We use panel U.S. tax data spanning 2008–2013 to study the impact of the Affordable Care Act (ACA) young adult provision on an important demographic outcome: childbearing. The impact is theoretically ambiguous: gaining insurance may increase access to contraceptive services while also reducing the out-of-pocket costs of childbirth. Because employer-reported U.S. Wage and Tax Statements (W-2 forms) record access to employer-provided benefits, we can examine the impact of the coverage expansion by focusing on young adults whose parents have access to benefits. We compare those who are slightly younger than the age threshold with those who are slightly older. Our results suggest that the ACA young adult provision led to a modest decrease in childbearing.


As an early provision of the Affordable Care Act (ACA), insurers and sponsors of self-insured plans were required to allow dependents up to age 26 to remain on their parents’ private health insurance policies. In this study, we examine whether providing a source of health insurance unconnected to one’s own employment affects childbearing behavior.

Prior to this legislative reform, young adults (generally defined as 19- to 25-year-olds) were the most uninsured age group. Several studies have examined the insurance and medical care access effects of the ACA young adult (YA) provision, finding generally positive impacts (see, e.g., Akosa Antwi et al. 2013; Barbaresco et al. 2015; Sommers et al. 2013). The resulting increase in health insurance coverage and access to health care may, in turn, affect childbearing behavior, although the expected direction of the effect is ambiguous.

Gaining access to coverage may increase the use of prescription contraceptives (Culwell and Feinglass 2007), which may reduce or postpone childbearing (Miller et al. 2013). However, health insurance coverage—and private health insurance coverage in particular—is associated with better prenatal care and birth outcomes (Braveman et al. 1993; Currie and Gruber 1997; Egerter et al. 2002; Kaestner 1999; Oberg et al. 1991), which may increase childbearing if young adults expect better prenatal care and more positive birth outcomes. On the other hand, DeLeire et al. (2011) found that Medicaid expansions for pregnancy coverage are not associated with increased childbearing. We are not aware of any published study that has examined the ACA YA provision’s impact on childbearing. In concurrent unpublished work, Abramowitz (2017) examined childbearing using data from the American Community Survey (ACS) and the National Survey of Family Growth (NSFG), finding that the YA provision decreased the probability of childbirth and abortion while increasing the use of long-term contraceptives. Ma (2015) used birth certificate data, finding that the provision decreased fertility rates but increased the share of children born to unmarried and less-educated mothers.

Changes in childbearing can, in turn, lead to changes in the likelihood of filing a tax return. Numerous tax code provisions reduce taxes owed for those with children, including dependent exemptions, the Child Tax Credit, the Earned Income Tax Credit, and the Child and Dependent Care Credit. Because claiming these benefits requires filing an income tax return, an increase in childbearing may lead to an increase in filing and vice versa. However, if childbearing is also associated with lower labor supply and earnings, filing rates may decline.

In this study, we use tax data spanning 2008–2013 to estimate difference-in-differences (DD) models of childbearing, comparing 24- to 25-year-olds who were affected by the YA provision with 27- to 29-year-olds who were not. We make four novel contributions. First, we use administrative data, which are less subject to misreporting than survey data. Second, we focus on those whose parents are likely to have employer-sponsored insurance (ESI) and thus are affected by the reform. Third and fourth, we estimate effects separately by schooling status and by parental socioeconomic status.

We find that the YA provision reduced childbearing among young women, particularly among the unmarried, those with fewer than two prior children, and those not in postsecondary school. However, we find little effect on the propensity to file a tax return.


We draw a sample from the population of U.S. federal tax documents spanning 2008–2013. Using an existing tax data file from 1997 linking the Social Security numbers (SSNs) of primary and secondary filers to the SSNs of their dependent children,1 we match the parents’ information from U.S. Wage and Tax Statements (W-2 forms) filed in 2008–2013 to their children’s information on childbearing, income, and other demographic variables from those same years.2 Because individuals older than age 18 in 1997, or born after 1995, were less likely to be claimed as dependents in 1997, we use information on birth cohorts from 1979 through 1995. This structure limits our pre-trends tests to 2008–2009 because we cannot go back further than tax year 2008 and still have the full set of control individuals aged 27–29, given that our oldest cohort (those born in 1979) was younger than 29 prior to 2008.

We use information from Social Security Administration (SSA) and tax records to measure childbearing. Our preferred measure of childbearing uses an SSA file to identify the date of birth for children of any of the young adults in our sample. Working backward from the birth date, we create a variable denoted “conception assuming full term,” which indicates whether the young woman conceived a child in a particular year, assuming that the newborn was born after a full-term pregnancy.3 This variable is available regardless of whether a young adult files a tax return, and it treats the timing of control and treatment periods correctly, given that any birth in a particular year should be influenced by policies in place before conception as well as during pregnancy. As a robustness check, however, we also use birth in a given tax year as the dependent variable.

As an alternative measure, we exploit the fact that tax data contain the SSN of any child claimed as a dependent of a taxpayer in a particular year. Using a file provided by the SSA, we merge the birthdate of each child and identify a newborn by whether the taxpayer had a child in that tax year. This measure is, however, limited to tax filers.

Ideally, we would know parental ESI information for each year of our data. However, the IRS employer requirement for reporting ESI started in 2012, and only for those firms with more than 250 workers, which comprise approximately 55 % of private sector employment.4 We thus also use parental employer-based retirement plans (available in all years) to proxy for ESI. Tabulations from the Current Population Survey (CPS) and the Medical Expenditure Panel Survey (MEPS) suggest that more than 90 % of families in which at least one parent contributes to a retirement plan are also covered by ESI, which suggests validity of the proxy measure. Because approximately 20 % of families in the MEPS without employer-sponsored retirement are covered by ESI, not contributing to a retirement plan is a weaker proxy for lack of health insurance.

We also pull demographic information from the young adults’ and parents’ tax records, including marital status (from Form 1040, the individual income tax return), postsecondary attendance (from Form 1098-T, the tuition statement), and parental income (from the parents’ Form 1040).

In our main specifications, we include only young adult women: male health insurance access is unlikely to affect the contraceptive use or pregnancy behavior of their partners.

We use a 1 % sample from the parent-child matched population for our analysis. When we limit the sample of children to 24- to 29-year-olds, excluding 26-year-olds and using all data from 2008–2013 except 2010, we obtain 401,922 person-year observations in our female sample.5 Table 1 presents sample statistics for two samples: females aged 24–29, and females aged 24–29 whose parents participated in a retirement plan. Approximately 9 % report a newborn in a given year, although the fraction is slightly lower when we limit to those whose parents contributed to a retirement plan and so were likely to be covered by ESI.


We initially estimate the impact of the YA provision with a simple DD specification.6 We compare those in the treatment ages (24–25) with those outside the treatment ages (27–29), before and after the enactment of the ACA. We exclude 26-year-olds7 because they are likely to have been in both the treatment and control groups in the prior year.

We estimate an equation of the following form:
where Outcomeit denotes childbearing, Youngit denotes being aged 24–25, Postit denotes the year being 2011–2013, and δt is a year fixed effect.8 The coefficient of interest is β2.

We next conduct regression-adjusted versions of the DD calculations in which we account for the national annual unemployment rate, age fixed effects, and an interaction between the two. Because these estimates may still mask causal effects that occur only among those whose parents have ESI, our preferred DD model focuses on young adults with such parents.

In all specifications, we exclude 2010 as a period of staggered implementation. Some insurers complied with the ACA as early as spring 2010. However, because most insurance plans renew on January 1, 2011, we consider that the full implementation date.

To verify that our estimates are not driven by differential preexisting trends between the treatment and control groups, we test whether time trends in childbearing differ between the treatment and control groups in our limited set of years prior to the policy change. Reassuringly, the difference in pre-policy trends is not statistically significant for any of the specifications.9

As a further specification test, we examine whether parental ESI (as proxied by parental participation in a retirement plan) was affected by the ACA. If access was affected, the composition of treatment and control groups could be endogenous to the reform. However, in a DD model with parental health insurance as the dependent variable, the estimated impact was small and statistically insignificant.10


Main Estimation Results

Table 2 presents the results from our main specification. In panel A, the dependent variable indicates whether a conception occurred that resulted in a live birth, full-term pregnancy. In column 1, we present results from a simple DD specification. The estimated coefficient suggests that the YA provision decreased childbearing by 0.4 percentage points, and this coefficient is marginally statistically insignificant. When controls are added in column 2, the result remains a decline of 0.4 percentage points and is now highly statistically significant. In column 3, we cut the sample to those who are likely to be “treated” by the YA provision by including only those whose parents have an employer-based retirement plan. In this preferred specification, the estimated impact of the YA provision increases slightly to a 0.5 percentage point decline (from a base of 7.7 percentage points, for a decrease of 6.5 %) and is still highly statistically significant. This reduction would amount to a decrease of approximately 4,500 births annually.11

To examine the robustness of these results to alternative definitions of childbearing, we change the timing of the dependent variable to be the birth (rather than conception) of a child in the SSA data in panel B and the presence of a newborn in tax data in panel C. Because the timing of these variables is not exact, one would expect the estimates to be biased downward. This is indeed the case: the estimated coefficients in column 3 are smaller in magnitude (–0.002 and –0.003) than in our preferred specification and are marginally statistically significant. Because the dependent variables in panel C are observed only when a woman files a tax return, one might be concerned that if the YA provision affected filing behavior, this change in the sample might affect our estimates. Therefore, in panel D, we estimate the impact of the YA provision on tax return filing. Although we find a significant increase in the DD specification with controls, the effect is small and insignificant in the other two specifications, suggesting that those results are likely not significantly impacted by policy-driven changes in filing behavior.

Taken together, these results suggest that the YA provision led to a decline in childbearing among the targeted population.

Alternative Treatment Group

To examine the robustness of our preferred estimates to include younger cohorts in our treatment group, we expand the estimation sample to 19- to 29-year-olds.12 These results are presented in Table 3. When 19- to 23-year-olds are added to the treatment group, so that the treatment group now includes those aged 19–25, the effect on childbearing remains negative and statistically significant, but it is now somewhat larger, with the YA provision estimated to have decreased the propensity to have a child by 0.7 percentage points (or 11.1 % compared with a base of 6.3 percentage points). These results could reflect that younger women’s usage of contraceptive services may be more price-sensitive, leading to larger reaction and thus an even greater decline in childbearing.

Results for Subsamples

To examine whether the impact of the YA provision differed according to young adults’ demographic characteristics, we reestimate our preferred specification using a sample of young adult men. We also split the sample according to the income of the young adult’s parents in 1997. In Table 4, column 1 presents the results from our preferred specification.

In column 2, when a sample of young men is used for the estimation, the estimated coefficient for young men is smaller than that for young women and is statistically insignificant.13 This finding is consistent with the expectation that the YA provision would primarily affect childbearing through young women gaining access to their parents’ insurance.

In columns 3 and 4, we split the sample according to whether the young adult’s parents’ income in 1997 was lower or higher than the median income (approximately 250 % of the federal poverty level). Splitting the sample according to parental income is preferable to splitting according to the young adults’ income: parental income is likely to closely correlate with the young adult’s SES, whereas the young adult’s income may differ substantially from their SES while in school or starting out at a job. These specifications do not reflect much of a difference across income groups, with childbearing reduced by similar magnitudes in the two income groups (–0.006 vs. –0.007 percentage points).

Finally, in Table 5, we estimate effects by marital status, birth parity, and enrollment in postsecondary education.14 Because childbearing behavior tends to differ by marital status, estimating different effects by marital status is a natural extension. However, Abramowitz (2016) found that the YA provision reduced marriage among the affected ages, and so these groupings may be endogenous to the policy being studied. The results in Table 5 suggest that the decline in childbearing was steeper among unmarried young adults (with no significant effect for those married), those who already had one child (with a smaller effect among those with no children and no effect among those with two or more children), and those who were not in postsecondary school. Given the findings in Abramowitz (2016), however, an alternative interpretation of the steeper decline among unmarried women could be that the YA provision led young women who were not going to bear a child to stay single, thus decreasing the childbearing rate among this group.


Very little evidence prior to the ACA exists regarding how access to health insurance affects the demographic outcomes of young adults. Tax data provide a unique opportunity for estimating the impact of the ACA YA provision on childbearing with a large sample of administratively reported data, focusing on those whose parents were likely to have ESI.

Taken as a whole, our results suggest that the YA provision led to a decrease in childbearing among all young adult age cohorts but that the effect may have been particularly strong for 19- to 23-year-olds: our estimates imply declines of 6.5 % to 11.1 %. Assuming that dependent coverage increased by 30 % among our treatment group (the preferred estimate of Akosa Antwi et al. (2013)), the implied elasticity of childbearing to coverage would be between 0.22 and 0.37. Finally, despite the decline in childbearing, we find little effect on tax filing post-reform.

We also find that reductions in fertility are statistically significant only among unmarried young adults (not married young adults), although marriage itself maybe declining in prevalence as a result of the YA provision. Thus, either YA led to less marriage among those who were anyway less inclined to have children soon than other unmarried women, or the YA provision (perhaps through access to contraception) led to greater declines in fertility among those who are unmarried. We also find larger reductions among those who already had one child (with a smaller effect among those with no children and no effect among those with two or more children) and those who were not in postsecondary school, suggesting heterogeneity in the effect among young adults.

Some limitations to this study should be noted. First, because of data availability, our pre- and post-reform periods are limited to two years pre-reform and three years post-reform (through the end of 2013). As a result, whether the effects found here will persist in the long term remains to be seen. Second, we cannot directly observe parental insurance coverage for many in our sample, and so we utilize a proxy. Finally, the results found here pertain to one population (young adults with insured parents); whether similar effects will result from other types of insurance expansion is a fruitful topic for future research.


The views expressed are those of the authors and are not necessarily those of the U.S. Department of the Treasury (USDT). We thank Angshuman Gooptu and Kate Yang for research assistance.



Almost all children younger than age 19 are likely claimed on a parent’s tax returns as a dependent, especially given the substantial tax benefits of claiming children thusly. The dependent file based on claiming behavior is comprehensive in tax years 1997 and 2001 and forward but is very limited prior to 1997 and in 1998–2000.


If the parents divorced between 1997 and the 2008–2013 period, we are still able to match the W-2 information from both parents to the young adult. However, if one of the parents married or remarried, and the new spouse provided a source of health insurance coverage for the young adult, we would miss such coverage.


Because a nontrivial share of births is less than full-term, this variable will be measured with error. Ideally, we would use an estimate of gestational age at birth, such as that found in recent birth certificate data, to better estimate when conception occurred. Unfortunately, our tax data do not contain such information. To the extent that pregnancies were less than full-term, this variable may wrongly assign conceptions in the treatment period to the earlier control period, which would tend to bias our estimate downward. A similar bias arises if time of birth is used to assign treatment and control periods because some conceptions that occurred in the control period would be treated as if they occurred in the treatment period.


We examined our sample by year and age and observed that the number of individuals does not change in any systematic way over time as we construct a balanced panel, except that there are consistently more older-age than younger-age individuals, likely because 17- and 18-year-olds are more likely to have left the parental household by 1997. We found no evidence of systematic difference in sample size that would affect our identification method (for example, between treatment and control, before and after the policy).


Because some state mandates existed prior to the federal mandate, an alternative estimation strategy would be to estimate a triple difference specification in which states with and without preexisting state mandates form the third difference. Unfortunately, this is not possible using our data because we do not observe state of residence for young adults who do not file a tax return and do not receive a W-2 or 1098-T form. Further, state mandates were notably weaker than the federal mandate (they did not change federal tax deductibility rules, they were less well publicized, and they often excluded married children or nonstudent children), and thus prior research has found that the ACA mandate had as much of an effect in states with as in states without prior mandates (see, e.g., Akosa Antwi et al. 2013). As a result, a specification that considers all states as being treated by the ACA mandate seems most appropriate.


We exclude 26-year-olds only in the year in which they turned 26. These individuals are included in the sample in other years under analysis.


We do not include state fixed effects because we cannot observe state of residence for young adults who do not file a tax return and do not receive a W-2 or 1098-T form.


Our preferred specifications are reported in column 3 of Table 2. In the pre-trends tests for this specification, the coefficients (standard errors) on Treatment × PlaceboPost were 0.000 (0.005) in the Conception Assuming Full Term in SSA Data specification, –0.001 (0.005) in the Newborn in SSA Data specification, –0.002 (0.005) in the Newborn in Tax Data specification, and 0.006 (0.007) in the Tax Return Filer specification. Abramowitz (2017) performed similar tests using a longer pre-reform period and also could not reject equality of trends. The levels are, however, different, with 5.2 % of the control group (24- to 25-year-olds) conceiving a child in 2009, compared with 7.2 % of the treatment group (27- to 29-year-olds).


The estimated coefficient was actually negative at –0.001, with a standard error of 0.002.


The sample in this specification includes 93,170 young adults aged 24–25, who represent 9,317,042 individuals given our 1 % sampling rate. Thus, a 0.5 percentage point decline (assuming singleton births) is 46,585 fewer births. Because these are short-run effects, it is not possible to know whether these are simply delayed births or reductions in completed fertility.


In this specification, we include all individuals who are aged 19–29 (excluding 26-year-olds) in any year of the sample. Thus, the DD estimator compares the change in fertility between 19- to 25-year-olds in the post-period and 19- to 25-year-olds in the pre-period, and compares this with the difference in fertility among 27- to 29-year-olds in the post-period and 27- to 29-year-olds in the pre-period.


Further, the difference between the coefficients for young women and young men is statistically significant at the 5 % level in a pooled, fully interacted model.


Enrollment in postsecondary education is observed through the issuance of a Form 1098-T Tuition Statement for the young adult by a postsecondary institution. It measures enrollment at some point during the tax year.


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