ABORTION LEGALIZATION AND CHILD LIVING...

ABORTION LEGALIZATION AND CHILD LIVINGCIRCUMSTANCES: WHO IS THE ‘‘MARGINAL CHILD’’?*

JONATHAN GRUBER

PHILLIP LEVINE

DOUGLAS STAIGER

We examine the impact of increased abortion availability on the average livingstandards of children through a selection effect. Would the marginal child who wasnot born have grown up in different circumstances than the average child? We usevariation in the timing of abortion legalization across states to answer thisquestion. Cohorts born after legalized abortion experienced a significant reductionin a number of adverse outcomes. We find that the marginal child would have been40–60 percent more likely to live in a single-parent family, to live in poverty, toreceive welfare, and to die as an infant.

Access to abortion is one of the most contentious public policyissues facing the United States today. The period since thelegalization of abortion under the Roe v. Wade decision of 1973 hasbeen marked by incessant debate over the appropriate govern-ment financing and legal status of abortions. Meanwhile, preg-nancy resolution through abortion is a very common outcome inthe United States; roughly 25 percent of all pregnancies areaborted [Ventura et al. 1995]. As a result, major changes inabortion access could have substantial effects on the birthrate.Indeed, Levine, Staiger, Kane, and Zimmerman find that thelegalization of abortion in the early 1970s led to an 8 percentreduction in the birthrate.1

To the extent that abortion access reduces the size of a birthcohort, one question of particular interest from a policy perspec-tive is its effect on the living circumstances of the children who areborn. Inherently, this is a question about selection: would thosechildren who were not born because of abortion access have livedin different circumstances than the average child in their cohort?For example, if the women who terminate their births would haveborne children into families that were single female-headed orpoor or both, then improved abortion access could lead to a

* We are grateful to Amber Batata for superb research assistance, and toLawrence Katz, two anonymous referees, and seminar participants at HarvardUniversity and the National Bureau of Economic Research for useful comments.Gruber acknowledges funding from the National Institute on Aging.

1. Although Kane and Staiger [1996] and Levine, Trainor, and Zimmerman[1996] do not find increases in the birthrate from more modest changes in abortionaccess.

r 1999 by the President and Fellows of Harvard College and the Massachusetts Institute ofTechnology.The Quarterly Journal of Economics, February 1999

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reduction in the rate of child poverty and welfare utilization.2 Yet,there is little direct evidence on the effect of abortion access onchild living circumstances.

The key to answering this question is understanding howabortion influences the selection of which women carry pregnan-cies to term. A priori, the direction and size of selection is unclear.On the one hand, if women use abortion to avoid bearing childreninto adverse circumstances, positive selection would result: theliving circumstances of the marginal child are not so good as thoseof the average child, so that increased abortion access will raiseaverage living standards of the children who are born. On theother hand, negative selection would result if, for instance, themost disadvantaged women are constrained in their abortionaccess, either geographically or financially.3 In this case, the livingcircumstances of the marginal child would be more advantageousthan those of the average child, and abortion legalization mayreduce the living standards of those children who are born.Ultimately, the direction of selection, and the effects on subse-quent child living circumstances, is an empirical question.

In this paper we examine the effect of the largest change inabortion availability in the United States, increased access in theearly 1970s through Roe v. Wade and comparable state laws, onthe living circumstances of the cohorts of children born in theseyears. More specifically, following Levine et al. [1996], we notethat Roe v. Wade followed on the heels of abortion legalization infive states around 1970. This generates two ‘‘natural experiments’’for analyzing the effect of abortion access: the change in these fivestates, versus the remainder of the country, beginning in 1971(incorporating a gestation lag after the 1970 legal changes), andthe change for the remainder of the country, versus these fivestates, beginning in 1974 following the 1973 Roe decision. Thelarge reduction in the number of births associated with legaliza-tion, as documented by Levine et al., provides the impetus forfocusing on the resultant living standards of the remaining cohortof children.

2. This point has been recognized, in reverse, in the recent debates overwelfare reform, as opponents of abortion expressed concern that reducing welfaregenerosity could lead single (potential) mothers to terminate their pregnancies.

3. In fact, there appears to be a strong geographic correlation between accessand income: in 1980, 27.2 percent of counties with poverty rates of 15 percent orbelow had abortion providers, while only 10.6 percent of counties with povertyrates above 15 percent had providers (author’s tabulation of 1980 census data,using data on abortion provider location from Kane and Staiger [1996]).

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We carry out our analysis using the 5 percent Public UseMicro Sample (PUMS) of the 1980 Census. The PUMS data allowus to observe the living circumstances in 1980 for cohorts ofchildren by state of birth and year of birth. In addition, the PUMSprovides sufficiently large samples to identify the relatively smallexpected effects on average living standards. We also use data onbirthrates and birth outcomes available by state and year of birthfrom the U. S. Vital Statistics.

We find evidence of sizable positive selection: the averageliving circumstances of cohorts of children born immediately afterabortion became legalized improved substantially relative topreceding cohorts, and relative to places where the legal status ofabortion was not changing. Our results suggest that the marginalchildren who were not born as a result of abortion legalizationwould have systematically been born into less favorable circum-stances if the pregnancies had not been terminated: they wouldhave been 60 percent more likely to live in a single-parenthousehold, 50 percent more likely to live in poverty, 45 percentmore likely to be in a household collecting welfare, and 40 percentmore likely to die during the first year of life.

I. REVIEW OF RELATED LITERATURE

Several types of studies have either directly or indirectlyaddressed the issue of selection in response to changes in abortionaccess. The first is state-level analyses of abortion, which regressabortion rates on state characteristics. Such analyses consistentlyfind a strong positive correlation between abortion rates and stateincome per capita (i.e., Blank, George, and London [1994]). Evenas states get richer and increase abortion access, however, there isno obvious implication for which women within the states areobtaining abortions, so that these studies offer little insight intothe process of selection.

The second type of study is micro-data analyses of theabortion decision, focusing on the characteristics of women thatare correlated with their decision to terminate their pregnancies.These studies yield mixed results: abortion among teens is morelikely if they are unmarried [Joyce 1988], but among unmarriedteens it is positively correlated with their mother’s education andwith living with both parents [Cooksley 1990; Lundberg andPlotnick 1995]. But these studies do not necessarily have implica-tions for average living standards, since there may be selection

WHO IS THE ‘‘MARGINAL CHILD’’? 265


along unobservable dimensions which counteracts, or augments,the selection that is observed. Moreover, most of these studiessuffer from the notoriously poor quality of data on abortion thatare available in micro-data surveys, particularly the NationalLongitudinal Survey of Youth (NLSY), the data used by bothCooksley and Lundberg and Plotnick. Based on national compari-sons with administrative data on abortions, Jones and Forrest[1992] find that only 40 percent of abortions are reported in theNLSY, and that underreporting of abortions is largest for disadvan-taged groups such as nonwhites and unmarried women. If thequality of the abortion data varies systematically with livingcircumstances, estimates of selection using micro data will bebiased.

Third, and more closely related to our approach, is studies ofthe effect of abortion availability on infant outcomes. A largenumber of studies demonstrate that there is positive selection onfetal health: abortion access, as measured by number of providersor abortion rates, is correlated with a sizable improvement ininfant outcomes such as low birth weight or neonatal mortality[Grossman and Jacobowitz 1981; Corman and Grossman 1985;Joyce 1987; Grossman and Joyce 1990; Currie, Nixon, and Cole1996]. But this evidence may not be pertinent for assessing therelative living circumstances of cohorts who do and do not haveaccess to abortion; the pregnancies that are terminated may havebeen those of well-off women who had unhealthy fetuses, so thatselection on living circumstances is negative even as selection onfetal health is positive. Moreover, the effects of marginal variationin provider access may be different than the large changesinherent in legalization.4

Perhaps the most relevant evidence comes from Levine et al.[1996], who employ the same quasi-experimental framework usedhere to identify the effect of abortion legalization on birthrates.They find that births to teens, women over age 35, nonwhitewomen, and unmarried women fell the most in response toabortion legalization. These findings do not tell a completelyconsistent story regarding the anticipated effect on children’s

4. This follows from the fact, noted above, that Levine et al. [1996] find muchlarger effects of legalization on birthrates than do other studies of variation inMedicaid funding restrictions [Levine, Trainor, and Zimmerman 1996] or provideraccess [Kane and Staiger 1996]. Grossman and Jacobowitz [1981] do include avariable for abortion reform in 1970 in their cross-sectional neonatal mortalityregression; but they rely on a broader set of repeal states (see the discussion below)and do not exploit the changes in legalization over time.



future living circumstances. For instance, the smaller share ofbirths born to teens or single mothers may improve average livingstandards, but the smaller share born to older mothers mayreduce them. Moreover, within each group, those mothers choos-ing to abort may have been positively or negatively selected. Theresults in Cooksley [1990] and Lundberg and Plotnick [1995]actually suggest this: the set of teen mothers who choose to abortin response to legalization come from higher income families. Wetherefore turn to a more direct analysis using the 1980 censusdata.

II. EMPIRICAL STRATEGY

We take a direct approach to measuring the effect of abortionaccess on the living circumstances of subsequent cohorts ofchildren, relying on the major changes in the legal status ofabortion across the United States in the early 1970s for identifica-tion. Prior to the late 1960s, abortion was illegal in every state inAmerica except when necessary to preserve a pregnant woman’slife. Between 1967 and 1973 a number of states implementedmodest reforms making it legal for some women to obtainabortions under very special circumstances, such as rape, incest,or a serious threat to the health of the mother. Abortion becamewidely available, however, in five states in 1970. In four of thesestates, there was a repeal of antiabortion laws: New York,Washington, Alaska, and Hawaii. In the fifth, California, therewas a ‘‘de facto’’ legalization, since in late 1969 the CaliforniaState Supreme Court ruled that the pre-1967 law outlawingabortion was unconstitutional.5 Following the 1973 SupremeCourt decision in Roe v. Wade, abortion became legal in all states.

This legislative history enables us to employ a ‘‘differences-in-differences’’ strategy to estimate the effect of abortion legalizationon average living circumstances, following Levine et al. [1996].The basic idea is to compare differences over time in the livingcircumstances of cohorts born in the ‘‘repeal’’ states (the five stateslisted above), relative to cohorts born in other states. Levine et al.show that there was little effect of the more modest reforms in

5. Furthermore, evidence indicates that legal abortion was widely availablein California beginning in 1970, with legal abortion rates among women living inCalifornia being comparable to rates for women living in New York. See Potts,Diggory, and Peel [1977] pp. 75–77, 149, and see Garrow [1994] pp. 377–380,410–411, and 457, and references cited in footnotes 25 and 76 from Chapter 7.



other states on birthrates, so we include these states in our controlgroup.6 We depict this strategy hypothetically in Figure I, for atypical measure of living circumstances, the percentage of thecohort living in poverty. We consider the case of positive selection,whereby abortion legalization improves living standards. The linein this figure is the difference in poverty rates between the cohortsborn in repeal and nonrepeal states over time. Time in this figurerefers to the year of birth of the cohort.

In region A, which is the 1970 and earlier cohorts, there issome constant difference in poverty rates between these two setsof states (k), due to underlying differences in the population ofresidents. Then, under our assumption of positive selection, thepoverty rate falls in the repeal states relative to other states forcohorts born after 1970, as abortion becomes widely available inthe repeal states. That is, since the children who are aborted werethose who would have lived in the most adverse circumstances,the average living standards of the remaining children improve.Thus, in region B the poverty rate is (relatively) low amongcohorts born in repeal states from 1971 to 1973. In 1973 abortion

6. Our results are very similar if we exclude this group of states from ourcontrols, or if we incorporate them into our analysis as a second treatment group.

FIGURE IHypothetical Difference in Poverty Rates between Cohorts Born in Repeal and

Nonrepeal States



becomes legal nationwide. At that point, poverty rates are onceagain equalized across these two sets of states in region C, asnonrepeal states experience a similar improvement in averageliving circumstances following legalization of abortion. Onceabortion is legal nationwide, the difference between the povertyrates in these two states returns to its steady-state (prelegaliza-tion) value.

This stylized depiction suggests two simple tests of the effectof legalization on average living standards. The first is to compareregion B with region A: if there is in fact positive selection, as isdepicted here, living circumstances should improve for cohortsborn after 1970 in the repeal states, relative to the nonrepealstates. The second test is to compare region C with region B: onceagain, under the hypothesis of positive selection, relative livingcircumstances should improve for cohorts born after 1973 in thenonrepeal states (or relatively deteriorate in the repeal states).These are the basic tests that we carry out below.

Reality, of course, deviates in at least three significant aspectsfrom this stylized depiction. First, in the absence of abortionreform, there may have been underlying trends in living stan-dards across these sets of states. For example, there may havebeen a falling poverty rate in the repeal states, relative to otherstates, for reasons other than abortion legalization. This wouldpotentially confound our first test, since there would be a relativedecline in adverse living circumstances over time regardless ofabortion policy. As we discuss below, this problem is exacerbatedin the census data by our use of a single 1980 cross section, whichconfounds aging and time effects.

We deal with this problem in three ways in our empiricalwork. First, we introduce distinct quadratic time trends for eachstate in our analysis, allowing us to distinguish our effects from a(parametric) trend. Second, we control for other state-specifictime-varying factors in the year of birth which could have affectedselection into the cohort. Finally, by finding consistent resultsfrom both of the tests described above, we can rule out spurioustrends unless they reverse for some reason after period B.

A second shortcoming of this framework is that the‘‘bounceback’’ from segment B to segment C may occur less rapidlythan does the reduction in adverse circumstances from segment Ato segment B. By being first movers in increasing abortion access,the five repeal states revealed their willingness to make abortionavailable. The states that were forced into legalization by Roe v.



Wade may have been less positively disposed toward abortionavailability, so even de jure legalization may not have implied alarge increase in de facto access.7 Moreover, the women whowanted abortions most in the nonrepeal states may have traveledto the repeal states to obtain them, so that the shift in use ofabortion after Roe v. Wade was muted.

In fact, this view is supported by the evidence on abortionlegalization and birthrates in Levine et al. [1996]. Their resultsfor the effect of legalization on birthrates are depicted in Figure II.This figure graphs the raw difference in birthrates for all womenof childbearing age between repeal and nonrepeal states over time(normalized so that the difference in 1970 is set equal to zero).Following legalization of abortion in the repeal states in 1970,birthrates in these states fell precipitously relative to birthratesin other states. There is then a corresponding fall in birthrates inthe nonrepeal states after 1973, so that by 1976 relative birth-

7. By 1976 the nonrepeal states continued to have lower abortion rates and alower percentage of women living near an abortion provider as compared withrepeal states. See Levine et al. [1996], Table 4.

FIGURE IIPercentage Difference in Birthrates between Repeal States and Nonrepeal States

Source. Levine et al. [1996], Figure 3. (Percentage Differences Are Normalizedto Equal Zero in 1970.)



rates were once again equalized. However, the bounceback is slow,only reducing the gap somewhat by 1974–1975. Levine et al.present regression results that support the narrative above:relative birthrates fell precipitously in the repeal states during1971–1973, recovered to some extent by 1974–1975, and fullyrecovered by 1976–1980. Overall, abortion legalization appears tobe correlated with roughly a 6 percent decline in relative birth-rates, which occurred immediately in the repeal states and moregradually in the nonrepeal states.8

A third shortcoming of this framework is that it assumes thatchanges in birth patterns brought about by abortion legalizationdo not have spillover effects onto those who would have been bornanyway. However, all children born around the time of abortionlegalization may directly benefit from this policy change. Inparticular, abortion legalization may reduce family size, and thismay lead to improvements in living circumstances for all childrenin the family through either a mechanical reduction in povertystatus or a quantity/quality trade-off as in Becker [1981].9 Thesefamily effects may affect all cohorts, even those born beforelegalization. To the extent that smaller families from abortionlegalization improve the living situation of children born prior tolegalization, we will tend to understate the overall effect ofabortion legalization on child outcomes.

On the other hand, our empirical framework will tend toisolate the effect of selection on child outcomes from family sizeeffects. Selection effects should appear discontinuously at the timeof legalization, while family size effects will appear more gradu-ally and tend to be differenced out in our framework. Of course, tothe extent that abortion legalization has larger effects on familysize for cohorts born after legalization as compared with cohorts

8. However, note that the effect of abortion legalization on relative birthratesunderstates the total effect of abortion on birthrates, since birthrates may havefallen in nonrepeal states as many women traveled to repeal states to obtainabortions. Levine et al. [1996] estimate that the total effect on birthrates was 8percent, based on a comparison of repeal states and states that were more than 750miles from repeal states.

9. Alternatively, falling cohort sizes may reduce congestion costs in somepublic resources like education: if teachers unions or other rigidities make itdifficult to adjust the number of teachers as cohort size falls, then there will befewer students per teacher and potentially improved student outcomes as a result.Indeed, changes in cohort size have been used in two recent papers [Hoxby 1997;Angrist and Lavy 1997] to identify the effect of class size on student outcomes.However, it is difficult to construct congestion-type stories for the outcomes that weexamine, household characteristics or birth outcomes; for welfare receipt, suchstories would presumably bias against our findings if states maintain their welfarebudgets in the face of a declining cohort.



born before legalization, we will tend to overstate the effects ofselection alone on child outcomes. In other words, some of theimprovements in child outcomes following abortion legalizationmay be due to legalization’s impact on family size rather than dueto differences between the marginal and average child (selection).

III. DATA AND REGRESSION FRAMEWORK

Data

Our primary data for this exercise are the 5 percent PublicUse sample of the 1980 Census.10 These data have two importantadvantages for our purposes. First, they include information onstate of birth for each child. State of birth, rather than currentstate of residence, is necessary for correctly determining howabortion laws at the time of birth affected selection into the cohort.Using state of residence in 1980 would potentially bias ourfindings if there is selective migration; for example, if thosechildren born into poor living circumstances because abortion isnot available are more likely to move, using state of residencewould understate the impact of making abortion available. There-fore, all of our analyses define cohort according to the child’s stateand year of birth.

Second, the census samples are the largest available foranalysis of living circumstances. This is important because, evenwith the fairly large change in birthrates documented by Levine etal. [1996], changes in average living circumstances of a birthcohort will only change quite modestly.11 For example, considerthe effects of abortion legalization if there is positive selection.Suppose that the baseline poverty rate in a birth cohort is 20percent, and that the marginal births that do not occur becauseabortion is available would have been 50 percent more likely tolive in poverty than the average birth in a cohort. This implies a

10. Ideally, we could use the 1990 Census to consider the effects of abortionaccess for later outcomes (i.e., schooling completion, fertility decisions, labor forcebehavior) of these cohorts. Unfortunately, our attempt to use these data was notfruitful. The confounding of aging and time effects, described below, in those datawere much more serious than in 1980, perhaps because the ages of the relevantcohorts in 1990 (roughly ages 13–20) are ages of extensive transition in livingcircumstances, schooling, and work. As a result, parametric trends were insuffi-cient to capture trends in the relative patterns of behavior across states.

11. In fact, the selection effect we are interested in is considerably smallerthan the dramatic shifts in child’s living circumstances, such as the share ofchildren living in single-parent households, taking place over this period. Themethodology we employ, described below, is designed to abstract from the generalsocial changes taking place and to focus on the effect of abortion legalization itself.



fall in the share of children living in poverty of about a percentagepoint from even a 10 percent drop in the birthrate, a quite smallchange on average despite this sizable positive selection effect onthe margin. Thus, very large sample sizes are required to identifyeven sizable selection effects.

The major cost to using the census for our analysis, asopposed to some source of annual data, is that we cannotseparately identify aging effects and time effects within a givencohort; children born later will also be younger in the 1980 census.The importance of this problem is illustrated by considering asimple comparison of the poverty rates of children born innonrepeal states in 1972 and 1976, using the 1980 census data. Ifthere is a positive selection into abortion, then the averagepoverty rates of those born in the nonrepeal states should declinebetween these two years. But at the same time, those born in 1972and 1976 are of different ages in 1980 (eight and four, respec-tively). Suppose further that mothers of children who are lessthan six do not work, but once children enter school they go towork. Then we would automatically see a countervailing increasein poverty rates over time in the nonrepeal states, simply becausethe children born later are less likely to have a mother in the laborforce. Indeed, on average, poverty rates fall with child’s age in the1980 census sample, so that they rise with birth year in this crosssection. This increase could mask true positive selection effects.Thus, by confounding aging and time effects, we potentiallyintroduce a spurious trend into our analysis.

Of course, this is not necessarily a problem for our analysis,since we are comparing the relative change in poverty rates (orother outcomes) in the repeal and nonrepeal states. But it mayintroduce problems if there are reasons to believe that child ageeffects have different impacts in different states. Indeed, visualinspection of the data suggests that there are underlying trends inthe state differentials, with a steady relative rise in adverse livingcircumstances in the repeal states for cohorts born between 1965and 1980. Thus, we include state-specific quadratic trends in ourregression framework that is described in more detail below.12

These controls should capture differences across states, for ex-ample, in the work patterns of mothers as their children age. Ourestimates of interest are identified by the deviation of average

12. The sensitivity of our findings to alternative specifications of trends isreported below.



living circumstances around these state-specific trends whenabortion is legalized.

Our sample consists of all noninstitutionalized children in the1980 census born between 1965 and 1979 (all children up to andincluding age 15 in 1980), which is roughly 2.4 million observa-tions.13 We focus on three measures of living circumstances: livingin poverty; living in a single-parent household; and living in ahousehold receiving welfare. To construct the first measure, wesimply compare total household income with the poverty line forthat size household. The second measure is a dummy variablethat is equal to one if the child has an unmarried mother or is thechild of a male head of household/subfamily with no spouse/partner present, and is zero if there is a second parent.14 The finalmeasure is a dummy variable for whether the child’s householdreports receiving any public assistance income.15

While we have 2.4 million observations in the Census, ourindependent variables of interest vary only at the state and yearlevel. Therefore, we aggregate these census data into state ofbirth/year of birth cells, and perform all of the analysis at the celllevel, weighting the regressions by the cell counts. This aggrega-tion leaves us with 750 observations from the 50 states and 15years of birth cohorts (1965–1979).16

In addition to the census data, we use data on birthrates andbirth outcomes, available by state of birth and year of birth fromVital Statistics of the United States. Average birthrates arecalculated for all women between the ages of 15 and 44. For eachstate-of-birth/year-of-birth cohort we focus on two additionalmeasures of adverse living circumstances using these data: the

13. Children born in 1980 are excluded because the income-based measuresused as dependent variables in some specifications refer to 1979. We do includechildren living in group quarters, such as halfway houses.

14. A key issue in constructing this measure is assigning children who are notclearly identified as a child of the household head or of a subfamily head. If otherrelatives of the head were present, we were able to assign some children to thosepersons; i.e. nieces of the head could be assigned if the sister of the head wascoresiding and reported having had children. If there was a coresiding partner ofthe head, children of the head were assigned to that partner as a second parent (ifshe reports having had children). Finally, if there was a roommate, boarder, oremployee in the household who reported having had children, then unrelatedchildren in the household were assigned to that person. Of the children living insingle-parent households, 10.4 percent were living with the father, and theremainder with the mother.

15. This may consist of either AFDC income or other forms of welfare income(i.e., state general assistance programs). For the purposes of our policy simulationsbelow, we assume that this is only AFDC income.

16. We do not include the District of Columbia because some observationscontain missing values for the control variables included in the analysis.



infant mortality rate, or the proportion of children born who die inthe first year of life; and the proportion of births that were lowbirth weight (under 2500 grams). Both measures are standardmeasures of adverse birth outcomes that have been shown byothers (using methods quite different from ours) to be negativelyrelated to abortion access. Furthermore, being born low birthweight has been shown to be correlated with subsequent adversechild outcomes such as cerebral palsy of significant degree, majorseizure disorders, blindness, deafness, and learning disorders[McCormick et al. 1992; U. S. OTA 1987; Chaikind and Corman1990]. While our primary focus is on how abortion affects livingcircumstances, it is obviously also of interest to assess the healthat birth of the marginal child.

Finally, we control for economic and demographic conditionsin the state and year of birth which may effect selection into thebirth cohort through the economic and social environment inwhich the birth decision was made. Per capita income, the crimerate, and the percent of the population that are white are obtainedfrom the Statistical Abstract. The insured unemployment rate isobtained from the United States Department of Labor, Employ-ment Training Administration [1983].

Regression Framework

Our discussion thus far suggests the following regressionframework for estimating the effect of abortion legalization onaverage living circumstances:

(1) OUTCOMEst 5 b1REPEAL*sD7173 1 b2REPEAL*sD7475

1 b3REPEAL*sD7679 1 b4ds 1 b5tt

1 b6d*sTREND 1 b7d*sTRENDSQ 1 b8Xst 1 est,

where OUTCOMEst is one of the measures of living circumstancesdescribed above for the cohort of children born in state s in year t;REPEALs is a dummy for a cohort born in a repeal state; D7173,D7475, and D7680 are dummies for the eras 1971–1973, 1974–1975, and 1976–1980, respectively; ds is a set of state dummies; tt

is a set of year dummies; TREND and TRENDSQ are linear andsquared time trends; and Xst are state-specific time-varyingcontrol variables.17 This fixed-effects specification provides ge-

17. Abortion legalization in these states may have been endogenous tochanges in birthrates within these states, but we believe it is unlikely to bias ourresults. Our models are identified from deviations from within-state (nonlinear)



neric controls for the multitude of otherwise unobservable differ-ences that exist across regions or take place over time.

Within this regression framework, the impact of abortionlegalization in the repeal states (the change from segment A tosegment B in Figure I) is captured by coefficient b1; for example, ifthere is positive selection, we will see a coefficient b1 , 0 (sincethese are adverse measures). The impact of abortion legalizationin the nonrepeal states (segment B versus C in Figure I) iscaptured by b3–b1; again, if there is positive selection, we will seeb3 . b1. In addition, it is independently of interest to assesswhether there is a full bounceback (b3 5 0).

In addition, we therefore pursue two additional tests, whichplace some more structure on the model but allow us more powerin testing for the effects of legalization. First, we impose therestriction that the repeal*76–79 interaction (b3) is zero (which isnever rejected in our results below); that is, that there is fullbounceback. Imposing this restriction increases the precision withwhich the repeal*71–73 interaction (b1) is estimated. An evenweaker test is simply to ask whether there is any evidence of ashift in the relative time/age pattern of these variables, condi-tional on including trends; that is, to test for the presence of anychange and bounceback, rather than testing individually for each.We do so by testing whether the coefficients on the repealinteractions are jointly zero, as would be true if there were nosignificant breaks in the relative time/age trend.

The Marginal Child

Estimates from the reduced-form model expressed in equa-tion (1) indicate the change in children’s average living circum-stances brought about by abortion legalization. A structural modelcan be used to identify what the living circumstances would havebeen for the marginal child that was aborted following legaliza-tion. The derivation of our approach is identical to that used toexpress the relationship between average cost curves and mar-

trends, so the precise timing of abortion legalization is critically important.Anecdotal evidence provided by Garrow [1994] indicates that legalization in NewYork, for instance, came as a complete surprise and even came within one vote ofbeing reversed before Roe v. Wade. The Supreme Court’s 1973 ruling in Roe was a5-4 decision. Moreover, this 1973 ruling led to a reversal of treatment and controlgroups in our quasi-experimental framework and makes the form of endogeneityrequired to bias our results very complicated. Both the initial effect of legalizationmainly in New York and California and the later effect in most of the remainder ofthe country had to coincide precisely with the timing of changes in preferencestoward abortion.



ginal cost curves (cf. Berndt [1991]). Let Ost/Bst represent theaverage outcome, O, of the B births born in state, s and year t.Taking the partial derivative of Ost/Bst with respect to the naturallog of the size of the birth cohort (ln Bst), implies that (suppressingsubscripts for convenience) (O/B)/(ln B) 5 O/B 2 O/B. In otherwords, the change in the average outcome of a birth cohort is equalto the difference in outcomes between the marginal birth and theaverage birth.

This relationship can be estimated in the following regressionframework:

(2) OUTCOMEst ; Ost/Bst 5 a1 ln (BIRTHRATEst)

1 a2ds 1 a3tt 1 a4d*sTREND

1 a5d*sTRENDSQ 1 b8Xst 1 est,

where BIRTHRATEst is the birthrate to women of childbearingage (i.e., BIRTHRATEst 5 Bst/(number of women of childbearingage in state s and year t)). Taking the derivative of equation (2)with respect to the log size of the birth cohort (ln Bst) implies thata1 is an estimate of the gap between the marginal outcome and theaverage outcome in the cohort.

Alternatively, if we specify the relationship between averageoutcomes and the birthrate as

(28) ln (OUTCOMEst) ; ln (Ost/Bst)5 a81 ln (BIRTHRATEst)

1 a82ds 1 a83tt 1 a84d*s TREND

1 a85d*s TRENDSQ 1 b8Xst 1 est,

then similar logic implies that a81 5 (O/B 2 O/B)/(O/B). In otherwords, if the dependent variable is in logs, the coefficient a1

becomes an estimate of the gap between the marginal outcomeand the average outcome stated in percentage terms.

Estimates of equation (2) or (28) by ordinary least squares(OLS) will misstate the amount of selection associated withabortion legalization, because much of the variation in birthratesis not due to changes in abortion access. For example, if transitoryeconomic conditions influence the timing of births (but noteventual family size), then much of the year-to-year variation inbirthrates may be unrelated to child outcomes. Similarly, ifpermanent improvements in the expected living circumstances offamilies result in higher birthrates, then there would tend to be apositive correlation between year-to-year variation in birthrates



and child well-being. Therefore, OLS estimates will misstate thedifferences between the average child and the marginal child notborn due to abortion access, and may be biased toward finding nodifference or toward finding that the marginal child would havebeen better off than the average child.

In order to isolate the selection effects of abortion legaliza-tion, we therefore estimate these equations by two-stage leastsquares (TSLS), using the variation in abortion legalizationacross states and years to instrument for the birthrate. Thefirst-stage equation is

(3) ln (BIRTHRATEst) 5 b1REPEAL*sD7173 1 b2REPEAL*sD7475

1 b3REPEAL*sD7679

1 b4ds 1 b5tt 1 b6d*sTREND

1 b7d*sTRENDSQ 1 b8Xst 1 est.

Thus, equations (1) and (3) are reduced-form equations relatingabortion legalization to average child outcomes and to birthrates.Equation (2) or (28), estimated by TSLS, is the structural equationfrom which we estimate the difference between the average childoutcome and the outcome of the marginal child whose birth isaffected by abortion legalization.

IV. RESULTS

Impact of Abortion Legalization on Average Child Outcomes

Regression results for the reduced-form equations (1) and (3)are in Table I. Each column of the table has test results andcoefficients of interest from a separate regression. For eachregression we report the coefficients for the repeal interactions (b1

through b3 in equation (1)), the p-value from a test of b1 5 b3 (i.e.,comparing segment B versus segment C in Figure I), and thep-value from a test of joint significance of the repeal interactions(the weak test described above).

The first two columns report estimates of the first-stageequation (3), in which the dependent variable is the log birthrate.These columns replicate the results of Levine et al. [1996], and thecoefficients suggest that abortion legalization reduced the birth-rate by about 6 percent. In particular, birthrates fell by about 6percent in repeal states relative to nonrepeal states in 1971–1973(b1 5 20.056), but then birthrates in nonrepeal states fell relative



TAB

LE

IO

LS

ES

TIM

AT

ES

OF

RE

DU

CE

D-F

OR

ME

QU

AT

ION

SF

OR

BIR

TH

RA

TE

AN

DB

IRT

HO

UT

CO

ME

S

(ST

AN

DA

RD

ER

RO

RS

INP

AR

EN

TH

ES

ES)

Dep

ende

nt

vari

able

:

ln(b

irth

rate

)

Per

cen

tli

vin

gw

ith

sin

gle

pare

nt

in19

80(m

ean

518

.6%

)

Per

cen

tli

vin

gin

pove

rty

in19

80(m

ean

518

.7%

)

Per

cen

tw

ith

wel

fare

rece

ipt

in19

80(m

ean

510

.6%

)

Per

cen

tw

ho

die

infi

rst

year

(mea

n5

1.9%

)

Per

cen

tw

ith

low

birt

hw

eigh

t(m

ean

57.

7%)

(1)

(2)

(3)

(4)

(5)

(6)

(7)

(8)

(9)

(10)

(11)

(12)

Inde

pen

den

tva

riab

le:

repe

alp

1971

–197

32

0.05

62

0.05

92

0.72

92

0.86

92

0.30

22

0.54

12

0.41

22

0.36

42

0.04

22

0.05

12

0.05

82

0.09

8(0

.006

)(0

.005

)(0

.303

)(0

.225

)(0

.295

)(0

.219

)(0

.233

)(0

.173

)(0

.027

)(0

.020

)(0

.070

)(0

.052

)re

peal

p19

74–1

975

20.

015

20.

021

20.

514

20.

776

0.22

52

0.22

12

0.57

62

0.48

72

0.03

02

0.04

82

0.11

22

0.18

7(0

.009

)(0

.005

)(0

.457

)(0

.255

)(0

.445

)(0

.248

)(0

.351

)(0

.196

)(0

.041

)(0

.023

)(0

.106

)(0

.059

)re

peal

p19

76–1

979

0.01

00.

468

0.79

92

0.16

00.

033

0.13

5(0

.014

)(0

.679

)(0

.660

)(0

.521

)(0

.062

)(0

.160

)P

-val

ue

for

test

ofeq

ual

ity

ofco

effi

-ci

ents

onre

peal

p

1971

–197

3an

dre

peal

p19

76–1

979

0.00

00.

023

0.03

20.

533

0.12

10.

120

P-v

alu

efo

rte

stof

join

tsi

gnifi

can

ceof

repo

rted

coef

fici

ents

0.00

00.

000

0.00

10.

000

0.05

30.

045

0.06

40.

028

0.05

40.

025

0.01

40.

007

Coe

ffic

ien

tsar

eth

ose

onre

peal

inte

ract

ion

sfr

omre

gres

sion

spec

ifica

tion

ssu

chas

equ

atio

n(1

),in

clu

din

gth

efo

llow

ing

oth

erre

gres

sors

::in

sure

du

nem

ploy

men

tra

te,p

erca

pita

inco

me,

crim

era

te,p

erce

nt

ofth

epo

pula

tion

that

isn

onw

hit

e,a

full

set

ofst

ate

and

year

dum

mie

s,an

dst

ate-

spec

ific

quad

rati

ctr

ends

.Odd

-nu

mbe

red

colu

mn

sin

each

pan

elsh

owre

sult

sfr

omeq

uat

ion

(1);

even

-nu

mbe

red

colu

mn

ssh

owre

sult

sfr

omre

gres

sion

mod

els

rest

rict

ing

the

coef

fici

ent

onre

peal

p19

76–1

979

(b3)

tobe

zero

.In

all

spec

ifica

tion

s,75

0ob

serv

atio

ns

are

avai

labl

ere

pres

enti

ng

the

50st

ates

and

15ye

ars

ofbi

rth

coh

orts

(196

5–19

79).



to repeal states following legalization in all states in 1973(b1–b3 5 20.066). Thus, we estimate significant effects of abortionon birthrates of similar magnitude in both the repeal and nonre-peal states. As a result, we cannot reject the hypothesis that therewas a full bounceback in relative birthrates (b3 5 0). The secondcolumn reports the results when b3 is constrained to be zero, andthe results are quite similar. In both specifications the repealinteractions are highly jointly significant.

The remaining columns of Table I estimate equation (1) foralternative outcome measures (in each case, we multiply thecoefficients of interest by 100, so that they can be interpreted aspercentage point effects). For the percentage of a cohort living insingle-parent households, the pattern of coefficients indicatespositive selection; that is, the legalization of abortion lowers theshare of children living in single-parent households. Legalizationin the repeal states over the 1971–1973 period is associated with areduction in the percentage of children living in single-parentfamilies of 0.73 percentage points (supporting positive selectionfor segment B versus segment A). This effect was reduced to someextent over the 1974–1975 period, and had actually reversed by1976–1979, although this estimate is not significantly differentfrom zero.18 More importantly, the coefficients on the 1971–1973and 1976–1979 interactions are significantly different from eachother (confirming positive selection in the nonrepeal states,segment C versus segment B). Whether or not we impose the fullbounceback (b3 5 0), the repeal interactions are very jointlysignificant.

For the percentage of the cohort in poverty, the directions ofthe coefficients support positive selection, but the estimates areimprecise. There is a negative coefficient on the 1971–1973interaction but it is insignificant, and there is an insignificantpositive coefficient on the 1976–1979 interaction, although it isfairly large. Despite the imprecision of these estimates, however,we can reject that the 1971–1973 and 1976–1979 interactions areequal at the .032 level, which supports positive selection. If we

18. In this and other specifications reported in this table, the repeal effect in1974–1975 is roughly of a magnitude similar to that in 1971–1973 even though wewould expect it to be smaller. In fact, the repeal effect is never significantlydifferent in these transitional years from 1971–1973. However, the repeal effect in1974–1975 is also not significantly different from that in 1976–1979 in any of thesemodels. These findings suggest that tests for the partial convergence in outcomesbetween repeal and nonrepeal states through the 1974–1975 period are relativelyweak.



impose b3 5 0, then the 1971–1973 interaction becomes negativeand significant, suggesting that abortion legalization reduced thepercentage of the cohort living in poverty by 0.54 percentagepoints. And, once again, the repeal interactions are jointlysignificant.

For welfare receipt, the coefficients are also supportive ofpositive selection, with a negative and significant (at the 10percent level) coefficient on the 1971–1973 interaction, and a zerocoefficient on the 1976–1979 interaction. The results indicate thatabortion legalization lowered welfare receipt rates by 0.41 percent-age points on average. However, the relative imprecision heremeans that we are unable to reject the equality of the 1971–1973and 1976–1979 interactions. Unexpectedly, the 1974–1975 interac-tion is actually larger than the 1971–1973 interaction althoughthese coefficients are not very precisely estimated. And we canagain reject the joint insignificance of the repeal interactions.

The final columns look at the impact of abortion legalizationon infant mortality and on the percentage of the birth cohort thatwas low birth weight. As with the measures of living circum-stances in 1980 from the census data, these birth outcomemeasures suggest positive selection: a negative coefficient on the1971–1973 interaction that reverses by 1976–1979, although noneare statistically significant. When we restrict the 1976–1979interaction coefficient to equal zero, however, we observe anegative and significant reduction in both infant mortality and inlow birth weight in repeal states in the 1971–1973 period ofroughly 0.05 percent and 0.1 percent, respectively.

Overall, the pattern of estimates is very suggestive of positiveselection. The 1971–1973 interaction (b1) is negative in everycase. When we impose the restriction that the repeal*76–79interaction is zero (which is not rejected in any of our models), itbecomes significant in every case (although only at the 10 percentlevel for low birth weight). Similarly, in each regression we findthat this difference is reversed after legalization of abortion in thenonrepeal states in 1973 (i.e., b3 . b1), although this difference isonly significant for living in a single-parent or poverty household.And, for all outcomes, the repeal interactions are found to bejointly significant at least at the 10 percent level. Thus, abortionlegalization appears to be associated with an improvement in theaverage living circumstances and birth outcomes among a birthcohort.

Our results thus far indicate that abortion legalization leads



to significant reductions in both the share of children living insingle-parent families and the share living in poverty. Single-parent families are much poorer than other families, however. Asa result, our finding that fewer children are living in poorhouseholds may arise mechanically from the reduction in the oddsof residing in a single-parent household, rather than from in-creases in the average income of families, conditional on familystructure. To examine this question, we compute state/yearspecific poverty rates separately for the single-parent and two-parent family samples, and use both as dependent variables. Oncestratified by family structure, we find no effect of legalization oneither the share of single-parent families in poverty or the share ofother families in poverty; we fail every single test described above(although standard errors are considerably larger as well, particu-larly for the single-parent sample). Thus, it appears that ourfindings for changes in poverty when abortion becomes availableis driven solely by changes in the distribution of family structure.19

Outcomes for the Marginal Child

Although our findings for these average measures of disadvan-tage in a cohort are fairly consistent in their signs and signifi-cance, it is of interest to interpret these magnitudes in terms ofthe size of the selection effect. That is, we can ask the followingquestion: what are the characteristics of the marginal childrenwho were not born due to abortion legalization? Estimates of thedifference between the marginal and the average birth outcomeare presented in Table II.

Each column in Table II reports OLS and TSLS estimates ofthe coefficient on the log birthrate from a regression of our averageoutcome measures on the log birthrate (equation (2) or (28)). TheTSLS estimates instrument for the birthrate with the repealinteractions. Thus, column (1) of Table I reports the first-stageequation for the TSLS estimates.20 As discussed earlier, thesecoefficients estimate the gap in child outcomes between themarginal and the average child. For specifications in which the

19. Previous literature suggests that we should find a reduction in theaverage income of children living in single-parent families. Cooksley [1990] andLundberg and Plotnick [1995] find evidence of negative selection on abortiondecisions among unmarried teens in data from the NLSY. Our contradictoryfinding of no selection conditional on family structure suggests that these earlierfindings may be due to the reporting bias in the NLSY data on abortions.

20. The first-stage F statistics for the excluded instruments in this table arevery high; in every case the F is over 60.



TA

BL

EII

ES

TIM

AT

ES

OF

RE

LA

TIO

NS

HIP

BE

TW

EE

NB

IRT

HR

AT

ES

AN

DC

HIL

DO

UT

CO

ME

SC

OE

FF

ICIE

NT

SA

RE

MU

LT

IPL

IED

BY

100

(ST

AN

DA

RD

ER

RO

RS

INP

AR

EN

TH

ES

ES)

Dep

ende

nt

vari

able

:P

erce

nt

livi

ng

wit

hsi

ngl

epa

ren

tin

1980

(mea

n5

18.6

%)

Per

cen

tli

vin

gin

pove

rty

in19

80(m

ean

518

.8%

)

Per

cen

tw

ith

wel

fare

rece

ipt

in19

80(m

ean

510

.6%

)

Per

cen

tw

ho

die

infi

rst

year

(mea

n5

1.9%

)

Per

cent

wit

hlo

wbi

rth

wei

ght

(mea

n5

7.6%

)

Isde

pen

den

tva

riab

lelo

gged

?n

oye

sn

oye

sn

oye

sn

oye

sn

oye

sC

oeff

icie

nt

esti

mat

esfo

rln

(bir

thra

te):

(1)

(2)

(3)

(4)

(5)

(6)

(7)

(8)

(9)

(10)

OL

S4.

830.

271

2.38

0.09

70.

769

0.09

60.

192

0.10

50.

544

0.07

4(1

.72)

(0.1

04)

(1.6

6)(0

.095

)(1

.31)

(0.1

45)

(0.1

54)

(0.0

86)

(0.4

00)

(0.0

53)

TS

LS

usi

ng

inst

rum

ents

:re

peal

p19

71–1

973

13.1

60.

603

9.28

0.47

94.

830.

439

0.77

00.

396

1.15

0.13

6re

peal

p19

74–1

975

(3.8

5)(0

.231

)(3

.71)

(0.2

12)

(2.9

1)(0

.320

)(0

.340

)(0

.189

)(0

.874

)(0

.115

)re

peal

p19

76–1

979

P-v

alu

efo

rH

ausm

ante

stof

equ

ival

ence

ofO

LS

and

TS

LS

esti

mat

es0.

013

0.10

40.

034

0.04

00.

114

0.22

70.

053

0.08

00.

434

0.53

9P

-val

ue

for

Bas

man

nte

stof

over

iden

tify

ing

rest

rict

ion

s0.

105

0.16

50.

557

0.69

90.

112

0.07

20.

313

0.22

90.

012

0.01

0O

LS

esti

mat

es,e

xclu

din

g19

71–1

975

4.25

(2.5

9)0.

276

(0.1

62)

1.05

(2.3

7)0.

058

(0.1

38)

20.

228

(2.0

2)0.

069

(0.2

32)

20.

105

(0.2

28)

20.

001

(0.0

13)

20.

197

(0.5

94)

20.

019

(0.0

79)

Coe

ffic

ien

tsar

eth

ose

from

esti

mat

ion

ofeq

uat

ion

s(2

)an

d(2

8),b

yO

LS

(in

firs

tro

w),

TS

LS

(in

seco

nd

row

),an

dO

LS

excl

udi

ng

the

year

s19

71–1

975

(in

fin

alro

w).

Odd

-nu

mbe

red

colu

mn

sin

each

pan

elsh

owre

sult

sfr

omeq

uat

ion

(2),

and

even

-nu

mbe

red

colu

mn

ssh

owre

sult

sfr

omeq

uat

ion

(28)

.In

each

mod

el,o

ther

regr

esso

rsin

clu

deth

ein

sure

du

nem

ploy

men

tra

te,

per

capi

tain

com

e,cr

ime

rate

,pe

rcen

tof

the

popu

lati

onth

atis

non

wh

ite,

afu

llse

tof

stat

ean

dye

ardu

mm

ies,

and

stat

e-sp

ecifi

cqu

adra

tic

tren

ds.

Inal

lsp

ecifi

cati

ons,

750

obse

rvat

ion

sar

eav

aila

ble

repr

esen

tin

gth

e50

stat

esan

d15

year

sof

birt

hco

hor

ts(1

965–

1979

).



dependent variable is logged, the coefficient gives this gap as apercentage of the average outcome. In addition to the OLS andTSLS estimates, we report the p-value of a test that the OLS andTSLS estimates are equivalent, and the p-value from a test of theoveridentifying restrictions in the TSLS models.

The first two columns considers the likelihood that themarginal child would have lived in a single-parent household in1980. The OLS estimate in the first column indicates that themarginal child would have been 5 percentage points more likely tolive in such a household, as compared with the average child intheir cohort. Alternatively, column (2) estimates that the marginalbirth was approximately 27 percent more likely to live in asingle-parent household. As discussed earlier, however, one wouldexpect OLS estimates to understate any positive selection effectsof legalization because much of the variation in birthrates is notthe result of changes in abortion access.

Indeed, when we instrument in the second row, our estimatesrise appreciably. The TSLS estimates indicate that the marginalbirth being affected by abortion legalization would have been 13.2percentage points more likely to have been living in a single-parent household in 1980, as compared with the average child intheir cohort. Column (2) shows that the marginal birth was 60percent more likely to live in a single-parent household. Bothestimates are fairly precisely estimated. Finally, the tests of theoveridentifying restrictions have p-values of 0.105 and 0.165,providing no evidence of misspecification in the TSLS models.

The remaining columns provide similar estimates for otheroutcome measures. The TSLS estimates imply that, comparedwith the average outcome in their birth cohort, the marginal birthwould have had higher poverty rates in 1980 (by 9.3 percentagepoints or 48 percent), and been more likely to have lived in afamily receiving welfare in 1980 (by 4.8 percentage points or 44percent). Similarly, the marginal birth would have had higherinfant mortality rates (by 0.77 percentage points or 40 percent)and higher incidence of low birth weight (by 1.15 percentagepoints or 14 percent). With the exception of low birth weight, theseestimates are statistically significant at or near the 5 percentlevel, and pass the test of overidentifying restrictions.

All of the TSLS estimates are larger than the OLS estimates.As discussed earlier, this would be expected if there were strongerselection arising from changes in abortion access, than arisingfrom other factors that influence the birthrate. In fact, the gap



between OLS and TSLS estimates may understate the differencein selection due to abortion versus other factors, since a largeshare of the year-to-year variation in birthrates that identifies ourOLS estimate comes from changes in abortion access. We addressthis in the final row of the table, by reestimating our OLSregression excluding the years 1971–1975. By considering onlythose years during which there was no difference across states inthe legality of abortion, we provide an estimate of the effect ofyear-to-year variation in birthrates for reasons other than abor-tion legality. Indeed, our estimates here are generally smaller, andsome point estimates even become negative.

Alternative Specifications

In all of the reported results, we have allowed quadraticstate-specific trends to capture potentially nonlinear changes inchildren’s living circumstances as they age that differ acrossstates. Although the discrete nature of the legal status of abortionshould still enable us to estimate its impact in a model with thesetrends, including them does eliminate a substantial share of thevariation in the data. To examine the sensitivity of our findings,we reestimated these models allowing for other specifications oftrends, including no trends, linear trends, and a linear splinekinked in 1974 (having a school-age child makes it easier formothers to work and six-year-old children in 1980 were born inthat year).

Results obtained for all models including the linear splinewere quite similar to those using a quadratic trend reported here.We even obtained similar estimates in models of living in asingle-parent family, infant mortality, and low birth weight thatincluded no trend and a linear trend, but models of welfare receiptand living in poverty were very sensitive to these two alternatives.For instance, results from Table II indicate that the marginalchild is 5 percent more likely to live in a household receivingwelfare in 1980, (column (5)), the analogous models omitting anytrend and with a linear trend suggests that these children areactually 7 percent and 4 percent less likely to live in a welfarehousehold, respectively. This sensitivity may not be surprising,however, because these are precisely the two outcomes for whichhaving a child in school rather than at home should have thegreatest impact. Based on our a priori beliefs regarding thenonlinearity in children’s living circumstances by age, we still



favor those models that include the quadratic trends (or linearsplines).

Another way in which our results may be sensitive toalternative specifications is that the distance between a woman’sstate of residence and a repeal state may be important. Womenwho live close to a repeal state may still have some access toabortion through travel and differences in birth outcomes andchildren’s living circumstances may emerge between these womenand those residing farther from a repeal state. In fact, Levine et al.[1996] find that the decline in births brought about by abortionlegalization follows this pattern. The decline in New York, Califor-nia, and other early legalization states was roughly twice as greatwhen compared with the decline in far away states rather than inneighboring states. When we estimate reduced-form models ofchild outcomes (as in Table I) that allow the estimated effect todiffer by travel distance to a repeal state, we find no suchsignificant differences—although the standard errors on theestimates are sufficient that it is impossible to rule out fairly largedifferences. Regardless, the estimates of outcomes for the mar-ginal child (as in Table II) are very similar when we use a largerlist of instruments that include interactions between the affectedyears and distance between each state and the nearest repealstate (measured in the categories ,250, 250–750, and .750miles).

Differences by Race

The fact that living circumstances for black children are fardifferent from those for white children has been well documented,and these differences are apparent in our data as well. Forinstance, in our data nonwhite children are almost twice as likelyto die in the first year of life and are three times more likely to livein poverty compared with white children.

These differences in average living circumstances indicatethat abortion legalization could have had considerably differenteffects for blacks compared with whites. In fact, if black and whitewomen make similar abortion decisions under similar circum-stances, then these differences on average would lead us to expectblack women to abort more frequently. For any threshold level ofchildren’s outcomes, more black children are likely to fall belowthat level. Moreover, if those white and black children who areaborted would have had similar living circumstances, then thedifference between the marginal and average child will be greater



for whites than for blacks because the average living circum-stances of whites are higher.

Some empirical support for both of these propositions isreported in Table III. The first two columns of the table reportestimates of the effect of abortion legalization on birthratesseparately for whites and nonwhites. Consistent with the resultsin Levine et al. [1996], birthrates in those states legalizingabortion in advance of Roe v. Wade fell by about 5 percent forwhites and 12 percent for blacks. Following Roe v. Wade, thedifferences across states were eliminated for both whites andblacks.

The remainder of the table compares the estimated effect onchild living circumstances separately by race: estimates in the toppanel are analogous to those reported in Table I, and estimates inthe bottom panel are analogous to the TSLS estimates reported inTable II. In all cases, results for whites are similar to those for thepopulation as a whole because they represent the vast majority ofthe population. In comparing results across racial groups, findingstatistically significant differences is hampered by the relativeimprecision with which parameters are estimated. Nevertheless,the point estimates reported here are generally supportive of thesecond proposition. The TSLS estimates of the difference betweenthe marginal and average child are larger among whites thannonwhites for all of the outcomes except welfare receipt.21

Implications

The implication from these findings is that the marginalchildren who were not born due to abortion legalization wouldhave lived in more disadvantaged circumstances than the averagechild in their cohort. This indicates sizable positive selectionamong those pregnancies that were carried to term followinglegalization of abortion. In other words, this evidence stronglysuggests that abortion is used by women to avoid bearing childrenwho would grow up in adverse circumstances.

21. Our findings by race contradict those of Grossman and Jacobowitz [1981],who estimate a 0.059 percentage point decline in neonatal mortality for whites inabortion reform states after 1970, and a 0.177 percentage point decline for blacks.Our estimates for whites are very similar but for blacks we find no effect. Theirestimates are identified from between-state variation in abortion availability inthe early 1970s. However, the states that had legalized abortion in 1970 had lowerinfant mortality rates for blacks (but not for whites) even prior to 1970. This factmost likely explains the difference between our within-state estimates and theirbetween-state estimates and suggests that the between-state estimates arebiased, particularly for blacks.



TA

BL

EII

IE

ST

IMA

TE

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(196

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79).



As noted above, this is a purely positive exercise, and we donot have much evidence on the long-run implications of thischange in average living standards. One clear implication of ourfindings, however, is that there was an effect of abortion legaliza-tion on the budgets of federal and state governments, throughreduced welfare receipt. We can compute the budgetary savings in1980 (the year of our data) to the government through the reducedwelfare receipt of the average child after abortion legalization. Indoing so, we abstract from welfare savings due to the overall dropin cohort size; we are only estimating the differential savingsarising from the change in cohort mix through positive selection.

Our calculation proceeds as follows. First, we compute thenumber of children in each age cohort in 1980 who were born afterabortion legalization, counting all children born in 1971 or later inrepeal states and all children born in 1974 or later in nonrepealstates. We then compute the drop in the number of children borninto welfare households in 1980 as the product of the number ofchildren born after legalization and the estimated decline inwelfare receipt after legalization (0.364 percent from column (8) ofTable I). We estimate that in 1980, the lower average welfarereceipt rate, due to positive selection only, reduced the welfarecaseload by 73,500 families. In 1995 dollars the average welfarepayment per family of two (mother and child) in 1980 was $6500.22

This implies that the government saved $480 million in 1980because of abortion legalization. If all children in 1980 had beenborn at a time when abortion was legal, our estimates imply thatpositive selection would have reduced the welfare caseload in1980 by 173,500 families for a total savings of $1.1 billion in 1980.

V. CONCLUSIONS

The most important change in government fertility policyover the past 30 years was the legalization of abortion under theRoe v. Wade decision. As has been shown elsewhere, this changehad a dramatic effect on the size of birth cohorts. As we demon-strate in this paper, the change also had a significant effect on theliving circumstances of the cohorts who were born after legaliza-tion. Subsequent cohorts were less likely to be in single-parenthouseholds, and as a result less likely to live in poverty, and less

22. We use benefits for a family of two because the mechanism through whichabortion legalization reduced welfare receipt appears to be through reducing theinitial formation of single-female-headed families.



likely to receive welfare. In addition, these cohorts experiencedlower infant mortality. In particular, we find that for the marginalchild not born due to increased abortion access, the odds of livingin a single-parent family would have been roughly 60 percenthigher, the odds of living in poverty nearly 50 percent higher, theodds of welfare receipt 45 percent higher, and the odds of dying asan infant 40 percent higher.

Perhaps more importantly, these findings may also haveimplications for the lifelong prospects of the average child bornafter legalization. The children not born due to abortion availabil-ity would have grown up in adverse living circumstances thatother studies have shown may be detrimental to later prospects.23

Of course, this conclusion is complicated by the fact that wecannot necessarily apply the effects on the average child of livingin poverty (for example) to the effects on the marginal child whowould live in poverty if their pregnancy were not terminated.However, as these cohorts age, researchers will be able to directlyobserve outcomes such as educational attainment, income, andfamily structure. This is an important question that should be thefocus of future analysis.

MASSACHUSETTS INSTITUTE OF TECHNOLOGY AND THE NATIONAL BUREAU OF ECONOMIC

RESEARCH

WELLESLEY COLLEGE AND THE NATIONAL BUREAU OF ECONOMIC RESEARCH

DARTMOUTH COLLEGE AND THE NATIONAL BUREAU OF ECONOMIC RESEARCH

REFERENCES

Angrist, Joshua D., and Victor Lavy, ‘‘Using Maimonides’ Rule to Estimate theEffect of Class Size on Scholastic Achievement,’’ Quarterly Journal of Econom-ics, CXIV (May 1999), forthcoming.

Becker, Gary S, A Treatise on the Family (Cambridge, MA: Harvard UniversityPress, 1981).

Berndt, Ernst, The Practice of Econometrics: Classic and Contemporary (Reading,MA: Addison-Wesley, 1991).

Blank, Rebecca, Christine George, and Rebecca London, ‘‘State Abortion Rates:The Impact of Policies, Providers, Politics, Demographics, and EconomicEnvironment,’’ Journal of Health Economics, XV (1996), 513–553.

Chaikind, Stephen, and Hope Corman, ‘‘The Special Education Costs of Low BirthWeight,’’ NBER Working Paper No. 3461, October 1990.

Cooksley, Elizabeth C., ‘‘Factors in the Resolution of Adolescent PremaritalPregnancies,’’ Demography, XXVII (1990), 207–218.

Corman, Hope, and Michael Grossman, ‘‘Determinants of Neonatal MortalityRates in the U. S.: A Reduced-Form Model,’’ Journal of Health Economics, IV(1985), 213–236.

23. See Haveman and Wolfe [1995]. On the other hand, Mayer [1997] andothers have argued that the relationship between growing up in poverty andsubsequent outcomes is not causal.



Currie, Janet, Lucia Nixon, and Nancy Cole, ‘‘Restrictions on Medicaid Funding ofAbortion: Effects on Pregnancy Resolutions and Birth Weight,’’ Journal ofHuman Resources, XXXI (1996), 159–188.

Garrow, David J., Liberty and Sexuality: The Right to Privacy and the Making ofRoe v. Wade (New York, NY: Macmillan Publishing Company, 1994).

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Joyce, Theodore, ‘‘The Impact of Induced Abortion on Black and White BirthOutcomes in the United States,’’ Demography, XXIV (1987), 229–244., ‘‘The Social and Economic Correlates of Pregnancy Resolution amongAdolescents in New York City, by Race and Ethnicity: A MultivariateAnalysis,’’ American Journal of Public Health, LXXVIII (1988), 626–631.

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Lundberg, Shelly, and Robert D. Plotnick, ‘‘Adolescent Premarital Childbearing:Do Economic Incentives Matter,’’ Journal of Labor Economics, XIII (1995),177–200.

Mayer, Susan E. What Money Can’t Buy: Family Income and Children’s LifeChances (Cambridge, MA: Harvard University Press, 1997).

McCormick, Marie C., Jeanne Brooks-Gunn, Kathryn Workman-Daniels, JoAnnaTurner, and George J. Peckham, ‘‘The Health and Development Status ofVery-Low-Birth Weight Children at School Age,’’ Journal of the AmericanMedical Association, CCLXVII (1992), 2204–2208.

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