosted point estimates of income effects slightly, with $1,000 and log-unit annual income increases associated with .06 and .60 standard deviation increases in child achievement, respectively. The addition of work hours and welfare as endogenous variables had little effect on the income effect estimates in site-based estimates but reduced coefficients and increased standard errors in the program-based estimates. Thus, it appears that the income effects we estimated were largely independent of the changes in employment and welfare receipt that may have been produced by assignment to the experimental treatments. Concern that results might be sensitive to the source of achievement reports led us to estimate the IV models presented in , all of which are based on the reduced set of studies and log income and use sites as instruments. As shown in the first column, averaging all available achievement reports for each child increased both coefficient estimates and standard errors modestly (Anderson, 2008). Restricting samples to include just the parent reports and test scores yielded .50–.65 coefficients when income was considered to be the only endogenous variable; in the multiple-endogenous-variable models, very unstable estimates are found.5 Table 6 By source of achievement score Average achievement score Parent reporta Test scoreb Variable Model 1 Model 2 Model 1 Model 2 Model 1 Model 2 Log average annual income 0.734 (0.256)*** 0.629 (0.369)* 0.648 (0.262)** 0.154 (1.447) 0.512 (0.231)** 0.179 (0.226) Average hr employed by quarter (in 100 hr) 0.011 (0.001) 0.165 (0.445) –0.140 (0.226) Proportion of quarters receiving any welfare over follow-up –0.159 (0.717) –0.019 (0.701) –1.400 (1.804) Sample size 5,693 4,280 3,549 Open in a separate window Finally, concern about the unique effects of the Canadian-based study led us to estimate models with and without SSP and to test for the interaction of country of study with our estimates of income effects. These analyses showed that models without SSP generated similar estimates of the effects of income (coefficients of .06 and .78 for linear and log income, respectively), but the loss of power from the substantial reduction in sample reduced these effects to nonsignificance. Consistent with these findings, formal tests of the significance of the difference of income estimated from models with and without SSP showed no significant differences,6 indicating that country of origin did not interact with the effect of income on child achievement in these IV models (findings are available from the authors).

Discussion We found noteworthy effects of family income on school achievement of young children in most of our IV models. This effect of income for young children is consistent with some of the nonexperimental research and with some of the emerging studies cited at the outset that attempted to estimate effects of income using models that allow for more definitive causal inference. The results are consistent with developmental theories suggesting that children's development is malleable and susceptible to family influences during the preschool period (Bronfenbrenner & Morris, 1998; McCall, 1981). Although we did not focus on income effects across the childhood age period because of data limitations (not enough of the welfare and employment studies included children across the full childhood age span to allow for such an analysis), our results do show that the preschool period, at least, is amenable to change as a result of parents’ income change generated by employment-incentive programs. How large are our effects? Our IV estimates suggest that a $1,000 increase in annual income sustained for between 2 and 5 years boosts child achievement by 6% of a standard deviation and that a log-unit increase in annual income increases child achievement by a little over half a standard deviation. These estimates are similar to those estimated in the quasiexperimental studies of Dahl and Lochner (2008) and Akee et al. (2010). Translated into an IQ-type scale, 6% of a standard deviation amounts to about 1 point and half a standard deviation amounts to 8 points. Translated into one of the achievement tests we used—the Bracken Basic Concept Scale—these effect sizes translate into about one and six additional correct answers, respectively, to a 61-question test regarding colors, letters, numbers/counting, comparisons, and shapes. Are these effect sizes policy-relevant? On the face of it, they seem quite small. And, in fact, experimental studies of early preschool intervention programs offering high levels of quality have shown much larger effects. Treatment effect sizes on IQ were 1.0 standard deviations at 3 years and .75 at age 5 for the Abecedarian Project and .60 for the Perry Preschool Project. But at $40,000 and $15,000, respectively, these large effect sizes came at a great cost. For $7,500, the Tennessee class size experiment showed that smaller K–3 class sizes increased achievement by about .2 of a standard deviation, which was estimated to increase benefits more than cost (Krueger & Whitmore, 2001). The earnings supplement programs in our study boosted family income for younger children by between $800 and nearly $2,200 per year, which corresponds to achievement effect sizes ranging from 5% to 12% of a standard deviation. Bos, Duncan, Gennetian, and Hill (2007) showed that the benefits to participants and to taxpayers outweighed the costs of one of these programs (the New Hope Project). Although we want to be cautious about extrapolating beyond our findings, it is possible that larger increases in income to families might produce proportionally larger impacts on children. Moreover, the fact that our income gains may be distributed across children within families argues that the per-child returns of income gains to families are even larger than we present here. By comparing income supplementation and early education policy effect sizes, we do not mean to imply that the two kinds of programs serve the same purpose. Child development is the explicit target of educational interventions, but it is only one of many possible goals for income redistribution policies. Ensuring school readiness for all children probably requires that some receive preschool education intervention programs, independent of whatever income redistribution program might be present. What might account for these income effects? One possibility is that higher incomes might reduce parental stress, which in turn might improve parenting (McLoyd, 1998). However, a review of the original impact reports for these studies shows that the earnings supplement programs failed to boost parenting warmth, monitoring, or provision of learning experiences in the home, nor did they consistently reduce parental harshness or depression (Duncan, Gennetian, & Morris, 2007; Morris, Huston, Duncan, Crosby, & Bos, 2001). Nor were there consistent impacts on marriage and cohabitation. The absence of effects on the home environment and parenting may be due to the fact that the increases in income were accompanied by increases in employment, offsetting any potential benefits of reduced financial strain with increased time pressure, a point to which we return later. Moreover, a few of the studies showed that the increased income was spent on child care, clothing, and food for children, which may simply not have been sufficient to reduce the strain of low income and result in measurable changes in parents’ behavior and emotional well-being. Another possibility is that some of the earnings supplement programs increased parents’ use of center-based child care arrangements. In fact, research conducted on these same samples has indeed suggested that programs that increase children's participation in center-based care arrangements also increase children's school achievement (Gennetian, Crosby, Dowsett, & Huston, 2007; Morris, Gennetian, & Duncan, 2005). Analyses parallel to those reported here have shown that that use of center-based care, as opposed to care in someone's home, during a child's preschool years has a positive effect on school achievement in the early grades of elementary school (Gennetian et al., 2007). In the Gennetian et al. (2007) research, effect sizes were modest but comparable to those for income—a .10 increase in probability of being exclusively in center-based care during the preschool years increased achievement by about 10% of a standard deviation. It is also likely that families use extra income to improve the quality of child care for their children. In this way, income-induced child care changes are separate from child care changes induced by the program directly (e.g., by encouraging families to take up a different kind of care without changing their income level). That is, the income effects on children can be viewed in a path model context: If money were truly randomly assigned, then some of that money might be spent on higher quality child care, reductions in work to spend more time with children, better health care, or a host of other ways. This article is focused on estimating the total effects of income itself. Estimating the process model behind these total effects is an important research priority but not the focus of the current article. Several caveats apply to our study. First, our data were drawn from children growing up in single-parent low-income families, precluding our ability to generalize to other family types and socioeconomic levels. Second, in pooling our data across sites, we assumed similarity in the ways in which income affected children across our studies and sites, an assumption that might not be met with the Canadian vs. U.S. data or for diverse sites across the United States. Notably, our individual study estimates suggest similarity in effects of income across sites, providing some justification for pooling these data. Finally, because we used earnings supplement programs to generate our effects of income on child achievement, our findings are likely most germane to income-boosting policies that link increases in income to increases in employment. Although we controlled for employment hours in all of these models, there may be psychological benefits to increases in earned but not other sources of income. To the extent that these benefits were part of our income effects, our results are most relevant to income increases arising from earnings supplements as opposed to policies providing cash grants not tied to work (such as child allowances). But of course this matters a great deal from a policy perspective. Although many studies have attempted to estimate the effects of income on children's development, few have relied on experimental or quasiexperimental variation in income. As such, our findings contribute to ongoing debates on whether and how much policy-induced increases in family income have a causal effect on the school achievement of preschool children (Blau, 1999; Duncan & Brooks-Gunn, 1997; Haveman & Wolfe, 1995; Jacob & Ludwig, 2007; Mayer, 1997). The effects reported here are compelling and informative for guiding developmental theory as well as future income-support policies. The extent to which such effects hold up under slightly varying economic contexts, evolving and more stringent welfare-to-work policies, or compositional changes among low-income workers is an open question that should guide future research in efforts to inform research and policy.

Acknowledgments This article was completed as part of the Next Generation project, which examines the effects of welfare, antipoverty, and employment policies on children and families. This article was funded by the Next Generation Project funders—the David and Lucile Packard Foundation, the William T. Grant Foundation, the John D. and Catherine T. MacArthur Foundation, and the Annie E. Casey Foundation—and by Grant R01HD045691 from the National Institute of Child Health and Human Development. We thank the original sponsors of the studies for permitting reanalyses of the data; Nina Castells, Beth Clark-Kauffman, Heather Hill, Ginette Azcona, and Francesca Longo for analytical and research assistance; Joshua Angrist, Raquel Bernal, Dan Black, David Blau, David Card, David Ellwood, Christopher Jencks, Jeffrey Kling, Steven Levitt, Sara McLanahan, Robert Moffitt, Stephen Raudenbush, and Chris Taber for thoughtful comments on earlier versions.

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[1] Url: https://www.ncbi.nlm.nih.gov/pmc/articles/PMC3208322/

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