Creating winners and losers: date of birth, relative age in
school, and outcomes in childhood and adulthood
Pablo A. Peña
August 2015
Abstract
This article presents three contributions. First, we estimate the causal effect of relative age (i.e.,
how old a person is relative to her school classmates) on test scores for a sample of students born
between 1992 and 2004 using a policy experiment that shifted four months the cutoff date for
school eligibility in Mexico. We exploit three distinct sources of identification and obtain similar
estimates. One year of relative age confers and advantage in test scores that ranges between 0.2
and 0.4 standard deviations. Second, using date of birth as a proxy for relative age in school in a
sample of Mexican adults born between 1960 and 1980, we estimate relative-age effects in six
labor and marriage market outcomes: college attainment, employment status, earnings, having
employer-provided medical insurance, college attainment of the spouse, and number of children.
We find significant relative-age effects in the six outcomes. Third, we present a theoretical
model to show that, starting with the same relative-age effects in academic performance in
childhood, wealth could magnify, attenuate or even reverse the sign of relative-age effects in
adulthood outcomes. This “anything goes” theoretical result is useful in interpreting different
estimates of relative-age effects in adulthood outcomes across countries. Altogether, the findings
indicate that institutional features of educational systems create “winners” and “losers” in
academic performance via relative age in school, ultimately affecting labor and marriage market
outcomes in adulthood, although possibly to varying degrees depending on other conditions such
as wealth.
Key words: relative-age effect; school-entry age.
JEL Classification: I21, J01, J13
1
1
Introduction
Everywhere in the world formal education has rules that make the birthdate of a child a
determinant of how old she is relative to her classmates. Elementary instruction is organized in
grades that are one year long. At the same time, there are cutoff dates for school eligibility:
children must be of a certain age by a specific date of the year in order to be allowed to enroll in
school. The combination of birthdates spread along the calendar, cutoff dates for school
eligibility, and year-long grades, mechanically produces age differences of up to one year among
classmates.
A well-established fact in the literature is that on average older students outperform
academically their younger classmates. Studies in a number of countries have documented
systematic differences in test scores favoring older students within the same grade. Those
differences are usually referred to as “relative-age effects.” Panel I of Table A in the appendix
presents a summary of studies on relative-age effects in academic performance.1 Most estimates
suggest that a difference of approximately one year of age between classmates is associated with
a difference of 0.1 to 0.5 standard deviations in tests scores.
There are two potential explanations for relative age effects in academic performance. The
first is that gaps in test scores are a reflection of differences in maturity that would not be
observed if students were tested at the exact same age. In other words, the observed relative-age
effects could be an artifact of age-at-test differences without necessarily implying real gaps in
skills ceteris paribus. The second explanation is that, when exposed to the same educational
experiences, younger students are less effective at learning than their older classmates. In this
case, relative age differences would result in real gaps in skills.
The best available evidence supports the first explanation over the second. Black, Devereux
and Salvanes (2011) use IQ tests given at different dates to individuals of similar age and find
that relative-age effects are mostly due to age-at-test differences. Once they control for age at
test, the age of a person relative to her school classmates has a small and negative effect on test
scores.
Even if relative age effects were solely due to age differentials at the moment of testing, they
are relevant from an economic perspective. Albeit illusory, systematic gaps in test scores among
classmates could affect human capital investment decisions under incomplete information.
Economic theory predicts that people with greater “ability” have an incentive to invest more
in their human capital (Becker 1964). However, ability is neither entirely nor directly observable.
1
Table A should be interpreted with caution because of potential “publication bias” favoring significant
results. Researchers finding no relative-age effects might decide not to attempt the publication of their results.
Franco, Malhotra and Simonovits (2014) provide evidence of publication bias in the social sciences. They find that
authors are less likely to write up and submit null findings.
2
2
To make decisions regarding investments in human capital, people must infer their ability from
their interaction with the world. How well someone does in school, particularly in standardized
test scores, is commonly seen as an indicator of ability. Students, parents, teachers, and
educational authorities drawing inferences on ability from signals biased in favor of older
students might turn illusory ability differentials into real differences in later outcomes that affect
welfare, such as educational attainment and earnings. 3
Several studies have found relative-age effects in intermediate outcomes that shape students’
academic paths (see Panel II of Table A.) According to their results, relatively older students are
less likely to be classified as having a learning disability, and they get into more demanding or
higher-quality tracks. They are more likely to have intentions to attend college, and to enroll in
flagship post-secondary institutions.4 To some degree, the evidence for adulthood outcomes
points in the same direction. Of the seven studies shown in Panel III of Table A, six find relativeage effects in educational attainment, and four find relative-age effects on wages or earnings.
Overall, the evidence indicates that relative age in school could be creating gaps that persist into
adulthood.
Properly accounting for relative-age effects in academic performance could increase fairness
and enhance efficiency. If ability signals were corrected by relative age, identical individuals
with different academic performance solely due to their relative age would not be treated
differently by the school system, their parents and even themselves. At the same time, more
human capital investment could be channeled to truly high-ability individuals otherwise
perceived as low-ability because of their lower relative age.
To properly account for relative-age effects we need unbiased estimates of the causal effect
of relative age on academic performance. Such task presents two challenges. The first is the
endogeneity of relative age. Parents can affect their children’s relative age by postponing their
school entry—due to lack of readiness or to give them an edge. School officials can also affect
relative age through grade retention of underperforming students. The second challenge is the
endogeneity of birthdates. To some extent, parents can choose in what season they have children,
and parents with different attributes might aim for different seasons. Thus, children’s
characteristics might not be independent of their season of birth. The endogeneity of relative age
2
Following Becker (1964), “‘ability’ would be measured by the average rate of return on human capital” (p.
98), and those “who produce more human capital from a given expenditure [would be said to] have more […]
‘ability’” (p. 124).
3
An example of how biased signals early in life can turn into differentials in adult outcomes is the case of
professional hockey players documented by Barnsley, Thompson, and Barnsley (1985), and made widely known by
Malcolm Gladwell’s bestseller Outliers: the story of success.
4
The study of Bellari and Pellizzari (2008) on grades in college is an exception. They find negative relativeage effects. The authors argue their result might be driven by positive relative-age effects in non-cognitive skills.
3
and season of birth implies that Ordinary Least Squares estimates of relative-age effects might be
biased.
Some studies have resorted to institutional rules to address the endogeneity challenges and
identify the causal effect of relative age on test scores. Following Bedard and Dhuey (2006), the
most frequent approach is to instrument students’ relative age with their “assigned” or
“expected” relative age, that is, their relative age computed under the assumption that students
enroll on time are not held back by parents or retained by school officials. A second approach is
to use differences in school eligibility cutoff dates across countries or local jurisdictions as a
source of identification (Bedard and Dhuey 2006, Elder and Lubotsky 2009, Sprietsma 2010,
Crawford, Dearden and Meghir 2010). A third approach is to use the discontinuity in relative age
created by the school eligibility cutoff date as the identification source (McEwan and Shapiro
2008, and Crawford, Dearden and Greaves 2014). 5
The general validity of the identification strategies mentioned above has been questioned. In
the case of using assigned relative age as an instrumental variable, a potential problem is the
violation of the monotonicity assumption discussed by Barua and Lang (2009). They argue that
greater assigned relative age increases actual relative age for some students but it could also
reduce actual relative age for others by decreasing their likelihood of being held back, creating
potential biases of unknown magnitude and direction. In the case of estimates based on the
discontinuity around the cutoff date, a potential threat is the precise manipulation of birthdates
around the cutoff. Shigeoka (2014) provides compelling evidence of this type of manipulation in
Japan, where redshirting is not permitted. There seems to be a deliberate effort to manipulate
birthdates to postpone school entry—although that does not seem the case in the studies of
McEwan and Shapiro (2008) and Crawford, Dearden and Greaves (2014).
Even if the estimates of relative-age effects were valid from a technical perspective, there is
an issue of how general their interpretation can be. Most studies of relative-age effects in test
scores focus on high-income countries. According to Table A only three countries in Africa,
Asia, and Latin America have been studied: Japan, Korea, and Chile. The role of countries’
wealth in magnifying or attenuating relative-age effects is theoretically unclear. In consequence,
whether the results for high-income countries can be generalized to lower-income contexts
remains an open question that needs to be addressed empirically.
This study presents three contributions. First, it provides estimates of relative-age effects in
test scores in Tlaxcala, one of the poorest states of Mexico—its income per capita is comparable
to that of Jamaica, Namibia or Thailand. We use test score data in grades 3 to 9 for students born
5
Other studies claim to use the discontinuity as source of identification but instead of a regression
discontinuity design they use fixed-effect models with monthly- or quarter-level data to estimate relative-age effects.
Those studies were not counted as using the discontinuity as the source of identification.
4
between 1992 and 2004, and estimate relative-age effects using a policy experiment: an
unanticipated reform that shifted four months the cutoff date for school eligibility. To our
knowledge, this is the first study that uses a change in the cutoff date for school eligibility to
identify relative age effects. 6 We estimate relative age effects by comparing pre- and post-reform
cohorts across seasons of birth using a difference-in-differences approach. At the same time,
since we have exact birthdates (something rare in the literature) we estimate the impact of
relative age at the unanticipated post-reform cutoff date using a regression discontinuity
approach. For comparability with other studies, we also estimate relative age effects using
assigned relative age as instrumental variable—as most other studies. Lastly, we compare sideby-side the estimates produced by the three distinct identification sources using the same data.
Relative-age effects in academic performance among school children are relevant to the
extent they make a difference in adulthood—otherwise they would be nothing but a curious fact.
The second contribution of this study is the estimation of relative-age effects in six outcomes in
the labor and marriage markets using a sample of Mexican adults born between 1960 and 1980.
The outcomes studied are: college attainment, employment status, earnings, having employerprovided medical insurance, college attainment of the spouse, and number of children. Relative
age in school is proxied with the date of birth. People who presumably were older relative to
their school classmates on average attained more college education, earn more, and have more
educated spouses. Relative age is associated with a higher probability of having employerprovided medical insurance among men, and with a higher probability of being occupied and
having fewer children among women.
The diversity in the results for adulthood outcomes found in the literature (see panel III of
Table A) compels us to theorize reasons why relative-age effects in adulthood outcomes could be
observed in some countries but not in others, especially given that relative-age effects in test
scores are observed everywhere. The third contribution of this study is a theoretical model à la
Becker to analyze the role of wealth in the persistence of relative-age effects from childhood into
adulthood. The model shows that it is a priori unclear whether we should expect larger relativeage effects in adulthood in poorer countries relative to rich countries, or vice versa. Wealth can
magnify, attenuate or even reverse relative-age effects in adulthood. Based on this “anything
goes” result, we can expect differences in relative-age effects in adulthood across countries due
to wealth disparities.
The remainder of the article is organized as follows. Section 2 presents the estimates of the
causal effect of relative on test scores in childhood. Section 3 shows the estimates of relative-age
6
Smith (2010) uses a policy change in the starting-school date in Canada that affected some students but not
others. The change was repealed soon after, students were reassigned, and the distribution of relative age was
unaffected.
5
effects in adulthood outcomes. Section 4 presents the theoretical model. The findings are
summarized in Section 5.
2
Relative-age effects in childhood
In this section we present the estimates of the causal effects of relative-age on test scores in
grades 3 to 9 using a sample of students in Tlaxcala, Mexico. The novelty of our estimates
presented lies in the use of an unanticipated change in the cut-off date for school eligibility as
part of the identification strategies. Additionally, this is the first study of relative-age effects in
test scores in a low-income context.
2.1
Institutional background
The state of Tlaxcala is located 75 miles east from Mexico City. It has a population of 1.17
million and a land area of approximately 1,550 square miles—it is similar to Rhode Island in
both respects. In 2006, Tlaxcala had an income per capita of roughly half the national average.
As the rest of Mexico, Tlaxcala has a comprehensive educational system—without academic
tracking. Students can enroll in preschool approximately at age three, and they start school
approximately at age six. They are expected to attend three years of preescolar, six years of
primaria (grades 1 to 6), three years of secundaria (grades 7 to 9), and three years of
bachillerato (grades 10 to 12). In order to enroll in preschool, students in Tlaxcala must be at
least three years old by December 31 of the year of enrollment. To enroll in elementary school,
they must be at least six years old by December 31 of the year of enrollment.
Dropout rates at each level are crucial for the appropriate interpretation of the estimates of
relative-age effects in test scores for different grades. Since students’ relative age might affect
the decision to drop out of school, there might be self-selection into the sample of students for
whom we observe test scores. In Tlaxcala the dropout rate in primaria is 0.7%, and 97.0% of
those who complete that level continue in school. In secundaria the dropout rate is 15.6%, and
99.5% of those who complete it start the next level, bachillerato, where the dropout rate is
35.8%. 7 Since we use data for grades 3 to 9, the estimates for the higher grades must be
cautiously interpreted since some degree of self-selection into staying in school could be taking
place.
7
Sistema Nacional de Información Estadística Educativa of Mexico’s Ministry of Education, academic year
2011-12.
6
2.1.1
Test score data
We use test scores from ENLACE, a high-stakes national standardized test given between 2006
and 2013 at the end of every academic year (around the start of June) to students in grades 3 to 9
and 12.8 The test is grade-specific and was designed, administered and graded by the federal
Ministry of Education. It covers three subjects: Spanish, Math, and a rotating third subject
(Science, Ethics, etc.) ENLACE constitutes a virtual census of the student population in the grades
covered.
The Ministry of Education of Tlaxcala provided the 2009 and 2012 individual test score data
for every student in the state, grades 3 to 9. The data include the Unique Population Registry Key
(CURP) of every student, which contains the birthdate as stated in the birth certificate. Some
birthdates are incomplete, and some others are invalid or anomalous (extremely young or old)
potentially due to data-entry mistakes. Of the 162,186 students tested in 2009, 4,870 had no
CURP recorded, two had invalid information, and nine were anomalous (born before 1980 or
implied enrolling at age four or younger.) For the 2012 test, out of the 161,295 test takers, 2,619
had no CURP recorded, 20 were invalid, and two were anomalous. Table 1 shows the composition
of the sample of analysis by year of assessment (2009 or 2012), year of birth of the students, and
grade attended. The observations without CURP, or with an invalid or anomalous birthdate are
grouped into the “N.A.” category.
Relative to previous studies, the data analyzed here have two distinctive features. First, they
cover seven contiguous grades. Therefore, we are able to observe at the same point in time
students of the same age enrolled in different grades. In contrast, most studies rely on singlegrade test score data. Second, our data provide exact dates of birth, allowing the study of age
differences of up to one day. Most studies in the literature rely on coarser birthdate data and
measure age differences in months.
We define the relative age of a student as the difference between her age (in days) and the
average age for her grade in the state (in days) divided by 365.25. We standardize test scores by
grade, setting the mean to zero and the standard deviation to one. Figure 1 shows relative age and
test scores in the 2012 data for students born between January 1997 and December 2003, by
month of birth. The top panel shows average and median relative age of test-takers. The bottom
panel shows average test scores in Spanish and Math, in standardized units relative to the
students in the same grade.
On average, students born in January are older than their classmates, whereas those born in
December are younger. The relationship is starker for median relative age. The differences in
median relative age between students born in January and December reach almost a full year.
8
ENLACE is scheduled to be replaced in 2015 with a test that will not be high-stakes.
7
The bottom panel shows a pattern in test scores that mimics the relative age pattern. Those born
earlier in the year on average have higher test scores than their classmates, and those born later
have lower test scores. For some years of birth the differences between those born in December
and those born in January exceed 0.2 standardized units.
It is worth emphasizing that Figure 1 shows students grouped by date of birth regardless of
grade attended. For instance, December 2001 includes all students born in that month regardless
of the grade they were attending at the time of the test. In other words, the patterns in relative age
and test scores in Figure 1 include redshirting and grade retention. It is clear that relative age and
test scores are not independent from date of birth. On average, children born earlier in the year
are older relative to their classmates and perform better in standardized tests.
2.1.2
The reform
The December 31 cutoff date is relatively recent in Tlaxcala. Prior to 2003 the cutoff date for
school eligibility was September 1. The shift took place in the context of a federal push to allow
earlier enrollment. In 2002 federal and state authorities agreed to make the September 1 cutoff
flexible for ineligible students who showed “enough maturity.” 9 In 2006 the federal law was
reformed and the cutoff date was moved from September 1 and December 31. 10
Figure 2 shows relative age and test scores in the 2009 data for students born between
September 1993 and December 2000, by month of birth.11 Relative age and test scores show a
saw-tooth pattern similar to that in Figure 1. However, the location of the highest and lowest
points in Figure 2 differs across cohorts. The shaded areas mark the months of September to
December. In the first four years shown, average and median relative age are higher in the
shaded areas than in the non-shaded areas. In the last four years shown, the relationship is
reversed: average and median relative age are lower in the shaded areas. The reform changed the
distribution of relative age. Students born in September through December became relatively
younger and the rest became relatively older. The change in the pattern in relative age is matched
by the pattern in tests scores. For students born prior to 1997, average test scores are higher in
the shaded areas. For students born in 1997 or after, average test scores are lower in the shaded
areas.
In sum, the shift in the cutoff date for school eligibility from September 1 to December 31
modified the relative age of students born in the same dates of different years. Thus, the reform
provides a policy experiment in which, holding constant the season of birth, relative age was
9
Agreement 312 published in Diario Oficial de la Federación, April 15, 2002.
Decree published in Diario Oficial de la Federación, June 20, 2006.
11
A potential factor that in principle could have affected the 2009 test score data is the influenza epidemic in
Mexico, which caused the application of the test to be postponed in two states. However, Tlaxcala was not one of
those states.
10
8
exogenously modified across cohorts. We can estimate the impact of relative age on test scores
contrasting pre- and post-reform cohorts across seasons of birth, using a difference-in-differences
approach. Additionally, the lack of anticipation of the reform provides an appropriate setting to
estimate the impact of relative age on test scores using a regression discontinuity approach
around the new cutoff date.
2.1.3
Birth patterns
The policy change took place years after the conception and birth of the cohorts who enrolled
shortly before or shortly after the reform. The reform was in effect in 2003 and there are no
records indicating it was publicly discussed before that. Students whose conception or birth
could have been affected by the reform would be expected to enroll approximately seven years
later, in 2010, and to be in second grade by 2012—consequently they would not be in the 2012
data.
To explore whether there was any response to the reform in terms of the timing of births, we
analyze the number of births by date. Figure 3 shows the distribution of students in the sample by
distance in days to December 31—the new cutoff date. The top panel shows the 2009 data. The
cutoff date when those students were born was September 1. There are two facts worth noting.
First, there is a spike in the number of students born in the days leading up to September 1. The
five birthdates with the highest number of students are August 28 to September 1. Second, there
are no noticeable patterns in other parts of the year.
The bottom panel of Figure 3 shows the 2012 data. For those students the cutoff date for
school eligibility was September 1 when they were born, but it was December 31 when they
enrolled in school. The pattern is virtually the same as in the top panel. The same spike is
observed in the days leading up to September 1. More importantly, there is no noticeable spike
around December 31. There is no evidence of manipulation of births in the vicinity of the new
cutoff date, which is consistent with the reform not being anticipated.
It is interesting to note that the spike in the number of students born in the days leading up to
September 1 indicates that birthdates were manipulated aiming at an earlier enrollment. In other
words, parents’ were trying to enroll children earlier than they were supposed to. This contrasts
with the evidence for Japan presented by Shigeoka (2014). In the Japanese case, redshirting is
not permitted and parents seem to try to increase their children’s relative age in school by
manipulating the timing of births, switching them from below to above the cutoff. In the case of
Tlaxcala, parents seem to deliberately try to decrease their children’s relative age in school by
doing the opposite, manipulating birthdates and switching them from above to below the cutoff.
Besides the precise manipulation of birthdates, another concern is self-selection into
gestational seasons. Parents of different characteristics might aim for their children to be born in
9
different parts of the calendar. Buckles and Hungerman (2013) found that in the US mother
characteristics vary by season of birth of the child. To explore if something similar is observed in
Tlaxcala we use the National Survey of Occupation and Employment, a household survey
collected by Mexico’s National Institute of Statistics and Geography. The survey records exact
birthdates of all household members, among other demographic and economic variables. In five
non-overlapping waves of the survey collected between 2005 and 2013 we identified 9,361
children born between July 3, 1997 and July 2, 2003 residing with their mothers in Tlaxcala.
Figure 4 shows the fraction of children whose mother has some college education (over 12 years
of schooling) and the average age of the mother when the child was born. Date of birth is
expressed as the distance to the closest December 31. The chart also shows fitted quadratic
polynomials with 95% confidence intervals. The fraction of children whose mother has some
college is lower for birthdates early in the calendar year. Therefore, if anything, children likely to
be older relative to their classmates seem to have less educated mothers, which would lead us to
expect them to have lower—not higher—test scores. Maternal age at childbirth shows no
discernible pattern. Figure 4 does not suggest a clear threat to the validity of the empirical
strategies described below.
2.2
Empirical strategies
The reform and the distinctive features of the data allow the separate application of three
different empirical strategies. First, using 2009 and 2012 data we compare relative age and test
scores between cohorts that started school right before and right after the reform with a
difference-in-differences approach across seasons of birth. Second, we use a regression
discontinuity approach around the new unanticipated cutoff date for school eligibility on the
2012 data. Lastly, we instrument relative age with assigned relative age using the 2012 data.
The three strategies estimate different counterfactuals. Consequently, their resulting
estimates might differ without necessarily being inconsistent. The difference-in-differences
estimates shed light on the effect of students “trading places” in the distribution of relative age:
those who would have been the older become the younger and vice versa. The regression
discontinuity estimates inform us of the relative-age effects for students born virtually at the
same time but placed with peers that on average are either significantly younger or significantly
older. Finally, the instrumental variable estimates provide information on relative-age effects
attributable to “small” age differences between students in the same grade.
A comparison of the three sets of estimates is valuable per se. Most studies rely on one
source of identification alone. The use of three different sources of identification on the same
data sheds light on the comparability of estimates with different caveats and subject to different
potential biases.
10
2.2.1
Comparison of pre- and post-reform cohorts
We define the “pre-reform cohort” as the students born in 1995-96 who took ENLACE in 2009,
regardless of grade, and the “post-reform cohort” as all students born in 1998-99 who took
ENLACE in 2012, also regardless of grade. The pre-reform cohort was expected to start school
approximately in 2001 or 2002, whereas the post-reform cohort was expected to start school
approximately in 2004 or 2005. The two cohorts are presumably fully covered by the test score
data (see Table 1). The measure of academic performance for the pre-reform cohort is given by
the 2009 test scores, and for the post-reform cohort it is given by the 2012 test scores. All tests
scores are standardized by grade and year, providing a metric of relative performance
comparable for students attending different grades and born in different years. 12 Students in both
cohorts were roughly the same age by the time of assessment: between 12.42 and 14.42 years.
The reform opened the possibility of enrolling earlier only to children born between
September 1 and December 31. Children born between January 1 and August 31 were not
directly affected by the reform. In order to estimate the causal effect of relative age on test scores
we compute a difference-in-differences Wald estimate. Let t = 0 denote the pre-reform cohort
and t = 1 the post-reform cohort. Let b = 0 denote birthdates between January 1 and August 31,
and b = 1 the birthdates between September 1 and December 31. Lastly, let y be the test score
and r the relative age. The difference-in-differences Wald estimate is:
{E[ y | b  0, t  1]  E[ y | b  0, t  0]}  {E[ y | b  1, t  1]  E[ y | b  1, t  0]}
{E[r | b  0, t  1]  E[r | b  0, t  0]}  {E[r | b  1, t  1]  E[r | b  1, t  0]}
(1)
The numerator is the gain in test scores for students born in January 1 to August 31 relative to
the gain for students born in September 1 to December 31 (i.e., the difference in test-score
differences.) The denominator is the gain in relative age for students born in January 1 to August
31 relative to the gain for those born in September 1 to December 31 (i.e., the difference in
relative-age differences.) The ratio of the differences in differences is our Wald estimate of the
causal effect of relative age on test scores. We compute the estimate and its standard errors by
bootstrap.
A caveat of the use of the shift in the cutoff date as the source of identification is that the
reform changed not only the distribution of relative age but also the distribution of absolute age.
12
This standardization also helps addressing “grade inflation” in the terms of Koretz (2009), Chapter 10. Since
was a high-stakes exam, it is not surprising that average test scores grew in time in a significant manner
(close to half a standard deviation) in 2006-2013.
ENLACE
11
The average age of students in any given grade decreased after the reform.13 Teachers
presumably made adjustments to cope with younger pupils, and therefore the education process
most likely was not held constant. This could affect learning differently for students of different
ages. Our difference-in-differences estimates should be interpreted bearing that in mind.
2.2.2
Discontinuity around the post-reform cutoff
The 2012 data provide an appropriate setting for a regression discontinuity approach because
seven contiguous grades (3 to 9) are tested at the same time. Thus the data cover students with
birthdates only a few days apart who attend different grades at the same point in time. Figure 1
shows clear differences between test scores of students born right before and right after the
December 31 cutoff. It is worth remarking that average test scores are shown by date of birth,
regardless of grade. The discrete jumps observed around December 31 are net of any mechanism
that parents or schools employ to cope with the cutoff date (e.g. redshirting or grade retention.)
We perform both parametric and non-parametric regression discontinuity analyses comparing the
relative age and the test scores of students born around December 31.
For our non-parametric analysis we restrict our sample to students born in neighborhoods of
±30, ±5 and ±1 days around the cutoff. We estimate differences in relative age and test scores
between students born before the cutoff and students born after the cutoff. With those differences
we compute Wald estimates of the impact of relative age on test scores (see Hahn, Todd and van
der Klaauw 2001). Let z = 0 denote birthdates before the cutoff and let z = 1 denote birthdates
after the cutoff. The non-parametric regression-discontinuity Wald estimate is:
E[ y | z  1]  E[ y | z  0]
E[r | z  1]  E[r | z  0]
(2)
The numerator is the difference in test scores between students born after the cutoff and students
born before the cutoff. The denominator is the difference in relative age between students born
after the cutoff and students born before the cutoff. The Wald estimate in (2) and its standard
errors are obtained by bootstrap. Since narrow neighborhoods around the cutoff imply fewer
observations, to preserve the statistical power of our non-parametric analysis we pool together all
students born around December 31, regardless of year of birth.
To obtain separate estimates for every year of birth we adopt a fuzzy regressiondiscontinuity parametric approach that is analog to our non-parametric approach. Based on the
13
This is not specific to the reform in question. Every change in the distribution of relative age is accompanied
by a change in the distribution of absolute age.
12
patterns in Figure 1 we assume a linear relationship between relative age and test scores. We
estimate the impact of relative age on test scores instrumenting relative age with a cubic
polynomial in the date of birth and a discontinuous increase at the cutoff.
A caveat of the regression discontinuity estimates is their local interpretation. The effect of
relative age could be different for students born in other seasons. However, at least as far as the
variables shown in Figure 4, there is no indication of seasonal patterns to the extent found in the
US, suggesting that self-selection into gestational seasons could be less of an issue in our sample.
2.2.3
Post-reform assigned relative age as an instrumental variable
Following Bedard and Dhuey (2006) and others, we also estimate the impact of relative age on
test scores using assigned relative age as an instrumental variable. Assigned relative age is
defined as the number of days between the date of birth of the student and December 31 of her
year of birth, divided by 365.25. Thus, assigned relative age always takes values between zero
and one, whereas actual relative age can be greater than one (when there is redshirting or
retention) or negative (when age-ineligible students enroll.) As in the literature, we assume a
linear relation between test scores and relative age, and estimate the model separately by grade,
for grades 3 to 9 in the 2012 data.
A caveat of this approach is the potential violation of the monotonicity assumption discussed
by Barua and Lang (2009). However, it is valuable to produce estimates comparable to other in
the literature with our data and also compare them to the estimates produced with the other two
strategies.
2.3
Results
Table 2 shows the comparison of the pre- and post-reform cohorts. The top panel shows results
for the full sample. The first set of columns shows the number of observations by cohort divided
into two groups: students born in January 1 to August 31, and students born in September 1 to
December 31.The composition of the cohorts by period of birth is very similar: 32.6% of the
1995-96 cohort was born in September 1 to December 31, compared to 32.1% of the 1998-99
cohort.
The second set of columns shows average relative age and the standard error in parentheses.
Among students born in January 1 to August 31, those in the 1995-96 cohort were on average
0.079 years younger than their classmates, whereas those in the 1998-99 cohort were on average
0.096 years older than their classmates. The change in relative age between cohorts amounts to
an increase of 0.172 years. For students born in September 1 to December 31, those in the 199596 cohort were on average 0.246 years older than their classmates, whereas those in the 1998-99
cohort were on average 0.268 years younger than their classmates. In this case, the change in
13
relative age between cohorts amounts to a decrease of 0.515 years. The difference in differences
is 0.687 years of relative age. In other words, in comparison to the 1995-96 cohort, students born
in January 1 to August 31 in the 1998-99 cohort gained 0.687 of relative age. By symmetry, the
loss for students born in September 1 to December 31 has the same magnitude.
The two sets of columns at the right hand side of Table 2 show average test scores in
standard deviations (σ.) In the pre-reform cohort, students born in January 1 to August 31 have
an average score of -0.027σ in Spanish and -0.023σ in Math. In contrast, in the post-reform
cohort, students born in January 1 to August 31 have an average score of 0.047σ in Spanish and
0.038σ in Math. Thus, for those born in January 1 to August 31 average scores increased 0.074σ
in Spanish and 0.061σ in Math across cohorts. In the pre-reform cohort, students born in
September 1 to December 31 have an average score of 0.064σ in Spanish and 0.062σ in Math. In
contrast, in the post-reform cohort, students born in September 1 to December 31 have an
average score of -0.072σ in Spanish and -0.078σ in Math. Thus, for those born in September 1 to
December 31 average scores decreased 0.136σ in Spanish and 0.140σ in Math across cohorts.
The difference in differences in average test scores is 0.210σ in Spanish and 0.201σ in Math. In
other words, when comparing the 1995-96 and 1998-99 cohorts, average test scores grew a fifth
of a standard deviation among those born in January 1 to August 31 relative to those born in
September 1 to December 31. The middle and bottom panels of Table 1 show separate results for
boys and girls. Although there are gender differences in levels (boys perform better in Math and
girls perform better in Spanish) the changes are roughly similar in magnitude.
Table 3 shows the difference-in-differences Wald estimates of the impact of relative age on
test scores described in equation (1). The estimates and their standard errors were obtained by
bootstrap using 1000 repetitions. The estimate of the impact of one year of relative age is 0.305σ
in Spanish and 0.292σ in Math. The impact is larger in Spanish for boys (0.325σ), and it is larger
in Math for girls (0.315σ.)
Table 4 shows the regression discontinuity non-parametric analysis. The top panel includes
boys and girls together. The first set of columns shows the number of observations born before
and after the cutoff date in neighborhoods of ±30, ±5, and ±1 days around the cutoff date. A
narrower neighborhood provides a finer analysis at the expense of a smaller sample size. The ±1
day neighborhood provides the finest analysis with 324 students born on December 31 (right
before the cutoff) and 290 students born on January 1 (right after the cutoff.)
The second set of columns in Table 4 shows average relative age for those born before the
cutoff and after the cutoff, and the average difference. Those born before the cutoff are relatively
younger, and those born after the cutoff are relatively older. The average difference in relative
age for those born at different sides of the cutoff but only one day apart is 0.641 years. The two
sets of columns at the right hand-side of Table 4 show averages for test scores. Those born
14
before the cutoff have lower average test scores than those born after the cutoff. The difference
for those born at different sides of the cutoff but only one day apart is 0.253σ in Spanish and
0.192σ in Math. The middle and bottom panels of Table 4 show separate estimates for boys and
girls. The sample sizes are reduced by approximately one half and standard errors are larger. The
qualitative results are similar. However, for the narrower neighborhoods the differences are
larger for boys than for girls.
Table 5 presents the regression-discontinuity Wald estimates of the impact of relative age on
test scores. The estimates and their standard errors were obtained by bootstrap with 1000
repetitions. The estimates of the impact of one year of relative age are for the neighborhoods of
±30, ±5, and ±1 days are 0348σ, 0.339σ, and 0.395σ in Spanish and 0.365σ, 0.347σ, and 0.305σ
in Math, respectively. The impact estimates are similar for boys and girls.
Table 6 shows parametric estimates of the discontinuities in relative age and tests scores
around December 31 of the years 1997 to 2002. Each coefficient was estimated in a separate
regression including students born within a ±1 year neighborhood of December 31 of the year
shown. The estimates for relative age show the results of regressing relative age on a cubic
polynomial in the date of birth together with a dummy variable for the discontinuity at the
December 31 cutoff. The estimates range between 0.387 and 0.837 years of relative age,
depending on gender and age (i.e., the year of the cutoff analyzed.)
Table 6 presents two different estimates for tests scores. The “sharp” estimates are the result
of regressing test scores on a cubic polynomial in the date of birth and a discontinuity at the
December 31 cutoff. They are interpreted as the difference in the test score averages at the
discontinuity. The “fuzzy” estimates are interpreted as the causal effect of relative age on test
scores at the discontinuity. They were computed instrumenting relative age with a cubic
polynomial in date of birth, and a discontinuity at the cutoff. Sharp estimates range between
0.101 and 0.305σ in Spanish, and between -0.013 and 0.34σ in Math. Fuzzy estimates range
between 0.222 and 0.478σ in Spanish, and between 0.067 and 0.555σ. Only one fuzzy estimate is
not statistically significant (for girls around December 31, 1997). There is no clear trend in the
estimates across years, suggesting relative-age effects do not dilute in the age range analyzed
(from 9 to 15 years.)
Table 7 shows the instrumental variable estimates of the impact of relative age on test
scores, by grade and gender. Each coefficient was estimated in a separate regression including
only students in the grade shown. The estimates range between 0.160 and 0.377σ in Spanish, and
between 0.094 and 0.390σ in Math, depending on the grade. Although the estimates remain
significant for 9th grade, they are smaller. This could suggest some dilution with age. However,
the number of students in 9th grade (16,133) is much smaller than the number of students in 8th
grade (20,683). An important fraction of 9th-graders might have dropped out of school before
15
taking the 2012 test. Dropouts make the estimates across grades not entirely comparable because
relative age could be a factor in the decision to abandon school.
In order to compare the results of the three different empirical strategies we focus on
students born around the 1998 discontinuity and those who were in 7th or 8th grade in 2012. Table
8 presents a side-by-side comparison. The largest discrepancy is found for girls in math: the
regression discontinuity estimate is 0.497 and the instrumental variable estimate for 8th grade is
0.185. Besides those two estimates, the rest are reasonably similar, ranging between 0.2 and
0.4σ. These results are generally consistent with what has been found in previous studies. More
importantly, this unique comparison shows that different sources of identification point at
relative-age effects estimates of similar magnitudes. Weather we consider variations in relative
age produced by trading places in the distribution of age holding season of birth constant, by
being born shortly before instead of shortly after the cutoff, or by being born in different dates
but attending the same grade, we obtain similar estimates for the advantage in test scores
conferred by relative age.
3
Relative-age effects in adulthood
The existence of relative-age effects in test scores is well-documented (see Panel I of Table A.)
However, the relevance of those estimates would be hard to justify if we did not observe relativeage effects in adulthood outcomes as well. In this section we estimate relative-age effects in
labor and marriage market outcomes using a sample of Mexican adults. To the best of our
knowledge, this is the first study of relative-age effects in adulthood outcomes outside of highincome countries.
3.1
Institutional background
Mexico is a middle-income country with a GDP per capita (at purchasing power parity) of
roughly half of Korea’s and a third of the US’. It has a comprehensive educational system,
without tracking or streaming. Like virtually any other country, for many years Mexico has had
cutoff dates for school eligibility. Unfortunately, there is not much information on those cutoff
dates prior to the 1990s. It is common knowledge that September 1 was the cutoff date, but it is
unclear since when or to what extent it was enforced—or even known. We do not know how
often the rules were bent to enroll ineligible students. For the purpose of this study we take
September 1 as the cutoff date for school eligibility, but we should entertain some rule-bending
as probable.
An issue that arises in the study of birthdates among Mexican adults is the potential
difference between actual and official birthdates—the latter is the one recorded in birth
certificates. It is not unusual to meet Mexican adults who claim having been born on a different
16
date to the one recorded in their birth certificate—my own mother is an example. In the past,
many people were born in private homes and the birthdate officially recorded depended entirely
on what parents reported to the authorities, which could have been inaccurate. In some cases
civil registry officials recorded the date of registration as the date of birth. Due to this potential
issue, relative age could be proxied with error: the birthdate used for enrollment decisions (from
the birth certificate) could be different from the observed birthdate (as recorded in the survey.)
3.2
Survey data
Our analysis is based on the National Survey on Occupation and Employment (ENOE) collected
by Mexico’s National Institute for Statistics and Geography. ENOE is a nationally representative
household survey with a quarterly-rotating panel structure. A distinctive feature of ENOE is that it
records the birthdates of all the members of the surveyed households as stated by the selected
respondent.
The sample of analysis consists of eight non-overlapping waves: 2005-I, 2006-II, 2007-III,
2008-IV, 2010-I, 2011-II, 2012-III, and 2013-IV. The sample has a total of 3,280,136
observations. Of those observations, 3,083,698 have the birthdate fully specified.14 The sample
of analysis is restricted to the 828,860 individuals born between March 3, 1960 and March 2,
1980. The birthdate bounds were chosen to provide a symmetric sample around September 1.
Everyone in the sample was approximately 24 to 54 years old by the time of the survey.
Six adult outcomes are analyzed, and the number of valid observations in the sample varies
by outcome. The first outcome is whether the person has some college education. It was defined
as a dummy indicating if the person attained any education at a four-year college level or
beyond. The second outcome is employment status defined as a dummy that indicates being
occupied versus not occupied. The third outcome is earnings, in logarithm. The fourth outcome
is a dummy indicating whether the person has employer-provided medical insurance. Since
employer-provided medical insurance is mandatory, it is proxy for working in the formal sector.
The fifth outcome is a dummy variable indicating whether the spouse (or the cohabitating
significant other) attained some college education. The variable was constructed for individuals
who live with their spouse or significant other in the same household. The sixth outcome is the
number of children and it is only recorded for women.
Table 9 shows the distribution of the sample by year of birth, together with the average
values for the six outcomes analyzed. The fraction of adults with some college ranges between
16 and 23%. The percent occupied is rather stable and slightly over 70%. The logarithm of
earnings is higher for older cohorts, which is consistent with the well-known experience wage
14
Of the 196,438 without a fully specified birthdate, 32,753 only specify year and month, 97,149 only specify
year and 66,536 have no information.
17
premium. The percent with employer-provided medical insurance ranges between 59 and 64%.
The percent whose spouse has some college is stable around 17%. Finally, the average number
of children for females ranges between 3.34 and 1.57, steadily declining from older to younger
cohorts.
Figure 5 shows the composition of the sample by day of birth relative to September 1,
expressed as the distance in days to the closest September 1, in 73 five-day bins. There is no
apparent bunching in the number around September 1. Thus, at least in terms of self-reported
birthdates, there is no pattern in the density of the sample around the cutoff date that could
invalidate a regression discontinuity design.
Figure 6 shows averages for the outcomes of interest by date of birth, expressed as the
distance in days to the closest September 1, in 73 five-day bins. The percentage of respondents
with some college shows different patterns at each side of the cutoff. The same can be said for
the percent occupied, the percent whose spouse has some college, and the number of children.
For the logarithm of earnings and the percent with employer-provided medical insurance no
pattern is obvious. The patterns in Figure 2 are not controlled for gender and time trends. The
econometric analysis described in the next section lays out two models to properly isolate
relative-age effects.
3.3
Empirical strategies
Since we do not observe time starting-school for the adults in the sample, we proxy their relative
age in school with the distance between the date of birth and September 1. We use two
approaches for the estimation of relative-age effects in adult outcomes. First, we use a regression
discontinuity design around September 1. The equation to estimate is:
yi  [ s (i )   w(i )  t 1 k bik ]   0  1 xi   2 xi2   0ci   1ci xi   2ci xi2   i
4
(3)
where yi is the outcome analyzed, δs(i) and φw(i) are state and survey-wave fixed effects,
respectively, bi is birthdate in days, xi is a variable denoting the shortest distance in days from the
birthday of person i to September 1 (it can be positive or negative), divided by 365, and ci is a
dummy variable indicating whether the birthday falls in September 1 to March 2. The third term
at the right-hand side of (3) is a fourth-degree polynomial that works a control for a smooth trend
across cohorts. The terms in brackets are controls, and the remaining terms at provide the
regression discontinuity design. The parameter of interest is γ0 and it is interpreted as the
discontinuous effect of the September 1 cutoff for school eligibility on outcome yi. The model
(3) is also estimated restricting the data to a window of ±0.25 years around the cutoff date, and
using a cubic (instead of quadratic) polynomial in the running variable xi.
18
In our second approach we use a month-of-birth fixed effects model. This second model
provides more flexibility, recognizing at the same time that the discontinuity might not be
sharp—some people were probably held back while others were likely enrolled in spite of being
age-ineligible. The fixed-effects specification we estimate is:
yi  [ s (i )   w(i )  t 1 k bik ]   0  t 1t dt (i )   i
4
11
(4)
The terms in brackets are the same controls as in model (1). dt(i) is a dummy indicating whether
individual i was born in month t, and ηt is a fixed effect for the month of birth t. The omitted
month is September, and t=1 indicates October and t=11 indicates August. The coefficients ηt are
interpreted as differences relative to September. The model in (4) allows us comparing outcome
differences around September 1 with differences around other dates in the year. We estimate
model (4) separately for different five-year age-at-survey groups.
3.4
Results
Table 10 shows the regression discontinuity estimates, with and without covariates (survey-wave
and state-of-birth fixed effects, and a smooth trend across cohorts.) Each coefficient is the result
of a separate regression. The standard error and the number of observations are presented below
each estimate. The discontinuity estimates are significant for four outcomes: educational
attainment, earnings, the marriage market and fertility. At the discontinuity, the fraction of adults
with some college increases 1.44 percentage points (the average is 18.3%), earnings are 2.4%
higher, the fraction of adults who have a spouse with some college increases 1.1 percentage
points (the average is 17.1%), and the average number of children decreases in 0.04 (the average
is 2.51). The middle and bottom panels show separate results for males and females. The main
differences are in the fraction occupied and the fraction with employer-provided medical
insurance. For females, the discontinuity implies an increase of one percentage point in the
fraction occupied. For males the estimate is not significant. In terms of employer-provided
medical insurance, for males the fraction increases in 0.9 percentage points but is only
marginally significant, and for females it is not significant.
When higher-order polynomials are used, the significance decreases. The second row within
each panel shows the results using a cubic polynomial in the running variable. The estimates
remain significant only for the fraction with some college, and when split by gender, the
significance only remains for females.
The third row within each panel shows a quadratic specification with a shortened window of
±0.25 years around September 1. The overall estimates remain significant for the fraction with
some college and for earnings. However, when split by gender, the results for males are not
19
significant. For females, the results are significant for the fraction with some college, earnings,
and percent with employer-provided medical insurance.
The loss in magnitude and significance using a higher order polynomial or a smaller window
around the cutoff date is a result of the data not showing a sharp change on September 1. That is
consistent with an environment where some people were bending the eligibility rule, or where
the date reported in the survey and the date used for school eligibility might be different.
Table 11 shows the estimates of the fixed-effects model. Each column within a panel is a
separate regression. The standard error is reported below each estimate. The coefficients for each
month are reported relative to September (the omitted category.) Estimates with and without
covariates (dummies for state of birth and survey wave) are presented for each of the outcomes.
Figure 7 provides a graphic summary of the results for the specifications with covariates. The
solid markers indicate significance at 95% confidence.
There are some noteworthy results in Figure 7. First, for the first five outcomes the only
significant estimates are negative—there are no positive and significant estimates. In the case of
the number of children, the only significant estimates are positive. In other words, relative to
people born in any other month, those born in September on average are more likely to have
attained some college education, have higher earnings, are more likely to be occupied, are more
likely to have employer-provided medical insurance, have more educated spouses, and have
fewer children. Second, there is a downward trend from October to August in the first five
outcomes, and an upward trend for number of children, although with varying degrees. The
clearest case is for the percent with some college. Third, the largest difference in absolute value
between estimates for adjacent months is observed between August and September—with the
exception the percent occupied among males, and the percent with employer-provided medical
insurance among females or overall. In other words, the greatest variation across adjacent
months is observed around September 1.
An issue treated in the literature when studying earnings is substitution along the lifecycle
(see Black et al. 2011, and Frederickson et al. 2013). People who attain more education also
postpone their earnings and forgo an experience premium. Thus, comparisons that do not take
into account timing might be misleading. A similar argument can be made about fertility.
Females attaining more education might postpone childbearing. To explore if the estimates in
Table 11 are the result of timing, several fixed-effects models are estimated separately for five
categories of age-at-survey. Since the sample includes different waves of the survey between
2005 and 2013, age at the moment of the survey and year of birth are not collinear—people of
the same cohort are observed at different ages.
Table 12 shows the estimates of the difference between August and September for five-year
categories of age-at-survey: 25-29, 30-34, 35-39, 40-44 and 45-53. The model is the same as in
20
Table 11, but only the coefficient on the dummy for the month of August is shown. Each
coefficient is estimated in a separate regression with dummies for state of birth and survey wave.
Below each estimate are the standard error and the number of observations in the regression.
There is variation across age groups. The estimates for the percent with college are all negative
and in the range from -2.2 to -0.4%, but not all are significant. For males, the significant
estimates are observed at ages 30-34 and 35-39, whereas for females they are observed at ages
35-39, 40-44, and 45-53. In the case of the percent occupied, some point estimates are positive
and others are negative, and the only significant estimate is for ages 40-44 and it is positive. For
females they point estimates are all negative and two are significant: for ages 40-44 and 45-53.
In terms of the logarithm of earnings, all but one estimate (for males 35-39) are negative. All
significant estimates are negative: ages 30-34 and 45-53 for males, and 35-39, 40-44 for females.
In the case of the percent with employer-provided medical insurance, the only significant
estimates are negative and observed for males at ages 35-39 and 40-44. In case of the percent
with spouse with some college, all point estimates are negative, but only the estimates for
females ages 30-34 and 35-39 are significant. Finally, the point estimates for number of children
(females only) are all positive, and they are significant for ages 35-39 and 40-44.
The main finding from the analysis across age groups is that the differences in adult
outcomes observed around September 1 are not limited to young adults. For all six outcomes we
observe significant and sizeable differences among adults age 35 or older. In other words,
relative-age effects in adult outcomes do not seem to be just an artifact of timing. However, there
is a great deal of variation across estimates which, in principle, could be due to relatively small
sample sizes.15 That is what the estimates pooling males and females suggest. They have greater
sample sizes and provide more similar estimates across age groups.
In sum, the empirical analysis indicates that the six outcomes studied are not independent
from date of birth. People born in months that presumably made them older relative to their
classmates on average attain more college education, have higher earnings, and have more
educated spouses. Relatively older males are more likely to have employer-provided medical
insurance. Relatively older women are more likely to be occupied and on average have fewer
children. Although the results of the regression discontinuity analysis are not robust to cubic or
higher-order polynomials or smaller windows of analysis, the results from the month-fixed
effects model indicate there is an inflection point between August and September. People look
“the most different” across those two months. No other month is above September in terms of
educational attainment, earnings, or spousal educational attainment. No other month is below
15
For every 10,000 people in the sample, approximately 849 are born in August and 821 in September. Those
would be the observations providing the identification of the August-September differences.
21
September in terms of fertility. Additionally, the results do not seem to be driven by timing—
relative-age effects are observed well pass age 35.
4
Theoretical model of wealth and persistence of relative-age effects
The previous sections show significant relative-age effects in childhood and adulthood. The
results for childhood are in line with prior studies. The results for adulthood add to a handful of
studies with differing findings. Of the group of countries analyzed so far, Mexico has the lowest
income per capita—roughly between one third and one half of the other countries’ GDP per
capita. A natural question is whether ex ante we would expect relative-age effects in adulthood to
be larger or smaller in Mexico, even if all countries had the same relative-age effects in academic
performance in childhood.
It is easy to imagine how wealth could attenuate the persistence of relative-age effects from
childhood into adulthood. Human capital investment in a poorer country might be limited to the
individuals showing the best academic promise, whereas a richer country could afford a more
egalitarian investment. It is equally easy to imagine wealth magnifying persistence. More
resources might widen the investment gap between individuals with different levels of ability,
whereas in the extreme situation with nothing to be invested, there would not be a gap.
The model below formalizes the idea that, under assumptions commonly used in human
capital theory, the relationship between wealth and persistence of relative-age effects from
childhood into adulthood cannot be signed. In other words, the model provides an example of
how “anything goes.”
Let us start by assuming a household where altruistic parents decide how much to invest in
the human capital of two children. The household can be interpreted as an economy where a
social planner allocates human capital investments across individuals. The only difference
between the two siblings is their age relative to their classmates. Sibling 1 is relatively older,
whereas sibling 2 is relatively younger. Because of a greater maturity, sibling 1 performs
significantly better in school than sibling 2. As a consequence, sibling 1 is perceived as having
greater ability than 2—even though they have identical ability. Based on children’s perceived
abilities, parents maximize:
u(c0 )  v(c1 )  v(c2 )
(5)
subject to the following two constraints:
w  c0  y1  y2
22
ci  r ( y i ; a i )
where u(c0) is the utility of parental consumption c0. v(ci) is the utility of consumption of child i.
The parameter δ is a measure of altruism of parents towards their children. yi is the investment in
the human capital of child i, and w is parental wealth. r(yi;ai) stands for the lifetime earnings of
child i when investment in human capital is yi and perceived ability is ai. Utility functions u and
v are assumed increasing and concave. Lifetime earnings are also assumed increasing and
concave in investment, i.e. r′(y;a) > 0, and r″(y;a) ≤ 0. Given the same investment, higher-ability
individuals are assumed to have greater lifetime earnings and a higher marginal return, i.e. if
aj > ak then r(y;aj) > r(y;ak) and r′(y;aj) > r′(y;ak) for all y.
It should be emphasized that the decision-maker does not observe true ability—the siblings
in the model have the same. The decision is based solely on the signal given by academic
performance. Parents or society make investments decision believing that a1 and a2 are their
children’s abilities. However, the actual ability for both children is a. Thus, child i’s actual
earnings are r(yi;a).
The model can be loosely interpreted as a societal choice problem. Under that interpretation,
streaming or tracking could be one of the ways in which a less egalitarian investment could
materialize in an economy. Merit-based scholarships would be another. In those cases more
investment resources would go to individuals perceived by society as having greater ability. On
the opposite end, free tuition and affirmative action policies could be ways in which a more
egalitarian investment could occur. Differences in wealth could cause societal choices to differ,
and those different choices would be reflected in different educational systems and different
admission and financial aid policies.
In order to solve for optimal investment in the model, the first order conditions require
equalizing the marginal utility produced by the investment in each child to the marginal utility of
parental wealth, represented by the Lagrange multiplier λ:
v(c1 )r( y1; a1 )  v(c2 )r( y2 ; a2 )  
(6)
Expression (6) makes explicit the trade-off between efficiency and equality in the investment
decision. Efficiency implies investing in a way that equalizes the marginal returns on human
capital—when they are equal there is nothing to be gained in terms of earnings by reallocating
investment. Equality implies allocating the investment so that no gains in the sum of children’s
utility can result from reallocating resources—they are equally happy at the margin. The
efficiency-equality trade-off is not constant across different levels of wealth. However,
23
expression (6) does not provide an indication of whether the gap in optimal investments across
siblings widens or narrows with greater parental wealth. It is unclear whether the difference y1-y2
grows or shrinks for smaller values of λ. The relationship can only be signed by making further
assumptions on functional forms and parameter values.
In order to formally establish that the relationship between wealth and persistence can go
either way, we can assume specific functional forms and parameters, solve equation (6) for
different values of λ (i.e. different levels of wealth), and then measure the gap in optimal
investments y1-y2 and the ratio of earnings r(y1;a)/r(y2;a). The magnitudes of the gap in
investments and the ratio of earnings are interpreted as the extent to which relative-age effects
persist into adulthood.
Let us assume that children’s utility function has the following form:
v(ci )  ci
(7)
and that lifetime earnings is defined as:
r ( yi ; ai )  ai yi  1 
exp( ai yi )
ai
(8)
with 0 < γ < 1, ai ≥ 1 and yi ≥ 0. Verifying that both equations are increasing and concave is
straightforward. Given those functional forms the marginal utility of investing in the human
capital of child i is:


1
v(r ( yi ; ai ))r( yi ; ai )   ai yi  1   exp( ai yi )
ai


 1
a  exp(a y )

i
i
i
(9)
Assume the actual ability of both children is a = 1.25. However, the perceived ability of
sibling 1 is a1 = 1.5, and the perceived ability of sibling 2 is a2 = 1.0. Assume also the parameter
values μ = 3.2 and γ = 0.948. Based on those assumptions, it is possible to numerically find the
investments that solve (9) for different levels of marginal utility of parental wealth λ. Those
solutions are depicted in Figure 8.
Figure 8 shows the gap in human capital investments y1-y2 that parents would choose for
different levels of parental wealth. It also shows the ratio of earnings that would result from
those investments, defined as r(y1;a)/r(y2;a)—notice that the ratio is computed using actual
ability a for both siblings. In the horizontal axis is the marginal utility of parental wealth, λ. The
order of the axis is reversed to be interpreted as a measure of parental wealth—greater parental
wealth is equivalent to a lower λ.
24
Figure 8 shows a non-monotone relationship between the gap in investments and parental
wealth. There are ranges where the gap in investment decreases with parental wealth, and there
are also ranges where the opposite holds. The same can be said for the earnings ratio—given that
siblings have the same ability it is only a reflection of the gap in investments. There are three
values of λ (1.53, 1.65 and 2.34) where the investment gap is zero. For those levels of wealth the
perceived difference in ability results in identical investments. Thus, relative-age effects in
adulthood do not exist at those three levels. Moreover, there are two ranges of λ where the
parents invest more in the sibling with lower perceived ability (when the marginal utility is
below 1.53 or between 1.65 and 2.34). In those cases the relative-age effects are reversed in
adulthood: the relatively older sibling has lower educational attainment and lower earnings than
the relatively younger sibling.
The patterns shown in Figure 8 in no way constitute a general result. They are just an
illustrative example. The functional forms and the parameters used were picked precisely to
exemplify that in a simple model of human capital investment “anything goes”: wealth could
magnify, attenuate, or even reverse relative-age effects.
Although highly stylized, the model shows that from a theoretical perspective we do not
know whether we should expect relative-age effects in adult outcomes to be greater in wealthy
countries or in poor countries—even when they have similar relative-age effects in childhood.
Thus, the evidence on relative-age effects in adulthood from high-income countries is not
necessarily informative of what happens in lower-income countries.
5
Summary of findings
The results of the policy experiment that shifted four months the cutoff date for school eligibility
indicate that the way formal education is structured creates academic “winners” and “losers.”
Three different sources of identification (difference-in-differences comparing pre- and postreform cohorts, a regression discontinuity design around the new cutoff, and using “assigned”
relative age as an instrument for relative age) provide similar estimates of the impact of relative
age on academic performance. One year of relative age confers and advantage in test scores that
ranges between 0.2 and 0.4 standard deviations. Such advantage does not vanish by grade 9 or
age 15. In a human capital investment context, those gaps in academic performance could be
costly for society on efficiency and equity grounds: investment in high-ability individuals might
be discouraged solely because they were born in the “wrong” part of the calendar.
This study also finds relative-age effects in labor and marriage market outcomes. People
who, based on their birthdate, were presumably older relative to their school classmates on
average attained more college education, earn more, and have more educated spouses. Relatively
older males are more likely to have employer-provided medical insurance, and relatively older
25
women are more likely to be occupied and have fewer children. The evidence for adults is
consistent with the gaps observed in childhood having lasting effects on outcomes related to
welfare.
The fact that some studies for other countries have found little or no relative-age effects in
adulthood is not necessarily in conflict with the evidence presented here. The theoretical model
shows that such differences across countries could be the result of differences in wealth—even if
all countries have the same relative-age effects in childhood. Prior studies on adulthood
outcomes are limited to high-income countries. Further evidence from middle- and low-income
countries would help clarifying the role of wealth in the persistence of relative-age effects into
adulthood.
Overall, the results of this study have clear policy implications. Standardized test scores
carry a lot of weight as measures of children’s potential in the opinion of parents, teachers,
students, and the general public. Their relevance in the public’s view was epitomized by the
November 2012 issue of the magazine Wired, which showed on its cover the top scorer in
ENLACE and called her “the next Steve Jobs.” Scores from standardized tests provide parents,
teachers, students, and authorities an accessible metric to draw inferences about ability. Such test
scores could be adjusted to better reflect ability and improve the allocation of human capital
investment. Crawford, Dearden and Greaves (2014) have suggested a policy response in the UK
“to adjust nationally set and administered tests appropriately by age and to provide feedback on
the basis of these adjusted scores” (p. 30).
In the specific case of Mexico, some standardized tests have direct consequences on the
educational outcomes and career paths of students. For instance, enrollment in public high
schools in the metropolitan area of Mexico City is determined in a competitive process based on
the scores obtained in standardized tests. Every year hundreds of thousands of 9th-graders take
one of the two tests given by Metropolitan Commission of Public Secondary Education
Institutions. As part of the process, students state their preferences over public high schools,
ranking up to 20 options. Students are allocated to the school of their highest preference,
provided there are slots available. Test scores define the order in which students are allocated
until all the spots are filled. In this context, relatively younger students have a handicap. Some of
them are missing potentially life-changing opportunities due to their relative-age. The most
coveted schools are the ones that automatically grant a spot in Mexico’s National Autonomous
University (UNAM) upon graduation with a mediocre GPA. UNAM is arguably the most
prestigious university in the country, and it is also tuition-free. A small disadvantage in test
scores could be the difference between having access to it or not.
Adjusting—or at least better communicating—test scores used as signals of ability in order
to avoid biases against relatively younger students is a simple policy that could enhance both
26
equity and efficiency. With appropriate adjustments equally able individuals would not be
treated differently, and truly abler individuals would be easier to identify.
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29
TABLE 1—Number of students by grade and year of birth in the two tests
Birth year
3
4
5
Grade
6
7
8
9
Total
ENLACE 2009
1989
1990
1991
1992
1993
1994
1995
1996
1997
1998
1999
2000
2001
N.A.
Total
2
24
79
361
1,986
19,861
11
582
22,906
6
29
107
441
2,311
19,949
18
484
23,345
1
5
24
155
727
3,144
19,148
27
4
22
168
829
6,333
18,084
23
506
23,737
509
25,972
1
25
133
758
7,321
14,346
24
978
23,586
1
2
22
138
673
7,009
13,189
32
2
14
120
802
6,504
12,289
21
910
21,976
912
20,664
3
16
143
970
7,337
20,254
21,546
21,569
21,772
21,843
21,962
19,879
11
4,881
162,186
ENLACE 2012
1992
1993
1994
1995
1996
1997
1998
1999
2000
2001
2002
2003
2004
N.A.
Total
4
45
241
1,830
21,149
3
386
23,658
2
14
57
397
2,027
20,684
3
14
62
354
3,460
20,880
11
441
23,625
346
25,127
2
9
67
387
2,235
18,986
15
288
21,989
1
16
87
417
2,333
19,270
9
9
96
571
2,966
17,689
28
421
22,554
464
21,823
3
13
76
575
5,424
16,112
21
295
22,519
3
13
86
689
6,091
19,578
20,506
21,948
22,897
23,163
22,525
21,152
3
2,641
161,295
N.A.: the birthdate was not available, was prior to 1980 or implied enrolling in school at age four or younger.
30
TABLE 2—Difference-in-differences analysis of the impact of the reform on relative age and test
scores
Date of birth
Observations
Year of birth
1995-96 1998-99
All
Jan. 1-Aug. 31
29,039 28,826
Sep. 1-Dec. 31
14,076 13,628
Relative age: mean (s.e.)
Year of birth
First
1995-96 1998-99 diff.
Sep. 1-Dec. 31
14,461 14,477
7,055
6,862
0.093 0.172
(0.003) (0.004)
-0.268 -0.515
(0.004) (0.006)
0.687
(0.007)
-0.027 0.047 0.074
(0.006) (0.006) (0.008)
0.064 -0.072 -0.136
(0.008) (0.009) (0.012)
0.210
(0.015)
-0.023 0.038
(0.006) (0.006)
0.062 -0.078
(0.008) (0.009)
0.061
(0.008)
-0.140
(0.012)
0.201
(0.015)
-0.034
(0.004)
0.279
(0.006)
0.124 0.158
(0.004) (0.006)
-0.233 -0.512
(0.007) (0.009)
0.670
(0.011)
-0.243
(0.008)
-0.131
(0.012)
-0.143 0.100
(0.008) (0.012)
-0.249 -0.118
(0.012) (0.017)
0.219
(0.020)
-0.057 0.016
(0.008) (0.008)
0.002 -0.105
(0.012) (0.012)
0.073
(0.012)
-0.107
(0.017)
0.180
(0.021)
-0.123
(0.004)
0.214
(0.005)
0.063 0.186
(0.004) (0.005)
-0.304 -0.517
(0.005) (0.008)
0.703
(0.009)
0.188 0.238 0.050
(0.008) (0.008) (0.011)
0.260 0.107 -0.153
(0.012) (0.012) (0.017)
0.203
(0.020)
0.012 0.060
(0.008) (0.008)
0.124 -0.049
(0.012) (0.012)
0.049
(0.012)
-0.173
(0.017)
0.222
(0.020)
Second diff.
Girls
Jan. 1-Aug. 31
Sep. 1-Dec. 31
14,578 14,348
7,021
6,766
Second diff.
Math: mean (s.e.)
Year of birth
First
1995-96 1998-99 diff.
-0.079
(0.003)
0.246
(0.004)
Second diff.
Boys
Jan. 1-Aug. 31
Spanish: mean (s.e.)
Year of birth
First
1995-96 1998-99 diff.
Notes: Based on ENLACE 2009 (1995-96 cohort) and ENLACE 2012 (1998-99 cohort) in Tlaxcala. Standard errors in parentheses. Test
scores were standardized at the state-level by grade and year.
TABLE 3—Difference-in-differences Wald estimates of the impact of relative age on test scores
All
Boys
Girls
Spanish
0.305
(0.022)
0.325
(0.032)
0.289
(0.030)
Math
0.292
(0.022)
0.268
(0.032)
0.315
(0.030)
Estimates and standard errors obtained by bootstrap
with 1000 repetitions.
31
TABLE4—Regression discontinuity non-parametric analysis of the impact of relative age on test
scores
Observations
±30 days ±5 days ±1 day
All
Before cutoff
10,507
1,716
324
After cutoff
10,567
1,806
290
Boys
Before cutoff
5,323
856
155
After cutoff
5,241
894
147
Girls
Before cutoff
5,184
860
169
After cutoff
5,326
912
143
Difference
Difference
Difference
Relative age: mean (s.e.)
±30 days ±5 days ±1 day
Spanish: mean (s.e.)
±30 days ±5 days ±1 day
Math: mean (s.e.)
±30 days ±5 days ±1 day
-0.245
(0.005)
0.338
(0.003)
0.583
(0.006)
-0.267
(0.013)
0.373
(0.007)
0.640
(0.015)
-0.273
(0.028)
0.368
(0.018)
0.641
(0.034)
-0.077
(0.010)
0.126
(0.010)
0.203
(0.014)
-0.095
(0.024)
0.121
(0.024)
0.217
(0.033)
-0.115
(0.056)
0.137
(0.058)
0.253
(0.080)
-0.086
(0.010)
0.127
(0.010)
0.213
(0.014)
-0.089 -0.036
(0.024) (0.055)
0.134
0.155
(0.024) (0.061)
0.223
0.192
(0.034) (0.082)
-0.220
(0.008)
0.350
(0.004)
0.57
(0.009)
-0.270
(0.018)
0.384
(0.010)
0.654
(0.021)
-0.290
(0.038)
0.367
(0.020)
0.657
(0.044)
-0.223
(0.013)
-0.024
(0.014)
0.199
(0.019)
-0.230
(0.033)
-0.011
(0.034)
0.219
(0.047)
-0.323
(0.076)
0.055
(0.084)
0.378
(0.113)
-0.135
(0.014)
0.079
(0.014)
0.214
(0.020)
-0.138 -0.080
(0.034) (0.082)
0.110
0.160
(0.034) (0.092)
0.248
0.241
(0.048) (0.123)
-0.271
(0.007)
0.326
(0.004)
0.597
(0.008)
-0.265
(0.018)
0.362
(0.010)
0.627
(0.021)
-0.257
(0.040)
0.369
(0.031)
0.626
(0.052)
0.074
(0.013)
0.274
(0.013)
0.200
(0.019)
0.038
(0.033)
0.250
(0.032)
0.212
(0.046)
0.075
(0.078)
0.222
(0.079)
0.147
(0.112)
-0.034
(0.014)
0.175
(0.013)
0.209
(0.019)
-0.040
0.004
(0.034) (0.074)
0.157
0.150
(0.032) (0.081)
0.198
0.146
(0.047) (0.110)
Notes: Based on ENLACE 2012 in Tlaxcala, students born between 1997 and 2003. Standard errors in parentheses. Test scores were standardized at the state-level by grade
and year.
TABLE 5—Regression-discontinuity non-parametric Wald estimates of the impact of relative age
on test scores
All
Boys
Girls
±30 days
0.348
(0.023)
0.349
(0.024)
0.348
(0.024)
Spanish
±5 days
0.339
(0.053)
0.338
(0.053)
0.341
(0.055)
±1 day
0.395
(0.131)
0.397
(0.132)
0.395
(0.129)
±30 days
0.365
(0.024)
0.365
(0.024)
0.365
(0.024)
Estimates and standard errors obtained by bootstrap with 1000 repetitions.
32
Math
±5 days
0.347
(0.055)
0.348
(0.055)
0.352
(0.056)
±1 day
0.305
(0.129)
0.301
(0.134)
0.300
(0.134)
TABLE 6—Regression-discontinuity parametric estimates of the impact of relative age on test
scores
Discontinuity on
Observations
Dec. 31 of:
All
1997
19,979
1998
21,109
1999
22,691
2000
22,880
2001
22,927
2002
22,095
1997
10,015
1998
10,621
1999
11,405
2000
11,407
2001
11,469
2002
11,223
1997
9,964
1998
10,487
1999
11,286
2000
11,473
2001
11,457
2002
10,871
Relative age
Spanish
Sharp
Fuzzy
Math
Sharp
Fuzzy
0.411
(0.015)
0.719
(0.016)
0.704
(0.014)
0.500
(0.015)
0.835
(0.011)
0.598
(0.006)
0.139
(0.038)
0.267
(0.037)
0.227
(0.035)
0.195
(0.035)
0.225
(0.036)
0.246
(0.036)
0.400
(0.066)
0.353
(0.035)
0.287
(0.032)
0.343
(0.040)
0.309
(0.028)
0.440
(0.044)
0.099
(0.039)
0.284
(0.037)
0.232
(0.035)
0.192
(0.035)
0.270
(0.035)
0.312
(0.036)
0.247
(0.065)
0.359
(0.035)
0.316
(0.032)
0.330
(0.040)
0.352
(0.028)
0.526
(0.044)
0.387
(0.023)
0.715
(0.024)
0.665
(0.021)
0.510
(0.022)
0.834
(0.016)
0.577
(0.009)
0.175
(0.053)
0.223
(0.052)
0.207
(0.049)
0.226
(0.051)
0.160
(0.051)
0.247
(0.050)
0.478
(0.099)
0.376
(0.049)
0.352
(0.047)
0.423
(0.059)
0.265
(0.040)
0.462
(0.063)
0.208
(0.054)
0.240
(0.053)
0.197
(0.050)
0.182
(0.051)
0.192
(0.051)
0.324
(0.050)
0.454
(0.102)
0.223
(0.050)
0.336
(0.048)
0.351
(0.059)
0.316
(0.041)
0.555
(0.064)
0.437
(0.018)
0.724
(0.020)
0.745
(0.017)
0.488
(0.019)
0.837
(0.014)
0.623
(0.008)
0.101
(0.054)
0.305
(0.052)
0.234
(0.049)
0.169
(0.048)
0.275
(0.049)
0.230
(0.051)
0.301
(0.084)
0.326
(0.047)
0.222
(0.042)
0.268
(0.053)
0.356
(0.037)
0.407
(0.060)
-0.013
(0.055)
0.326
(0.052)
0.261
(0.049)
0.203
(0.049)
0.340
(0.049)
0.292
(0.051)
0.067
(0.085)
0.497
(0.048)
0.295
(0.042)
0.309
(0.053)
0.387
(0.037)
0.486
(0.060)
Boys
Girls
Standard errors in parentheses. Each coefficient was estimated in a separate regression including students born in the
years immediately before and after December 31 of the year shown. Sharp estimates computed using birthdate as the
running variable with a cubic polynomial. Fuzzy estimates were computed instrumenting relative age with a cubic
polynomial in birthdate and a discrete increase at the cutoff date.
33
TABLE 7—Instrumental Variable estimates of the impact of relative age on test scores
Grade
All
3
4
5
6
7
8
9
0.263
(0.027)
[23,269]
0.321
(0.029)
[23,184]
0.297
(0.034)
[24,781]
0.277
(0.034)
[21,690]
0.302
(0.030)
[22,029]
0.280
(0.032)
[20,683]
0.177
(0.028)
[16,133]
Spanish
Boys
0.255
(0.039)
[11,874]
0.261
(0.040)
[11,833]
0.284
(0.051)
[12,346]
0.264
(0.049)
[10,866]
0.320
(0.043)
[11,127]
0.273
(0.044)
[10,345]
0.193
(0.041)
[7,729]
Girls
0.274
(0.037)
[11,395]
0.377
(0.041)
[11,349]
0.311
(0.046)
[12,435]
0.289
(0.045)
[10,824]
0.279
(0.040)
[10,901]
0.283
(0.045)
[10,338]
0.160
(0.038)
[8,404]
All
0.316
(0.027)
[23,269]
0.361
(0.029)
[23,184]
0.290
(0.034)
[24,781]
0.290
(0.034)
[21,690]
0.340
(0.030)
[22,029]
0.206
(0.032)
[20,683]
0.120
(0.028)
[16,133]
Math
Boys
0.330
(0.039)
[11,874]
0.329
(0.041)
[11,833]
0.260
(0.051)
[12,346]
0.302
(0.050)
[10,866]
0.363
(0.044)
[11,127]
0.228
(0.045)
[10,345]
0.148
(0.041)
[7,729]
Girls
0.304
(0.037)
[11,395]
0.390
(0.040)
[11,349]
0.318
(0.046)
[12,435]
0.278
(0.045)
[10,824]
0.316
(0.040)
[10,901]
0.185
(0.046)
[10,338]
0.094
(0.039)
[8,404]
Standard errors in parentheses. Number of observations in square brackets. Each coefficient was estimated in a
separate regression. Relative age was instrumented with assigned relative age, computed as the number of days
between birthdate and December 31 of the year of birth, divided by 365.25.
TABLE 8—Comparison of estimates of the impact of relative-age on test scores
Spanish
Math
Regression
Instrumental Instrumental
Regression
Instrumental Instrumental
Difference in discontinuity variables, 7th variables, 8th
Difference in discontinuity variables, 7th variables, 8th
differences
(parametric)
grade
grade
differences
(parametric)
grade
grade
All
0.305
0.353
0.302
0.280
0.292
0.359
0.340
0.206
(0.022)
(0.035)
(0.030)
(0.032)
(0.022)
(0.035)
(0.030)
(0.032)
Boys
0.325
0.376
0.320
0.273
0.268
0.223
0.363
0.228
(0.032)
(0.049)
(0.043)
(0.044)
(0.032)
(0.050)
(0.044)
(0.045)
Girls
0.289
0.326
0.279
0.283
0.315
0.497
0.316
0.185
(0.030)
(0.047)
(0.040)
(0.045)
(0.030)
(0.048)
(0.040)
(0.046)
Standard errors in parentheses. Difference-in-differences bootstrapping estimates for cohorts born in 1995-96 and 1998-99. Regression
discontinuity fuzzy estimates around the December 1998 discontinuity. See Tables 3, 6 and 7.
34
TABLE 9—Composition of the sample of analysis of adulthood outcomes
% with employer% with
%
Logarithm of
% with spouse
Number
Year of
provided medical
some college
occupied
earnings
with some college
of children
birth
insurance
1960
17.8 [30,094]
70.4 [30,094]
8.32 [16,012]
60.1 [30,094]
16.7 [16,136]
3.34 [22,429]
1961
18.1 [33,541]
70.9 [33,541]
8.32 [17,935]
60.0 [33,541]
17.1 [17,946]
3.25 [25,085]
1962
18.1 [36,330]
72.1 [36,330]
8.33 [20,001]
59.7 [36,330]
17.5 [19,567]
3.19 [27,184]
1963
18.3 [37,462]
72.6 [37,462]
8.33 [20,696]
59.4 [37,462]
17.6 [20,330]
3.09 [28,002]
1964
17.9 [38,461]
73.2 [38,461]
8.33 [21,574]
60.0 [38,461]
17.5 [20,732]
3.01 [28,860]
1965
17.3 [39,246]
73.3 [39,246]
8.32 [22,282]
59.4 [39,246]
17.3 [21,390]
2.96 [29,319]
1966
17.0 [40,189]
73.7 [40,189]
8.31 [22,996]
59.4 [40,189]
17.1 [21,784]
2.88 [29,758]
1967
16.8 [39,608]
73.2 [39,608]
8.32 [22,748]
60.5 [39,608]
17.2 [21,643]
2.80 [29,261]
1968
16.8 [42,057]
73.8 [42,057]
8.32 [24,270]
60.1 [42,057]
17.5 [22,688]
2.71 [30,752]
1969
16.6 [42,076]
73.4 [42,076]
8.31 [24,275]
60.0 [42,076]
16.9 [22,814]
2.65 [30,657]
1970
16.6 [44,617]
73.5 [44,617]
8.30 [25,776]
59.8 [44,617]
16.8 [23,961]
2.57 [31,775]
1971
16.9 [42,450]
72.9 [42,450]
8.31 [24,245]
61.1 [42,450]
17.2 [22,854]
2.48 [30,153]
1972
16.8 [45,430]
72.9 [45,430]
8.30 [26,297]
60.3 [45,430]
17.1 [24,475]
2.39 [31,683]
1973
17.3 [45,014]
72.7 [45,014]
8.30 [25,973]
60.8 [45,014]
16.8 [24,266]
2.30 [30,774]
1974
18.2 [45,398]
72.2 [45,398]
8.29 [26,024]
61.7 [45,398]
17.3 [24,505]
2.19 [29,954]
1975
18.6 [44,697]
71.5 [44,697]
8.28 [25,423]
62.3 [44,697]
16.8 [24,214]
2.10 [28,625]
1976
19.1 [43,519]
71.3 [43,519]
8.27 [24,694]
62.6 [43,519]
17.0 [23,544]
2.00 [26,978]
1977
20.1 [43,546]
71.2 [43,546]
8.26 [24,712]
62.6 [43,546]
16.8 [23,573]
1.89 [25,817]
1978
22.3 [42,839]
71.1 [42,839]
8.28 [24,135]
63.3 [42,839]
17.4 [23,018]
1.76 [23,777]
1979
23.1 [44,224]
70.6 [44,224]
8.27 [24,758]
63.9 [44,224]
16.9 [23,642]
1.62 [22,720]
1980
23.3
[8,062]
70.3 [8,062]
8.23 [4,540]
64.2 [8,062]
16.0 [4,258]
1.57 [3,992]
1960-80
18.3 [828,860]
72.3 [828,860]
8.30 [469,366]
60.9 [828,860]
17.1 [447,340]
2.51 [567,555]
Notes: Based on ENOE 2005-I, 2006-II, 2007-III, 2008-IV, 2010-I, 2011-II, 2012-III, and 2013-IV. Only includes adults born between
March 3, 1960 and March 2, 1980.
35
TABLE 10—Regression discontinuity estimates of the impact of an additional year of relative-age
on in adulthood outcomes
Percent with some
college
Covariates
All
Quadratic
Cubic
Quadratic with
±0.25
Males
Quadratic
Cubic
Quadratic with
±0.25
No
Yes
Percent occupied
No
Yes
Logarithm of earnings
No
Yes
Percent with employerprovided medical
insurance
No
Yes
Percent with spouse
with some college
No
Yes
1.527
1.436
(0.254)
(0.252)
[825,837] [825,837]
0.994
0.903
(0.340)
(0.337)
[825,837] [825,837]
0.902
0.798
(0.363)
(0.360)
[413,626] [413,626]
0.450
(0.295)
[825,837]
0.479
(0.395)
[825,837]
0.170
(0.419)
[413,626]
0.422
(0.294)
[825,837]
0.413
(0.394)
[825,837]
0.101
(0.418)
[413,626]
0.0237
0.0239
(0.007)
(0.007)
[468,123] [468,123]
0.0075
0.0087
(0.010)
(0.009)
[468,123] [468,123]
0.0199
0.0199
(0.010)
(0.010)
[234,586] [234,586]
0.544
(0.322)
[825,837]
0.156
(0.431)
[825,837]
0.580
(0.457)
[413,626]
0.488
(0.319)
[825,837]
0.262
(0.427)
[825,837]
0.620
(0.454)
[413,626]
1.172
(0.300)
[565,413]
0.499
(0.401)
[565,413]
0.714
(0.428)
[282,930]
1.075
(0.297)
[565,413]
0.405
(0.398)
[565,413]
0.611
(0.425)
[282,930]
1.553
1.442
(0.392)
(0.388)
[379,968] [379,968]
0.836
0.736
(0.524)
(0.520)
[379,968] [379,968]
0.392
0.277
(0.559)
(0.554)
[190,997] [190,997]
-0.213
(0.253)
[379,968]
-0.022
(0.338)
[379,968]
-0.293
(0.358)
[190,997]
-0.229
(0.252)
[379,968]
-0.013
(0.338)
[379,968]
-0.296
(0.357)
[190,997]
0.0177
0.0171
(0.009)
(0.008)
[280,284] [280,284]
-0.0003
-0.0009
(0.011)
(0.011)
[280,284] [280,284]
0.0031
0.0005
(0.012)
(0.012)
[140,979] [140,979]
0.929
(0.486)
[379,968]
-0.046
(0.650)
[379,968]
0.104
(0.691)
[190,997]
0.922
(0.480)
[379,968]
0.226
(0.643)
[379,968]
0.239
(0.683)
[190,997]
0.944
(0.396)
[274,774]
0.401
(0.530)
[274,774]
0.308
(0.566)
[138,021]
0.836
(0.393)
[274,774]
0.297
(0.526)
[274,774]
0.189
(0.562)
[138,021]
Females
Quadratic
Number of children
No
Yes
1.483
1.406
0.992
0.977
0.0359
0.0357
0.232
0.129
1.409
1.335
-0.046
-0.041
(0.330)
(0.328)
(0.446)
(0.444)
(0.012)
(0.012)
(0.410)
(0.407)
(0.444)
(0.440)
(0.015)
(0.015)
[445,869] [445,869] [445,869] [445,869] [187,839] [187,839] [445,869] [445,869] [290,639] [290,639] [445,850] [445,850]
Cubic
1.061
0.990
0.483
0.409
0.0151
0.0178
0.561
0.583
0.643
0.546
-0.020
-0.016
(0.442)
(0.439)
(0.597)
(0.595)
(0.016)
(0.016)
(0.549)
(0.546)
(0.594)
(0.589)
(0.020)
(0.019)
[445,869] [445,869] [445,869] [445,869] [187,839] [187,839] [445,869] [445,869] [290,639] [290,639] [445,850] [445,850]
Quadratic with
1.287
1.199
0.186
0.128
0.0400
0.0424
1.193
1.172
1.124
1.034
-0.030
-0.023
±0.25
(0.472)
(0.468)
(0.634)
(0.632)
(0.017)
(0.017)
(0.582)
(0.578)
(0.635)
(0.629)
(0.021)
(0.021)
[222,629] [222,629] [222,629] [222,629]
[93,607] [93,607] [222,629] [222,629] [144,909] [144,909] [222,622] [222,622]
Notes: Based on ENOE 2005-I, 2006-II, 2007-III, 2008-IV, 2010-I, 2011-II, 2012-III, and 2013-IV. Only includes adults born between March 3, 1960 and March 2,
1980. Standard errors in parentheses. Number of observations in square brackets. Each coefficient is the result of a separate regression. The covariates are dummies
for state of birth and survey wave.
36
TABLE 11—Fixed-effects estimates the impact of relative-age on adulthood outcomes
Percent with some
college
Covariates
All
Constant
October
November
December
January
February
March
April
May
June
July
August
Males
Constant
October
November
December
January
February
March
April
May
June
July
August
Females
Constant
October
November
December
January
Percent occupied
Logarithm of earnings
Percent with employerprovided medical
insurance
No
Yes
No
Yes
No
Yes
No
Yes
19.502
(0.147)
-0.035
(0.208)
-0.670
(0.210)
-1.044
(0.207)
-1.264
(0.207)
-1.321
(0.211)
-1.735
(0.207)
-1.822
(0.210)
-2.181
(0.207)
-2.424
(0.208)
-1.859
(0.207)
-1.591
(0.207)
825,837
11.763
(0.639)
-0.058
(0.206)
-0.667
(0.208)
-1.049
(0.205)
-1.265
(0.205)
-1.351
(0.209)
-1.487
(0.206)
-1.522
(0.208)
-1.841
(0.206)
-2.086
(0.206)
-1.631
(0.206)
-1.425
(0.205)
825,837
72.628
(0.171)
0.128
(0.241)
-0.001
(0.243)
-0.295
(0.240)
-0.206
(0.240)
-0.445
(0.245)
-0.248
(0.241)
-0.433
(0.244)
-0.616
(0.241)
-0.305
(0.241)
-0.434
(0.241)
-0.552
(0.240)
825,837
74.679
(0.746)
0.141
(0.241)
-0.005
(0.243)
-0.284
(0.240)
-0.200
(0.239)
-0.447
(0.244)
-0.193
(0.240)
-0.367
(0.243)
-0.559
(0.240)
-0.243
(0.241)
-0.434
(0.240)
-0.519
(0.239)
825,837
8.327
(0.004)
-0.007
(0.006)
-0.011
(0.006)
-0.027
(0.006)
-0.030
(0.006)
-0.030
(0.006)
-0.037
(0.006)
-0.027
(0.006)
-0.050
(0.006)
-0.049
(0.006)
-0.031
(0.006)
-0.027
(0.006)
468,123
8.285
(0.013)
-0.006
(0.006)
-0.009
(0.006)
-0.022
(0.006)
-0.027
(0.006)
-0.027
(0.006)
-0.036
(0.006)
-0.025
(0.006)
-0.044
(0.006)
-0.043
(0.006)
-0.029
(0.006)
-0.027
(0.006)
468,123
61.469
(0.186)
0.104
(0.263)
-0.037
(0.266)
-0.304
(0.262)
-0.199
(0.261)
-0.312
(0.267)
-1.007
(0.263)
-0.864
(0.266)
-1.054
(0.262)
-1.370
(0.263)
-0.723
(0.262)
-0.626
(0.261)
825,837
21.723
(0.227)
0.225
(0.320)
-0.618
(0.323)
-1.113
(0.320)
-1.160
(0.318)
-1.345
(0.325)
-1.585
(0.319)
-1.779
(0.324)
-1.939
(0.320)
-2.413
(0.320)
-1.947
(0.319)
-1.459
(0.318)
379,968
21.381
(0.701)
0.250
(0.317)
-0.568
(0.320)
-1.023
(0.317)
-1.102
(0.315)
-1.280
(0.322)
-1.385
(0.316)
-1.551
(0.321)
-1.706
(0.317)
-2.125
(0.317)
-1.781
(0.316)
-1.316
(0.315)
379,968
92.649
(0.146)
0.085
(0.207)
0.002
(0.208)
0.073
(0.206)
0.066
(0.205)
-0.134
(0.210)
0.056
(0.206)
0.002
(0.209)
-0.122
(0.206)
0.199
(0.206)
0.266
(0.206)
0.125
(0.205)
379,968
90.047
(0.455)
0.083
(0.206)
-0.004
(0.208)
0.089
(0.206)
0.108
(0.205)
-0.096
(0.210)
0.027
(0.205)
-0.056
(0.209)
-0.194
(0.206)
0.166
(0.206)
0.227
(0.205)
0.105
(0.205)
379,968
8.467
(0.005)
0.001
(0.007)
-0.007
(0.007)
-0.023
(0.007)
-0.018
(0.007)
-0.021
(0.007)
-0.032
(0.007)
-0.022
(0.007)
-0.041
(0.007)
-0.040
(0.007)
-0.027
(0.007)
-0.020
(0.007)
280,284
8.449
(0.015)
0.004
(0.007)
-0.003
(0.007)
-0.016
(0.007)
-0.015
(0.007)
-0.017
(0.007)
-0.031
(0.007)
-0.020
(0.007)
-0.036
(0.007)
-0.034
(0.007)
-0.027
(0.007)
-0.019
(0.007)
280,284
17.595
(0.192)
-0.224
(0.270)
-0.718
(0.274)
-0.932
(0.269)
-1.338
(0.269)
8.229
(0.841)
-0.280
(0.268)
-0.745
(0.271)
-0.988
(0.266)
-1.380
(0.266)
55.432
(0.259)
0.441
(0.365)
-0.042
(0.369)
-0.114
(0.363)
-0.300
(0.363)
57.615
(1.142)
0.444
(0.363)
-0.059
(0.368)
-0.113
(0.361)
-0.310
(0.362)
8.118
(0.007)
-0.011
(0.010)
-0.018
(0.010)
-0.024
(0.010)
-0.046
(0.010)
8.023
(0.022)
-0.011
(0.010)
-0.015
(0.010)
-0.020
(0.010)
-0.042
(0.010)
37
Percent with spouse
with some college
No
Yes
53.032
(0.809)
0.069
(0.261)
-0.035
(0.264)
-0.270
(0.260)
-0.147
(0.259)
-0.328
(0.265)
-0.920
(0.261)
-0.735
(0.264)
-0.823
(0.260)
-1.089
(0.261)
-0.531
(0.260)
-0.520
(0.259)
825,837
18.228
(0.174)
-0.039
(0.245)
-0.692
(0.247)
-0.943
(0.244)
-1.599
(0.244)
-1.221
(0.249)
-1.470
(0.244)
-1.622
(0.247)
-2.035
(0.244)
-2.080
(0.245)
-1.334
(0.244)
-1.322
(0.244)
565,413
17.262
(0.545)
-0.038
(0.243)
-0.609
(0.245)
-0.866
(0.242)
-1.511
(0.242)
-1.138
(0.247)
-1.347
(0.242)
-1.447
(0.245)
-1.792
(0.242)
-1.823
(0.243)
-1.189
(0.242)
-1.205
(0.242)
565,413
50.791
(0.281)
0.538
(0.397)
0.285
(0.400)
-0.658
(0.396)
0.087
(0.394)
-0.456
(0.403)
-1.094
(0.395)
-1.067
(0.401)
-1.430
(0.397)
-1.884
(0.397)
-1.251
(0.395)
-1.142
(0.394)
379,968
55.698
(0.867)
0.507
(0.393)
0.214
(0.396)
-0.626
(0.392)
0.141
(0.390)
-0.550
(0.399)
-0.946
(0.391)
-0.947
(0.397)
-1.157
(0.392)
-1.475
(0.392)
-1.065
(0.391)
-1.064
(0.390)
379,968
14.880
(0.229)
0.245
(0.325)
-0.455
(0.326)
-0.745
(0.324)
-0.986
(0.322)
-1.017
(0.329)
-1.177
(0.322)
-1.186
(0.327)
-1.802
(0.323)
-1.660
(0.323)
-1.240
(0.322)
-1.029
(0.322)
274,774
12.219
(0.724)
0.290
(0.322)
-0.393
(0.324)
-0.665
(0.321)
-0.944
(0.320)
-0.951
(0.327)
-0.991
(0.320)
-0.983
(0.324)
-1.547
(0.321)
-1.363
(0.321)
-1.089
(0.320)
-0.892
(0.319)
274,774
70.641
(0.238)
-0.411
(0.336)
-0.293
(0.340)
-0.269
(0.334)
-0.516
(0.334)
63.549
(1.047)
-0.436
(0.333)
-0.245
(0.337)
-0.225
(0.331)
-0.460
(0.331)
21.413
(0.258)
-0.346
(0.364)
-0.902
(0.368)
-1.219
(0.361)
-2.209
(0.361)
25.170
(0.810)
-0.409
(0.360)
-0.809
(0.364)
-1.184
(0.358)
-2.080
(0.358)
Number of children
No
Yes
2.461
(0.009)
-0.005
(0.013)
-0.002
(0.013)
0.006
(0.012)
0.024
(0.012)
3.810
(0.037)
-0.001
(0.012)
0.008
(0.012)
0.016
(0.012)
0.041
(0.012)
February
-1.269
-1.373
-0.426
-0.504
-0.037
-0.035
-0.340
-0.298
-1.455
-1.370
0.007
0.029
(0.274)
(0.272)
(0.370)
(0.369)
(0.010)
(0.010)
(0.341)
(0.338)
(0.369)
(0.366)
(0.013)
(0.012)
March
-1.879
-1.568
-0.634
-0.537
-0.044
-0.042
-0.866
-0.796
-1.723
-1.709
0.083
0.032
(0.271)
(0.268)
(0.365)
(0.364)
(0.010)
(0.010)
(0.336)
(0.334)
(0.363)
(0.360)
(0.013)
(0.012)
April
-1.831
-1.447
-0.567
-0.420
-0.032
-0.026
-0.818
-0.714
-2.067
-1.972
0.099
0.044
(0.273)
(0.271)
(0.369)
(0.368)
(0.010)
(0.010)
(0.339)
(0.337)
(0.367)
(0.363)
(0.013)
(0.012)
May
-2.334
-1.901
-0.588
-0.467
-0.058
-0.049
-0.973
-0.781
-2.330
-2.136
0.113
0.059
(0.269)
(0.267)
(0.364)
(0.362)
(0.010)
(0.010)
(0.334)
(0.332)
(0.361)
(0.358)
(0.013)
(0.012)
June
-2.447
-2.063
-0.856
-0.758
-0.064
-0.057
-0.865
-0.655
-2.427
-2.258
0.118
0.070
(0.272)
(0.269)
(0.366)
(0.365)
(0.010)
(0.010)
(0.337)
(0.335)
(0.365)
(0.362)
(0.013)
(0.012)
July
-1.798
-1.499
-1.180
-1.160
-0.040
-0.035
-0.190
0.016
-1.430
-1.328
0.097
0.058
(0.271)
(0.268)
(0.365)
(0.364)
(0.010)
(0.010)
(0.336)
(0.333)
(0.362)
(0.359)
(0.013)
(0.012)
August
-1.687
-1.499
-0.975
-0.931
-0.039
-0.038
-0.268
-0.154
-1.606
-1.544
0.072
0.046
(0.269)
(0.266)
(0.363)
(0.361)
(0.010)
(0.010)
(0.334)
(0.331)
(0.361)
(0.358)
(0.012)
(0.012)
445,869 445,869
445,869
445,869
187,839
187,839
445,869 445,869
290,639 290,639
445,850
445,850
Notes: Based on ENOE 2005-I, 2006-II, 2007-III, 2008-IV, 2010-I, 2011-II, 2012-III, and 2013-IV. Only includes adults born between March 3, 1960 and March
2, 1980. Standard errors in parentheses. Each column within each panel represents a separate regression. The covariates are dummies for state of birth and survey
wave.
38
TABLE 12—August-September difference across age groups in adulthood outcomes, fixed effects
model
Age
group
All
25-29
30-34
34-39
40-44
45-53
Males
25-29
30-34
34-39
40-44
45-53
Percent with
some college
Percent
occupied
Logarithm of
earnings
Percent with
employer- Percent with
provided
spouse with
medical
some college
insurance
-1.182
(0.733)
[73,280]
-1.470
(0.445)
[180,821]
-1.766
(0.389)
[217,623]
-1.111
(0.407)
[202,942]
-1.453
(0.477)
[151,171]
-0.783
(0.822)
[73,280]
-0.442
(0.515)
[180,821]
-0.083
(0.461)
[217,623]
-0.364
(0.477)
[202,942]
-1.339
(0.564)
[151,171]
-0.0277
(0.017)
[41,720]
-0.0266
(0.012)
[104,007]
-0.0178
(0.011)
[126,018]
-0.0293
(0.012)
[116,314]
-0.0366
(0.015)
[80,064]
-0.284
(0.839)
[73,280]
0.163
(0.549)
[180,821]
-1.182
(0.504)
[217,623]
-1.574
(0.530)
[202,942]
0.879
(0.615)
[151,171]
-0.530
(0.914)
[34,811]
-1.466
(0.536)
[113,869]
-1.990
(0.464)
[154,101]
-0.734
(0.473)
[150,327]
-0.714
(0.546)
[112,305]
-1.287
(1.104)
[33,671]
-2.211
(0.673)
[83,149]
-1.615
(0.596)
[99,950]
-0.422
(0.632)
[93,697]
-1.119
(0.759)
[69,501]
-0.461
(0.756)
[33,671]
0.010
(0.432)
[83,149]
-0.011
(0.379)
[99,950]
1.059
(0.399)
[93,697]
-0.621
(0.516)
[69,501]
-0.0105
(0.019)
[25,727]
-0.0260
(0.013)
[63,420]
0.0058
(0.013)
[75,585]
-0.0252
(0.014)
[68,584]
-0.0449
(0.018)
[46,968]
-0.935
(1.288)
[33,671]
0.319
(0.831)
[83,149]
-1.568
(0.760)
[99,950]
-2.800
(0.789)
[93,697]
0.300
(0.919)
[69,501]
-0.235
(1.291)
[15,134]
-1.336
(0.742)
[53,489]
-0.972
(0.621)
[74,373]
-1.054
(0.607)
[74,815]
-0.355
(0.689)
[56,963]
Females
25-29
Number of
children
-1.042
-0.910
-0.0544
0.190
-0.814
0.0504
(0.979)
(1.212)
(0.031)
(1.042)
(1.275)
(0.031)
[39,609]
[39,609]
[15,993]
[39,609]
[19,677]
[39,608]
30-34
-0.836
-0.507
-0.0207
-0.148
-1.557
0.0069
(0.592)
(0.773)
(0.020)
(0.694)
(0.766)
(0.022)
[97,672]
[97,672]
[40,587]
[97,672]
[60,380]
[97,669]
34-39
-1.891
-0.089
-0.0479
-0.877
-2.928
0.0508
(0.510)
(0.698)
(0.018)
(0.645)
(0.681)
(0.022)
[117,673]
[117,673]
[50,433]
[117,673]
[79,728]
[117,667]
40-44
-1.692
-1.724
-0.0419
-0.531
-0.476
0.0939
(0.525)
(0.734)
(0.020)
(0.686)
(0.721)
(0.026)
[109,245]
[109,245]
[47,730]
[109,245]
[75,512]
[109,238]
45-53
-1.674
-1.727
-0.0293
1.222
-1.213
0.0151
(0.596)
(0.847)
(0.024)
(0.791)
(0.842)
(0.033)
[81,670]
[81,670]
[33,096]
[81,670]
[55,342]
[81,668]
Notes: Based on ENOE 2005-I, 2006-II, 2007-III, 2008-IV, 2010-I, 2011-II, 2012-III, and 2013-IV. Only
includes adults born between March 3, 1960 and March 2, 1980. Standard errors in parentheses. Number
of observations in square brackets. Each coefficient is the result of a separate regression. The regressions
include dummies for state of birth and survey wave.
39
FIGURE 1—Relative age and test scores in 2012 by date of birth
Source: ENLACE 2012 test scores for Tlaxcala, grades 3 to 9. Relative age was computed as the difference in
days between the date of birth of each student and the average for all students in the same grade, divided by
365.25. Test scores were standardized at the state level by grade. Observations were grouped by month of birth.
40
FIGURE 2— Relative age and test scores in 2009 by date of birth
Source: ENLACE 2009 test scores for Tlaxcala, grades 3 to 9. Relative age was computed as the difference in
days between the date of birth of each student and the average for all students in the same grade, divided by
365.25. Test scores were standardized at the state level by grade. Observations were grouped by month of birth.
41
FIGURE 3—Test-takers by distance between day of birth and December 31
Notes: Based ENLACE 2009 and 2012, grades 3 to 9 in Tlaxcala. The horizontal axis shows the
number of days between the birthdate of the students and the closest December 31. The top panel only
includes test-takers in 2009 born between July 3, 1994 and July 2, 1999. The bottom panel only
includes test-takers in 2012 born between July 3, 1997 and July 2, 2003.
42
FIGURE 4—Mother characteristics by distance between day of birth and December 31
Notes: Based on ENOE 2005-I, 2006-II, 2007-III, 2008-IV, 2010-I, 2011-II, 2012-III, and 2013IV. It includes 9,361 children born between July 3, 1997 and July 2, 2003, residing in Tlaxcala
with their mother. The horizontal axis shows the number of days between the birthdate of the
child and the closest December 31. The solid lines show the fit of quadratic polynomials at each
side of December 31, and the shaded areas show their 95% confidence intervals.
43
FIGURE 5—ENOE sample: number of respondents by birthdate in five-day bins
Distance in days to the closest September 1
Notes: Based on ENOE 2005-I, 2006-II, 2007-III, 2008-IV, 2010-I, 2011-II, 2012-III, and 2013-IV.
Only includes adults born between March 3, 1960 and March 2, 1980. The horizontal axis shows the
number of days between the birthdate of the person and the closest September 1. The solid lines
show the fit of quadratic polynomials at each side of September 1, and the shaded areas show their
99% confidence intervals.
44
FIGURE 6—Adulthood outcomes around the September cutoff, averages for five-day bins
% with some college
% occupied
Logarithm of earnings
% with employer-provided medical insurance
% with spouse with some college
Number of children (women only)
Distance in days to the closest September 1
Notes: Based on ENOE 2005-I, 2006-II, 2007-III, 2008-IV, 2010-I, 2011-II, 2012-III, and 2013-IV. Only includes adults born between March 3,
1960 and March 2, 1980.
45
FIGURE 7—Estimates of month-of-birth fixed effects in adulthood outcomes relative to September
% with some college
% occupied
Logarithm of earnings
% with employer-provided medical insurance
% with spouse with some college
Number of children (women only)
Month of birth (September is the omitted category)
Notes: Based on ENOE 2005-I, 2006-II, 2007-III, 2008-IV, 2010-I, 2011-II, 2012-III, and 2013-IV. Only includes adults born between March 3,
1960 and March 2, 1980. Estimates produced with fixed-effects models with covariates (see Table 11). Baseline month is September. Solid
markers indicate estimate is significant at 95% confidence.
46
FIGURE 8—Simulation results to illustrate that “anything goes”: wealth can magnify, attenuate or
reverse relative-age effects in adulthood
Notes: Based on a simulation using the functional forms and parameters mentioned in the text. The
gap in investments illustrates differences in the allocation of resources to siblings perceived as
having different abilities. It is computed as the investment in the high-ability sibling minus
investment in the low-ability sibling. The ratio of earnings is calculated using those investments and
actual ability of each sibling (which is assumed to be the same.) It is computed as the earnings of the
high-ability sibling divided by the earnings of the low-ability sibling.
47
APENDIX
TABLE A—Relative-age effects: literature review
Author(s)
Country and data source
Outcome
Technique
Main results
IV relative age with
assigned relative age.
Controls for season
of birth effects are
possible because of
the cross-country
variation in cutoff
dates for school
eligibility.
The difference between the oldest
and the youngest in 3rd or 4th grade
ranges between 0.20-0.47σ across
the 11 countries analyzed. Of the
19 countries only two (Denmark
and Finland) do not have
significant estimates. For the rest
they range in 0.14-0.42σ. For the
pooled samples they are 0.26-029.
σ in 4th grade and 0.16-0.18σ in 8th
grade.
Panel I. Test scores
Bedard and Dhuey
(2006)
Datar (2006)
Lawlor, Clark,
Ronalds and Leon
(2006)
Austria, Belgium, Canada, Czech
Republic, Denmark, England, Finland,
France, Greece, Iceland, Italy, Japan,
New Zealand, Norway, Portugal, Slovak
Republic, Spain, Sweden, United States.
Trends in International Mathematics and
Science Study (TIMSS) 1995 and 1999,
Early Childhood Longitudinal Study
(ECLS) and National Education
Longitudinal Study (NELS). Sample
sizes across grades and countries range
between 2,920 and 25,062.
United States. Early Childhood
Longitudinal Study-Kindergarten Class.
Representative sample of children who
entered kindergarten in school year 19981999. Sample size in main regressions
ranges between 13,039 and 13,777.
Scotland. Aberdeen Children of the
1950s cohort study. Sample size is
12,150.
Cascio and
US. Project STAR, Tennessee. Sample
Schanzenbach (2007) size is 5,719.
Puhani and Weber
(2007)
Germany. Progress in International
Reading Literacy Study (PIRLS) 2001.
Sample size ranges between 1,123 and
6,591.
McEwan and Shapiro Chile. Eight annual surveys of first
(2008)
graders (JUNAEB 1997-2004) and
census of fourth graders from SIMCE
2002, TIMSS 1998
Elder and Lubotsky
United States. Early Childhood
(2009)
Longitudinal Study-Kindergarten
cohort (ECLS-K) and the National
Educational Longitudinal Survey of 1988
(NELS:88)
Kawaguchi (2009)
Crawford, Dearden
and Meghir (2010)
Smith (2010)
Math and science test
scores in grades 4
and 8 (3 for ECLS
and 8 for NELS)
Math and reading
test scores at the start
of kindergarten and
the end of first grade.
IV using as
instrument the
number of days
between child’s 5th
birthday and the
school’s cutoff date,
and state’s
kindergarten cutoff
date.
Different domains of OLS with age at
childhood
starting school and
intelligence at ages season of birth fixed
7, 9, and 11.
effects.
Reading and math
Stanford
Achievement Test
scores at the end of
kindergarten.
PIRLS tests scores in
grade 4.
IV using expected
age.
Age at starting primary school and
age relative to class peers were
both associated with the different
measurements of childhood
intelligence.
Test-score differential between
children who enter kindergarten
with a one-year difference in age is
0.71σ.
IV using assigned
One year of relative age has an
relative age. Month- effect of 0.40σ in PIRLS in 4th
level observations. grade.
Test scores in grades RDD
4 (JUNAEB) and 8
(TIMSS)
Math and reading
test scores, grade
repetition
Delaying entrance to kindergarten
one year increases test scores in
0.6-0.8σ in kindergarten, and
results in gains of 0.07-0.10σ in the
first two years of school. The
benefits are larger for at-risk
children.
Reading: 17-19 percentiles in
kindergarten, 14 in 1, 11 in 3, 11 in
5, and 6 in 8
Math: 24-25 percentiles in
kindergarten, 18 in 1, 12 in 3, 9 in
5, and 4 in 8
Japan. TIMSS 2003. Sample size ranges Test scores in grades OLS with quarter-of- 4th graders born in Jan-Mar (the
between 2,453 and 4,558.
4 and 8.
birth fixed effects.
youngest) score 0.186-0.222σ
below those born in Apr-Jun (the
oldest). For 8th graders the
estimates are 0.113-0.159σ.
England. Census of all children attending Test scores at ages 7, Month-fixed effects, 0.35σ at 7, 0.21σ at 11 and 0.13σ at
state (public) schools in England,
11, 14 and 16.
comparing versus
16
national achievement (Key Stage) test
Sep., Different cutoff
results and some background
dates by LEA, IV
characteristics date of birth, home
postcode and a school identifier
Canada. British Columbia. Students born Repetition of 3rd
2SLS, identifying
One additional year of age at test
between May 1985 and December 1987. grade and test scores SSA effect using a
reduces the probability of repeating
Administrative records for 3rd grade and in 10th grade.
temporary variation 3rd grade in 6 percentage points,
Foundation Skills Assessment in 10th
in policy that created and increases test scores in 0.090σ
grade. Sample size ranges between
differences.
in numeracy and 0.107σ in literacy.
94,428 and 109,956.
48
IV: actual age is
instrumented with
predicted age
Increase test scores by more than
0.3σ
Sprietsma (2010)
Black, Devereux and
Salvanes (2011)
Grenet (2011)
Robertson (2011)
Crawford, Dearden
and Greaves (2014)
Nam (2014)
Belgium, Canada, Denmark, France,
Iceland, Italy, Japan, Korea, Latvia,
Norway, New Zealand, Poland, Portugal,
Spain, Sweden, Yugoslavia. Program for
International Student Assessment (PISA)
2003. Sample size ranges between 2,160
and 10,465.
Norway. Norwegian military records
from 1980 to 2005. Sample size is
652,215, all males.
France. Panel Primaire de l’Éducation
Nationale (PPEN) 1997, with a sample
size of 9,342 for 1st grade and 7,653 for
3rd grade. Panel Secondaire de
l’Éducation Nationale (PSEN) 1995, with
a sample size of 16,790 for 6th grade,
10,894 for 9th grade, and 5,460 for 11th
grade. Diplôme National du Brevet
(DNB) 2004, with sample size of
781,391 for 9th grade.
US. Suburban school district of Chicago.
Administrative records and test scores of
Illinois Standards Achievement Test
(ISAT) 2004-2007 in grades 3, 5 and 8.
Sample size in main regressions ranges
between 1,604 and 1,730.
UK. Avon Longitudinal Study of Parents
and Children, children born in August
and September. Sample size of 982.
Millennium Cohort Study, cohort
members who were born in England
between September 2000 and August
2001. Sample size is 5,019.
Test scores at age 15 OLS with controls
for institutional
settings (grade
retention, vocational
education, etc.)
In 10 out of 16 countries the results
are positive and significant. In
those countries older students (by
11 months) outscore younger peers
by 0.096-0.226σ in reading and
0.108-0.305σ in math.
IQ approximately at IV with estimated
age 18.
school starting age.
On year of additional age-at-test
increases score in 0.10σ, and SSA
decreases the score by 0.03σ.
Test scores in grades IV relative age with Older students (born in Jan.) score
1, 3, 6, 9 and 11.
assigned relative age. 0.66σ above the youngest (born in
Dec.) in 1st grade, 0.40-0.53σ in 3rd,
0.25-0.30σ in 6th, and up to 0.18σ
in 9. Not significant effect is found
in 11th grade.
ISAT scores reading OLS using quarterand math grades 3, 5 of-birth fixed effects.
and 8. Probability of
being retained.
National
achievement test
scores at age 7, IQ
and Wechsler
objective language
dimensions
(comprehension and
expression), locus of
control, self-esteem
at age 8.
Korea. Korean Education and
Test scores in grades
Employment Panel, grades 9 (2004) and 7, 8, 9, and 12.
12 (2007). TIMSS, grade 9 (1999, 2003,
2007). Korean education Longitudinal
Survey, grades 7 (2005), 8 (2006) and 9
(2007). Korea Youth Panel Survey,
grades 9 (2003) and 12 (2009). Sample
size ranges between 1,229 and 6,789.
RDD. Day-level
observations.
Students born in Sep.-Nov. perform
better than those born in other
quarters. The effects are up to
0.24σ in 3rd grade, 0.20σ in 5th, and
0.16σ in 8th grade. They are also
less likely to have been retained.
Older students do better when tests
are given at the same point in time
but not when given at the same age.
IV relative age with In grades 7-9 the effects range
assigned relative age between 0.13-0.31σ comparing
older (born in Mar.) versus younger
(born in Feb.) The effects are not
significant or negative in 12th
grade.
Panel II. Intermediate outcomes
Bedard and Dhuey
(2006)
Puhani and Weber
(2007)
US and Canada. Administrative data
Participating in prefrom BC, Ministry of Education, Canada. university program
NELS restricted use, US
(CA), writing the
SAT and enrolling in
4-year college in the
US
Germany. State of Hessen, administrative
records for academic year 2004-05 for
students who entered school between
1997 and 1999. Sample size ranges
between 32,059 and 182,676.
Billari and Pellizzari Italy. Bocconi University administrative
(2008)
records of applicants and students who
enrolled from 1995 to 1998. Sample size
is 5,269 for students and 12,676 for
applicants.
Dhuey and Lipscomb US. Project Talent, 10th through 12th
(2008)
graders attending high school in 1960.
Sample size ranges between 250,069 and
264,986. National Longitudinal Study of
the High School Class of 1972, high
school seniors. Sample size ranges
Probability of
attending higher
track secondary
track.
Relatively older students in British
Columbia and the US are more
likely to participate in preuniversity academic programs
during the final years of high
school, and more likely to enter a
flagship postsecondary institution
in the United States.
IV using assigned
One year of relative age increases
relative age. Month- by 12 percentage points the
level observations. probability of attending the highest
secondary track.
Grades in college,
time to completion,
and admission test
scores.
IV using the
incidence of private
pre-schools in the
province of birth
Younger students have higher
graduation marks and higher
admissions test scores.
Indicator of whether
the student was
sports team captain
or club president.
Self-reported
leadership skill
OLS using quarterly
relative-age
dummies. Relative
age measured with
respect to the
statewide school
Relatively oldest 25 percent of
students are between 4 and 11
percent more likely to hold a
leadership position than the
relatively youngest.
49
IV relative age with
assigned relative age.
Month-level
observations.
between 15,960 and 15,968. High School
and Beyond, 1980 senior and sophomore
classes. Sample size ranges between
18,031 and 18,066.
Dhuey and Lipscomb US. ECLS 1998-2004, with a sample size
(2010)
of 8,120. NELS 1988, with a sample size
of 16,870. ELS 2002, with a sample size
of 12,140.
Mühlenweg and
Puhani (2010)
Grenet (2011)
Schneeweis and
Zweimüller (2014)
(Project Talent).
Probability of
disability
classification in
kindergarten, and
grades 1, 3, 5, 8 and
10.
Germany. State of Hessen.
Probability of
Administrative records of students born attending, upgrading
in June or July in general and vocational to, or downgrading
schools in academic years 2002-03
from the highest or a
through 2006-07. Sample size ranges
higher secondary
between 10,192 and 11,077 per academic track.
year.
entry cutoff date.
IV using assigned
An additional month of relative age
relative age. Month- decreases the likelihood of
level observations. receiving special education services
by 2–5 percent.
IV using assigned
Younger students (born in July,
relative age. Month- after the cutoff) are 8-19 percentage
level observations. points less likely to be in the
highest track. The effects are
mitigated: in 10th grade younger
students are more likely to upgrade
to and less likely to downgrade
from a higher track.
2000-2005 Scolarité data base. Sample
Admission into
Multinomial probit. Younger students are about 21
size of 772,561.
academic track,
Month-level
percentage points less likely to
vocational track,
observations.
choose a high-track school than
dropping out.
their older peers in grade 9
Austria. Administrative student-level
Choosing, upgrading IV using assigned
Strong positive relative-age effect
data from the city of Linz, with a simple or downgrading
relative age. Month- on track choice in grades 5–8, it
size of 25,248. PISA 2003 and 2006,
different tracks.
level observations. persists beyond grade 8 for students
with a sample size of 8,136.
from less-favorable socioeconomic
backgrounds and students in urban
areas (younger students are about
21 percentage points less likely to
choose a high-track school than
their older peers in grade 9)
Panel III. Adulthood outcomes
Kawaguchi (2009)
Dobkin and Ferreira
(2010)
Black, Devereux and
Salvanes (2011)
Grenet (2011)
Japan. Employment Status Survey 2002. Years of education,
Adults born in Apr. 1968-Mar. 1972,
employment status
who were 30-34 years old in 2002.
and income.
Sample size ranges between 16,310 and
27,801.
OLS with quarter-of- Younger males have 0.13 fewer
birth fixed effects.
years of education and 3.9% lower
Age in months.
earnings. Younger females have
0.08 fewer years of education and
are 0.019 more likely to be
employed.
United States. 2000 Decennial Census
Educational
RDD. Age in days. Younger individuals are more
Long Form for the states of California
attainment and,
likely to complete more years of
and Texas (approximately 15% of the
wages, employment,
schooling below the college level.
population in each state.) Individuals
household income,
The effects are below 0.01. No
over the age of 30. Sample size in main house ownership,
effects found at the college level or
regressions ranges between 479,500 and house value, marital
on other variables.
767,302.
status.
Norway. Norwegian Registry Data.
Earnings at age 24- IV. Age in months. SSA lowers earnings up to 11.6%
Individuals born between 1932 and 1970. 35, educational
for females and 9.9% for males at
Sample size ranges between 220,418 and attainment,
the beginning of their careers (ages
701,676.
childbearing, full24-25) and the effects disappear by
time employment,
age 30. For full time workers the
mental health, receipt
figures are 4.1 and 3.8%,
of social assistance.
respectively. No effect on
educational attainment. SSA makes
boys 0.005 less likely to have poor
mental health at age 18 from
(average is 0.07.) And reduces in
0.018 (average is 0.08) the
probability of teenage pregnancy.
France. Enquête Emploi (1990-2002).
Age left full-time
OLS using monthly- Older women (born in Dec.) stay
Individuals born between 1945 and 1965. education, highest
fixed effects. Age in 0.07 fewer years in school. Older
Sample size ranges between 74,129 and held qualification,
months.
individuals are more likely to have
102,532.
probabilities of
“academic qualification”
employment,
and less likely to hold a “vocational
working part-time,
qualification.” Older men are less
and being a civil
likely to be unemployed. Older
servant, and hourly
individuals are more likely to be
wage.
civil servants, and have 0.8-2.3%
higher hourly wages (not
controlling for educational
50
Fredriksson and
Ockert (2013)
Zweimüller (2013)
Nam (2014)
attainment).
Fuzzy RDD with
SSA increases educational
two-sample IV. Age attainment in 0.16 years, only a
in months.
timing effect on earnings, primeage earnings unaffected, for low
people with educated parents,
earnings in prime age increase with
SSA
Austria. Austrian Social Security
Starting wages, type OLS using assigned Younger students are more likely to
Database. Individuals who entered the
of entry job,
relative age as the
pursue an apprenticeship and less
labor market between 1997 and 2000,
educational
explanatory variable. likely to have higher education.
and their wages are observed up until
attainment, wages 1 RDD. Age in
Older males (born in Sep.) are less
five years after entry. Sample size ranges to 5 years after job months.
likely than to work in a blue-collar
between 153,777 and 169,987.
entry.
job and significantly more likely to
work in a white collar-job. Wage
penalty of 1.4-1.9 percentage points
for students born in August (the
youngest) compared to students
born in September (the oldest.)
After five years of labor market
experience, the wage penalty
amounts to 0.8-1.1 percent.
Korea. August Supplementary Data of
Attending two- or
OLS using assigned No significant effect.
the 2010 Economically Active
four-year college,
relative age as the
Population Survey. Individuals born
attending four-year explanatory variable.
between March 1976 and February 1986. college, employment, Age in months.
Sample size ranges between 2,657 and
holding a regular job,
5,274.
and wages.
Sweden. Administrative data from
Statistics Sweden. Individuals born
between July 1935 and June 1955.
Sample size ranges between 307,585 and
2,037,166.
Educational
attainment in years
of schooling,
employment and
wages
51