EducationforGrowth: WhyandForWhom? 2000_kruegerlindahl.pdf · 5 The German figures are from Krueger and Jorn-Steffen Pischke (1995). The American and Swedish figures are based on

Journal of Economic LiteratureVol. XXXIX (December 2001) pp. 1101–1136

Krueger and Lindahl: Education for GrowthJournal of Economic Literature, Vol. XXXIX (December 2001)

Education for Growth:Why and For Whom?

ALAN B. KRUEGER and MIKAEL LINDAHL1

1. Introduction

INTEREST IN the rate of return to in-vestment in education has been

sparked by two independent develop-ments in economic research in the1990s. On the one hand, the micro laborliterature has produced several new esti-mates of the monetary return to school-ing that exploit natural experiments inwhich variability in workers’ schoolingattainment was generated by some ex-ogenous and arguably random force, suchas quirks in compulsory schooling laws orstudents’ proximity to a college. On theother hand, the macro growth literaturehas investigated whether the level ofschooling in a cross-section of countriesis related to the countries’ subsequent

GDP growth rate. This paper summa-rizes and tries to reconcile these twodisparate but related lines of research.

The next section reviews the theoreti-cal and empirical foundations of the Min-cerian human capital earnings function.Our survey of the literature indicatesthat Jacob Mincer’s (1974) formulationof the log-linear earnings-education re-lationship fits the data rather well. Eachadditional year of schooling appears toraise earnings by about 10 percent inthe United States, although the rate ofreturn to education varies over time aswell as across countries. There is sur-prisingly little evidence that omittedvariables (e.g., inherent ability) thatmight be correlated with earnings andeducation cause simple OLS estimatesof wage equations to significantly over-state the return to education. Indeed,consistent with Zvi Griliches’s (1977)conclusion, much of the modern lit-erature finds that the upward “abilitybias” is of about the same order ofmagnitude as the downward bias causedby measurement error in educationalattainment.

Section 3 considers the macro growthliterature. First, we review the majortheoretical contributions to the litera-ture on growth and education. Then werelate the Mincerian wage equation tothe empirical macro growth model. The

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1 Krueger: Princeton University and NBER.Lindahl: Stockholm University. We thank AndersBjörklund, David Card, Angus Deaton, RichardFreeman, Zvi Griliches, Gene Grossman, BertilHolmlund, Larry Katz, Torsten Persson, NedPhelps, Kjetil Storesletten, Thijs van Rens, threeanonymous referees, and seminar participants atthe University of California at Berkeley, the Lon-don School of Economics, MIT, Princeton Uni-versity, University of Texas at Austin, UppsalaUniversity, IUI, FIEF, SOFI, the NorwegianConference on Economic Growth, and the Tinber-gen Institute for helpful discussions, and PeterSkogman, Mark Spiegel, and Bob Topel for pro-viding data. Krueger thanks the Princeton Univer-sity Industrial Relations Section for financial sup-port; Lindahl thanks the Swedish Council forResearch in the Humanities and Social Science forfinancial support.

Mincer model implies that the changein a country’s average level of schoolingshould be the key determinant of in-come growth. The empirical macrogrowth literature, by contrast, typicallyspecifies growth as a function of theinitial level of education. Moreover, weshow that if the return to educationchanges over time (e.g., because ofexogenous skill-biased technologicalchange), the macro growth models areunidentified. Much of the empiricalgrowth literature has eschewed theMincer model because studies such asJess Benhabib and Mark Spiegel (1994)find that the change in education is nota determinant of economic growth.2 Wepresent evidence suggesting, however,that Benhabib and Spiegel’s finding thatincreases in education are unrelated toeconomic growth results because thereis virtually no signal in the educationdata they use, conditional on the growthof capital.

Until recently (e.g., Lant Pritchett1997) the macro growth literature hasdevoted only cursory attention to poten-tial problems caused by measurementerrors in education. Despite their aggre-gate nature, available data on averageschooling levels across countries arepoorly measured, in large part becausethey are often derived from enrollmentflows. The reliability of country-leveleducation data is no higher than thereliability of individual-level educationdata. For example, the correlation be-tween Robert Barro and Jong-WhaLee’s (1993) and George Kyriacou’s (1991)measures of average education across68 countries in 1985 is 0.86, and thecorrelation between the change inschooling between 1965 and 1985 from

these two sources is only 0.34. Addi-tional estimates of the reliability ofcountry-level education data based onour analysis of comparable micro datafrom the World Values Survey for 34countries suggests that measurementerror is particularly prevalent for secon-dary and higher schooling. The measure-ment errors in schooling are positivelycorrelated over time, but not as highlycorrelated as true years of schooling.Consequently, we find that measure-ment errors in education severely at-tenuate estimates of the effect of thechange in schooling on GDP growth.Nonetheless, we show that measure-ment errors in schooling are unlikely tocause a spurious positive association be-tween the initial level of schooling andGDP growth across countries, condi-tional on the change in education. Thus,like Norman Gemmell (1996) and RobertTopel (1999), our analysis suggests thatboth the change and initial level of edu-cation are positively correlated witheconomic growth.

Finally, we explore whether the sig-nificant effect of the initial level ofschooling on growth continues to holdif we estimate a variable-coefficientmodel that allows the coefficient oneducation to vary across countries (asis found in the microeconometric esti-mates of the return to schooling), andif we relax the linearity assumption ofthe initial level of education. Theseextensions indicate that the positiveeffect of the initial level of educationon economic growth is sensitive to eco-nometric restrictions that are rejectedby the data.

2. Microeconomic Analysis of the Returnto Education

Since at least the beginning of thecentury, economists and sociologistshave sought to estimate the economic

2 There are also notable exceptions that haveembraced the Mincer model, such as Mark Bilsand Peter Klenow (1998), Robert Hall and CharlesJones (1999), and Klenow and Andrés Rodriguez-Clare (1997).

1102 Journal of Economic Literature, Vol. XXXIX (December 2001)

rewards individuals and society gainfrom completing higher levels ofschooling.3 It has long been recog-nized that workers who attended schoollonger may possess other characteristicsthat would lead them to earn higherwages irrespective of their level of edu-cation. If these other characteristics arenot accounted for, then simple compari-sons of earnings across individuals withdifferent levels of schooling would over-state the return to education. Early at-tempts to control for this “ability bias”included the analysis of data on siblingsto difference-out unobserved familycharacteristics (e.g., Donald Gorseline1932), and regression analyses whichincluded as control variables observedcharacteristics such as IQ and parentaleducation (e.g., Griliches and WilliamMason 1972). This literature is thor-oughly surveyed in Griliches (1977), Sher-win Rosen (1977), Robert Willis (1986),and David Card (1999). We briefly re-view evidence on the Mincerian earn-ings equation, emphasizing recent stud-ies that exploit exogenous variations ineducation in their estimation.

2.1 The Mincerian Wage Equation

Mincer (1974) showed that if the onlycost of attending school an additionalyear is the opportunity cost of students’time, and if the proportional increasein earnings caused by this additionalschooling is constant over the lifetime,then the log of earnings would be lin-early related to individuals’ years ofschooling, and the slope of this relation-ship could be interpreted as the rate ofreturn to investment in schooling.4 He

augmented this model to include aquadratic term in work experience to al-low for returns to on-the-job training,yielding the familiar Mincerian wageequation:

ln Wi = β0 + β1Si + β2Xi + β3Xi2 + εi, (1)

where ln Wi is the natural log of thewage for individual i, Si is years ofschooling, Xi is experience, Xi

2 is experi-ence squared, and εi is a disturbanceterm. With Mincer’s assumptions, thecoefficient on schooling, β1, equals thediscount rate, because schooling deci-sions are made by equating two presentvalue earnings streams: one with ahigher level of schooling and one with alower level. An attractive feature ofMincer’s model is that time spent inschool (as opposed to degrees) is the keydeterminant of earnings, so data on yearsof schooling can be used to estimate a com-parable return to education in countrieswith very different educational systems.

Equation (1) has been estimated formost countries of the world by OLS,and the results generally yield estimatesof β1 ranging from .05 to .15, withslightly larger estimates for women thanmen (see George Psacharopoulos 1994).The log-linear relationship also providesa good fit to the data, as is illustrated bythe plots for the United States, Sweden,West Germany, and East Germany infigure 1.5 These figures display the co-efficient on dummy variables indicating

3 Early references are Donald Gorseline (1932),J. R. Walsh (1935), Herman Miller (1955), andDael Wolfe and Joseph Smith (1956).

4 This insight is also in Gary Becker (1964) andBecker and Barry Chiswick (1966), who specify thecost of investment in human capital as a fraction ofearnings that would have been received in the ab-

sence of the investment. There are, of course,other theoretical models that yield a log-linearearnings-schooling relationship. For example, ifthe production function relating earnings and hu-man capital is log-linear, and individuals randomlychoose their schooling level (e.g., optimizationerrors), then estimation of equation (1) woulduncover the educational production function.

5 The German figures are from Krueger andJorn-Steffen Pischke (1995). The American andSwedish figures are based on the authors’ calcula-tions using the 1991 March Current PopulationSurvey and 1991 Swedish Level of Living Survey.The regressions also include controls for a qua-dratic in experience and sex.

Krueger and Lindahl: Education for Growth 1103

each year of schooling, controlling forexperience and gender, as well as theOLS estimate of the Mincerian return.It is apparent that the semi-log specifi-cation provides a good description of thedata even in countries with dramati-cally different economic and educationalsystems.6

Much research has addressed thequestion of how to interpret the edu-

cation slope in equation (1). Does itreflect unobserved ability and othercharacteristics that are correlated witheducation, or the true reward that thelabor market places on education? Iseducation rewarded because it is a sig-nal of ability (Michael Spence 1973), orbecause it increases productive capa-bilities (Becker 1964)? Is the social re-turn to education higher or lower thanthe coefficient on education in the Min-cerian wage equation? Would all indi-viduals reap the same proportionate in-crease in their earnings from attendingschool an extra year, or does the returnto education vary systematically withindividual characteristics? Definitive an-swers to these questions are not avail-able, although the weight of the evi-dence clearly suggests that educationis not merely a proxy for unobservedability. For example, Griliches (1977)

Log

Wag

e

10.5

10

9.5

9

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A. United States

10 11 12 13 14Years of Schooling

15 16 17 18 198.5

Log

Wag

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9

8.5

8

7.5

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C. West Germany


15 16 17 18 197

Log

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4.5

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B. Sweden


15 16 17 18 193.5

Log

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7.5

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6.5

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D. East Germany


Figure 1. Unrestricted Schooling-Log Wage Relationship and Mincer Earnings Specification

15 16 17 18 196

6 Evaluating micro data for states over time inthe United States, Card and Krueger (1992) findthat the earnings-schooling relationship is flatuntil the education level reached by the 2nd per-centile of the education distribution, and thenbecomes log-linear. There is also some evidence ofsheep-skin effects around college and high schoolcompletion (e.g., Jin Huem Park 1994). Althoughstatistical tests often reject the log-linear relation-ship for a large sample, the figures clearly showthat the log-linear relationship provides a good ap-proximation to the functional form. It should alsobe noted that Kevin Murphy and Finis Welch(1990) find that a quartic in experience provides abetter fit to the data than a quadratic.


concludes that instead of finding the ex-pected positive ability bias in the returnto education, “The implied net bias iseither nil or negative” once measure-ment error in education is taken intoaccount.

The more recent evidence from natu-ral experiments also supports a conclu-sion that omitted ability does not causeupward bias in the return to education(see Card 1999 for a survey). For exam-ple, Joshua Angrist and Krueger (1991)observe that the combined effect ofschool start age cutoffs and compulsoryschooling laws produces a natural ex-periment, in which individuals who areborn on different days of the year startschool at different ages, and then reachthe compulsory schooling age at dif-ferent grade levels. If the date of theyear individuals are born is unrelatedto their inherent abilities, then, in es-sence, variations in schooling associatedwith date of birth provide a natural ex-periment for estimating the benefit ofobtaining extra schooling in responseto compulsory schooling laws.

Using a sample of nearly one millionobservations from the U.S. censuses,Angrist and Krueger find that men bornin the beginning of the calendar year,who start school at a relatively older ageand can drop out in a lower grade, tendto obtain less schooling. This patternonly holds for those with a high schooleducation or less, consistent with theview that compulsory schooling is re-sponsible for the pattern. They furtherfind that the pattern of education byquarter-of-birth is mirrored by the pat-tern of earnings by quarter-of-birth: inparticular, individuals who are born earlyin the year tend to earn less, on average.7Instrumental variables (IV) estimatesthat are identified by variability in

schooling associated with quarter-of-birth suggest that the payoff to educa-tion is slightly higher than the OLS esti-mate.8 Angrist and Krueger concludethat the upward bias in the return toschooling is of about the same order ofmagnitude as the downward bias due tomeasurement error in schooling.

Other studies have used a variety ofother sources of arguably exogenousvariability in schooling to estimate thereturn to schooling. Colm Harmon andIan Walker (1995), for example, moredirectly examine the effect of compul-sory schooling by studying the effect ofchanges in the compulsory schoolingage in the United Kingdom, while Card(1995a) exploits variations in schoolingattainment owing to families’ proximityto a college in the United States. J.Maluccio (1997) uses data from thePhillippines and estimates the rate ofreturn to education using distance to thenearest high school as an instrumentalvariable for education. Esther Duflo(1998) bases identification on variationin educational attainment related toschool building programs across islandsin Indonesia. Arjun Bedi and Noel Gas-ton (1999) use variation in schoolingavailability over time in Honduras toestimate the return to schooling. Thesefive papers find that the IV estimates ofthe return to education that exploit a“natural experiment” for variability ineducation exceed the correspondingOLS estimates, although the differencebetween the IV and OLS estimatesoften is not statistically significant.

7 Again, no such pattern holds for college gradu-ates.

8 John Bound, David Jaeger, and Regina Baker(1995) argue that Angrist and Krueger’s IV esti-mates are biased toward the OLS estimates be-cause of weak instruments. However, DouglasStaiger and James Stock (1997), Steven Donaldand Whitney Newey (1997), Angrist, Guido Im-bens, and Krueger (1999), and Gary Chamberlainand Imbens (1996) show that weak instruments donot account for the central conclusion of Angristand Krueger (1991).


In a formal meta-analysis of the lit-erature on returns to schooling, OrleyAshenfelter, Harmon, and Hessel Ooster-beek (1999) compiled 96 estimates from27 studies, representing nine differentcountries. They find that the conven-tional OLS return to schooling is .066,on average, whereas the average IV esti-mate is .093. Ashenfelter, Harmon, andOosterbeek also explored whether pub-lication bias—the greater likelihood thatstudies are published if they find statis-tically significant results—accounts forthe tendency of IV estimates to exceedthe OLS estimates. Because IV esti-mates tend to have large standard er-rors, publication bias could spuriouslyinduce published studies that use thismethod to have large coefficient esti-mates. After adjusting for publicationbias, however, they still found that thereturn to schooling is higher, on aver-age, in the IV estimates than in theOLS estimates (.081 versus .064).9

A potential problem with the naturalexperiment approach is that variabilityin schooling owing to the natural ex-periment may not be entirely exoge-nous. For example, it is possible thatdate of birth has an effect on individu-als’ life outcomes independent of com-pulsory schooling. Likewise, some fami-lies may locate near schools becausethey have a strong interest in education,so distance from a school may not be alegitimate instrument. To some extent,researchers have tried to probe thevalidity of their instruments (e.g., byexamining the effect of date of birth onthose not constrained by compulsoryschooling), but there is always a linger-ing concern that the instruments are

not valid. The fact that a diverse set ofnatural experiments, each with possiblebiases of different magnitudes and signs,points in the same direction is reassur-ing in this regard, but ultimately theconfidence one places in the studies ofnatural experiments depends on the con-fidence one places in the plausibilitythat the variability in schooling generatedby the natural experiments is otherwiseunrelated to individuals’ earnings.

An additional problem arises in less-developed countries because income isparticularly hard to measure when thereis a large, self-employed farm sector. Inpart for this reason, much of the litera-ture has focused on developed coun-tries. Macroeconomic studies of GDPhave the advantage of focusing on amore inclusive measure of income thanmicro studies of wages. It is worthnoting, however, that the small numberof microeconometric studies that usenatural experiments to estimate thereturn to education in developing coun-tries tend to find similar results as thosein developed countries. In addition,studies that look directly at the relation-ship between farm output (or profit)and education typically find a positivecorrelation (see Dean Jamison andLawrence Lau 1982), although thedirection of causality is unclear.

These caveats notwithstanding, weinterpret the available micro evidenceas suggesting that the return to anadditional year of education obtainedfor reasons like compulsory schoolingor school-building projects is morelikely to be greater, than lower, thanthe conventionally estimated return toschooling. Because the schooling levelsof individuals who are from more disad-vantaged backgrounds tend to be af-fected most by the interventions exam-ined in the literature, Kevin Lang(1993) and Card (1995b) have inferredthat the return to an additional year of

9 For studies that based their estimates on vari-ability in schooling within pairs of identical twins,they found an average rate of return of .092. Whenthey adjusted for publication bias, the averagewithin-twin estimate was a statistically insignifi-cant .009 greater than the average OLS estimate.


schooling is higher for individuals fromdisadvantaged families than for thosefrom advantaged families, and suggestthat such a result follows because dis-advantaged individuals have higherdiscount rates.

Other related evidence for theUnited States suggests the payoff toinvestments in education are higher formore disadvantaged individuals. First,while studies of the effect of schoolresources on student outcomes yieldmixed results, there is a tendency tofind more beneficial effects of schoolresources for disadvantaged students(see, for example, Anita Summers andBarbara Wolfe 1977; Krueger 1999; andSteven Rivkin, Eric Hanushek, and JohnKain 1998). Second, evidence suggeststhat pre-school programs have particu-larly large, long-term effects for dis-advantaged children in terms of re-ducing crime and welfare dependence,and raising incomes (see Steven Barnett1992). Third, several studies have foundthat students from advantaged and dis-advantaged backgrounds make equiva-lent gains on standardized tests duringthe school year, but children from dis-advantaged backgrounds fall behindduring the summer while children fromadvantaged backgrounds move ahead(see Doris Entwisle, Karl Alexander,and Linda Olson 1997). And fourth,evidence suggests that college stu-dents from more disadvantaged familiesbenefit more from attending elite col-leges than do students from advantagedfamilies (see Stacy Dale and Krueger1998).

2.2 Social versus Private Returns to Education

The social return to education can, ofcourse, be higher or lower than the pri-vate monetary return. The social returncan be higher because of externalitiesfrom education, which could occur, for

example, if higher education leads totechnological progress that is not cap-tured in the private return to that edu-cation, or if more education producespositive externalities, such as a reduc-tion in crime and welfare participation,or more informed political decisions.The former is more likely if humancapital is expanded at higher levels ofeducation while the latter is more likelyif it is expanded at lower levels. It isalso possible that the social return toeducation is less than the private re-turn. For example, Spence (1973) andFritz Machlup (1970) note that educa-tion could just be a credential, whichdoes not raise individuals’ productivi-ties. It is also possible that in some de-veloping countries, where the incidenceof unemployment may rise with educa-tion (e.g., Mark Blaug, Richard Layard,and Maureen Woodhall 1969) andwhere the return to physical capitalmay exceed the return to human capi-tal (e.g., Arnold Harberger 1965), in-creases in education may reduce totaloutput.

It should also be noted that educa-tion may affect national income in waysthat are not fully measured by wagerates. For example, particularly in de-veloping countries, education is nega-tively associated with women’s fertilityrates and positively associated with in-fants’ health (see Paul Glewwe 2000).In addition, education is positively asso-ciated with labor force participation;most of the micro human capital lit-erature uses samples that consist ofthose in the labor force, so this effectof education is missed.

A potential weakness of the micro hu-man capital literature is that it focusesprimarily on the private pecuniary re-turn to education rather than the socialreturn. The possibility of externalitiesto education motivates much of themacro growth literature, to which we


now turn. Micro-level empirical analysisis less well suited for uncovering thesocial returns to education.

3. Education in Macro Growth Models

Thirty years ago, Machlup (1970, p. 1)observed, “The literature on the subjectof education and economic growth issome two hundred years old, but only inthe last ten years has the flow of publi-cations taken on the aspects of a flood.”The number of cross-country regressionstudies on education and growth hassurged even higher in recent years.Rather than exhaustively review the en-tire literature, we summarize the mainmodels and findings, and explore theimpact of several econometric issues.10

Two issues have motivated the use ofaggregate data to estimate the effect ofeducation on the growth rate of GDP.First, the relationship between edu-cation and growth in aggregate datacan generate insights into endogenousgrowth theories, and possibly allow oneto discriminate among alternative theo-ries. Second, estimating relationships withaggregate data can capture external re-turns to human capital that are missedin the microeconometric literature.

Human capital plays different roles invarious theories of economic growth. Inthe neoclassical growth model (RobertSolow 1956), no special role is given tohuman capital in the production of out-put. In endogenous growth models hu-man capital is assigned a more centralrole. Aghion and Howitt (1998) observethat the role of human capital in en-dogenous growth models can be dividedinto two broad categories. The firstcategory broadens the concept of capi-tal to include human capital. In these

models sustained growth is due to theaccumulation of human capital over time(e.g., Hirofumi Uzawa 1965; RobertLucas 1988). The second category ofmodels attributes growth to the existingstock of human capital, which generatesinnovations (e.g., Paul Romer 1990a) orimproves a country’s ability to imitateand adapt new technology (e.g., Rich-ard Nelson and Edmund Phelps 1966).This, in turn, leads to technologicalprogress and sustained growth.11 Theobservation that an individual’s produc-tivity can be affected by the humancapital in the economy is also promi-nent in early work on the economics ofcities by Jane Jacobs (1969).

In Lucas’s model the aggregateproduction function is assumed to be:

y = Akα(uh)1 − α(ha)γ,

where y is output, k is physical capital, uis the fraction of time devoted to produc-tion (as opposed to accumulating humancapital), h is the human capital of therepresentative agent, and ha is the aver-age human capital in the economy. Tak-ing logs and differentiating with respectto time establishes that the growth ofoutput depends on the growth of physi-cal capital and the accumulation of hu-man capital. If γ > 0 there are positiveexternalities to human capital. It is fur-ther assumed that human capital growsat the rate:

d log(h) ⁄ dt = δ(1 − u),

10 See Phillippe Aghion and Peter Howitt (1998)for a thorough review of growth models andJonathan Temple (1999a) for a review and critiqueof the new growth evidence.

11 In Aldo Rustichini and James Schmitz (1991),innovation and imitation are combined in an en-dogenous growth framework. Also see DaronAcemoglu and Fabrizio Zilibotti (2000) for amodel that posits that technologies are developedin advanced countries to complement skilled la-bor, while developing countries would benefitmost from technologies that are complementarywith unskilled labor, so technology-skill mismatchcomplicates the adaptation of new technology indeveloping countries. Even if developing countrieswould have full access to the newest technology,productivity differences would still exist in thismodel.


where 1 – u is the time devoted to creat-ing human capital and δ is the maximumachievable growth rate of human capital.In steady state, output and human capi-tal grow at the same rate, and depend onδ and the determinants of the equilib-rium value of u. Sustained growth arisesbecause there are constant returns inthe production of human capital in thismodel.

In Romer’s (1990a) model, the pro-duction function for a multi-sectoreconomy is:

Y = HyαLβ∫ X

0

A(i)1 − α − βdi

where HY is the human capital employedin the non-R&D sector and L is labor.Physical capital is disaggregated intoseparate inputs, denoted X(i), which areused in the production of Y. Note thatthe “capital stock” depends on the tech-nological level, A. Capital is disaggre-gated in this way because for each capi-tal good there is a distinct monopo-listically competitive firm. Technologicalprogress evolves as:

d log(A) ⁄ dt = cHA,

where HA is the human capital employedin the R&D sector. If more human capi-tal is employed in the R&D sector, tech-nological progress and the production ofcapital are greater. This, in turn, gener-ates faster output growth. In steady-state, however, the rate of growth equalsthe rate of technological progress, whichis a linear function of the total humancapital in both sectors.

It should be emphasized that the dif-ferent roles played by human capital inthese two classes of models generatetestable implications. The growth of hu-man capital in the Lucas model shouldaffect output growth, while the stockof human capital in the Romer modelshould affect growth. An early test ofthese implications is provided by Romer

(1990b), who regressed the average an-nual growth of output per capita be-tween 1960 and 1985 on the literacyrate in 1960 and the change in the liter-acy rate between 1960 and 1980, hold-ing the initial level of GDP per capitaand share of GDP devoted to invest-ment constant. He found evidence thatthe initial level of literacy, but not thechange in literacy, predicted outputgrowth. Romer noted that in this modelinvestment could reflect the rate oftechnological progress, so the effects ofthe level and change of literacy are hardto interpret when investment is also heldconstant. When the investment rate wasdropped from the growth equation,however, the change in literacy was stillstatistically insignificant.

3.1 Empirical Macro Growth Equations

The empirical macro growth litera-ture yields two principally differentfindings from the micro literature. First,the initial stock of human capital mat-ters, not the change in human capital.12

Second, secondary and post-secondaryeducation matter more for growth thanprimary education. To compare the ef-fect of schooling in the Mincer modelto the macro growth literature, firstconsider a Mincerian wage equation foreach country j and time period t:

ln Wijt = β0jt + β1jtSijt + εijt, (1′)where we have suppressed the expe-rience term.13 This equation can be

12 One exception is Gemmell (1996), who used ahuman capital measure of the workforce derivedfrom school enrollment rates and labor force par-ticipation data. He found evidence that both thegrowth and level of primary education influenceGDP growth, although the growth of secondaryeducation had an insignificant, negative effect onoutput growth.

13 Ignoring experience is clearly not in the spiritof the Mincer model. However, as ordinarily cal-culated, experience is a function of age and educa-tion. Since life expectancy is almost certainly afunction of living standards across countries (e.g.,Smith 1999), controlling for average experience


aggregated across individuals each yearby taking the means of each of the vari-ables, yielding what James Heckman andKlenow (1997) call the “Macro-Mincer”wage equation:

ln Yjtg = β0jt + β1jtSjt + εjt, (2)

where Yjtg denotes the geometric mean

wage and Sjt is mean education. Heck-man and Klenow (1997) compare the co-efficient on education from cross-countrylog GDP equations to the coefficient oneducation from micro Mincer models.Once they control for life expectancy toproxy for technology differences acrosscountries, they find that the macro andmicro regressions yield similar estimatesof the effect of education on income.14

They conclude from this exercise that the“macro versus micro evidence for humancapital externalities is not robust.”

The macro Mincer equation can bedifferenced between year t and t – 1,giving:

∆ln Yjg = β′0 + β1jtSjt − β1jt − 1Sjt − 1 + ∆ε′jt, (3)

where ∆ signifies the change in the vari-able from t – 1 to t, β′0 is the meanchange in the intercepts, and ∆ε′jt is acomposite error that includes the devia-tion between each country’s interceptchange and the overall average. Differ-encing the equation removes the effectof any additive, permanent differences intechnology. If the return to schooling isconstant over time, we have:

∆ln Yjg = β′0 + β1j∆Sj + ∆ε′jt. (4)

Notice that this formulation allows thetime-invariant return to schooling to varyacross countries. If β1j does vary acrosscountries, and a constant-coefficientmodel is estimated, then (β1 – β1j)∆Sjwill add to the error term.

Also notice that if the return toschooling varies over time, then byadding and subtracting β1jtSjt – 1 fromthe right-hand-side of equation (3), weobtain:

∆ln Yjg = β′0 + β1jt∆Sj + δSjt − 1 + ∆ε′jt, (5)

where δ is the change in the return toschooling (∆β1j). If the return to school-ing has increased (decreased) secularlyover time, the initial level of educationwill enter positively (negatively) intoequation (5). An implicit assumption inmuch of the macro growth literaturetherefore is that the return to educa-tion is either unchanged, or changedendogenously, by the stock of humancapital.

Although the empirical literature forthe United States clearly shows a fall inthe return to education in the 1970sand a sharp increase in the 1980s (e.g.,Frank Levy and Richard Murnane 1992),the findings for other countries aremixed. For example, Psacharopolous(1994; table 6) finds that in the averagecountry the Mincerian return to edu-cation fell by 1.7 points over periodsof various lengths (average of twelveyears) since the late 1960s. By contrast,Donal O’Neill (1995) finds that be-tween 1967 and 1985 the return to edu-cation measured in terms of its contri-bution to GDP rose by 58 percent indeveloped countries and by 64 percentin less developed countries.

One strand of macro growth modelsestimated in the literature is motivatedby the convergence literature (e.g.,Robert Barro 1997). This leads to in-terest in estimating parameters of anunderlying model such as ∆Yj = αj –

would introduce a serious simultaneity bias. In themacro models, part of the return attributable toschooling may indirectly result from changes inlife expectancy.

14 When they omit life expectancy, however,education has a much larger effect in the macroregression than micro regression. Whether longerlife expectancy is a valid proxy for technology dif-ferences, or a result of higher income, is an openquestion (see Smith 1999).


β(Yjt – 1 − Yj∗) + µj, where ∆Yj denotes

the annualized change in log GDP percapita in country j between t – 1 andt, αj denotes country j’s steady-stategrowth rate, Yjt – 1 is the log of initialGDP per-capita, Yj

∗ is steady-state logGDP per capita, and β measures thespeed of convergence to steady-stateincome. The intuition for this equationis straightforward: countries that arebelow their steady-state income levelshould grow quickly, and those that areabove it should grow slowly. Anotherstrand is motivated by the endogenousgrowth literature described previously(e.g., Romer 1990b). In either case, atypical estimating equation is:

∆Yj = β0 + β1Yj,t − 1 + β2Sj,t − 1

+ β3Zj,t − 1 + εj(6)

where ∆Yj is the change in log GDP percapita from year t – 1 to t, Sj,t – 1 is aver-age years of schooling in the populationin the initial year, Yj,t – 1 is the log of ini-tial GDP per capita, and Zj,t – 1 includesvariables such as inflation, capital, or the“rule of law index.”15 Also note thatschooling is sometimes specified in loga-rithmic units in equation (6). The equa-tion is typically estimated with data for across-section or pooled sample of coun-tries spanning a five-, ten-, or twenty-yearperiod. Barro and Xavier Sala-i-Martin(1995), Benhabib and Spiegel (1994), andothers conclude that the change inschooling has an insignificant effect if itis included in a GDP growth equation,even though this variable is predicted tomatter in the Mincer model and in someendogenous economic growth models(e.g., Lucas 1988).

The first-differenced macro-Mincerequation (4) differs from the typicalmacro growth equation in several re-spects. First, the macro growth model

uses the change in log GDP per capitaas the dependent variable, rather thanthe change in the mean of log earnings.If income has a log normal distributionwith a constant variance over time, andif labor’s share is also constant, then thefact that GDP is used instead of laborincome would not matter.16 If the ag-gregate production function were a sta-ble Cobb-Douglas production function,for example, then labor’s share wouldbe constant and this link between themacro Mincer model and the GDPgrowth equations would plausibly hold.With a more general production func-tion, however, there is no simple map-ping between the effect of schooling onindividual labor income and the effectof schooling on GDP. Without microdata for a large sample of countries overtime, the impact of using aggregateGDP as opposed to labor income is dif-ficult to assess. When cross sections ofmicro data become available for a largesample of countries in the future, thiswould be a fruitful topic for furtherresearch.

Second, the empirical macro growthliterature typically omits the change inschooling, and includes the initial level ofschooling. If the change in schooling isincluded, its estimated impact couldpotentially reflect general equilibriumeffects of education at the country level.

Third, because much of the macro lit-erature is motivated by issues of conver-gence, researchers hold constant the ini-tial level of GDP and correlates forsteady-state income. Indeed, a primarymotivation for including human capitalvariables in these equations is to controlfor steady state income, Y∗. In the endoge-nous growth literature, on the otherhand, the initial level of GDP would bean appropriate variable to substitute for

15 Henceforth we use the terms GDP per capitaand GDP interchangeably.

16 Heckman and Klenow (1997) point out thathalf the variance of log income will be added tothe GDP equation if income is log normal.


the initial capital stock if the productionfunction is Cobb-Douglas.

There are at least five ways to inter-pret the coefficient on the initial levelof schooling in equation (6). First,schooling may be a proxy for steady-state income. Countries with moreschooling would be expected to have ahigher steady-state income, so condi-tional on GDP in the initial year, wewould expect more educated countriesto grow faster (β2 > 0). If this were thecase, higher schooling levels would notchange the steady-state growth rate,although it would raise steady-state in-come. Second, schooling could changethe steady-state growth rate by enablingthe work force to develop, implementand adopt new technologies, as arguedby Nelson and Phelps (1966) and

Romer (1990), again leading to the pre-diction β2 > 0. Third, a positive or nega-tive coefficient on initial schooling maysimply reflect an exogenous change in thereturn to schooling, as shown in equa-tion (5). Fourth, anticipated increasesin future economic growth could causeschooling to rise (i.e., reverse causality),as argued by Bils and Klenow (1998).Fifth, the schooling variable may “pickup” the effect of the change in educa-tion, which is typically omitted from thegrowth equation.

3.2 Basic Results and Effectof Measurement Error in Schooling

Table 1 replicates and extends the“growth accounting” and “endogenousgrowth” regressions in Benhabib and

TABLE 1REPLICATION AND EXTENSION OF BENHABIB AND SPIEGEL (1994)

DEPENDENT VARIABLE: ANNUALIZED CHANGE IN LOG GDP, 1965–85

Log Schooling Linear Schooling

Variable (1) (2) (3) (4) (5) (6)

∆ Log S –.072(.058)

.178(.112)

.614(.162)

— — —

Log S65 — .010(.004)

.026(.005)

— — —

∆S — — — .012(.023)

.039(.024)

.151(.034)

S65 — — — — .003(.001)

.004(.001)

Log Y65 –.009(.002)

–.012(.002)

–.015(.003)

–.008(.002)

–.014(.002)

–.014(.004)

∆ Log Capital .523(.048)

.461(.052)

— .521(.051)

.465(.052)

—

∆ Log Work Force .175(.164)

.232(.160)

— .110(.160)

.335(.167)

—

R2 .694 .720 .291 .688 .726 .271

Notes: All change variables were divided by 20, including the dependent variable. Sample size is 78 countries.Standard errors are in parentheses. All equations also include an intercept. S65 is Kyriacou’s measure of schooling in1965; ∆ Log S is the change in log schooling between 1965 and 1985, divided by 20; and Y65 is GDP per capita in1965. Mean of the dependent variable is .039; standard deviation of dependent variable is .020.


Spiegel’s (1994) influential paper.17

Their analysis is based on Kyriacou’s(1991) measure of average years ofschooling for the work force in 1965and 1985, Robert Summers and AlanHeston’s GDP and labor force data, anda measure of physical capital derivedfrom investment flows for a sample of78 countries. Following Benhabib andSpiegel, the regression in column (1)relates the annualized growth rate ofGDP to the log change in years ofschooling. From this model, Benhabiband Spiegel conclude, “Our findingsshed some doubt on the traditional rolegiven to human capital in the develop-ment process as a separate factor ofproduction.” Instead, they concludethat the stock of education matters forgrowth (see columns 2 and 5) by en-abling countries with a high level of edu-cation to adopt and innovate technologyfaster.

Topel (1999) argues that Benhabiband Spiegel’s finding of an insignificantand wrong-signed effect of schoolingchanges on GDP growth is due to theirlog specification of education.18 Thelog-log specification follows if one as-sumes that schooling enters an aggre-gate Cobb-Douglas production functionlinearly. Given the success of theMincer model, however, we wouldagree with Topel that it is more naturalto specify human capital as an exponen-tial function of schooling in a Cobb-

Douglas production function, so thechange in linear years of schoolingwould enter the growth equation. Inany event, the logarithmic specificationof schooling does not fully explain theperverse effect of educational improve-ments on growth in Benhabib andSpiegel’s analysis.19 Results of estimat-ing a linear education specification incolumn 4 still show a statistically insig-nificant (though positive) effect of thelinear change in schooling on economicgrowth.

Columns 3 and 6 show that control-ling for capital is critical to Benhabiband Spiegel’s finding of an insignificanteffect of the change in schooling vari-able. When physical capital is excludedfrom the growth equation, the changein schooling has a statistically signifi-cant and positive effect in either thelinear or log schooling specification.Why does controlling for capital havesuch a large effect on education? Asshown below, it appears that the insig-nificant effect of the change in educa-tion is a result of the low signal in theeducation change variable. Indeed, con-ditional on the other variables that Ben-habib and Spiegel hold constant (espe-cially capital), the change in schoolingconveys virtually no signal.20

Notice also that the coefficient on

17 Our results are not identical to Benhabib andSpiegel’s because we use a revised version of Sum-mers and Heston’s GDP data. Nonetheless, ourestimates are very close to theirs. For example,Benhabib and Spiegel report coefficients of –.059for the change in log education and .545 for thechange in log capital when they estimate themodel in column 1 of table 1; our estimates are–.072 and .523. Some of the other coefficients dif-fer because of scaling; for comparability with laterresults, we divided the dependent variable andvariables measured in changes by 20.

18 Mankiw, Romer, and Weil (1992; table VI)estimate a similar specification.

19 The log specification is part of the explana-tion, however, because if the model in column (3)is estimated without the initial level of schooling,the change in log schooling has a negative and sta-tistically significant effect, whereas the change inthe level of schooling has a positive and statisti-cally significant effect if it is included as a regres-sor in this model instead.

20 Pritchett (1998) estimates essentially thesame model as Benhabib and Spiegel (i.e., column1 of table 1), and instruments for schooling growthusing an alternative education series. However, ifthere is no variability in the portion of measuredschooling changes that represent true schoolingchanges conditional on capital, the instrumentalvariables strategy is inconsistent. This can easilybe seen by noting that there would be no variabil-ity due to true education changes conditional oncapital in the reduced form of the model.


capital is high in table 1, around 0.50with a t-ratio close to 10. In a competi-tive, Cobb-Douglas economy, the coef-ficient on capital growth in a GDPgrowth regression should equal capital’sshare of national income. Douglas Gol-lin (1998) estimates that labor’s shareranges from .65 to .80 in most coun-tries, after allocating labor’s portion ofself-employment and proprietors’ in-come. Consequently, capital’s share isprobably no higher than .20 to .35. Thecoefficient on capital could be biasedupwards because countries that experi-ence rapid GDP growth may find iteasier to raise investment, creating asimultaneity bias. In addition, as Ben-habib and Boyan Jovanovic (1991) ar-gue, shocks to technological progresswill bias the coefficient on the growthof capital above capital’s share in amodel with a constant-returns to scaleCobb-Douglas aggregate production func-tion without externalities from capital.If the coefficient on capital growth incolumn (5) of table 1 is constrained toequal .20 or .35—a plausible range forcapital’s share—the coefficient on theschooling change rises to .09 or .06, andbecomes statistically significant.

3.2.1 The Extent of Measurement Errorin International Education Data

We disregard errors that arise be-cause years of schooling are an imper-fect measure of human capital, and focusinstead on the more tractable problemof estimating the extent of measure-ment error in cross-country data onaverage years of schooling. Benhabiband Spiegel’s measure of average yearsof schooling for the work force wasderived by Kyriacou (1991) as follows.First, survey-based estimates of averageyears of schooling for 42 countries inthe mid-1970s were regressed on thecountries’ primary, secondary and terti-ary school enrollment rates. Coefficient

estimates from this model were thenused to predict years of schooling fromenrollment rates for all countries in1965 and 1985. This method is likelyto generate substantial noise since thefitted regression may not hold for allcountries and time periods, enrollmentrates are frequently mismeasured, andthe enrollment rates are not properlyaligned with the workforce. Changes ineducation derived from this measureare likely to be particularly noisy. Ben-habib and Spiegel use Kyriacou’s educa-tion data for 1965, as well as the changebetween 1965 and 1985.

The widely used Barro and Lee(1993) data set is an alternative sourceof education data. For 40 percent ofcountry-year cells, Barro and Lee mea-sure average years of schooling by survey-and census-based estimates reported byUNESCO. The remaining observationswere derived from historical enrollmentflow data using a “perpetual inventorymethod.”21 The Barro-Lee measure isundoubtedly an advance over existinginternational measures of educationalattainment, but errors in measurementare inevitable because the UNESCOenrollment rates are of doubtful qualityin many countries (see Jere Behrmanand Mark Rosensweig 1993, 1994). Forexample, UNESCO data are oftenbased on beginning of the year enroll-ment. Additionally, students educatedabroad are miscounted in the flow data,which is probably a larger problem forhigher education. More fundamentally,secondary and tertiary schooling is de-fined differently across countries in theUNESCO data, so years of secondaryand higher schooling are likely to benoisier than overall schooling. Notice alsothat because errors cumulate over timein Barro and Lee’s stock-flow calculations,

21 Each country has a survey- and census-basedestimate in at least one year, which provides ananchor for the enrollment flows.


the errors in education will be positivelycorrelated over time.

As is well known, if an explanatoryvariable is measured with additive whitenoise errors, then the coefficient onthis variable will be attenuated towardzero in a bivariate regression, with theattenuation factor, R, asymptoticallyequal to the ratio of the variance of thecorrectly-measured variable to the vari-ance of the observed variable (see, e.g.,Griliches 1986). A similar result holdsin a multiple regression (with correctly-measured covariates), only now thevariances are conditional on the othervariables in the model. To estimateattenuation bias due to measurementerror, write a nation’s measured yearsof schooling, Sj, as its true schooling,Sj

∗, plus a measurement error denotedej: Sj = Sj

∗ + ej. It is convenient to startwith the assumption that the measure-ment errors are “classical”; that is, er-rors that are uncorrelated with S∗,other variables in the growth equation,and the equation error term. Now let S1

and S2 denote two imperfect measuresof average years of schooling for eachcountry, with measurement errors e1

and e2 respectively (where we suppressthe j subscript).

If e1 and e2 are uncorrelated, thefraction of the observed variability in S1

due to measurement error can be esti-mated as R1 = cov(S1,S2)/var(S1). R1 isoften referred to as the reliability ratioof S1, and has probability limit equalto var(S∗)/{var(S∗) + var(e1)}. Assumingconstant variances, the reliability of thedata expressed in changes (R∆S1) will belower than the cross-sectional reliabilityif the serial correlation of the true vari-able is higher than the serial correla-tion of the measurement errors becauseR∆S1 = var(S∗)/{var(S∗) + var(e)(1 – re)/(1 – ρS∗)}, where re is the serial correla-tion of the errors and ρS∗ is the serialcorrelation of true schooling. In prac-

tice, the reliability ratio for changesin S1 can be estimated by: R∆S1 =cov(∆S1,∆S2)/var(∆S1). Note that if theerrors in S1 and S2 are positively corre-lated, the estimated reliability ratioswill be biased upward.

We can calculate the reliability of theBarro-Lee and Kyriacou data if we treatthe two variables as independent esti-mates of educational attainment. It isprobably the case, however, that themeasurement errors in the two datasources are positively correlated be-cause, to some extent, they both relyon the same mismeasured enrollmentdata.22 Consequently, the reliability ra-tios derived from comparing these twomeasures probably provide an upperbound on the reliability of the dataseries.

Panel A of table 2 presents estimatesof the reliability ratio of the Kyriacouand Barro-Lee education data. Appen-dix table A.1 reports the correlation andcovariance matrices for the measures.The reliability ratios were derived byregressing one measure of years ofschooling on the other.23 The cross-sectional data have considerable signal,with the reliability ratio ranging from.77 to .85 in the Barro-Lee data and

22 Another complication is that the Kyriacoudata pertain to the education of the work force,whereas the Barro-Lee data pertain to the entirepopulation age 25 and older. If the regressionslope relating true education of workers to thetrue education of the population is one, the reli-ability ratios reported in the text are unbiased. Al-though we do not know true education of workersand the population, in the Barro-Lee data set aregression of the average years of schooling ofmen (who are very likely to work) on the averageeducation of the population yields a slope of .99,suggesting that workers and the population mayhave close to a unit slope.

23 Barro and Lee (1993) compare their educa-tion measure with alternative series by reportingcorrelation coefficients. For example, they reporta correlation of .89 with Kyriacou’s education dataand .93 with Psacharopolous’s. Our cross-sectionalcorrelations are not very different. They do notreport correlations for changes in education.


exceeding .96 in the Kyriacou data. Thereliability ratios fall by 10 to 30 percentif we condition on the log of 1965 GDPper capita, which is a common covari-ate. More disconcerting, when the dataare measured in changes over thetwenty-year period, the reliability ratiofor the data used by Benhabib andSpiegel falls to less than 20 percent. Byway of comparison, note that Ashenfel-ter and Krueger (1994) find that the re-liability of self-reported years of educa-tion is .90 in micro data on workers, andthat the reliability of self-reported dif-ferences in education between identicaltwins is .57.24

These results suggest that if therewere no other regressors in the model,the estimated effect of schoolingchanges in Benhabib and Spiegel’s re-sults would be biased downward by 80percent. But the bias is likely to beeven greater because their regressionsinclude additional explanatory variablesthat absorb some of the true changes inschooling. The reliability ratio condi-tional on the other variables in themodel can be shown to equalR′∆S1 = (R∆S1 − R2) ⁄ (1 − R2), where R2 isthe multiple coefficient of determina-tion from a regression of the measuredschooling change variable on the otherexplanatory variables in the model. Aregression of the change in Kyriacou’seducation measure on the covariates in

TABLE 2RELIABILITY OF VARIOUS MEASURES OF YEARS OF SCHOOLING

A. Estimated Reliability Ratios for Barro-Lee and Kyriacou Data

Reliability of Barro-Lee Data Reliability of Kyriacou Data

Average years of schooling, 1965 .851(.049)

.964(.055)


.966(.069)

Change in years of schooling, 1965–85 .577(.199)

.195(.067)

B. Estimated Reliability Ratios for Barro-Lee and World Values Survey Data

Reliability of Barro-Lee Data Reliability of WVS Data


.727(.093)

Average years of secondary and higherschooling, 1990

.719(.167)

.512(.119)

Notes: The estimated reliability ratios are the slope coefficients from a bivariate regression of one measure ofschooling on the other. For example, the .851 entry in the first row is the slope coefficient from a regression in whichthe dependent variable is Kyriacou’s schooling variable and the independent variable is Barro-Lee’s schoolingvariable. The .964 ratio in the second column is estimated from the reverse regression. In panel B, the reliabilityratios are estimated by comparing the Barro-Lee and WVS data. In the WVS data set, secondary and higherschooling is defined as years of schooling attained after 8 years of schooling.

Sample size for panel A is 68 countries. Sample size for panel B is 34 countries. Standard errors are reported inparentheses.

24 Behrman, Rosenzweig, and Paul Taubman(1994) find reliability ratios of .94 across twins and.70 within twins for a sample of 141 twin pairs.


column (4) of table 1 yields an R2 of 23percent. If the covariates are correlatedwith the signal in education changesand not the noise, then there is no vari-ability in true schooling changes leftover in the measured schooling changesconditional on the other variables in themodel. Instead of rejecting the tradi-tional Mincerian role of education ongrowth, a reasonable interpretation isthat Benhabib and Spiegel’s resultsshed no light on the role of educationchanges on growth.

The Barro and Lee data convey moresignal than Kyriacou’s data when ex-pressed in changes. Indeed, nearly 60percent of the variability in observedchanges in years of education in theBarro-Lee data represent true changes.This makes the Barro-Lee data pref-erable to use to estimate the effect ofeducational improvements. Despite thegreater reliability of the Barro-Lee data,there is still little signal left over inthese data conditional on the other vari-ables in the model in column 4 of table1; a regression of the change in theBarro-Lee schooling measure on thechange in capital, change in population,and initial schooling yields an R2 of .28.Consequently, conditional on thesevariables about 40 percent of the re-maining variability in schooling changesin the Barro-Lee data is true signal.

As mentioned, we suspect the esti-mated reliability ratios are biased up-ward because the errors in the Kyriacouand Barro-Lee data are probably posi-tively correlated. To derive a measureof education with independent errors,we calculated average years of school-ing from the World Values Survey(WVS) for 34 countries. The WVS con-tains micro data from household surveysthat were conducted in nearly fortycountries in 1990 or 1991. The surveywas designed to be comparable acrosscountries. In each country, individuals

were asked to report the age at whichthey left school. With an assumption ofschool start age, we can calculate theaverage number of years that individu-als spent in school. We also calculatedaverage years of secondary and higherschooling by counting years of school-ing obtained after eight years of school-ing as secondary and higher schooling.Notice that these measures will not beerror free either. Errors could arise, forexample, because some individuals re-peated grades, because we have madean erroneous assumption about schoolstart age or the beginning of secondaryschooling, or because of sampling errors.But the errors in this measure shouldbe independent of the errors in Kyria-cou’s and Barro and Lee’s data. Theappendix provides additional details ofour calculations with the WVS.

Panel B of table 2 reports the reli-ability ratios for the Barro-Lee data andWVS data for 1990. The reliability ratioof .90 for the Barro-Lee data in 1990 isslightly higher than the estimate for1985 based on Kyriacou’s data, but withinone standard error. Thus, it appearsthat correlation between the errors inKyriacou’s and Barro-Lee’s data is not aserious problem. Nonetheless, anotheradvantage of the WVS data is that theycan be used to calculate upper second-ary schooling using a constant (if im-perfect) definition across countries. Asone might expect given differences inthe definition of secondary schooling inthe UNESCO data, the reliability of thesecondary and higher schooling (.72) islower than the reliability of all years ofschooling.

Lastly, it should be noted that themeasurement errors in schooling arehighly serially correlated in the Barro-Lee data. This can be seen from thefact that the correlation between the1965 and 1985 schooling levels acrosscountries is .97 in the Barro-Lee data,


while less than 90 percent of the vari-ations in the cross-sectional data acrosscountries appear to represent true sig-nal. If the reliability ratios reportedin table 2 are correct, the only waythe time-series correlation in educa-tion could be so high is if the errorsare serially correlated. The correlationof the errors can be estimated as:[cov(S85

BL,S65BL) − cov(S85

BL,S65K )] / [(1 − R85

BL)var(S85

BL)(1 − R65BL)var(S65

BL)]1⁄2, where the su-perscript BL stands for Barro-Lee’s dataand K for Kyriacou’s data. Using the re-liability ratios in table 2, the estimatedcorrelation of the errors in Barro-Lee’sschooling measure between 1965 and1985 is .61. The correlation betweentrue schooling in 1965 and 1985 is esti-mated at .97.25 Since the serial correla-tion of true schooling is higher than theserial correlation of the errors, the reli-ability of the first-differenced educationdata is lower than the reliability of thecross-sectional data.

3.3 Growth Models Estimated Over Varying Time Intervals

Measurement errors aside, one couldquestion whether physical capital shouldbe included as a regressor in a GDPgrowth equation because it is an en-dogenous variable. A number of authorshave argued that capital is endoge-nously determined in growth equationsbecause investment is a choice variable,and shocks to output are likely to influ-ence the optimal level of investment(see, for examples, Benhabib andJovanovic 1991; Blomström, Lipsey, andZejan 1993; Benhabib and Spiegel1994; and Caselli, Esquivel, and Lefort1996). In addition, because of capital-skill complementarity, countries may at-tract more investment if they raise their

level of education. Part of the return tocapital thus might be attributable toeducation. Romer (1990b) also notesthat the growth in capital could in partpick up the effect of endogenous tech-nological change. There is also a practi-cal issue: we only have reliable capitalstock data for the full sample in 1960and 1985.26 In view of these considera-tions, and the low signal in schoolingchanges conditional on capital growth,we initially present models without con-trolling for capital to focus attention onthe effect of changes in education ongrowth over varying time intervals. Wepresent estimates that control for capitalin long-difference models in section 3.6.

Table 3 reports parsimonious macrogrowth models for samples spanningfive-, ten- or twenty-year periods. Thedependent variable is the annualizedchange in the log of real GDP per cap-ita per year based on Summers andHeston’s (1991) Penn World Tables,Mark 5:6. Results are quite similar ifGDP per worker is used instead ofGDP per capita. We use GDP per cap-ita because it reflects labor force par-ticipation decisions and because it hasbeen the focus of much of the previousliterature. The schooling variable isBarro and Lee’s measure of averageyears of schooling for the populationage 25 and older. When the change inaverage schooling is included as a re-gressor in these models, we divide it bythe number of years in the time span sothe coefficients are comparable acrosscolumns. The equations were estimatedby OLS, but the standard errors re-ported in the table allow for a country-specific component in the error term.27

25 We estimate the serial correlation betweentrue schooling levels in 1985 and 1965 using theformula: ρs∗ = [cov(S85

BL, S65K )cov(S65

BL, S85K ) ⁄ cov(S85

BL,S85

K )cov(S65BL, S65

K )]1⁄2.

26 Topel interpolates the capital stock data toestimate models over shorter time periods, butthis probably introduces a great deal of error andexacerbates endogeneity problems.

27 An alternative approach would be to estimatea restricted seemingly unrelated system or randomeffects model. Absent measurement error, these


We exclude other variables (e.g., rule oflaw index) that are sometimes includedin macro growth models to focus oneducation, and because those othervariables are probably influenced them-selves by education.28 Topel (1999) hasestimated stylized growth models overvarying length time intervals similar tothose in table 3, but he subtracts an es-timate of the change in the capital stocktimes 0.35 from the dependent variable.

Our findings are quite similar toTopel’s. The change in schooling haslittle effect on GDP growth when thegrowth equation is estimated with highfrequency changes (i.e., five years). How-

ever, increases in average years ofschooling have a positive and statisti-cally significant effect on economicgrowth over periods of ten or twentyyears. The magnitude of the coefficientestimates on both the change and initiallevel of schooling over long periods arelarge—probably too large to representthe causal effect of schooling.

The finding that the time span mat-ters so much for the change in educa-tion suggests that measurement error inschooling influences these estimates.Over short time periods, there is littlechange in a nation’s true mean school-ing level, so the transitory componentof measurement error in schoolingwould be large relative to variability inthe true change. Over longer periods,true education levels are more likelyto change, increasing the signal relativeto the noise in measured changes. Mea-surement error bias appears to be

estimators are more efficient. But because biasdue to measurement errors in the explanatory vari-ables is exacerbated with these estimators, weelected to estimate the parameters by OLS andreport robust standard errors.

28 If we control for the initial fertility rate, theinitial education variable becomes much weakerand insignificant. See Krueger and Lindahl (1999).

TABLE 3THE EFFECT OF SCHOOLING ON GROWTH

DEPENDENT VARIABLE: ANNUALIZED CHANGE IN LOG GDP PER CAPITA

5-year changes 10-year changes 20-year changes

(1) (2) (3) (4) (5) (6) (7) (8) (9)

St – 1 .004(.001)

— .004(.001)

.003(.001)

— .004(.001)

.005(.001)

— .005(.001)

∆S — .031(.015)

.039(.014)

— .075(.026)

.086(.024)

— .184(.057)

.182(.051)

Log Yt – 1 –.005(.003)

.004(.002)

–.006(.003)

–.003(.003)

.004(.001)

–.005(.003)

–.010(.003)

–.001(.002)

–.013(.003)

R2 .197 .161 .207 .242 .229 .284 .184 .103 .281

N 607 607 607 292 292 292 97 97 97

Notes: First six columns include time dummies. Equations were estimated by OLS. The standard errors in the firstsix columns allow for correlated errors for the same country in different time periods. Maximum number ofcountries is 110. Columns 1–3 consist of changes for 1960–65, 1965–70, 1970–75, 1975–80, 1980–85, 1985–90.Columns 4–6 consist of changes for 1960–70, 1970–80, 1980–90. Columns 7–9 consist of changes for 1965–85. LogYt – 1 and St – 1 are the log GDP per capita and level of schooling in the initial year of each period. ∆S is the change inschooling between t – 1 and t divided by the number of years in the period. Data are from Summers and Hestonand Barro and Lee. Mean (and standard deviation) of annualized per capita GDP growth is .021 (.033) for columns1–3, .022 (.026) for columns 4–6, and .022 (.020) for columns 7–9.


greater over the five- and ten-year hori-zons, but it is still substantial overtwenty years. Since the change inschooling and initial level of GDP areessentially uncorrelated, the coefficienton the twenty-year change in schoolingin column 8 is biased downward by afactor of 1 − R∆S, which is around 40percent according to table 2. Thus, ad-justing for measurement error wouldlead the coefficient on the change ineducation to increase from .18 to .30 =.18/(1 – .4). This is an enormous returnto investment in schooling, equal tothree or four times the private return toschooling estimated within most coun-tries. The large coefficient on schoolingsuggests the existence of quite large ex-ternalities from educational changes(Lucas 1988) or simultaneous causalityin which growth causes greater educa-tional attainment. It is plausible that si-multaneity bias is greater over longertime intervals, so some combination ofvarying measurement error bias andsimultaneity bias could account forthe time pattern of results displayed intable 3.29

Like Benhabib and Spiegel, Barroand Sala-i-Martin (1995) conclude thatcontemporaneous changes in schoolingdo not contribute to economic growth.There are four reasons to doubt theirconclusion, however. First, Barro andSala-i-Martin analyze a mixed samplethat combines changes over both five-year (1985–90) and ten-year (1965–75 and1975–85) periods; examining changesover such short periods tends to exacer-bate the downward bias due to mea-surement errors. Second, they examinechanges in average years of secondaryand higher schooling. As was shown in

table 2, the cross-sectional reliability ofsecondary and higher schooling is lowerthan the reliability of all years ofschooling, and the changes are likely tobe less reliable as well. Third, they in-clude separate variables for changes inmale and female years of secondary andhigher schooling. These two variablesare highly correlated (r = .85), whichwould exacerbate measurement errorproblems if the signal in the variables ismore highly correlated than the noise.If average years of secondary andhigher schooling for men and womencombined, or years of secondary andhigher schooling for either men orwomen, is used instead of all years ofschooling in the ten-year change modelin column 6 of table 3, the change ineducation has a sizable, statistically sig-nificant effect. Fourth, they estimate arestricted Seemingly Unrelated Regres-sion (SUR) system, which exacerbatesmeasurement error bias because asymp-totically this estimator is equivalent toa weighted average of an OLS andfixed-effects estimator.

Barro (1997) stresses the importanceof male secondary and higher educa-tion as a determinant of GDP growth.In his analysis, female secondary andhigher education is negatively related togrowth. We have explored the sensitiv-ity of the estimates to using differentmeasures of education: namely, primaryversus higher education, and male ver-sus female education. When we test fordifferent effects of years of primary andsecondary and higher schooling in themodel in column 6 of table 3, we cannotreject that all years of schooling havethe same effect on GDP growth (p-value equals .40 for initial levels and .12for changes). We also find insignificantdifferences between primary and sec-ondary schooling if we just use maleschooling. We do find significant dif-ferences if we further disaggregate

29 An additional interpretation of the time pat-tern of results was suggested by a referee: it ispossible that externalities generated by educationare not realized over short time horizons, but arerealized over longer periods.


schooling levels by gender, however.The initial level of primary schooling hasa positive effect for women and a nega-tive effect for men, the initial level ofsecondary school has a negative effectfor women and a positive effect formen, the change in primary schoolinghas a positive effect for women and anegative effect for men, and the changein secondary schooling has a negativeeffect for women and a positive effectfor men.

Francesco Caselli, Gerardo Esquivel,and Fernando Lefort (1996) also exam-ine the differential effect of male andfemale education on growth over fiveyear intervals. They estimate a fixed ef-fects variant of equation (6), and instru-ment for initial education and GDPwith their lags. Contrary to Barro, theyfind that female education has a posi-tive and statistically significant effect ongrowth, while male education has anegative and statistically significant ef-fect. This result appears to stem fromthe introduction of fixed effects: if weestimate the model with fixed effectsbut without instrumenting for educa-tion, we find the same gender pattern,whereas if we estimate the model with-out fixed country effects and instrumentwith lags the results are similar toBarro’s. Although country fixed effectsarguably belong in the growth equation,it is particularly difficult to untangleany differential effects of male andfemale education in such a specifica-tion because measurement error is ex-acerbated.30 But Caselli, Esquivel, andLefort’s findings are consistent with themicro-econometric literature, which oftenfinds that education has a higher returnfor women than men.

We conclude that because schooling

levels are highly correlated for men andwomen, one needs to be cautious in-terpreting the effect of education inmodels that disaggregate education bygender and level of schooling. For thisreason, and because the total number ofyears of education is the variable speci-fied in the Mincer model, we have apreference for using the average of allyears of schooling for men and womencombined in our econometric analysis.

3.4 Initial Level of Education

The effect of the initial level of edu-cation on growth has been widely inter-preted as an indication of large exter-nalities from the stock of a nation’shuman capital on growth. Benhabib andSpiegel (1994, p. 160), for example,conclude, “The results suggest that therole of human capital is indeed one offacilitating adoption of technology fromabroad and creation of appropriate do-mestic technologies rather than enter-ing on its own as a factor of produc-tion.” And Barro (1997, p. 19) observes,“On impact, an extra year of male upper-level schooling is therefore estimatedto raise the growth rate by a substantial1.2 percentage points per year.” Topel(1999), however, argues that “the mag-nitude of the effect of education ongrowth is vastly too large to be inter-preted as a causal force.” Indeed, Topelcalculates that the present value of aone percentage point faster growth ratefrom an additional year of schoolingwould be about four times the cost,with a 5 percent real discount rate. Heconcludes that externalities from school-ing may exist, but they are unlikely tobe so large. One possibility—which weexplore and end up rejecting—is thatlevel of schooling is spuriously reflect-ing the effect of the change in schoolingon growth.

Countries with higher initial levelsof schooling tended to have larger

30 Note that instrumenting with lagged educa-tion does not solve the measurement error prob-lem because we find that measurement errors ineducation are highly correlated over time.


increases in schooling over the next tenor twenty years in Barro and Lee’s data,which is remarkable given that mea-surement error in schooling will inducea negative covariance between thechange and initial level of schooling.We initially suspected that the baselevel of schooling spuriously picks upthe effect of schooling increases, eitherbecause schooling changes are excludedfrom the growth equation or becausethe included variable is noisy. The fol-lowing calculations make clear that thisis unlikely, however.

To proceed, it is convenient to writethe cross-country growth equation as:

∆Yt = β0 + β1St − 1∗ + β2St

∗ + εt (7)

where asterisks signify the correctlymeasured initial and ending schooling

variables, and we have suppressed thecountry j subscript.31 We have also ig-nored covariates, but they could easilybe “preregressed out” in what follows. Ifall that matters for growth is the changein schooling, we would find β1 = –β2. Atest of whether the initial level of school-ing has an independent, positive effecton growth conditional on the change inschooling turns on whether β1 + β2 > 0.

In practice, equation (7) is estimatedwith noisy measures of schooling thathave serially correlated errors, as pre-viously documented. Under the assump-tion of serially correlated but otherwiseclassical measurement errors, it can be

TABLE 4THE EFFECT OF MEASUREMENT ERROR ON THE SUM OF SCHOOLING COEFFICIENTS


OLS IV

5-year changes 10-year changes 20-year changes 20-year changes

(1) (2) (3) (4) (5) (6) (7) (8)

St – 1 –.004(.003)

–.004(.003)

–.005(.002)

–.005(.002)

–.005(.003)

–.004(.003)

–.020(.010)

–.023(.011)

St .007(.003)

.008(.003)

.008(.002)

.009(.002)

.007(.003)

.009(.003)

.020(.009)

.028(.010)

Log Yt – 1 — –.006(.003)

— –.005(.003)

— –.013(.003)

— –.020(.006)

b1 + b2 .0026(.0005)

.0042(.0009)

.0023(.0005)

.0037(.0009)

.0020(.0008)

.0052(.0011)

.0001(.0015)

.0055(.0024)

Measurement ErrorCorrected b1 + b2

.0030 .0052 .0028 .0047 .0041 .0067 — —

R2 .197 .207 .272 .284 .159 .281 — —

N 607 607 292 292 97 97 67 67

Notes: All regressions include time dummies and an intercept. The standard errors in the first four columns allowfor correlated errors within countries over time. The time periods covered are the same as in table 4. In columns 7and 8, Kyriacou’s education data are used as instruments for Barro and Lee’s education data. All other columns onlyuse Barro and Lee’s education data. See text for description of the measurement error correction. Mean (andstandard deviation) of dependent variable are .021 (.033) for columns 1–2, .022 (.026) for columns 3–4, .022 (.020)for columns 5–6, and .019 (.019) for columns 7–8.

31 Notice that the scaling differs here from thatin tables 1 and 3: namely, we do not divide anyexplanatory variable by the number of years in theperiod in table 4.


shown that the limit of the coefficienton initial schooling is:

plim b1 =RSt − 1 − λr2

1 − r2β1 +

λ − RSt

1 − r2

×cov(St − 1,St)

var(St − 1)β2

(8)

where RSt – 1 and RSt are the reliabilityratios for St – 1 and St, r is the correlationbetween St – 1 and St, and λ = cov(St − 1

∗ ,St

∗)/cov(St – 1,St) is less than one if themeasurement errors are positively corre-lated. An analogous equation holds forb2. Some algebra establishes that thesum b1 + b2 has probability limit:

plim(b1 + b2)

= β1RSt − 1(1 − ψr) + λr(ψ − r)

1 − r2(9)

+ β2RSt(1 − ψ−1r) + λr(ψ−1 − r)

1 − r2

where ψ = var(St)/var(St – 1).Notice that if the variance in the

measurement errors and the variance intrue schooling are constant, then:

plim(b1 + b2) = (β1 + β2)RS + λr

1 + r(10)

where RS is the time-invariant reliabilityratio of the schooling data.32 Since (RS +λr)/(1 + r) is bounded by zero and one,in this case the sum of the coefficients isnecessarily attenuated toward zero, sowe would underestimate the effect of theinitial level of education. Hence, mea-surement error in schooling is unlikely todrive the significance of the initial effectof education.

Table 4 presents estimates of equa-tion (7) over five-, ten- and twenty-yearperiods. The bottom of the table reportsb1 + b2, as well as the measurement-error-corrected estimate of b1 + b2. Weestimated the numerator of λ using the

covariance between the 1990 WVS dataand lagged Barro-Lee data (either five-,ten- or twenty-year lags), and we esti-mated RS from the WVS data as well.33

Over each time interval, the results in-dicate that the negative coefficient oninitial education is not as large in mag-nitude as the positive coefficient onsecond-period education, consistentwith our earlier finding that the initiallevel has a positive effect on growthconditional on the change in education.Moreover, the correction for measure-ment error tends to raise b1 + b2 by.0004 to .0021 log points.

Finally, as an alternative approach tothe measurement error problem, in col-umns 7 and 8 we use Kyriacou’s school-ing measures as instruments for Barroand Lee’s schooling data. If the mea-surement errors in the two data sets areuncorrelated, one set of measures canbe used as an instrument for the other.Although the IV model can only be esti-mated for a subset of countries, theseresults also suggest that measurementerror in schooling is not responsible forthe positive effect of the initial level ofschooling on economic growth.34 More-over, if Barro and Lee’s data are usedto instrument for Kyriacou’s data inthis equation, the sum of the schoolingcoefficients in column (8) nearly doubles.

3.5 Measurement Error in GDP

Another possibility is that transitorymeasurement errors in GDP explain

32 Griliches (1986) derives the correspondingformula if measurement errors are serially uncor-related.

33 In models that include initial GDP, we firstremove the effect of initial GDP before calculat-ing RSt – 1, RSt and λ. In the models without initialGDP, we assume RSt – 1 = RSt.

34 If the model in columns (7) and (8) are esti-mated by OLS with the subsample of 67 countries,the results are virtually identical to those for thefull sample shown in columns (5) and (6). For ex-ample, if the model in column (6) is estimated forthe subsample of 67 countries, the coefficients onSt – 1 and St are –.004 and .009, and the estimate ofb1 + b2 after correcting for measurement error is.0060.


why initial schooling matters in thegrowth equation. Intuitively, this wouldwork as follows: If a country has a lowlevel of education for its measuredGDP, it is likely that its true GDP is lessthan its measured GDP. If the error inGDP is transitory, then subsequent GDPgrowth will appear particularly strongfor such a country because the negativeerror in the GDP is unlikely to repeatin the second period. One indicationthat this may contribute to the strongeffect of the level of education comesfrom including second period GDP in-stead of initial GDP in the growth equa-tion. In this situation, measurement er-rors in GDP would be expected to havethe opposite effect on the initial level ofeducation. And indeed, if second periodGDP is included instead of initial GDPin the model in column (7) of table 3, thecoefficient on initial education becomesnegative and statistically insignificant.

For two reasons, however, we con-clude that measurement error in GDPis unlikely to drive the significant effectof the initial schooling variable. First,in table 3 and table 4 it is clear that theinitial level of education has a signifi-cant effect even when initial GDP is notheld constant. Second, using the WVS,we calculated the reliability of the Sum-mers and Heston GDP data for 1990.Specifically, to estimate the reliabilityof log GDP, RY, we regressed the log ofreal income per person in the WVS onthe log of real GDP per capita in theSummers and Heston data. The result-ing coefficient was .92 (t-ratio .3), indi-cating substantial signal. Both measureswere deflated by the same PPP measurein these calculations, which may inflatethe reliability estimate, but if we addlog PPP as an additional explanatoryvariable to the regression the reliabilityof the GDP data is .89 (t-ratio = 11.9).Although the WVS income data neglectnon-household income and these esti-

mates are based on just seventeen coun-tries, the results indicate that Summersand Heston’s data convey a fair amountof signal, and that the errors in GDPare highly serially correlated. If we as-sume that RY is .92 and the serial corre-lation in the errors is .5, the coefficienton initial education in the ten-yearGDP growth equation would be biasedupward by about a third.35

3.6 The Effect of Physical Capital

The level and growth rate of capitalare natural control variables to includein the GDP growth regressions. First,initial log GDP can be substituted forcapital in a Solow growth model only ifcapital’s share is constant over time andacross countries (e.g., a Cobb-Douglasproduction function). Second, and moreimportantly for our purposes, the posi-tive correlation between education andcapital would imply that some of theincreased output attributed to highereducation in table 3 should be attributedto increased capital (see, e.g., ClaudiaGoldin and Lawrence Katz 1997 oncapital-skill complementarity). As men-tioned earlier, however, the endoge-nous determination of investment is areason to be wary about including thegrowth of capital directly in a GDPequation. Here we examine the robust-ness of the estimates to controlling forphysical capital.

Column (1) of table 5 reports an esti-mate of the same twenty-year growth modelas in column 9 of table 3, augmented to

35 With constant variances, the limit of the coef-ficient on initial log GDP is RYβ – (1 – RY)(1 – r),where RY is the reliability of log GDP, β is thepopulation regression coefficient with correctly-measured GDP, and r is the serial correlation inthe measurement errors. To estimate the effect ofmeasurement error in GDP on the schooling coef-ficient, we constrained the coefficient on initialGDP to equal {b + (1– RY)(1 – r)}/RY, where b isthe coefficient on initial GDP obtained by OLSwithout correcting for measurement error, andre-estimated the growth equation.


include the growth of capital perworker. We use Klenow and Rodriguez-Clare’s (1997) capital data because theyappear to have more signal than Ben-habib and Spiegel’s capital data.36 Thecoefficient on the change in educationfalls by more than 50 percent whencapital growth is included, although itremains barely statistically significant atthe .10 level. In column (2) we add theinitial log capital per worker, and in col-umn (3) exclude the initial log GDPfrom the column (2) specification. In-

cluding the initial log of capital drivesthe coefficient on the change in school-ing to close to zero. Notice also that theinitial log of capital per worker has littleeffect in columns (2) and (3).37 Thegrowth of capital per worker, however,has an enormous effect on GDP growth.With Cobb-Douglas technology andcompetitive factor markets, the coeffi-cient on the growth in capital in table5 would equal capital’s share; instead,the coefficient is at least double capi-tal’s share in most countries (see Gol-lin 1998). This finding suggests endo-geneity bias is a problem. To explore

TABLE 5THE EFFECT OF SCHOOLING AND CAPITAL ON ECONOMIC GROWTH

DEPENDENT VARIABLE: ANNUALIZED CHANGE IN LOG GDP PER CAPITA, 1965–85

OLS OLS IV

(1) (2) (3) (4) (5) (6)

∆S .066(.039)

.017(.032)

.015(.042)

.083(.043)

.013(.052)

.069(.167)

S65 .004(.001)

.0013(.0008)

.0005(.0010)

.002(.001)

.0006(.0011)

–.0001(.002)

Log Y65 –.009(.003)

–.026(.003)

— — — —

∆ Log Capital per Worker .598(.062)

.795(.058)

.648(.073)

.35∗ .608(.083)

.597(.120)

Log Capital per Worker 1960 — .016(.002)

.002(.002)

–.002(.002)

.001(.002)

.001(.004)

R2 .63 .76 .58 .12 .56 .55

Sample Size 92 92 92 92 66 66

Notes: Change variables have been divided by the number of years spanned by the change (20 years for schoolingand log GDP, 25 years for capital). Schooling data used in the regressions are from Barro and Lee. Capital data arefrom Klenow and Rodriguez-Clare (1997), and pertain to 1960–85. The coefficient on the change in log capital incolumn 4 is constrained to equal .35, which is roughly capital’s share. The instrumental variables model incolumn (6) uses Kyriacou’s schooling data as excluded instruments for the level and change in Barro-Lee’s schoolingvariables. The model in column (5) is estimated by OLS for the same subset of countries used to estimate the modelin column (6).

36 A regression of Benhabib and Spiegel’schange in log capital on the corresponding vari-able from Klenow and Rodriguez-Clare yields aregression coefficient (and standard error) of .95(.065). The reverse regression yields a coefficientof .69 (.05). Hence, Klenow and Rodriguez-Clare’smeasure appears to have a high signal-to-noiseratio.

37 If the change in log capital per worker isdropped from the model in column (3), then ini-tial log capital per worker does have a statisticallysignificant, negative effect, and the schooling coef-ficients are similar to those in column 9 of table 3.


the sensitivity of the results, in column(4) we constrain the coefficient on thegrowth in capital to equal 0.35, which ison the high end of the distribution ofnon-labor’s share around the world.These results indicate that both thechange and initial level of schooling areassociated with economic growth. More-over, the coefficient on the change ineducation is quite similar to that foundin microeconometric studies.

As mentioned earlier, controlling forcapital exacerbates the measurementerror in schooling. Indeed, we find thatthe reliability of Barro-Lee’s twenty-year change in schooling data falls from.58 to .46 once we condition on thechange in capital, suggesting that thecoefficient on the change in schoolingin columns 1–3 of table 5 should beroughly doubled.38 In column (6), totry to overcome measurement error weestimate the growth equation by in-strumental variables, using Kyriacou’sschooling data as excluded instrumentsfor the change and level of schooling.(Because Kyriacou’s data are only avail-able for 66 of the countries in the sam-ple, the sample used in column (6) issmaller than that used for OLS; column(5) uses the same subsample of 66countries to estimate the model byOLS.) This is the same estimation strat-egy previously used by Pritchett (1998),but we employ different schooling dataas instruments. Unfortunately, becausethere is so little signal in education con-ditional on capital, the IV results yield ahuge standard error (.167). Pritchettsimilarly finds large standard errors

for his IV estimates, although hispoint estimates are negative.39 One fi-nal point on these estimates is that, tobe comparable to the Mincerian returnto schooling, the coefficient on thechange in education should be dividedby labor’s share if the aggregate produc-tion function is Cobb-Douglas and hu-man capital is an exponential functionof years of schooling. This would raisethe cross-country estimate of the returnto schooling even further.

We draw four main lessons from thisinvestigation of the role of capital.First, the change in capital has an enor-mous effect in a GDP growth equation,probably because of endogeneity bias.Second, the impact of both the leveland change in schooling on economicgrowth is sensitive to whether thechange in capital is included in thegrowth equation and allowed to have acoefficient that greatly exceeds capital’sshare. Third, controlling for capital ex-acerbates measurement error problemsin schooling. Instrumental variables es-timates designed to correct for measure-ment error in schooling yield such alarge standard error on the change inschooling that the results are consistentwith schooling changes having no effecton growth or a large effect on growth.Fourth, when the coefficient on capitalgrowth is constrained to equal a plausi-ble value, changes in years of school-ing are positively related to economicgrowth. Overall, unless measurementerror problems in schooling are over-come, we doubt the cross-country growthequations that control for capitalgrowth will be very informative inso-far as the benefit of education isconcerned.

38 Temple (1999b) finds that eliminating obser-vations with large residuals causes the coefficienton the growth in education in Benhabib andSpiegel’s data to rise and become statistically sig-nificant, conditional on the growth in capital. Wefind a similar result with Benhabib and Spiegel’sdata, although similarly eliminating outliers has lit-tle effect on the results in table 5 which use theBarro and Lee education data.

39 Aside from the different data sources, the dif-ference between our IV results and Pritchett’s ap-pears to result from his use of log schoolingchanges. If we use log schooling changes, we alsofind negative point estimates.


4. Less Restrictive Macro Growth Model

The macro growth equations imposethe restriction that all countries havethe same relationship between growthand initial education, and that the rela-tionship is linear. The first assumptionis particularly worrisome because themicro evidence indicates that the returnto schooling varies considerably acrosscountries, and even across regionswithin countries. For example, institu-tional factors that compress the wagestructure in some countries result inlower returns to schooling in thosecountries (see, e.g., the essays in Rich-ard Freeman and Lawrence Katz 1995).One might expect externalities fromeducation to be greater in countrieswhere the private return is depressedbelow the world market level. Perhapsmore importantly, differences in thequality of education among countrieswith a given level of education shouldaffect the speed with which new tech-nology is adopted or innovated, andgenerate cross-country heterogeneity inthe coefficient on education. We there-fore allow the effect of the stock of edu-cation on growth to vary by country.Next we relax the assumption of a linearrelationship between growth and initialeducation. Both of these extensions tothe standard growth specification sug-gest that the constrained linear specifi-cation estimated in the literature shouldbe viewed with caution.

4.1 Heterogeneous Country Effectsof Education

Consider the following variable-coefficient version of the macro growthequation:

∆Yjt = β0 + β1jSj,t − 1 + εj

j = 1, . . . , N and t = 1, . . . , T(11)

where we allow each country to have aseparate schooling coefficient (β1j) and

ignore other covariates.40 If there is morethan one observation per country, equa-tion (11) can be estimated by interactingeducation with a set of dummy variablesindicating each country. Denote b1j as theestimated values of β1j. It is instructiveto note that the coefficient on educationestimated from an OLS regression with ahomogenous education slope, denotedb1, can be decomposed as a weightedaverage of the country-specific slopes(b1j). That is,

b1 = ∑wjj

b1j =

(12)

∑j

∑(t − 1

Sj,t − 1 − S−)2 + TS−(S−j − S−)

∑j

∑(t − 1

Sj,t − 1 − S−)2

b1j

where the weights are the country-specific contributions to the variancein schooling plus a term representingthe deviation between each country’smean schooling (S−j) and the grand mean(S−) .

Of course, if the assumption of aconstant-coefficient model and the otherGauss-Markov assumptions hold, theOLS weights (wj) are the most efficient;they also yield more robust results inthe presence of measurement error. Butif a variable-coefficient model is appro-priate, there is no a priori reason toprefer the OLS weights. Indeed, if thecountry-specific slopes are correlatedwith the weights, then OLS will yield anestimate that diverges from that for theaverage country in the world. A morerelevant single estimate in this caseprobably would be the unweighted-average coefficient (Σb1j/N), which rep-resents the expected value of the edu-cation coefficient for countries in the

40 See Cheng Hsiao (1986, ch. 6) for an over-view of variable-coefficient models in panel data.


sample.41 One reason why the weightsmight matter is that researchers havefound a positive correlation betweenschool quality and educational attainment(e.g., Behrman and Nancy Birdsall1984).

Table 6 summarizes estimates of avariable-coefficient model using five-year and ten-year changes in GDP.Panel A reports results of regressing

GDP growth on average years of school-ing for the population age 25 and older,initial GDP and time dummies. Columns1 and 3 report the constant-coefficientmodel, whereas columns 2 and 4 reportthe mean of the country-specific educa-tion coefficients. The constant educationslope assumption is overwhelmingly re-jected by the data for each time span(p-value < 0.0001). Of more impor-tance, the average slope coefficient isnegative, though not statistically signifi-cant, in the variable-coefficient model.These results cast doubt on the inter-pretation of initial education in theconstrained macro growth equationcommon in the literature.

Panel B of table 6 reports results inwhich average years of secondary andhigher schooling for males is used in-stead of average years of all educationfor the entire adult population. This

TABLE 6MEAN ESTIMATES FROM A RANDOM COEFFICIENT SPECIFICATION


5-Year Changes 10-Year Changes

ConstantCoefficient

(1)

Mean Variable-Coefficient Estimate

(2)

ConstantCoefficient

(3)

Mean Variable-Coefficient Estimate

(4)

A. All Years of Schooling

Coefficient Estimate for St – 1 .0040(.0007)

–.0033(.0036)

.0033(.0008)

–.0064(.0059)

p-value — .000 — .000

R2 .197 .481 .242 .690

B. Male Secondary and Higher Schooling

Coefficient Estimate for MaleSecondary + St – 1

.0088(.0017)

–.0196(.0114)

.0081(.0020)

–.0353(.0179)

p-value — .0000 — .0000

R2 .190 .469 .242 .658

Notes: All regressions control for initial Log GDP per capita and time dummies. The number of countries is 110 forthe five-year change equations and 108 for the ten-year change models. The p-value is for test of equality ofcountry-specific education coefficients in the variable coefficient model. Sample size is 607 in columns 1–2 and 292in columns 3–4.

41 Notice that if equation (11) is augmented toinclude covariates, the simple weighted averageinterpretation of the constant-coefficient modelin (12) does not apply, but the average of thecountry-specific coefficients is still informative. Ifcountry fixed effects are included as covariates inequation (11), however, the OLS constant coeffi-cient can still be decomposed as a weighted aver-age of the country-specific coefficients even ifthere are other covariates. But we exclude countryfixed effects so that these estimates are compara-ble to the earlier ones, and because includingfixed effects would greatly exacerbate measure-ment error bias.


variable has been emphasized as a keydeterminant of economic growth inBarro’s work. Again, however, the re-sults of the constant-coefficient modelare qualitatively different than those ofthe variable-coefficient model. Indeed,for the average country in the sample,a greater initial level of secondaryand higher education has a statisticallysignificant, negative association witheconomic growth over the ensuing tenyears.

If a constant-coefficient model is appro-priate, estimating a variable-coefficientmodel places greater demands on thedata and measurement error bias islikely to be exacerbated compared withestimating a constant-coefficient OLSmodel. Nevertheless, we suspect thatmeasurement error in schooling cannotfully account for the qualitatively differ-ent results in the variable-coefficientmodel. First, classical measurement er-ror would not be expected to cause theeffect to switch signs. Second, althoughmany more parameters are estimated inthe variable-coefficient model, we takethe average of the coefficients, whichimproves precision. Third, to gauge thelikely impact of measurement error inthe variable-coefficient model, we con-ducted a series of simulations in whichwe randomly generated correctly mea-sured data that conformed to a homoge-neous coefficient model, and then esti-mated the variable-coefficient model withsimulated noisy schooling data. Thesimulated data had roughly the samevariances, measurement error and serialcorrelation properties as the actual data.With the simulated noisy data, the aver-age schooling coefficient was about halfas large when we estimated a variable-coefficient model as it was when we es-timated a constant-coefficient model.42

Thus, attenuation bias due to measurementerror is greater if a variable-coefficientmodel is estimated, but we would ex-pect to still be able to detect a positiveeffect of education with the variable-coefficient estimator if the correct modelhad a constant coefficient of roughlythe same order of magnitude as thatfound in the literature.

It appears from table 6 that educa-tion has a heterogenous effect on eco-nomic growth across countries. Whatbearing does this finding have on theconvergence literature? Kevin Lee, M.Pesaran and Ron Smith (1998) show thatcountry heterogeneity in technologicalprogress that is assumed homogeneousacross countries in a fixed-effects modelwith a lagged dependent variable willgenerate a spurious correlation betweenthe lagged dependent variable and theerror term. A similar result will followif heterogeneous education coefficientsare constrained to equal a constant co-efficient, so we would regard the con-vergence coefficient with some cautionsince it depends on controlling for St – 1.Nonetheless, it is worth emphasizingthat we still obtain a negative averagecoefficient on education if we drop initiallog GDP from the variable-coefficientmodel. Because we are interestedin understanding the role of educationin economic growth, we do not pursuethe convergence issue further, but wethink the results of the variable-coefficientmodel reinforce Lee, Pesaran, and Smith’sskeptical interpretation of the con-ventional estimate of the convergenceparameter.

4.2 The Importance of Linearity

It is common in the empirical growthliterature to assume that the initial levelof education has a linear effect on sub-sequent GDP growth. The linear speci-fication is more an ad hoc modeling

42 We also controlled for initial GDP and timedummies in these simulations.


assumption than an implication of aparticular theory. Moreover, the resultsin table 6 suggest that linearity isunlikely to hold. The importance ofthe linearity assumption has not beenexplored extensively in growth models.

To probe the linear specification, wedivided the sample into three subsam-ples of countries, based on whethertheir initial level of education was inthe bottom, middle or top third of thesample. We then estimated the modelsin table 3 separately for each subsam-ple. The results consistently indicatedthat education was statistically signifi-cantly and positively associated withsubsequent growth only for the coun-tries with the lowest level of education.For countries in the middle of the edu-cation distribution, growth was typicallyunrelated or inversely related to educa-tion, and for countries with a high levelof education growth was typically in-versely related to the level of education.Similar results were obtained if we usedthe full sample and estimated the effectof a quadratic function of education. Forexample, if we use this specification ofeducation in the model in column 4 oftable 3, the relationship is inverted-Ushaped, with a peak at 7.5 years of edu-cation. Because the mean education levelfor OECD countries in 1990 was 8.4 yearsin Barro and Lee’s data, the average OECDcountry is on the downward-slopingsegment of the education-growth pro-file.43 These findings underscore W.Arthur Lewis’s (1964) observation that,“it is not possible to draw a simplestraight line relating secondary educa-

tion to economic growth.” The positiveeffect of the initial level of educationon growth seems to be a phenomenonthat is confined to low-productivitycountries.

5. Conclusion

The micro and macro literatures bothemphasize the role of education in in-come growth. A large body of researchusing individual-level data on educationand income provides robust evidence ofa substantial payoff to investment ineducation, especially for those who tradi-tionally complete low levels of school-ing. From this micro evidence, however,it is unclear whether the social returnto schooling exceeds the private return,although available evidence suggests thatpositive externalities in the form of re-duced crime and reduced welfare par-ticipation are more likely to be reapedfrom investments in disadvantaged thanadvantaged groups. The macro-economicevidence of externalities in terms oftechnological progress from invest-ments in higher education seems tous more fragile, resulting from impos-ing constant-coefficient and linearityrestrictions that are rejected by the data.

Our findings may help to resolve animportant inconsistency between themicro and macro literatures on education:Contrary to Benhabib and Spiegel’s(1994) and Barro and Sala-i-Martin’s(1995) conclusions, the cross-countryregressions indicate that the change ineducation is positively associated witheconomic growth once measurement er-ror in education is accounted for. In-deed, after adjusting for measurementerror, the change in average years ofschooling often has a greater effect inthe cross-country regressions than in thewithin-country micro regressions. Thelarger return to schooling found inthe cross-country models suggests that

43 Although these findings may appear surpris-ing in light of the macro growth literature, theyare consistent with results in Barro (1997; table1.1, column 1). In particular, the interaction be-tween male upper-secondary education and logGDP has a negative effect on growth, and the re-sults imply the effect of schooling on growth be-comes negative for countries whose GDP exceedsthe average by 1.9 log units.


reverse causality or omitted variablescreate problems at the country level ofanalysis, or that increases in averageeducational attainment generate nation-wide externalities. Although the micro-econometric evidence in several coun-tries suggests that within countries thecausal effect of education on earningscan be estimated reasonably well bytaking education as exogenous, it doesnot follow that cross-country differ-ences in education can be taken as acause of income as opposed to a resultof current income or anticipated incomegrowth. Moreover, countries that improvetheir educational systems are likely toconcurrently change other policies thatenhance growth, possibly producing adifferent source of omitted-variable biasin cross-country analyses.

“Education,” as Harbison and Myers(1965) stress, “is both the seed and theflower of economic development.” It isdifficult to separate the causal effectof education from the positive incomedemand for education in cross-countrydata over long time periods. N. G.Mankiw (1997) describes the presumedexogeneity of the explanatory variables,including human capital accumulation,as the “weak link” in the empiricalgrowth literature. In our opinion, thislink is unlikely to be strengthened un-less researchers can identify naturalexperiments in schooling attainmentsimilar to those that have been exploitedin the microeconometric literature, andunless measurement errors in the cross-country data are explicitly taken intoaccount in the econometric modeling.In view of the difficulties in obtainingaccurate country-level data on changesin educational attainment, it might bemore promising to examine growthacross regions of countries with reliabledata. Acemoglu and Angrist (1999), wholook across U.S. states, and James Rauch(1993) and Enrico Moretti (1999), who

look across U.S. cities, provide goodstarts down this path, although theyreach conflicting conclusions regardingany deviation between the social andprivate returns to education.

Data AppendixThe second wave of the World Values Survey

(WVS) was conducted in 42 countries between1990 and 1993. The sampled countries repre-sented almost 70% of the world population, in-cluding several countries where micro data nor-mally are unavailable. The survey was designed bythe World Values Study Group (1994), and con-ducted by local survey organizations (mainly Gal-lup) in each of the surveyed countries. In mostcountries, a national random sample of adults(over age 18) was surveyed. For 12 of the coun-tries in our sample (Belgium, Brazil, Canada,China, India, Italy, Netherlands, Portugal, Spain,Switzerland, West Germany and U.K.), samplingweights were available to make the survey repre-sentative of the country’s population; the othersamples are self-weighting. A feature of the surveyis that the questionnaire was designed to be simi-lar in all countries to facilitate comparisons acrosscountries. There are, however, drawbacks to usingthe WVS for our purposes. The primary purposeof the WVS was to compare values and normsacross different societies. Although questionsabout income and education were included, theyappear to have been a lower priority than the nor-mative questions. For example, family income wascollected as a categorical variable in ten ranges,and some countries failed to report the currencyvalues associated with the ranges. We were able toderive comparable data from the WVS on meanyears of schooling for 34 countries and on meanincome for 17 countries.

Mean years of schooling is calculated from ques-tion V356 in the WVS, which asked, “At what agedid you or will you complete your formal educa-tion, either at school or at an institution of highereducation? Please exclude apprenticeships.” Thevariable is typically bottom coded at 12 years ofage and top coded at 21 years of age. Althoughthere are some benefits of formulating the ques-tion this way, for our purposes it also creates someproblems. First, we do not know the age at whichrespondents started their education. For this rea-son, we have used data from UNESCO (1967) onthe typical school starting age in each country.Second, the top and bottom coding is potentially aproblem. For almost one third of the countries(Austria, Brazil, Denmark, India, Norway, Poland,South Korea, Sweden, Switzerland and Turkey),however, a question was asked concerning formaleducational attainment. Since, as mentioned above,one of the benefits with the WVS is that the samequestions are asked in all the countries, we usedthis variable only to solve the bottom and top


coding problem.44 We have coded illiterate school-ing as 0 years of schooling and incomplete primaryschooling as 3 years. In the two countries wheregraduate studies are a separate category, we haveset this to 19. For the countries in which the edu-cational attainment variable does not exist, we setyears of schooling for those in the bottom-codedcategory equal to the midpoint of 0 and the bot-tom coded years of schooling.45 Similarly, we setyears of schooling for the highest category equal to

the midpoint of 18 and the top coded years ofschooling.

As mentioned, the family income variable inWVS is reported in 10 categories. We coded in-come as the midpoints of the range in each cate-gory. This variable is also censored from belowand above. For simplicity, we set income for thosewho were bottom coded at the midpoint betweenzero and the lower income limit. We handled topcoding by fitting a Pareto distribution to familyincome above each country’s median income. As-suming that this distribution correctly charac-terizes the highest category, we calculated themean of the censored distribution. We convertedthe family income variable to a dollar-valueequivalent by multiplying the family income vari-able in each country by the ratio of the purchasingpower parity in dollars to the corresponding localcurrency exchange, using Summers and Heston’s(1991) data.

The logarithm of mean income per capita wascalculated as the logarithm of the sum of familyincome in common currency divided by the totalnumber of individuals in all households in thesample. The total number of individuals in each

APPENDIX TABLE A1CORRELATION AND COVARIANCE MATRICES FOR BARRO-LEE AND KYRIACOU

YEARS OF SCHOOLING DATA

A. Correlation MatrixS65

BL S85BL S65

K S85K ∆SBL ∆SK

S65BL 1.00

S85BL 0.97 1.00

S65K 0.91 0.92 1.00

S85K 0.81 0.86 0.88 1.00

∆SBL 0.23 0.46 0.36 0.51 1.00

∆SK –0.12 –0.03 –0.17 0.33 0.34 1.00

B. Covariance MatrixS65

BL S85BL S65

K S85K ∆SBL ∆SK

S65BL 6.65

S85BL 7.07 8.01

S65K 5.66 6.29 5.88

S85K 5.27 6.19 5.38 6.41

∆SBL 0.42 0.93 0.62 0.92 0.51

∆SK –0.39 –0.10 –0.50 1.02 0.30 1.52

Notes: Sample size is 68. A superscript BL refers to the Barro-Lee data and asuperscript K refers to the Kyriacou data. The subscript indicates the year. Unlikethe other tables, the change in schooling is not annualized.

44 For South Korea and Switzerland, however,we exclusively used this variable to derive years ofschooling because the question about school leav-ing age is not asked in these countries. For Tur-key, school leaving age is only coded as three pos-sible ages, so we use both the educationalattainment and school leaving age variable to de-rive years of schooling.

45 For East and West Germany the bottom codewas 14, and for Finland it was 15. Because schoolstart age was 7 in Finland and East Germany, and6 in West Germany, we set years of schoolingequal to 6 in West Germany and Finland and 5 inEast Germany for those who were bottom coded.


APPENDIX TABLE A2INTERNATIONAL DATA DERIVED FROM THE WORLD VALUES SURVEY

Country

Mean yearsof schooling

(Std. deviation)Log family

income per capita Survey Year Sample Size

Argentina 10.23 (4.88) — 1991 766

Austria 8.69 (4.88) 8.78 1990 1,296

Belgium 11.53 (3.29) 8.92 1990 2,328

Bulgaria 11.29 (3.83) — 1990 877

Brazil 4.04 (3.04) — 1991–92 1,154

Canada 12.60 (3.19) 9.48 1990 1,483

Czechoslovakia 11.78 (2.86) — 1990 1,190

Chile 10.48 (4.37) 7.81 1990 1,137

China 10.32 (3.51) — 1990 745

Denmark 12.50 (3.66) — 1990 862

East Germany 9.12 (3.90) — 1990 1,175

Finland 12.61 (3.81) 9.00 1990 534

France 11.12 (3.62) — 1990 830

Hungary 9.79 (3.57) 7.91 1990 895

Iceland 12.16 (3.74) — 1990 575

Ireland 10.20 (2.81) — 1990 847

India 2.97 (4.48) 7.07 1990 1,908

Italy 7.88 (4.90) 9.02 1990 1,616

Japan 12.29 (2.85) 9.10 1990 855

Mexico 8.44 (5.47) — 1990 835

Netherlands 11.89 (3.65) 9.17 1990 876

Norway 13.43 (4.46) 9.20 1990 1,063

Poland 10.11 (3.56) — 1989 803

Portugal 6.12 (4.79) 8.41 1990 823

Romania 10.50 (4.36) — 1993 933

Russia 12.35 (3.67) — 1991 1,551

Spain 8.61 (4.49) 8.24 1990 2,991

South Korea 12.00 (3.58) — 1990 1,040

Sweden 12.79 (3.40) — 1990 848

Switzerland 8.63 (2.61) — 1988–89 1,154

Turkey 6.13 (4.65) 8.09 1990–91 805

U.K. (excl. N.I.) 11.20 (2.50) 9.17 1990 1,288

USA 13.26 (2.96) 9.49 1990 1,477

West Germany 9.78 (3.34) 9.19 1990 1,770

Note: Sample size pertains to the number of observations used to calculate years of schooling.


household is calculated as the sum of the numberof children living at home and the number ofadults present. (Two adults were assumed to bepresent if the respondent was married; otherwise,one adult was assumed to be present.) AppendixTable A2 reports the weighted mean years ofschooling and log income per capita derived fromthe WVS. The weights for these calculations werethe sampling weights reported in the WVS. Thesample size used to calculate mean schooling isalso reported.

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EducationforGrowth: WhyandForWhom? 2000_kruegerlindahl.pdf · 5 The German figures are from Krueger and Jorn-Steffen Pischke (1995). The American and Swedish figures are based on