The Impact of Early Fertility Shocks on Women’s Fertility and Labor Market Outcomes

Abstract

This paper evaluates the effect of unplanned fertility shocks on women’s careers. I exploit the early repeal of abortion bans in five US states. This leads to variation in access to abortion across states and birth cohorts, which allows the estimation of the effect of accessing abortion at a certain age on women’s fertility. The evidence suggests that accessing abortion before the age of 21 delayed the age at which women gave birth to their first child by half a year on average. I also document an increase in completed fertility among Black women who received access to abortion early in their fertility cycle. The resulting variation in fertility realizations is then used to estimate the effect of fertility on women’s careers. I find that wages increase significantly as a result of the delay of an unplanned start of motherhood. This increase in wages translates into a 10% increase in labor earnings among Black women, and it is completely offset by the a decrease in labor supply for White women.

Appendices

Appendix

A Data

The data available for the purpose of this study are the 1960, 1970, 1980, 1990 and 2000 samples of the 5 percent Public Use Microdata Samples (IPUMS Bureau of the Census). In this section, I describe in detail the construction of the main outcome variables as well as the different sample restrictions imposed to estimate the effect of access to abortion throughout the fertility cycle. I first restrict the focus of study to women born in the US between 1930 and 1955. This restriction guarantees that at the time of early state level legalization of abortion in 1970, the age of women observed extend between 15 and 40, which is the assumed range of fertility cycle in this study. Further restrictions are imposed to estimate the effect on various fertility and labor market outcomes, which is detailed in what follows.

A.1 Fertility Outcomes

Identification of the effect of abortion access on fertility outcomes requires observation of these outcomes once they have been achieved. Observing outcomes earlier than achievement can lead to estimation bias. This is particularly true in the case of cross sectional data such as the one used in this paper. For instance, if in a sample year we observe the total number of children born to women prior to achieving their fertility cycle, estimation of the effect of abortion will likely be overstated for the younger birth cohorts, since at the time of observation total number of children born to older women is a better measurement of completed fertility as compared to younger women.

The first outcome considered is the age at which women enter motherhood. This variable is constructed by taking the difference of the age of the eldest child in the household and the age of the mother. There are two potential challenges constructing this variable. First, it requires observation of women after they had given birth to at least one child. Second, the survey reports the age of the eldest child still living in the household, and consequently the observation should be at a time where the first born child still live in the household. To satisfy these two restrictions, women in the sample should be at least 30 years old and not older than 40. I therefore restrict the sample to include women born between 1935 and 1941 and observed in 1970, women born between 1942 and 1948 and observed in 1980, and women born between 1949 and 1955 and observed in 1990. Moreover, the PUMS reports the total number of children ever born to the interviewed woman as well as the total number of children currently living in the household. I then further restrict the sample to households where total number of children living in the household is equal to total number of children the mother gave birth to. This was due to some women being older than 40 at observation and hence their eldest child might have left the household. This restriction potentially excludes women who had children very early in their life. This restriction reduces the sample by 22%. Moreover, the resulting attrition is homogeneous across the different birth cohorts in the sample. When comparing across states, the attrition resulting from sample selection is slightly higher in non-repeal states (23%) than repeal states (22%). It should also be noted that the eldest birth cohorts in this restriction (1935–1941) are observed prior to legal change. I am assuming that for this birth cohort, the birth of first child occurred prior to abortion legalization and hence the legal changes had no effect on this particular fertility realization. This assumption is reasonable given that the average age at birth of a child in the sample is 24.¹⁵

The second outcome of interest, completed fertility, is defined as the total number of children a woman gave birth to during her fertility cycle. An accurate measurement of completed fertility requires the observation of total number of children born to a woman after she has concluded her fertility phase, which is usually around the age of 45. The census reports total number of children women gave birth to by the time they were interviewed. Given that birth cohorts are restricted to women born between 1930 and 1955, the ideal measurement of completed fertility is the observed total number of children in the 2000 sample. Unfortunately this variable is not reported in that sample year, as such completed fertility is set to equal the total number of children a woman gave birth to observed in the 1990 sample. This potentially creates a measurement error for the completed fertility observation of the younger birth cohorts. Knowing that most women give birth to their children by the age of 42, this measurement error is most likely restricted to women in the sample born after 1948.

A.2 Labor Market Outcomes

The sample used in estimation of labor market outcomes is the same as the one used for estimating the effect of abortion access on age at first birth. There are two sets of labor outcomes I study in this paper: labor supply and labor earning outcomes. I use multiple labor supply variables in order to study the effect on labor supply at intensive and extensive margins. The first of these variables is labor force participation status, which is readily available in the data. Weekly hours worked are reported as a continuous variable in the data for the 1980 and 1990 sample. However, in the 1970 sample the hours worked are reported in intervals. Therefore, in constructing the continuous measure of hours worked, I used the reported values in the 1980 and 1990 samples and take the midpoint of the reported interval in the 1970 sample. Women who are not working are assigned a value of zero hours worked. Analysis of labor market outcomes is conducted using both the full sample and the subsample of working women.

The survey reports nominal values of yearly labor earnings. Since I’m stacking three years of surveys that span over 20 years, nominal wages in the later samples will be automatically larger due to inflation. To make wage earnings comparable across survey years, I deflate the earnings and express them in 2012 dollars. Moreover, as stated in the text, for the labor market outcome analysis I include year of observation fixed effects to control for differences in macroeconomic conditions across years. I construct a wage rate variable for working women by taking the ratio of yearly labor earnings and hours worked. This variable is likely to suffer from division bias as a result of measurement error in the hours worked variable, so analysis of results on this variable should be studied with care. The last labor market outcome variable I study is an occupation index variable reported in the IPUMS. The occupation index takes values between 0 and 100, with larger values indicating occupation with higher median earned income.

B Additional Tables and Figures

B.1 Estimates of Age Group Regressions

In this section, I include tables and figures reporting secondary results that are complementary to the analysis provided in the text. In the first part of this appendix, I include estimation results of Eq. (2) and the difference-in-differences estimates for the two main fertility outcomes. Estimation results concerning birth timing are reported in Tables 5 and 6, and the results for completed fertility are reported in Tables 7 and 8. Results on marriage outcomes of Black women are reported in second part of the appendix, estimates of Eq. (2) for marriage outcomes of black women are reported in Table 9, and difference-in-differences measures are reported in Table 10 and Fig. 6. For completeness I also estimate Eq. (1), which evaluates the impact of individual age-years of exposure to abortion. All the relevant estimates are reported in the third part of this appendix. The last part of the appendix reports placebo test results to rule out possible changes in fertility trends.

Table 5 Cross states differences in birth timing (age group)

Table 6 Difference-in-differences estimates of the effect of abortion access on birth timing

Table 7 Cross states differences in completed fertility (age group)

Table 8 Difference-in-differences estimates of the effect of abortion access on completed fertility

B.2 Impact on Black Women’s Marriage Outcomes

See Fig. 6 and Tables 9, 10.

Fig. 6

Effect of access to abortion on marriage outcomes for black women. The figure reports point estimates with 95% confidence intervals

Table 9 Cross states difference in black women’s marriage outcomes

Table 10 Difference-in-differences estimates of the effect of abortion access on black women’s marriage

B.3 Estimation Results by Year of Age

See Tables 11, 12, 13 and 14.

Table 11 Cross states differences in birth timing (age years)

Table 12 Difference-in-differences estimates of the effect of abortion access on birth timings

Table 13 Cross states differences in completed fertility (age years)

Table 14 Difference-in-differences estimates of the effect of abortion access on completed fertility

B.4 Placebo Test: Ruling Out Changes in Fertility Trends

One might worry that the observed effect on age of start of motherhood is due to a fertility trend change among younger birth cohorts that coincided with the legal changes. To rule out this possibility, I extend the specification of Eq. (2) to include women born between 1956 and 1958. The added cohorts were between the ages of 12 and 14 at the time of the state legal changes and hence are unlikely to be affected by the treatment. These birth cohorts experienced equal access to abortion across states, as they all obtained access to abortion at the start of their fertility cycle through federal legalization. Estimation results for the full sample and by race are reported in Fig. 7. The results show that exposure between the ages of 12 and 14 had no effect on age of start of motherhood. This result provides further evidence that the effect found above is indeed due to abortion access and not due to a trend change in fertility preferences.

Fig. 7

Effect of abortion access on age of motherhood. The figure reports point estimates with 95% confidence intervals

B.5 Estimation Excluding the Reform States

I drop all observations from the reform states (see discussion in section on Policy Changes in the US). In the main estimation results discussed in the text, these observations were included in the control group. Reform states have allowed various degrees of access to abortion prior to Roe v Wade, however abortion was still not fully accessible on demand for women who wanted it. The plots below report the difference-in-differences estimates obtained by estimating Eq. (2) by excluding observations from reform states. The results are similar in direction and magnitude to the main results reported in the text (Figs. 8 and 9).

Fig. 8

Effect of abortion access on age of motherhood. The figure reports point estimates with 95% confidence intervals

Fig. 9

Effect of abortion access on completed fertility. The figure reports point estimates with 95% confidence intervals

B.6 Evidence on the Importance of Distance

As discussed earlier, the main assumption in this empirical study is that state legalization created a cross-state cost variation in access to abortion, since women in various states had the option to travel to receive access to abortion

B.6.1 Drop Neighboring States

This exercise consists of dropping the states that are adjacent (“Neighbor” states) to repeal states from the sample. These states should have a lower cost of travel to repeal states, therefore making abortion more accessible in the Neighbor states compared to the other states in the control group. In this case, the coefficients of the impact of legalization in repeal states should be larger in comparison to the new control group, since that group now contains states in which the average cost of access is higher. Estimates of Eq. (2) using the restricted sample (excluding Neighbor states) are reported in the plots below (Figs. 10 and 11).

Fig. 10

Effect of abortion access on age of start of motherhood. The figure reports point estimates with 95% confidence intervals

Fig. 11

Effect of abortion access on completed fertility. The figure reports point estimates with 95% confidence intervals

The difference-in-differences estimates are slightly larger than those in the main estimation. While this is the expected direction of change in the results, the magnitude of the difference is not large. This could be due to several reasons, most notably that two of the five repeal states shared no borders with any other state, moreover the neighboring states to California and Washington have a small population, and therefore had a small weight in the estimation of the average effect. Moreover, Alaska, California and Hawaii had residency requirements for obtaining abortions, making them less attractive for out of state abortion seekers.

B.6.2 Mid-Atlantic Experience

In addition to the repeal states that are the main focus of this study, it became legal to obtain an abortion in Washington DC in 1971. I take advantage of the proximity of Washington DC and New York to a large group of states where abortion was not legalized to estimate the impact of legalization on nearby and distant states. I define three regions: region 1 is where abortion was legalized and is composed of Washington DC and New York, the region 2 is composed of the directly adjacent states and include the states of Connecticut, Delaware, Maryland, Massachusetts, New Hampshire, Pennsylvania, Rhode Island, Vermont and Virginia. Region 3 includes states in the eastern United States that are not directly adjacent to region 1, which includes the states of Indiana, Kentucky, Maine, Michigan, North Carolina, Ohio, South Carolina, Tennessee and West Virginia. If distance is an important determinant of access, then legalization of abortion in New York and Washington DC should have the highest impact on women residing within them (region 1), followed by impact on women residing in the adjacent states (region 2), and not much effect on women residing in region 3. Using observations from these three groups of states, I estimate the following equation:

$$\begin{aligned} y_{sg}&= \sum _{g=1}^9 \alpha _{1g} {\textit{Region}}_1*AG^{70}_g \sum _{g=1}^9 \alpha _{2g} {\textit{Region}}_2*AG^{70}_g\\&\quad + \sum _{g=1}^9 \beta _g AG^{73}_g + \theta _1 {\textit{age}} + \theta _2 {\textit{age}}^2 + \delta _s + \epsilon _{sg} \end{aligned}$$

where ${\textit{Region}}_1$ and ${\textit{Region}}_2$ are dummy variables indicating a woman’s state of residency is in the first region or second region respectively. The third region is the baseline region to which the other two regions are compared. Following the main empirical methodology in the text, I report the difference-in-differences estimates comparing women exposed to legal abortion at age g compared to those who were exposed at the end of their fertility cycle. The main addition in this framework is that I assume three levels of exposure: repeal, neighbor and distant states compared to repeal and non-repeal in the main estimation. Figure 12 reports the difference-in-differences estimates for age at start of motherhood. The results confirm the hypothesis that legalization had a significant and large impact in delaying start of motherhood in repeal states compared to states that did not repeal abortion ban and were distant from repeal states. Moreover, the results show that repeal of abortion ban had also an impact on women living in nearby non-repeal states, but that impact was smaller. The estimates show that in the north eastern U.S., “full” access to legal abortion when in the age group 15–17 delayed start of motherhood by 9 months, and delayed it by 4 months if accessed between the age of 18 and 20. “Partial” access to legal abortion, in neighboring states, delayed age of start of motherhood by 4 months if the access started when a woman was between the age of 15 and 17, and no effect for later exposure. The results found in this section show that access to abortion is not a binary outcome (access or no access), rather it should be thought of as a continuous scale of accessibility, where state regulations shift the cost of access function, making it more or less accessible.

Fig. 12

Effect of abortion access on age of start of motherhood. The figure reports point estimates with 95% confidence intervals

C Robustness to Potential Migration

In the main estimations reported in the text, a woman’s state of birth is used to determine her exposure to legal abortion. The possibility of between state migration implies that the treatment variable (interaction of repeal with age at repeal) is measured with error. This measurement error could bias the estimates of the effect of abortion access on fertility outcomes. What could be concerning in particular is the possibility that migration decisions are correlated with the state legislative changes. Such correlation could arise as a result of selective migration of women due to state decisions to repeal or uphold abortion bans. It might as well be due to migration decisions due to other factors that could correlate with the legal status of abortion in the state. For instance, if repeal state colleges were more appealing for females, there would a systematic migration from repeal to non-repeal states for college-age women. Information on state of residency at various points in time available in the IPUMS is used to check the sensitivity of the results found above. The details of these robustness checks are discussed in what follows. However, it should first be noted that a systematic measurement error due to selective migration from non-repeal to repeal states would most likely cause a downward bias. Given the magnitude of the estimates found, I believe it is highly unlikely that such measurement error exists.

C.1 Estimation Using Potential Non-Movers

In addition to state of birth, the IPUMS includes the state of residency of women at the time of observation. While these observations do not provide full information on the complete migration history of observed individuals, they inform us about which women did indeed migrate at some point during their life. If a woman at the time of observation is observed in the same state as her birth state, then she is assumed to have been living in her birth state during her fertility cycle. I then estimate Eq. (2) using the subsample of potential non-movers, which excludes all women that are known to have migrated. Estimation results for the fertility outcomes are reported below. Comparing these results with the results found in the main estimation, I find that the direction of the effects are preserved with slight change in the magnitude and precision of the estimates (Tables 15, 16, 17 and 18).

Table 15 Cross states differences in completed fertility (potential non-movers)

Table 16 Difference-in-differences estimates of the effect of abortion access on completed fertility (potential non-movers)

Table 17 Cross states differences in birth timing (potential non-movers)

Table 18 Difference-in-differences estimates of the effect of abortion access on birth timing (potential non-movers)

C.2 Evidence on Selective Migration

To further check that there was no systematic migration among women of various ages between repeal and non-repeal at the time of the legal changes, I take advantage of state of residency information available in the 1970 sample of the census, which reports both the state of residency at observation (1970) and 5 years earlier (1965). This information allows investigation of women’s migration decisions using men as a comparison group. Migration decisions of men were not potentially affected by the state abortion legal status or any other factor that could be appealing to women. I construct two migration dummy variables. The first variable $M^R_{i(b)}$ takes value 1 in case individual i of birth cohort b migrated from a non-repeal to a repeal state and 0 otherwise. The second migration variable $M^{NR}_{i(b)}$ takes value 1 if individual i of birth cohort b migrated from a repeal to a non-repeal and 0 otherwise. I then estimate the following equation for each of the migration outcomes

$$\begin{aligned} M_{i(b)}=\sum _{b=1930}^{1955} \alpha _b BC_{i(b)} + \sum _{b=1930}^{1955} \beta _b {\textit{Female}}_i * BC_{i(b)} \end{aligned}$$

where $BC_i$ is a birth cohort indicator and ${\textit{Female}}_i$ is a gender indicator of individual i. In case of positive selective migration among women of certain birth cohorts, $\beta$ coefficients of these cohorts should be positive and significant. Estimation results are reported in the table below for both migration outcomes. No serious selective migration is detected. I find that there is no difference between men and women of all birth cohorts in the propensity to emigrate from repeal to non-repeal states. As for the migration from non-repeal to repeal, men who were between the ages of 19 and 24 at the time of legal changes were significantly more likely to migrate compared to women, while no significant difference in the propensity to migrate for the other birth cohorts (Table 19).

Table 19 Evidence on selective migration