First in the Class? Age and the Education Production Function

There is a large literature on the so-called “relative age” effect in school, with results suggesting that being the oldest in the class is beneficial to a student. The concept was popularized by Malcolm Gladwell in his 2008 book Outliers. Over time, more and more parents—particularly those in affluent areas—have chosen to delay their child's entry into kindergarten to give them a strategic advantage in school (Deming and Dynarski 2008; Bassok and Reardon 2013). This practice is commonly referred to as academic “redshirting.”

The academic literature that has informed this phenomenon has been dominated by estimates of the relationship between the child's age and schooling outcomes, such as performance on standardized tests. Influential papers in this literature, such as Bedard and Dhuey (2006), have interpreted the resulting reduced-form coefficient on age as a “relative age” impact. But this parameter is actually a composite of three separate effects: that of the child's age at school entry, her age at the time of the test, and her age relative to her peer group. These three aspects of age often move together. For example, in this literature it is typical to compare end-of-year test scores of children with birthdays near school entry cutoff birthdates. In such a comparison, the child with the birthday after the cutoff (e.g., a child with an October birthday in a state with a 1 September cutoff) is not only older at school entry and at the time of the test than a child with a birthday right before the cutoff (e.g., an August birthday), but also in relation to her classmates. Recent literature has attempted to disentangle the effects of age at school entry from age at test, finding small positive effects of starting school younger that are dominated by larger positive effects of age at test (Black, Devereux, and Salvanes 2011; Carlsson et al. 2015). Less attention has been paid to the final piece: a child's age in relation to his peers.

Estimating the effect of relative age is important in its own right for better understanding the education production function. But it is also important for understanding the spillover impacts of educational policies and practices. For example, a policy change that moves the school entry cutoff date from 1 October to 1 September will not change the school entry age for most children (i.e., those born between October and August), but it will expose them to relatively older peers and thus reduce their relative age. Similarly, children who enter school on time in an area where substantial numbers of parents opt to redshirt will have their relative age shifted by the other parents’ choices to delay school entry. To understand the impacts in cases like these, that is, when own age is held constant but relative age shifts, it is important to have separate estimates of the effects of age and relative age.

To generate such estimates, we use data from Tennessee's Project STAR (Student–Teacher Achievement Ratio), a randomized experiment in which kindergarten students are randomly assigned to classrooms. As a result, their classmates’ age distribution is random, and their own relative age is randomly determined. We can also follow children with different relative age rankings over time to observe how their achievement trajectories compare. We find that, contrary to conventional wisdom, being relatively young improves test scores. In other words, having older peers improves achievement across children of the same age. This finding implies that having redshirted classmates has positive spillovers on children who enter on time. Further, our results suggest that the reduced-form benefit of age found in the prior literature is primarily being driven by an absolute age effect (some combination of age at entry and age at test effects), which more than offsets the negative impact of having relatively younger peers.

It is potentially helpful to think more precisely about these three distinct effects. First, older entrants have greater preparation for school, and may therefore perform better over both the short and longer term, because they have had more time to develop (they have had more months of life to play, hear language, etc.). This is the “age at school entry” effect. By the same token, however, older school entrants will always have more life experience, which may independently improve their academic performance. This is the “age at test” effect. The “relative age” effect, by contrast, stems from the role of the peer composition of a child's classroom in his achievement level. Higher-achieving peers may have positive spillover effects.¹ The effects of peer ability may load onto the age distribution of the class, because calendar age and test scores are highly correlated in early life. As a result, the age distribution of a student's classmates is also expected to contribute to achievement and may vary based on the child's own age.

Distinguishing between these effects is important because they have very different implications for educational policies and practices. For example, if largely reflects age at test, it would imply that redshirting or changes in school entry age regulations would have very little direct impact on children. It is therefore not surprising that recent work has focused on obtaining clean estimates of age at test effects (Black, Devereux, and Salvanes 2011; Carlsson et al. 2015). Likewise, if largely reflects a relative age effect, then postponing a child's school entry, either by redshirting or by changing school entry laws, has negative consequences for other children. On the other hand, if the parameter represents absolute age (whether driven by school starting age or age at test), peer spillovers from shifts in relative age may in fact be zero or even positive.

In this application, we specify relative age as the difference in age (in fractions of a year) between a child and the average of her classmates. That is, ⁠, where represents the average age of student i's classmates at the start of school. Thus, we assume that relative age is linear, continuous, increasing in own age, and decreasing in the average age of kindergarten classmates. This specification captures the zero-sum implications of manipulating relative age: In order for a given student to become relatively old, another student must become relatively young. Relative age, so defined, thus has implications for the distribution of achievement across students, but not its level. A key advantage of our data is that classmate age is randomly assigned within school, so our thought experiment compares two students of the same age who by random chance fall into different spots in the classroom relative age distribution.

With regard to previous literature, our approach is similar to that of Elder and Lubotsky (2009), who first pointed out the subtlety of interpreting the reduced-form parameter on age in model 1. Like us, Elder and Lubotsky (2009) separately estimate the effects of absolute age and relative age on end-of-year test scores and several other outcomes. Unlike us, however, they define relative age as the difference between a student's age and the average age of her schoolmates and use data from a sample, rather than the entire population of students within a school.²

Perhaps more significantly, there is an important (and somewhat nuanced) difference in the variation we use to identify the relative age impact, and therefore our results speak to different situations. The variation in peer age used by Elder and Lubotsky (2009) derives primarily from policy differences across states in minimum kindergarten starting ages. As a result, their estimates may in part reflect differences across states in other determinants of the pace of learning for relatively old children, such as the rigor of the kindergarten curriculum. Relatedly, Bedard and Dhuey (2012) estimate separate effects of increases in state-mandated minimum school entry ages for individuals whose ages were likely directly affected, and for individuals who were only affected indirectly (for example, through reductions in relative age) based on quarter of birth. They hesitate to interpret the latter estimates as “relative age” effects, however, because the educational experience of the entire cohort might have been changed by the policy shift. By contrast, the identifying variation in relative age in the current paper is from random differences in classroom age distributions. Our estimates thus hold constant the kindergarten curriculum and other factors: Not only do we compare children of different relative ages within the same state at a given point in time, but also within the same school.

To be sure, the parameters estimated by Elder and Lubotsky (2009) and Bedard and Dhuey (2012) are important, particularly for policy makers considering changing regulations governing age at school entry. Our approach, however, produces estimates that are more relevant for parents deciding whether to redshirt their child, and also for parents who are concerned about whether the redshirting behavior of others may harm their own child. Our results are broadly consistent with Elder and Lubotsky’s, in that both papers find the absolute age effect for test scores is strongly positive, whereas being relatively old actually lowers test scores in the early grades. Some of our results conflict, however, possibly because of the difference in the type of variation used to identify the estimates. In particular, Elder and Lubotsky find relative age effects dissipate as a child advances through school, whereas we do not find this pattern.

Two identification problems arise when estimating model 3. First, the coefficient on relative age may be biased, because children may be endogenously sorted across kindergarten classrooms on the basis of the ages of other children. We address this by using a dataset in which students were randomly assigned to classrooms, thus making peer average age randomly assigned. In the following we validate the random assignment assumption by showing that relative age is not systematically related to observables.

The second identification problem stems from endogeneity in a child's observed age in the kindergarten year. Some variation in age is due to differences in month of birth relative to the school entry cutoff. For example, in Tennessee at the time of Project STAR, a child was meant to be age five by 30 September in the year they enroll in kindergarten. Because we observe one cohort of students who entered school in September 1985, this implies that if everyone complied with the school entry rule, we would only observe students who were born between 1 October 1979 and 30 September 1980. Among children who comply with this requirement, a child born on 1 October would be three months older than a child born on 1 January. We seek to identify the absolute age effect from this type of variation. Not all families comply with the entry age rule, however, and we observe children who are born either before or after the expected range of birthdates. Students who are older than expected were likely retained in kindergarten or redshirted, and students who are younger than expected were likely enrolled early. Kindergartners with an age not as expected may differ in unobservable ways from on-time kindergartners. In particular, children who are a year older because they delayed entry or were retained are likely negatively selected, imparting a downward bias on ordinary least squares (OLS) estimates of both absolute age and relative age effects.

To isolate differences in age that arise only from differences in birth month relative to the entry cutoff, we adopt the same empirical approach as previous researchers and construct an instrument for a_i (and for the a_i component of relative age) using information on a child's birthday and Tennessee's cutoff birthdate for starting kindergarten.³ The instrument, “expected” age at the start of kindergarten (ea_i), uses variation in the month and day, but not the year, of kindergartners’ birthdays. Expected age is highly predictive of actual age, as shown in figure 1. The solid line in figure 1 illustrates the relationship between birthday and ea_i, under the assumption that the school year begins 1 September. The figure shows clearly that actual age on 1 September 1985 (daily averages of which are represented by the hollow circles) is strongly but not perfectly related to ea_i. In particular, actual age in fourth-quarter birthdays is sometimes below the predicted age, suggesting that some parents pushed their child forward to start school early. In the first through third quarters, average actual age is a little higher than predicted age, suggesting that some of these children were retained or redshirted.

Our preferred estimates are those that use expected age as an instrument for absolute age. Two-stage least squares (TSLS) estimates of will be consistent if ea_i is uncorrelated with unobserved determinants of achievement.⁴ Although we cannot test this assumption directly, we show in the following that expected age at the start of kindergarten generally does not predict observed characteristics of a child that are correlated with academic performance. These estimates capture local average treatment effects for compliers—children who enter kindergarten on time.

When it comes to estimating relative age effects, one could make a case for wanting to estimate those based on either the distribution of actual age or the distribution of expected age of a child's classmates. Because of random assignment to classes, both measures are uncorrelated with own age and with the error term in model 3. When we use the distribution of actual age of a student's classmates, some of the older kindergarten classmates will have lower than average ability for their age because they were held back by their parents or teachers on the basis of their perceived school readiness. Conversely, some younger kindergarten classmates will on average be relatively high ability for their age, signaled by the fact that they started school early. For us, this is the preferred estimate because it reflects actual variation in relative age from all sources, including academic redshirting. When we instead instrument for relative age using classmates’ average expected age, we isolate a relative age effect that abstracts from the fact that some of the observed older students have been redshirted or retained. This parameter is more comparable to that which has been estimated in the prior literature (e.g., Elder and Lubotsky 2009; Bedard and Dhuey 2012). Both sets of estimates are therefore interesting, and so we present both in table 5, our main results table.

Project STAR was an experiment designed to study the effects of class size on student achievement. In the fall of 1985, kindergarten students and teachers in 79 Tennessee schools were randomly assigned to three different class types: (1) small (with target enrollment of 13–17 students), (2) regular (with target enrollment of 22–25 students), and (3) regular with a full-time teacher's aide.⁵ This cohort was to have maintained its class type through third grade, after which all participants were returned to regular-sized classes. Random assignment of children to class types took place within schools. Our analysis exploits the fact that most, if not all, Project STAR participants would have been randomly assigned to classrooms, not just class types, as a result of the experimental design.^6,7

We restrict our estimation sample to participants for whom each of the available background characteristics (birthday, race, gender, free lunch status in kindergarten) and kindergarten teacher characteristics (experience, education, and race) is observed.⁸ To construct average age and other characteristics of kindergarten classmates, however, we use all available data on the Project STAR kindergarten cohort, not just those individuals with nonmissing outcomes data.

Table 1 gives summary statistics on these students and their teachers in our estimation sample. Consider first the statistics on age, given in panel A. As has been found in nationally representative data, children in our sample tend to be slightly older at the start of kindergarten than expected (5.43 years old versus 5.38 years old). Approximately 6 percent of students are older than expected at the start of kindergarten, due to either retention or delay, and 1.3 percent are younger than expected.⁹ The standard deviation of relative age exceeds that of age and implies a standard deviation in the average age of a child's kindergarten classmates of about 1.11 months. The within-school variation in kindergarten classmate average age that we use for identification is of similar magnitude.

The Project STAR sample is not nationally representative. As shown in panel B, nearly half of Project STAR participants received free or reduced-price lunch in kindergarten, and 33 percent were black. By comparison, only 15.4 percent of five-year-olds in the United States were black in fall 1985.¹⁰ About 17 percent of kindergarten teachers were black, 35 percent had master's degrees, and 10 percent had fewer than two years of experience (panel D). Students were roughly equally divided across class size types (panel E).

Our main outcomes come from tests administered to STAR participants through the end of high school. In the spring of kindergarten, STAR participants were administered the Stanford Achievement Test. For participants still attending public school in Tennessee, we have scores on the Comprehensive Test of Basic Skills in grades 5 through 8, regardless of year attended.¹¹ Both tests are multiple-choice standardized tests with reading and math components. We average the reading and math scale scores on each test, then standardize this average to have a mean of zero and a standard deviation of one using data on all STAR participants with nonmissing test scores in a given year. Thus, coefficient estimates in the test-score models are in standard deviation units. Table 1, panel F, shows that the kindergartners in our sample scored on average 0.12 standard deviation above the mean in spring 1994, when they would have been in eighth grade with normal school progression. Kindergarten attendees may have been slightly positively selected because it was not mandatory for the STAR cohort to go to kindergarten.

Our analysis focuses on test scores at the end of kindergarten (in spring 1986) and in spring 1994, when STAR participants progressing through school normally would have been completing eighth grade.¹² We focus on the spring 1994 scores because many existing studies have considered the relationship between age and test scores in eighth grade. We present estimates for the year that the cohort was expected to be in eighth grade instead of eighth-grade test scores because our sample includes individuals in the same school-entry cohort, and we wish to have our estimates be consistently interpretable across tests taken at different points in time. Because either one of the treatment variables may have affected grade progression, we also estimate separate models for whether a child was enrolled below eighth grade when tested in spring 1994. By this measure, one quarter of students tested are categorized as having been retained (panel F).

Our final outcome measure is an indicator for whether a respondent took the ACT or SAT college-entrance exam. Researchers gathered college-entry test information on STAR participants from graduating classes through 1999 (i.e., for students who graduated early, on-time, or no later than one year behind “normal” grade progression) from all high schools in the United States.¹³ Perhaps not surprisingly, individuals in our sample are less likely to have taken the ACT or SAT (47 percent) than individuals in the United States overall (table 1, panel F).¹⁴

Before turning to the estimates, it is useful to provide evidence that our instruments for absolute and relative age are unrelated to unobserved determinants of test scores, a necessary assumption for identification. To this end, the first three columns of table 2 give the coefficients on absolute age and relative age, ea_i and ⁠, along with their joint significance, in models where observed characteristics are the dependent variables. Columns 4 through 6 do the same, but replacing the measurement of relative age with the predicted relative age alternative, ⁠. In table 3, we present the results from similar exercises where the dependent variables are instead indicators for whether key outcomes are observed.¹⁵ The underlying regressions also include school fixed effects, because random assignment of children to class types took place within schools. Standard errors are consistent for heteroskedasticity and correlation of error terms among children in the same kindergarten classroom.

The estimates largely serve to validate our identification strategy and support the assumption that students were randomly assigned to classrooms.¹⁶ As shown in the first three columns of table 2, in only one case are the baseline instruments individually significant predictors of an observable—having a kindergarten teacher with a master's degree (columns 1 and 2)—but these relationships are only marginally statistically significant, and teacher education is not a strong correlate of academic outcomes in these data. For our preferred set of instruments, the instruments are jointly significant for only one variable—whether a child was eligible for free or reduced-price lunch in kindergarten (p = 0.018, column 3). Consistent with these findings, including all of these variables as controls has little impact on the TSLS point estimates, as shown subsequently. Table 3 shows that the instruments also do not predict observation of our dependent variables, individually or jointly, using either identification strategy. This suggests observations with missing values of dependent variables are random with respect to the identifying variation in absolute and relative age, and the estimates presented here are not biased by sample selection.

To provide a useful benchmark to the prior reduced-form literature, table 4 presents OLS and TSLS estimates of the coefficients on own age from a version of model 3 that omits relative age. The dependent variables include the standardized average of math and reading scores at the end of kindergarten and eight years later, when children progressing through school normally would have been in spring of eighth grade. Both the OLS and TSLS estimates are also plotted in figure 2, along with OLS and TSLS estimates for test scores in the intervening grades.¹⁷ Table 4 also includes estimates of age gradients in our proxy for grade retention—whether a respondent is enrolled in a grade lower than expected in 1994—and in taking a college-entrance exam. All specifications include fixed effects for school attended in kindergarten, and estimation accounts for heteroskedasticity and arbitrary correlation of error terms within kindergarten classrooms.

Consider first the estimates for test scores at the end of kindergarten, in column 1. The OLS estimates (panel B) imply that STAR participants who were one year older at the start of kindergarten scored on average about 0.24 standard deviation higher at the end of kindergarten (column 1). These estimates will be biased downward, however, if, as we expect, children previously retained or delayed in entering kindergarten are negatively selected on unobservables. As described earlier, we confront this possibility by comparing children who should have entered kindergarten with a one-year difference in age, given their birthdays; if birthday is randomly assigned, these children will be on average identical in all other ways, such as inherent ability. As shown in panel A of the same column, TSLS estimates using expected age at kindergarten entry as an instrument imply that the test-score differential between two otherwise identical children who enter kindergarten with a one-year difference in age is a significantly higher 0.71 standard deviation.¹⁸ Adding controls for predetermined individual and classroom characteristics (column 2) does not appreciably change this estimate. This estimate is comparable to those previously found in nationally representative data for the United States.¹⁹

The test score differences between older and younger school entrants decline as children progress through school.²⁰ For example, the TSLS estimate of the age gradient in test scores is 0.22 standard deviation in spring 1994, when children progressing through school normally would have been in eighth grade (column 3). Figure 2 shows that most of the decline in the gradient occurred by the end of elementary school, as the TSLS estimates for grades 5 and 6 (with normal grade progression) are not much larger in magnitude. Older school entrants are also significantly less likely to have been retained at any point in the eight years following kindergarten (column 4). Again, these estimates are in line with what has previously been documented for test scores and grade retention at the end of eighth grade in the United States.²¹ Unlike previous research, however, we do not find that older school entrants are more likely to take a college entrance exam (column 5).²² In general, however, the consistency of our estimates with the existing literature suggests the possible broader applicability of inferences made from our data.

As discussed previously, the reduced-form estimates presented in table 4 capture the combined effects of absolute age and relative age. In table 5, we present estimates of model 3, which allow us to separately identify these effects. Our preferred TSLS estimates, in panel A, identify own-age effects from only variation in month and day of birthday—that is, they account for negative selection among students who were retained or redshirted—but measure peer effects relative to the actual age distribution. That is, in panel A we use ea_i as an instrument for absolute age and as an instrument for relative age. In panel B, we present estimates from the alternative TSLS model keeping all else the same but identifying peer effects based on predicted age (i.e., using as an instrument for relative age). For completeness, OLS estimates are presented in panel C.

The first thing to notice in table 5 is that all of the estimates for relative age effects on test scores (columns 1 to 3) are negative—a finding that holds true across both TSLS approaches and in OLS.²³ This suggests that being relatively old, holding own age constant, harms student outcomes. Accordingly, controlling for relative age increases estimates of the coefficient on school entry age (compare column 1 in tables 4 and 5). While the standard errors on our preferred TSLS estimates in panel A do not allow us to reject a positive relative age effect for test scores at the end of kindergarten, we can reject a positive effect for test scores eight years later.

Figure 3 shows how the TSLS coefficients on age and relative age evolve across the grade levels, based on our preferred estimation strategy (as in panel A of table 5). The figure shows that the point estimate on relative age declines (increases in magnitude) as the cohort ages, and by sixth grade we can reject that relative age has a positive impact on test scores.²⁴ On the other hand, the coefficient on absolute age is positive and relatively stable in the years subsequent to kindergarten. In general, our findings for test scores are thus inconsistent with the interpretation of reduced-form age gradients in test scores, such as those presented in table 4 or in figure 2, as (positive) relative age effects.

Turning to magnitudes, our estimates imply that a one-year increase in relative age in kindergarten lowers test scores eight years later by about 0.43 standard deviation. A one-year increase in relative age is a relevant margin only for a child who delays school entry, however, and such a child would also be one year older in absolute terms. The net impact of redshirting is the sum of both coefficients, which is positive and consistent with the estimate of a positive net effect of age for spring 1994 test scores (table 4, panel A, column 3). We therefore would not conclude that delaying kindergarten entry is harmful to the academic achievement of the child experiencing the delay in the following sense: The child's performance in a given grade is predicted to be higher if the child has been redshirted. This is driven by the fact that the child will be a year older in absolute terms at the time of the test and not because the child is relatively old. But in fact, at any given age, the child's achievement will be harmed by being among the oldest in the class.

Importantly, the estimates in table 5 allow us to rule out negative effects for a given child of other families’ redshirting decisions. In fact, we can conclude with some confidence that there are positive spillovers from this practice.²⁵ Consider how classmates’ redshirting decisions change the relative age of a child with a birthday outside of the typical redshirting range, such as a child born in January in a state with a 1 September school entry cutoff. Although the January-born child is not likely to be redshirted himself (i.e., his own age will be unaffected) his classmates’ decisions about whether to redshirt will alter his relative age. For example, if half of classmates born in July or August opt to redshirt, then on average the January-born child's relative age declines by one month.²⁶ Other plausible redshirting “rules”—such as only boys born in summer redshirt or only boys born in summer who will also be the youngest in the class redshirt—yield an average decline in relative age of about 0.5 to 1.2 months for a child born in January. Note that the redshirting rules we used in our simulations yielded an overall redshirting rate between 4 and 9 percent, similar to rates observed in recent years (Deming and Dynarski 2008; Bassok and Reardon 2013).

According to our estimates, holding one's own age constant, a one-month decline in relative age in kindergarten—the margin of variation typical in our data and the likely shift induced by others’ redshirting behavior—raises test scores eight years later by a statistically significant 0.036 standard deviation. In other words, classmates’ redshirting behavior is predicted to benefit the student. Likewise, a one-month decline in relative age in kindergarten increases the likelihood of taking the ACT or SAT by about 1.3 percentage points (significant at the 10 percent level, column 5). This is a larger effect than would be predicted on the basis of the relationship between spring 1994 test scores and college-exam taking alone, suggesting the benefits of being relatively young continue to accumulate through high school or are working through other (noncognitive) channels.²⁷

The corresponding estimates in table 5, panel B, which use variation in the expected entry ages of classmates instead of their actual ages, are noisier, but are broadly consistent with these findings. If anything, however, they imply larger negative impacts of relative age, and negative impacts that emerge as early as the end of kindergarten. In particular, a one-month decline in relative age in kindergarten increases test scores by a marginally significant 0.06 standard deviation (0.724/12; column 2). This finding serves to reinforce the interpretation that the mechanism for the negative relative age effects is that children benefit from having higher-achieving, better-behaved peers. In other words, while the first instrumental variables approach does not remove the negative selection of some older kindergarten classmates, the second instrumental variables approach identifies the peer component using variation from children with abilities and behavior consistent with their ages and finds larger point estimates, especially in the kindergarten year.²⁸

The likelihood of delayed school entry is more common for some subgroups in the population. For example, past research has found that boys are much more likely to be held back than girls. Children from higher-income families are also more likely to start kindergarten at an age older than expected (West, Meek, and Hurst, 2000; Bassok and Reardon, 2013). We see a similar pattern in our data. For example, nearly 8 percent of boys, but only 3.7 percent of girls, are older than expected in kindergarten.²⁹

For boys and higher-income children, revealed preference thus suggests that being higher up in the classroom “pecking order” is more important for academic outcomes. If this were the case, relative age effects for these groups should be less negative, or even positive. At the same time, recent research on peer effects has found that girls are more responsive to higher-achieving peers than boys (Jackson 2012; Lavy, Silva, and Weinhardt 2012). This suggests being relatively young may be more beneficial to girls. To investigate these possibilities, we estimated separate models by gender and free or reduced-price lunch status in kindergarten. We present the TSLS estimates by gender in table 6 and by free lunch status in table 7. We return to our baseline identification strategy, where we instrument for relative age using the difference between a student's expected age and the average actual age of her peers. Per our argument above, this approach should deliver estimates of relative age that are closer to being in the positive range. For the purposes of comparison and interpretation, each table includes subsample-specific means of the dependent variables.

We find in table 6 that the relative age effect on test scores becomes more negative for boys as the cohort ages, and is statistically significant and negative for eighth grade test scores. Relative age is only significant for girls when looking at retention by eighth grade, and that estimate is only marginally significant. Turning to absolute age, in kindergarten its effect is similar for boys and girls.³⁰ After kindergarten, however, the absolute age effect drops substantially for girls and is relatively small and insignificant for taking the ACT or SAT. Among boys, the absolute age effect is stronger throughout, and is still marginally statistically significant for taking the ACT or SAT. These results suggest that boys may be more sensitive to having higher-performing peers, contrary to the existing literature.

In table 7, we separately examine effects by whether a student qualifies for free or reduced-price lunch. Relative age effects are stronger for low-income students, suggesting that being exposed to older, higher-scoring peers is more important for low-income students than for higher-income ones. At kindergarten entry, there is no difference in own-age effects between students who do and do not qualify for free or reduced-price lunch. Subsequently, however, the own-age impact remains strong only for low-income children, where it is a strong predictor of eighth grade test scores, grade retention, and whether a student takes a college-entrance exam. For higher-income students, the own-age effect declines and is not statistically significant in later grades. These results—stronger age effects for low-income students—stand in contrast to the observed patterns in which higher-income children are substantially more likely to be redshirted.

In this paper, we have estimated the net effects of having older peers—and being young relative to one's peers—using data from an experiment where children of the same age were randomly assigned to different classrooms in kindergarten. We find that, holding own age constant, children who were young relative to their kindergarten classmates generally performed no worse on achievement tests, were no more likely to be retained, and were no less likely to take the ACT or SAT. In fact, though some of our estimates are imprecise, having older classmates appears to have made the average child better off. And while our analysis of heterogeneity suggests that absolute age effects might be more present for boys (consistent with the higher incidence of delay for them) on net, boys and higher-income children still appear to benefit from having older kindergarten classmates.

These findings suggest that the reduced-form age effects frequently estimated in the literature on school-entry age are better interpreted as reflecting the positive impact of being older in an absolute sense, rather than in a relative one. In other words, when we separate the reduced-form age parameter into absolute age and relative age, we find that, after holding own age constant, being old relative to one's peers is predicted to reduce a student's academic achievement. When a student is redshirted, the negative effect of being relatively old is outweighed by the positive effect of being absolutely older, yielding a positive overall (reduced-form) effect.

Furthermore, our findings suggest that the tendency for some parents to opt to hold back their child's kindergarten entry, so-called “redshirting,” does not harm the student's classmates by making them relatively younger in the classroom age distribution. In fact, the spillover effects are predicted to be positive, yet modestly sized. Likewise, our estimates imply that the consequences of increasing minimum school entry age laws for children whose own entry ages are not directly affected (for whom relative age declines but absolute age remains unchanged) are likely to be positive. Our estimates have held school entry age regulations constant, however, and thus some caveats apply when generalizing to this scenario.

All in all, our findings are consistent with the broader peer-effects literature documenting positive spillovers from having higher-quality peers. They add another dimension to the evidence on how kindergarten classrooms matter over the long term (Chetty et al. 2011). The ages of a child's kindergarten classmates—a feature of the kindergarten experience than can be easily manipulated by school principals—appear to have a lasting impact on that child's own school outcomes.

We thank Bruce Sacerdote for helpful conversations. We are also grateful to Joshua Angrist, Sandra Black, Kristin Butcher, David Card, Damon Clark, Ethan Lewis, Jens Ludwig, Heather Royer, Douglas Staiger, two anonymous referees, and seminar participants at Case Western Reserve University, Dartmouth College, the Federal Reserve Bank of San Francisco, the University of Florida, Wellesley College, the Association for Public Policy Analysis and Management Fall Conference, and the Society of Labor Economists Annual Meeting for comments on earlier drafts. All errors are our own.