Same-Sex Marriage Recognition and Taxes: New Evidence about the Impact of Household Taxation

THE United States uses a progressive, family-based system of income taxation that necessarily creates unequal tax burdens between unmarried and married couples (Rosen, 1977). In other words, two couples with the same total earnings can face differing tax liabilities upon marriage, depending on how those earnings are split between the partners. Although some couples in the United States face a tax-induced marriage penalty, giving rise to the colloquial term “marriage tax,” many more currently face a tax-induced marriage subsidy.¹

In this paper, we estimate the effect of the tax-induced marriage subsidy on the probability of being married. Two key features differentiate our analysis from most previous research, which we summarize in table 1. First, our focus on same-sex couples enables a new identification strategy. While earlier studies incorporated variation in the tax code arising from tax reforms, those often induced small average changes in marriage subsidies or were local to particular earnings ranges, for example, involving the earned income tax credit. Our key variation depends on the recognition of same-sex marriage for tax purposes. Tax recognition began as some states legalized same-sex marriage, so same-sex married couples were required to file state income taxes as a household when marrying in or moving to those states. In 2013, the federal government was required by United States v. Windsor in 2013 to recognize legal marriages in those states, so previously married same-sex couples became subject to household taxation at the federal level. The remaining states allowed couples to marry (because of additional state laws and finally Obergefell v. Hodges in 2015), so same-sex married couples were required to file state and federal income taxes as a household when marrying in or moving to those states. These legal and judicial sources of variation, combined with conventional variation over states and years in tax progressivity and cross-sectionally in (predicted) household earnings and earnings splits, yield heterogeneous and sometimes quite large changes in the marriage subsidy.² This paper is the first, to the best of our knowledge, to leverage variation arising from a switch in tax regime (from individual to joint taxation) to identify marriage effects.

The second feature that distinguishes our analysis from many previous studies is our use of the American Community Survey (ACS), which reports both cohabitation and marriage, allowing us to define a sample exclusively of couples in a relationship.³ We use the 2012–2017 waves, which are the first of the U.S. Census Bureau Surveys to explicitly identify same-sex married couples.⁴ Thus, we consider the margin between cohabitation and marriage, compared to past studies that either used samples including married, cohabiting, and single individuals (Alm & Whittington, 1995a; Sjoquist & Walker, 1995; Dickert-Conlin & Houser, 2002; Herbst, 2011; Isaac, 2020) or use data in which cohabitation is not measured (Alm & Whittington, 1997, 1999; Eissa & Hoynes, 2003) or must be inferred (Ellwood, 2000; Fisher, 2013). We demonstrate that an analysis that ignores cohabitation information would result in substantial upward bias in the estimated elasticity of marriage. Another feature in some of the previous studies is their use of cross-sectional data and therefore marriage stocks as an outcome (Alm & Whittington, 1995a; Sjoquist & Walker, 1995; Ellwood, 2000; Eissa & Hoynes, 2003; Fisher, 2013), which are necessarily less responsive than marriage flows. Ours is close to a flow approach because the stock and flow of married couples is identical immediately following marriage legalization. And notably, the analysis we undertake is not possible using administrative data because, for example, all same-sex couples would appear to be unmarried in federal tax return data through 2012.⁵

As in other studies, we use self-reported household income from the ACS and impute income in the counterfactual marital state in order to calculate the marriage subsidy. We find a mean subsidy of $442 among married couples, meaning that they would pay $442 less in federal and state taxes than if they were single, compared to $264 among cohabiting couples, with sizable variation within both groups. As a counterfactual, this calculation assumes that individuals would have the same earnings in both states, so we address concerns that variation in the marriage subsidy may be endogenously determined. For example, couples may change their labor supply in response to marriage or marriage-induced tax changes (Isaac, forthcoming). Also, couples may report income with error and may not report enough information for us to accurately compute tax liability. We address such concerns in part by controlling for year and state fixed effects, which capture evolving attitudes toward same-sex marriage nationally as well as state-varying attitudes that may be correlated with tax progressivity or marriage recognition, as well as with residential, earnings, and marriage choices of same-sex couples. We further implement a simulated instruments approach, in which we calculate each individual's predicted earnings and then the couple's predicted marriage subsidy to use as an instrument for their observed marriage subsidy.

Following the general methods of Dahl and Lochner (2012) and Isaac (forthcoming), we predict earned income for each individual using observable household and individual characteristics in the ACS and use predicted earned income, legal marriage recognition status, and the NBER TAXSIM simulator to calculate each couple's predicted marriage subsidy. We implement a machine learning Lasso approach for the predictions in order to gain as much explanatory power as possible.⁶ Then, after instrumenting for the observed marriage subsidy with the predicted marriage subsidy in our baseline marriage specification, we gradually add controls for predicted earnings to ensure that identification comes purely from predicted changes in the marriage subsidy due to legal marriage recognition and not from a spurious relationship between predicted earnings and marriage rates.⁷

Our instrumental variables estimates indicate a statistically significant and robustly estimated but quite small effect of the tax-induced marriage subsidy on marriage. For the sample as a whole, we estimate that a $1,000 increase in the marriage subsidy (well above the mean subsidy of $341) causes a 0.8 to 1.4 percentage point (1.9 to 3.2%) increase in the probability of being married, implying an elasticity of 0.006 to 0.011. Our estimates are robust to controlling for state-by-year fixed effects or marriage incentives introduced by the Affordable Care Act or employer-sponsored health insurance, and are not driven by migration across states.⁸ We find somewhat bigger effects, but still quite modest, for female couples and childless couples; for the response to the federal component of the marriage subsidy, suggesting that federal taxes are more salient than state taxes; and for low-earning households, with the elasticity reaching as high as around 0.05 and falling gradually below 0.015 as household earnings pass $100,000.⁹ The interpretation of the federal subsidy elasticity of 0.015 is particularly clean because it avoids concerns about estimates that leverage staggered rollout of policy (Goodman-Bacon, 2021).

Finally, we use our estimates to simulate changes in marriage behavior for unmarried cohabiting couples as a result of the 2018 Tax Cuts and Jobs Act (TCJA). The TCJA increased the marriage subsidy for many high-earning couples by reducing progressivity: at the low end of the tax schedule by increasing the standard deduction and married-filing jointly tax brackets, and at the high end by reducing marginal tax rates. Our simulations suggest that the TCJA, by boosting average marriage subsidies, would increase the propensity of most high-earning cohabiting couples to marry, by an average of over 20% among couples with earnings above $300,000. Meanwhile, the changes in the marriage propensity for couples earning less than $230,000 range between a 10% increase or decrease but average to about 0.

Some of the recent research in this area estimates higher elasticities for low earners, compared to elasticities in earlier papers incorporating comprehensive tax variation. Those papers, focused on the earned income tax credit (EITC)—notably Michelmore (2016) and Bastian (2017)—report elasticities of over 0.20. In comparison, our estimated elasticities have a similar relative pattern by earnings but are significantly and substantially smaller. Other researchers have found significant but small effects of taxes on both marriage and divorce (Alm & Whittington, 1995a, 1999; Whittington & Alm, 1997; Dickert-Conlin, 1999; Eissa & Hoynes, 2003; Herbst, 2011; Fisher, 2013; Gayle & Shephard, 2019), while some have found little to no effect (Sjoquist & Walker, 1995; Ellwood, 2000; Dickert-Conlin & Houser, 2002; Light & Omori, 2008; Herbst, 2011; Isaac, 2020). Regardless of the effect size, significant impacts on marital status can be economically and socially meaningful by influencing tax revenue (Stevenson, 2012; Alm, Leguizamon, & Leguizamon, 2014; Isaac, forthcoming), retirement finances (Zissimopoulos, Karney, & Rauer, 2015; Borella, De Nardi, & Yang, 2023), health and access to health care (Carpenter et al., 2021; Friedberg, Guo, & Lin, 2018), and children's well-being (Lyle, 2006; Finlay & Neumark, 2010).

This paper is grounded in traditional taxation and marriage questions but also adds to the small yet growing literature on same-sex couples. Most closely related to this paper, Oreffice (2016) and Carpenter et al. (2021) also study marriage among same-sex couples, though neither focuses on taxation. Other research on same-sex couples and LGBT individuals has analyzed labor supply (Hansen, Martell, & Roncolato, 2020; Sansone, 2019; Isaac, forthcoming), labor market behavior compared to different-sex couples (Tebaldi & Elmslie, 2006; Oreffice, 2011; Antecol & Steinberger, 2013), workplace discrimination (Badgett, 1995; Carpenter, 2007; Plug, Webbink, & Martin, 2014), health outcomes (Buchmueller & Carpenter, 2010; Gonzales & Blewett, 2014; Carpenter et al., 2021), and predicted revenue effects of same-sex marriage legalization (Stevenson, 2012; Alm et al., 2014). This paper is the first, to the best of our knowledge, to use same-sex married couples to identify the effects of taxation on marriage.

This section describes the legal landscape for same-sex marriage at the federal and state levels and relevant tax implications since the federal Defense of Marriage Act (DOMA) was passed in 1996.

Each of these changes (state legalization, United States v. Windsor, post-Windsor state legalization, and Obergefell v. Hodges) introduced different treatment effects. We parameterize two classes of treatment: the legalization of same-sex marriage itself and the resulting marriage subsidy or penalty for same-sex couples, whether coming from the state, federal, or both tax schedules (which we will sometimes distinguish as separate treatments as well). Appendix table A1 provides a summary of these treatment effects, discussed below.

At the outset, state legalization laws before Windsor included legalization and tax treatment. The tax treatment in those early states is only generated by state tax progressivity. Same-sex married couples were still required to file as single individuals at the federal level and therefore were not exposed to the federal marriage subsidy.¹¹

Next, United States v. Windsor introduced only a federal tax treatment without a marriage legalization treatment. The ruling striking down DOMA did not affect states' same-sex marriage legislation and only required the federal government to recognize same-sex marriages that were permitted by some states. This treatment affected all same-sex married couples regardless of their current state of residence. Same-sex married couples were required to file at the federal level as married (filing jointly or separately) beginning in tax year 2013 even if their state of residence did not recognize same-sex marriages and required them to file as single individuals at the state level.¹² For states that had already legalized same-sex marriage by that time, Windsor aligned state and federal policy. For states that had not, it still exposed same-sex married couples living in those states to the federal marriage subsidy.

After that, state legalization that followed Windsor included a legalization treatment and introduced marriage subsidy variation arising from both the state and federal tax codes. Similarly, the Obergefell v. Hodges ruling, by mandating state legalization and recognition of same-sex marriages, included all treatment effects. Both of these changes aligned state and federal policy.

The staggered rollout of marriage equality at the state and federal levels meant that same-sex couples, even in the same financial situation, were exposed to varying magnitudes of marriage subsidies. As figure 2 made clear, pre-Windsor state-level marriage recognition generated a state but not federal tax treatment; the 2013 Windsor ruling generated a federal tax treatment only; and subsequent state-level recognition, followed by the 2015 Obergefell ruling, generated combined state and federal tax treatments.

The tax-induced marriage subsidy is defined as $MarriageSubsidyct=(Tit+Tjt)-Tct$⁠, where $Tit$ and $Tjt$ are each partner's tax liability if they file as single in year $t$ and $Tct$ is the couple's tax liability if they file jointly in year $t$⁠.¹³ A positive value of the marriage subsidy indicates a decline in tax liability and, hence, an increase in after-tax income as a result of marriage. Variation in the observed marriage subsidy is driven not only by the couple's total earned income but also by the partners' earned income split, which are the horizontal and vertical axes, respectively, in figure 1. The marriage subsidy is more positive the more uneven is the split in household earnings. Also, given the current tax code, the average marriage subsidy is more negative (i.e., a penalty) relative to income at very low and high household income levels than at other levels.

The means and standard deviations of the marriage subsidy for same-sex couples in the ACS appear in table 2, while details about these calculations appear later. We find that approximately 89% of the average observed marriage subsidy for this sample originates in the federal tax code. Among married couples, the observed marriage subsidy is $442, and among cohabiting couples, it is $264. The smaller value for cohabiting same-sex couples suggests a potential causal effect deterring marriage that we investigate below.

The average marriage subsidy in most of the early-legalizing states was negative but small in figure 3; the exception is California, which briefly legalized marriage in 2008. While state tax codes introduced some marriage nonneutrality, much of the variation we exploit was generated by federal marriage recognition following Windsor, which is evident in the jump in the average marriage subsidy arising when couples became exposed to substantial federal tax progressivity. This, along with subsequent state and federal recognition in the remaining states, also generated a substantial spread across states in the average marriage subsidy, arising from the interaction of progressivity at the state level with systematic differences in the typical level and split of household earnings among same-sex couples across states. Meanwhile, we will control separately for the legalization of marriage to distinguish its effect from the tax recognition of marriage.

Married is a binary variable that takes a value of 1 if couple $c$ in state $s$ in year $t$ is married. Marriage Subsidy is 0 when same-sex marriages are recognized by neither state nor federal tax authorities, and it takes positive or negative values as calculated from the relevant tax code otherwise, depending on the sequence of recognition delineated in figure 2. We additionally control for the variable Legal Marriage to capture whether the state allows same-sex marriages to occur, since this generates part of the variation in tax recognition. Therefore, the coefficient $β1$ isolates the effect of marriage nonneutrality of the tax code, while $β2$ captures the direct effect of marriage legalization, as in Carpenter et al. (2021). $Xcst$ controls for the couple's sex, racial composition, age, education, and presence and number of children, along with whether state $s$ expanded Medicaid under the ACA; in some specifications, we add controls that we discuss later to help deal with potential endogeneity or omitted variable concerns. $δt$ and $μs$ are year and state fixed effects, and in some specifications later, we control for state-by-year fixed effects. Year fixed effects capture time-varying nationwide shocks that may affect same-sex marriage rates, such as changing attitudes about same-sex relationships that may be correlated with the Windsor or Obergefell rulings. State fixed effects capture, for example, state attitudes toward same-sex relationships or discrimination against LGBT individuals, which may be correlated with the state's decision to legalize same-sex marriages (Gao & Zhang, 2016). We assume that the effect of the marriage subsidy on marriage is linear and explore this assumption further in appendix B.2.¹⁴

OLS estimation of equation (1) may be problematic for several reasons, resulting in an ambiguous direction of bias. First, measurement error in Marriage Subsidy may introduce bias into OLS estimates. Income in the ACS is likely to be reported with error and is reported for the previous twelve-month period rather than the calendar year. Furthermore, we do not observe enough about the household to determine its exact tax liability and hence its marriage subsidy. We do not know enough about either problem to determine whether the resulting measurement error is classical.

Second, it is possible that community-level omitted variables introduce bias because they are correlated with the marriage subsidy through attitudes toward both marriage recognition and labor supply in the LGBT community. If norms in favor of marriage recognition also drive, say, greater earnings equality within same-sex couples (reducing the marriage subsidy), then our OLS estimates would be biased downward, or, if norms in favor of marriage recognition also drive more traditional household specialization (raising the marriage subsidy), then our OLS estimates would be biased upward. Overall, we observe relatively more equal earners in same-sex couples than in different-sex couples (appendix figure A1), suggesting the first possibility.

Third, and most important, the labor supply of a married couple may change in response to marriage or to the same tax progressivity that causes nonneutrality of marriage. Isaac (forthcoming) demonstrates that Windsor-induced changes in the marriage subsidy caused secondary earners in already-married same-sex couples to reduce their labor supply. This labor supply response alters the observed marriage subsidy, introducing bias into an estimate of equation (1). The direction of simultaneity bias depends on the magnitude of the relationship between the marriage subsidy and marriage itself, but our results suggest that it may bias estimates upward.¹⁵

$MarriageSubsidy^$ is the fitted value from equation (2). Following the general methods of Dahl and Lochner (2012) and Isaac (forthcoming), we predict earned income for each individual and use predicted earned income and the NBER TAXSIM simulator to calculate each couple's predicted marriage subsidy. In doing so, we find that an accurate prediction of the marriage subsidy is critical, so we implement a machine learning Lasso approach in order to gain as much explanatory power as possible.¹⁶

The idea, therefore, is to use individual and couple characteristics to predict earnings of each partner and then use predicted earnings to compute a predicted marriage subsidy. Lacking an untreated control group for a standard difference-in-differences specification, we instead incorporate rich variation in the magnitude of the treatment. For example, the Predicted Marriage Subsidy$cst$ variable is non-0 only after state legalization or federal recognition (i.e., in the $Post$ period), which resembles a difference-in-differences treatment specification, and we leverage further variation in the strength of the treatment across couples. The orthogonality condition necessary for identification is $E(ɛcst|$Predicted Marriage Subsidy$cst,Zcst)=0$⁠, where Z$cst$ are the remaining covariates in equation (3). In other words, we require that Predicted Marriage Subsidy$cst$ is exogenous with respect to marriage decisions in the years after state legalization or federal recognition.

To check whether our approach identifies $β1$ strictly from the rollout of same-sex marriage recognition, we gradually add controls for predicted earnings when estimating equation (2) and equation (3). This ensures that identification arises purely from predicted changes in the marriage subsidy due to legal marriage recognition and does not reflect a spurious relationship between predicted earnings and marriage rates.¹⁷ These expanded earnings controls include a fifth-order polynomial in the couple's earnings and the earnings split between partners, in one specification, and also a control function in another.¹⁸

Our instrumental variables strategy thus alleviates measurement error, omitted variables bias, and endogeneity concerns by leveraging tax variation in the predicted marriage subsidy generated by state and federal same-sex marriage legalization and recognition. We also find that our estimates are robust to including state-by-year fixed effects, which exploits variation solely from the federal tax code and further controls for state-time varying unobservables that may affect same-sex marriage or its legalization, alleviating concerns about identification based on the staggered rollout of policy (Goodman-Bacon 2021).

We use the 2012–2017 waves of the American Community Survey to construct a sample of same-sex married and cohabiting couples.¹⁹ We restrict the sample to couples where both partners are between 18 and 60 years old to ensure that both partners are adults and to avoid potential marriage incentives originating from Social Security. Our main sample includes 37,234 couples (21,136 cohabiting couples and 16,098 married couples).²⁰

Appendix tables A2 and A3 present couple-level and individual-level summary statistics for same-sex married and cohabiting couples from 2012 to 2017. In the sample, 43.2% of same-sex couples are married. Married couples are more likely to be women and to have children and are older and have slightly lower employment compared to cohabiting couples.

The ACS reports earnings for each individual household member over the past twelve months. To alleviate endogeneity concerns that we noted earlier, we implement a simulated instrumental variable approach. We predict earned income for each individual, use predicted earned income and the NBER TAXSIM simulator to calculate each couple's predicted marriage subsidy, and use that as an instrumental variable for each couple's observed marriage subsidy. We limit our prediction sample to individuals observed in 2012 so that predictions do not reflect potential labor supply responses to the policies we study.

Because we have found that an accurate prediction of the marriage subsidy is critical, we implement a machine learning Lasso approach, as in Isaac (forthcoming), to gain explanatory power. The Lasso is a model selection method that uses a penalized regression to select the variables that best predict earned income using OLS (Tibshirani, 2011).²¹ It considers a large number of covariates and interactions while selecting the subset of variables that best fit the data. Variables that we included (but that the Lasso may have ultimately ignored) are five-year age group dummies; four education-level dummies; number of children; dummies for race and sex, two-digit occupation, college major, and state of residence; and pairwise interactions among all these.²²

We found that we gained important explanatory power when we first use a Lasso to predict whether individuals have positive earnings with a linear probability model. We convert these predicted probabilities into a binary variable by setting a threshold in the predicted earnings distribution resulting in the same value as the sample mean of having positive predicted earnings. For individuals with resulting positive predicted earnings, we use another Lasso regression to predict their earnings level, estimated on those in the prediction sample with positive observed earnings.²³

Appendix figure A2 displays kernel densities for reported and predicted earned income, split to show the higher-earning and lower-earning member of each couple. Our two-step approach to predict 0 and then positive conditional earnings helps us capture the relatively higher nonemployment rate for secondary earners, on the right side of the figure, although for both, we underpredict the frequency of positive but very low earnings and overpredict the frequency of earnings in the middle range. The $R2$ of the first- and second-step Lasso regressions are 0.449 for having positive earnings and 0.301 for earnings conditional on having positive earnings, and the mean predicted earnings split is 0.644, compared to the mean reported earnings split of 0.733, all of which suggest a reasonably accurate prediction process. Table 2 reports these mean values separately for married and cohabiting couples, appendix table A3 reports them separately for each partner, and appendix B.3 compares the joint distribution of the couple's total earned income and the earnings split between partners for reported and predicted earned income. They make it clear that our prediction process tends to understate earned income and the earnings split a little.

We use predicted earned income and the NBER TAXSIM simulator to calculate the predicted marriage subsidy for each couple. We focus on earned income rather than total income because positive income from other sources is infrequent and often small, making it difficult to predict precisely.²⁴ We calculate the tax liability as a function of only predicted earned income, number of children, and state of residence. As reported in table 2, the prediction process naturally yields more compressed variation than observed for actual marriage subsidies. Nevertheless, as we show later, we obtain a strong first-stage estimate.

Table 2 also makes it clear that the majority of the variation in the marriage subsidy arises from the federal rather than state subsidy, which is only 10.7% of the total. Therefore, our identification of the causal effect of the marriage subsidy comes largely from the federal subsidy and the United States v. Windsor ruling.

One issue with our approach to sample definition is that we omit noncohabiting people, some of whom are in relationships and may be encouraged or discouraged from marrying by the tax code, so our analysis offers an incomplete picture of marriage responses. We cannot determine how many couples married without cohabiting first using the ACS, so we use the 2014 Survey of Income and Program Participation (SIPP) to gauge this, although the resulting sample of same-sex couples is small. The 2014 panel was the first to differentiate between same-sex and different-sex partnerships and therefore allows us to observe transitions into cohabitation or marriage.

Appendix table A4 presents relationship transitions for individuals in same-sex relationships (panel A) and, for comparison, different-sex relationships (panel B), whom we can observe for at least two years. Among newly married same-sex couples in year $t$ (whom we observed as not married in year $t-1$⁠), 81.5% were cohabiting the year before. In contrast, among newly married different-sex couples, 61.0% were cohabiting the year before.²⁵ Thus, while the newly married were more commonly cohabiting than not beforehand, this was especially the case for a large majority of same-sex couples. Though the sample size is small, this analysis suggests that our approach using the ACS does not omit many noncohabiting couples who are contemplating marriage.

We first present results for our baseline IV model in equations (2) and (3), which estimates the impact of the marriage subsidy on the probability of being married. Then we add controls for predicted earned income and earned income split to ensure that our estimated marriage subsidy effect is driven by tax variation and not by our method for predicting earnings. After that, we estimate effects of the marriage subsidy that vary by household earnings, sources of variation in tax recognition, and other couple characteristics. Finally, we explore robustness of our estimates.²⁶

Table 3 presents the OLS and IV estimates of the effect of the combined federal and state marriage subsidy on the probability of being married, with the first-stage coefficients from the simulated IV reported in the bottom panel. The OLS estimates indicate that a $1,000 increase in the total marriage subsidy is associated with a 0.4 to 0.5 percentage point increase (0.9 to 1.2%) in the probability of being married, which implies a marriage-subsidy elasticity of 0.003 to 0.004 (⁠$p<0.01$⁠). These estimates are very small but precisely estimated and are smaller than most non-0 estimates found in the literature (Alm & Whittington, 1995a; Eissa & Hoynes, 2003; Bastian, 2017; Michelmore, 2016).

As noted earlier, however, OLS estimates of the effect of the marriage subsidy on marriage may be either positively or negatively biased due to measurement error, omitted variables, or endogeneous labor supply changes caused by marriage. The first-stage coefficients from our IV estimation are highly significant and range between 0.41 and 0.46. The first-stage coefficients differ from 1 because we only use predicted earned income instead of income from all sources when computing the predicted marriage subsidy and because our simulated IV approach, as designed, abstracts from endogenous determinants of earnings. For example, some couples who marry are likely to specialize within the household, which would tilt the earnings split and raise the observed marriage subsidy but not our predicted one, for married relative to cohabiting households.

The IV estimates remain statistically significant at the 1% level. We estimate that a $1,000 increase in the combined federal and state marriage subsidy causes a 0.8 to 1.4 percentage point (1.9% to 3.2%) increase in the probability of being married. These estimates are substantially larger than the OLS estimates. Nevertheless, the coefficient estimates translate to a quite small and precisely estimated marriage-subsidy elasticity of 0.006 to 0.011 (⁠$p<0.01$⁠).²⁷ Among estimates from the literature, some are relatively small as well (Alm & Whittington, 1995a; Eissa & Hoynes, 2003; Herbst, 2011) or are insignificant, while others are considerably higher (Alm & Whittington, 1999; Fisher, 2013; Gayle & Shephard, 2019), especially some recent ones based on EITC variation (Bastian, 2017; Michelmore, 2016); we consider possible heterogeneity in responsiveness by household income level below, which helps reconcile our results to recent ones to an extent. We further demonstrate in appendix B.1 the improvement in precision resulting from the considerably greater magnitude in marriage incentives that we exploit, compared to the literature; this gives us the statistical power to implement our IV approach and still gain more precision in our second-stage estimates than in some of the other papers, allowing us to obtain statistical significance of an estimate that is nonetheless quite small.²⁸

Moreover, the IV estimates are insensitive to the inclusion of predicted earnings controls. These additional specifications, shown in the remaining columns of table 3, isolate the variation arising from the tax code exclusive of the predicted level of earnings, predicted split in earnings, and the inputs to predicted earnings. It is also notable that access to legal same-sex marriage in one's state increases the probability of being married by 6.6 to 11.6 percentage points (15.2–26.9%), controlling for the tax-related effect. This estimate is smaller than those from Carpenter et al. (2021) but corroborates their main conclusions that legalizing same-sex marriage increases marriage rates.

Finally, one of the distinguishing features of our analysis is the use of cohabitation data in the ACS, which allows us to define a sample exclusively of couples in a relationship. In comparison, most estimates in the literature consider single and married people together, which, we demonstrate, inflate the estimated marriage elasticity. If we ignored information about cohabitation, the expanded sample that includes same-sex unrelated householders yields estimates that appear in appendix table B7.²⁹ The newly added nonpartner roommates are obviously unmarried, which results in a level drop in the sample mean marriage rate and are largely equally distributed around the mean marriage subsidy if they were to marry their roommate, which thus does little to pull the slope downward. Therefore, we continue to estimate effects of the marriage subsidy on marriage that are almost the same in magnitude, yet the much lower marriage rate in the extended sample including noncohabitors results in elasticity estimates that are approximately 2.5 times larger, a substantial upward bias. This analysis confirms the improvement that results from observing nonmarried partners, so we can determine who is on the margin of marriage.³⁰

As we noted, the marriage elasticity implied by our baseline estimates is quite small, especially compared to recent estimates based on EITC variation, which affects low-earning couples. Thus, it is worth exploring whether responsiveness to the marriage subsidy in our sample differs by household earnings level. We estimate our baseline IV model again while interacting the marriage subsidy with a fifth-order polynomial in household earned income.

Our results therefore confirm, as recent EITC-based estimates suggest compared to earlier estimates, that the marriage elasticity is higher for low-earning households. However, our estimate still fails to come anywhere close to the high recent estimates, based on EITC variation, of over 0.20 in Michelmore (2016) and Bastian (2017).

Table 4 presents IV estimates that distinguish the effect of the marriage subsidy arising from differing tax recognition policy treatments or from the federal versus state tax codes. We find that the marriage subsidy has an effect that is sometimes opposite signed, but imprecisely estimated and insignificant, before United States v. Windsor, and has comparable and significant effects of 0.8 to 1.5 percentage points per $1,000, relative to the baseline estimates in table 3, as a result of Windsor and post-Windsor state legalization that persists until Obergefell. Thus, the introduction of the federal marriage subsidy due to and after Windsor plays an important role in our estimation.

The second specification in table 4 explicitly allows the effects of the federal versus state marriage subsidies to differ. This shows that our main estimates are driven by variation in the federal subsidy, with an estimated effect of 0.022 in the most detailed specification, corresponding to a still-small elasticity of 0.015. In contrast, the estimated effect of the state subsidy is small, negatively signed, significantly different from the federal subsidy, and insignificantly different from zero. The interpretation of the effect of the federal subsidy in this specification is particularly clean because it avoids concerns involving the staggered rollout of policy (Goodman-Bacon, 2021). Our findings corroborate Light and Omori (2008), who find no significant effect of the state marriage tax penalty on the probability of marrying or divorcing. The relative lack of state-level variation, however, makes it difficult to conclude whether this reflects weaker identification arising from less state progressivity or weaker salience of state income taxes.³¹

Next, table 5 explores heterogeneous effects of the marriage subsidy depending on whether the couple has children and whether the partners are male or female. We estimate significantly larger effects among childless couples and among female couples relative to couples with children or male couples.³² The mechanical equivalence of the effect of marriage subsidies on women and men in studies of different-sex couples no longer holds in our setting, and so our estimates speak more broadly to possible differences in responsiveness to taxes by gender. We conclude that women are more responsive across the marriage margin in response to the tax-induced marriage subsidy.

Here, we address concerns that may remain about endogeneity or omitted variables, including estimating a state-by-year fixed-effect specification, controlling for employer-sponsored health insurance coverage, exploring migration effects, and considering how a traditional Mincer approach to predicting earnings performs as a simulated IV.³³

It may yet be that state-level attitudes toward same-sex relationships and discrimination against LGBT individuals are correlated with states' decisions to legalize same-sex marriage. It is also possible that state-time varying social norms within the LGBT community confound our estimates. To address these concerns, we include a full set of state-by-year fixed effects to capture state-time varying shocks and unobservables (such as changes in state-level transfer programs or health insurance coverage policies for same-sex couples) that may affect marriage rates or same-sex marriage legalization. This specification no longer allows us to identify coefficients on the Legal Marriage and Medicaid expansion variables. Identification of the effect of the federal subsidy should be similar in this context as in our main specifications because the Windsor ruling affected all same-sex married couples regardless of where they live or whether their state of residence recognized same-sex marriage. Identification of the effect of the state marriage subsidy, already weak, becomes more so because it is no longer driven by state same-sex marriage legalization, but by cross-sectional variation in predicted earnings and number of children.

Table 6 presents the estimates with state-by-year fixed effects. All of our first-stage estimates continue to be quite similar in magnitude and remain highly significant. Our main estimates that use the combined federal and state subsidy are essentially unchanged. When separating the effect of the federal and state subsidies, the specification with state-by-year fixed effects continues to show a significant and comparable effect of the federal subsidy relative to table 4. The coefficient on the state subsidy is negative as in our main estimates, and it is sometimes significant with slightly larger standard errors, which may reflect weaker identification. Thus, it does not appear that state-time varying omitted variables are confounding our estimates of the effect of the marriage subsidy on the probability of being married.³⁴

Yet another concern is that the marriage effects we estimate are instead driven by new access to health insurance coverage through one spouse's employer. Windsor did not mandate employer-sponsored health insurance (ESHI) coverage for same-sex spouses outside the federal government (Dawson, Kates, & Rae, 2018). Rather, access was granted by state marriage legalization or alternative partnership policies (e.g., civil unions).³⁵

An analysis of correlations of ESHI coverage, as observed in the ACS, and our predicted and observed marriage subsidy measures indicate that ignoring the possibility of spousal coverage following marriage might impart a negative bias to our estimate of the marriage subsidy impact on marriage, as detailed in appendix B.10. However, the estimated marriage subsidy impact when we include observed ESHI along with expanded predicted income controls is quite similar, suggesting little remaining correlation between ESHI coverage and the marriage subsidy.³⁶

A further concern related to health insurance is that the Affordable Care Act (ACA) introduced marriage incentives in 2014 via the tax credit available to households with income between 100% and 400% of the federal poverty line that purchased insurance through the exchanges. The ACA tax credit can introduce marriage incentives depending on the age-adjusted premium for each partner and the partners' income split because unmarried couples are considered separate health insurance units for the purposes of the tax credit. As detailed in appendix B.11, we calculate the ACA-induced marriage subsidy, which is small relative to the federal income tax–induced marriage subsidy, in appendix table B12. Same-sex couples over 2015 to 2017 in our sample faced an average ACA marriage subsidy of only $4 to $5, but, conditional on having a non-0 value, faced an average subsidy of approximately $400.

Appendix table B13 presents estimates controlling for the ACA marriage subsidy. Our main estimates are essentially unchanged, and the coefficient on the ACA marriage subsidy is negative and insignificant in all specifications. We conclude that marriage incentives created by the ACA tax credit do not confound our estimated effect of the marriage subsidy.

Migration responses to state legalization and state tax incentives may affect our main estimates, though recall that couples who married in a state that licensed same-sex marriage may live in a state that does not. To examine this, appendix table A4 reports that moves within the previous year are relatively infrequent; that moves from states that did not grant same-sex marriages to states that did were even more infrequent; and that such moves by married couples were yet more infrequent than by cohabiting couples. Moreover, while same-sex couples who moved experienced gains in their state tax marriage subsidy, and the gains were greater for married than for cohabiting couples, in both cases they were quite small on average, on the order of less than $100.

Finally, we consider a more traditional method than the Lasso of simulating income for our IV approach, instead based on a simple Mincer specification, in order to demonstrate our improvement in precision.³⁷ The values of the predicted marriage subsidy using the Mincer approach are, on average, negative rather than positive, as shown in appendix table B4, due to more equal predicted earnings splits using the Mincer earnings prediction. Appendix figure B3 makes clear that the traditional Mincer earnings prediction does not match the observed data well. Moreover, the Mincer-predicted marriage subsidy does not yield as good a fit in the first-stage estimates explaining the observed marriage subsidy, and the resulting IV estimates are all either wrong-signed relative to what theory would suggest, statistically insignificant, or both.

We finish by using our estimated responses to the marriage subsidy to simulate changes in the probability of being married for the population as a whole as a result of the 2018 Tax Cuts and Jobs Act (TCJA).³⁸ The TCJA increased the marriage subsidy (or decreased the marriage penalty) for many high-earning couples by reducing progressivity: at the low end of the tax schedule by increasing the standard deduction and married-filing jointly tax brackets and at the high end by reducing marginal tax rates. While the TCJA may have increased the probability of marrying, the highly nonuniform changes, depending on both the level and split of household earnings, means that some couples faced dramatic increases in marriage incentives while others faced less pronounced increases or even decreases.

We use our earnings-specific estimates, as shown in figure 4, for this exercise. We multiply these point estimates by the simulated dollar change in the marriage subsidy between 2017 and 2018 for each unmarried same-sex cohabiting couple in our sample and calculate the change in the marriage probability as a percentage of the base marriage rate.

The largest predicted effects of the TCJA are at the top of the income distribution because the TCJA flattened out the progressivity of the tax code, reducing the marriage penalties by far more than through the rest of the income distribution. Therefore, even though the elasticities that we estimated by income are largest for lower-income households, the average increase in the marriage subsidy in the lower section of the income distribution is small, leading to negligible predicted changes in the average probability of being married due to the TCJA.

We provide new evidence of the effects of progressive household-based taxation on the probability of being married among couples in a relationship. We use a sample of same-sex married and cohabiting couples from the 2012–2017 American Community Surveys, along with recent state and federal tax variation created by same-sex marriage legalization and recognition.

Our instrumental variables estimates imply that a $1,000 increase in the total marriage subsidy causes a 0.8 to 1.4 percentage point (1.9% to 3.2%) increase in the probability of being married, implying a significant marriage-subsidy elasticity of 0.006 to 0.011. This estimate is precisely and robustly estimated but quite small. We find somewhat bigger effects, though still quite modest, for women and for childless couples; for the response to the federal as opposed to state tax subsidies; and for low-earning households.

Finally, we use our estimates to simulate changes in the probability of being married as a result of the 2018 Tax Cuts and Jobs Act. Our simulations suggest that there were small changes in the probability of being married, averaging to about 0 but with a range of $+$/$-$10%, for cohabiting couples earning less than $230,000, and sizable increases for higher-earning cohabiting couples.

The Tax Cuts and Jobs Act is only the most recent policy that alters marriage incentives, and while some such changes have been incidental, at other times policy has been designed to deliberately reward marriage, as when the tax code was altered to reduce the “marriage tax” in the late 1990s and early 2000s. One statistic of interest, therefore, is the size of tax incentives needed to generate one marriage. Our baseline estimate suggests it would require approximately $71,500 in a tax-based marriage subsidy to generate one marriage.⁴⁰

This analysis not only speaks to the tax-induced economic impact of marriage for same-sex couples, therefore, but also offers an opportunity to learn more generally about couples' responsiveness to marriage incentives, and especially how these responses differ by income.