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American Economic Association

Natural "Natural Experiments" in EconomicsAuthor(s): Mark R. Rosenzweig and Kenneth I. WolpinSource: Journal of Economic Literature, Vol. 38, No. 4 (Dec., 2000), pp. 827-874Published by: American Economic AssociationStable URL: http://www.jstor.org/stable/2698663

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Journal of Economic Literature

Vol. XXXVIII(December 2000) pp. 827-8 74

a t u r a l Natural Experiments '

in Economics

MARK R. ROSENZWEIGand KENNETHI. WOLPIN1

1. Introduction

THE COSTLINESS OF and limitationson experiments involving human

subjects have long been identified as ma-

jor constraints on the progress of eco-

nomic science. Indeed, it has been in-

creasingly recognized that identification

of many interesting parameters, such as

the effects of schooling or work experi-

ence on earnings or of income on sav-

ings, requires attention to the fact that

the variation in many of the variables

whose effects are of interest may not be

orthogonal to unobservable factors that

jointly affect the outcomes studied. Such

unmeasured or unmeasurable factors

may include pre-existing or endowed

skills ( ability ), preferences, or tech-

nologies that vary across individuals or

firms in the economy. The possible exis-

tence of heterogeneity in these attributes

means that almost all estimates are open

to alternative interpretations in terms ofself-selection by such traits. In determin-

ing the returns to schooling, for example,

individuals cannot be considered to be

randomly sorted among schooling levels.

Thus, that more-schooled individuals

have higher earnings may reflect the fact

that more able individuals prefer school-ing or face lower schooling costs. Simi-

larly, that fertility and female labor sup-

ply are negatively correlated may reflect

variation in preferences for children and

work in the population.Economists have used experiments

that purposively randomize treatments

to assess their effects in the presence of

heterogeneity. Among the issues that

some of the most prominent experi-ments have addressed are the impact of

a negative income tax on labor supply,the effects of class size on test out-

comes, and the effects of job training

programs on earnings. However, these

man-made experiments are subject to

the criticisms that they lack gener-

alizability and, most importantly, often

do not adhere in implementation to the

requirements of treatment randomness.

The most widely applied approach to

identifying causal or treatment effects,

which has a long history in economics,employs instrumental variable tech-

niques. This approach essentially as-

sumes that some components of non-

experimental data are random. That is,

it is assumed that some variable or

event satisfies the criterion of random-

ness -the event or variable is orthogo-

nal to the unobservable and unmalle-

able factors that could affect the

outcomes under study. This assumption,

along with a set of additionalassumptions

1University of Pennsylvania.We are grateful totwo anonymousreferees and the editor for helpfulcomments on an earlier draft of this paper. Partialsupport for the research was provided by NIH

grants HD30907 and AG11725 and NSF grantsSBR95-11955 and SBR93-08405.

827



828 Journal of Economic Literature, Vol. XXXVIII (December 2000)

about behavior, yields estimates of eco-nomic parameters that are of generalinterest, e.g., the returns to schooling,

the income elasticity of savings. Notsurprisingly, the assumptions made, in-clusive of randomness, are subject tomuch skepticism.

Given the difficulties of carrying outand financing experiments with near-perfect random treatments to answerquestions of general importance andthe lack of credibility of many of theassumptions of standard instrumentalvariable studies, economists as well as

researchers in other fields have soughtout natural experiments, randomtreatments that have arisen serendipi-tously. These putative natural experi-ments are usually changes or spatialvariation in rules governing behavior,which are assumed to satisfy the ran-domness criterion. Indeed, 72 studiesusing the phrase natural experimentin the title or abstract issued or pub-lished since 1968 are listed in the Jour-nal of Economic Literature cumulativeindex.2 Many of these studies do notproduce easily generalizable results aboutbehavior because of the specific natureof the rule changes that are studied, asin the randomized-experiment litera-ture. The major problem with these

studies, however, is that the assumptionof randomness is not credible.

In recent years economists, in recog-

nition that nature provides almostperfect randomness with respect to im-

portant variables, have ingeniously ex-ploited naturally random events as in-strumental variables.3 These natural

natural experiment studies have at-tracted a great deal of attention bothbecause of the appeal of the instru-ments and because the studies have ad-dressed important questions in econom-ics. Five major random outcomes thatarise from biological and climate mech-anisms have been used as instruments:twin births, human cloning (monozy-gotic twins), birth date, gender, andweather events. These natural out-

comes, which are plausibly random withrespect to at least two of the majorsources of heterogeneity in humanpopulations-tastes and abilities-havebeen used to study three issues: Whatare the returns to schooling and labormarket experience? How sensitive areconsumption, savings, and labor supplyto temporary and permanent changesin income? How responsive is women'slabor force participation to fertilitychange?

This review essay examines this re-cent literature exploiting natural eventsas instruments to assess to what extentit has advanced empirical knowledge.The advantage of the natural natural ex-perimental approach is that the assump-tion of randomness for the instrumentalvariables employed is more crediblethan for those instruments used in al-

most all other studies. But a weaknessof many of the studies that adopt thisapproach is that the necessary addi-tional behavioral, market, and techno-logical assumptions needed to justify theauthors' interpretations of the estimatesobtained are absent. The impression

2 Among the natural experiments in thesestudies are changes in nineteenth-century Brook-lyn welfare laws, cross-country differences in EastAfrican educational policies, the introduction of aCivil-War-eraunion pension plan, cross-state dif-ferences in wage distributions, trade policy reformin New Zealand, the passage of the U.S. Tax Re-form Act of 1986, differences in salary restrictionsacross U.S. professional basketball and baseball,the introduction of Eastern European privatiza-tion rules, changes in Ohio rules for financingmental health care, and British dividend tax re-forms.

3 Other scientists have also exploited naturalevents, the most prominent studies being thosebased on human cloning (twins) that attempt toidentify the separate roles of genetics and environ-ment (e.g., K. McCourt, T. J. Bouchard, David T.Lykken, M. A. Tellegen, M. Keyes 1999).



Rosenzweig and Wolpin: Natural Natural Experiments 829

left by this literature is that if one ac-cepts that the instruments are perfectlyrandom and plausibly affect the variablewhose effect is of interest, then the in-

strumental-variables estimates are con-clusive. Indeed, part of the appeal ofthis literature is its simplicity, in con-trast, for example, to the structural esti-mation literature, in which complex es-timation strategies are used to identifythe structural parameters of fully param-eterized but highly restrictive models. Acharacteristic of this approach is that allassumptions are transparent, but thestructure of these models incorporates,as does any economic model, strong andsometimes unappealing assumptionsabout behavior or markets, and aboutfunctional forms and statistical distri-butions, often made strictly for reasonsof tractability.

However, the absence of models inthe natural natural experiment litera-ture does not mean that there are noimportant and implausible assumptions

being implicitly used by the authors ininterpreting the estimates they have ob-tained. Randomness and explanatorypower are necessary but not sufficientconditions for identification of a pa-rameter that is of interest. Moreover, inthe few cases where an explicit model isused to motivate the specification andexclusion restrictions used, it is not al-ways clear how robust is the study's in-terpretation to even minor changes in

the model. In this review we (i) summa-rize the methodology and findings fromtwenty studies employing natural eventsas instruments; (ii) examine and clarifythe set of assumptions, beyond the ran-domness of the natural events, that areimplicitly made in these studies thatlead to the authors' conclusions aboutthe empirical results obtained; (iii) showhow the relaxation of some of theserestrictions, consistent with empiricalevidence or with well-established mod-

els and/or evidence in the literature,changes the interpretation of the re-sults; and (iv) provide additional em-pirical evidence on the validity of these

implicitly made assumptions using thesame set of natural events. We clarifythe assumptions and the interpretationof the studies' findings by constructingsimple economic models pertinent tothe phenomena studied. The new evi-dence is used to suggest the additionalresearch, empirical and theoretical, that isneeded to obtain a more reliable under-standing of the results from this litera-ture and for future inquiries using thenatural natural experimental approach.

2. Instrumental Variables, NaturalNatural Experiments,and the Role

of Economic Theory

To clarify the empirical methodologythat underlies the natural natural ex-periment studies and to highlight the is-sues which we will illuminate by em-ploying simple behavioral models in this

review essay, it is useful to start with apresentation of the statistical modelused in almost all of the natural naturalexperiment studies in its simplest form.The first element is the equation that

contains the parameter of interest 13:

Y= OC+X+ ?. (1)

The canonical problem is that in thepopulation X is correlated with the error

term ? so that least squares estimates of

,1 will be biased. The solution proposed

is some variable Z that affects X but is

not correlated with a.4 This variable is

then used as an instrument for X, and

the instrumental variables estimator is:

cov(Y,Z) cov(X,Z)P+ COv(E,Z) (2

COV(X,Z) COV(X,Z)

4 Most studies in this literature in fact conve-

niently assume that only one X is correlated with

C, since then only one natural natural instrumentis required.




A variant of (2), applied frequently in

the natural natural experiment literature,

is the Wald estimator, which is simply

an instrumental variables estimator based

on grouped data (Abraham Wald 1940).

As seen in (2), identification of ,B hus

requires that Z and X covary but not Z

and ?. Each study must therefore define

what is in the error term in order to

provide a plausible story for why the in-

strument Z is not correlated with it.

The description of what is in the error

term is thus the critical part of all stud-

ies employing instrumental variables.

Because what is in the error term de-pends in turn on the specification of the

equation of interest, it is important to

have some explicit criteria or frame-

work for deciding what constitutes a

plausible specification of (1), in particu-

lar, what other variables besides X be-

long in (1) and what are the relation-

ships between these other variables and

the X, Z, and ?? It is in providing a co-

herent framework for answering these

questions that most of the studies em-ploying natural natural experiments fall

short. And, what is excluded from (1)

turns out to be critical in most of the

studies for achieving identification of f3.

Our strategy is to show using very sim-

ple behavioral models what assumptions

about the characteristics of technology,

preferences, and markets are required

to justify these exclusion restrictions.

We divide our review essay into three

main sections defined by the P3f inter-

est. In the first section, we examine

studies in which Y is (log) earnings and

P is the return to human capital invest-

ments in the form of either schooling or

post-school investments. The natural

natural experiments considered in this

section include a child's date of birth, a

child's gender, the date-of-birth draft

lottery, and human cloning. We first

show that these studies provide a widerange of estimates of P, are almost

evenly divided with respect to the di-rection of ability bias, and do not

often provide estimates that differ verymuch from those obtained using least

squares. With respect to the propertiesof the instrumental-variable estimates,the two studies concerned with the re-turns to schooling assume that the onlyother variable in (1) besides schoolingis age and that the only component of

the error term correlated with school-

ing is ability. And the sex of one's sib-ling, or one's month of birth, the instru-ments used, are plausibly assumed to

be uncorrelated with ability. We showusing a very simple model of schoolingchoice that the date-of-birth and childgender instrument do identify, under

these assumptions, the returns to

schooling, but for different abilitygroups in the population. We also show,

however, that (i) if work experience is a

better proxy for post-school human

capital than is age, the instrumental es-

timates of the returns to schooling from

the two natural natural experiment in-struments are biased, and the biases goin opposite directions, and that (ii) if

work choices after school are made op-

timally and work experience affects

earnings, there is additional bias in thetwo IV estimates that will depend on

the age of the sample population. We

also present evidence from U.S. panel

data, using the same natural natural in-

struments, that work experience is cor-

related with the error term in (1) and

with schooling. Thus, the particular ap-

plications of the two instruments are

likely to provide biased estimates of the

return to schooling. Moreover, the twoinstrumental variables estimators will

differ from each other when applied to

the same population, especially if re-

turns differ by ability group, and each

instrumental variable estimate will pro-

vide different (biased) estimates fordifferent-aged populations.




The seemingly innocuous but empiri-

cally dubious assumption used in the

two natural natural experiment school-

ing studies, that age is the only other

determinant of earnings besides school-

ing (and ability), turns out to be critical

for identification even if the natural

events used as instruments are uncorre-

lated with ability. Similarly, we show

using the same behavioral model that

the unstated critical assumptions in the

draft-lottery study of the returns to ci-

vilian work experience (where ? is again

defined to be ability and X = experience

in (1)) are (i) that schooling is uncorre-lated with ability and (ii) schooling is

uncorrelated with experience. The for-

mer assumption is inconsistent with

that made in the natural natural experi-

ment studies of schooling, and the lat-

ter we show to be empirically untrue.

Finally, we also consider in this section

the growing set of studies that make use

of natural human cloning to estimate

the return to schooling. We show that

most of these studies provide downwardbiased estimates of the return to school-

ing if work experience is an important

determinant of earnings, even if the

critical assumption that the differences

in the schooling within twin-pairs is

purely random holds. We also show,

however, that evidence on -differing

birthweights within pairs of monozy-

gotic (genetically identical) twins and a

plausible model of optimal job-taking

suggest that even with information on

work experience, twin-studies yield esti-

mates of schooling returns that are

likely to be biased, and it is not clear a

priori whether the bias is upwards or

downwards.

In the next section, we look at studies

using weather events as natural instru-

ments to estimate and test hypotheses

about the effects of changes in perma-

nent and transitory income on con-sumption and labor supply. In these

studies f3 s the permanent or transitoryincome effect, and weather events are

plausibly assumed to be orthogonal tothe error term, which implicitly is de-fined to contain farmer preferences. Inall studies, the sample population con-sists of farmers. We show using a simpletwo-period model that identification oftransitory income effects in these stud-ies depends critically on a number of

assumptions about the structure of pref-erences and labor markets. In particu-lar, the studies have implicitly assumed

that either family and hired labor are

perfect substitutes, or, if not, that amarket exists for all types of labor, that

labor is perfectly spatially mobile,and/or that leisure and consumption are

strongly separable. We show that if the

assumption of perfect labor mobility is

relaxed, that even if family and hired la-

bor are perfect substitutes and marketsare complete, the weather-based instru-mental estimates of transitory income

effects are biased upwards given the

specifications used in two of the mostwell-known studies. We also show, how-

ever, using data from a setting similarto those used in these studies, that the

assumption that family labor is perfectlysubstitutable for hired labor is rejected.

The third major section contains a re-

view of studies in which the 3 of inter-

est is the effect of an exogenous changein fertility (X) on the labor supplychoices of married women (Y) and that

rely on the occurrence of a twin firstbirth or the sex composition of the first

two children as natural natural instru-

ments. In these studies, the error term

is defined to contain preferences, and it

is plausibly assumed that neither havinga twin on the first birth nor the sex of

children are correlated with prefer-ences. To illustrate plausible conditions

under which the random sex-sameness

of children or a twin birth may directlyaffect labor supply net of fertility (so




that Z and ? are not orthogonal as as-sumed), however, we again set out abare-bones model, in this case one inwhich parents care about the sex com-position of children and make laborsupply and fertility decisions. Themodel illustrates the types of strong re-strictions required so that the naturalnatural instrumental-variable estimateof the fertility effect on labor supplybased on the sex-sameness of initialbirths or twin births corresponds to theexperiment in which fertility itself isvaried exogenously. Here we show that

it is necessary to assume that the sex-sameness of births or having twins has noeffect on the costs of children for iden-tification to be achieved, or'that strongassumptions about the separability offertility, labor supply and sex-compositionmust be imposed. We adduce evidencefrom data from rural India that suggeststhat the sex-composition of children atleast in that context has significant ef-fects on child-rearing costs so that the

sex-composition instrumental-variablesestimate does not identify f3.

In the final section, we assess thecontribution of the natural natural ex-periment studies and propose a re-search strategy which makes use of thegeneral insights of this literature.

3. Estimating the Return to HumanCapital Investments:Schooling and

WorkExperience

The presence of ability bias in esti-mates of the return to human capital in-vestments in the form of schooling is alongstanding problem. Early proposedsolutions to the problem include usingtest scores as (imperfect) measures ofability (e.g., Zvi Griliches and WilliamMason 1972) and using siblings to con-trol for family-level unobservables

(Gary Chamberlain 1977). More re-cently, it has been suggested that natu-

ral experiments that induce variation in

school attainment unrelated to ability

can be used to eliminate ability bias in

estimating the return to schooling.

These natural natural experiments in-

clude date of birth, as used in Joshua

Angrist and Alan Krueger (1991), and

child gender, as used in Kristin Butcher

and Anne Case (1994). In addition,

seven studies have used differences in

the schooling attainment of individuals

in monozygotic twin pairs-human

cloning-to eliminate the contamina-

tion of returns estimates from genetic

differences in ability. And one study(Angrist 1990) has exploited the date-

of-birth draft lottery during the Viet-

nam War to estimate the returns to

civilian work experience.

Table 1 summarizes the results from

these studies of the human capital de-

terminants of earnings that exploit natu-

ral natural experiments. One interesting

feature of the set of studies is that only

one of the studies examines jointly the

returns to both work experience andschooling. And, of the two studies pro-

viding estimates of experience returns,

one excludes schooling from the specifi-

cation. As we discuss, these omissions

are not only (or at all in some cases)

due to data restrictions, but are related

importantly to the limitations of the

natural natural experiment approach.

What is also striking about the set of

natural natural-experiment schooling

returns estimates is that, not only do

they have an extraordinary range-from

less than one percent to over 18 per-

cent-they also are almost exactly

evenly divided between those that indi-

cate a negative ability bias (4) and those

that indicate a positive ability bias (6),

although in many cases the estimated

returns do not differ significantly when

the instrument is used. It is difficult to

infer from the pattern of estimatesacross the studies the precise role of




TABLE1ESTIMATESOF THE RETURNS TO SCHOOLINGAND WORK EXPERIENCEUSING NATURALEVENTS AS INSTRUMENTS

Instru- Instru-

OLS mented mentedReturn o Return o Return o Control

Study NaturalEvent Data Set Schooling Schooling WorkExp. Variables

Angrist1990 Date of birth+ U.S. SocialSecurityAd- .102-Vietnamdraft ministrationContinuous .003*yearslottery WorkHistorySample, or of work

men exp.

Angrist nd Date ofbirth+ 1970 and 1980 U.S.Cen- .080 .072 Age,Krueger1991 school eaving suses, menaged41-50 (1970) (1970) race,

age + school .071 .102 SMSA,entryage (1980) (1980) married

Butcherand Gender (any PanelStudyof Income .091 .184 AgeCase1994 sisters) Dynamics,whitewomen

Behrman, Humancloning U.S. NAS-NRCTwins .080 .003 AgeHrubec, SampleofWhite VeteranTaubman, nd Males Born n 1917-27Wales 1980

Ashenfelter Humanclon- Twinsburg,Ohio Annual .116a .129 Age, ten-and Krueger ing + instru- TwinsFestivalSample, urein1994 ments (report 1991-men andwomen last ob,

by co-twin) union,married

Behrman, Humanclon- BiographicalQuestion- lOla .050 Age

Rosenzweig ing + instru- naire sample romtheand Taubman ments(report MinnesotaTwinRegistry,1994 by twins'old- twinsborn n Minnesota

est child) 1936-55-men

Miller,Mulvey Humanclon- Australian winRegister .073a .045 Age,mar-and Martin ing + instru- 1980-2 and1988-9 ried

-1995 ments(reportby co-twin)

Ashenfelter Humanclon- Twinsburg,Ohio Annual .113 .100 Age,ten-and Rouse ing + instru- TwinsFestivalSample, ure in1998 ments(report 1991,1993-men and last ob,

byco-twin) women union,

marriedBehrmanand Humanclon- 1994MinnesotaTwin .113a .104 .0084 Age, post-Rosenzweig ing + instru- Registry urvey ample, school1999 ments(report twinsborn n Minnesota full-time

by co-twin) 1936-55-men and workex-women perience

Rouse1999 Humanclon- Twinsburg,Ohio Annual .111 .119 - Age,ten-ing + instru- TwinsFestivalSamples, ureinments(report 1991-93,and 1995-men lastjob,by co-twin) andwomen union,

married

a Estimate singsame nstrumentso correct or measurement rrornschooling s used ncloning-basedstimates.




the different natural natural experi-ments exploited, as some use samples ofmales only, one uses only females, andsome use a sample including both males

and females. However, as we show, animportant factor in explaining the dif-ferences in findings is the natural-experiment based instrument used. Onereason, as shown in human capital mod-els by David Card (1994) and JamesHeckman (1997) and generalized in alarge literature concerned with evalu-ation (e.g., Guido Imbens and Angrist1994), is that when there is heterogene-ity in returns, the treatment effectthat is identified is for the group orgroups whose behavior is influenced bythe intervention. And the instrumentsaffect different groups.

To show how these natural experi-ments are used to estimate the returnsto human capital investments, the es-sence of the problem that is beingsolved, some of the factors that lead todifferences among the estimates, and

the assumptions made implicitly by theauthors of the studies, we begin with astandard model of schooling choice in-corporating ability heterogeneity. Weassume that earnings at any age a, ya,

depends on three factors-the level ofschool attainment, S; the amount of workexperience at age a, Xa; and ability [t-according to

lnya=f(S,g) + g(Xa,g), (3)

where f and g are monotonically increas-ing in their arguments. We initially as-sume, as do all but two of the studies,that all individuals work full-time aftercompleting schooling. Each individualenters school at a mandated school entryage ae and must remain in school untilthe mandated minimum school leavingage aK.Thus, school attainment at aK is

So= aK_ae. It will be convenient for whatfollows to limit the decision horizon by

assuming that the individual decides on

whether to attend school only for oneperiod beyond the school leaving age.School attendance in the period follow-ing aK, period one, is denoted by si = 1

and nonattendance by si - 0; completedschooling, at the end of period one, Si, istherefore either So+ 1 or So. An individ-ual who decides not to attend school inperiod one works that period and all sub-sequent periods; i.e., the individualworks from period a = 1 to the end ofworking life a = A, while an individualwho attends school does not work in thatperiod, but works in all subsequent peri-ods, i.e., from a = 2 to A + 1. There is adirect cost of attending school denotedby c. In addition, the assumption thatschool attendance precludes working im-plies that school attendance entails anopportunity cost in terms of the earningsthat are foregone.

The individual is assumed to makethe choice of whether or not to attendschool according to which option maxi-mizes the present discounted value of

lifetime earnings. Denoting the dis-count factor as (=- )' the presentvalue of each alternative, Vi(si = 1 ISo)and Vi(si =OI So), is:

Vi(si = 1 ISo)= exp[f(So+ l,g)].A - 1

a+1'exp[g(a,g)] - c,

VJSa=- (4)

Vi(si= 0 1So)=

expf(So,g)].(-1

AiIaexp[g(a,g)]

a =

The decision rule is to attend schoolif Vi(si = 1 ISo)? Vi(so= 1 ISo), whichreduces, after some manipulation, to:5

Si = 1 if f(So + 1,,) -f(So,g)

>,r+ In[V11 -? So)+ 1], (5)

sj =0 otherwise.

5We use the approximationln(1+ r) = r in de-rivingthe decision rule.




The individual ttends schoolif the percent-age increase in earnings from attendingschool, the marginalreturnto schooling, issufficientlygreater than the interest rate.6

If ability increases the marginal school-ing return,

D[f(so+ 1,g) -f(So,g)]

then there exists a cut-off value of abil-ity, *, such that individuals with abilityat or above that cut-off attend school andthose below it do not.7 Thus, the differ-ence in earnings among the two school-completion groups will reflect, in part,

these induced ability differences. Al-though ability is distributed randomly inthe population, optimizing behavior cre-ates a positive correlation between abil-ity and completed schooling, which im-plies that the (average) return toschooling calculated from (ln) earningsdifferences between the two schoolinggroups (given experience) overstates the(average) return to schooling, i.e.,

Eg[f(So+ 1,g) Ig g*] - Eg[f(So,g) g <g*1]> Eg[f(So 1,g) -f(So,)]. The challengeis to obtain an estimate of the returnsto schooling without this ability biasfor every ability group in the popula-tion. Almost all of the empirical litera-ture assumes that the return to school-ing is identical for all ability groups, sothat there is one true return to schooling.

3.1 The Returns to Schooling WhenSchooling Is a Choice: TheAngrist-Krueger and Butcher-CaseNatural Experiments

3.1.1 Angrist and Krueger:Age at Birth

Angrist and Krueger (AK) suggest that

natural variation in dates of birth, in con-

junction with the existence of a birth

date cut-off for school entry and a mini-

mum compulsory school leaving age, can

be used as an instrument for com-

pleted schooling that provides an esti-

mate of the returns to schooling with-

out ability bias. This study exemplifies

well the difference between the natural

natural experiment approach and the

more prevalent natural experiment ap-

proach which often relies on variations

in government-determined laws or reg-

ulations. The AK study does not use the

variation in mandatory school leaving

ages across or within states or other ad-

ministrative units as a source of identifi-

cation. To illustrate the reasoning, con-

sider a particular locality, defined by aset of fixed school entering and school-

leaving ages, in which a child must at-

tain the age of six as of September 1 in

order to enter the first grade and cannot

leave school prior to attaining the age of

sixteen. Then, a child whose birthday falls

on September 1 will have completed ten

years of schooling at the minimum school

leaving age. However, a child born in

the same calendar year but a day later,

on September 2, will enter the firstgrade one year later and will have com-

pleted only nine years of schooling

upon reaching age sixteen. Thus, if chil-

dren in the two (day of birth) cohorts

are otherwise identical and at least

some of them prefer nine or fewer years

of schooling, average completed school-

ing of the two cohorts will differ be-

cause some of the children in the Sep-

tember 1 cohort will have been forced to

obtain an additional year of schooling.

6 If the direct cost of attending school is smallrelative to the present discounted value of lifetimeearnings, then the right hand side can be approxi-mated by r + c / V1(s1= 0 iSo). Regardless, if thedirect cost of schooling is zero, either conditionreduces to the marginal return to schooling ex-ceeding the interest rate. With continuous school-ing choices and zero direct cost, the rule for opti-mal schooling is to equate the marginal earningsreturn to the rate of interest, i.e., fs = r. The sec-ond order condition would require in that casethatfss < 0.

7 Notice that when c is non-zero, the right-handside is falling monotonically with ability. A cut-off ability level will exist, therefore, even if the

marginal return to schooling is independent ofability.




An additional simplification of themodel illuminates how the AK instru-mental variable estimator works. As-sume that there are just two ability

types, denoted as g1i and R2, with thefirst type of higher ability. Type l'scomprise li proportion of the popula-tion and type 2's 1 -Xi. The insight ofAK is that, given laws governing theages at which children can enter andleave school, completed schooling willvary with birth date for some part of thepopulation. Date of birth is assumed byAK to be a random variable uncorre-lated with ability (as transmitted inter-generationally), while the laws govern-ing school-entering and leaving ages,set by each state, can be correlated withother state-specific unobservables thatinfluence earnings.8 These are sub-sumed in a state fixed-effect. Thus,variation in state schooling laws are nottreated as natural experiments, can beendogenously determined, and do notcontribute to identification. It is vari-

ation in date of birth within states thatserves to identify schooling effects. Hav-ing information on multiple states, withdiffering laws, merely adds precision tothe estimates.

AK present Wald estimates of the re-turn to schooling based on comparing(ln) weekly earnings and school comple-tion levels for two cohorts of men aged41-50 who differed in their quarter ofbirth, specifically comparing those born

in the first quarter of a calendar year tothose born in the other three quarters(of the previous calendar year). Interms of the model, it is easy to showwhat their Wald estimator identifies.

Suppose, according to (5), that the opti-

mal level of schooling for type l's is

So + 1 and that for type 2's is exactly So,

given the school entry age ae and the

minimum school leaving age aK. Con-sider reducing the age at entry by one

year, leaving the minimum school leav-

ing age unchanged. In that case, both

ability types will complete So + 1 years

of schooling; type l's do so because it is

optimal, while type 2's are forced to re-

main in school an extra year. The differ-

ence in expected (ln) incomes associ-

ated with the alternative school entry

ages divided by the corresponding dif-

ference in expected schooling levels,

that is, the Wald estimator, is f(So + 1,

,u2) -f(So,,u2), which is the marginalreturn to schooling of the less able type.

AK found that for the group of men

aged 41-50 in 1970 (1980), those bornin the first quarter of a calendar year

obtained .1256 (.1088) fewer years of

schooling on average than those born in

the other quarters. Presumably, those

men born in the first quarter of a calen-dar year were more likely to have had to

delay school entry than those born in

the previous three quarters. Dividingthose differences by the concomitant

differences in (ln) weekly wages im-

plied a return to schooling of .0715 in

1970 and of .1020 in 1980; In contrast,

the OLS estimate was larger in 1970,

.0801, and smaller in 1980, .0709.9

3.1.2 Butcher and Case:Child Genderas a Schooling Instrument and the

Quality-Quantity Tradeoff

Butcher and Case (BC) suggest that

natural variation in the sex of siblings,in particular whether a girl has any sis-

ters, can be used to obtain an estimate

of the schooling return (to women) that

is free of ability-bias. They discuss

8 ohn Bound and David Jaeger (1996) presentevidence that date of birth is correlated with anumber of attributes of children that might be di-rectly related to their later earnings net of school-ing effects, including personality, mental health,and parental income. They do not provide any be-havioral model that suggests why these correla-tions exist.

9Two-stage least squares estimates that controlfor age trends tend to provide

estimates that arealso close to the OLS estimates.




several reasons for the gender of sib-lings to affect parental human capitalinvestments in a given child. In particu-lar, the gender of siblings may affect

the cost of investing in a child's humancapital through the existence of borrow-ing constraints if there are exogenousgender differences in the return to hu-man capital. According to BC, in thepresence of borrowing constraints andassuming that boys receive a higher re-turn to each level of schooling, weshould expect to see not only that boysreceive more education, but also that

the presence of sons reduces the educa-tional attainment of daughters. Also,independent of preferences, there maybe exogenous differences in the cost ofraising girls relative to boys, thus affect-ing the household's overall budget con-straint. In addition, they argue that thegender of one's siblings may affect achild's preferences for schooling invest-ments, with girls who have brothersperhaps adopting masculine traits and

vice-versa. Finally, parents may simplyprefer to invest differentially in girlsand boys depending on the overallgender composition of their children.

BC provide evidence from three dif-ferent data sources, the Panel Study ofIncome Dynamics (PSID), the CurrentPopulation Survey (CPS), and the Na-tional Longitudinal Surveys MatureWomen's cohort (NLSMW), in supportof the hypothesis that gender composi-

tion affects human capital investmentsin children. Specifically, they find thatgirls who have any sisters, conditionalon the number of siblings, have lowerschool attainment than do girls with nosisters.10Given this result coupled withthe inherent randomness of child gen-der, BC argue that the existence of anysisters can serve as a valid instrument

for school attainment in estimating theearnings return to schooling.

BC recognize, however, that the exis-tence of sisters, even if gender is ran-domly determined, depends on the choiceof family size. There are economic mod-els in the literature that suggest that thischoice may be correlated with ability.Although the gender of any particularchild is random, the probability of hav-ing a sister obviously increases with thenumber of siblings. Assuming fertility issubject to -control, to the extent thatfertility is related to the ability of chil-

dren, the any sisters instrument willbe invalid, and inclusion of number ofsiblings as a regressor to control for thisrelationship requires an assumptionthat parents are indifferent about thesex-composition of their children. Onesuch behavioral mechanism creating acorrelation between the immutablecomponent of the abilities of childrenand number of siblings arises in the con-text of the joint fertility-child investment

decision models first proposed by GaryBecker and H. Gregg Lewis (1973) andelaborated by Becker and Nigel Tomes(1976) to include heritable endowmentsof parents and children.

In these models, which highlight thetrade-offs between the quality andquantity of children, parents receiveutility from the number of children theyhave (fertility) and from the averagequality of their children. Child quality

is produced through the application ofparental (time and goods) inputs condi-tional on parental (innate and heritable)ability. Parents with higher ability forgiven inputs are assumed to be able toproduce higher quality children. Theessence of the quality-quantity model isthat the cost of children depends on to-tal child quality (the price per unitquality times quality per child times

fertility), which implies that the shadowprice of fertility is increasing in the

10 On the other hand, the school attainment of

boys is found to be unrelated to gender composi-tion.




average quality of children. An implica-tion of this model is that parents withhigher ability will tend to have fewerchildren that are of higher quality.11

Given the heritability of parental abil-ity, family size and child ability willthus be negatively related.

One of the earliest uses of the birthtwinning natural experiment (Rosen-zweig and Wolpin 1980a) was for thepurpose of testing the quality-quantityframework. In that study, data on house-holds from rural India were used to as-sess whether an exogenous increase in

the number of children, brought about bya twin birth, led to reduced schoolingattainment for children. Explicit atten-tion was paid to the fact that like the

anysisters variable, having a twin birthis positively correlated with the propen-sity to have a large family by dividingthe number of twin births by the totalnumber of pregnancies. This measureof extra births clearly does not com-pletely conform to the randomness cri-

terion if family size is a choice variableand led to the subsequent use of havinga twin on the first birth as a naturalnatural instrument, described below.

BC, recognizing the existence of a re-lationship between family size and hav-ing a sister, also incorporate family sizein their instrumental variables estima-tion procedure. They note, however,that sex-composition may still not berandom if fertility is chosen in a se-

quential decision process. In particular,if parents have a preference for mixed-gender families then among parents whohave the same completed family size,

those with same-sex children will differfrom those with mixed-gender in somecharacteristic that leads to having fewerchildren, e.g., lower income. BC provide

as evidence that the any sister instru-ment is not contaminated by fertility se-lection that, for two-child families, boyswith a brother have no less educationthan boys with a sister even though girlswith a sister have less education than dogirls with a brother. Although this evi-dence clearly shows that boys and girlsare treated differently, in the absenceof a priori knowledge of how they are

treated differently, it does not refutethe possibility that parents prefer mixedgenders. Indeed, Angrist and Evans(1998), as described below, present di-rect evidence that parents do prefermixed-gender families, which they useas the basis for the identification offertility effects on labor supply.

BC employ two specifications in esti-mating the returns to schooling usinginstrumental variables. In one specifica-

tion, BC include the number of siblingsas a determinant of both earnings andschooling. The validity of this estimatorrests on the assumption that parents areindifferent about gender composition.In a second specification, they omitnumber of siblings from the earningsfunction but still include it as a deter-minant of schooling, thus using thenumber of siblings as an additional in-strument. Clearly, if number of siblings

is related to a child's innate ability, astheory suggests, this specification willnot provide a consistent estimate of the

schooling return.12 The distribution ofthe total number of children acrosshouseholds is not the outcome of anatural natural experiment.

For the BC instrument any sisters

11The effect of higher ability on the level ofchild investments is ambiguous and depends onhow ability affects the marginal product of inputs.The higher income of higher ability parents willalso tend to reduce fertility if, as was posited byBecker and Lewis, the income elasticity of qualityexceeds that of quantity. For a life-cycle model

with the same implications see Rosenzweig andWolpin (1980b).

12The estimate of the schooling coefficient isonly statistically significantly different from zero

in the specification that uses family size as an ad-ditional identifying instrument.




to be valid it is thus sufficient that fer-tility not be correlated with ability, thatthe models of fertility choice are incor-

rect in some way. For example, parentsmay not know their children's abilityprior to making their fertility decisions.Without a measure of innate ability, itis of course not possible to demonstrateconclusively the existence of a correla-tion of ability with number of siblings(or having sisters). Indeed, if a test thatperfectly measured innate ability wereavailable, obtaining an unbiased esti-mate of the return to schooling would

not be a problem in the first place. Wecan provide evidence, however, onwhether having sisters is correlated withscores from tests administered to veryyoung children that are designed tomeasure ability, recognizing that suchmeasures are unlikely to be themselvesimmutable and that such a correlationmight exist as a result of parental in-vestment behavior. For this purpose,we make use of the ability measurespresent in the 1979 Youth and Childcohorts from the NLS.13

We restrict the sample to the first-

born children of women in the NLSYwho had a first birth by the age of 29.The gender of firstborn children, ab-sent sex-selective abortion, meets therandomness criterion for all householdswith any children. The sample consistsof 2311 first births for whom there is a

valid score on the Peabody Picture Vo-cabulary Test (PPVT) and for whosemothers there is a valid score on the

Armed Forces Qualifying Test (AFQT).The PPVT is for children aged three to

six and is designed to measure verbal

ability. The AFQT has been shown tobe highly correlated with IQ-type tests.A necessary condition for this exercise

to be minimally credible is that the gen-der of the firstborn not be correlatedwith either the firstborn child's nor themother's test score. The first and thirdcolumns of Table 2 provide evidenceconsistent with that condition; the OLScoefficient from a regression of thefirstborn child's PPVT score and themother's AFQT score on the gender ofthe firstborn child (being a female) isneither statistically significant nor large

in magnitude.14 The data confirm thatthe gender of the first child satisfies thecondition of randomness.

The second and fourth columns ofTable 2 provide evidence based on thesame data, however, that calls into

question the implicit behavioral as-sumptions that would render the BC

any sisters instrument as valid. Re-stricting attention to the 1135 firstbornchildren who were female, we regressedthe child's PPVT score and the mother'sAFQT score on whether that child hadany sisters. In contrast to the correla-tions with respect to the gender of thefirstborn, it appears that the child'sPPVT score and the mother's AFQTscore are both negatively related to

whether the firstborn female child has

any sisters. Further, as seen in columnfive, the mothers of female children

with more children have lower AFQTscores. These results together are con-sistent with the notion that the less

able mothers have more children (asis demonstrated in column five) andthat their lower ability is transmittedto their offspring.15

13 Note that while there is some empirical evi-dence calhng nto question the randomnessof monthof birth (Bound and Jaeger 1996), no behavioralmodel has been presented as to why ability andintra-annual birth timing should be correlated.The randomnessof fertilitywith respect to parentalability is called into question by well-establishedeconomic models, but there is limited evidence.

14The mean PPVT score for the sample is 90with a standarddeviationof 20. Similarly, he meanAFQTscore is 611 with a standarddeviation of 215.

15 All of the results in Table 2 are the same for

boys. These results are available from the authorsupon request.




TABLE 2

GENDER, SIBLING GENDER, AND ABILITY TEST SCORES OF CHILDREN AND THEIR MOTHERS

(MOTHERS AGED 29+ IN 1992 FROM THE NLSY79)

Firstborn's PPVT Score Mother's AFQT Score

Mothers with Mothers with

All mothers firstborn girl All mothers firstborn girl All mothers

Fisb.I.4irstborn is a girl -.462 -6.44 -

(0.580)a (8.26)

Firstborn has a sister -2.83 -31.4

(1.11) (11.8)

Children ever born -25.9to mother (3.89)

Mother is Black -16.3 -16.7 -175 -171 -172

(0.953) (1.33) (9.90) (14.1) (9.82)Mother is Hispanic -13.2 -13.8 -152 -145 -147

(1.11) (1.51) (11.5) (16.1) (11.5)

R2 .133 .155 .147 .148 .162

N 2,311 1,135 2,311 1,135 2,311

a Standard errors in parentheses.

The problem that the any-sisters in-strument is correlated with ability via

fertility stems from the fact that the in-strument incorporates information onthe gender of births subsequent to thefirst. Recognizing the source of theproblem suggests that a remedy wouldbe to use as an instrument the genderof the first birth, which our resultsshow conforms to the randomness crite-rion.16 Thus, assuming that all womenhave at least two births, the gender ofthe first birth can be used as a valid in-strument for the schooling of the sec-ond child.17 In particular, the gender of

the first child cannot be correlated withthe innate ability of the second child,

but would be correlated with theschooling of the second child throughthe avenues discussed by BC.

To illustrate the Wald estimator ofthe return to schooling based on thegender of the first birth instrumentalvariable, in the context of the modelused to elucidate the AC experiment,we incorporate the BC assumption thatthe cost of schooling to a second-borngirl is higher if the first born is a boy asopposed to a girl, specifically Cb and cgrespectively with Cb > Cg. We also adoptthe assumption that ability is indepen-dent of sex. Now, suppose that withthese costs, it is optimal for the girlwith a firstborn brother not to attendschool regardless of her ability, so thatshe completes only the minimum, So,years of schooling. On the other hand,suppose that among girls with a first-

born sister, who face a lower cost ofschooling, type I's optimally choose to

16The same remedy, as will be shown, applies tothe twins instrument used by Rosenzweig andWolpin (1980a). We show below that this instru-ment has some limited power to explain schoolingvariation for siblings.

17 Of course, sample selection based on havingat least two births, given that fertility is a choice,may be a source of bias. Angrist and WilliamEvans' (1998) natural natural experiment estimateof the effects of fertility on labor supply also must

assume that the two-birth minimum does not re-sult in a choice-based sample.




attend school, thus completing So+ 1years, while the type 2's still do not at-tend. In this case, the difference inexpected (ln) incomes of girls with

firstborn sisters vs. firstborn brothers(experience constant) divided by thedifference in their expected schoolinglevels, that is, the Wald estimator, issimply f(So + 1,.ti) -fi(So,iL), the returnto schooling for the more able group.Thus the variation in completed school-ing that arises from the sex of the firstborn sibling, variation that is indepen-dent of ability, provides identification

of the schooling return, but only for themore able group.

3.1.3 Specification Matters:Schooling,Age and Experience

We have shown in one model that theAK and BC (suitably modified) naturalexperiments yield estimates of returnsto schooling for different ability groupsin the population, exemplifying that theinstrumental approach identifies treat-

ment effects only for the treated. Othermodels may yield different results foreach instrument when ability and school-ing returns are correlated. Again, theinterpretation of what has been esti-matedand for whom depends on how onemodels behavior. If the schooling re-turn is independent of ability, however,in principle the two experiments yieldthe, same estimate of the schooling re-turn in (3). But AK and BC do not esti-

mate equation (3). Both the BC and AKspecifications of the earnings functioncontrol for age rather than for work ex-perience. Our model suggests that thisseemingly innocuous specification choiceleads to bias in both the AK and BCestimates and, perhaps surprisingly, thebiases are of opposite sign. The existenceof a theoretically valid natural instru-ment thus does not mean that the speci-

fication of the equation of interest doesnot matter for identification. That is,

bias can still arise due to misspecification.Suppose that, as suggested in Jacob

Mincer (1974), time spent in the laborforce after completing schooling-post-

school work experience-is the appro-priate proxy for post-school humancapital investments, as in (3). As Mincerfirst demonstrated, in this case control-ling for age rather than experience willunderstate the return to an additionalyear of schooling by the earnings lossassociated with having one less year ofexperience. Under the assumption thatall post-schooling periods are spent at

work, the assumption used in theschooling choice model, experience atany age X, in equation (3) is simply a -

S -ae. It is easily seen that the Waldestimator for the BC experiment isgiven by [f(So+ l,gi) -f(So,gi)] - [g(a-

a-, - l,gi) - g(a - aK,gl)].Because the ad-ditional year of schooling comes at theexpense of an additional year of experi-

ence, the consequence of omitting ex-perience from the BC specification is

exactly as Mincer showed-what isidentified is the difference between thereturns to schooling and experience (forthe more able group).

In contrast, the Wald estimator basedon the quarter-of-birth experiment ofAK overstates the schooling returnwhen age is used to proxy experience.The reason is that this experimentaltreatment is based on an exogenous de-lay in schooling, and school delay not

only affects schooling attainment, butmust also affect post-school experiencefor members of the same year-of-birthcohort. To see this, we rewrite the ex-

pected (ln) earnings at age a for the

population with two ability types, wherewe do not control for work experience,with school entry age ae and minimumschool leaving age aK:

E(lnya)= ni[f(So+ l,gi) + g(a aK -l,giL)]

+ (1 - 7ti)[f(S0,g2) + g(a - aK,g2)1- (6)




Type l's attend school an extra year andso have one year less of accumulatedworkexperience at age a. Under the alternative

scenario with the school entry age re-duced by one year, type l's achieve theiroptimal level of schooling exactly at theschool leaving age, rather than one yearlater,and thus have accumulatedone moreyearof workexperience,a - aK years,atage a. Type 2's, as before, will be forcedto obtain one year of schooling beyondtheir optimal level, will leave school at a,and will have accumulated a - aK years ofwork experience at age a. Expected (ln)

earnings under this scenario are thus

E(lnyya)= ntuf(So+ l,gi) + g(a - axgi)]+ (1 - 7l)[f(So + 1,W2)+ g(a - aK,b2)]. (7)

The difference in expected (ln) earn-ings divided by the difference in ex-pected schooling (0 . 7tl + 1 -(1 - ltl) = 1 -

itl), the Wald estimator, is thus

AE(lflya) iti= [g(a - aK,,) - g(a

AS 1 - it,- aK- l,g,)] + [f(So+ 1,g2) -f(So,2)]. (8)

Compared to the experience-constantWald estimator, the return to schoolingis overstated by the return to an addi-tional year of experience weighted by thetype one odds ratio in the population. Al-

though reducing the age at entry forcestype 2's to obtain an additional year ofschooling,an additional onsequenceis thattype l's gain a year of work experience.

3.2 The Returns to Civilian WorkExperience:TheAngrist NaturalLottery Experiment

Obtaining additional schooling is notthe only factor reducing Mincer expe-rience for members of the same birthcohort, if that definition is restricted tocivilian labor force experience. Onecomponent of the cost of military ser-

vice to an individual is the loss in life-time earnings that is incurred that

arises in part by reducing time in thecivilian labor force, given that the twoforms of experience are imperfect sub-

stitutes. Measuring the loss from mili-tary service is complicated by the factthat those who enter military serviceare not usually randomly selected. Evenin a regime of military conscriptiondraftees are not necessarily randomwith respect to traits that are related toearnings because some individualschoose voluntarily to enter military ser-vice and some individuals are ex-empted. Angrist (1990) uses the theo-

retical natural randomness of theVietnam War draft lottery, based onbirth dates, to assess both the totalcosts of military experience on earningsand to estimate the returns to civilianexperience. Angrist exploits the factthat the draft lottery randomly assignsthe pool of those eligible for the draft.18

The suitability of the draft lottery asan instrument requires that a randomprocess choose who serves and, equally,

who does not. However, although thedraft lottery randomly chose who mustenter military service, subject to some

qualifying criteria, some who were notdraft-eligible as determined by the lot-

tery entered the military. There wereno barriers to volunteer one's serviceeven if not chosen, and some incentivesto volunteer prior to knowing whetherone would be drafted (e.g., choice of

service). This unnatural military draftlottery thus does not strictly conform tothe randomness criteria and, as Heck-man (1997) has pointed out, if thosewho enter the military voluntarily do soin anticipation of high earnings gainsfrom military service or have traits that

18 The randomness of the draft lottery was alsoexploited in articles in the biomedical literatureto estimate the effects of military service on post-service mortality (N. Hearst, T. B. Newman, andS. B. Hulley 1986) and IV drug use (Hearst, J. W.

Buehler, Newman, and G. W. Rutherford 1991) (atrue IV estimator).




are related to unobservables that affectearnings, then the lottery cannot strictlyserve as a valid instrument for militaryservice. Throughout our discussion, we

will assume this problem away, as doesAngrist. Even if the draft lottery were avalid instrument, its use to identify thereturns to civilian experience requires

still more assumptions about behavior.Angrist obtains an estimate of the im-

pact of military service on earningsusing a Wald estimator given by [y~e y]/

[pe - An], where yje is mean earnings

of draft eligibles, 9Jn mean earnings of

draft ineligibles, Ae the proportion of

draft eligibles who enter the military

and pn the proportion of ineligibles who

enter the military (voluntarily). The Wald

estimates (over different birth cohorts)

imply that military service reduced an-

nual earnings of Vietnam War veterans

by 15 percent. Conditional on the draft

lottery randomly assigning individuals

to the military, the gross earnings im-

pact (gross of all other investments

influenced by being draft-eligible) ofmilitary service is thus identified.

To quantify the importance of the

earnings loss from the reduction in ci-

vilian experience, Angrist uses the same

instrumental variables approach. Unlike

in the later AK study, however, he

adopts the Mincer earnings specifica-

tion in which post-school years of expe-

rience, and not age, matter for earn-

ings, modified such that potential

experience is net of time spent in themilitary service, m. Because Angrist

uses Social Security-based data that

does not provide schooling, the earn-

ings function for an individual at age a

who spends time m in the military is

written as:

lya = O + OClSa + OC2Xa + Ua (9)

= ot'o + oX2(a- m) + U'a,

where the second line is obtained by

substituting for potential civilian experi-

ence, Xa= a - Sa- m - ae, and where the

composite error contains both the unob-

served earnings endowment and the

omitted schooling variable, U'a= (oci-

OC2)Sa+ Ua'19

As seen in (9), if military service is

correlated with unobservables that af-

fect earnings (the composite error),

then an OLS estimator of the return to

civilian experience will be biased. Now,

the original motivation for using draft

eligibility derived from the lottery as an

instrument for military service was that

m and (some permanent component of)

u, ability, might be correlated. How-

ever, given the non-observability of

schooling in the data set used, in order

to get a valid estimate of the experience

return, it is also necessary to assume

that the variation in military service in-

duced by the lottery system is uncorre-

lated with completed schooling. Angrist

notes that such a correlation might exist

because eligibility for G.I. benefits

would increase the schooling of veter-

ans relative to nonveterans. This corre-lation would lead to an understatement

of the return to civilian experience if

the return to schooling exceeds the re-

turn to experience, i.e., al - aC2> 0.20

Alternatively, as Angrist notes, one can

interpret the Wald estimator as a com-

posite of the effect of military service

on experience and schooling.

However, Angrist ignores the possi-

bility that schooling and ability may be

correlated due to the fact that there isanother effect of military service on

completed schooling that arises from

the interruption of schooling (for those

19 For simplicity, the quadratic in potential ex-perience is ignored. Angrist's specification differsslightly as well in that the length of military ser-vice, conditional on service, is estimated as a sepa-rate parameter.

20In this case, where veterans obtain moreschooling than nonveterans, a - m and S are nega-tively correlated and S increases earnings, condi-tional on a - m.




who had not completed their school-ing). The effect is analogous to the ef-fect of a delay in school entry associatedwith the AK natural experiment.21 Sup-pose in the model of school choice wepresented ae is redefined not as the ageof school entry but as the age at whichmilitary service is completed, for thosewho were inducted. Assume that all in-dividuals had completed So years ofschooling at the time of induction, sayat age ae - 1, andthat it was optimal forthose not inducted to have completedan additional year of schooling regard-

less of their ability by age ae. Thus,those who actually served in the mili-tary have one less year of schooling at ae

than those who had not served. Now,given either a finite schooling or agehorizon, as in the model presented inthe previous section, those who experi-enced the (exogenous) interruption dueto military service will optimally obtainless schooling overall. Moreover, re-gardless of military service, completed

schooling will be higher for the moreable and therefore the more able willalways have less civilian work experi-ence.22 This means that unless theschooling subsidy in the form of theG.I. Bill offset these factors the Waldestimator cannot be interpreted as acomposite of experience and schoolingeffects; that composite effect is biasedupward because of the schooling-abilitycorrelation. The single draft-lottery in-

strument cannot be used to identify thereturns to experience when both school-ing and military service are correlatedwith ability, as in this very simplemodel, and schooling is unobserved.

3.3 Estimating the Returns to SchoolingWhen WorkExperience Is a Choice

The AK, BC, and Angrist studies as-sume that individuals work full-timeafter completing school or military ex-perience. Given this assumption, consis-tent estimates of the schooling returncan be obtained based on the first-birth

gender instrumental variable or thequarter of birth instrumental variablewhen schooling is a choice and thatchoice is influenced by an unobserv-able, as depicted by the simple model,holding Mincer work experience Xaconstant.23 However, suppose that indi-viduals, after leaving school, make laborsupply decisions. Would the Wald esti-mators proposed by BC and AK, or suit-ably modified estimators that accountfor actual work experience, consistentlyestimate the schooling return? If not,how will that affect the estimates of theschooling returns for the instrumentsused? Note that the issue of post-schoolwork choice is not relevant for methodsthat attempt to directly control for un-measured ability using test scores orfixed-effects.

Before turning to these issues, it is

useful to consider the empirical plausi-bility of the post-schooling full-timework assumption. Table 3, based on the1979 National Longitudinal Survey ofYouth (NLSY79), depicts the amount ofaccumulated work experience, sepa-rately for men and women, over theten-year period from age 25 through 34

21 The lottery experimentdiffers from the schoolentry age experiment in that there is no analog tothe mandatoryminimumschool leaving age.

22 The condition for obtaining an additional yearof schooling for those who served in the military isgiven by (5). Individualswho did not serve choosebetween having S0+ 1 and So+ 2 years of school-ing. If the marginalreturn to an additionalyear ofsc ooling is increasing in ability, one would expectthat at least the more able among those who didnot, serve will obtain the additional year. Onewould also expect that a greater proportion of

those who served would obtain the additional yeariff(S) is concave.

23 The differential effect of military experienceon earnings found by Angrist appears to have beenignored in the subsequent AK study. The 1990

Census indicates that in the male cohorts studiedin AK, over 30 percent were veterans.




TABLE 3

MEAN ACCUMULATEDHOURS OF WORK

BETWEEN THE AGES OF 25 AND 34, BY

SCHOOL ATTAINMENT AND SEXa

(WEIGHTED NLSY79)

Males Females

HS dropout 15,741 6,793

(11,645) (9,446)

HS graduate 18,971 11,892

(10,993) (10,202)

Some college 18,164 13,929

(10,797) (8,789)

College graduate 19,908 15,958

(7,662) (7,127)

a Standard deviation in parentheses.

for four levels of completed schooling.24For men, the largest difference in accu-mulated work experience is betweenhigh school dropouts and all others.Specifically, high school graduates ac-cumulated 3,000 more hours of workover the period than dropouts; dropouts

accumulated on average about 1600hours per year. Males with some collegeactually accumulated 800 fewer hoursof work experience than high schoolgraduates, while those with college de-grees accumulated 1,000 more hoursthan high school graduates. For fe-males, accumulated work experience in-creases monotonically with school com-pletion levels. High school graduatesaccumulated over 4,000 more hours

than high school dropouts (who aver-aged only about 700 hours per year overthe period), those with some college2,000 more than high school graduatesand those with college degrees 2,000more than those with some college. Theevidence suggests that the full-timework assumption is certainly not univer-sally valid and that there is systematic

variation in work intensity amongschooling groups.

To illustrate the consequences of in-troducing a labor supply decision for es-

timates of the schooling return basedon the BC and AK natural experiments,consider an extension of the schoolingmodel as presented above that allowsfor a work participation decision in eachpost-schooling period. For simplicity,assume that utility is additively separa-ble in income (= consumption) and themonetary-equivalent value of leisure(home production) and that the individ-ual maximizes the present value of life-time utility. In each period the individ-ual receives a wage offer that dependson schooling, experience, and ability asbefore, and additionally depends on aperiod-specific shock that is iid over pe-riods, i.e., lnya=f(S,g) + g(Xa,g) + ?a, The

value of leisure, b(S,Xa,g), may also de-

pend on schooling, experience, and

ability, but, for simplicity, is assumed to

be deterministic.

In the terminal period, age A, the in-dividual will work, pA = 1, if the current

wage offer exceeds the current value of

leisure. That decision thus depends on

whether the wage shock is larger than

some cut-off value that itself depends

on the individual's schooling, experience,

and ability, namely,

pA = I iff -A> A(S,XA,g) (10)= 0 otherwise,

where sA(S,XA,g) = ln[b(S,XA,g)] -f(S,g) -

g(XA,g). Clearly, the effects of schooling,

work experience and ability on the pro-

pensity to work will depend on their

relative effects on the value of leisure

and on wage offers. For concreteness,

suppose that neither schooling nor work

experience affects the value of leisure,

but that ability increases the value of lei-

sure. In that case increasing schooling or

experience will increase the propensity to

work at age A. However, ability may either

24To maintain a large enough sample, the final

age is the last age, between 32 and 34, that weobserve, he individual.




increase or decrease the propensity towork (given schooling and experience).

The participation decision in periodA - 1 depends on a comparison of the

expected present values of working andnot working, namely,

VA-1(PA- = 1 QA- 1) = exp[f(S,g)+ g(XA- 1,) + SA- 1]

+ 6Emax[yA(S,XA - 1 + 1,g,SA)b(g)] (11)

VA - 1(PA -1 = QA - 1) = b(g)+ 6Emax[YA(S,XA - 1,g,?A),b(g)j,

where QA-1, the state space at A -1,consists of the elements of S, XA 1R,

and -A -1, and where the expectation istaken over the wage shock at A. Thedecision rule, as in the last period, is towork if the wage draw at A - 1 is largerthan a cut-off value that depends on thenon-stochastic elements of the statespace at A - 1, that is,

PA-1=1 iff SA-1>S?A- 1(S,XA-1,L) (12)=O otherwise.

The extent to which the AK and BCnatural-experiment instrumental esti-mates provide consistent estimates ofschooling returns depends on whetherparticipation and schooling are uncorre-lated, on whether schooling attainmentaffects participation choices beyond themechanical effect on Mincer-type expe-rience. It is clear that as long as thewage offer is monotonically increasingin S, the cut-off value of the wage shock

is declining in completed schooling. Be-cause an increase in S increases the cur-rent wage, the future wage, and thepropensity to work in the future, an in-crease in S also increases the propensityto work in the current period. Unlikethe effect of schooling, an increase inthe effect of ability on the propensity towork is ambiguous; however, if abilityincreases the (positive) effect of experi-ence on wages, the propensity to workwill be more likely to increase with abil-

ity in period A - 1 than in period A.25 If

we continue to solve backwards, by in-

duction the effect of schooling on the

propensity to work will be positive at all

ages. Thus, because experience at any ageis simply the cumulation of past partici-

pation decisions, the deficit in work ex-

perience of the more schooled that re-

sults from their delayed entry into the

labor market will diminish once they do

enter and continue to diminish with

age. And, it is possible that work experi-ence of the more schooled may exceed

that of the less schooled after some age,

as is consistent with the data in Table 3.One effect of this endogenous accu-

mulation pattern is to make the bias in

the BC and AK instrumental variables

estimators that control for age but not

for actual work experience depend on

the age at which wages are measured. To

see that, consider our previous exampleof the AK experiment with two ability

types. It is easy to show that the Wald

estimator based on the difference in

earnings at age a for the population withentry age ae - 1 vs. the population with

entry age ae (assuming that everybodyworks at age a) is:

AE(Inya)= {g[Xa(So+ 1a

AS 1- 7ci

- aK,gl,sa - O)g1] - g[Xa(So+ l,a- alK- 1,91,Ea - 0),Wl]} (13)+ {g[Xa(So + l,a - aK,j2,Sa - 1),42]

- g[Xa(So,a - aK,g2,sa -1),9211

+ [f(So + 1,,u2) -f(S0,g2)],

where Ea-i represents the vector of wageshocks through age a - 1, all of which are

known at a. The first term reflects the

fact that the more able, and thus more

25 The effect of an increase in experience ismore complicated. Even if the wage is monotoni-cally increasing in experience the effect on partici-pation of an increase in experience depends on thesecond derivativeof the g function. Because of the

finite horizon, for given experience the propensityto work is lower at A - 1 than at A.




schooled, have one more year of poten-tial experience when they are permittedto enter school a year earlier. It is thesame term as in the model imposing the

exogenous full-time work assumption.The second term reflects the fact thatwhen the less able are forced to attendschool for an additional year, they nowhave the option of choosing a differentsequence of participation. The simplemodel of participation presented aboveimplies that they will be more likely toparticipate at each age, and that the dif-ference in work experience will be nega-tive at early ages and possibly positive atlater ages. Thus, the magnitude and eventhe direction of the bias in the Wald esti-mator will be age-dependent. Notice thatcontrolling for potential (Mincer) experi-ence rather than age as in AK when par-ticipation is a choice corrects for the biasassociated with the first term to the ex-tent that an additional year-of potentialexperience leads to an additional year ofactual experience. Replacing age by po-

tential experience cannot correct for thebias from the second term because thesecond term only arisesbecause potentialand actual experience differ.

Replacing age by actual work experi-ence also does not eliminate the bias inthe natural natural experiment-basedWald estimator of the estimated return toschooling (the third term in (9)) if par-ticipation decisions are dependent onability, as suggested in the model. It is

possible to develop a test for the endo-geneity of experience using the BC and/orAK natural experiments based on linear-ized versions of the decision rules fromthe model. Specifically, consider thestatistical framework that correspondsto the AK experiment (where all equa-tions are in deviation from mean form):

Inya = (XIS + cX2Xa+ sU+ Sa,

S = 1iae(q) + P2s- + ?s, (14)

Xa = YIS + Y24U ?x,

where q is quarter of birth. Notice first

that as long as 72 is not zero, the return

to schooling is not identified; there is es-

sentially one instrument, the age of

school entry (which is not related to abil-ity) and two endogenous variables,

schooling and experience. Although we

cannot identify the earnings function pa-

rameters in (10), it is still possible to test

whether experience is correlated with

ability (assuming that schooling is corre-

lated with ability), that is, whether y2 is

zero, using a modified Wu-Hausman

test. First, note that estimating the

schooling equation provides a consistent

estimate of Pi. Next, form the residuals

from the estimated schooling equation,

S - 9, which must be correlated with

ability under the maintained assumption

that 52 iS not zero. Finally, estimate the

experience equation, including S and

S - 9. If the coefficient on the residuals

is non-zero, then y2 must be non-zero.

An analogous set of equations substituting

a firstborn sex dummy for age of school

entry describes the BC experiment.Table 4 presents regression estimates

of the p-values for the coefficient on

the schooling residual for men and for

women using data from the NLSY79.

Experience is defined as actual total

hours worked from age 18 until the last

year the individual is observed in the

data (for all individuals observed at least

through age 25). The first column for

each sex presents the estimates using

the AK instrument, quarter of birth in-teractions with state of birth. The second

column presents estimates using the

modified BC instrument, the sex of the

firstborn sibling and the third column

presents estimates based on using the

two instruments together. The results

indicate that for males the exogeneity of

experience is rejected based on either

the AK or the BC instrumental vari-

ables, but not on the combination of the

two sets of instruments. For females,




TABLE 4

TESTS OF THE ENDOGENEITY OF WORK EXPERIENCE USING NATURALNATURAL NSTRUMENTS

(NLSY79)

Males Females

AKa BCb AK + BCC AKa BCb AK + BCC

P-valueof schooling .008 .031 .277 .666 .733 .097

residual oefficient

No. of observations 2,592 1,250 1,245 2,793 1,341 1,336

First-stageR2 .161 .172 .271 .120 .110 .187

aInstrumentalariables re quarterof birth nteractionswithstate of birth.Additional egressors re stateof birth,

stateof residenceatage 14,a blackdummy,a Hispanicdummyandage.bInstrumentalariable s sex of firstborn ibling.Additional egressors s above.cInstrumental ariables re quartersof birth nteractionswithstate of birth and sex of firstborn ibling.Additional

regressors s above.

however, the exogeneity of experienceis rejected only with the combined setof instruments. Although the lack of ro-bustness of these results to the choice ofinstruments does not lead us to a firm

conclusion, the results are certainly notinconsistent with the hypothesis thatwork intensity, for both males and fe-

males, is subject to choice.26 In sum, ina world in which schooling and workchoices are made optimally by individu-als heterogeneous in ability, as charac-terized even in a very simple model andfor which there is some evidence, nei-ther the AK nor the BC natural naturalinstrument as implemented identifies the

returns to schooling. And the model sug-gests that the estimates obtained usingthe different instruments but on thesame sample will result in different esti-mates of schooling returns if such re-turns vary by ability and, even if not,because of the use of age as a proxy forwork experience. Due to the latter, theestimates will further differ if there areage differences in the samples used.

3.4 The Returns to Schooling and WorkExperience When Both Are Choices:The Natural Human CloningExperiment

The natural natural experiment ap-

proach exemplified by Angrist, AK, and

BC exploited random events occurring

in nature that affect schooling or (mili-tary) experience decisions but are unre-

lated to ability. The use of these natural

natural experiments is an attempt to

mimic the conceptual experiment of

forcing otherwise identical people to in-

vest differently in human capital. A ma-

jor problem with this approach, as we

have seen, is the limited number of in-

struments, for if both schooling and

post-school investments, as proxied by

actual work time, are correlated withability (and with each other), then at

least two instruments are required.

Butcher and Case and Angrist and

Krueger must assume that work experi-

ence is exogenous in their studies, an

assumption often made in earnings

studies, because they only have one in-

strument. The exogeneity of work expe-

rience is thus a necessary assumption

for their methodology in addition to the

randomness of the instrument. The

260ne of the reasons for the difference in re-sults may be the fact that the date of birth of a

child does not strictly conform to the criterion ofrandomness, as noted.




military draft lottery, birth date, andthe sex of a firstborn child could poten-tially be used together as instruments toestimate the returns to schooling, and

military and civilian work experiencefrom a more realistic specification ofthe earnings function, but this has notbeen carried out. However, there is evi-dence that other dimensions of laborforce experience than cumulated yearsmatter for earnings, such as the timingand length of work interruptions. Ifthese work characteristics also reflectchoices that are related to ability andschooling, additional natural instrumentswould be needed to obtain consistentestimates of schooling returns.

An alternative experimental approachis to identify people who are actuallyidentical but who, for whatever reason,obtain different levels of human capital.Of course, the underlying problem is thatwe do not observe abilities and so can-not a priori identify people who are thesame. This fundamental observational

problem has led researchers to exploitwithin-pair differences of identicaltwins starting in the late 1970's (JereBehrman, Z. Hrubec, Paul Taubman,and Terrence Wales 1980; Orley Ashen-felter and Krueger 1994; Behrman, Rosen-zweig, and Taubman 1994; Paul Miller,Charles Mulvey, and Nick Martin 1995;Ashenfelter and Cecilia Rouse 1998;Behrmanand Rosenzweig 1999;and Rouse1999).27 Monozygotic (MZ) twins are

identical at conception. It has been arguedthat the differential levels of schooling

obtained by monozygotic twins, which can-

not be due to differences in genetic en-

dowments, corresponds exactly to the

conceptual experiment described above.

A major advantage of natural human

cloning, in contrast to the Angrist, AK,

and BC natural experiments, is that the

twins experiment is robust to the intro-

duction of endogenous labor supply

choices, or to the addition of any num-ber of endogenous choices that may af-

fect outcomes of interest. To see why,

note that the cloning experiment can be

placed within an instrumental variables

framework. The difference in the

schooling of twins, because it is inde-

pendent of genetic endowments, can

serve as an instrument for the school at-

tainment of either twin. Similarly, the

difference in the work experience of twins

can serve as an instrument for either

twin's work experience. Thus, unlike the

previous experiments, the cloning ex-

periment supplies as many instruments

as there are endogenous variables.

A number of assumptions are needed

to achieve identification of the parame-

ters of interest in the earnings equation

given by (3) based on the cloning ex-

periment. To see how identification is

achieved, consider (3) rewritten in lin-ear form for a pair of identical twins 1

and 2 born to familyj:

lnyg o S+vS ' 1,2 (15)

where the superscript M refers to MZ

twins, X is actual work experience, and

the returns to schooling and experience

are ,1 and 6, respectively. We can also

write in linear form the relationships be-

tween schooling, work experience, andthe unmeasured common ability en-

dowment of the twins gJ, other com-

mon family factors given by f and

twin-specific factors usij and uxij.

Sm= bs +fsj +usij, (16)

Xj = bxM +fxj +uxij. (17)

Estimation of (15) by OLS for any in-

dividual, a twin or not, given (16) and

(17), results in biased estimates of Iand 6. Put another way, there are more

27 The first published study of earnings determi-nants based on twins appears to be Behrman andTaubman (1976), which presents preliminary re-sults to the study Behrman, Hrubec, Taubman,and Wales 1980.




parameters than there are empiricalmoments in the data. Within-MZ-twinestimates are obtained by differencing(15) across the twins, which sweeps out

the common unobserved endowmentcom-ponent t'. Given the assumptionthat theability endowment is common acrossthe twins, that the twin-specific factorsdetermining schooling and experience

usij and uxij are orthogonal to the errorsv0 in the earnings equation, and thatthese random factors are drawn fromthe same distribution for each twin, thewithin-family variances and covariancesbased on the twin differences in termsof the parameters of the model are:

Var(AlnM) = 2p22Su + 28262 + 2aG, (18)

Var(ASM) 262S (19)

Var(AXM) 2a2 (20)

Cov(ASM,AXM)2cov(us,ux), (21)

Cov(Aln M,ASM) -62

+ 26cov(us,ux)and (2)

Cov(Aln yM,AXM)= 26a2

+ 2Pcov(us,ux).

As can be seen, there are now as manyempirical moments as there are parame-ters and the equations are linearly inde-pendent. There is exact identification.Adding more determinants of earningspotentially correlated with the endow-ment to (15), given the same set of as-

sumptions for these additional determi-

nants, adds as many additional empiricalmoments as additional parameters. Thus,as noted, under the maintained assump-tions, there is no limit to the number ofobserved earnings factors, potentiallycorrelated with ability, that can be addedfor which returns can be identified.

Only one of the twins human cloningstudies so far has employed informationon actual work experience. As a conse-quence, under the assumption that allworkers work full-time after school and

that post-school work experience Xa is

the appropriate measure of post-school

human capital, all but one of the set of

estimates from the cloning studies are

subject to the downward Mincer bias.Twins are always the same age, so the

twin with the greater (lesser) amount of

schooling must have less (more) work

experience. All but one of the twins-

based schooling returns estimates thus

actually identify the difference between

the returns to schooling and work expe-

rience, not the returns to schooling

given work experience. Relatedly, the

ability bias identified from such stud-

ies is not the bias in the returns to

schooling but the bias in the difference

in schooling-experience returns.

Ironically, then, only if post-school

work choices vary among twins such

that schooling and age do not com-

pletely determine work experience can

twins-based studies be used to identify

the returns to schooling, as long as in-

formation on actual work experience is

collected and used in the earningsspecification. In fact, actual work expe-

rience appears to differ significantly

across identical twins. In data collected

in 1994 by Behrman, Rosenzweig, and

Taubman based on all twins born in

Minnesota from 1936-55, 35 percent of

(215) male-twin pairs had differences of

three or more years of actual full-time

work experience beyond that accounted

for by differences in completed school-

ing. The comparable figure for the 339female-twin pairs in the data is 64 per-

cent, with more than half of those ex-

hibiting differences of eight or more

years of actual full-time work experience

net of schooling attainment differences.

With appropriate information on work

experience, there are two remaining

problems with the cloning experiment

approach, however. The first is that the

existence of errors in measurement in

any of the earnings determinants is not




only a barrier to identification, as oneor more error variances are introducedbut no more empirical moments, but theresulting biases due to measurement

error are larger when within-twin esti-mators are used compared with esti-mates based on individuals (John Bishop1976; Griliches 1979). This is becausethe bias from measurement error isgreater the higher the within-pair corre-lation of the true variables. These areespecially high among identical twins.Behrman and Rosenzweig (1999) reportfor their sample of Minnesota-borntwins that the within-pair correlation inschooling is .74 for identical twins. Thiscompares with a correlation of .52 fornonidentical twin pairs.28

With respect to the- measurement-error problem, Ashenfelter and Krueger(1994) proposed using reports by eachtwin of his or her twin's schooling as aninstrument to eliminate the bias due tomeasurement error in schooling. With asufficient set of restrictions on the or-

thogonality of the measurement errorsin these reports, these instrumentsadd more empirical moments thantheoretical parameters so that, withmeasurement error confined to school-ing, the returns to true schooling areidentified. All recent studies usingtwins to identify the returns to school-ing have used a variant of this approachto correct for measurement errors inschooling.29 Of course, there is nothing

natural about the instruments em-ployed in twins studies to correct formeasurement error. Without knowledgeof true schooling attainment, it is not

possible to test the orthogonality as-sumptions about the correlation in mea-surement errors across the twins oracross own and cross-twin reports for a

twin that are necessary for identification.The second potential problem with

the cloning experiment, and it is a ma-jor one, is that the twin-specific errors

uij may not be orthogonal to earnings,as assumed. One reason is that the un-observables that affect schooling deci-sions and wages (productivity) are notnecessarily only genetic in origin, i.e,monozygotic twins may be identical atconception, but not identical at birth oras children. For example, monozygotictwins differ in birth weight, which mayindicate that such twins do not faceidentical environments within thewomb. In a sample of 1534 monozygotic

twin pairs from the Minnesota Twin

Registry, described in Behrman, Rosen-

zweig, and Taubman (1994), the aver-

age absolute value of the difference in

birth weights between identical twins

is 10.5 ounces. The corresponding fig-ure for same-sex nonidentical twin pairs

(N = 1357) is 11.2 ounces. Thus,

monozygotic twins may have unequal

mental and/or physical capacities that

manifest themselves at birth and beyond.

In fact, Behrman, Rosenzweig, and Taub-

man (1994) report a significant positive

correlation between the difference in

the birth weights of identical twins

and subsequent differences in their

schooling attainment and thus earn-ings.30 Additionally, during childhood

28 They estimate that if the proportionof the totalvariance in schooling that was measurement errorwas ten percent, the bias towards zero in estimatesbased on individuals would be nine percent butwould be 35 percent for the within-MZ estimator.

29 In Behrman, Rosenzweig, and Taubman(1994), the report by each twin's son of the twin's

schooling attainment is used as an instrument tocorrect for measurement error.

30 There are few studies of the relationship be-tween birth weight and adult outcomes. One re-cent exception is Richard Strauss (2000), whofinds that low birth weight predicts lower aca-demic achievement and income at age 26 based onthe 1970 British Birth Cohort. The problem withthis study, and all prior studies of the conse-quences of birth weight variation, however, is thatthe separate effects of increasing the nutrition re-ceived by a fetus, which accounts for birth weight

variation within MZ twin-pairs, and possible ge-netic influences are not distinguished.




seemingly random events may occur toone twin that have long-lasting, if notpermanent, effects on characteristicsthat affect both schooling and earnings.For example, one twin may suffer an ac-cidental physical or mental impairmentthat hinders schooling attainment andearnings capacity. The permanent un-observable in these cases is not fullycaptured by a genetic endowment. Suchhealth shocks or in-womb nutritionaldifferences are likely to result in a posi-tive bias in human capital returns that isnot eliminated by differencing across

MZ twins.Even if monozygotic twins were iden-tical at birth and substantial healthshocks are relatively rare, economictheory that recognizes that investmentin human capital is a decision suggeststhat unobservables specific to twins willbe systematically related to their invest-ment decisions and to their earnings. Itis straightforward to provide an exam-ple in which optimizing behavior in-

duces a downward-biased estimate fromtwins-based estimators. Recall that theoriginal schooling choice models as-sumed that either wages were determi-nistic, with exogenous post-schoolingfull-time work, or that wage offers werereceived only after completing school-ing. Suppose, instead, the original for-mulation is changed so that a randomwage offer is received at the beginningof the first period, when the individualis deciding on whether or not to attendschool. Also, assume that this wage, ifaccepted, is fixed over the workinglife.31 If the individual rejects the offerand attends school for that period, an-other wage is drawn (independently ofthe first period wage draw) at the be-ginning of the next period that is alsopermanent. Denoting the stochastic

component of the wage draw as e, theexpected present values of earnings forthe school attendance choices are:

Vi(si = 1i So)= exp[f(So+ 1,g)]EI{exp[s2]}A

I3a + lexp[g(a,g)] - c, (24)

Vi(si = 0 So) = exp[f(So,g)]exp[si]A

* Paexp[g(ag)].

a = O

Notice that these values differ from thecorresponding ones in (3) by the actual(permanent) wage shock if the individual

does not attend school in period one andby the expected wage shock if the in-dividual attends school. The decisionrule, as before, is to attend schoolif Vi(si = I ISo)? Vi(so= I J So). However,because in this case the value of not at-tending school depends on the actualwage draw, the individual will attendschool only if the wage draw is below acut-off value, which depends on the rateof interest, the cost of schooling, the pa-rameters of the wage function (f and g),and the expectation of the (exponentialof the) wage draw, i.e.,

SI= 1 if ?1 < E{r,c,f,g,E(exp(E2))}, 25

si =O otherwise.

Thus, if one of a twin pair does notattend school and the other does at-tend, for the former we only observewages that satisfy the condition that

?1 > s*, while for the latter we observewages that span the entire wage distri-bution. The average (accepted) wagefor twins with lower schooling willtherefore overstate the average (of-fered) wage and thus the return toschooling will be understated.

Thus, despite the potential advantageof natural human cloning in providingas many instruments as there are mea-

sured earnings determinants, it is diffi-cult to conclude from the human cloning

31 The assumption of a permanent wage is only

illustrative, although it is necessary for the argu-ment that there be a persistent component.




experiment, as implemented to date,what the true returns to schooling are oreven to define their bounds. This is be-cause of (i) the possibility that schooling

decisions are influenced by persistentwage shocks, which biases schooling re-turn estimates based on within-twin es-timators downward, (ii) the omission ofwork experience, which evidently dif-fers across twins and is correlated withschooling, and (iii) the existence of atleast early environmentally-determineddifferences in endowments acrossclones that may lead to upward biases

in schooling. And, given that monozy-gotic twins differ neither in birth datenor gender, twins-based estimates can-not be used in conjunction with the AK,BC, or Angrist natural instruments tocircumventsome of these sources of bias.

4. Estimating Determinantsof Consumptionand Labor Supply

Using Weather Variation

4.1 Permanentand Transitory IncomeElasticities of ConsumptionandSavings

One of the most widely employed andtested models of life-cycle savings and

consumption is the permanent in-

come model. In recent years, re-searchers have been interested in pro-viding evidence on the extent to whichcapital markets are incomplete, as is in-dicated if consumption is excessively

sensitive to contemporaneous income.Life-cycle models of consumptionwhich admit to uncertainty about futureincome flows have the feature that theresponsiveness of consumption (and

savings) to income depends on the ex-tent to which fluctuations in income areunanticipated and transitory. Distin-guishing between transitory and perma-nent income components and identi-fying their effects are the principalchallenges of this literature. Data sets

do not provide measures of income thatconveniently identify incomes by thesetheoretical concepts. Moreover, fluctua-tions in incomes may reflect the choices

of agents-because income at any givenpoint in the life-cycle may reflect pastinvestment and savings decisions, corre-lations between income changes andconsumption may not provide much in-sight into these models. For example, inagricultural populations farmers plantseeds or invest in equipment that affectsthe level and variability of incomes(Rosenzweig and Hans Binswanger

1993), and these may reflect prefer-ences (e.g., for risk) that also affectconsumption choices.

Five studies have used weather vari-ables, in the context of farm house-holds, as a means of identifying the ef-fects of transitory and permanentcomponents of income (Wolpin 1982;Christina Paxson 1992; Hanan Jacobyand Emmanuel Skofias 1998; Anjini Ko-char 1999; and Elaina Rose 1999).

Weather has desirable features for theanalysis of income effects: weatherevents have significant effects on farmincome; weather events cannot be af-fected by the behavior of the farmersthemselves and satisfy the criterion ofrandomness; weather distributions arecharacterized by stationarity over peri-ods of time relevant to the study of in-come effects on consumption so thatthe distinctions between permanent and

transitory are meaningful; and longtime-series of data describing dailyrainfall, which are available in manycountries of the world, enable the pre-cise estimation of the permanent pa-rameters describing the moments of theweather distributions.32 Despite these

32 Note that there can be more than one mea-sure of weather (e.g., daily rainfall, the timing ofthe onset of the rainy season, number and length

of dry spells) that affects output and multiple mo-ments describing the distributionof each measure.




advantages, however, the estimates ofincome effects based on weather eventshave been based on theoretical frame-works, implicit or explicit, that haveemployed strong and untested assump-tions about the operation of rural labormarkets, preferences, and farm technol-ogy, assumptions that appear to be nec-essary for identification of the effects ofinterest. Indeed, recent work has usedweather informationto look at the directrelationship between income risk, in-come shocks, and labor supply (Roseforthcoming; Kochar 1999).

4.1.1 Income and Consumption withoutLabor Supply

To illustrate what weather-based in-struments identify and theoretical is-sues that weather-based instrumental es-timates must confront, we construct asimple farm model that incorporatestransitoryand permanent income effects.We begin with the simplest two-periodcase in which there are no inputs to

production other than weather and onlyconsumption provides utility. Thus weinitially abstract from the choice of la-bor supply and non-farm labor earningsEach farm household maximizes its ex-pected present discounted utility flowfrom consumption, E1{U(c1) PU(c2)1,where P(= ) is the subjective dis-count factor, subject to income con-straints. In each period the farmer re-ceives farm income from his output andan exogenous amount of assured in-come yo that is known in advance.33Farm income is stochastic, such thatfarm output yt=ft(t), with 0t a measureof weather at t (e.g., the amount of rain-

fall). Weather is random and iid overtime. A weather realization is drawn

each period independently from aknown distribution with finite moments.To distinguish permanent and transitoryweather, let (0t = Co+ ?t, where cois meanweather and St is an unforecastableweather shock (iid over time).

Farmers can save and borrow, but

they cannot purchase insurance and donot make bequests. With a unit outputprice, the budget constraints in the firstand second periods are thus:

cl + a2 =y1 + yo (26)C2= a2(1 + r) +y2 +yo (

where a2 is savings in period 1 andr

isthe interest rate.34In the second period,because all income is consumed, havingan extra dollar of income from anysource-whether due to living in an areain which mean rainfall is higher, gettinga favorable weather shock, or having ahigher amount of assured income-willincrease second-period consumption byone dollar. In period one, however, con-sumption effects will differ depending

on whether the assured income level isincreased (a permanent income change)or whether only farm income increasesin the period. In the first period thefarm household's problem is to choosethe level of assets to carryover to periodtwo that maximizes expected discounted

lifetime utility, U[f(i) + yo - a2] + PE.

U[(1 + r)a2 +f(0)2) + yo].

The first-orderconditionis the standardEuler equation,

U'1= P(1 + r)E(oU'2.35 (27)

It is straightforward to show that theeffect of a change in the assuredincome flow on first-period savings is

Da2/ YO= U ( r)EU2 (28a)U 1+ P(I + r)2Eo)U 2

33We assume the existence of a permanent as-sured income flow as a means of contrasting itsimpact on savings to that of income effects gener-ated by differences. in permanent weather. Ex-

tending the model to more than two periods wouldnot change any essential points of the argument.

34 Given the assumption of no bequests, initialassets (al), other than land, is zero. Thus, assetscarried into period two is identical to savings from

period one.35 We are assumingthe Inada conditions hold.




In contrast, the instrumental vari-ables estimator of the effect of perma-nent income on savings that uses vari-ation (say, over space) in permanentweather characteristics, in this case themean (6c)of the weather distribution, is

Ja2/J3

ay, / aco (28b)

U 1 yl / tT - ,(1 + r)Eow[U 2 y / aW]

U 1+ ,(1 + r)2Ew3U 2] yl / Diw

Comparing (28a) and (28b), it is clearthat the instrumental variables estimatorof the permanent income effect on sav-ings is equivalent to the true permanentincome effect only if weather affects out-put linearly, i.e., only if yt = y(c3+ St).36

Unlike permanent weather, the in-strumental variables estimator based ona change in transitory weather in periodone does identify the effect on savingsof a one-dollar increase in transitory in-

come, say from a one-dollar increase in

income that occurred in period oneonly, namely

Aa2/8S1Da2/ Dyl-=a

E

U 1 (28c)

U 1+ ,(1 + r)2EwU 2

If the model is correct, as seen in (28a)and (28c), the estimated effect on sav-ings of a one-dollar increase in transitoryincome in period one should exceed the

effect of an anticipated permanentone-dollar increase in income.37

Wolpin used differences across In-dian districts in the mean of the rainfalldistribution in order to estimate thepermanent income effect for ruralfarmers.38 He did not use an explicitoptimizing model, instead assumingboth a consumption function that waslinear in permanent income and anincome-generating function that was

linear in the rainfall mean. His findingof a permanent income elasticity close

to unity could, in the context of theoptimizing model presented above, beartifactual.39

Wolpin used contemporaneous village-level indicators of weather deviationsas instruments to estimate the transi-tory income effect. He found thoseeffects to be statistically indistinguish-able from zero, although point estimateswere quite imprecise. Paxson used house-hold survey data on farmers in rural Thai-land and time-series of regional rainfallto estimate the effects of transitory in-

come on savings. In particular, Paxson

jointly estimated the effects on savingsand on income of deviations in contem-poraneous rainfall from regional meansfor each of four crop seasons. She thentested what she called a strong ver-

sion of the permanent income hy-

pothesis-that the four season-specific

36 Using second period output in the first stageof the IV estimator, or any fixed-weighted averageof output in the two periods, would not change thegeneral result, although the bias in the estimatorwould be different for different measures of out-put.

37In the special case of quadratic utility, andwhere the rate of interest and the rate of timepreference are both zero, one-half of any increasein transitory ncome is saved (and consumed in the

next period) while none of any increase in perma-nent income is saved.

38 Note that spatial differences in permanentcharacteristics of the weather distribution couldbe poor instruments for differences in permanentincome levels if property values reflect the returns

to weather and each generation pays for these re-turns. In the worst. case, each generation pur-chases land at the market price with those inbetter-climate areas paying a higher price. In thatcase, permanent climate characteristics wouldhave no explanatory power in the determinationof income variation across space. Wolpin finds,however, that these variables produce preciseestimates of income effects on consumption inIndia.

39 Paxsonused measures of land holdings to pre-dict permanent income. This latter instrumentdoes not appear to qualify as a natural natural ex-periment, as, for example, households with larger

accumulated land holdings may be more likely tobe savers.




estimated weather-variable effects onsavings and on income were identical,equivalent to the IV estimator of thetransitoryincome effect on savings beingequal to one. Her estimates could notreject this hypothesis.40

4.1.2 Endogenous Labor Supply, LaborMarkets, and Savings

Both Paxson and Wolpin used grossfarm income net of the cost of paid in-puts as the measure of farm income.However, farm households often use

unpaid family labor instead of or in

addition to hired labor. It is obviousthat if the household uses only hired la-bor inputs, the IV estimators in (28b,28c) would have to be based on netrevenues, i.e., the value of output net ofthe cost of the hired labor.41When fam-ily labor is also used, however, the IVestimator based on the income measureused in the Paxson and Wolpin studiesyields biased estimates of income ef-fects on consumption. The direction ofthe bias and the appropriate measure ofincome to use in order to retrieve pa-rameters of interest depend on what isassumed about family labor, and moregenerally on the extent to which labormarkets are complete.

We now augment the simple farmconsumption model to allow the house-hold a choice of how to allocate the la-bor of its family members to show that

the properties of the IV estimator usingrandom weather as an instrument forincome depend importantly on assump-tions about the heterogeneity and mar-ketability of farm family labor. We fo-

cus on the identification of transitoryincome effects both because expres-sions are simpler and because the per-manent income effect cannot be cor-rectly estimated using permanentweather except under strong simplifyingassumptions about its effect on produc-tion. For convenience, we assume thatthe household's utility in each perioddepends on the total amount of leisureconsumed by its household membersand total household consumption,Ut(Ct,lt). With respect to production,we assume that there are two types of

labor inputs-manual labor and super-visory labor. Family labor and hired la-bor supplied to manual tasks are as-sumed to be perfect substitutes inproduction, while supervisory labormust be supplied by household mem-bers alone. Output in period t is thus

yt =f(ht + mt,st,0t), where ht is theamount of hired manual labor, mt is theamount of family manual labor, and st isthe amount of family supervisory labor.

Hired labor can be purchased competi-tively at wage w. The total amount ofhousehold labor is normalized to one.We assume that labor utilization deci-sions take place after the realization ofthe weather shock and that the wage isneither affected by these decisions norby the weather shock.

Assuming no bequests (other thanland and other fixed inputs) as before,the household's problem in period twois to choose the amounts of hired andfamily manual labor and the amountof supervisory labor to use in farm pro-duction. Defining maximized utility inperiod two as

V2(a2,F2) = max U[(1 + r)a2h2,M2,S2

+f(h2+ m2,S2,) + 62) + Yo (29)- wh2, 1 - mf2 -s2],

the Kuhn-Tucker first-order conditionsare:

40 Interestingly, the IV estimates using land-holdings to test the strong version of the perma-nent income hypothesis led to rejection, becauselarger land holders appeared to save too much.This is consistent with wealth and savings bothbeing related to unobservedpropensities to save.

41 Wolpin notes that profits should be defined as

net of the implicit cost of family labor, but, as withPaxson, did not have data on familylaborinputs.




DU/DI2>lM2:

JU/IC2 (30)

DU/D128 U/Jc2 f

There are two important cases to con-

sider: (i) when the marginal rate of sub-

stitution between leisure and consump-

tion equals the market wage for manual

labor (m2 > 0), which in this case means

that family labor and hired labor are

both marketed, and (ii) family labor is

only used to supervise and supervisors

cannot be hired (m2= 0), in which casethe relevant first-order condition is an

inequality and no market wage exists for

family labor.Case I: In this case, the marginal

product of (total) manual labor and the

marginal product of supervisory labor

are both equal to the market wage of

hired labor. Thus, their input demand

functions depend only on the market

wage and the weather realization, i.e.,

h2+m2= hm((02,w) and S2= S(02,W), aswell as technology parameters.42Unlike

family-supplied supervisory labor, how-

ever, family manual labor depends not

only on weather and the market wage,

but also on the level of assured income,

i.e., m2 =Mm(02,w,yo). As long as family

leisure is a normal good, an increase in

assured income will reduce the amount

of family-supplied manual labor.43

Weather has two effects on familymanual

labor. First, a favorable weather outcome

that increases output reduces m2 through

the income effect. Second, weather af-

fects the use of supervisory labor and

thus leisure, which changes the leisure-

consumption marginal rate of substitu-

tion. However, because the latter is

equal to the (unchanged) wage rate for

hired labor, family manual labor must

change one-for-one in the opposite

direction. Specifically,

Dm2 _S2 Dm2

O2 DO)2 +f3yo

Consumption increases with assured

income, but less than dollar for dollar, assome of the increased income is taken

in leisure; specifically,

DC2 Dm2=w + 1.

Dyo Dyo

The effect of the weather realization on

consumption is proportional to this pure

income effect,

DC2 DC2

=f3D(02 D/O'

Given this relationship, the IV estimator

of the pure income effect on consump-

tion must be based not on revenues net

of only the cost of hired labor inputs, but

on revenues net of the cost of hired la-

bor and family labor inputs, where the

latter are valued at the market wage for

hired manual labor. Thus, the effect of a

change in last period income on con-

sumption (the same as the effect of

assured income) is

DC2 DC2/ ?2 (31

Y2 D(y2 - wh2 - wm2 - WS2) / DS2 (

It is tedious but straightforward to

demonstrate that the IV estimator of

the effect on first-period savings of a

transitory change in first-period income

also requires that this same income

measure be used (as in period two, we

are assuming that the family supplies a

positive amount of labor to the manual

42 The effects of the weather realization on in-put demands are:

aJhm2 aS2Dh, OC

Y23Y12- Y13Y22 and a cc y13y21 - Y23Y11

43 The pure income effect on familymanual abor,

am2oc U28 1 1- 2

YOU1- UlU21,

ayo

is negative as long as leisure is a normal good.Because supervisory labor is independent of as-sured income, an increase in leisure due to an in-

crease in assuredincome must be exactly offset bya reduction in familymanuallabor.




task in period one). For example, theeffect on savings of a transitory changein income in period one is

Da2 Da2/ ae1 (32)

ayi D(yi- whi - wmi - wsi)/Del

These results imply that in the

Wolpin (1982) and Paxson (1992) stud-ies which used crop revenues net of

only hired inputs as the measure of in-come, the weather-based estimates of

savings effects are biased upward. If lei-

sure is a normal good, then favorable

weather must reduce the total amountof family supplied labor and, therefore,the effect of weather on profits net of

the cost of hired labor will understateits effect on profits net of the cost ofhired plus family labor. Thus, the IV

estimator of the impact on savings of

a transitory income change will beoverstated. Conversely, the impact on

consumption will be understated. The

study by Kochar, based on longitudinal

data from forty households in each ofthree villages in South India, focuses

explicitly on how labor supply by familymembers is responsive to income shocks

and, indeed, can serve as a consumption-smoothing mechanism. She employs a

model in which labor supply is a choice,

and, in particular, pays attention to the

fact that there are different cases or

corner solutions; in particular, that in

some households family members do

not work in the wage labor market. Ko-char estimates a household consump-tion equation only for those households

with labor market participants, takinginto account the selectivity of that sam-

ple. However, transitory income, instru-mented by monthly rainfall levels, is

measured, as in Paxson's and Wolpin'sstudies, gross of the value of family la-

bor. Kochar's finding of a small effectof the income shock on consumptioncould therefore also be due to the pres-

ence of on-farm labor-supply responses,

highlighted in her model, that are

embedded in her measure of farm profits.Jacoby and Skoufias (1998) assume,

in contrast to Kochar, that family andhired labor are perfect substitutes andnet out the cost of both hired and fam-

ily labor, valued at the market wage, asis required to obtain consistent esti-

mates of income effects in the modelunder that assumption. Jacoby andSkoufias used the same data set as Ko-

char. Profits are decomposed into an-

ticipated and unanticipated compo-

nents. Estimates of anticipated profitsare based on household and farm char-acteristics considered to be predeter-mined and their interactions with rain-

fall characteristics that are realized

prior to planting, and thus known to thefarmer at the time planting decisionsare made. Estimates of unanticipatedprofits are based on interactions of the

predetermined variables with rainfall

characteristics realized after planting

and just prior to harvesting, which areunknown at the time of planting. Aggre-

gate (village) level shocks are thus as-sumed to affect profits of individualfarmers idiosyncratically. The results ofthe instrumental variables estimation

using rainfall show that neither the ef-

fect of anticipated nor unanticipatedprofits on consumption expenditureswithin a season is statistically or eco-

nomically significant. This result im-

plies that farm households are able tosmooth consumption over seasons as if

there were perfect markets.Case II. m2= 0. We now show that

the validity of the Jacoby and Skoufias

findings, and the inferences about the

biases in the Wolpin, Paxson, and Ko-

char studies, rest importantly on the as-

sumption that hired and family labor

are perfect substitutes for at least one

labor task and that family labor is actu-

ally employed in that task. In particular,




we consider the case in which family la-bor is not employed in the manual task,e.g., the value of leisure is sufficientlyhigh and/or the marginal product of su-

pervisory labor is sufficiently high. Thiscase is equivalent to one in which thereare no production tasks in which familylabor and hired labor are perfect substi-tutes. As a consequence of this, the sup-ply of farm labor to the supervisory taskas well as the demand for hired manuallabor will not be independent of thelevel of income; that is, the productionand consumption sectors are no longerseparable. In

particular,if leisure is a

normal good, then the supply of farmsupervisory labor will decline as incomein any period increases and the demandfor hired labor will also decline if man-ual labor and supervisory labor are com-plements (and increase if they aresubstitutes).

As in the previous case, a dollar in-crease in last-period income (assuredincome) increases consumption by less

than a dollar as leisure is increased;specifically,

&C2 DS2=f2 +1.

Dy2 Dy2

This expression differs from the previouscase in that the marginal product of theinput that is affected by the change inincome (supervisory labor in this caseand manual labor in the previous case)cannot be valued at a marketwage. How-

ever, the lack of a market for tasks per-formed by family labor implies that theeffect of weather on consumption is nolonger proportional to the (assured) in-come effect. The expressionfor the effectof weather on consumption is given by:

&C2 f &C2 +f2 fl3f21 fllf23

f6 3f11f22 (33)

where A > 0 is the appropriate borderedHessian for the maximization problem.As seen in (33), the effect of weather on

consumption has two components, onethat arises from the direct effect ofweather on income (the effect that isproportional to the income effect on

consumption) and one that arises fromthe effect of weather on net profitsthrough its effect on the supply of super-visory labor (an effect that does not arisein equilibrium in the previous case be-cause the marginal product of supervi-sory labor is equal to the fixed marketwage).44 Dividing (33), the weather effect

on consumption, by the input-constant

effect of weather on revenues, i.e., by

Dh2 DS2f3 =f(h2,s2,(o2) - W 2 -f2 aO2

will not provide a consistent estimate of

the transitory income effect on consump-

tion because of the existence of the sec-

ond term in (33). Moreover, the direc-

tion of the bias in the IV estimator based

on such an income measure can be of

either sign. Similar results can be dem-

onstrated for the effect of transitory in-

come effects on period-one savings.

Thus, in this case, there is no measure of

net income that can be used as the basis

of a weather-based IV estimator of tran-

sitory income effects that would be

consistent.

The conclusions made by Rose (1999)

about Indian households' ability to

smooth consumption, in her innovative

study of the effects of weather shocks

on sex-specific child survival, based on

the same national probability sample ofrural households used by Wolpin, also

rests importantly on these labor-market

and technology assumptions. In that

study, Rose looks at the reduced-form

relationship between weather shocks-

district-specific deviations in annual

44This is just an application of the envelopetheorem in the complete markets case. In fact, thebracketed component of the second term in (33) is

exactly the effect of weather on supervisorylaborin the complete markets case.




rainfall from a 21-year average-occur-

ring at three life-cycle stages for a

child: at birth, in its first year of life,

and in its second year. She finds that

girls are less likely to survive than are

boys if an adverse weather shock occurs

in the first year after birth. She inter-

prets this as indicating that households

cannot successfully smooth consump-

tion and that when income levels are

low, resource allocations are such as to

discriminate against girl infants. How-

ever, while the inferences about dis-

crimination appear to be appropriate,

the absence of information on the rela-tionship between the weather shocks

and income in the study means that it is

not possible to assess whether the ef-

fects of the weather shocks on child sur-

vival indicate that income shocks on re-

source allocations are small or large.

Moreover, if there are no perfect sub-

stitutes for the mother's time, for exam-

ple, in the caring of children and in

farm production, then the effect of the

weather shock may reflect optimaltime-allocation responses (and prefer-

ences for boys) to weather-induced land

productivity changes and not just the

effect of income shocks, consistent with

Rose's work (Rose forthcoming) show-

ing that an adverse weather shock leads

to more off-farm work.

It would appear that a necessary con-

dition for weather variation to be useful

for estimating income effects and the

degree of consumption smoothing,given the appropriate measurement of

net income, is that family and hired la-

bor are perfect substitutes in at least

one task. If, for example, it is not possi-

ble for reasons of moral hazard to hire

supervisory farm labor, then weather-

based income effects obtained from

farm populations, where this instrument

has the most power, will be biased. To

validate studies of income effects based

on the natural natural weather experi-

ment thus requires tests of separability.Such tests themselves, however, oftenrequire additional identifying restric-tions.45 We can carry out a simple test

of the plausibility of the labor-marketassumptions used in the Wolpin, Pax-son, and Jacoby and Skoufias studiesusing a weather instrument. We use asample of 2,567 farm households from anational sample survey of all rural In-dian households, numbering 4,896, car-ried out in 1982, the Rural Economicand Demographic Survey (Vashishtha1978), supplemented by rainfall data. A

unique feature of these data is that theydistinguish between supervisory andcrop-labor time (days worked in thecrop year 1981-82) among family mem-bers. The data indicate that in over 12percent of farms at least one familymember devotes time to supervisorytasks. These are the larger farm house-holds in which the labor force is suffi-ciently large to have family membersspecialize and therefore where it is pos-

sible to readily distinguish supervisoryactivities from manual labor tasks.

We would expect that if there arehired substitutes for supervisory labor,as there appear likely to be for crop ormanual labor, exogenous variations in

permanent attributes of weather shouldhave the same effects on the amounts ofboth types of family labor. In particular,given that leisure is a normal good, inthe Indian context higher average levels

of weather should be associated withlower days worked in both supervisoryand crop tasks among family workers.Based on an annual time-series of aver-age daily rainfall from 1961 through1980 at the district level we constructedthe mean rainfall per day in the districtin which each farm household resided.

45For example, a critical assumption in Ben-jamin's (1992) test of separability among Indone-

sian farm households is that household size vari-ation conformsto the randomnesscriterion.




TABLE 5

RURAL INDIAN FARM HOUSEHOLDS: AVERAGE DAILY RAINFALL, ANNUAL CROP-LABOR DAYS

PER FAMILY WORKER AND ANNUAL FAMILY SUPERVISORY DAYS

(NCAER REDS)

Ratio of Supervisory to

Crop-Labor Days per Family Supervisory Days Crop-Labor Days

Variable Family Worker (OLS) (ML Tobit) (ML Tobit)

Mean (S.D.) 41.0 (39.6) 2.73 (13.5) .356 (5.18)

Mean rainfall -.00825 .0208 .00647

(mmper day) (.0016)a (.0030) (.0010)

Constant 49.3 -83.6 -27.8

(1.79) (5.36) (21.4)

S.E. 52.5 16.6

(2.38) (.712)

N 2,567 2,567 2,567

a Standard errors in parentheses.

We then regressed number of crop daysper family worker (adults aged 15-59)on this rainfall measure. Table 5 pre-sents the estimates. As can be seen, inareas in which rainfall levels are higher

on average, adult family members worksignificantly fewer days per year. This isconsistent with leisure being a normalgood, given that higher rainfall levelsare associated with higher output, andwith family crop labor being substitut-able with hired labor. The result alsodemonstrates why it is necessary to netout the cost of family labor from in-come in assessing income effects basedon weather variation. However, family

time in supervisory activities is actuallyhigher in such areas, as is the ratio ofsuperyisory to crop-labor family days,indicating the difficulty of obtainingmarket substitutes for supervisory la-

bor. This suggests that netting out totalfamily labor time valued at the hired la-bor wage may not be sufficient to ob-tain identification of either permanentor transitory ncome effects using weatherevents as instrumental variables.

Finally, assumptions about the local

marketability of labor inputs are notsufficient to pin down income effectsusing weather variables. Weather events

and labor supply decisions can affectnot only income but also relative com-

modity prices. In the agricultural modelincorporating labor supply choice, iden-tification of income effects using spatialand intertemporal variation in weatherevents also requires that the localweather events not affect the locale-specific price of the consumption goodrelative to the wage. One sufficient con-dition is that either all inputs, includinglabor, or all goods are perfectly spatiallymobile. Another is that leisure and con-

sumption are strongly separable. Thatthe permanent income studies do notinclude relative prices, inclusive of

wages, in the consumption function es-timated reflects one or another of theseadditional assumptions, although the as-

sumptions are never stated. In the ab-sence of these restrictions, more instru-ments would be needed than weatherevents to account for both endogenously-determined price and income effects, asrelative prices would likely be correlated




with weather-driven income variationand consequent consumption and laborsupply choices. In that case too, the ef-fects on consumption choices of uncer-

tainty about prices and wages wouldalso have to be considered.46

5. Estimating the Effect of Childrenon Female Labor Supply

A major challenge in labor economicsis to explain the secular increase in thelabor force participation of marriedwomen in the United States and mostindustrialized countries. One of the

candidate factors in the rise in femalelabor-force participation is the declinein fertility. Given that both labor supplyand fertility decisions are endogenouslychosen, instrumental variables havebeen employed in many studies (e.g.,Belton Fleisher and George Rhodes1982; T. Paul Schultz 1980; and seeMartin Browning 1992) to assess thecontribution of changing fertility onmaternal participation and work time.47The first to use a random naturalevent-twins on the first birth-to esti-mate how fertility change affects mater-nal labor supply was Rosenzweig andWolpin (1980b), followed by StephenBronars and Jeff Grogger (1994), Jaisri

Gangadharan and Joshua Rosenbloom(1996), and Joyce Jacobsen, JamesPearce and Rosenbloom (1999). Re-cently Angrist and Evans employed the

gender of the first two births, specifi-cally sex-sameness, as a natural instru-ment to estimate fertility effects onmarried women's labor supply. In thissection we show that the specific identi-fication strategies used in both the setof twins-first studies and that by An-grist and Evans place strong restrictionson both preferences and on householdtechnology and we present empiricalevidence based on unique data from In-dia that calls into question one of theseimportant restrictions. Before turningto the issue of identification, we firstreview the main empirical results of thestudies that make use of the initialtwin-births and child gender naturalexperiments.

Rosenzweig and Wolpin (1980b),using data from the 1965 and 1973 Na-tional Fertility Surveys, found that

among women who had their first birthsbetween the ages of 15 and 24, thosewho had twins on their first birth had0.65 more children on average ten yearslater.48 The same comparison forwomen who had their first births be-tween 25 and 34 yielded a difference of0.31 births. However, for the youngerage at first birth group of women, com-

pleted fertility for those with twins, asmeasured twenty years later, was only

46At least in the Indian context, spatial wagedifferences are significant and sensitive to weatherevents (Rosenzweig 1986). Given that consump-tion and leisure are substitutes, then if wage ratesand income both co-move positively with favorable

weather shocks and the wage is excluded from thespecification of the consumption equation, the es-timated transitory income effect is positively bi-ased because it also contains a substitution term.In the case in which family (supervisory) labor isnot marketed, an additional omitted variable is the

shadow wage of this labor, which is endoge-nously determined and varies with local weather.

47Almost all of these restrictions and assump-tions appear to be arbitrary. For example, inFleisher and Rhodes' study (1982) of the effects offertility on labor supply the authors assume thatparents' schooling is exogenous (there are no com-mon unobservable elements that affect both deci-

sions), and that father's schooling affects fertilitybut not the mother's labor force decisions.

48 As noted, analogous to the any sisters in-strument of BC, the existence of any twin births ina household would be an inappropriateinstrumentbecause its probability is increasing in the numberof pregnancies, even if the probability of a twinbirth is independent of the number of prior preg-nancies (actually, the probabilityof twinning is in-creasing in the number of prior births). Usingtwinning on the first birth only avoids this prob-lem. However, the probability of having a twin atany parity is increasing in age at birth. RW showthat holding age at first birth constant, eventhough the timing of the first birth may itself be a

choice, maintains the validity of the twins-firstinstrument.




0.15 greater than for those without

twins.49 This rather small difference in

completed family size leads to two im-

portant conclusions: (i) that contracep-

tive adjustment costs are small and (ii)that the twins first experiment would

seem to correspond mainly to a differ-

ence in the timing of births, i.e., having

one additional child at an earlier age

offset by having one less child over the

remaining fecund period. Bronars and

Grogger (1994) and Jacobsen, Pearce,

and Rosenbloom (1999) use 1970 and

1980 Census data and thus have larger

first-birth twins samples. Using true co-

horts, they find a similar attenuation in

total births over the ten-year period

subsequent to the birth.50With respect to labor supply, RW

found that among women who had their

first births between the ages of 15 and

24, those who had twins had a .37

percentage-point lower labor force par-

ticipation rate in that age interval than

did women without twins. Between the

ages of 25 and 34, the labor force par-ticipation rate differential fell to .10.

However, between 35 and 44, twins

mothers actually had a .14 percentage-

point higher labor force participationrate.51Dividing the labor supply effects

by the fertility effects of twins-first

yields the Wald estimates of the effect

of an additional child on labor force

participation rates.RW interpret the twins first experi-

ment within the context of a two-periodmodel of fertility and labor supply. Par-

ents also derive utility from the qualityof their children, which depends di-

rectly on their number and on the

amount of time the woman spends at

home. In addition, the market wage in

the second period depends on work ex-

perience gained in period one. There is

a fixed price of having an additional

child, e.g., birth and contraceptivecosts, independent of child quality. In

the first period, women decide on how

many children to have and on hours

worked (and implicitly on child quality)

and in the second period on hours

worked. RW's main result is that the ef-

fect of an exogenous additional child on

hours worked in either period is the ra-

tio of the compensated effect of the

fixed price of a child on hours worked

to the same compensated effect on fer-

tility.52 Note that the Wald estimator

that used the price of a child, if it were

observed, as an instrumental variable

would correspond to the ratio of un-

compensated price effects, which differs

from the effect of an exogenous addi-

tional child on labor supply that cor-

rectly is derived from the conditional

demand function.53

Angrist and Evans (1998) showedthat, as is the case for twin-first births,

the sex ratio of the first two children

affects subsequent fertility decisions.

Using data from the 1980 and 1990 U.S.

Census, they found that among parents

who have two or more children the pro-

portion who have a third birth is greater

by .06 if the first two children were of

the same sex than if they were of the

opposite sex. In terms of labor supply

effects, AE estimate that the additional(third) child reduces female labor force

participation rates by about .12 (1980).

49These figures are based on synthetic cohorts.50 See also Gangadharan nd Rosenbloom(1994).51 This reversal also occurred using true cohort

corparisons, althoughthe sample sizes were quite

sma. BG find that labor force participationratesdo not differ after ten years.

52 This result is a direct application of rationingtheory (James Tobin and Hendrik Houthakker1950-51). The resulting relationship between la-bor supply and (exogenous) fertility is a condi-tional demand function (Robert Pollak 1969).

53 Of course, full estimation of the ordinaryde-mand functions for labor supply and fertilitywould, in the context of the two-period model,

provide all of the information necessary to calcu-late the conditional demand function.




In contrast, they also find that using as aninstrument having twins on the secondbirth reduces labor force participationrates by .08.

AE's published paper does not pre-sent a behavioral model within which tointerpret their estimates. However, theydo refer to a specific model set out in anearlier version of the published article(Angrist and Evans 1996). This highlyrestrictive model, however, fails to de-liver the result that the Wald estimatorof the labor supply effect of exogenousadditional children based on the same-sex instrument is identical to the directeffect of manipulatingfertility except inthe case of having a perfect measure ofand controlling for lifetime wealth.

The twins-based and child-gender-based Wald estimators both require re-strictions on preferences and (house-hold) technology in order to go fromthe identification of an exogenous vari-able beyond the control of economicagents to the identification of how fer-

tility affects labor supply. Both thestudies that use the twins-first and sex-sameness natural experiments imposethe (exclusion) restriction that the naturalevent-having twins on the first birth or

having children of the same sex in thefirst two births-does not directly affectthe subsequent labor supply of eitherparent except through its effect on hav-ing an additional birth. What assump-tions about behavior or technology yield

this restriction? What does the Wald es-timate reveal about behavior and/ortechnology? We set out a simple modelof fertility and labor supply choices toelucidate the interpretation of the Waldestimators from these studies and to

provide a framework for garnering addi-tional empirical evidence that shedslight on the realism of the identifica-tion restrictions. The model shows thatthe restrictions required for identifyingthe fertility effect on labor supply

using either natural experiment involvestrong (and similar) assumptions aboutpreferences and household technology.

The model we set out incorporates

features highlighted in the twins-firstand sex-sameness studies-parentalpreferences and child rearing costs de-pend on the spacing of children and onthe sex composition of children. Spe-cifically, in each period of the model awoman decides on whether or not tohave a child, n {0,1}, and whether ornot to work, h= {0,1}, up to a last pe-riod when she can have no more chil-dren. In that period, the woman thusmakes a labor supply decision only. Thewoman's utility in each period dependson her consumption, c, her labor sup-

ply, the stock of children at the begin-ning of the period, N, the stock of chil-dren at the beginning of all priorperiods, and the sex composition of herchildren, where we denote r as the frac-tion of female children. The woman re-ceives a wage, w, in each period that

she works, has an exogenous income floweach period, y, and bears a per-child rear-ing cost, e. The child rearing cost is as-sumed to depend on the spacing of birthsand the sex composition of children.

All of our points can be illustrated byconsidering the final-period labor supplydecision. To obtain analytical solutions,we adopt a quadratic utility function.We also assume that the bliss-pointsex-ratio is one-half (parents prefer to

have mixed-sex children) but that thechild rearing cost, reflecting the savingsfrom sex-specific hand-me-downs, isminimized when all children are thesame sex, i.e., r = 0 or 1. Both the sex-ratio and the spacing of children are al-lowed to affect the marginal utility ofleisure. Assuming that the terminal pe-riod of the model is the fourth,54 the

54A minimum of four periods is needed to cap-

ture the possibility of different sex ratios, whichrequire at least two births.




final-period optimization problem isthen to maximize

U4 = C4 + caN3 - CC2N23

-CL3(r3- .5)2 +ac4(1-h4)+ cC4N3 + cC6C4(1- h4)

+ CC7N3(1- h4) (34)

+ CC7lNl(1 - h4) + ca72N2(1 - h4)

+ cC8(1- h4)(r3 - .5)2

with respect to the choice of h4 subjectto the budget constraint

C4= y + wh4 - elN3 - eliNi - e12N2

- e2(r3 - ,5)2 (35)

The final-period work decision ismade by comparing utility over the twowork alternatives, which will dependon both the stock and spacing of chil-dren and the sex-ratio. Specifically,suppose that the woman has two non-twin children of the same sex by theend of the third period, then the differ-

ence between the utility of working andnot working in the final period is given

byU4[h4 =

11 N3 = N2 = 2,N1 = L,r3

= fO,1}] u4[h4 = O| N3= N2

= 2,N1 = 1, r3 = fO,1}] (36)

= w(l + 2aX5) - cX4 Ud6[y - 2ei - 2e12

- eii - .5e2] - 2c7 - 20a72 - ?a71 .250C8.

If we assume that some of these pa-

rameters are stochastic from the re-

searcher's perspective, then (36) can

serve as the basis for probability state-

ments, namely that the probability thata woman with a given wage and with

two non-twin children of the same sex

works is the probability that (36) is

positive.

To determine the impact of the sex-

ratio on the probability of working net

of the effect of varying family size and

spacing, (36) can be compared to the

same utility difference when the sex-

ratiois .5 (the only other possibility

with two children), namely

u4[h4 - 1IN3 = N2 = 2,N1 = 1, r3 = .5]

-U4[h4=0 N3= N2= 2,N1 = 1,r3

= .5] = w(l + 2ca) - oC4- Ud6[y (37)

- 2el - 2el2 - ell] - 2c7 - 2ca72 - ca71.

Subtracting (36) from (37) determines

the extent to which the utility gain to (or

loss from) working is affected by having

two non-twin children of the same sex as

opposed to two non-twin children of dif-

ferent sexes-the sex-composition effect

holding fertility constant. Denoting the

left hand side of (37) as U4(1,0), this

difference is given by

Au4(1,0)Ir* N3=N2 = 2,Nj= 1

3r | (38)

= .5ca6e2 + .25ca8,

where rt = Irt 0.5 is the absolute de-

viation of the period-t sex ratio from

0.5.55 As seen from (38), three parame-

ters determine the magnitude of the sex-

sameness effect, UC6, 0C8 and e2. Thus, the

deviation from sex-sameness will affect

the labor supply decision, net of family

size effects, as long as either (i) the de-viation from sex-sameness directly affects

the marginalutility of leisure (MC8? 0) or

(ii) changes in sex-sameness affect the cost

of child rearing (e2 ? 0) and consumption

and leisure are not strongly separable.

Conversely, in this model to assume that

sex-sameness does not affect the labor

supply decision directly as in AE re-

quires that the child sex-composition and

leisure be strongly separable in the util-

ity function and that either sex-samenessnot affect child costs or consumption and

leisure are strongly separable.56

55 Notice that this expression is independent ofthe spacing of children, i.e., of whether there weretwins on the first birth, given the separabilityas-sumed between the sex-ratio and birth spacing inutility and child-rearingcost functions.

56As noted, birth spacingis ignored in the modelpresented by RW. In the model referenced in AE

(1998) contained in their prior unpublished paper(AE 1996), leisure and the sex-composition of chil-

dren are separable, child costs are independentof the sex composition of children and parental




Analogously, the effect on labor sup-ply of having twins in the first birth asopposed to two single births in the firsttwo periods, given the same sex-ratio, is

AU4(1OIN3= 2,r3= ai6el -a71, (39)

ANi1Thus, to assume that having twins in thefirst birth does not affect the labor supplydecision directly as in RW requires thatbirth spacing and leisure be stronglyseparable in the utility function and thateither having twins does not affect childcosts or consumption and leisure arestrongly separable.

In this model, the impact of havinghad an additional child on labor supplyfor a given sex-ratio can be similarly as-sessed by comparing, say, the utility inthe final period associated with thework decision when the woman has hadthree children that are all of the samesex and all single births with havingonly two (non-twin) children of thesame sex. The fertility effect on thisutility difference is

AU4(1,0)) | N2 = N1 - 1,r3 = {0,1}

AN3 (40)

= WCA + cL6(el - .25e2) - 7.

Fertility thus affects labor supply in the

model, for a given sex composition andbirth spacing, as long as either consump-tion and family size are non-separable,consumption and leisure are non-separable, or family size and leisure are

non-separable 57Comparing (40) with (38) and (39), it

can be seen that it is possible, by ignor-ing the effect of twins and sex-sameness

on child costs and imposing separabilitybetween the spacing and sex-compositionof children and leisure, for twins in thefirst birth and for the sex-composition of

children to affect fertility but not laborsupply net of fertility while exogenousvariations in fertility affect labor supply

decisions. These assumptions are requiredfor using twins in the first birth or thesex-composition of initial births as instru-ments to obtainan estimate that is equiva-lent to that of the effect of exogenousvariation in N on labor supply.58

The Wald estimate of the labor sup-ply response to an increase in the num-

ber of children based on an instrumentalvariable x is

Ah4 / A

AN3AX'

where the numerator is the change inthe fraction of women who work due tothe change in x and the denominator isthe change in the mean number of chil-dren ever born due to the change in x. In

the case of studies using twins in the firstbirth, Ax = AN1 represents the one addi-

tional child that is born. In AE, Ax = Ar2

represents the sex ratio at the beginning

of the penultimate period, r2. The sex-

sameness and twins first instrumental

variables estimates, assuming that (39)

and (40) are non-zero, are

Ah4/Ar4 Ah4

AN3/Ar* AN3 Iri,N2

Ah4 A-r3 (41)+ N3,N2,N2 X

'r3 ~ AN3

consumption is fixed at zero. Sex-sameness, theidentifying instrument, does not appear as a spe-cific measure in the model separate from sex-composition.

57In the model in AE (1996), fertility affectslabor supply directly by affecting child costs. Thisis equivalent, as in the model here, to fertility andleisure being non-separable in the utility function(Pollak and Michael Wachter 1975).

58The use of instrumental variables to estimatethe labor supply response to an additional child,

Ah4IAN3,s predicated on the assumption that di-rect estimation, i.e., comparing the fraction ofworking women among those with twins in thefirst birth to those with single births or those withtwo same-sex children to those with three same-sex children, will give a biased estimate. Thiswould be the case, for example, if women who hadtwo children differed systematically from womenwho had three children in any parameters that de-

termine their labor supply.




and

Ah4/AN1 Ah4AN4/ANi = -~ I ,N1,N2AN3/ANi AN3

Ah4 AN3 (42)+ IN3'r A

ANi , ANi

The first term in (41) and (42) is the

direct effect of a change in family size

on labor supply, the object of inter-

est. The sex-sameness and twins first

instrumental variable estimates, how-

ever, each contain a second term if no

additional restrictions are imposed on

preferences and child costs. In the case

of sex-sameness, this second term arisesbecause having a third birth will in al-

most all cases also change the sub-

sequent sex-ratio, and this may directly

affect both the marginal utility of lei-

sure and child costs and thus labor sup-

ply.59 In the case of twins, having twochildren simultaneously may directly af-

fect both the marginal utility of leisure

and child costs and thus labor supply.60

Besides clarifying the multiplicity of

structural assumptions that are required

to justify the interpretation of the

instrumental-variable estimates based

on these natural experiments, themodel indicates the information thatwould be useful in gauging their plausi-bility. Although providing credible esti-

mates that would reveal whether spe-cific commodities are separable or notin the preference function is likely notfeasible, it is possible to examine the re-lationship between the sex-sameness ofchildren and child costs. We use uniqueinformation from the same Indian dataset we used to examine the relationshipbetween permanent weather and familylabor time. These data provide for 4,896

rural households in 1982 household ex-penditures on clothing and footwear forevery child in the household, likely can-didate commodities for which sex-specifichand-me-down savings are possible.

India is a country well-known forchild sex-bias among parents. Parentalpreferences for boys in India probablydominate their concern for achieving abalance in the sex ratio that Angrist andEvans highlight for U.S. parents. This

preference at the household level re-flects in part cost differentials by sex, asin most parts of India a dowry mustbe paid when daughters are married(Behrman, Andrew Foster, Rosenzweig,and Prem Vashishtha 1999). Thus, thesex of children affects child-rearing costsdirectly, as allowed for in the Angristand Evans' two-stage least-squares esti-mates, and we would expect due to pa-rental sex-bias that measures of the sex-

ratio of the first two births will also affectfertility in India, although perhaps in adifferent way than in the United States.However, in both countries the econo-mies associated with sex-sameness fromthe use of same-sex hand-me-downsshould be similar in kind if not in mag-nitude. The empirical issue is whetherchild-rearing costs are also affected bysameness, the identifying instrument.

As part of the sample survey, allmothers aged 15 through 50 residing in

59For example, in the extreme 'case in whichonly families with children of the same sex have anadditional child, approximately half could not ex-ploit same-sex hand-me-down savings for thisadditional child. Unless consumption and laborsupply are separable and ignoring the issue ofwhether or not sex composition and leisure areseparable, as indicated by (41), the sex-sameness

instrumental-variableestimator confounds the di-rect effect of changing family size on labor supplywith the effect of also changing child costs or aconsiderableproportionof women

60AE also compare he sex-samenessnstrumental-variable estimate to that based on twins (in thesecond birth) to draw inferences about the effectsof birth spacing. However, without the special re-strictions on costs and on the utility function thatmake expression (41) vanish, the comparison ofthe sex-sameness estimate with that obtainedusing twins as an instrument does not identify theeffect of birth spacing. If (41) and (42) were bycoincidence identical and non-zero, one would get

the same biased estimate of fertility effects onlaborsupply.




TABLE 6

AVERAGESAMPLE CHARACTERISTICS:

RURALINDIAN MOTHERSAGED 30-50 AND THEIR CHILDREN AGED 6-7(NCAER REDS)

Mothers Girls Boys

Number of live children 4.51

(1.79)a

Average hours worked per day 4.67

(3.69)

Age 39.8 11.8 11.8

(5.37) (3.27) (3.29)

Per-child clothing expenditures (1982 - 95.2 100.2

rupees) (175.9) (121.8)

Per-child educationalexpenditures 76.6 107.0

(1982 rupees) (371.9) (230.1)

Number in sample 2,356 2,703 3,040

a Standard deviation in parentheses.

the sampled households were inter-viewed to obtain a complete fertilityroster providing the birth dates, order,sex, and survival status of each child

born, along with information on the av-erage hours that the mothers worked ina day in each of three crop seasons.Each mother was also asked to provideinformation on expenditures in the pastyear for each child on clothing and foot-wear. Expenditures on education (books,school fees, writing instruments) werealso provided. Unlike for clothes, how-ever, as most Indian children attendmixed-sex schools, the sex-sameness of

bir-ths should not affect cost savingsfrom hand-me-downs with respect toeducational expenditures. We should nottherefore expect to see sex-samenessaffect the patterns of these expenditures.

Table 6 provides descriptive statisticsfor the sample of mothers aged 30-50and their children of potential schoolage. As can be seen, compared to coun-tries like the United States, fertility isvery high in India-mothers aged 30 andabove in 1982 had 4.5 living children. Sex

discrimination is apparent in schoolingexpenditures, which are on average al-most 40 percent higher for boys in theage range 6 through 17 than for simi-

larly aged girls, a difference that is sta-tistically significant at the .001 level.61Expenditures on clothing do not, how-ever, differ significantly across boys andgirls in that age range. More impor-

tantly, for the purposes of examining

the relationship between changes in

child costs, fertility, and labor supply, itcan be seen that expenditures on chil-

dren's clothing are a non-trivial part ofthe household budget in rural India. At

the time of the survey, the averagewage for rural male workers was 8.5 ru-

pees per day, and that for women 6.7rupees per day. For the average house-hold in the sample, earnings are about3000 rupees. For women aged 30through 50 in the sample, there are on

61 Discrimination may as well be reflected in theratio of boys to girls-girls represent 47 percent ofall surviving children. There is evidence that this

disparity in part represents selective mortality(Rosenzweig and Schultz 1982; Rose 1999).




TABLE 7

NONPARAMETRIC,OLS,AND WALD ESTIMATES:SEX COMPOSITIONOF FIRST Two CHILDREN, LABORSUPPLY,AND

FERTILITY,RURAL INDIAN WOMEN AGED 30-50a

(NCAER REDS)

OLS Reduced-Form

Sample Nonparametric Reduced- Estimates, with Wald

Means Form Estimates Restrictions, Estimate

Total Hours Total Hours Hours

Dependent variable children worked children worked worked

Girl/girl .208 .386 -.169

(.114)b (.228)

Boy/boy .324 -.112 -.301 -

(.100) (.206)

Boy/girl .243 -.198 .368

(.103) (.223)

Girl/girlor Boy/boy = 1 .532 .185 -.441

(.073) (.154)

Total children 4.51 -2.38

(1.27)

Constant 4.51 4.72 4.41 4.91 15.4

(.076) (.158) (.052) (.115) (5.75)

F 10.6 3.68 6.36 8.24 3.49

(d.f., d.f.) (3,2250) (3,2250) (1,2250) (1,2250) (1,2250)

a Number of women = 2,356; number of households = 2,251.b Standard errors in parentheses corrected for household clustering.

average 2.4 children aged 6 through 17residing in the household. Annual cloth-ing expenditures on these school-agedchildren thus represent 8 percent of in-

come, and about 11 percent includingall children younger than 18.

The high fertility of the Indianwomen means that the decision to have

a third child, examined by AE in thecontext of the United States, is not ascritical a fertility decision. Indeed, inthe sample of mothers aged 30 andabove, 80 percent had at least three liv-ing children. However, the Indian dataindicate that, consistent with both sex-bias and sex-sameness interpretations,the sex-composition of the first two(surviving) children has a significant ef-fect on total fertility, as in the UnitedStates. The first and second column of

estimates in Table 7 report nonpara-

metric reduced-form estimates of the

relationship between the exhaustive

set of variables characterizing the sex-

composition of the first and second liv-

ing children and total children and av-

erage hours worked per day by the

Indian sample mothers. The set of sex-

composition variables explains a statisti-cally significant proportion of the vari-

ation of both variables, with mothers

with two girls as their first two children

having on average almost 1/2 more chil-

dren than women who have both first and

second-born boys. Interestingly, moth-

ers with two boys have both lower fer-

tility and lower hours worked compared

with women who have two girls. How-

ever, imposing the restriction as in An-

grist and Evans' initial set of Wald




TABLE 8

OLSESTIMATESOF SEX AND SAME-SEX HAND-ME-DOWN EFFECTS,

BYBIRTH ORDER AND EXPENDITURE TYPE: RURAL INDIAN CHILDREN AGED 6-17(NCAER REDS)

Per-Child Educational

Expenditure Type Per-Child Clothing Expenditures Expenditures

Birth order of child 1 3 1 3

Has same-sex older sibling - -19.9 4.88

(9.34) (13.6)

Child is a girl 0.729 -10.1 -27.0 -43.0

(5.21)a (6.39) (10.6) (18.6)

Age 4.31 4.72 8.84 8.14

(.807) (1.40) (1.72) (1.89)

Constant 42.8 92.9 116.9 177.7(24.3) (33.1) (47.7) (87.9)

F-statistic 14.4 5.12 15.4 8.88

(d.f., d.f.) (2, 1718) (3, 982) (2, 1718) (3, 982)

Number of mothers 1,878 1,023 1,878 1,023

Number of households 1,719 993 1,719 993

a Standard errors in parentheses corrected for household clustering.

estimates that only sex-sameness mat-

ters for fertility yields results qualita-tively similar to those from U.S. data:Indian women with same-sex first andsecond births have higher subsequentfertility and lower hours worked (col-umns three and four), and the restric-tive Wald estimate of the effect of totalchildren on labor supply, which makesuse of the same-sex exclusion restriction, snegative and statistically significant (finalcolumn).

The finding that the Wald estimate isnegative for sex-sameness, as we haveshown, does not indicate anything aboutthe structure of child costs, in particu-lar of the absence of same-sex effectson costs. A direct test of the existenceof same-sex hand-me-down cost savingsthat is highlighted in the model is to as-sess whether there are lower clothingexpenditures among higher-parity chil-

dren who have an older sibling of thesame sex. The illustrative model that we

have set out omits, however, the possi-

bility that parents care about a child'ssex per se or exogenous differencesin costs by sex. Identification of sex-sameness effects from sex effects onchild costs is potentially a key issuehere, as it is in AE's study of fertilityeffects on labor supply. This is particu-larly so if in general girls impose highercosts than boys, as is plausibly the casein India. However, it is possible to sepa-rate sex preference and general sex-

specific cost differential effects fromsex-sameness effects on clothing costsby looking at the relationship betweenthe child's sex and child-specific expen-ditures on clothing for first children.Because same-sex hand-me-down costsavings are irrelevant for first births,the effect of the sex of the first child onclothing costs only reflects either pref-erences, e.g., parents may prefer to

spend more on male children, or in-come effects, e.g., the birth of the male




child reduces lifetime income less thandoes that of a female child.

Table 8 reports in the first columnthe relationship between a child's sex

and the child's clothing costs for school-age first children. As can be seen, thereis no statistically or economically sig-nificant effect of the child's sex forthese children-families who have aboy first compared with families whohave a girl first do not spend any moreor less on clothing for that first child.This is consistent with the absence ofimportant sex-differentials in clothing

costs or income effects on clothing ex-penditures related to the sex-compositionof children.62 In the second column ofTable 8, we report for order-three chil-dren the relationship between thechild's clothing costs and whether ornot that child has an older sibling of thesame sex, controlling again for thatchild's sex and age. The estimates indi-cate that sex-sameness has a statisticallysignificant and substantial negative effect

on child costs for children aged 6-17; thepoint estimate indicates among order-three children clothing costs are 20 per-cent less for children with same-sex oldersiblings compared with those childrenwithout same-sex younger siblings.63

What happens to the sex composition ofchildren when the third child is bornevidently matters for child costs. Giventhat on average Indian families would

have two same-sex children, the existenceof these hand-me-down economies wouldevidently save 40 rupees a year, orslightly more than one week of full-timework for women,64 for a considerablesegment of the women's life-cycle.

To assess whether the same-sex effectfor clothing is merely spurious and pos-sibly reflective of complex but generalsex-composition effects not related to

hand-me-down savings, we estimate thesame specification for educational ex-penditures, for which, in India, thescope for cost savings related to sex-sameness would be relatively limited.The educational expenditure estimatesfor first children in column three of Ta-ble 8 indicate that, unlike for clothing,having a boy first rather than a girl re-sults in higher expenditures for the firstchild, so that for this component of

child costs, sex composition evidentlymatters.65However, consistent with theabsence of a cost advantage for schoolexpenditures that are related to sexsameness, school expenditures on thirdchildren, controlling for their sex andage, are no different for those childrenwho have same-sex older siblings andthose who do not.

62 Incorporating cost differentials in the tech-nology of the model is straightforwardand wouldimply that sex-sameness effects on costs forhigher-order children would differ by sex. Allow-ing for sex-composition induced income effects on

child expenditures would entail enlarging themodel choice set. Consistent with the results forfirst children, however, we could find no statisti-cally significant difference in cost savings fromsex-sameness for boys or girls (p = .21). The datathus do not suggest that either of these explora-tions would be empiricallyfruitful.

63 If there is heterogeneity in preferences forgirls and boys among ouseholds and this is re-fected in differential survival, then these esti-mates are likely to understate savings from same-sex births. This is because those households thatprefer more strongly boys or girls are more likelyto have surviving same-sex children compared

with households with a more mixed-sex composi-tion. In that case the third child in a same-sex

household will be on average in the preferred

group and thus may be provided with more re-sources. Note that the existence of preference het-erogeneity for sex-ratios, even if there were no se-lective mortality as is presumably the case in theUnited States, implies that the fertility variationinduced by exogenous variation in sex ratios wouldreflect preference variation. In that case additionalrestrictions on preferences would be required touse sex-ratio variation as an instrument to identifyhow additional children affect labor supply.

64 The average (8-hour) daily wage for women is6.5 rupees as noted, and a standardwork week issix days.

65This differential mainly reflects the fact that

boys attend school for more years than girls onaveragein India.




That sex-sameness is related to ex-

penditures on children's clothing and to

educational expenditures in ways con-

sistent with the existence of same-sex

hand-me-down cost economies suggests

that instrumental variable estimates of

the effect of fertility on labor supply

based on measures of sex sameness, as

used in Angrist and Evans, will in the

Indian context confound the effect of

an exogenous increase in children on

labor supply with direct child-rearing

cost effects on labor supply-the sex

composition of children plausibly alters

labor supply through mechanisms otherthan through fertility change alone. Of

course, it is not possible to infer from

this evidence whether hand-me-down

economies associated with the sex-mix

of births are an important phenomenon

in the United States, the context in

which Angrist and Evans carried out

their empirical work. Even if child costs

were not importantly related to sex-

composition, one still has to make

strong assumptions about preferencesto obtain identification of fertility ef-

fects as interpreted in AE. These re-

sults suggest, however, that additional

data and theoretically grounded empiri-

cal work are required to better under-

stand the relationship between fertility

choices and labor supply.

6. Conclusion

The pioneering studies that have ex-

ploited the natural experiments pro-

vided by nature clearly demonstrate the

potential value of these newly discov-

ered tools. The contribution of these

studies, however, is not in providing

dramatically different results than ob-

tained using more conventional ap-

proaches-most of the estimates are not

very different-nor in providing esti-

mates that are conclusive. It is evident

that natural events used as instrumentsdo not provide estimates that can be

unambiguously interpreted, althoughthe range of possible alternative inter-pretations may have been reduced. Wehave seen, for example, that the choiceof which natural events to use as an in-strument matters-the use, for exam-ple, of date-of-birth as an instrumentfor schooling attainment provides an es-timate of schooling returns for a differ-ent segment of the population thandoes the estimate based on gender as aninstrument for schooling, and each is

subject to a bias from the same mis-

specification that is of opposite sign.

Nor is there a breakthrough here thatobviates the need to specify behavioralmodels and market structure, to take carein measurement, or to pay attention tomatters of specification.

What then is the contribution and thefuture for the natural natural experi-mental approach? The contribution is inboth focusing attention on the impor-tant matter of identification in a worldin which measurement of all relevant

characteristics of agents is impossibleand in drawing our attention to a set ofvaluable tools, provided by nature, thatreduce the number of untestable as-sumptions required to obtain useful es-timates. And, such gifts of nature mayalso limit the range of possible alterna-tive interpretations that could be givento estimates obtained with them. Evi-

dently, however, the potential for the

strictly natural natural experimental ap-proach, which relies exclusively on natu-ral events as instruments, is constrained

by the small number of random eventsprovided by nature and by the fact thatmost outcomes of interest are the resultof many factors associated with prefer-ences, technologies, and markets. Andthe prospect of the discovery of newand useful natural events is limited.This is not to say that all natural events

have been exploited-the contrasts oftwin (first) birth effects that depend on



I Rosenzweig and Wolpin: Natural Natural Experiments 873

whether the twins are both girls or boysor mixed gender or identical have notbeen used in any empirical studies toour knowledge, and information based

on lightning strikes that destroy specificfacilities or stores could be employed todraw inferences about optimal store orfacility location.66

But it is clear that the number ofnatural instruments will never be suf-ficient to eliminate the necessity ofimposing auxiliary assumptions or ofobtaining supplementary empirical in-formation relevant to the assumptions

needed for identification. In combininginformation on natural events withinthe context of a coherent model that de-scribes the behavior under study andwith supplementary empirical informa-tion on the model structure, such as ontechnology or the extent of market com-pleteness, future work can provide amore solid foundation for further ad-vancement of empirical knowledge.Measurement without theory, however,

is not significantly more valuable than itever was before the use of natural naturalexperiments.

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