The Relationship Between Education and Adult Mortality in ...people.tamu.edu/~ganli/publicecon/lleras-muney.pdfThe Relationship Between Education and Adult Mortality in the United

Review of Economic Studies (2005)72, 189–221 0034-6527/05/00090189$02.00c© 2005 The Review of Economic Studies Limited

The Relationship BetweenEducation and Adult Mortality in the

United StatesADRIANA LLERAS-MUNEY

Princeton University

First version received May2002; final version accepted February2004(Eds.)

Prior research has uncovered a large and positive correlation between education and health. Thispaper examines whether education has a causal impact on health. I follow synthetic cohorts usingsuccessive U.S. censuses to estimate the impact of educational attainment on mortality rates. I usecompulsory education laws from 1915 to 1939 as instruments for education. The results suggest thateducation has a causal impact on mortality, and that this effect is perhaps larger than has been previouslyestimated in the literature.

1. INTRODUCTION

Access to healthcare insurance1 and expenditures on healthcare,2 have been shown to havelittle effect on health. On the other hand, there is a large and positive correlation betweeneducation and health (Grossman and Kaestner, 1997). This correlation is strong and significanteven after controlling for different measures of socio-economic status, such as income and race,and regardless of how health is measured (morbidity rates, self-reported health status or othermeasures of health). Given that the measured effects of education are large, investments ineducation might prove to be a cost-effective means of achieving better health,3 if educationindeed helps us to be healthier. But prior research has not ascertained whether the relationshipbetween education and health is causal.

The purpose of this paper is to determine whether education has a causal effect on health,in particular on mortality. The negative relationship between education and mortality, the mostbasic measure of health, has become well established since the famous (Kitagawa and Hauser,1973) study, which found significant differences in mortality rates across educational categoriesfor both sexes. More recent studies (e.g.Christenson and Johnson(1995), Deaton and Paxson(1999)) confirm these findings.Elo and Preston(1996) control for a variety of other mortalityfactors such as income, race, marital status, region of residence, and region of birth.Rogers,Hummer and Nam(2000) further control for access to healthcare, insurance, smoking, exercise,occupation, and other factors.Figures1 and 2 document this relationship using consecutivecensus data for the U.S.: in all cohorts, those who survive have higher education than thosewho do not.

The existing literature has explained this correlation in three ways. One controversialhypothesis is that education increases health, either because education makes people betterdecision makers (Grossman, 1972a,b) and/or because more educated people have better

1. SeeNewhouse(1993).2. For example, seeFilmer and Prichett(1997).3. This was first suggested byAuster, Leveson and Sarachek(1969).

189

190 REVIEW OF ECONOMIC STUDIES

Birth year

1960 census

1970 census

1980 census

0

5000

10,000

15,000

20,000

25,000

1901 1903 1905 1907 1909 1911 1913 1915 1917 1919 1921 1923 1925

FIGURE 1

Number of observations per cohort

1901 1903 1905 1907 1909 1911 1913 1915 1917 1919 1921 1923 1925Birth year

1960 census

1970 census

1980 census

9·00

10·00

11·00

12·00

FIGURE 2

Average years of education by cohortNote: Figures1 and2 follow the same cohorts from the 1960 census up to the 1980 census. InFigure1 we can observethat 10-year mortality increases with age: for older cohorts the number of individuals observed in 1980 is much smallerthan in 1960 or 1970. InFigure2 we can see that the average level of education is higher in 1980 than in 1960 for all

cohorts, suggesting that those who died in each cohort had below average levels of education.

information about health (Kenkel (1991), Rosenzweig and Schultz(1991)). Another possibilityis that poor health results in little education (Perri(1984), Currie and Hyson(1999)). Finally, thiscorrelation could be caused by a third unobserved variable that affects both education and health,for example, genetic characteristics or parental background. Many studies have attempted toinclude these factors.4 However,Fuchs(1982) argued that discount rates (which no study controlsfor) would also explain the correlation: people who are impatient invest little in education andhealth, while people who are patient invest a lot in both.5 Of course, these theories are notnecessarily mutually exclusive.

4. Duleep(1986), Wolfe and Behrman(1987) andMenchik (1993) find no education effect once controls areadded.

5. Farrell and Fuchs(1982) andFuchs(1982) examined this issue but their evidence is inconclusive.

LLERAS-MUNEY EDUCATION AND ADULT MORTALITY 191

In this paper I address this issue using a unique quasi-natural experiment: between 1915and 1939, at least 30 states changed their compulsory schooling laws and child labour laws. Ifcompulsory schooling laws forced people to get more schooling than they would have chosenotherwise, and if education increases health, then individuals who spent their teens in statesthat required them to go to school for more years should be relatively healthier and live longer.The intuition that compulsory education laws provide a natural experiment was put forward firstby Angrist and Krueger(1991). They argued that because compulsory education laws forcedindividuals to stay in school until a certain age, those born in later quarters would stay in schoollonger. Although they were criticized for their choice of quarter of birth as an instrument,6 theunderlying principle is appealing and implementable.7

No other papers have used natural experiments to measure the effect of education onmortality. A few studies (Berger and Leigh(1989), Sander(1995), Leigh and Dhir(1997))have used instrumental variable (IV) estimation with other measures of health, such as bloodpressure, smoking or exercise.8 But these studies are inconclusive because each paper’s choice ofinstrument is questionable. For example, all of these studies use parents’ background/educationas instruments, but we know these are correlated with children’s health,9 and furthermore,we know that health shocks during childhood or gestation have persistent health effects intoadulthood.10 Income and education expenditures in state-of-birth could serve as instruments(Berger and Leigh, 1989), but again they might be correlated with state expenditures on health,state industrial composition and other state characteristics that affect health.

Using the 1960, 1970 and 1980 censuses of the U.S., I select those individuals who were14 years of age between 1915 and 1939. I then construct synthetic cohorts and follow themover time to calculate their mortality rates. I then match cohorts to the compulsory attendanceand child labour laws that were in place in their state-of-birth when they were 14 years old.The census data have not been used to calculate mortality rates before in economic analyses.11

This method could be used to analyse mortality experiences in periods where no other data areavailable.

I start by looking at the direct effect of changes in compulsory schooling on the mortalityrates of the cohorts immediately preceding and following the change in legislation in a regressiondiscontinuity fashion, taking care to look at states where the changes appear to have been bindingfor many children. These results suggest that compulsory laws had an effect on adult mortalityand are consistent with the hypothesis that education affects health.

Then I look at the effect of these laws on educational attainment and show that one moreyear of compulsory schooling increased education by 5% of a year. Then several IV estimationsof the effect of education on mortality are presented, including an original two-stage procedurefor grouped data that can be applied when the first stage can be estimated at the individual level

6. SeeBound, Jaeger and Baker(1995) andBound and Jaeger(1996).7. Harmon and Walker(1995) look at the effects of the laws in the U.K.Meghir and Palme(1999) used Swedish

data.Acemoglu and Angrist(1999) used U.S. laws to determine the size of the social returns to education.8. Berger and Leigh(1989) estimate the effect of education on blood pressure using the NHANES I. They use

state-of-birth, income and education expendituresper capitafrom year-of-birth to age 6 in state-of-birth, and dummiesfor ancestry as instruments for education. They also estimate the effect of education on disability with NLS data, usingIQ and family background measures as instruments. In both cases schooling is significant. Using a sample of olderpersons from the 1986 PSID,Leigh and Dhir(1997) use parental education, background, and state-of-residence at age16 to instrument for education in regressions for disability and exercise. Alternatively, they include direct measures oftime preferences and risk aversion. Education was not always significant. FinallySander(1995) examines the effect ofschooling on the odds of quitting smoking using the General Social Survey. He uses parental schooling as an instrumentfor schooling and finds that the effect of schooling is quite large for whites.

9. Development studies show that family background affects children’s health (seeStrauss and Thomas, 1995).10. For examples see studies that looked at the consequences of the Dutch famine on the health of adults conceived

during the famine, such asHoek, Brown and Susser(1998) or Roseboomet al. (2000).11. However, this methodology is used in epidemiology. For example, see the work byHaines and Preston(1997).


but the second stage can only be estimated at the aggregate level. This procedure can easily beapplied to other cases as well.

The results provide evidence that suggests there is a causal effect of education on mortalityand that this effect is perhaps larger than the previous literature suggests. While GLS estimatessuggest that an additional year of education lowers the probability of dying in the next 10 yearsby approximately 1·3 percentage points, my results from the IV estimation show that the effectis much larger: at least 3·6 percentage points. However, the results also suggest that the OLSand the IV estimates are not statistically different. The direct effect of compulsory schooling onmortality suggests that changes in compulsory schooling affected mortality. Furthermore, theseestimates are consistent with the implied IV effects.

This paper is organized as follows.Section2 describes the data used in this project,including a description of how the census is used to obtain mortality rates.Section3 brieflydescribes compulsory schooling and child labour laws and then looks at the direct effect ofchanges in these laws on education and mortality rates using a regression discontinuity approach.Section4 presents the general econometric framework used for estimating the effect of educationon mortality. The results are presented inSection5, including the first stage results of the effectof the laws on education, the OLS and IV estimates of the effect of education on mortality and thereduced form estimates.Section6 discusses the results and conclusions are given inSection7.

2. DATA

I use the U.S. censuses of 1960, 1970 and 1980, which are 1% random samples of thepopulation.12 The census provides information on age, sex, race, education, and state-of-birth.My samples include all white persons born in the 48 states,13 that were 14 years of age between1914 and 1939, with no missing values for completed years of education.14

I use the censuses to follow “synthetic cohorts”. Although I do not observe the sameindividuals over time (so I cannot observe individual deaths), I do observe the same groups overtime, which allows me to estimate group death rates. I aggregate the censuses into groups definedaccording to their gender, cohort and state-of-birth (descriptive statistics inTable1). Using the1960, 1970 and 1980 censuses, I can calculate two 10-year death rates for each group: one for1960–1970, and another for 1970–1980. For example, the 1960–1970 death rate for a group is thenumber of people alive in 1960(N60) minus the number of people alive in 1970(N70) dividedby the population in 1960(N60). The average 10-year mortality in my data is about 0·11.

One issue that arises in estimating death rates by groups is measurement error. AsFigure3shows, because of random sampling the number of deaths will be overestimated about half thetime and underestimated half the time for all cohorts. As a result, some estimated death ratesare negative. In the data, we observe more negative death rates for younger cohorts and fewernegative death rates for older cohorts (seeFigure4(a)); this is a pattern we should expect. Aswe can see inFigure3(b), with a zero death rate (no change in the population) two successivesamplings of the same population result in a negative death rate half the time. When the deathrate increases (as the population ages) the likelihood that the second sample will contain moreobservations than the first falls, resulting in fewer negative death rates. We also observe fewernegative death rates for states with large population (Figure4(b)), which is also to be expectedsince the sampling error is smaller for larger populations.

12. The data come from the IPUMS 1960 general sample, the 1970 Form 2 State sample (originally 15% statesample), and the 1980 1% Metro sample (originally B sample).

13. Hawaii and Alaska were not then part of the Union.14. For consistency across censuses, I recoded completed years of education to be a maximum of 18 years instead

of 20 in 1980.


TABLE 1

Summary statistics

Census∗ NEFS∗∗

Variables Mean Std dev. Mean Std dev.

Individual 10-year death rate 0·106 0·136 0·254 0·435characteristics Years of completed education 10·697 1·020 10·360 3·326

1970 Dummy 0·471 0·499Female 0·517 0·500 0·540 0·498Age 50·366 8·482 62·941 7·561Born in 1901 0·029 0·167 0·039 0·193Born in 1902 0·025 0·157 0·054 0·226Born in 1903 0·028 0·166 0·056 0·230Born in 1904 0·029 0·169 0·056 0·230Born in 1905 0·031 0·174 0·061 0·239Born in 1906 0·032 0·177 0·068 0·251Born in 1907 0·033 0·180 0·055 0·227Born in 1908 0·036 0·186 0·042 0·200Born in 1909 0·036 0·187 0·025 0·155Born in 1910 0·038 0·191 0·026 0·160Born in 1911 0·039 0·193 0·027 0·161Born in 1912 0·040 0·195 0·028 0·165Born in 1913 0·042 0·200 0·028 0·165Born in 1914 0·043 0·202 0·031 0·174Born in 1915 0·044 0·205 0·033 0·178Born in 1916 0·044 0·205 0·032 0·177Born in 1917 0·044 0·206 0·034 0·182Born in 1918 0·046 0·209 0·035 0·184Born in 1919 0·047 0·213 0·041 0·198Born in 1920 0·048 0·213 0·037 0·188Born in 1921 0·048 0·214 0·038 0·192Born in 1922 0·050 0·217 0·039 0·194Born in 1923 0·049 0·216 0·034 0·182Born in 1924 0·049 0·215 0·044 0·206Born in 1925 0·050 0·217 0·036 0·187

State-of-birth % Urban 53·523 21·279 49·846 20·734characteristics % Foreign 11·737 8·523 11·489 8·434

% Black 8·983 11·901 10·108 13·652% Employed in manufacturing 0·067 0·039 0·065 0·040Annual manufacturing wage 7161·911 1368·253 6971·696 1380·099Value of farm per acre 540·048 276·353 549·371 292·371Per capitanumber of doctors 0·001 0·000 0·0013 0·0003Per capitaeducation expenditures 96·474 42·142 86·305 44·411Number of school buildings per sq. mile 0·174 0·090 0·173 0·092

∗N = 4795, corresponding to cells defined at the gender, state-of-birth, and cohort. All means calculated using weights,where the weights are given by the number of observations in each cell. Monetary values are in 1982–1984 dollars.∗∗N = 4554. Monetary values are in 1982–1984 dollars.

The negative death rates are not a source of concern for two reasons. First, the estimateddeath rates result in consistent estimates of the true death rates.15 Second, average cohort deathrates from the censuses are very similar to those obtained from individual data from the NHEFSdescribed below (seeFigure4(c)).

These graphs suggest there are two issues concerning the death rates. First there is evidenceof age heaping: for ages that are multiples of 10, the death rates fall, because individuals tendto over-report their age and chose a multiple of 10 when doing so. Also, unexpectedly, there are

15. Also note that IV estimates are only consistent, not unbiased, estimates of structural parameters. A consistentestimate of the dependent variable is sufficient for the IV estimators to be consistent.


The 1960 and 1970 census are 1/100 randomsamples of the population, therefore the number of individuals in any given group is alwaysobserved with error. Because of this samplingerror the death rates for any given group are over-estimated 50% of the time and underestimated 50% of the time. However, since the sampling is truly random, the observed death rates are consistent estimates of the true death rates.

If the true death rate is 0 then I observe 50% negative death rates. As cohorts age, the death

n/100

n/100

1960 1970

1960 1970

t

t

Population

n/100

Population

(a)

(b)rate increases (see example above) and thenumber of negative death rates falls.

FIGURE 3

Calculating death rates with the census. (a) Measurement error in death rates due to sampling. (b) An example for ayoung cohort: 0 death rate

large falls in the death rates for younger cohorts between the 1960 and 1970 census (highernumber of negative death rates). This might be due to the relatively few observations per cohort(48 states∗ 2 genders= 96): the standard deviation around the percentage of negative death ratesis quite large (if, for example, one aggregates also by education then the differences are smaller).I will try to address both of these concerns in my estimations.

I also use the National Health and Nutrition Examination Survey I Epidemiologic Follow-up Study, 1992 (hereafter NHEFS). This survey followed 14,407 individuals who were between25 and 74 years of age when interviewed for the first National Health and Nutrition ExaminationSurvey (NHANES I) between 1971 and 1974. The NHEFS followed individuals and recordedwhether they had died by 1985. The sample is composed of whites16 that were 14 years ofage between 1914 and 1939, who were alive in 1975 and followed successfully, with no missingobservations for years of completed education(N = 4554). Table1 shows the summary statisticsfor this data.

16. Other researchers have suggested that blacks had significantly different school experiences during thebeginning of the century. SeeCard and Krueger(1992). Also, Lleras-Muney(2002) suggests that compulsory schoolinglaws and child labour laws did not affect blacks.


1901 1904 1907 1910 1913 1916 1919 1922 1925Birth year

0

0·1

0·2

0·3

0·4

0·5

0·6

0·7

1960–1970 Death rate

1970–1980 Death rate

100

200

300

400

500

600

700

800

0 0·1 0·2 0·3 0·4 0·5 0·6 0·7Percentage of negative death rates

Ave

rage

num

ber

of o

bser

vatio

ns in

sta

te

0

900

(a)

(b)

(c)

Age– 0·1

0

0·1

0·2

0·3

0·4

0·5

0·6

1960 Census

1970 Census

1975 NHEFS

35 37 39 41 43 45 47 49 51 53 55 57 59 61 63 65 67 69 71 73

FIGURE 4

(a) Percentage of negative death rates per cohort. (b) Percentage of negative death rates by average state size. (c) Observed10-year death rates by age

The data on compulsory attendance and child labour laws come from a number of sources.There are 8 years of state-level data (1915, 1918, 1921, 1924, 1929, 1930, 1935 and 1939) on


these laws,17 and some additional information for other years. I imputed missing observations byusing the older values. I also collected data on state-level factors that contributed to the growthof secondary education from 1915 to 193918 or that could affect mortality. These include stateexpenditures on education, the number of school buildings per acre, per cent of the populationthat was living in urban areas, per cent of the white population that was foreign born, per centof the population that was black, per cent of the population employed in manufacturing, averageannual wages in manufacturing per worker, average value of farm property per acre, and numberof doctorsper capita(seeLleras-Muney, 2002for information on data sources).

Each individual is matched to the laws and state characteristics that were in place in theirstate-of-birth when they were 14 years old. I choose this age because it is the lowest commondrop-out age across states. This procedure assumes that individuals went to school in their state-of-birth. Inevitably some individuals were mismatched. However,Card and Krueger(1992) showthat mobility was low during this period. AlsoLleras-Muney(2002) shows that mobility seemsto be uncorrelated to these laws and that restricting the sample to those that are still living in theirstate-of-birth does not change the effect of the laws.19

3. THE DIRECT EFFECT OF COMPULSORY SCHOOLING ON EDUCATION ANDMORTALITY: REGRESSION DISCONTINUITY RESULTS

3.1. Background on compulsory attendance and child labour laws

Since their inception in Massachusetts in 1852, compulsory attendance laws have been complex.They specify a minimum and a maximum age between which school attendance is required; aminimum period of attendance; penalties for non-compliance; and the conditions under whichindividuals could be exempted from attending school, such as the completion of a given grade,mental or physical disability, distance from school, and so on. The most common exemptionwas for work. Work permits were available even for young children, generally even youngerthan the minimum drop-out age specified by compulsory education laws. Child labour laws,which extensively regulated the employment of minors, also included several conditions for thegranting of such permits and for exemptions.

Child labour laws and compulsory attendance laws often were not coordinated. Eachstipulated different requirements for leaving school. For example, in 1924 in Pennsylvania, theages for compulsory attendance were 8–16, but the child labour laws allowed 14 year olds toget work permits and leave school.20 Continuation school laws, which forced children at workto continue their education on a part-time basis, were the only laws that attempted to bridge thisgap. Compulsory attendance laws and child labour laws were in place in all states by 1918, andwere modified frequently thereafter.

There is little agreement regarding the effectiveness of these laws.21 Previous studies(including my own)22 suggest that only three of the many aspects of these laws had an impacton individual educational attainment: the age at which a child had to enter school (enter age),

17. Acemoglu and Angrist(1999) have gathered similar data. The data for this project were collectedindependently.

18. The state-level variables were suggested by the work ofGoldin (1994) andGoldin and Katz(1997).19. I regressed mobility between state-of-birth and state-of-residence in 1960 as a function of education,

compulsory education laws and all other covariates used in this paper. TheF-statistic of joint significance of the lawshas a value of 1·17 (P-value of 0·3151), suggesting the laws cannot explain mobility. AlsoLleras-Muney(2002) showsthat restricting the sample to those that are still living in their state-of-birth yields estimates of the effect of the laws thatare statistically identical to those presented here.

20. During this early period work permits effectively allowed children to leave school. SeeWoltz (1955).21. For a detailed review of these studies seeLleras-Muney(2002).22. SeeSchmidt(1996), Acemoglu and Angrist(1999) andLleras-Muney(2002).


the age at which the child could get a work permit and leave school (work age), and whether ornot the state required children with work permits to attend school on a part-time basis (contsch).FollowingAcemoglu and Angrist(1999), I combine the age at which a child had to enter schooland the age required for a work permit into a single variable,childcom, defined as:childcom=

work age− enter age. This variable is the implicit number of years that a child had to attendschool, given that the entering age and the work permit age were enforced. It takes the values of0, 4, 5, 6, 7, 8, 9 or 10. The other variable,contsch, takes the value of 1 if continuation schoollaws were in place. Tabulations describing these laws throughout the period for each state areshown in Appendices A and B. Importantly note that it is not always the case that more yearsof compulsory schooling were required, although on average states required more schoolingtowards the end of the period.

The period from 1915 to 1939 is when compulsory education laws (hereafter I refer to bothcompulsory attendance laws and child labour laws as “compulsory education laws”) are morelikely to have affected many individuals. Secondary schooling was experiencing remarkablegrowth, especially in the first 40 years of the 20-th century.23 Also, in the previous period (upto 1915), these laws were perceived as ineffective.24 But social scientists agree that the lawswere enforced by the 1920’s25 andSchmidt’s work (1996)—the only study to concentrate onthis period—confirms it.Edwards(1978) andAngrist and Krueger(1991) suggest that the lawsdeclined in importance after the 1940’s. So the first part of the 20-th century provides the perfectwindow of opportunity for using the laws as instruments. Finally, from a technical point of view,this period is interesting because states were constantly changing their compulsory education andchild labour laws.

3.2. Regression discontinuity results

In this section I take a regression discontinuity approach to look at the direct effect of changes incompulsory schooling on mortality rates by comparing the mortality rates of cohorts immediatelybefore and after there was a change in legislation.

The advantage of this approach is that I concentrate on cohorts right before and right afterthe state changed its legislation. These cohorts are presumably similar. On the other hand thesample is small. Additionally we are not looking at cohorts more than 1–3 years away fromchanges in legislation even though these cohorts could have been affected by legislation changes.Most importantly, there could still be errors in the exact year when legislation took place in whichcase this approach possibly underestimates the effects of these laws. Note that this approachassumes that there were no other discontinuous jumps in unobserved characteristics in the yearthat laws were changed. I look at increases and decreases in years of compulsory schoolingseparately.

I drop states that did not change their compulsory schooling laws, eliminate changes thatwere in place only for 1 year,26 and keep 7 cohorts per change: 3 cohorts before, 3 cohorts afterand the cohort of the change. The final sample contains 57 changes in legislation that took placein 36 states, 16 decreases and 41 increases.Figure5 shows the changes in mortality rates forall states that increased their compulsory schooling laws. In these states we see evidence thatcompulsory schooling lowered mortality: mortality rates drop for the first cohort affected by

23. Goldin and Katz(1997) show that the percentage of young adults with high school degrees increased from 9%in 1910 to more than 50% in 1940.

24. Many state laws did not even provide enforcement mechanisms, and if they did, there were often insufficientmeans to enforce them, especially in rural areas. SeeEnsign(1921) andKatz (1976).

25. SeeKatz (1976).26. These changes were presumably never enforced—these changes are possibly due to measurement error in the

laws. In Appendix B all changes that were dropped are highlighted.


All states

0·06–3 –2 –1 0 1 2 3

0·08

0·1

0·12

0·14

0·16

0·18

States where many were affected

FIGURE 5

Effect of increasing compulsory schooling on mortality rates

the law (labelled 0) and it remained low for the 3 cohorts after the law was passed. Due to theimprecision of my death rates and the small sample size, these estimates are not significant.27

However, they do provide suggestive evidence that compulsory laws lowered mortality.A potential concern with these results is that states passed laws when they were no longer

binding, or alternatively that these laws were passed but not enforced. To address this concern, Irestrict attention only to changes that could have affected many. For each increase in compulsoryschooling I calculate the number of individuals in the previous cohort “at the margin”, as apercentage of the number of individuals that were in compliance with the previous law. Sofor example, Alabama went from 4 to 6 years of compulsory schooling in 1921. In 1920, 68individuals were obtaining exactly 4 and 5 years of schooling, and about 425 were obtainingmore than 4 years of schooling, so I calculate that 16% of individuals would be affected (seeAppendix B). I then drop states for which this percentage is lower than 15, somewhat above themedian value in the data. The results are not very sensitive to the cut-off. This further reducesthe sample to 15 states and 21 increases in compulsory schooling.

Figure5 shows the effect of increases in compulsory schooling on mortality rates for thisrestricted sample. Again we see that even though the sample is smaller (and differences are notsignificant), there is an unusually high decrease in mortality rates for the first cohort affected bythe legislative change. This effect is, as expected, larger than the effect for the full sample. Wealso see that mortality remains low for subsequent cohorts.

The results for decreases in compulsory schooling are not shown. They yielded insignificantand unstable effects depending on the sample. There are several reasons why we cannotestimate the effect of decreases in compulsory schooling on mortality. First notice that thereare only 16 downward changes in the law in my data. Notice that in seven of those cases(California 1918, Florida 1918, Georgia 1918, North Carolina 1918, Rhode Island 1918,Utah 1918 and Washington 1918) these changes were in place only for 2/3 years before thelaw changed again to increase the number of compulsory schooling years. Also for Tennesseeand Oregon 1939, we do not observe any cohorts after the change in the law. So indeed thereare only seven cases when the downward changes lasted more than 3 years and for which we

27. Results are shown in Appendix C.


9·6

9·8

10

10·2

10·4

10·6

10·8

–3 –2 –1 0 1 2 3

All states

States where many were affected

FIGURE 6

Effect of increasing compulsory schooling on education

observed cohorts before and after. Aside from the statistical reasons, it is possible that oncecompulsory schooling has been set at some given level, that level becomes the norm and sosubsequent decreases might not have any effect at all.

Figure6 shows the effect of increases in compulsory schooling on educational attainment,for both the entire and restricted samples. We observe that education increased in the yearthe legislation changed for both samples, although again these changes are not statisticallysignificant. Interestingly states where the laws appear binding using my measure, had highermortality rates and lower educational attainment than other states.

These results suggest that compulsory laws had an effect on adult mortality and education,and they are consistent with the hypothesis that education affects health. So I proceed to estimatethese effects more precisely in the following sections.

4. ESTIMATING THE EFFECT OF EDUCATION ON MORTALITY

4.1. Econometric model

The econometric model for the relationship between education and health can be written as

Hi = Xi β + Ei π + εi (1)

where Hi is individual i ’s health stock,E is his education level,X is a vector of individualcharacteristics that affect health, such as smoking, and genetic factors. The purpose of this paperis to determine only whether or not education affects health (i.e. π = 0?). Notice, however, thatOLS estimates of this equation can be biased. One reason is because of measurement error ineducation, although there is evidence that measurement error is relatively small. For example,Angrist and Krueger(1999) find that “measurement error can be expected to reduce the return toa year of education by about 10% (assuming there are no other covariates)”. More importantlythere could be omitted variable bias. For example an individual’s health during childhood canbe correlated with his adult health and may also affect his educational attainment. Alternatively,ability or discount rates can be correlated with both education and health. Lastly it could be


the case that improved health increases investments in education. For example, a longer lifeexpectancy induces individuals to stay in school longer (since a longer life expectancy increasesthe time period over which there will be returns to investments in education, seeBen-Porath(1967)).

4.2. OLS estimation using mortality as the health outcome

Assuming that the model is properly specified (i.e. the previously mentioned endogeneityconcerns are absent) then we can estimate the equation of interest by OLS once we specify theappropriate health outcome. Although health is unobserved, mortality is observable. FollowingGrossman’s model of health (reviewed in his 1999 paper), death occurs when the stock of healthfalls below a certain threshold. In a less deterministic model,Hi is proportional to the underlyingprobability (index) of being alive, and death is the observed result. This is the usual limited-dependent variable set-up. This mortality equation can be estimated at the individual level usingthe NHEFS but not the census. If individuals could be followed from the 1960 census to the 1970census (or from 1970 to 1980), then (based on the previous discussion) the following individuallinear probability model could be estimated:

Di tcs = b + Eicsπ + Xicsβ + Wcsδ + γc + αs + εics, (2)

whereDi tcs is equal to 1 if the individuali (belonging to cohortc and born in states) is deceasedat time t . Eics is i ’s education (measured by completed years of education),X are other time-invariant individual characteristics such as gender,Wcs is a set of characteristics of individuali ’sstate-of-birth at age 14,γc is a set of cohort dummies,αs is a set of state-of-birth dummies,b isan intercept, andε is the error term.

Using the census, individuals cannot be tracked over time, but I can track groups thatare constant over time, and calculate their death rates by aggregating the data. I aggregate bygender, cohort, and state-of-birth. This aggregation level usesall of the available individualcharacteristics that are time invariant (except for education), and therefore it maximizes thenumber of observations in the aggregate data. The aggregate model is derived from the individualmodel by averaging over individuals in a given gender/cohort/state-of-birth group as follows:

Dgtcs = b + Egcsπ + Xgcsβ + Wcsδ + γc + αs + εgcs, (3)

where Dgtcs represents the proportion of individuals that died at timet in a given group orthe death rate for that group, andXgcs represents the average characteristics of that group (forexample, the percentage of females in the group).28 Notice that omitted variable bias at theindividual level will be carried over to the aggregate level.

I use a linear probability model for the estimation. The existence of negative death ratesmakes it impossible to use a (more desirable) non-linear model such as a Logit or Probit.However, since the dependent variable (the death rate) is not censored below by 0, the linearprobability assumption is less problematic in this case than in general. In this linear modelthe error term is heteroscedastic however. A standard estimation procedure29 in this case is torun weighted least squares, where the weights are constructed using the observed probabilities.Again, due to random sampling and the error it generates, these observed probabilities can benegative, so this estimation is not possible. In order to address the heteroscedasticity problem Iestimate the equation by GLS (weighted least squares) using the number of individuals in thegroup as weights. To correct for further heteroscedasticity, I use White’s robust estimator.

28. Including a dummy for gender.29. SeeGreen(1997, p. 895) andMaddala(1997, p. 29).


4.3. IV estimates

4.3.1. Efficient Wald estimates. One obvious solution to correct for the bias in the GLScoefficient is to use instrumental variables (IV). Given that many instruments are available, twostage least squares (2SLS) would be the preferred estimation method. At the individual level, the2SLS model is

Di tcs = b + Eicsπ + Xicsβ + Wcsδ + γc + αs + εics

Eics = b + C Lcsπ + Xicsβ + Wcsδ + γc + αs + εics,

whereD is equal to one if the individual is deceased at timet . E is i ’s education (measured bycompleted years of education),X are other individual characteristics (including gender),Wcs isa set of characteristics of individuali ’s state-of-birth at age 14,γc is a set of cohort dummies,αs is a set of state-of-birth dummies,b is an intercept, andε is the error term. CL is the setof compulsory education laws that serve as instruments to identify the education equation. Thismodel can be estimated using the individual NHEFS data but not with the census.

Since the census data can be used only as grouped data, the Wald estimator is an alternativeestimator for the effect of education.Angrist (1991) showed that the Wald estimator for groupeddata is efficient and in fact equivalent to 2SLS using individual level data. In the case of manyexplanatory variables the efficient Wald estimator is found by GLS estimation of the followingequation:

Dtcrl = Ecrl π + γc + δr + εcrl , (4)

where Dcrl is the death rate for individuals born in cohortc in region r under compulsorylaw l , and Ecsl is the average education of individuals born in cohortc in region r undercompulsory lawl . The weights are given by the population in each group. In other words, Waldis estimated by grouping the data by gender/cohort/region-of-birth and compulsory educationlaw. This procedure is equivalent to 2SLS at the individual level, where gender, cohort dummiesand region dummies serve as their own instruments (since they are exogenous), and compulsoryeducation laws serve as instruments for education, the endogenous variable. The estimates arereferred to as the efficient Wald estimates.

Note that because compulsory education laws are defined at the state-of-birth and cohortlevel, I cannot control for both state-of-birth and cohort when using this estimator. This is adrawback of the Wald estimator, especially if one thinks that state-of-birth and the laws arecorrelated. In order to alleviate this problem, I control instead for region-of-birth. But region-of-birth may not be a good proxy for state-of-birth. Furthermore, other state-of-birth characteristics(Wcs) cannot be included in this specification.

4.3.2. Two-stage least squares with aggregate data.Alternatively, I can estimate the2SLS model at the data that has been aggregated at the state-of-birth/cohort and gender level.Estimation at the aggregate level results in less efficient estimates (seeGreen, 1997, pp. 433–434) but all the covariates (especially state-of-birth) can be included. Using the aggregate data2SLS is obtained by estimating the following model:

Dgcs = b + Egcsπ + Xgcsβ + Wcsδ + γc + αs + εgcs

Egcs = b1 + C Lcsπ + Xgcsβ + Wcsδ + γc + αs + εgcs

where nowDt gcs is the proportion of individuals who died in a given gender/cohort and state-of-birth, Egcs is the average education of that group andXgcs are other average characteristics.Again, the weights are given by the number of observations in each cell, and the excluded


instruments from the mortality equation are the compulsory education dummies,C Lcs. The firststage (estimation ofEgcs) will be shown as well in the results section.

4.3.3. Mixed two-stage least squares estimation.The census allows me to estimate thefirst stage using individual data. The intuition behind Mixed-2SLS is that it might be possibleto take advantage of this fact and gain efficiency (relative to the previous 2SLS) by estimatingthe first stage at the individual level (as done in the previous section) and then aggregating thedata by gender/cohort/state-of-birth (seeDhrymes and Lleras-Muney, 2001).30 Mixed-2SLS isobtained by estimating the following equation through weighted least squares:

Dgcs = b + Egcsπ + Xgcsβ + Wcsδ + γc + αs + εgcs.

Again Dgcs represents the proportion of individuals who died in a given gender/cohort andstate-of-birth group,Xgcs represents the average characteristics of the group, but now I include

Egcs, the average predicted education for that group from the first stage.31 The weights aregiven by the number of observations in each cell. The excluded instruments from the mortalityequation are the compulsory education dummies. The only difference between standard 2SLSwith aggregated data and Mixed-2SLS is in the predicted education term. 2SLS uses predictedaverage education whereas Mixed-2SLS uses average predicted education.

More formally, letH be the matrix that transforms the data into group means and weightseach group mean by the number of individuals in the group.X contains all the same variables asin the GLS estimation, but with education replaced by the predicted level of education from the

first stage regressionX =[E | X | γc | αs

]. Then the estimatorβMixed can be expressed as

βMixed = (X′H ′H X)−1X′H ′H D.

This procedure also results in consistent estimates. As usual the variance–covariance matrixneeds to be corrected.32

5. RESULTS

5.1. The effect of the laws on educational attainment

Before presenting the IV results, this section estimates the first stage, showing that the lawsare good predictors of educational attainment both at the individual and aggregate level. I alsoprovide additional evidence here that the laws are good instruments. These results will then beused in the two-stage (IV) estimations.

As preliminary evidence of the effect of these laws on education, I graph the averageeducation bychildcomfor the entire sample (Figure7) and by cohort, for every fifth cohort in thedata (Figure8). Additionally recall thatFigure6 shows average education for the cohorts beforeand after laws were increased. These graphs show that average education is higher for those instates where more education was compulsory, and higher within states, after compulsory lawsincreased. In order to add further controls, I turn now to regression analysis. Pooling individualdata from the 1960 and 1970 census, I estimate the following equation:

Eics = b + C Lcsπ + Xicsβ + Wcsδ + γc + αs + εics.

30. Dhrymes and Lleras-Muney(2001) compare 2SLS and Mixed-2SLS estimators. The question of whichestimator has lower variance turns out to be data dependent.

31. The expression for the first stage was given in the previous section.32. The standard errors were bootstrapped using 2000 replications.


0 4 5 6 7 8 9 10

8

7

9

10

11

12

Years of compulsory education

FIGURE 7

Average education level by years of compulsory education

1915

1920

1925

1930

1935

1939

Years of compulsory education

6·000 4 5 6 7 8 9 10

7·00

8·00

9·00

10·00

11·00

12·00

13·00

FIGURE 8

Average education level by compulsory education for selected cohorts

The dependent variable is the number of years of completed education for individuali of cohortc born in states. CL is a set of dummies for compulsory education laws in place in stateswhen the individual was 14,Xics are individual characteristics such as gender and region ofcurrent residence,Wcs is a set of characteristics of individuali ’s state-of-birth at age 14 (suchas manufacturing wages, expenditures in education,per capita doctors, etc.),γc are cohortdummies,αs are state-of-birth dummies. The regression also includes interactions betweenregion-of-birth and cohort, an intercept(b) and a dummy for 1970. I also estimate the modelby aggregating the data at the state-of-birth/cohort and gender level.

Table 2 shows the results. The first column estimates the relationship at the individuallevel including only state effects, cohort effects, a female dummy, and a set of dummies forthe laws. The coefficients are fairly robust to the addition of other controls (compare columns


1 and 2 ofTable2).33 The third column shows the results from estimating the equation usingthe data aggregated at the state-of-birth, cohort and gender level. The estimations show thatthe laws increased the educational attainment of individuals. As expected, all dummies for thelaws are positive and significant and they generally increase as the number of compulsory yearsincreases. I reject the null hypothesis that all the coefficients on the dummies are identical (F-statistic= 8·11, P-value 0·0000). However, it is not always the case that education increaseswith more demanding laws, for example in the aggregate estimation, the coefficient on 6 years ofcompulsory schooling is smaller than that for 5 years, and the coefficient for 10 years is smallerthan that for 9 years. This is unexpected, but it is most likely due to the fact that individuals inthe sample are very unequally distributed across categories: only about 3% of individuals are incategories 0, 4 and 5; 25% are in category 6, 56% in category 7, and about 15% are in categories8, 9 and 10. If I re-estimate the model using only these broader categories (as inAcemogluand Angrist, 1999), then the coefficients are monotonically increasing as expected.34 It is alsoimportant to remember that these laws were not necessarily binding for many individuals, as wediscussed in previous sections. Therefore the estimated effect for any one category is the averageof positive effects for those individuals in states where the laws were binding, a zero effect forstates where it was not.

Additional estimations suggest that these results are not due to any one level of compulsoryschooling: dropping all observations in any one category (for example dropping all individualsfor whom there was no required years of school,i.e. childcom= 0) does not diminish theexplanatory power of the other categories.35 Because the individual regressions only controlfor gender and no other individual-level covariates theR-squared in these regressions is low. Bycontrast theR-squared for the aggregate regression is quite high since the state level covariatescan explain much of the between state variation.

Columns 4 and 5 suggest that the overall implied increase in educational attainment due tochildcomis around 4·8% of a year. This estimate is similar to those reported byEisenberg(1988),Angrist and Krueger(1991) andAcemoglu and Angrist(1999). Also, the continuation schooldummy is positive.36 The last column reports the results using aggregate data and restrictingthe sample only to those states where laws were binding, and includes only three cohorts beforeand three cohorts after the increase in the law, so this regression uses the same sample that wasused to create the graphs inSection2. The effect for this restricted sample is also significant butsomewhat smaller(0·035), although standard errors are large.

Other coefficients are also positive and statistically significant in both individual andaggregate estimations. The results are not surprising forper cent urbansince cities had moreschools. The coefficient onper capita number of doctorsmight reflect the fact that healthierchildren obtain more schooling, but it could also be proxying for urbanicity: even though I controlfor per cent urban this variable is only available in decennial censuses and has been interpolated,whereas number of doctors exists every 2 years. Alternatively it could also proxy for wealth.Unexpectedly,per cent blackis positive and significant. This could reflect the fact that blacks

33. Inclusion of other variables, such as income, immigrant status of parents, has no impact on them. Also,regressions by region-of-birth or by gender yield similar results. SeeLleras-Muney(2002) for these results.

34. Relative to 5 or fewer years of compulsory schooling, the estimated coefficients (and standard errors) on thecategories are as follows:

6 years 0·058(0·040);7 years 0·155(0·042);8 years or more 0·182(0·046).

35. TheF-statistics of the joint significance of the laws are always significant no matter which categories aredropped from the sample. Results available upon request.

36. Continuation school is not significant in this sample, but previous work (seeLleras-Muney, 2002) showed thatthis law affected white males and individuals born in the north and south of the U.S. Therefore I include it.


TAB

LE2

Effe

cto

fco

mp

uls

ory

ed

uca

tion

law

so

ne

du

catio

n

Varia

bles

Indi

vidu

alIn

divi

dual

Agg

rega

teIn

divi

dual

Indi

vidu

alA

ggre

gate

data

data

data

data

data

rest

ricte

dsa

mpl

e

Dep

ende

ntE

duca

tion

varia

ble

Edu

catio

nY

ears

ofco

mpu

lsor

ysc

hool

ing

0·0

48∗∗

0·04

6∗∗

0·03

5∗∗∗

law

s(0

·007

)(0

·008

)(0

·015

)

Chi

ldco

mca

tego

ry4

0·347

∗∗

0·37

3∗∗

0·32

8∗∗

(0·0

75)

(0·0

87)

(0·1

12)

Chi

ldco

mca

tego

ry5

0·323

∗∗

0·28

8∗∗

0·34

2∗∗

(0·0

90)

(0·1

00)

(0·1

18)

Chi

ldco

mca

tego

ry6

0·274

∗∗

0·33

3∗∗

0·28

2∗∗

(0·0

69)

(0·0

85)

(0·1

09)

Chi

ldco

mca

tego

ry7

0·385

∗∗

0·44

1∗∗

0·38

2∗∗

(0·0

70)

(0·0

86)

(0·1

10)

Chi

ldco

mca

tego

ry8

0·416

∗∗

0·42

8∗∗

0·32

7∗∗

(0·0

75)

(0·0

88)

(0·1

13)

Chi

ldco

mca

tego

ry9

0·580

∗∗

0·54

6∗∗

0·47

7∗∗

(0·0

76)

(0·0

91)

(0·1

16)

Chi

ldco

mca

tego

ry10

0·325

∗∗

0·36

2∗∗

0·30

9∗∗

(0·0

80)

(0·0

94)

(0·1

21)

Con

tinua

tion

scho

olre

quire

d(=1)

0·02

70·

021

0·02

3(0

·026

)(0

·028

)(0

·030

)

Indi

vidu

alF

emal

e0·1

16∗∗

0·11

6∗∗

0·09

6∗∗

0·11

6∗∗

0·11

6∗∗

0·47

9∗∗∗

char

acte

ristic

s(0

·014

)(0

·014

)(0

·018

)(0

·014

)(0

·014

)(0

·055

)


TAB

LE2—

Con

tinue

d

Varia

bles

Indi

vidu

alIn

divi

dual

Agg

rega

teIn

divi

dual

Indi

vidu

alA

ggre

gate

data

data

data

data

data

rest

ricte

dsa

mpl

e

Sta

te-o

f-bi

rth

%U

rban

0·022

∗∗∗

0·02

7∗∗

0·02

0∗∗

char

acte

ristic

s(0

·004

)(0

·005

)(0

·004

)

%F

orei

gn−

0·00

50·

001

−0·

001

(0·0

08)

(0·0

10)

(0·0

08)

%B

lack

0·02

8∗∗

0·02

3∗∗

0·02

6∗∗

(0·0

09)

(0·0

10)

(0·0

08)

%E

mpl

oyed

inm

anuf

actu

ring

−0·

340

−1·

082

0·00

3(0

·523

)(0

·676

)(0

·465

)

Ann

ualm

anuf

actu

ring

wag

e−

2·0e

−06

1·2e

−06

−0·

000

(1·2

e−05

)(1

·6e−

05)

(0·0

00)

Valu

eof

farm

per

acre

−1·

3e−

04∗

−1·

3e−

04−

0·00

0∗

(7·7

e−05

)(9

·5e−

05)

(0·0

00)

Pe

rca

pita

num

ber

ofdo

ctor

s14

4·909

∗∗

173·

002∗

153·

477∗

(72·

921)

(89·

739)

(73·

481)

Pe

rca

pita

educ

atio

nex

pend

iture

s7

·3e−

04∗

2·8e

−04

0·00

1∗∗

(3·8

e−04

)(4

·3e−

04)

(0·0

00)

Num

ber

ofsc

hool

build

ings

per

sq.

−0·

277

−0·

279

0·40

1m

ile(0

·289

)(0

·334

)(0

·269

)

Reg

ion

ofbi

rth∗

coho

rtdu

mm

ies

No

Yes

Yes

No

Yes

No

N81

4,80

581

4,80

547

9281

4,80

581

4,80

554

0R

-squ

ared

0·081

10·0

815

0·882

0·08

0·08

0·88

F-s

tatis

ticon

inst

rum

ents

14·93∗

∗8·

67∗∗

4·69

∗∗

Par

tialR

-squ

ared

0·000

30·0

002

0·011

9

∗S

igni

fican

tat1

0%;∗∗

sign

ifica

ntat

5%.A

llre

gres

sion

sin

clud

ea

dum

my

fort

he19

70ce

nsus

,sta

te-o

f-bi

rth

dum

mie

s,co

hort

dum

mie

san

dan

inte

rcep

t.T

hest

anda

rder

rors

(inpa

rent

hese

s)ar

ecl

uste

red

atth

est

ate-

of-b

irth

and

coho

rtle

vel.

Chi

ldco

m=

wor

kpe

rmit

age−

entr

yag

e.C

hild

com=

0is

the

excl

uded

cate

gory

.Dat

aag

greg

ated

byge

nder

/coh

ort/s

tate

-of-

birt

h.


were moving to areas where whites obtain higher levels of schooling, but it is difficult to beconclusive on this point.

Before turning to the effect of education on mortality, I present evidence that the lawsare good instruments. At the bottom ofTable 2, I report the F-test of joint significanceof the laws; it shows that the laws are always jointly significant at the 5% level for bothspecifications. Additionally theF-statistic is greater than 5 (or very close to), which suggeststhat the instruments are strong given the number of instruments used. I also report the partialR-squared coefficient, another measure of the instruments’ strength.37 It has values of either0·0002 or 0·0119, which compare favourably to those reported byBoundet al. (1995).

It is also worth pointing out that the changes in the laws that took place during thisperiod appear to have been exogenous to individuals. Although different states might have haddifferent tastes for education, the regressions here include a very large set of controls (cohortdummies, state-of-birth dummies and region-of-birth∗cohort interactions are included) whichshould capture this effect. Also note that the addition of controls (compare columns 1 and 2 ofTable2) has little effect on the coefficients of the laws, suggesting that any excluded state-of-birth/cohort level variables are not correlated with the laws. Furthermore,Lleras-Muney(2002)presents evidence consistent with exogenous laws: her results suggest that the laws impactedonly the lower end of the distribution of education. She rejects the hypothesis that changes in thelaws during this period resulted from (rather than caused) increases in education.38

A final concern is that the laws must affect individual health only through their effect oneducation. There is no evidence that the laws included any clauses or restrictions that would haveaffected health independently. For example, there were no lunch programmes provided as partof school attendance. Also the states that led in education during this period (the prairie states)39

were not the same states that led in health (north-eastern states).40 But again, the controlsincluded here are meant to rule out this possibility. Finally, exogeneity tests are performed inthe IV estimation (see the next section).

Overall the results show that the laws did have an impact on educational achievement, andthat their predictive power is large, so they can be used as instruments. Therefore I turn now tothe question of the effect of education on mortality.

5.2. Least squares estimates of the effect of education on mortality

Although we have good reason to believe that GLS produces biased estimates, I report them hereas the benchmark for comparison with the IV results. Using the census, I estimate the GLS modeldescribed above. The results are in the first column ofTable3. The estimated coefficient of theeffect of education on the death rate is about−0·017. The coefficient is highly significant and isrobust to the inclusion of more controls.41

The validity of the aggregation procedure rests on the assumption that the aggregate datacan be understood as coming from unobserved individual data. It is important that this intuition

37. Boundet al. (1995) suggest that: 1—theF-statistic on the excluded instruments in the first stage should bestatistically significant and large (Staiger and Stock(1997) further suggest that a value of less than 5 could signal weakinstruments. This is a rule of thumb); 2—the partialR-square should be high.

38. The test, inspired byLandes and Solomon(1972), consists of matching individuals to the laws in place in theirstate-of-birth when they were 17, 18 and up to 26 years of age, when these laws should no longer have affected them.

39. SeeGoldin and Katz(1997).40. Starr’s (1982) book provides anecdotal evidence that the northern states lead in a variety of health aspects. My

own data support this conclusion. For example, the north had the highest number of doctorsper capitathroughout theperiod. And the number of doctorsper capitain the north did not decline from 1915 to 1939 but did decline in the rest ofthe country. The north also had the highest declines in infant mortality rates during this period. (Results available uponrequest.)

41. Results available upon request.


TABLE 3

Effect of education on mortality—least square results

Variables

Data Census NHEFS NHEFS NHEFSMethod WLS OLS Probit(a) WLSLevel(d) Aggregate(b) Individual Individual Aggregate(c)

Dependent 10-Year Died Died Death ratevariable death rate 75–85 75–85 75–85

Individual Education −0·017∗∗−0·011∗∗

−0·011∗∗−0·011∗∗

characteristics (0·004) (0·002) (0·002) (0·005)Female −0·074∗∗

−0·139∗∗−0·151∗∗

−0·136∗∗

(0·003) (0·014) (0·014) (0·029)

State-of-birth % Urban 1·0e−04 −0·002 −0·002 −0·002characteristics (9·4e−04) (0·005) (0·005) (0·005)

% Foreign −5·6e−04 0·004 0·013 0·004(0·002) (0·007) (0·009) (0·008)

% Black −0·002 −0·012 −0·011 −0·012(0·002) (0·008) (0·009) (0·009)

% Employed in manufacturing −0·071 −0·107 −0·095 −0·108(0·101) (0·590) (0·611) (0·633)

Annual manufacturing wage 7·4e−07 −2·2e−06 −8·1e−06 −2·2e−06(3·1e−06) (1·6e−05) (1·8e−05) (1·7e−05)

Value of farm per acre 2·7e−06 −8·1e−07 4·0e−05 −2·2e−07(1·7e−05) (8·6e−05) (8·9e−05) (9·3e−05)

Per capitanumber of doctors 0·242 −6·190 12·891 −6·730(13·891) (47·447) (42·636) (51·387)

Per capitaeducation expenditures 1·9e−05 1·6e−04 1·0e−04 1·6e−04(7·9e−05) (3·8e−04) (3·2e−04) (4·0e−04)

Number of school buildings per sq. mile −0·008 0·699∗∗ 0·778∗∗ 0·704∗

(0·062) (0·347) (0·367) (0·379)

N 4792 4554 4554 942R-squared 0·3575 0·1697 0·516

All regressions include 24 cohort dummies, 47 state-of-birth dummies, region-of-birth∗cohort, and an intercept.Standard errors (in parentheses) are clustered at the state-of-birth and cohort level. The census regressions alsoinclude a dummy for the 1970 census.(a) The reported coefficients are the mean marginal effects. The standard errors are calculated using the Delta method.(b) Data are aggregated at the cohort/gender and state-of-birth level.(c) Data aggregated at the cohort and state-of-birth level only.(d) All regressions at the aggregate level are weighted by the number of observations in the original cell.∗Significant at 10%;∗∗significant at 5%.

be confirmed, so I compare aggregate results from the census with those obtained with theNHEFS individual data. Using individual NHEFS data, I estimate a linear probability modeland a probit model, where the dependent variable is a dummy indicating whether or not theperson died between 1975 and 1985. Then I aggregate the NHEFS data and again estimate thesame linear model estimated with the census data. Because of the small number of observationsin the NHEFS aggregating by gender, state-of-birth and cohort results in very few observationsper cell, so I aggregate only by state-of-birth and cohort. The results are shown inTable3.

Comparing the results from LS regressions from the census with results from the NHEFSshows that the census data give estimates of the effect of education that are very similar to thoseobtained using the NHEFS aggregated data, which in turn are similar to those obtained at the


individual level, using either LS or probit estimations. These results suggest that sampling (andthe measurement error it generates) does not significantly affect the estimates for education,that there is no aggregation bias and that the linear model is a good approximation of theeducation–death rate relationship. The comparison is also useful in terms of interpretation: a−0·011 coefficient for education means that increasing the education of a given cell by 1 yearlowers its death rate by 1·1 percentage points. This coefficient also implies that increasing anindividual’s education by 1 year will lower his probability of dying between 1960 and 1970 (orbetween 1970 and 1980) by 1·2 percentage points. This latter interpretation is more intuitive anduseful. Note again that the OLS effect is quite large: at the mean, this result implies that a 10%increase in education lowers mortality by about 11%, therefore an elasticity of about−1.

The only other significant coefficient in these equations is the effect of thenumber ofschool buildings per square milewhich increasesmortality (this is also the case in the followingIV estimations). It is unclear why this would be the case unless again this variable capturesurbanization.

5.3. IV estimates of the effect of education on mortality

The first column inTable4 presents the 2SLS results using the NHEFS. This estimation is doneat the individual level and using standard 2SLS. The estimate is positive (the effect of educationis about−0·017) but not significant: because this sample is small, the first stage estimation42 ispoor. Nonetheless, although the standard errors are high, the estimates from this sample are alsolarger than the GLS estimates obtained from the same data(−0·011).

The second column shows the results from the Wald estimation. The Wald estimate of theeffect of education is about−0·037 and significant at the 5% level. The third column presentsthe results of 2SLS estimation using aggregated data at the gender/state-of-birth and cohort level.The effect of education is about−0·051 and significant at the 5% level. The Mixed-2SLS results(last column) show that the coefficient on education is approximately−0·061 and is significantat the 5% level. Overall the results suggest that increasing education by 1 additional year lowersthe 10-year death rate by at least 3·6 percentage points.43

For the last two estimators I perform a test of overidentifying restrictions. Theχ2 statisticfor the aggregate 2SLS model is 2·84 and 1·49 for the Mixed-2SLS model. This statistic teststhe hypothesis that the model is well specified. It is calculated as the sample size times theR2

from a regression of the residuals from the second stage on all exogenous variables, includingthe instruments. In both cases the overidentifying restrictions are not rejected at a 5% level(critical value 14·06). This test in conjunction with earlier results from the first stage suggeststhat compulsory education laws are legitimate instruments.

Additional checks are presented inTable 5. As a last attempt to address the potentialendogeneity of the laws, I repeat the estimations above using a larger set of instruments thatinclude compulsory attendance and the interactions of quarter of birth and the laws (quarter ofbirth is not used as an instrument, it is included in both first and second stages). Presumably theseindividual-level instruments will increase the efficiency of the estimates, and they are perhapsless likely to be endogenous.44 The results (Panel A) are identical to those presented above. Theresults are also very similar if only the interactions between the laws and quarter of birth are

42. Results available upon request. Only two of the dummies for compulsory education laws were significant atthe 10% level, and the set of dummies was jointly insignificant.

43. Estimates by region are comparable in size to those presented here except that they are generally not significant.44. Note however that the use of these instruments might be questionable (see papers in footnote 10). AlsoLleras-

Muney(2002) shows, for example, that the laws affected whites but not blacks. However, quarter of birth does appear toaffect blacks’ educational attainment. This again raises the issue of whether quarter of birth has an independent effect oneducation unrelated to compulsory attendance laws.


TABLE 4

Effect of education on mortality—IV results

Variables

Data NHEFS(b) Census(a)(c) Census(a)(b)(c) Census(a)(b)(c)

Method 2SLS Wald 2SLS Mixed-2SLSLevel Individual Aggregate Aggregate Aggregate

Dependent Died 10-Year 10-Year 10-Yearvariable 1975–1985 death rate death rate death rate

Individual Education −0·017 −0·037∗∗−0·051∗∗

−0·061∗∗

characteristics (0·058) (0·006) (0·026) (0·025)1970 Dummy 0·003 0·003 0·007

(0·004) (0·005) (0·006)Female −0·137∗∗

−0·071∗∗−0·071∗∗

−0·068∗∗

(0·027) (0·004) (0·004) (0·004)

State-of-birth % Urban −0·002 0·001 0·001characteristics (0·006) (0·001) (0·001)

% Foreign 0·004 −0·0001 0·000(0·007) (0·002) (0·000)

% Black −0·012 −0·0009 −0·0005(0·009) (0·002) (0·0020)

% Employed in manufacturing −0·115 −0·110 −0·074(0·604) (0·108) (0·139)

Annual manufacturing wage 0·000 0·000 0·000(0·000) (0·000) (0·000)

Value of farm per acre 0·000 0·000 0·000(0·000) (0·000) (0·000)

Per capitanumber of doctors −2·178 7·926 8·59(64·968) (15·059) (16·47)

Per capitaeducation expenditures 0·000 0·000 0·000(0·000) (0·000) (0·000)

Number of school buildings per sq. mile 0·685∗ −0·005 −0·003(0·377) (0·065) (0·072)

State-of-birth dummies Yes No Yes YesRegion-of-birth dummies No Yes No NoCohort dummies Yes Yes Yes YesRegion-of-birth∗cohort Yes No Yes Yes

N 4554 1396 4792 4792

All regressions include an intercept.(a) Regressions are weighted by the number of observations in the original cell.(b) Standard errors (in parentheses) are clustered at the state-of-birth and cohort level and have been corrected in thesecond stage.(c) Note: Mixed-2SLS and aggregate 2SLS use data aggregated at the gender/cohort/state-of-birth level. Wald uses dataaggregated at the gender/cohort/region-of-birth/compulsory education laws level.∗Significant at 10%;∗∗significant at 5%.

used as instruments, and quarter of birth as well as compulsory schooling laws are included ascontrols in both the first and second stages.45 This again suggests that the instruments are notendogenous.

Since, it is well known that there exist persistent differences in mortality rates by genderI reproduce results by gender in Panel B. The coefficient on education is somewhat smaller for

45. Results available upon request.


TABLE 5

Additional estimations

Dependent variable 10-Year death rate 2SLS Mixed-2SLS

Panel A Quarter of birth, laws andinteractions used as instrumentsEducation −0·072∗∗

−0·065∗∗

(0·026) (0·025)

Panel B By genderMales −0·046 −0·076

(0·036) (0·037)Females −0·045 −0·051

(0·037) (0·035)

Panel C Exclude ages 40, 50 and 60Education −0·047∗ −0·062∗∗

(0·027) (0·024)

Panel D Interact cohort dummies and1970 dummyEducation −0·054∗∗

−0·065∗∗

(0·026) (0·025)

Panel E By regionNorth −0·007 −0·078

(0·059) (0·111)South −0·049 −0·071∗∗

(0·043) (0·031)West −0·034 −0·054

(0·045) (0·090)Midwest −0·023 −0·032

(0·072) (0·089)

Note: All coefficients come from separate estimations that contain the same controls as inprevious tables.∗Significant at 10%;∗∗significant at 5%.

females than for males, confirming the findings in the literature that the effect of education islarger for males. These results also suggest that World Wars I and II did not result in significantselection bias for men.

Panels C and D address concerns related to the mortality data. Panel C shows the resultsexcluding ages 40, 50 and 60 since the data showed evidence of age heaping. This is a potentialproblem if age heaping is correlated with education. Panel D includes interactions between cohortdummies and the 1970 census dummy. The results are unaffected by these modifications.

Finally in Panel E I repeat the estimations by region of birth. Except for the North wherethe 2SLS is 0, these are quantitatively similar to all the results presented before. So the previousestimates are not purely based on differences between regions.

5.4. Reduced form results

Finally Table 6 presents the results from the reduced form equations,i.e. the direct effect ofthe laws on mortality. These results are the numerical counterparts of the graphs presented inSection3, except that I use the number of years of compulsory school rather than dummies forthe cohorts before and after. By regressing mortality rates on compulsory schooling laws, state,and cohort dummies, and additional state and time varying controls, we estimate the effect ofincreasing compulsory schooling by one more year within states over time. This estimate is moreinformative than an estimate of the average effect of any increase in the law (what the regressiondiscontinuity estimates), since laws did not always change by 1 year.


TABLE 6

Effect of increases in years of compulsory school on10-year mortality rates—census data

Full Drop states with no Restrictedchanges sample

(1) (2) (3) (4) (5)

Years of compulsory school −0·002∗∗−0·003∗∗∗

−0·002∗∗−0·003∗∗∗

−0·0036(0·001) (0·001) (0·001) (0·001) (0·0032)

1970 Dummy −0·003 −0·003 −0·004 −0·004 0·053∗∗∗

(0·004) (0·004) (0·005) (0·005) (0·014)Female −0·076∗∗∗

−0·076∗∗∗−0·076∗∗∗

−0·076∗∗∗−0·114∗∗∗

(0·003) (0·003) (0·003) (0·003) (0·009)

% Urban −1·1e−04 8·2e−05(9·3e−04) (0·001)

% Foreign −4·1e−04 −0·002(0·002) (0·002)

% Black −0·002 −0·003(0·002) (0·002)

% Employed in manufacturing −0·079 −0·096(0·104) (0·105)

Annual manufacturing wage −1·1e−04 1·1e−06(9·3e−04) (3·2e−06)

Value of farm per acre −4·1e−04 −1·4e−05(0·002) (2·0e−05)

Per capitanumber of doctors −0·002 13·879(0·002) (13·626)

Per capitaeducation −0·079 −7·4e−06expenditures (0·104) (0·810)

Number of school buildings 7·2e−07 0·003per sq. mile (3·1e−06) (0·075)

Cohort dummies Yes Yes Yes Yes YesRegion-of-birth∗cohort No Yes No Yes No

dummiesState-of-birth dummies Yes Yes Yes Yes Yes

R-squared 0·35 0·36 0·35 0·35 0·41N 4792 4792 3696 3696 540

All regressions include an intercept. Regressions also include dummies for cohorts before the change in the law.Regressions are weighted by the number of observations in the original cell. Standard errors (in parentheses) areclustered at the state-of-birth and cohort. Census data have been aggregated at the census/gender/cohort/state-of-birthlevel. See the text for an explanation of how the sample was selected.∗Significant at 10%;∗∗significant at 5%.

The first two columns present results using the entire census sample, the second column addsmore controls. Both coefficients are significant and they imply that one more year of compulsoryschooling decreases mortality by 0·003 or about 3% at the mean. In the next two columns I dropstates without changes in compulsory schooling throughout the period. The effect of compulsoryschooling remains significant and it is identical to the previous estimates. Finally in the lastcolumn I present results using the restricted sample that keeps only states where laws werebinding and uses only 3 cohorts before and after the change in compulsory school. Althoughinsignificant, the coefficients are qualitatively very similar to those in columns 1–4.

These results are consistent with previous estimations: if the effect of childcom on educationis about 5%, and the effect of education on mortality is about 6%, then the direct effect of thelaws on mortality should be about 0·3%, which is approximately what the reduced form resultsin Table6 show.


6. DISCUSSION

The previous sections presented different estimates of the effect of education on mortality. Threedifferent estimators, using two different data-sets and three different levels of aggregation, wereused. Although each estimate has weaknesses, all estimates point to the same conclusion: theeffect of education is causal and in fact larger than OLS suggests. Also note that there is asignificant direct effect of compulsory schooling laws on mortality during adulthood. Given thisvariety of estimates, this result is very robust. The result is surprising for two reasons. The first isthat the IV estimates are larger than the LS estimates. The second is that the effect of educationis quite large. In this section I discuss these two issues.

6.0.1. Larger IV estimates. In all the IV estimations presented here, the effect ofeducation is much larger than the LS estimates suggest. The Mixed-2SLS estimates suggestthe effect is as large as−0·058, whereas Wald estimates imply a coefficient of about−0·036.At first, this could seem to be a surprising result: thea priori expectation was that LS estimateswould be too large. However, there are two important points to note.

First note that the standard errors in the IV estimates are large. Even though the IV estimatesare significantly different from 0, it is unclear whether they are statistically different from theOLS estimates. To test whether the IV and OLS estimates are different, one can perform aDurbin–Wu–Hausman test. TheF-statistic for this test is 0·05 (P-value 0·82). Therefore I cannotreject the null hypothesis that OLS and IV are the same.

Note that an implication of this test is that education is in fact exogenous, since it suggeststhat the IV estimates are no different from the OLS estimates in a statistical sense. From thistest, I conclude that education appears to have a large causal effect on mortality. The larger IVestimates are therefore of no particular concern.

However, if one still thought that education was endogenous, then the most plausibleexplanation for the difference between the IV and the OLS estimates in this case is related to thechoice of instrument.46 Under the assumption that different individuals face different returns toeducation due to unobserved characteristics, IV estimates reflect the marginal rate of return of thegroup affected by the instrument (Angrist, Imbens and Rubin, 1996). In this case IV capture thereturns to those affected by the compulsory schooling laws. If I estimate a regression of mortalityas a function of education and education squared, where both are instrumented with compulsoryschooling laws, I do indeed find some evidence that the relationship is convex. However I donot place too much weight on these results given that (a) under the hypothesis that educationis endogenous, the instruments can only identify a non-linear relation for those affected by thelaws, rather than for the population at large, and (b) education does not appear to be endogenous!

6.0.2. What is the effect of education on health? The second issue is that the effect ofeducation is quite large, and it is important to understand why. I categorize the potential effectsof education into two categories: direct and indirect effects.

First note that if the effect of compulsory schooling was to remove kids from unhealthy jobsand bring them to the classroom, then the effect of education cannot be distinguished from theeffect of not working.

46. Another explanation is that the omitted variable bias is smaller than the bias that results from measurementerror in education (Card, 1995). The health literature has not been concerned with this potential problem although there isevidence of measurement error in education. If the measurement error is random, then the IV estimate will be larger thanthe OLS estimate. Larger IV returns can also be explained if there exist health externalities from education for exampleif average education affects individual health. However, note that the fact that individual and aggregate estimations usingthe NHEFS result in similar effects for education suggests that externalities are not the main reason for larger IV.


Among the direct effects, education provides individuals with critical thinking skills thatare useful in the production of health (Grossman’s hypothesis). There is some evidence to thiseffect. For example,Goldman and Smith(2001) find that the more educated are more likely tocomply with treatments for diabetes and Aids.Goldman and Lakdawalla(2001) suggest thatthe more educated are better able to manage chronic conditions. These two papers suggest thateducation matters when treatments are complex and there is scope for learning by doing. Thesemechanisms have also been documented byRosenzweig and Schultz(1989), who comparedsuccess rates of different contraception methods for women with different levels of education:they find that success rates are identical for all women for “easy” methods such as the pill, butthe rhythm method is only effective for educated women.

If this is the case, then the interaction of education with a variety of factors might berelevant. For example, although access to information alone cannot explain health differencesacross education groups (Kenkel, 1991), information available to the more educated will resultin greater benefits for them if they can use the information better. For example, when analysingthe effects of the 1964 Surgeon General Report,Meara(2001) concluded that “the responseto knowledge plays a more important role than knowledge itself in creating differential healthbehaviour”.

Another possibility is that the more educated might be more likely to adopt and use newmedical technologies.47 Since the rate of medical innovation dramatically increased in thelast century, especially for particular diseases such as heart disease (Cutler, McClellan andNewhouse, 1998), it is reasonable to think that the more educated were able to capture veryhigh returns during this period.Lleras-Muney and Lichtenberg(2002), for example, show thatthe more educated are more likely to use newer drugs.

There are a few indirect mechanisms through which education might affect health whichare also consistent with the results reported in this paper.

Education gives you access to a higher income and different types of jobs, both of whichaffect health. For example, only high school graduates in the first half of the century hadaccess to white collar jobs, which provided healthier work environments than manufacturingor agriculture. Controlling for income (or occupation) does not change the results in this paper.48

But, since income is endogenous, it is not possible (given that I have no instruments for income)to distinguish the direct effect of education on health from its indirect effect through income. Thesame is true for occupation. However, standard results suggest that the returns to education areabout 10% and that the elasticity of mortality with respect to income is about−0·3.49 If the soleeffect of education is through income, one more year of education should decrease mortality by0·003 (for average mortality of 0·11),50 which is a much smaller effect than what was estimatedhere. With respect to occupation, I simply note here that since the effect of education is similar

47. SeeNelson and Phelps(1966).48. Results available upon request.49. Deaton and Paxson(1999).50. The calculation is performed as follows:Deaton and Paxson(1999) estimate that

log

(d

1 − d

)= −0·3 log(inc).

Studies in labour have found thatlog(inc) = 0·1ed

so by replacing I find that

log

(d

1 − d

)= −0·03ed

the marginal effect is given by∂d

∂ed= −0·03d(1 − d).

Evaluated at the mean (i.e. for d = 0·11) this effect is about−0·003.


for men and women, it would appear that occupation is not the only channel through whicheducation affects health.

Finally note that the cognitive psychology literature has documented that lack of educationis correlated with stress, depression and hostility, all of which have been shown to adverselyaffect health (Adler et al., 1994).

The results in this paper do not imply that time preferences do not affect health andeducation choices nor that there is no reverse causality from health to education. They simplyshow that there is a causal effect of education on health, and that this effect is not due to timepreferences. However, asBecker and Mulligan(1997) argue, education could lower the discountrate, making people more patient. This is yet another indirect mechanism that could explain myresults.

7. CONCLUSION

This paper has shown that there is a large causal effect of education on mortality. While GLSestimates suggest that an additional year of education lowers the probability of dying in thenext 10 years by approximately 1·3 percentage points, my results from the IV estimation showthat the effect is perhaps much larger: at least 3·6 percentage points. Moreover there is a directeffect of compulsory schooling laws on mortality during adulthood: one more year of compulsoryschooling decreased mortality after age 35 by about 3%.

However, it is worth noting that the OLS and the IV estimates are not statistically different.So, contrary to expectations, I find no evidence that education is endogenous in the mortalityequation.

To better understand the impact of education, I calculate how this effect translates into lifeexpectancy gains. I find that in 1960, one more year of education increased life expectancy at age35 by as much as 1·7 years (using the OLS estimate). This is a very large increase.

A few notes of caution on how to interpret these results for public policy purposes arenecessary. First, in order to make policy recommendations, we need to know more about thespecific mechanisms by which education affects health. This paper analyses the effects ofincreasing education from relatively low initial levels. It is unclear what the effects would beat higher initial levels of education. The average education level for white Americans bornin 1901 was at most 8·87 years.51 Today many developing countries, including most LatinAmerican countries, have average levels of education that are similar. This paper implies thatmore aggressive education policies could dramatically increase adult longevity in such countries.But cost benefit analysis of such policies is extremely complex, since, for example, we do notknow what the cost of increasing education would be, or its effectiveness. Questions such asthese are beyond the scope of this paper. But the results presented here suggest that the benefitsof education are large enough that we need to consider education policies more seriously as ameans to increase health, especially in the light of the fact that other factors, such as expenditureson health, have not been proven to be very effective.

This evidence that education increases life expectancy implies that the returns to education,measured only in terms of earnings increases, substantially underestimate the true returns toeducation. In view of the large magnitude of the effect of education on health, it is clear that moreattention needs to be devoted to the pathways of influence. Existing models of the relationshipbetween education and health are very imprecise about the mechanisms through which educationoperates on health.

51. This is the average education level of that cohort in 1960. Data for the entire population in 1901 do not existfor the U.S., but the average was probably much lower.


APPENDIX A

Years of compulsory schooling

Gra

phs

by S

tate

Yea

r

Ala

bam

a

010

Ariz

ona

Ark

ansa

sC

alifo

rnia

Col

orad

oC

onne

ctic

utD

elaw

are

Flo

rida

010

Geo

rgia

Idah

oIll

inoi

sIn

dian

aIo

wa

Kan

sas

Ken

tuck

y

010

Loui

sian

aM

aine

Mar

ylan

dM

assa

chus

etts

Mic

higa

nM

inne

sota

Mis

siss

ippi

010

Mis

sour

iM

onta

naN

ebra

ska

Nev

ada

New

Ham

pshi

reN

ew J

erse

y

New

Mex

ico

010

New

Yor

kN

orth

Car

olin

aN

orth

Dak

ota

Ohi

oO

klah

oma

Ore

gon

Pen

nsyl

vani

a

010

Rho

de Is

land

Sou

th C

arol

ina

Sou

th D

akot

aT

enne

ssee

Tex

asU

tah

1539

Ver

mon

t

1539

010

Virg

inia

1539

Was

hing

ton

1539

Wes

t Virg

inia

1539

Wis

cons

in

1539

Wyo

min

g

1539


APPENDIX B. CHANGES IN COMPULSORY SCHOOL IN EVERY STATE AND %POTENTIALLY AFFECTED BY THE CHANGE

TABLE B1

State Year when Years of Previous law % in previous % compliant % affected aslaw changed compulsory cohort at the in previous a fraction of

schooling margin cohort % compliant

Alabama 16 4 0 0·20 0·80 0·26Alabama 21 6 4 0·14 0·88 0·16Alabama 35 7 6 0·08 0·83 0·10Arkansas 18 7 6 0·08 0·82 0·10California 18 6 8California 21 7 6 0·02 0·96 0·02California 28 6 7California 29 7 6California 35 6 7California 36 7 6Connecticut 36 9 7 0·09 0·97 0·10Florida 16 6 0 0·34 1·34 0·25Florida 18 0 6Florida 21 7 0 0·33 1·00 0·33Georgia 16 6 0 0·42 1·42 0·29Georgia 18 4 6Georgia 21 6 4 0·16 0·85 0·19Georgia 39 7 6 0·06 0·85 0·07Idaho 18 8 6 0·15 0·95 0·15Idaho 21 6 8Idaho 39 7 6Kansas 23 7 6 0·02 0·98 0·02Louisiana 16 0 6Louisiana 21 6 0 0·36 1·00 0·36Louisiana 23 7 6 0·06 0·63 0·09Maine 21 8 7 0·09 0·99 0·09Maryland 24 7 6 0·10 0·81 0·12Massachusetts 39 9 7 0.09 0·96 0·10Michigan 18 7 8Michigan 24 8 7 0·06 0·95 0·07Mississippi 18 5 0 0·20 1·00 0·20Mississippi 21 7 5 0·16 0·82 0·20Missouri 21 7 6 0·05 0·90 0·05Montana 21 8 6 0·06 1·00 0·06Montana 28 6 8Montana 29 8 6Montana 35 6 8Montana 36 8 6Nevada 24 7 6New Mexico 21 8 0 0·00 0·56 0·00New York 21 7 6 0·03 0·97 0·03New York 36 9 7 0·10 0·98 0·10North Carolina 18 4 5North Carolina 21 6 4 0·18 0·90 0·20North Carolina 24 7 6 0·09 0·76 0·12North Carolina 37 9 7 0·19 0·78 0·24North Dakota 18 7 6 0·04 0·96 0·04Ohio 21 8 7 0·06 0·94 0·06Ohio 24 10 8 0·29 0·91 0·32Oklahoma 28 8 6Oklahoma 29 6 8Oklahoma 35 8 6


TABLE B1—Continued

State Year when Years of Previous law % in previous % compliant % affected aslaw changed compulsory cohort at the in previous a fraction of

schooling margin cohort % compliant

Oklahoma 36 6 8Oklahoma 37 7 6 0·03 0·96 0·03Oregon 30 7 5 0·02 0·70 0·03Oregon 39 6 7Pennsylvania 36 8 6 0·05 0·98 0·05Rhode Island 18 6 7Rhode Island 21 7 6 0·07 0·99 0·07Rhode Island 24 8 7 0·07 0·88 0·08Rhode Island 36 9 8 0·14 0·85 0·16South Carolina 16 6 0 0·37 1·00 0·37South Carolina 37 8 6 0·16 0·83 0·19South Carolina 39 9 8 0·09 0·67 0·14South Dakota 24 6 7Tennessee 21 7 6 0·05 0·80 0·06Tennessee 39 6 7Texas 16 4 0 0·11 1·00 0·11Texas 21 7 4 0·16 0·91 0·17Texas 35 4 7Texas 36 7 4Texas 39 8 7 0·06 0·84 0·07Utah 18 5 6Utah 21 10 5 0·27 0·97 0·28Utah 28 6 10Utah 36 8 6 0·01 0·98 0·01Vermont 18 7 6 0·04 0·98 0·04Vermont 21 6 7Virginia 18 6 4 0·14 0·86 0·17Virginia 28 7 6 0·10 0·82 0·13Washington 18 4 6Washington 21 6 4 0·02 1·00 0·02West Virginia 21 7 6 0·03 0·84 0·04West Virginia 39 9 7 0·22 0·94 0·23Wisconsin 36 9 7 0·22 0·97 0·23Wyoming 21 9 0 0·11 1·00 0·11Wyoming 28 7 9

Highlighted states are states where laws were unlikely to be effective because changes were in place only for a year.Lines in bold correspond to years when the years of compulsory schooling declined.

APPENDIX C. REGRESSION DISCONTINUITY RESULTS

TABLE C1

Samples All states with Restricted samplechanges binding changes(1)

Cohort before changeexcluded

10-year death rate3 Cohorts before 0·010 −0·003

(0·49) (0·11)2 Cohorts before 0·000 −0·022

(0·02) (0·74)


TABLE C1—Continued

Samples All states with Restricted samplechanges binding changes(1)

Cohorts during change −0·014 −0·030(0·68) (1·27)

1 Cohort after −0·010 −0·030(0·48) (1·26)

2 Cohorts after −0·016 −0·027(0·80) (1·05)

3 Cohorts after −0·029 −0·042(1·45) (1·74)

Observations 1632 540R-squared 0·01 0·01

Mean education3 Cohorts before −0·086 0·018

(0·31) (0·08)2 Cohorts before −0·010 0·066

(0·04) (0·30)Cohorts during change 0·095 0·121

(0·35) (0·59)1 Cohort after 0·035 0·112

(0·12) (0·52)2 Cohorts after 0·132 0·239

(0·47) (1·16)3 Cohorts after 0·174 0·135

(0·58) (0·60)

Observations 1632 540R-squared 0·00 0·00

Robustt statistics in parentheses.(1) See text for definition of this sample.∗Significant at 5%;∗∗significant at 1%.

Acknowledgements. I would like to thank Ann Bartel, Francisco Ciocchini, Ana Corbacho, Rajeev Dehejia,Phoebus Dhrymes, William Gentry, Bo Honore, Kenneth Leonard, Manuel Lobato, Christina Paxson, AlexanderPeterhansl, Nachum Sicherman, and the seminar participants at the Federal Reserve Board, Harvard University, MichiganState University, MIT, Princeton University, University of Montreal, UNC-Greensboro, UC Berkeley, UC Davis, UCIrvine, University of Illinois at Urbana Champaign for their comments and suggestions. I would also like to thankHidehiko Ichimura, Bernard Salanie and two anonymous referees for their very helpful suggestions. I am especiallygrateful to my advisor Sherry Glied who fully supported me throughout this project. All errors are mine. This researchwas partially funded by Columbia University’s Public Policy Consortium, and the Bradley Foundation.

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