Long-Term Health Effects of Childhood Parental Income

A. Panel Study of Income Dynamics

Our primary data source is the Panel Study of Income Dynamics (PSID). The PSID data set was chosen because it is the longest running panel survey that contains information on individuals’ health, family demographic characteristics and family income. It allows us to measure family income during childhood along with health outcomes and potential mechanisms in adulthood. The PSID started in 1968 with 4,802 households- 1,872 families from the Survey of Economic Opportunity, which oversamples the low-income population, and 2,930 families from a nationally representative sample. Since inception, information was collected for individuals living within a sample household and for descendants of original sample members. The survey was conducted on an annual basis until 1997 when the survey became biennial.

We use data from 1968 through 2017 for the analyses. The sample of interest includes individuals born between 1962 and 1992 who were the head of the household (used to mean husband when there is a heterosexual couple and to an adult of either sex when single) or spouse at least once, since 1999. This group is of interest for two reasons. First, information related to health is only collected for heads of household and their spouse. Second, except for general health status and physical limitation, data on health outcomes are collected starting in 1999. Given that one limitation is having health information only for heads and spouse could introduce bias, we restrict the sample to individuals aged 25 and older. By age 25, more than 80 percent of the sample is a head of the household or a spouse. This approach is also consistent with Braga, Blavin, & Gangopadhyaya (2020) and Hoynes, Schanzenbach, & Almond (2016). We further restrict the sample to individuals born in a PSID family and whose family was active in at least 1 survey year between each of the following age ranges: age 0-6, age 7-12 and age 13-18. We imposed this restriction to construct a representative measure of economic resources available during childhood. Using these criteria, the final sample contains 6,370 individuals. We then stack outcomes in different years for each individual, which gives 49,459 person-year observations. That is, we use an unbalance panel for the outcomes in adulthood, where some individuals are observed in fewer years than others. Table 1 contains summary statistics for the sample of interest and Table 2 contains summary statistics for the health outcomes and health behaviors that are studied.

One potential concern with using the PSID data is sample attrition. However, two features of the PSID mitigate these concerns. First, in 1992, the PSID initiated a large-scale recontacting effort for former non-response sample members and individuals who should have been included in the sample but never responded in any previous survey wave. Second, the PSID publishes sampling weights which adjust for attrition so that the sample continues to be nationally representative. Because of sample attrition and the initial oversampling of families with low-income, we use the published PSID cross sectional weights when estimating regressions as well as for descriptive statistics.

The PSID does not collect information on EITC receipt, so we use information on parental income, marital status, number of children and state of residence to estimate the annual amount of EITC benefits for which each family would be eligible using the NBER TAXSIM program (Feenberg & Coutts, 1993). We then add this to the measure of family income that is available in the PSID data. This is important because one source of variation our instrument exploits comes from the EITC.

B. Current Population Survey

Given that family income is arguably endogenous, we use data from the Current Population Survey (CPS) to construct a simulated instrument. The CPS has a very long history, dating back to the early 1940s. It is the primary data source for information on labor force statistics in the U.S. It collects information monthly from roughly 50,000 households. Each household is surveyed for 4 consecutive months, then exits the survey for an 8-month period. Once a household re-enters the sample, it is surveyed for an additional 4 months, then exits the sample permanently. Information is collected on a wide range of topics including employment, earnings, and a detailed set of demographic characteristics. We use data on income and the demographic characteristics for head and spouse to construct a simulated instrument for family income. After constructing the simulated instrument, we link it to PSID families using the demographic information for head and spouse at the time the child was born. We outline the steps for constructing the simulated instrument in the appendix.

4.1. Discussion of Potential Threats to the IV Validity

Regarding the first assumption about the instrument’s relevance, the simulated income is particularly relevant because there is a strong correlation between parental income and economic conditions, which is one of the primary sources of variation driving changes in income across demographic groups. Additionally, parental income is also correlated with EITC benefits, which provides an additional source of variation. The first stage results provide strong evidence in support of the instrument’s relevance.

Even though the instrument is relevant, the validity of the IV strategy is threatened if the simulated instrument affects children’s health in adulthood other than through parental income. In our context, this exclusion restriction requires two things. The first requirement is that changes made to the state and federal EITC parameters should not have a direct effect on child health other than through parental income. Previous discussions have demonstrated that federal and state governments' motivations for modifying the EITC structure over time are not directly tied to health. For example, Johnson (2001) and Leigh (2010) highlight three reasons governing authorities made changes to the EITC. First, the federal government wanted to allow states to redirect funding from block grants for the Temporary Assistance to Needy Families (TANF) to fund the EITC after the 1996 reforms. Second, there was a strong push by lobbyists in favor of promoting the EITC. Notably, as Leigh (2010) pointed out, political differences impact the extent of the push for stronger EITC support, with Democratic states being more likely to introduce new state level benefits. Third, states decided to use their budget surpluses on the EITC. Kliewer (2017) also highlights the bipartisan support enjoyed by the EITC as another reason for pushing to enhance EITC benefits. Because the generosity of state EITC might be correlated with other state programs, we follow the approach in the EITC literature to control for a set of state level variables (Bastian & Michelmore, 2018; Braga et al., 2020). Additionally, because children are not in the workforce, these health effects will likely occur only through changes in parental income (other studies using a similar approach include Larrimore (2011) and Schmeiser (2009)).

The second requirement for the exclusion restriction to be satisfied is that all the parental characteristics used to construct the instrument are exogenous. The set of parental characteristics used to define demographic groups are the race of the head and spouse, sex of the head and spouse, age of the head and spouse, marital status and the number of children. One obvious concern is that over a long period of time, changes in many of these demographic variables will be correlated with unobserved factors that affect children’s health. For example, if we are using the marital status of the parents in each childhood year, then if parents separate, the instrument will assign a lower level of income for the instrument since, on average, married households have higher income. This kind of variation in the instrument would not only affect children’s health through the available resources in the family, but it might also pick up effects from any unobserved changes that impact child health and are correlated with family resources. To address these concerns, we use parental demographic characteristics and the number of children in the household at the time of the child’s birth. For example, if the head of the household was married when the child was born, we assume they remain married or if the head of the household was black, we assume the head was always black. The age of the head and spouse at the time of the child’s birth is allowed to grow by 1 each year. In essence we restrict the set of parental characteristics from varying in potentially non-random ways. By restricting the set of demographic conditions to the child’s birth-year, we rely on the much weaker assumption that the parental characteristics are plausibly exogenous within a short period of time, specifically, at the time of birth. This assumption reduces the explanatory power of the instrument, but it allows us to exploit only the variations in the income distribution that are uncorrelated with non-random changes in the family characteristics over time.

Because many of the parental characteristics are reasonably expected to impact the child’s health, we include them as controls in all of the regressions. By including these as controls, our instrument exploits only the variation coming from idiosyncratic changes in the income of each demographic group over time. In other words, we exploit variation in how well individuals from one demographic group are doing financially relative to individuals from other demographic groups. Changes in income that identify our model come from factors that differentially affect wage growth across demographic groups, such as technological advancement and trade agreements. Because identification depends on the within demographic group variations in income over time, a fully saturated model that controls for non-linear effects of parental characteristics and include a full set of interactions for parental characteristics, child’s birth cohort and the age of the head and spouse in each year during childhood, would in theory not be identified. One implicit assumption with this set up is that non-linear effects of the parental characteristics are small and stable, conditional on including linear controls for parental characteristics. As a sensitivity check, we estimate a model that includes interactions of the parental characteristics, and we find that the results are robust. We also vary the set of parental characteristics used to identify demographic groups and show that the results do not depend on the set of demographic characteristics used.

Using the simulated instrument breaks the link between an individual’s own parental income and unobserved characteristics that are possibly correlated with the health of the children in the long run. For example, parents’ ability to effectively care for their children might be correlated with their earnings potential. However, by taking within-group averages, we circumvent decisions at the parental level that make own parental income endogenous. In essence we are using demographic group averages to instrument for own family’s income. Our simulated instrument approach builds on the idea espoused by Currie & Gruber (1996a, 1996b) which simulates Medicaid eligibility across states for different demographic groups. Several studies use various types of group averages as exogenous sources of variation when the variable defined at the individual level is arguably endogenous because of person specific characteristics. For example, studies use local area labor market conditions, such as employment rate, as an exogenous source of variation for studying the impact of income shocks and economic conditions on health (Kuehnle, 2014; Page et al., 2019).

One potential concern with our IV strategy is that there is an inherent positive correlation between parental hours worked and parental income. Our IV strategy does not account for the possibility that parental hours worked might also directly affect child health. This concern does not invalidate our results, but instead, might alter the way we interpret our results. However, we do not believe this is a major concern because even though we think that parental labor supply is endogenous, we show that if it is included in the regression models, the coefficient on parental hours worked is statistically insignificant and our estimated coefficients for parental income remain virtually unchanged.

5.1. First Stage Results

We begin with our first stage results from our main model, where we use average parental income between birth and age 18. We present the results in Table 3, for all the different outcomes of interest, but focus only on the results using very good or excellent general health as the reference sample. The estimated coefficient on the simulated instrument is 1.86. This implies that a $1 increase in the average simulated income between birth and age 18 is associated with a $1.89 increase in average parental income between birth and age 18. The point estimate has the expected sign and is statistically significant at the 1% level. If the income variations across demographic groups perfectly predicted own family income, then the first stage coefficient would be equal to 1. However, we do not expect that the simulated income would have a dollar-for-dollar link with family income because all the parental demographic characteristics are held constant at the time of birth. The non-random changes in family structure are expected to result in the instrument either over- or under-predicting family income. The first stage F-stat is 78.67, which is well above the conventional rule of thumb of 10, in the case of a single endogenous variable and a single instrument (Staiger & Stock, 1994). Hence, we are not concerned about having a weak instrument.

5.2. Main Results for the Effect of Parental Income on Child Health

Table 4 contains the regression results for the effect of parental income on children’s health in adulthood. Health outcomes and risky health behaviors are measured between ages 22 and 56. Panel A of Table 4 contains the IV regression results where we instrument for parental income using the simulated instrument and Panel B contains the corresponding OLS results. Each coefficient is from a separate regression and is presented with its associated standard error in parentheses.

The results from the IV regressions show statistically significant effects for very good or excellent general health, physical limitation, current smoking, and the number of cigarettes smoked per day. We find that a $10,000 increase in average parental income between birth and age 18 (an approximately 12.1% increase in parental income) increases the likelihood of very good or excellent general health in adulthood by 2.5 percentage points, or 3.7%. For metabolic syndrome, we do not find a statistically significant effect, but the sign on the estimated coefficient suggests that more income reduces the likelihood of metabolic syndrome (see Table A1 for results on the variables used to construct metabolic syndrome). The estimated coefficient implies that a $10,000 increase in average parental income between birth and age 18 reduces the likelihood of metabolic syndrome by 6.7%. For physical limitation, we find that a $10,000 increase in parental income reduces the likelihood of having a physical limitation in adulthood by 0.9 percentage points, or 10.3%. For current smoking, we find that a $10,000 increase in parental income reduces the likelihood of being a current smoker in adulthood by 2.9 percentage points, or 12.7%. Regarding the number of cigarettes smoked per day, we find that a $10,000 increase in average parental income reduces the number of cigarettes smoked in adulthood by 0.52 sticks per day or 16.7%. The estimated coefficient for the effect of parental income on binge drinking is not statistically significant and the implied magnitude is small (less than a 1% increase).

5.3. Comparing IV and OLS Estimates

We motivate our IV approach by concerns that OLS could be biased in an unknown direction because of unobserved attributes, such as parents’ abilities, risk preferences and genetics. We present the OLS results in Panel B of Table 4. We make two fundamental observations. The first is that both estimation methods yield qualitatively similar conclusions- the signs of the estimated coefficients are always the same across both estimation methods. The second observation is that the absolute magnitude of the point estimates from the OLS regressions are generally smaller than the corresponding IV estimates. This is consistent with Kuehnle (2014) that also finds that OLS results are biased toward zero.

The differences between IV and OLS estimates are economically meaningful in most cases. Larger IV estimates could be suggestive of attenuation bias in the OLS estimates, which results if income is measured with error (Aydemir & Borjas, 2011). With classical measurement error in income (Bingley & Martinello, 2017), I IV approach solves the measurement error problem (Angrist & Pischke, 2008). However, given that income is being averaged between birth and age 18, potential concerns about measurement error is mitigated and we do not expect that the entire difference between the OLS and IV estimates arise because of measurement error alone, insofar as the measurement error is independent across the different waves of the data,.

We examine the role of measurement error directly by separating parental income from birth to age 18 into parental income received at even ages and parental income received at odd ages, and estimate the effect of average income at even ages and income at odd ages on each outcome using OLS. We then estimate those same regressions using average parental income at odd ages as an instrument for average parental income at even ages. Under the assumption that measurement error in even years is independent of measurement error in odd years, the difference between the magnitudes of the OLS and IV estimates gives a sense of the degree of the measurement error (see Wald (1940) and Durbin (1954) for further discussion). If coefficients from the OLS regressions and the IV regressions are similar in terms of magnitudes, that suggests the measurement error problem is not severe. If coefficients are very different, that suggests a high degree of measurement error. We present the second stage results in Table 5 and the first stage results in Table A2. We do not find systematic differences between the OLS estimates and the IV estimates. In some cases, the OLS estimates are larger than the IV estimates while in other cases the IV estimates are larger. For ease of comparison, when we focus only on the estimated effects of income received at even ages (the more conservative estimates), the IV estimates are in the order of 20 to 30 percent larger. This implies that measurement error may account for some of the bias in the OLS estimates, but it alone cannot explain all of the differences between IV and OLS estimates.

Since measurement error alone cannot explain the differences between OLS and IV estimates, this implies that some of the differences arise because of endogeneity. As discussed previously, risk preferences could also contribute to this pattern. The PSID contains information on risk avoidance for the head of the household, from 1968 to 1972. Arguably, this is an imperfect measure of risk preferences, but its importance might be elevated given the evidence of intergenerational risk transmission (Dohmen et al., 2011). When risk avoidance is included as a covariate, we find that the IV estimates generally reduce, for example, a 28% reduction in the point estimate for the variable very good or excellent general health (see Table A3). This is consistent with our expectation that if we block risk preferences as a pathway through which parental income can impact health, then the estimated effects will be smaller.

5.4. Subgroup analysis

Next, we examine whether the effect of childhood parental income varies across different subgroups of the population. Given that females are usually healthier and live longer than males, (Austad, 2006), it might be the case that higher income will lead to greater investments in the health of female children. However, because females are usually in better health, it also implies that further increases in income might contribute only very little to improving the health or females while the contributions for men could be larger. It is thus theoretically unclear whether we might expect larger effects among men or women. We also consider the effects by race, white and non-white. Non-whites on average have worse health than whites, which suggests the gains for non-whites could be larger from income increases. However, because the quality of care received among non-whites is also lower (Chandra & Skinner, 2003), non-whites might not observe large gains in health even if they receive additional health services with more income.

In Table 6, we present the results by gender for women and men, and by race, for whites and non-whites. Consistent with Hoynes et al. (2016), we find that childhood parental income has a larger effect among females for very good or excellent health. For physical limitation, we find larger benefits for males. For smoking and the number of cigarettes smoked per day, we find larger reductions for men. As it relates to racial differences, we generally find that the beneficial impacts of childhood parental income are larger for white individuals. Furthermore, for all the outcomes except physical limitation, we do not find statistically significant effects among non-white individuals. However, the estimated effects are economically meaningful for most of the outcomes. The lack of statistical significance among the non-white individuals might be because of the relatively smaller sample size.

5.5. Non-linear Developmental Effects During Childhood

There is a fast-growing literature suggesting that early childhood years are more important for health and cognitive development (Cunha & Heckman, 2007). We examine whether there is any suggestive evidence that the effects of childhood parental income on health vary by the age at which it was received (Table 7). We separate parental income into 3 age ranges during childhood: birth to age 6, age 7-12, and age 13-18. However, because the instrument is highly correlated overtime, we cannot separately identify the effect of each age range while holding the effects of the other age ranges constant. In other words, we cannot include all three age ranges in the same regression. As such we estimate separate regressions for each age range. We find some suggestive evidence that parental income between birth and age 6 might have larger beneficial impacts on general health. We also find some suggestive evidence that parental income between birth and age 6 results in larger reductions for smoking and the number of cigarettes smoked per day in adulthood.

5.6. Sensitivity analysis

Estimates from our sensitivity analyses are generally consistent with our main results. First, we examine whether parental hours worked between birth and age 18 might have an additional effect on children’s health in adulthood beyond the effect through parental income. While parental labor supply is also arguably endogenous, if the estimated coefficients on parental income change in meaningful ways, this might be suggestive evidence that parental labor supply is contributing substantially to the estimated coefficients on parental income indirectly. This would alter the interpretation of the estimated coefficients. However, all the conclusions remain unchanged and the estimated coefficients for parental income change only slightly. Furthermore, the coefficients on parental hours worked are not statistically significant (see Table A4).

Second, we explore whether varying the set of demographic parental characteristics used to construct the instrument alters the findings. In one case, we exclude parental marital status at the time of birth. In another case, we exclude the number of kids in the household at the time of birth. And in yet another case, we exclude both parental marital status at birth and the number of kids in the household at birth. The first stage results are presented in Table A5, and the second stage results are presented in Table A6. When we vary the set of parental controls used to construct the instrument, the first stage remains strong, with the smallest F-stat being 78.67. Hence, even when fewer parental characteristics are used, we are not concerned about having a weak instrument. The second stage results are consistent with our main findings and lead to the same conclusions.

Third, we examine whether our results change when we include interactions of the parental characteristics used to construct the simulated instrument. The results show a large first stage F-stat (103.8), and the second stage results are similar to the main results. These are presented in Table A7 and Table A8. We also explore whether the results change meaningfully when we include state specific linear time trends. We find that the results are robust to the inclusion of state specific linear time trends. The first stage results are presented in Table A9, and the second stage results are presented in Table A10.

5.7. Putting the Effect Size into Context

These results are consistent with the previous studies that examine the contemporaneous relationship between parental income and child health and find that parental income is associated with subjective measures of child health, such as very good or excellent health, but not with more objective measures of health or chronic conditions (Kuehnle, 2014). However, the estimated health effects are larger, which is likely explained by the fact that health outcomes are measured later in life, and we anticipate that the health effects accumulate over time (Apouey & Geoffard, 2013; Case et al., 2002). Kuehnle (2014) uses an IV approach and estimates larger effects relative to other studies that focus on the contemporaneous link between parental income and child health, but our estimated effects are larger than found in Kuehnle (2014). The effect sizes among studies that consider the long-term health effects of specific income shocks in early childhood are generally larger (Braga et al., 2020); Duncan, Ziol-Guest, & Kalil, 2010).