First-time mothers and the labor market effects of the earned income tax credit

The Earned Income Tax Credit (ETIC) is one of the largest anti-poverty programs in the United States,

Only Medicaid, SNAP (Food Stamps), and Social Security spend larger amounts.

However, such strategies are threatened by the extent to which childbearing, marriage, and education decisions are endogenous to the EITC. Specifically, the EITC encourages childbearing and generally discourages marriage; its effects on education are ambiguous. As a result, using these measures to define treatment groups or divide the sample could yield biased estimates and, in particular, could lead to estimates that overstate the positive labor market incentives of the EITC for single mothers. For example, if the EITC results in some women remaining unmarried, and the group who do so work more (and at higher wages) than the group average,

This could occur if these women are more financially independent and are less likely to rely on a partner’s income.

The variation used in this paper is the timing of a woman’s first/only birth around the end of the calendar year.

Although similar to the approach is used in Wingender and LaLumia (2017), there are several differences between their approach and mine, which I detail later in this section.

In this paper, I leverage this end-of-year cut-off for EITC eligibility to estimate the EITC’s labor market effects for women who have their first/only child. I use the Survey of Income and Program Participation (SIPP) to identify the 12-month period following when women give birth to their first/only child.

Alternatively, one could imagine using the child’s becoming ineligible based on age (where December births are now controls and January births are treated), but this would be confounded by anticipation effects as well as the age threshold changing based on whether the child is a full-time student (which could itself be endogenous to the EITC (Bastian and Michelmore, 2018)).

I subject my baseline specification to several robustness checks to explore the validity of my findings as well as to uncover interesting heterogeneity. I explore the timing of these responses, finding that for low-ed unmarried women the effect is concentrated in the first six months following the birth of a child. As the labor market outcomes of the two groups (treatment and control) converge over time, this finding is further consistent with a knowledge effect. As we move forward in time, mothers are more likely to receive information regarding the EITC from some other means (e.g., word of mouth) or, eventually, from receiving it. Thus, it is sensible that my estimation strategy would only find short-run effects as all eligible women will receive the EITC within the first year and a half following the birth of their child. To reinforce this, I restrict the sample to only observations when the mother could have filed her tax return; my results show this time period does drive my findings. Given my crude running variable (month of birth), I use approaches where I vary the months (using only November to February births and excluding December and January births) to ensure that my results stand up to such checks. In the latter case, some results do become weaker, inviting future research with more accurate birth data. Finally, I show that my results are stronger in the second half of my sample period (2006–2016), further distancing this paper from critiques of traditional EITC studies levied by Kleven (2019).

Utilizing an RD research design requires several key assumptions, namely that women are unable to precisely manipulate the timing of their birth (or that they are unaware of the benefits of doing so) and that the mothers on either side of the end-of-year threshold do not differ from each other along other dimensions. I investigate the veracity of these claims in detail in Appendices A and B, but I find it pertinent to discuss the primary takeaways at the forefront. While it is true that the first week of the calendar year has the lowest average number of births during the time period (1969–1988) for which national birth data by date is available, the reduction in below average births per week is only around 8%. Furthermore, LaLumia, Sallee, and Turner (2015) find using the universe of tax returns from 2001 to 2010 that, although some birth timing manipulation occurs around the end-of-year threshold, it is not driven by low-income parents who stand to gain the most from shifting a child’s birth from early January into late December. Confirming this as best I can with the available SIPP data, I do not observe any birth movements. In fact, while I observe a similar number of January (719) and December (632) births, the relationship is the opposite of what would be expected if women were manipulating their birth timing.

For mothers to manipulate the timing of their birth, two conditions must simultaneously be fulfilled: they must be aware of the tax-related benefits of doing so and they must have the agency to perform either a Cesarean section or labor induction; either in isolation is insufficient. Further, there are factors including concerns regarding infant’s health (Schulkind and Shapiro, 2014) that discourage such behavior. Of course, I also investigate whether the data show any signs of such manipulation. In the Data section, I discuss in detail the observable characteristics of mothers as well as their labor market outcomes leading up to childbirth, as these should endogenously respond to the EITC if mothers know of the credit and anticipate receiving it. For unmarried women, the sample of greatest interest here, I find no evidence that women are endogenously selecting the timing of their children’s birth.

I also run a specification where I exclude December and January births as this is the only region where such manipulation could occur. Results become slightly weaker but remain generally consistent.

There are a few notable differences between the approach used in this paper and those used in traditional EITC studies. First, the Local Average Treatment Effect (LATE) identified by the regression discontinuity design is a causal estimate of a treatment’s average effect on compliers. Here, I assume perfect compliance and utilize a sharp regression discontinuity design. This is due to the fact that all individuals who had children during a calendar year and filed a tax return are eligible for the EITC, provided their income lies under the end of the phase-out region ($39,296 for one child in 2016).

There are a few other technical eligibility criteria, such as a maximum yearly investment income and rules governing care of the child, but earned income is the predominant criterion.

Although not explicit, my sharp RD design implicitly assumes that all women having a child are eligible for the EITC, including those with earnings beyond the phase-out region. One potential alternative would be to take earnings for women before the end of the calendar year and use NBER’s TAXSIM to simulate the amount each woman would receive from the EITC. However, I am reluctant to do this for several reasons. First, because one outcome is earnings in the 12 months following the child’s birth, the treatment would become (partially) a function of an outcome of interest. Second, there is some evidence of bunching around tax thresholds (LaLumia et al., 2015; Gans and Leigh, 2009; Neugart and Ohlsson, 2013), implying that a single EITC parameter for all women (conditional on state and year) is a more parsimonious way of measuring labor market responses to varying degrees of EITC generosity. Third, this would require me to continuously observe women for a longer period before their giving birth than is necessary for the analyses I present. As I would be forced to impute or make assumptions about pre-birth earnings, it would be difficult to accomplish this without my sample sizes being reduced to the point of being unable to detect genuine effects.

For the sake of transparency, I show that earnings are not meaningfully different across my treatment and control groups in the year prior to childbirth, at least for the subsample of women for whom such information is available in the SIPP.

As previously noted, the sample used here is restricted to mothers whose labor market outcomes are observed in the 12 months following the birth of their first child. This strategy differs from most research on the EITC, which typically includes all mothers with children in the household and, at most, controls for whether there are any children in the household too young to attend school (e.g., Meyer and Rosenbaum, 2001; Neumark and Shirley, 2020). Consequently, one caveat of this paper is that the population for which the LATE is identified cannot be considered representative of all mothers. At the same time, all women, excluding those whose first birth is also a multiple birth (e.g., twins), belong to this sample at some point in their childbearing history, providing useful information on the effects for women at a particular stage of their childbearing.

As mentioned earlier, there are two potential mechanisms under this identification strategy, and they differ in their hypothetical effects on labor market outcomes for new mothers. The primary mechanism I focus on here comes via an information shock for women as they receive the EITC for the first time.

Technically, from 1994 onwards there is a small childless EITC. However, due to its small size both in absolute terms and relative to the one-child EITC, as well as the much smaller income range over which it can be claimed, I ignore this zero-child credit. This is common practice in the EITC literature.

This mechanism closely relates to that of Chetty and Saez (2013), who use a field experiment where tax preparers at H&R Block were randomly assigned whether to go over the EITC schedule in detail with clients. They hypothesize that people do not fully understand the tax and transfer system in the United States, and providing information about that system to individuals and families could affect their decision-making. This mechanism is the same as the one I investigate in this paper with one important wrinkle. Here, I contend that people do not understand parts of the tax and transfer system with which they lack personal experience; upon interacting with a new part of the system (e.g., by having a child and receiving the EITC for the first time), they gain knowledge about the part’s mechanisms, at least in a broad sense. Chetty and Saez do not find statistically significant earnings effects from their field experiment, consistent with the evidence I provide here. Under my hypothesis that first-time mothers receive their largest information shock upon initial receipt of the credit, the information gain for the treated individuals and families in Chetty and Saez (2013) would have been minimal; their behavior in response to the EITC has already adapted from previous receipts of the credit on past tax returns.

Chetty and Saez (2013) do find some effects on reported self-employment income.

Generally speaking, these information effects should encourage single mothers who are not working to enter the labor force and push married mothers to reduce their hours or leave the labor force entirely. Non-working single mothers effectively receive a large wage subsidy from the EITC whereas married mothers, who are more likely to be in a dual-earner household, face larger effective marginal tax rates along the phase-out region of the EITC, in some cases nearly 50%. My results are consistent with these theoretical incentives; first-time mothers who are unmarried experience more positive labor market incentives from the EITC whereas married mothers are more negatively affected.

The income effect from the credit itself represents the second mechanism present under my research design. Not only do first-time mothers learn about the EITC upon initial receipt, but they also receive a larger-than-anticipated tax return. Given that low-income individuals heavily discount (Green et al., 1994; 1996), these mothers likely respond by using the EITC as a substitution for maternity leave and decrease their hours or leave the labor market entirely. Another factor in this direction is a mother’s increased value of time, driving up her reservation wage (Klerman and Leibowitz, 1994), from her desire to be with her child. Wingender and LaLumia (2017) provide evidence of these negative income effects with a similar identification strategy to mine, assigning differences in after-tax incomes calculated from NBER TAXSIM to mothers giving birth around the end of the tax year. Another advantage of their data set is the availability date of birth in the restricted-access American Community Survey, whereas my publicly available SIPP provides only month of birth. Their identification strategy allows them to estimate the effects of four policies in conjunction: the EITC, Child Tax Credit (CTC), additional dependent exemption, and head of household filing status (for unmarried women having their first child). They find that women who give birth in December return to the labor force more slowly than those who give birth in January. The mechanism through which they propose these findings occur is the income effect on labor supply, specifically that labor supply could be much more elastic following the birth of the child and the larger tax return via these policies encourages women to delay their return to the labor force.

At the surface, their findings and mine may seem to contradict one another, but I believe they are complementary as this paper focuses on a specific group of women, i.e., first-time mothers. As previously discussed, first-time mothers are exposed to both the income and information effects whereas Wingender and LaLumia (2017) focus solely on the income effects, which apply to having any child. My empirical strategy also isolates the effects of the refundable EITC from other non-refundable benefits associated with a December birth.

Mortenson et al. (2018) find evidence consistent with this, finding no effect of the CTC on labor market outcomes using a similar RD approach. However, as the CTC is worth less than the EITC and until the Tax Cuts and Jobs Act of 2017 was nonrefundable, it is more plausible that mothers respond to the EITC.

Although the specific parameters of the EITC have evolved over time via several reforms, the basic formula has remained constant. The EITC is designed to encourage work for the lowest earners so an individual or household with no income does not receive a credit. As income increases from zero, for every dollar an individual or household earns, they receive an additional fraction of a dollar in credit. The specific amount they receive is commonly referred to as the phase-in rate.

Since 2009, the phase-in rates for one, two, and three or more children have been 34, 40, and 45%, respectively.

Figure 1

The Omnibus Budget Reconciliation Act of 1993 was the single largest expansion of the EITC, increasing the phase-in rate for one child (two children) from 14% (14%) in 1990 to 34% (40%) in 1996. Other notable EITC changes include the introduction of a modest zero-child credit with a phase-in rate of 7.65% in 1994 (also part of the OBRA 1993) and the addition of a three or more children credit in 2009, which phases in at 45%. Starting in 1986, the maximum available credit was also indexed to inflation. Combined with the earlier EITC expansions, the maximum credit for one child rose from $1,192 in 1991 to $3,373 in 2016. Given that the minimum income necessary to receive the maximum credit was $9,920 in 2016, the EITC represents a potentially massive subsidy to low-income families. In addition to expansions by the federal government, 25 states (including the District of Columbia) have state supplements to the EITC as of 2016. In almost every case, the state supplements offer tax filers a flat percentage of the household’s federal EITC.

Wisconsin, the lone exception, awards a different percentages of the federal credit based on the number of children. As of 2016, these percentages were 4, 11, and 34 for one, two, and three or more children, respectively.

As Figure 1 shows, the two primary determinants of EITC eligibility are children and earned income. Among eligible groups, single mothers are generally the primary sample of interest when investigating the effects of the EITC for two reasons. First, single mothers with children are the largest group benefiting from the EITC, accounting for more than a third of recipients and nearly half of payments (Meyer, 2010). Second, estimating labor market outcomes for single mothers is a straightforward and parsimonious way to select a group of individuals relatively more likely to be affected by the positive extensive margin labor market effects of the EITC. Married mothers, to contrast, are both more likely to be in a dual-earner household and to be the secondary earner. A secondary earner in a dual-earner household likely faces the negative labor market effects from the EITC, which are a result of large effective marginal tax rates for households in the phase-out region

Two spouses working in 2016 at the US federal minimum wage of $7.25 per hour would reach the phase-out region if they each work approximately 30 hours per week.

The two most well-known papers in the EITC literature are Eissa and Liebman (1996) and Meyer and Rosenbaum (2001). Each focuses on an EITC expansion in the 1980s and 1990s, respectively, and each estimates the effects of these expansions on the labor market outcomes of single mothers. Both find robust evidence that, relative to women without children, the EITC increased the employment of single mothers. Together, they lay the foundation of the EITC’s reputation as a pro-work, anti-poverty policy. Adding to this popularity is the work of Eissa and Hoynes (2004), who focus on married women and find little evidence that these mothers respond to the EITC via their labor market decisions. Although the incentives exist for these mothers to decrease their work, a lack of evidence that such responses actually occur lessens this concern.

Subsequent work has focused on other potential outcomes, such as infant’s health (Hoynes et al., 2015), mothers’ health (Evans and Garthwaite, 2014), or children’s education (Bastian and Michelmore, 2018).

To a slightly lesser extent, the number of children and mother’s education can also play important roles in the analyses of the EITC’s effects. As the credit a household receives is partially determined by the number of children, some (e.g., Grogger, 2003) use this as identifying variation rather than using only a children or no-children distinction. Trying to assign EITC eligibility directly using earned income is problematic, as a mother may choose her earnings endogenously with respect to the EITC and because earnings are often an outcome of interest. To avoid this issue, education level is often used as a proxy for earnings and, thus, eligibility. Mothers with low levels of education, say a high school degree or less, are assumed eligible for the EITC and women with higher levels of education are assumed ineligible or less likely to be eligible.

Many studies estimate these effects in a DiD or generalized DiD framework, which require parallel trends for the treatment and control groups in the absence of the treatment and no compositional change in the two groups as a result of the treatment. Neumark and Shirley (2020) demonstrate that there is little evidence that the parallel trends assumption does not hold in most of the outcome and treatment/control group combinations frequently studied using data from the Panel Study of Income Dynamics, and that this same data replicates the results of earlier studies (specifically Eissa and Liebman (1996) and Meyer and Rosenbaum (2001)) with a reasonable degree of precision. The compositional change assumption requires that women’s fertility, marital, and educational decisions are not influenced by the EITC.

However, it is not difficult to imagine a scenario where the EITC does indeed alter these decisions. For example, generally the EITC is seen as a penalty to marriage.

I discuss the specific dynamics of when the EITC is a marriage penalty or subsidy in the following paragraphs.

The amount of EITC an individual or family is eligible for is strictly non-decreasing in the number of children they have, with the largest jump from zero children to one child. Given the pro-fertility incentives from subsidizing childbearing, the question is whether women respond to the EITC through increased childbearing and, if so, to what degree. Baughman and Dickert-Conlin (2003, 2009) directly explore the relationship between the EITC and fertility, finding mixed evidence. In their baseline specification, they find small reductions in higher-order fertility for white women as well as consistently large and positive fertility effects of state child tax (or child care) credits. They also note that the results they find when estimating their model separately for married and unmarried women may be driven by endogenous marriage decisions in response to the EITC. Duchovny (2001) also finds some evidence of increases in fertility for married white women and unmarried non-white women. More recent evidence that the EITC influences fertility decisions exists, including Bastian (2017), who estimates state EITC expansions increase completed fertility by around 7%. Although not overwhelming, the net of this evidence demonstrates, at a minimum, that care should be exercised when relying on assumptions regarding the lack of fertility effects from the EITC.

Depending on the earnings of two individuals considering marriage, the EITC may act as either a subsidy or penalty. Under a scenario where a non-working person with children considers marrying a working individual without children, the EITC acts as a marriage subsidy if the working individual’s income would qualify for the EITC and is marriage-neutral if their income lies beyond the phase-out region. Alternatively, if both individuals work, the EITC will, in most cases, act as a marriage penalty. If the two individuals’ combined incomes reach the phase-out region ($23,740 for one or more children in 2016

Again, this income could be reached by two individuals each working about 30 hours per week at the federal minimum wage.

In addition to subsidizing and penalizing marriage itself, married and unmarried women, on average, face fundamentally different incentives in response to the EITC. A primary objective of the EITC is to encourage work and subsidize earnings for low-income workers with children, and single mothers drive this response. A single mother who is not working would view the EITC as a large wage supplement, greatly increasing her effective wage and encouraging entry into the labor force. On the other hand, married women with a working spouse experience very large effective marginal tax rates if the combined dual-income reaches the phase-out region, in some cases as high as 50%. Taking marital decisions as exogenous to the EITC allows for exploration of differential EITC effects across this dimension, which is particularly interesting given these starkly contrasted predictions. The general consensus is that these theoretical responses are borne out empirically, with the EITC increasing labor force participation for single women with children (Eissa and Liebman, 1996; Meyer and Rosenbaum, 2000, 2001; Neumark and Wascher, 2011) and perhaps having negative intensive margin effects for married women (Eissa and Hoynes, 2004; Meyer, 2010; Neumark and Shirley, 2020).

The intersection of these two forces—that the EITC may reward or penalize marriage and the differences in labor market responses for married and unmarried women—is a potential issue for identifying the labor market effects of the EITC. Both Eissa and Hoynes (1999) and Herbst (2011) investigate this relationship and find that although the EITC indeed affects marriage decisions, the effects are relatively modest and not of an economically meaningful magnitude. Ellwood (2000) and Dickert-Conlin and Houser (2002) also explore the EITC’s marriage incentives, but find little effect of a response. More recently, however, Michelmore (2016) uses the SIPP and finds that the average EITC-eligible woman would lose approximately $1,300 in EITC benefits in the year following their marriage. Additionally, Michelmore finds that, relative to single mothers who expect no change or to gain EITC benefits from marriage, single mothers who expect to lose EITC benefits from marriage are less likely to marry and more likely to cohabitate. More recently, Bastian (2017) finds the opposite, with the EITC actually encouraging marriage. Regardless of the direction, such effects could introduce bias into estimates of the EITC’s labor market effects. Not all current research finds this, however, with Isaac (2018) using the National Longitudinal Survey of Youth and concluding the EITC affects marriage in line with the theory discussed above.

Taking a long-run perspective, Neumark and Shirley (2020) estimate the effects of the EITC on the proportion of years women spend unmarried or with children from ages 22 to 40. They find highly significant effects of the EITC on both outcomes, increasing the likelihood a woman is unmarried or has children. These effects, however, appear to wash out by the time a woman reaches 40, implying that the EITC marginally delays marriage or accelerates childbirth, rather than permanently changing these decisions. Thus, although not unanimous, there is enough evidence of endogenous marriage and fertility choices with respect to the EITC to warrant alternative identification strategies that estimate the labor market effects of the credit but are not subject to these biases.

Finally, the EITC also theoretically has implications for the educational attainment of mothers. In contrast to fertility and marital status decisions, it is ambiguous how a given mother’s educational attainment decisions might be influenced by the EITC. For example, if mothers are constrained by the costs of going back to school due to tuition and fees, foregone earnings, increases in child care costs, or any combination of these, then the EITC could help to offset those and encourage further educational attainment. Women may be able to reduce their hours worked, freeing up time for classes without decreasing their total income. On the other hand, the EITC acting as a wage subsidy decreases the returns to schooling. Depending on the relative size of these competing incentives, the EITC’s effects on mothers’ education could be positive, negative, or zero. In contrast to the fertility and marriage incentives, no work to my knowledge exists exploring this relationship.

There is a work estimating the educational effects for children of EITC recipients. See Manoli and Turner (2014) and Bastian and Michelmore (2018).

The literature on the EITC examines its effects on numerous labor market outcomes across a variety of groups most likely to receive its benefits. Almost all of these studies use observable characteristics including having children, marital status, and education level to identify treatment and control groups. However, these categories are all theoretically endogenous to the EITC and there is suggestive evidence that endogenous responses indeed occur. In order to estimate the effects of the EITC without relying on these categorizations, I use a different source of identifying variation and find results broadly consistent with the rest of the literature, an encouraging result for the view of the EITC as an effective anti-poverty program.

The data set utilized for the empirical analysis in this paper comes from the SIPP. The SIPP is a nationally representative survey designed to collect detailed data about incomes and labor force participation, as well as eligibility for and take-up of various social programs. To achieve these objectives, the SIPP uses a continuous series of national panels, with durations ranging from 2.5 to 4 years. Interviews are conducted in waves, with each interview utilizing a 4-month recall period.

This recall period was increased to one year beginning with the 2014 Panel.

To identify my sample of mothers with newborn children, I first identify whether a family unit has a newborn child in each period. If so, I record the age of the newborn (in months) as well as the identity of the child’s mother.

For twin births, I record the birth as usual but note that appropriate number of children for that women. These account for roughly 3% of newborns in the SIPP, similar to the national average.

Restricting the original survey to only women observed in the year following the birth of their first/only child yields a sample containing 59,717 person-month observations. Table 1, which contains descriptive statistics for the sample of women used in the primary analysis, shows that the sample comprises primarily married women, a reflection of the sampling frame of the SIPP. Additionally, we see that married women generally have higher monthly earnings ($2,079 versus $1,037) and are more likely to be highly educated. Employment rates and birth timings across marital status are fairly comparable, conditional on education. Although not detailed enough for the types of analyses I perform using the National Vital Statistics System (NVSS) data in Appendix A, births appear relatively uniform across months for all groups of women during our sample period, as shown in Figure 2. Focusing in particular on December and January, note that the total number of births across the two months (652 births in December and 723 births in January) are very similar, with more January births than December births— the opposite of what would be expected if birth timing manipulation were occurring. This fact aids the validity of my regression discontinuity strategy.

Figure 2

Another issue addressed at the bottom of Table 1 regards earnings in the year prior to women’s first births. It is not unreasonable to postulate that unmarried women who are aware of the EITC’s benefits but are not yet at the plateau region may, in the year prior to their child’s birth, be more likely to work (or to work more) in order to maximize a future EITC payment. On the other hand, those on the phase-out reason (particularly due to a spouse’s earnings) may choose to work less. Finding no differences between these groups on labor market outcomes prior to birth would be a useful piece of evidence in justifying my RD design. To explore this concern, Table 1 shows earnings and employment for women in the 12 months prior to their first birth, both aggregated across all women and divided into the treatment and control groups.

To identify this sample, I “project” the age of the child to periods before its birth where I observe the mother.

Before moving on to estimates designed to probe the robustness of my findings or explore avenues of effect heterogeneity, I first show the equivalent of specification 3 from Table 2, but only for the women having their second child. Such an estimate should isolate the income effects of the EITC, which are likely negative, as theory would predict and Wingender and LaLumia (2017) demonstrate. Table 4 appears to confirm this prediction. The information effect from the EITC drives the positive results for unmarried women in Table 2 and 3 and makes the negative estimates for the married women even more negative. Many more estimates here are statistically significant, including employment and IHS earnings for both unmarried groups, all of which are significant at the 5% level using the linear functional form.

In the next subsection I show a similar table, pooling women having their first, second, or third child.

It need not be the case that the effects of the EITC are symmetrical across the 12 months following the birth of a woman’s first child. One reason for this is the age of the child itself and the recovery of the mother after childbirth. At extremely young ages, mothers may have much higher reservation wages (Klerman and Leibowitz, 1994) and are more hesitant to return to work relative to when the child is slightly older. This argument is similar to, but operates on a much shorter time scale than, the distinction of whether a mother’s youngest child is school-age or not; this measure has been used in previous EITC studies, including Meyer and Rosenbaum (2001) and Neumark and Shirley (2020). Many women will naturally return to the workforce as their child ages, but the EITC may accelerate or slow down this phenomenon. On the other hand, the aforementioned slack in a new mother’s labor market outcomes will be largest early in the 12-month period, yields ambiguous predictions, and provides an opportunity for empirical evaluation.

This discussion touches upon an important and prescient wrinkle: the timing of when the information gain occurs. Individuals or families typically learn about the EITC when filling out their tax returns. That is, the information shock occurs when the tax return is completed and mothers notice that the return is (up to) $3,000 greater than anticipated. This windfall would obviously come as a pleasant surprise, and knowledge of the EITC is gained as recipients identify the source of the increased return. Because filers have up until 15th April to file their taxes in a normal year, they may not notice the increase until this date. Consequently, although mothers may be eligible to receive the EITC as a result of having a child right before the end of the calendar year, it could be up to four months

This number could be even higher for births in November or earlier. I address this in three ways, as shown in Tables 6–8.

The analysis in Table 5 is identical to that of specification 3 in Table 3, but splits the sample into two halves, based on whether the newborn is between 0 and 5 or 6 and 11 months old. The key takeaway here is that although the directions are similar in the first and second six months following the child’s birth, the results tend to be stronger in magnitude for all unmarried women during the second six months; for the low-ed married women, the results are rather consistent across the full year. For example, employment effects for all unmarried women are 2.6 and 2.4 pp in the first six months and 2.2 and 2.5 pp in the second six months. A similar pattern holds for earnings effects for this group with positive effects in the first six months and slightly smaller effects in the second six months, although these results are not statistically different from zero (or each other). For low-ed unmarried women, employment effects are positive across the first six months, but are very small and negative in the latter six months, while positive earnings effects also seem more likely at ages 0 to 5 months, with the log earnings effects marginally significant across both functional forms. For the low-ed married women, the effects are negative and relatively consistent, with marginal significance on the two linear functional form log earnings estimates (−16.4 and −15.1%, respectively).

Next, I disaggregate the previous analyses a bit further by estimating for each age in quarters. The benefit of this approach, of course, is that it allows me to demonstrate the EITC’s labor market effects at a finer level of detail. An additional benefit is that I can visually represent these effects. The obvious disadvantage is that I must effectively divide my baseline sample into fourths to perform this analysis generating further imprecision in my estimates. Given that some of my samples are rather small to begin with, especially the low-ed unmarried women, it could easily be the case that real employment or earnings effects that are detectable at more aggregate levels are impossible to detect. Figure 4A–C are divided by outcome with each bar representing an estimate using a quadratic f (X_i). The estimates are grouped into the four samples and are in order from left to right by the age of the woman’s newborn in quarters. These figures largely reflect what is shown in Table 5, albeit in a more visually digestible fashion.

Figure 4A

Figure 4B

Figure 4C

One flaw with the baseline regression discontinuity design employed here is the running variable itself, month of birth; date of birth would provide a much cleaner approach. That is to say, it is likely more convincing to say women giving birth within a few days of each other are more similar than those giving birth a few months from each other. To address the issue as best I can with the available data, I re-estimate my baseline results using all mothers who give birth within two months of the end-of-year cut-off. Thus, Table 6 shows results using births from November to February. Using this approach, the results are reasonably similar to the baseline specification but are, unsurprisingly, less precise. The IHS earnings effects for low-ed unmarried women remain positive, but the other measures become negative, although none are precisely estimated. For the low-ed married women, the effects are consistently negative and large but, again, sample sizes are much smaller than in the full sample. Admittedly, it is difficult to draw clear conclusions using a more restricted sample of women.

Although I have argued throughout the paper and in Appendix A that birth timing is not an issue for the low-ed, unmarried first-time mothers who are the primary sample of interest in this paper, excluding births within a small window on either side of the cut-off is one approach that could be used to directly combat the issue. This approach is similar in spirit to the donut-RD of Barreca et al. (2011) but, again, given that the running variable is birth month, the implementation is a bit crude. Excluding December and January births, as Table 7 shows, does not qualitatively change the results relative to the baseline. The strong positive IHS earnings effects for all unmarried women remain, as well as the negative earnings effects for low-ed married women, but some estimates become sensitive to functional form. While this specification does not refute the discussion so far, it does unfortunately fail to provide much corroborating evidence.

The next two tables will further explore my results in the context of when specifically women will be exposed to the information effects of the EITC. The first, Table 8, excludes the month where women have their child. This is done for two primary reasons. First, regardless of whether a woman learns about the EITC in that month, it is unlikely that she would desire to return to the workforce with such haste. Second, the notion that a woman could even do so in the first place requires a specific set of circumstances. A woman who has a child in late December and files her tax return early in January, i.e., as soon as a person is able to do so, will be exposed to the information effects of the EITC within the first month of her child’s birth. At the same time, for women having births in non-December months (July–November), this will not be the case. As a result, I do not exclude this period in the main analyses, but find it pertinent to show how the results are affected. Table 8 shows results quite similar to the baseline.

In Table 9, I take the same idea even further, restricting each treated woman’s time period to the months when she has had her child, it is under one year old, and the period is in the subsequent calendar year. The first two are the same sample criteria as every other table thus far, but the third restriction is done to ensure that each woman could have feasibly filled out her tax return and observed the additional EITC she will receive. As an example, the earliest treated group, women with births in July, have a 12-month period that runs from July until the following June in the baseline sample. The treated period for those women runs from January to June in the following year. The July to December period, while corresponding to when the newborn is between 0 and 5 months, does not align with a period when they would have been able to file their tax return.

The results are similar to using a slightly more restrictive version where I also exclude January and February in the following year.

The last set of robustness results presented are in Table 10. Here, I explore whether women appear to respond differently across the two halves of the overall sample period. Overall receipt of the EITC conditional on eligibility has risen over time and so has general knowledge of the program. As a result, it would be interesting to know whether the women receiving the EITC also seem to react differently along this dimension. Additionally, this allows me to distance my results even further from the critique of Kleven (2019), as responses in the second half of my sample period are more than a decade from the OBRA 1993 EITC expansions and the welfare reform that occurred during the same general time period. Table 10 runs the same analyses as Table 3, but splits the cohorts into two even halves (by number of years), with the first set of results covering the time period 1995–2005 and the second half covering 2006–2016. As the results indicate, the positive effects for unmarried women, especially the least educated, and the negative results for low-ed married women appear to be much stronger during the latter part of the sample window. This is consistent with the theory postulated here and throughout the paper that women learn about the EITC via initial receipt and that this effect is stronger during the period where the amount of knowledge regarding the program in the general public is stronger and there is more access to such resources.

One important element of this work’s contribution relative to Wingender and LaLumia (2017) is my identification of important treatment effect heterogeneity by birth order as well as the separation of the income and knowledge effects of the first-time receipt of the EITC. To further underscore these findings, I provide one final set of analyses in Table 11. Here, the premise is to recreate, as closely as I can using my sample and estimation strategy, a method that allows direct comparisons to Wingender and LaLumia (2017). In practical terms, this combines the simple estimation strategy from Table 2 across women having their first, second, or third child. Note that this will capture the income and knowledge effects for women having their first child as well as the income effects for women having their second or third child. This table clearly shows the treatment effect heterogeneity across birth order. Most estimates for unmarried women, both low-ed and otherwise, are negative and statistically significant. Similarly, all but one of the results for the third specification are negative for both groups of married women. For the all unmarried group, every single estimate is statistically significant at the 1% level save one, which is significant at the 5% level. From this, it is clear that the EITC has an overall negative effect on labor market outcomes in the first year following the birth of a child for most women. However, as the previous tables have argued and shown evidence for, the effects on low-ed unmarried first-time mothers tend to be positive, likely due to the information effect from receiving the EITC for the first time. At the same time, few of the results are statistically significant for these women, making it difficult to draw conclusions beyond suggestive evidence.

Before concluding, I wish to briefly mention the other analyses included in the Appendix. The broad takeaway from these additional tables is that my findings are not qualitatively changed, but they show additional approaches a reader may find interesting or pertinent. Appendix Table A1 shows the two children to three children diff-in-disc, finding mostly null effects, with the exception of high-ed married women. This is consistent with the notion that the stronger results for the one child to two children diff-in-disc shown in Table 3 is largely driven by the information effect and not the income effect. Appendix Table A2 takes this a step further, performing a diff-in-diff-in-disc, showing strong positive earnings results for low-ed unmarried women, weaker positive effects for all unmarried women, and negative (but insignificant) effects for both groups of married women. In the other tables, I use the sample weights (Appendix Table A4), alter the employment definitions and trim earnings outliers (Appendix Table A5), parameterize the EITC using the phase-in rate (Appendix Table A6) or the federal credit only (to avoid potential endogenous commuting (Shirley, 2018) behavior) (Appendix

Table A7), and estimate separate regressions for black mothers (Appendix Table A8). The sum of the evidence from these additional approaches reinforce the conclusions found in the main analyses.

The ETIC is one of the largest anti-poverty programs in the United States and has been widely praised for its anti-poverty effects and pro-work incentives. A number of studies have analyzed these effects, particularly for single mothers who are a primary target and recipient of the credit. Most of these studies separate women into treatment and control groups based on having children, marital status, and education level. However, as all of these categories are potentially endogenous to the EITC, it is possible the estimated labor market effects of the policy are biased upwards. This paper has discussed these potential biases, noted some evidence that endogenous responses occur, and implemented a different identification strategy using another source of EITC variation to avoid them: the timing of a woman’s first birth around the end of the calendar year.

Utilizing data from the SIPP and a regression discontinuity design around this end-of-year eligibility cut-off, I find positive employment and IHS earnings effects of the EITC for unmarried women, including those with a high school degree or less. These effects are consistent with the rest of the EITC literature but are driven here primarily via a knowledge effect stemming from receipt of the credit for the first time. When using a diff-in-disc approach to isolate the knowledge effect from the income effect from the credit itself, I find effect sizes roughly similar to the literature, although my earnings effects are larger in magnitude. This is not unexpected, however, as women have particularly low earnings during the period immediately following childbirth and, thus, my effect sizes reflect this lower baseline. Further, I find some evidence of negative earnings effects for low-ed married women, primarily along the intensive margin of employment. I conclude that, although endogenous marital, fertility, and educational responses to the EITC pose a potential threat to identification in traditional studies of the policy and there is sufficient empirical evidence to merit concern, these biases are not sufficient to demonstrably alter the conclusions of these previous studies. At the same time, my running variable (month of birth) is rather crude and further research using higher-quality data could provide additional evidence and further validation of the work here.