School Starting Age and Long-Run Health in the U.S.

Transcription

1 School Starting Age and Long-Run Health in the U.S. Grace Arnold Louisiana State University Briggs Depew Utah State University April 26, 2017 Abstract School starting age has been shown to have long-run effects that persist throughout adolescence and into adulthood. Using variation from state-level school starting age laws in the U.S., we find that males who are older when they enter school are more likely to have higher levels of self-reported health later in life. We are largely able to rule out education and labor market outcomes as significant channels for this finding. Building from the previous studies that have found conflicting evidence on the effect of school starting age on educational attainment and labor market outcomes in the U.S., we find that school starting age decreases the likelihood of high school completion among males, but has no significant effect for females. We do not find that labor market outcomes are affected by school starting age. JEL: I14, I20, I31, J01 Keywords: School Starting Age; Long-Run Health; Self-Reported Health; ADHD Main Text Word Count: 4917 Number of Figures: 4 Number of Tables: 7 The authors declare that we have no relevant financial or personal interests that relate to the research described in this paper. Corresponding author: Grace Arnold, Department of Economics, Louisiana State University, garnol2@lsu.edu

2 1 Introduction The age at which a child begins kindergarten has been shown to have long-run effects that persist throughout adolescence and into adulthood. Potential benefits from delayed entry into school include relative maturity older students on average have relatively higher developmental advantages relative to their classmates and absolute maturity formal schooling is more appropriate for students who are more mature and developmentally advanced. It has been well documented in early grades that children who start school at an older age perform better in the classroom. Such findings are challenging to interpret because of a direct-age at-test effect, i.e. students who start school at a later age are also older when they take tests in school. Although studies such as Bedard and Dhuey (2006), Datar (2006), Elder and Lubotsky (2009), and Cascio and Lewis (2006) account for the endogenous decision by parents to enroll their child in school, the age-at-test effect is still difficult to disentangle. In order to avoid this problem, much of the recent attention of the effect of school start age (SSA) has centered on long-run effects, such as educational attainment and labor market earnings (Bedard and Dhuey, 2006; Dobkin and Ferreira, 2010; Black et al., 2011; Bedard and Dhuey, 2012; Fredriksson and Öckert, 2014).1 The purpose of this paper is two-fold: first, we seek to reexamine the long-run effects of school start age on educational attainment and labor market outcomes within the U.S., outcomes for which previous studies have shown mixed results; second, we investigate the question: does SSA affect long-run health in the United States? We discuss a number of potential mechanisms for why SSA may impact health both in the short- and long-run. Using data from the Survey of Income and Program Participation (SIPP), we exploit exogenous variation in an individual s SSA generated by state entry laws and an individual s 1 Other research on the long-run effects of SSA include fertility, marriage formation, inter-generational health (McCrary and Royer, 2011), teen pregnancy (Black et al., 2011), and crime (Landersø et al., 2015; Cook and Kang, 2016; Depew and Eren, 2016). 1

3 month and year of birth. An advantage to our research design is the use of variation in state school entry laws from across states and over time to identify the effect of SSA, rather than just relying on one state or one cutoff date. This variation allows our study to be less susceptible to potential spurious effects from unobservable factors correlated with an individual s month of birth or the timing of specific state laws. Similar to other U.S. based studies, we are limited in our interpretation of the results: students who start school at an older age have fewer years of compulsory schooling and are at risk of dropping out of high school for a longer duration of time (Angrist and Krueger, 1991). Therefore, variation in SSA arising from U.S. school entry laws produces a combined effect of school entry and school leaving legislation. Studies using European data, where compulsory schooling laws are tied to educational attainment and not age, avoid this confounding effect (Black et al., 2011; Fredriksson and Öckert, 2014). For the purpose of our study, when referring to the effect of SSA, it is relative to the U.S. and it represents a net effect of SSA and increased exposure to dropping out of high school. We find that starting school a year later decreases the likelihood that a male completes high school and has roughly no impact on female educational attainment. We find no significant evidence for either gender that higher SSA improves labor market outcomes. However, our estimates for male earnings, although imprecise, are positive, suggesting that higher SSA may positively impact monthly personal earnings (Bedard and Dhuey, 2012). We find that males with higher SSA are more likely to have higher levels of self-reported health. Particularly, males with higher SSA are significantly less likely to report fair or poor health and more likely to report excellent or very good health. SSA does not appear to affect the self-reported health of females. Our findings are robust to alternative estimation strategies, including a regression discontinuity design, and do not appear to be driven by one specific school entry cutoff date. It is challenging to pin down the precise mechanism of how SSA affects long-run health. 2

4 SSA may impact health through the accumulation of human capital and/or through the labor market, such as increased earnings or occupational sorting. Education affects both healthy behaviors (Cutler and Lleras-Muney, 2010) and health in general (Cutler et al., 2008). Similarly, income is an important determinant of health (Deaton and Paxson, 1999). We are largely able to rule out education and labor market outcomes as channels through which SSA affects health. Furthermore, we find no strong evidence that SSA is related to objective health measures, such the number of days an individual was sick or health care utilization; however, we have limited outcomes available within our study. Mental health may be an important channel in understanding the long-run health effects of SSA. In Norway, Black et al. (2011) find that boys who start school at a later age are less likely to have poor mental health at age 18. Particularly, delayed entry by one year decreases the probability of poor mental health by half a percentage point (from a mean rate of 7 percent). Using data from Denmark, Dee and Sievertsen (2015) show that a oneyear increase in SSA significantly improves mental health outcomes at age seven. Following children up to age 11, they find that the effects persist in childhood. Other papers have shown that children who are older when they start kindergarten are less likely to be diagnosed with attention-deficit/hyperactivity disorder (ADHD) (Elder and Lubotsky, 2009; Elder, 2010; Evans et al., 2010). ADHD is a neurological condition that is more than twice as likely to be diagnosed in males than females. These studies show a discontinuous decrease in ADHD diagnoses for those born just after their school entry cutoff. Since ADHD incidence should not discontinuously change around the school entry birthdate cutoff, these findings imply significant misdiagnosis of ADHD caused by relative maturity. Further evidence from Elder (2010) and Evans et al. (2010) suggest that SSA affects the likelihood of using prescribed stimulant medication to treat ADHD. Elder (2010) finds that fifth and eighth graders born just before the cutoff date (youngest in their cohort) are twice as likely to use prescription stimulant medication to treat ADHD; Evans et al. (2010) use 3

5 two independent data sources of individuals ages 7-12, and find that those born just after the school entry cutoff are significantly less likely to use stimulant treatment for ADHD. Their findings are most prevalent for males and the effect persists at older ages (ages 13-17). 2 These findings are potentially important with respect to long-run health since ADHD diagnosis in youth is known to be highly comorbid with other mental disorders (Kessler et al., 2006; Biederman et al., 2006). 3 2 Data 2.1 SIPP and Data Construction Our primary data comes from the 1996, 2001, 2004, and 2008 SIPP. We limit our sample to individuals ages We use only one observation per individual, not the longitudinal component of the SIPP, since our variable of interest, SSA, does not vary within an individual. Since we are interested in long-run effects, we chose the last observation available for each individual in the data. Using the SIPP migration history topical module, we restrict our sample to individuals who we can accurately identify their state of residence when they would have started kindergarten. For our effective sample, we can identify an individual s age five state of residence for approximately 74% of the data. 5 2 Table 6 of Evans et al. (2010) presents small and potentially negligible effects for females. The use of stimulants by individuals is similar or even larger then their baseline estimates. 3 Potential long-run adverse effects of prescribed stimulants for ADHD are less clear. Early research on stimulant therapy suggested that pharmacologically treated youth were more susceptible to substance abuse disorders. More recent research finds no relationship between stimulant therapy and risk of substance abuse disorders (Barkley et al., 2003; Wilens et al., 2003). 4 We choose age 24 as a lower bound to be consistent with the previous literature studying long-run effects of SSA. Age 52 is an upper bound by way of data construction; our first cohort was born in 1959 and the final year we observe an individual in the 2008 SIPP panel is Including movers does not significantly affect the results. 4

6 2.2 School Entry Laws and Calculating Predicted School Starting Age We observe 46 states that have school entry age laws at some point in time. Figure 1 shows the histogram, weighted by observations from our effective sample, of the state entry law dates that are observed from Our data on these laws comes from Bedard and Dhuey (2012) and Evans and Garthwaite (2014). We cross-referenced this information with each state s statute as well as Cascio and Lewis (2006). Since exact date of birth is not observed, we follow Bedard and Dhuey (2012) by coding state laws as either beginning of the month or mid-month. 6 States without laws or states where laws are left to the local-level are excluded from the analysis. 7 Using these laws, we calculated the predicted school starting age (PSSA) for each individual in the data. 8 Figure 2 reports the distribution of age at interview (top) and the distribution of predicted start age (bottom). 2.3 Self-Reported Health Status For our study, we focus on an individual s self-reported health status, which is available in the SIPP. Unfortunately, other more objective measures are not available. Self-reported health is commonly used due to its availability in large survey data sets. 9 Previous research suggests that using self-reported health as an outcome is useful since it provides information for a wide range of health outcomes and serves as a meaningful predictor of future health and mortality. Maddox and Douglass (1973) found that there is a persistent and positive congruence of selfreported and physician assessed health status, and that self-reported health ratings tend to better predict future physicians ratings than actual current physicians ratings. Idler and 6 Individuals born in the same month as a mid-month school entry cutoff are omitted from the analysis. 7 Colorado, Massachusetts, New Jersey and Washington are completely excluded from the analysis. 8 If the state entry cutoff is November 1st, the predicted start age is calculated by: P SSA = For example, see Bound (1991), Mazumder (2008) and Clark and Royer (2013). 5

7 Benyamini (1997) examine 27 studies and finds that self-rated health is an independent predictor of mortality. More recently, DeSalvo et al. (2006) use 163 studies to analyze selfreported health as an outcome and conclude that persons with poor self-rated health had twice as high mortality risk compared to persons with excellent self-rated health; these ratings maintained a strong association with mortality even after adjusting for key covariates such as demographics and comorbidities. 2.4 Descriptive Statistics of the Sample Our effective sample consists of 51,142 individuals. Table 1 reports the descriptive statistics of our sample by gender. Individuals indicate their self-reported health status as excellent, very good, good, fair, or poor. Placing the responses on an ordinal scale from 1-5, males tend to report a slightly higher health status, as the mean ordinal ranking for males and females is 3.93 and 3.82, respectively. Males are more likely to report being in excellent or very good health (69.7%) than are females (65.4%). Furthermore, males are less likely to be in fair or poor health (7.8%) than are females (9.4%). 3 Empirical Strategy We begin by considering the following estimation equation that relates SSA to an outcome of interest: Y i,y,s = α 0 + α 1 SSA i,y,s + X i,y,s Θ + δ y + λ s + ε i,y,s, (1) where Y i,y,s is the outcome of interest for individual i, in school entry cohort y, living in state s at age five. SSA represents the school starting age for the individual, X is a vector of observed characteristics, δ y and λ s represent fixed effects for kindergarten cohort and age five state of residence, respectively. ε captures unobserved factors that may affect the outcome 6

8 of interest. OLS estimation of equation (1) will produce a biased estimate of the effect of SSA since SSA is not randomly assigned. Particularly, parents and/or school administrators may endogenously delay or early enroll a child s start in school. To address the endogeneity problem, we exploit the exogenous variation in school start age that is generated by school entry laws. A plausibly valid instrument for SSA is the calculated PSSA obtained from an individual s birthdate and the school entry law in the state they resided at age five. Since we do not observe SSA in our data, we instead estimate the following reduced form equation: Y i,y,s = β 0 + β 1 P SSA i,y,s + X i,y,s Γ + δ y + λ s + µ i,y,s, (2) where Y represents an outcome of interest, P SSA represents the predicted school starting age, X represents a vector of observed characteristics that includes indicators for an individual s race and a number of fixed effects (described below), and µ is the unobserved term that is assumed to be uncorrelated with P SSA. To assure that our identification strategy is capturing only exogenous variation in PSSA, we include a number of important sets of fixed effects. First, to capture variation in school starting age generated from state entry age laws, we include fixed effects for kindergarten cohort, δ y, and residence at age five, λ s. Second, since the socioeconomic status of the mother may be correlated with the time of conception and birth (Buckles and Hungerman, 2013), we include birth month fixed effects to eliminate any confounding effect entering through seasonality in the types of children being born in different months of the year. We also include age at interview fixed effects to flexibly control for the expectation that individual health outcomes are influenced by their age at time of interview. Under the assumption that an individual s predicted school start age is random after conditioning on fixed effects for state, cohort, and birth month, the estimate of β 1 can be 7

9 interpreted as the effect of increasing an individual s SSA by one year (around the neighborhood of age five) if the population fully complies with the state starting age law. When there exists a degree of noncompliance, the local average treatment effect of SSA for the subpopulation of compliers is calculated by dividing the estimate, β 1, by the coefficient estimate for PSSA from the first stage equation. 10 There are five estimation points to make clear: (i) since we do not observe actual SSA, our analysis considers the reduced form effects of PSSA, (ii) all models use person sample weights, (iii) all regressions are estimated using OLS, (iv) standard errors are estimated by clustering at the state level (state of residence at age 5), and (v) we partition our sample by gender to allow the effects to flexibly vary by sex. 4 Results 4.1 Tests of Internal Validity Our identification assumption is that conditional on our sets of fixed effects, PSSA is random. Although this assumption is not entirely testable, we can investigate whether plausibly exogenous individual characteristics are correlated with PSSA. Ideally we would have a wide array of observable characteristics that are predetermined before a child enters school. However, in our data we observe individuals at later ages and have few characteristics that precede school entry. The internal validity tests are limited to testing PSSA against an individual s race and to whether an individual attended a private high school. Private high school attendance proxies for parental income, however, it may be endogenous to PSSA since attending private high school is determined after a child enters kindergarten. Table 2 presents falsification tests for males (Panel A) and females (Panel B). The outcome for 10 Black et al. (2011) estimate the first stage effect of PSSA on SSA to be 0.80 for men. Depew and Eren (2016) use data from Louisiana and show that those born just after school entry law are approximately 0.8 to 0.9 years older, depending on the demographic group. 8

10 each regression is an indicator variable (1 = yes; 0 = no) and is presented in the heading of each column. The relatively small and imprecise point estimates suggest that PSSA is not correlated with individual characteristics; further supporting the internal validity of the empirical strategy. 4.2 Education and Labor Market Outcomes We now turn to the discussion of the regression results for the education and labor market outcomes. Table 3 reports the regression results for the coefficient estimate of PSSA for the outcomes: years of schooling, high school degree or higher, received a GED, at least some college, and a college degree. PSSA is measured by years so the coefficient estimate measures the effect of being one year older at the time of school entry. Panel A and Panel B presents the estimates for males and female, respectively. For both genders, we observe a negative coefficient on years of schooling; however, the point estimates are not statistically different from zero. For males, being one year older when starting kindergarten decreases the probability of obtaining a high school degree or GED equivalent by 1.56 percentage points and is statistically significant at the 10 percent level. A 1.56 percentage point effect implies a 1.74 percent decrease from the mean high school completion rate. When our estimate is compared to the RDD estimates presented by Dobkin and Ferreira (2010) for individuals in California and Texas, our estimate is noticeably larger, but not statistically different given the relatively large standard error (0.9 percentage points). Dobkin and Ferreira (2010) present estimates for males in the range of negative.7-.8 percentage points. Dobkin and Ferreira (2010) also find similar estimate for females. We do not find a significant effect for females when using variation from across the U.S.; this finding is similar to Bedard and Dhuey (2012) who find a negative, but not statistically significant, effect of legal entry age on high school completion rates. For males and females, the remaining point estimates are consistent with the argument 9

11 that SSA increases an individual s exposure to dropping out and therefore reduces educational attainment. Notably, we observe a positive estimate for obtaining a GED and negative estimates on some college and college degree. For males, the estimate on some college is statistically different from zero at the 10 percent level; however, this result is sensitive to alternative specifications discussed later. Table 4 presents the regression results for the labor market outcomes: labor force participation, currently employed, log of monthly earnings, and log of monthly earnings for the subsample of employed workers. 11 We find no significant evidence that SSA affects labor market outcomes within the U.S. For both genders, the point estimates are statistically insignficant. This is similar to Dobkin and Ferreira (2010) who do not find a discontinuous change in the likelihood of employment or log wages around the school entry cutoff in California and Texas. Their results stand in contrast to more recent estimates from Bedard and Dhuey (2012) that find backing up entry laws increases log wages for men. It is worth noting that at least for males, we observe a positive and imprecise coefficient estimate on log monthly earnings. 4.3 Self-Reported Health We now turn our attention to studying the impact of SSA on long-run health, which to our knowledge has not previously been analyzed. Table 5 presents the results for the outcomes: health status (ordinal health ranking from one to five with five representing excellent health) and indicators for excellent or very good, and fair or poor health. For males, we observe a consistent pattern that suggests higher SSA increases selfreported health. Particularly, higher PSSA increases ordinal health status by.078 points from a mean of 3.93, approximately a 2 percent increase. One additional year of P SSA 11 We set log monthly earnings to zero when we observed a non-positive amount. The results are insensitive to this transformation. 10

12 increases the likelihood of reporting excellent of very good health by 2.6 percentage points, a 3.7 percent increase from the mean of.70. The effect of PSSA on fair or poor health, -.029, is significant at the 1 percent level and implies that individuals who should be one year older when they enter school are 2.9 percentage points less likely to report fair or poor health. This effect is large relative to the mean of.078 and it represents a 37 percent decrease in the likelihood of reporting fair or poor health. 12 Panel B of Table 5 presents the results of selfreported health for females. Similar to the prior analysis for females, we find no significant effects of PSSA. 4.4 Robustness Checks and Alternative Specifications Omitting cutoff dates from the analysis In this section we investigate the sensitivity of our estimates by exploring alternative specifications and robustness checks. We begin by considering whether one specific cutoff date is driving the results. We estimate the effect of PSSA when we eliminate one school entry cutoff date from the analysis. As depicted in Figure 1, our main analysis consists of 13 school entry cutoffs. For each outcome we estimate 13 regressions, each regression excludes all observations corresponding to one of the 13 school entry cutoffs. 13 The estimates from this exercise, and their corresponding 95 percent confidence interval, are presented in Figure 3. The numbers on the horizontal axis represent the beginning of the month entry date. The results suggest that one specific cutoff date is not influencing the 12 It is worth mentioning that our results may represent relatively conservative estimates. We obtained more precise estimates when we chose alternative data restrictions or specifications. For example: not using individual level sampling weights; restricting our data to only individuals who report no change of state residency; expanding the sample to younger ages; restricting the sample to exclude older ages; expanding the sample to observe the same individual multiple times and then clustering our standard errors in two dimensions at the state and individual level; using state-by-cohort fixed effects as our baseline specification; clustering standard errors at the state-by-cohort level; clustering standard errors in the RDD at the stateby-running variable level; and, including controls in the RDD specifications. 13 The 13 school entry cutoffs are the beginning of January, February, June, July, August, September, October, November, and December, and the middle of August, September, October, and November. 11

13 results Including Alternative Fixed Effects or Trends Table 6 presents our results for males using alternative specifications. Panel A presents our main results that include indicators for: state of school entry, cohort, age at interview, birth month, and race. Panel B adds to the specification in Panel A by including state specific linear time trends. Panel C adds to Panel A by including state of entry-by-cohort fixed effects. In this specification we are identifying the effect of PSSA from within state-bycohort variation in month of birth that is used to generate PSSA, rather than allowing for variation to be used across cohorts and across states. The results in Panels B and C provide largely similar estimates to our main analysis presented in Panel A. When using these alternative specifications, the results are slightly more significant and larger in magnitude. However, the same overall story emerges: an additional year of PSSA for males decreases the likelihood of completing high school and entering college and increases one s self-reported health. Although not shown, we continue to observe no significant effects of PSSA for females when using alternative specifications Regression Discontinuity Design As an alternative identification strategy, we implement a regression discontinuity design (RDD) to estimate the effect of PSSA on our outcomes of interest. For many studies analyzing SSA, a RDD has been a natural empirical strategy. These studies share a common feature in their data: observing exact day of birth. Although using month of birth in a RDD framework is not uncommon, it requires a more restrictive identifying assumption: individuals born a month apart, instead of a day apart, have unobserved characteristics that are smooth around the cutoff Barua and Lang (2016) provide evidence that legal entry age as an IV may violate the required monotonicity assumption. They propose an alternative instrument: an indicator equal to one if an individual was 12

14 To obtain the effect of PSSA within the RDD framework, we recenter the data around the school entry cutoff for each state-kindergarten cohort according to an individual s month and year of birth. In most instances, there are six bins on each side of the cutoff in which an individual may be placed. 15 To estimate the effect of PSSA we consider the following reduced form equation, Y i = γ 0 + γ 1 1 {Index i 0} + f(index i ) + σ i, (3) where Index i is the distance individual i is from the school entry cutoff and f( ) is a polynomial in Index i. In this setup, the coefficient estimate γ 1 can be interpreted as the effect of being assigned to enter school almost a year later. Panels D-F of Table 6 report the RDD coefficient estimates. Panel D allows for a local linear spline regression (the linear relationship between the running variable, Index i, may differ on each side of the cutoff); Panel E is the same as Panel D but uses a three-month bandwidth; Panel F allows for a local quadratic spline regression. When comparing the point estimate on high school attainment from the main specification (Panel A) to the point estimates from the RDD specifications, we observe a roughly similar effect. The estimates are less precise with the reduced bandwidth and quadratic spline, but the magnitudes are within a standard error of those presented in Panels A-C. This is not true for the outcome of some college. The estimate is not statistically significant in any of the three RDD specifications and is consistently much closer to zero than the estimates in Panels A-C. The RDD results for the health outcomes continue to show a positive relationship between SSA and self-reported health. The RDD framework produces point estimates for health status, excellent or very forced to delay school entry. Our findings using this instrument are not meaningfully different in terms of magnitude or significance. Barua and Lang (2016) acknowledge that their paper uses laws from the 1950s, when entry policies allowing early enrollment were not strongly enforced; early enrollment has become much more difficult. 15 Exceptions include: years when a law change moves back the school entry cutoff date or states with mid-month cutoff laws. 13

15 good health, and fair or poor health that are statistically significant and of similar magnitude as those presented in Panels A-C. 16 The graphical results for the RDD specification using a local linear spline regression are presented in Figure 4. As an additional robustness check, we randomly generated school entry laws and calculated the placebo discontinuity using a local linear spline regression. We iterated over this process 500 times in order to generate a distribution of placebo estimates. The distribution of these estimates are found in the right column of Figure 4. The discontinuity estimate from the actual state laws (presented in Panel D of Table 6) is represented as a vertical line in each figure. For the outcome of high school attainment, the actual estimate is in the left tail, but not too extreme. This is consistent with the estimate only being significant at the 10 percent level. For the outcomes of health status, excellent or very good health, and fair or poor health, we observe that the point estimate from the actual state laws is an extreme outlier relative to the distribution of placebo estimates, suggesting that the effect of SSA has a persistent effect on health and that it is not generated from the empirical design. 4.5 Potential Channels After establishing a relationship between SSA and long-run health for males, we now investigate whether educational attainment and labor market outcomes play a central role in the relationship between SSA and health. To examine these potential channels, we begin with our baseline specification (estimates presented in Panel A of Tables 5 and 6) and include controls that may be a channel, or highly correlated with a channel, for how SSA affects health. By comparing the coefficient estimates of PSSA between specifications, we can potentially trace out the mechanism through which SSA affects self-reported health. Specifically, if we include a rich set of education controls and observe that the effect of PSSA on health 16 The RDD results for labor market outcomes are similar in magnitude and significance to the main results. 14

16 significantly diminishes relative to the estimates from the baseline specification, then it is plausible that SSA is affecting health through the avenue of education. If we instead see no significant impact on health when a rich set of covariates is included, than those covariates are likely not correlated with the potential channel. Table 7 presents the results from this exercise. Panel A includes the baseline estimates with no additional controls. Panel B includes years of education fixed effects. Panel C includes fixed effects for labor force participation and employment. Panel D controls for personal earnings and personal earnings squared. And, Panel E includes occupation fixed effects using three digit occupation codes. In general, we do not observe a consistent pattern that suggests either educational attainment or labor market outcomes play a central role as mechanisms for the effect of PSSA on long-run health. This is not surprising given that we found no evidence within our data that PSSA significantly impacts education, other than high school attainment, or labor market outcomes. Furthermore, we would expect that the documented decrease in educational attainment associated with SSA for males would potentially decrease health (Lleras-Muney, 2005); further suggesting that the mechanism is not educational attainment. We also investigated whether PSSA affects health care utilization by regressing our main empirical specification, equation (2), on the following outcomes: number of days sick, indicators for health insurance, Medicaid, daily prescription drug use, visiting a doctor in the past year, and the number of doctor visits in the past year. We found no statistically significant effect on any of these outcomes. However, among males we found that being one year older at school entry decreases daily use by 1.87 percentage points from the mean of.20; the point estimate is close to being significantly different from zero at the ten percent level (p-value of 0.11). As discussed, a potential channel is through ADHD diagnoses and treatment. Since we cannot analyze ADHD in the SIPP, we looked to data from the Medical Expenditure 15

17 Panel Survey (MEPS) for the years The MEPS provides information on adult ADHD diagnosis through the Prescribed Medicine data files. Unfortunately, the MEPS data does not allow us to identify PSSA. Therefore, we can only compare whether adults diagnosed with ADHD are more likely to have lower self-reported health. Simple correlations from individuals aged show that adults diagnosed with ADHD are significantly more likely to have lower self-reported health. 17 This does not confirm that the effect of SSA on self-reported health is operating through ADHD diagnosis and treatment, however, it does suggests that ADHD diagnosis and treatment cannot be ruled out as a possible channel. 5 Discussion and Conclusion The preponderance of previous literature suggests that school starting age has a significant effect on long-run outcomes. This paper makes an important contribution by showing that SSA affects the long-run self-reported health of males. Amid growing health care costs in the U.S. and the influential role that an individual s self-reported health has on their daily life, understanding the role of SSA on health is important. Although we are unable to determine the exact mechanisms that explain this finding, we largely rule out educational attainment and labor market outcomes as potential channels. We conjecture that ADHD diagnosis and the use of prescribed stimulants among males that are young for their school cohort may be an important channel. Previous papers have consistently found that children in the U.S. who are older when they start kindergarten are less likely to be diagnosed with ADHD and less likely to use prescribed stimulants (Elder and Lubotsky, 2009; Elder, 2010; Evans et al., 2010). Data with detailed information regarding ADHD diagnosis and prescription stimulant 17 We estimated the correlation of self-reported health and having a clinical classification code of 652. Individuals with ADHD prescribed medicines were 10.4 percentage points less likely to have excellent or very good health and 8.9 percentage points more likely to have fair or poor health. These estimates were statistically different from zero at the one percent level and were robust to conditioning on observable covariates. 16

18 use would be valuable for future researchers studying the long-run effects of school start age and health. Since school dropout laws are tied to a student s age in the U.S., the estimated effect of SSA can only be interpreted as the net effect of school entry age and increased exposure to dropping out of school. Understanding the direction of the net effect is important since state laws continue to set compulsory schooling to age. For males, we observe that SSA decreases the likelihood of graduating high school. However, we find no affect for females nor for labor market outcomes in general. We believe that our estimates play an important role in contributing to the previous studies because we use variation across the U.S., rather than one or two states. Due to the difficulty of disentangling relative maturity from absolute maturity, policy recommendations with respect to the optimal school entry age are challenging. However, our findings coupled with evidence from others, suggest that SSA may have substantial heterogeneous effects across populations. The robust result of SSA on the self-reported health of males within this study is not without reservation. Although self-reported health has been shown to be a reliable proxy for general health, more objective measures of health would facilitate research to understand the mechanisms behind our findings. Furthermore, longitudinal data that links child health outcomes to adult health outcomes would be optimal. Our empirical analysis could be improved by utilizing data that provides exact date of birth, rather than month of birth, to more fully operationalize a RDD. With these limitations in mind, additional research investigating the affect of SSA on long-run health is needed. 17

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23 Figures and Tables Figure 1: Histogram of school entry laws Fraction School Entry Law Date 22

24 Figure 2: Distribution of interview age and predicted school starting age Fraction Interview Age Fraction Predicted Start Age 23

25 Figure 3: Robustness check: Excluding one cutoff date High School Health Status (1-5) School Entry Law Date School Entry Law Date Estimate 95% CI Estimate 95% CI Excellent or Very Good Health Fair or Poor Health School Entry Law Date School Entry Law Date Estimate 95% CI Estimate 95% CI 24

26 Figure 4: Regression discontinuity estimates and placebo estimates High School Months from Entry Date Frequency Estimated Coefficients Health Status (1-5) Months from Entry Date Frequency Estimated Coefficients Excellent or Very Good Health Months from Entry Date Frequency Estimated Coefficients Fair or Poor Health Months from Entry Date Frequency Estimated Coefficients 25

27 Table 1: Descriptive statistics (1) (2) Males Females Demographic Variables: White (0.376) (0.409) Black (0.326) (0.370) Age at interview (7.159) (7.091) Private High School (0.259) (0.260) Predicted school start age (0.315) (0.316) Education and Labor: Years of schooling (2.541) (2.490) High school degree (0.303) (0.286) Received GED (0.290) (0.291) Some college (0.494) (0.481) College degree (0.420) (0.439) Labor force participation (0.297) (0.413) Employed (0.363) (0.444) Personal monthly earnings ( ) ( ) Health: Self-reported health (1-5) (0.969) (0.989) Excellent health (0.468) (0.451) Very good health (0.483) (0.483) Excellent or very good health (0.460) (0.476) Good health (0.418) (0.434) Fair health (0.240) (0.263) Poor health (0.128) (0.138) Fair or Poor health (0.268) (0.292) Num. of Obs. 24,148 26,994 Data comes from the 1996, 2001, 2004, and 2008 SIPP. 26

28 Table 2: Falsification test: Effect of school starting age on race Coefficient (St. Error) (1) (2) (3) (4) Other Private Dependent Variable: White Black Race High School Panel A: Males Predicted School Starting Age ( ) ( ) ( ) ( ) Num. of Obs. 24,148 24,148 24,148 24,148 Panel B: Females Predicted School Starting Age ( ) ( ) ( ) ( ) Num. of Obs. 26,994 26,994 26,994 26,994 Data comes from the 1996, 2001, 2004, and 2008 SIPP. The dependent variable is listed in the top of each column. The regressions include fixed effects for birth month, interview age, cohort and state. Standard errors clustered at the state level are reported in parentheses. * 0.10, ** 0.05 and *** 0.01 denote significance levels. 27

29 Table 3: Effect of school starting age on educational attainment Coefficient (St. Error) (1) (2) (3) (4) (5) Years of High Some Dependent Variable: Schooling School GED College College Panel A: Males Predicted School Starting Age * * ( ) ( ) ( ) ( ) ( ) Num. of Obs. 24,148 24,148 24,148 24,148 24,148 Panel B: Females Predicted School Starting Age ( ) ( ) ( ) ( ) ( ) Num. of Obs. 26,994 26,994 26,994 26,994 26,994 Data comes from the 1996, 2001, 2004, and 2008 SIPP. The dependent variable is listed in the top of each column. Controls include month of birth fixed effects, age at interview fixed effects, state fixed effects, cohort fixed effects, and race fixed effects. Standard errors clustered at the state level are reported in parentheses. * 0.10, ** 0.05 and *** 0.01 denote significance levels. 28

30 Table 4: Effect of school starting age on labor market outcomess Coefficient (St. Error) (1) (2) (3) (4) Conditional on Employed Labor Force Log Monthly Log Monthly Dependent Variable: Participation Employed Earnings Earnings Panel A: Males Predicted School Starting Age ( ) ( ) ( ) ( ) Num. of Obs. 24,148 24,148 24,148 20,376 Panel B: Females Predicted School Starting Age ( ) ( ) ( ) ( ) Num. of Obs. 26,994 26,994 26,994 19,712 Data comes from the 1996, 2001, 2004, and 2008 SIPP. The dependent variable is listed in the top of each column. Controls include month of birth fixed effects, age at interview fixed effects, state fixed effects, cohort fixed effects, and race fixed effects. Standard errors clustered at the state level are reported in parentheses. * 0.10, ** 0.05 and *** 0.01 denote significance levels. 29

31 Table 5: Effect of school starting age on self-reported health status Coefficient (St. Error) (1) (2) (3) Health Excellent or Fair or Dependent Variable: Status (1-5) Very Good Poor Panel A: Males Predicted School Starting Age ** * *** ( ) ( ) ( ) Num. of Obs. 24,148 24,148 24,148 Panel B: Females Predicted School Starting Age ( ) ( ) ( ) Num. of Obs. 26,994 26,994 26,994 Data comes from the 1996, 2001, 2004, and 2008 SIPP. The dependent variable is listed in the top of each column. Controls include month of birth fixed effects, age at interview fixed effects, state fixed effects, cohort fixed effects, and race fixed effects. Standard errors clustered at the state level are reported in parentheses. * 0.10, ** 0.05 and *** 0.01 denote significance levels. 30

32 Table 6: Robustness checks: Effect of school starting age for males Coefficient (St. Error) (1) (2) (3) (4) (5) High Some Health Excellent or Fair or Dependent Variable: School College Status (1-5) Very Good Poor Panel A: State, Cohort, Age, Birth Month, and Race FEs Predicted School Starting Age * * ** * *** ( ) ( ) ( ) ( ) ( ) Num. of Obs. 24,148 24,148 24,148 24,148 24,148 Panel B: State, Cohort, Age, Birth Month, and Race FEs; State Trends Predicted School Starting Age ** ** *** ** *** ( ) ( ) ( ) ( ) ( ) Num. of Obs. 24,148 24,148 24,148 24,148 24,148 Panel C: State-Cohort, Age, Birth Month, and Race FEs Predicted School Starting Age ** ** *** ** *** ( ) ( ) ( ) ( ) ( ) Num. of Obs. 24,148 24,148 24,148 24,148 24,148 Panel D: RDD Linear Spline Discontinuity * *** ** *** ( ) ( ) ( ) ( ) ( ) Num. of Obs. 24,148 24,148 24,148 24,148 24,148 Panel E: RDD Linear Spline (BW=3 Months) Discontinuity ** * ** ( ) ( ) ( ) ( ) ( ) Num. of Obs. 12,050 12,050 12,050 12,050 12,050 Panel F: RDD Quadratic Spline Discontinuity ** ** ** ( ) ( ) ( ) ( ) ( ) Num. of Obs. 24,148 24,148 24,148 24,148 24,148 Data comes from the 1996, 2001, 2004, and 2008 SIPP. The dependent variable is listed in the top of each column. Standard errors clustered at the state level are reported in parentheses. * 0.10, ** 0.05 and *** 0.01 denote significance levels. 31