New Evidence against a Causal Marriage Wage Premium

Abstract

Recent research shows that men’s wages rise more rapidly than expected prior to marriage, but diverges on whether this indicates selection or a causal effect of anticipating marriage. We seek to adjudicate this debate by bringing together literatures on: (1) the male marriage wage premium, (2) selection into marriage based on men’s economic circumstances, and (3) the transition to adulthood, during which both union formation and unusually rapid improvements in work outcomes often occur. Using data from the NLSY79, we evaluate these perspectives. We show that wage declines predate rather than follow divorce, indicating no evidence that staying married benefits men’s wages. We find that older grooms experience no unusual wage patterns at marriage, suggesting that the observed marriage premium may simply reflect co-occurrence with the transition to adulthood for younger grooms. We show that men entering shotgun marriages experience similar premarital wage gains as other grooms, casting doubt on the claim that anticipation of marriage drives wage increases. We conclude that the observed wage patterns are most consistent with men marrying when their wages are already rising more rapidly than expected and divorcing when their wages are already falling, with no additional causal effect of marriage on wages.

The benefits of marriage for men’s wages are of long-standing interest to both economists and sociologists (Cheng 2016, Chun and Lee 2001, Cohen 2002, Cornwell and Rupert 1997, Dougherty 2006, Ginther and Zavodny 2001, Gray 1997, Hersch and Stratton 2000, Killewald and Gough 2013, Korenman and Neumark 1991, Loh 1996). Traditional fixed-effects models typically estimate that marriage increases men’s wages by about 5 to 7 percent (Cornwell and Rupert 1997, Dougherty 2006, Killewald 2013, Killewald and Gough 2013).

Taking a more nuanced approach, Dougherty (2006) and Cheng (2016) tracked men’s wages in the years leading up to marriage and through subsequent marital durations. Both find that men’s wages are already rising more rapidly than expected several years prior to marriage and argue that, including this premarital increase as part of the marriage premium, the long-term marriage wage premium is about 20 percent, much higher than estimated by traditional fixed-effects models. The interpretation of this descriptive pattern, however, is ambiguous. Both Cheng and Dougherty acknowledge three possible sources of the positive association between marriage and wages for men: (1) a causal effect of marriage on wages; (2) a causal effect of wages on marriage; (3) a spurious association between wages and marriage due to a latent maturation process. Furthermore, Cheng and Dougherty use the same dataset, the NLSY79, to estimate their models. Despite the similarity of theoretical framing, data, and research design, however, the authors arrive at different conclusions. Dougherty (2006, p. 442) argues that, since the increase in wages associated with marriage begins five or more years prior to marriage, household specialization is unlikely to be responsible for the gains. If specialization is the only possible mechanism for a causal effect of marriage on wages, Dougherty’s results suggest that marriage does not affect wages. However, marriage may affect wages through pathways other than specialization, such as by changing men’s priorities and preferences, and these effects may begin prior to the marriage date. Similarly, Cheng (2016) finds that men’s wages begin to increase as early as four years before marriage, but she concludes that marriage has a causal effect on men’s wages, accelerating wage growth.

We take as a starting point the finding from Dougherty and Cheng that men’s wages begin to increase more rapidly than expected several years before marriage and develop new tests to evaluate whether the pattern of wage growth in the years surrounding marriage is more consistent with a causal effect of marriage that predates marriage or with the alternative reverse causality or latent maturation perspectives. Using the same dataset as Dougherty and Cheng (NLSY79), we begin by replicating their findings of unexplained premarital wage increases. Next, we show that men who marry after age 26 experience no premarital increase in wages and no wage premium following marriage. This is consistent with the hypothesis that marriage has no causal effect on men’s wages, and that instead the premarital wage gains observed for young husbands are due to spurious rapid growth in wages in early adulthood, while men who marry later have largely completed this period well prior to their marriage and therefore experience no premarital wage increase.

We also compare the experiences of men whose marriage is followed by a birth within seven months—shotgun marriages—to those who do not have a birth shortly following their marriage. If the premarital rise in wages is due to anticipating marriage, men entering shotgun marriages should not experience this rise, as their marriage is less anticipated. Instead, we find similar patterns for both groups. We also estimate the wage benefits of staying married. Prior research suggests that at least some of the marriage premium dissipates following divorce (Killewald 2013, Korenman and Neumark 1991). However, we find that wage declines predate divorce. These results are consistent with reverse causality and with prior research that finds that job loss or lack of full-time employment increases men’s risk of divorce (Charles and Stephens 2004, Killewald 2016).

We argue that our results are more consistent with the hypothesis that marriage, including its anticipation, has no effect on men’s wages. These findings call for situating transitions to marriage within the more general life stage of the transition to adulthood and recognizing that divorce may be a consequence rather than cause of men’s falling wages.

Background

Married men experience wage advantages compared to both never-married and divorced men (Cheng 2016, Chun and Lee 2001, Cohen 2002, Cornwell and Rupert 1997, Ginther and Zavodny 2001, Hersch and Stratton 2000, Killewald and Gough 2013, Korenman and Neumark 1991), with some evidence of marriage premia increasing with marital duration (and the reverse for divorce) (Cheng 2016, Ginther and Zavodny 2001, Korenman and Neumark 1991).

In this section, we first describe why marriage might increase men’s wages and discuss what this means for likely effects of staying married compared to divorce and for changes in wages in advance of the marriage date. We then discuss the possibility that the association between marriage and wages is driven by selection rather than a causal effect of marriage.

Why might marriage affect men’s wages?

Specialization is the most prominent theory to explain a causal male marriage wage premium. It posits that wives’ contributions to unpaid labor allow husbands to increase effort in paid labor (Becker 1991), increasing husbands’ wages relative to single men who do not benefit from the sexual division of labor. Consistent with this perspective, marriage is associated with less time in household labor for men, particularly in female-typed tasks (Gupta 1999, Hersch and Stratton 2000). Cohabiting men might also experience wage gains from specialization compared to men living singly, but for men living singly no premarital increase in wages is predicted. Since divorce is associated with increases in men’s housework time compared to remaining married (Gupta 1999, Hersch and Stratton 2000), specialization also predicts a decline in men’s wages following divorce.

Employer discrimination may also cause higher wages for married men, especially if marriage generates biased perceptions by employers of men’s stability or competence. While this perspective is difficult to test empirically, it predicts no premarital marriage premium and a likely erosion of the premium following divorce.

Cheng (2016) and Dougherty (2006) document that men’s wages begin to increase more rapidly than expected several years before marriage, with no evidence that the marriage date itself immediately increases wages or accelerates wage growth. These findings cast doubt on the specialization and discrimination perspectives for the male marriage premium, since neither can explain the premarital wage increase and both suggest that the formation of the marital union itself should have wage consequences. Based on his findings, Dougherty (2006) argues against attributing the male marriage premium to specialization. Other research has similarly rejected the specialization explanation. For example, Killewald and Gough (2013) use the fact that married women, too, experience a wage premium to argue against the specialization explanation for married men’s higher wages. More directly, Hersch and Stratton (2000) and Pollmann-Schult (2011) show that men’s time in housework does not substantially mediate the male marriage premium. Given these results, we assume that, if marriage does affect men’s wages, it does not do so primarily through household specialization or discrimination.

However, the male marriage premium may arise for other reasons. Because wage-earning and financial providership are normative for husbands (Nock 1998), marriage may motivate men to invest more in wage-earning. Following divorce, motivation for wage-earning may decline, reducing wages. Cheng (2016, p. 32) describes this as the “motivation theory” of the male marriage premium. Consistent with this perspective, pay is ranked a more important job trait by married than unmarried men (Gorman 2000). This perspective, unlike specialization or discrimination, allows that men’s wages might increase prior to marriage, “as grooms-to-be shrug off bachelor habits and begin to assume the outlook and priorities of married men” (Waite and Gallagher 2000, p. 100). Killewald and Gough (2013) who, like Dougherty, focus on ruling out the specialization hypothesis, find that both men and women experience higher wages in the year immediately prior to marriage than in other pre-marriage years. Although they interpret their results primarily as indicative of a causal marriage premium, they write: “These results suggest that some of the returns to marriage may not be due to the marital union itself, but instead to the benefits of romantic partnerships more generally, or to time-varying selection into unions following wage increases” (page 493).

Thus, for scholars arguing against the specialization explanation for the male marriage premium, the premarital increase in wages is treated as either unproblematic or even further supportive evidence. These analyses, however, do not clarify whether there is a causal marriage premium for reasons other than household specialization, such as changing attitudes and motivation. When the potential mechanisms for the effect of marriage on wages are expanded beyond specialization, a premarital increase in wages, such as that found by Dougherty, Cheng, and Killewald and Gough, no longer rules out a causal marriage wage premium.

Petersen, Penner, and Høgsnes (2011), in a sample of Norwegian men, find that to-be-married men’s wages already exceed those of their peers and increase little at the transition to marriage, consistent with selection or with preemptive action by men who will ultimately marry. They write (p. 302): “What is clear…is that the premia to marriage and parenthood occur even before entrance into marriage and having children, and that these premia on balance are stronger than the premia for actually entering into marriage and fatherhood when using the results from within-individual changes in wages. The empirical fact is solid. How this is interpreted, however, is still open.” Our paper aims to provide evidence on the appropriate interpretation.

Selection into marriage

While premarital wage gains may reflect causal anticipation, an alternative interpretation is that the marriage premium arises due to selection of men into marriage on the basis of unobserved traits that are also positively associated with wages (Cheng 2016, p. 39, Dougherty 2006, p. 434). Fixed-effects or first-difference models, commonly used to estimate the marriage premium, alleviate bias of this kind only if the unobserved characteristics are time-invariant rather than time-varying. For example, men’s employment and earnings are positively associated with subsequent marriage (Oppenheimer, Kalmijn, and Lim 1997, Oppenheimer 2003, Sweeney 2002, Xie et al. 2003). Given that unmarried couples discuss postponing marriage until they have achieved financial goals (Edin and Kefalas 2005, Smock, Manning, and Porter 2005), a premarital increase in men’s wages is equally consistent with men’s wages affecting the transition to marriage as with an anticipatory effect of marriage on men’s wages. A similar problem may arise for divorce, since job loss and lack of full-time employment are associated with heightened risk of divorce (Charles and Stephens 2004, Killewald 2016). Thus, reverse causality poses a substantial threat to estimates of the effect of marriage on wages.

An association between marriage and wages may also be purely spurious, due to a heterogeneous maturation process (Cheng 2016, p. 39; Dougherty 2006, p. 434). Marriage typically occurs during young adulthood, a demographically dense time of high rates of both union formation and work instability and growth (Rindfuss 1991, Shanahan 2000). Men may experience several years of rapid changes in both work and family formation, as transitions to partnership and steady work are likely to be gradual or “blurred,” taking place over a prolonged period rather than crisply at a particular moment in time (Rindfuss 1991). These transitions happen in different orders and at different ages for different individuals (Hogan and Astone 1986, Rindfuss 1991, Shanahan 2000), as some individuals experience greater challenges navigating the transition to adulthood than others, particularly in employment (Oppenheimer et al. 1997). If blurred transitions to marriage and careers overlap in the transition to adulthood, men’s wages will begin to rise more rapidly than usual in the years prior to marriage, but not because of a causal effect of marriage anticipation on wages. Because the transition to adulthood is individual-specific in timing and duration, even flexible controls for age-wage associations will not fully net out this pattern.

Although there is no clear age at which the transition to adulthood ends, 30 may be used as an approximation (Rindfuss 1991). Since in our analytic sample men are age 32, on average, at divorce, compared to age 25 at marriage, we expect that the association between divorce and wages will not suffer as much from this spurious association, as most men approaching divorce have already completed the transition to adulthood. Men marrying later should also be less susceptible to this source of bias.

Plan for analyses

As described previously, both Cheng and Dougherty acknowledge the possibility that the male marriage premium may be driven by a causal effect, reverse causality, or spurious maturation processes. Although both observe increases in men’s wages prior to marriage, Dougherty interprets this pattern as evidence against the male marriage premium being driven by household specialization, implicitly arguing against a causal effect of marriage on wages, while Cheng argues that marriage exerts a long-term effect on men’s wages, although the process begins before the marriage date. Our analyses begin by replicating the findings of Dougherty and Cheng.

We then perform additional analyses that seek to adjudicate between these interpretations. First, we examine trends in wages prior to marriage for men marrying at different ages. If the pre-marriage trends are due to the transition to adulthood, we hypothesize that the ramp-up will be greater for men marrying earlier, while men marrying later will have already completed their period of rapid wage gains, experiencing no additional gains just prior to marriage. If the premarital ramp-up in wages is due to anticipation effects or reverse causality, we expect that it will be shared by all marrying men, regardless of their age at marriage. Of course, it is possible that marriage induces greater premarital motivation for wages among younger grooms (causal anticipation), or that younger grooms select more strongly into marriage on the basis of wage growth (reverse causality), possibly because their pre-marriage earnings are below a normative threshold. However, the transition to adulthood is the most parsimonious theory that would predict a stronger pre-marriage ramp-up among those who marry young.

Second, we take advantage of a group of marriages that follow a different selection process: shotgun marriages (Ginther and Zavodny 2001). We argue that marriages following a premarital conception are less anticipated than other marriages. If the premarital rise in wages is due to either a causal effect of marriage anticipation on wages or selection into marriage following wage gains, the premarital wage increase for men forming shotgun marriages should be smaller than for other husbands, as shotgun marriages are, on average, less anticipated and deliberately timed. Similar wage gains for both groups are more consistent with a spurious association.

Separately, we examine men’s wages in the years surrounding divorce. We expect that, if marriage has a causal effect on wages, it will fade following divorce, leading to declining wages. If divorce is prompted by declines in economic resources, the reverse causality perspective, we expect wage declines that predate divorce rather than follow it. Finally, since men are older at divorce than marriage, the transition to adulthood perspective suggests stability in wages in the years surrounding divorce, as most men are no longer experiencing rapid wage growth. Table 1 summarizes these empirical tests and the three theories described previously.

Table 1.

Theories relating marriage to wages

	(1)	(2)	(3)
	Causal marriage premium: Anticipation	Reverse causality: Wages affect marriage	Spurious association: Transition to adulthood
Theory	Men’s work behavior changes due to marriage, including in anticipation of taking on the husband role.	Men delay marriage until financial goals are achieved.	During the transition to adulthood, men mature rapidly, often marry, and experience wage increases.
Relevant literature	Cheng (2016), Waite and Gallagher (2000)	Edin and Kefalas (2005), Oppenheimer (2003), Oppenheimer, Kalmijn and Lim (1997), Smock, Manning and Porter (2005), Sweeney (2002), Xie et al. (2003)	Hogan and Astone (1986), Rindfuss (1991), Shanahan (2000)
Empirical predictions
Marriage exit	Wages decline after divorce.	Wages decline before divorce.	Wages flat through divorce.
Heterogeneity by timing	Wages increase prior to marriage regardless of marriage timing.	Wages increase prior to marriage regardless of marriage timing.	Wages increase more among those who marry young.
Shotgun marriage	Smaller premarital wage increases for shotgun marriages than others.	Smaller premarital wage increases for shotgun marriages than others.	Similar premarital wage increases, regardless of shotgun marriage status.

Data and Methods

Our analyses use the 1979–2012 waves of the 1979 cohort of the National Longitudinal Survey of Youth (NLSY79) (Bureau of Labor Statistics 2016a). The NLSY79 is a nationally-representative panel study that follows individuals from 1979, when they were age 14–22, through the present. We include observations from men’s entry into the adult labor force through the end of data collection at age 47–56. We define labor force entry as the first year the respondent is not enrolled in full-time school, provided he remains out of full-time school in the next interview. We exclude observations prior to labor force entry,¹ prior to age 18, and when the respondent is a full-time student or active-duty military. We exclude person-year observations from the self-employed and those working not for pay or in a family business, since for this population wages are an incomplete measure of labor income.

As described in more detail below, we use fixed-effects models, which rely on within-person variation. Therefore, we exclude from the models of marriage men who are followed through 2012 but never marry (10.6 percent) or attrit from the sample prior to 2012 and have not married when they attrit (13.9 percent). We also exclude observations that lack wage values because men are not employed (8.7 percent). Finally, we exclude 0.4 percent of the remaining observations because they do not contribute at least two observations for the fixed-effects model. The analytic sample for marriage entry includes 49,649 observations on 4,218 men.

Similarly, we exclude from the models of divorce those who are followed through 2012 but never divorce (31.2 percent of those who marry), attrit from the sample prior to 2012 and without having divorced (24.5 percent of those who marry), or end their first marriage due to widowhood (2.1 percent of those whose first marriage ends). We exclude 9.5 percent of observations for nonemployment and 0.8 percent of remaining observations for providing only one wage observation. The analytic sample for divorce includes 15,312 observations on 1,755 men.

Our dependent variable is the log of hourly wages in the respondent’s current or most recent job since the last interview.² We use the Bureau of Labor Statistics Consumer Price Index to adjust to 2012 dollars, and we bottom- and top-code hourly wages at $1 and $100 to reduce the effect of outliers.

To adjust for age differences between married and unmarried individuals, we control for potential experience, defined as the respondent’s age minus the age at which he entered the labor market, plus one (so that all values are non-zero), and then logged.³ If men with unusually rapid wage growth tend to marry early, conventional fixed-effects models will produce upwardly-biased estimates of the marriage premium (Loughran and Zissimopoulos 2009). To address this source of selection bias, we allow the background potential experience-wage profile to vary by educational attainment, academic achievement, race, and age at marriage (under 23, 23–26, and over 26). We measure education with four categories: no high school degree, a high school degree but no postsecondary education, some college, and four or more years of college. Academic achievement is measured with percentile on the Armed Forces Qualification Test (AFQT). We measure race as classified by the NLSY79 during household screening: non-Hispanic white or other, non-Hispanic black, and Hispanic. For the 154 observations missing education data, we use surrounding years to impute values. We multiply impute missing AFQT values.

We include controls for other family formation changes (cohabitation and parenthood) in order to isolate the effects of marriage. We measure cohabitation with a dummy variable set to one if the individual is currently unmarried and reports a partner in the household roster. We measure parenthood with the respondent’s number of own coresidential children. Lastly, we measure period or business cycle effects with year indicators.

Models

To examine wage patterns in the years leading up to and following marriage or divorce, we estimate wage trajectories at the time of marital status transitions using linear splines with knots one year before and after the transition. Similar to Duncan, Wilkerson, and England’s (2006) study of marriage and drug use, this approach allows us to report wage growth rates in the years before, during, and after marriage. Our approach also builds on Dougherty’s (2006) notion that fixed-effects models should be sufficiently flexible to describe the temporal structure of wage growth relative to marriage.⁴ The marriage model is represented by equation (1) below, with vectors and matrices in bold type. The outcome is logged hourly wages for respondent i at time t[ln(Y_it)].

$$ln(Y_{it})=M_{it}^{[-5,-1]}{\beta }_1+M_{it}^{[-1,1]}{\beta }_2+M_{it}^{[1,5]}{\beta }_3+M_{it}^{[5,10]}{\beta }_4+{\mathit{X}}_{it}\mathit{\nu }+{\alpha }_i+{\delta }_t+{\epsilon }_{it}$$ (1)

While conventional fixed-effects models measure marriage with a dummy variable for current marital status, or current status plus years spent in that status, our key independent variables are a linear spline for years since marriage, represented by the M terms in the equation. Each of the M terms is a truncated measure of how long before or after the marriage date the current year is, with each term representing a different range for which values are not truncated, reflected in the numbers in superscripts. For example, the first term, $M_{it}^{[-5,-1]}$, is untruncated for observations 1 to 5 years before marriage; for these years the value is coded -1 through -5. For observations after the year prior to marriage it is coded -1, and for observations more than five years prior to marriage it is coded -5. This approach makes interpretation simple: rates of log wage growth before, during, after, and long after marriage, net of control variables, are captured by β₁, β₂, β₃, and β₄, respectively. Throughout, when we refer to “wage growth” in the years surrounding marital transitions, we mean growth that is not explained by the control variables, including aging. The reference category is those who will marry in five or more years, and respondents are censored after the ends of their first marriages.

Like conventional fixed-effects models, our models estimate unique intercepts for each person (α_i ) and year (δ_t) to net out time-invariant, unobserved characteristics of individuals and years associated with both wages and the independent variables. Time-varying control variables (X_it) are as previously described. All models are weighted, and unweighted results are similar. Standard errors are clustered at the individual level.

The models analyzing wage changes around divorce, represented by equation (2), are analogous. We censor respondents prior to the start of their first marriage and after the start of their second marriage, if one exists. Therefore, the sample includes only observations from individuals who are currently married and will divorce, or are currently divorced but have not yet remarried. Because respondents who divorce often do so within a few years of marriage, and remarriage often occurs shortly after divorce, we estimate wage trajectories for a shorter period of time than in the marriage models: three years before to five years after divorce.

$$ln(Y_{it})=D_{it}^{[-3,-1]}{\gamma }_1+D_{it}^{[-1,1]}{\gamma }_2+D_{it}^{[1,5]}{\gamma }_3+{\mathit{X}}_{it}\mathit{\nu }+{\alpha }_i+{\delta }_t+{\epsilon }_{it}$$ (2)

Our choice of a spline specification is designed to strike a middle ground between parsimony and flexibility in the shape of wage changes during the years surrounding marital transitions. Both Dougherty and Cheng use single-year dummies for each of the years surrounding marital transitions, maximizing flexibility.⁵ Our spline models closely replicate the patterns of these more flexible specifications (see online supplement).

An advantage of the linear spline specification is that it facilitates clear tests of our hypotheses. In our first analysis of transitions to marriage, we confirm Cheng and Dougherty’s findings that wages increase more rapidly than expected in the years prior to marriage (β₁ > 0). We subsequently test whether it is possible to reject the null hypothesis of linear increases in wages throughout the entire period from five years before through ten years after marriage (β₁ = β₂ = β₃ = β₄). If we cannot reject this hypothesis, minimally, it indicates that the marriage itself does not speed wage increases, relative to the years just before.

As in the marriage model, in our divorce model we test whether we can reject the null hypothesis of a linear relationship in wages throughout the entire period, from three years before to five years following divorce (γ₁ = γ₂ = γ₃). If the wage pattern is linear, this suggests that divorce does not exert a unique effect on wage patterns, whereas a greater decline in wages in the periods during and following divorce suggests a divorce wage penalty. We additionally examine whether wages begin to fall prior to the divorce (γ₁ < 0), consistent with reverse causality — divorce following wage declines. Alternatively, if we see no evidence that wages change unusually in the years surrounding divorce (γ₁ = γ₂ =γ₃ = 0), this is most consistent with no causal association between wages and divorce in either direction.

Next, we return to the marriage models to examine how wage growth in the years surrounding marriage varies by age at marriage. As described previously, the transition to adulthood perspective suggests that wages should increase more rapidly in the years prior to marriage, on average, for men marrying younger ( ${\beta }_1^{\mathit{young}}>{\beta }_1^{\mathit{old}}$). If preparation for marriage encourages wage growth or wage growth encourages marriage, by contrast, we might expect similar premarital wage increases, regardless of age at marriage. To test this hypothesis, we test for significant differences in wage patterns in the years surrounding marriage by terciles of age at marriage, particularly examining whether wages in this period are flatter for men marrying older than those marrying younger.⁶

Finally, we test whether men whose marriage is followed by a first birth within 7 months experience a similar premarital wage increase to other grooms. In this analysis, men who became fathers before marriage are excluded.⁷ In our sample, 42 percent of men with premarital conceptions enter a shotgun marriage. If a causal anticipatory effect of marriage drives the observed premarital run-up in wages, these premarital gains should be smaller for men entering shotgun marriages, which are less likely than other marriages to be anticipated ( ${\beta }_1^{\mathit{shotgun}}<{\beta }_1^{\mathit{not}\mathit{shotgun}}$). Smaller premarital wage increases for men entering shotgun marriages is likewise consistent with reverse causality: these grooms are less likely to have timed their marriage to a period when their wages are already rising unusually quickly. On the other hand, if premarital wage gains are similar regardless of shotgun marriage status, this is most consistent with the transition to adulthood perspective, which suggests that the marriage process is incidental to other factors shaping wage growth.

Results

Table 2 provides weighted descriptive statistics for the samples used to evaluate the marriage wage premium at entry to and exit from a first marriage. Compared to when never-married, married men are older (34 versus 25) and have higher average wages ($24.66 versus $16.71). Divorced men are older than to-be-divorced men (36 versus 29), but their average wages are similar ($19.60 versus $19.88).

Table 2.

Descriptive statistics of sample, by marital status

	Marriage premium		Divorce penalty
	Never married	Married	Married, will divorce	Divorced
Cohabiting	0.12	-	-	0.20
Number of children	0.04 (0.28)	1.16 (1.09)	1.03 (1.03)	0.24 (0.65)
Age	24.59 (4.71)	33.72 (8.38)	29.34 (6.20)	35.89 (8.30)
Potential experience	5.05 (4.55)	13.81 (8.24)	10.23 (6.14)	16.83 (8.19)
Education
Less than high school	0.14	0.11	0.19	0.17
Exactly high school	0.48	0.44	0.49	0.53
Some college	0.18	0.18	0.18	0.19
4+ years of college	0.20	0.27	0.14	0.12
Race
Hispanic	0.06	0.06	0.07	0.07
Black	0.12	0.11	0.13	0.13
White/other	0.82	0.83	0.80	0.80
Hourly wage (2012 $)	16.71 (10.21)	24.66 (15.96)	19.88 (11.23)	19.60 (12.91)
Observations	16,749	32,900	9,016	6,296
Respondents	3,359	4,006	1,566	1,470

Note: Samples are restricted to observations on employed respondents who are included in the models in Figure 1. Observations are weighted using sample weights to be representative of the national population within the age range of the cohort. The married columns refer to individuals in a first marriage. The divorced column refers to those whose first marriage has ended and who have not yet remarried. The racial distribution is estimated at the respondent level.

All other descriptive statistics are estimated at the observation level.

Figure 1 shows modeled wage trajectories in the years surrounding the entry to and exit from a first marriage. Tabular results are available in the online supplement. Because the outcome is the log of hourly wages, we exponentiate the predictions and subtract one to yield the predicted percent change in wages for each year, relative to 5 or more years prior to marriage or 3 or more year prior to divorce. The shaded areas show 95 percent confidence intervals for the estimated effects.

Figure 1.

Spline wage trajectories at marriage and divorce

Note: Models are linear regression models with person fixed-effects estimated with sampling weights. Figures show the predicted percent change in wages, relative to the value 5 or more years prior to marriage or 3 or more years prior to divorce. The marriage model excludes respondents who never marry and observations after the end of a first marriage. The divorce model excludes respondents who never divorce, observations prior to the start of a first marriage, and observations after the start of a second marriage. Conventional fixed-effects models with dummy variables for current marital status show a 3.8% marriage premium and a 5.0% divorce penalty. We cannot reject the joint null hypothesis of linearity throughout the entire window in either model, nor can we reject the null of linearity at any of the individual knots in either model. Full results are available in the online supplement, Tables A1 and A2.

The left panel in Figure 1 shows men’s changing wages in the years prior to and following entry into marriage. For comparison, we estimated a traditional fixed-effects model with an indicator variable for being married and found a 3.8 percent marriage wage premium, similar to prior results that use this method. In the more flexible spline specification, between five years before marriage and one year before marriage, men’s wages increase each year 0.5 percent more than expected, although the rate of increase is not statistically distinguishable from zero. In the years immediately before and after the marriage, men’s wages increase each year 1.5 percent more than expected, which is statistically significantly different from zero. Descriptively, men accumulate a wage premium of 2 percent by the year before marriage, which grows to 5 percent by the year after marriage. The premium increases only very modestly over the next nine years, stabilizing at about 6 percent. The results do not lend themselves to clear interpretation. On the one hand, wage growth is most rapid in the years immediately surrounding marriage, consistent with a causal marriage premium. On the other hand, the general upward trend in wages throughout the years surrounding marriage is similar to that found by Dougherty (2006) and Cheng (2016), and we cannot reject the null of constant wage gains throughout the entire period, with no special increase at the transition to marriage.⁸

The right panel in Figure 1 shows the results from our divorce model. We find a statistically significant decline in wages of 2.2 percent per year in the years leading up to divorce. We cannot reject the null hypothesis that this trajectory is linear over the entire period, and, descriptively, the rate of decline is slower during and following divorce than in the years prior to divorce. Our comparison conventional fixed-effects model estimates a divorce penalty compared to remaining married of 5.0 percent. Our models, however, reveal that divorce appears to be the consequence rather than cause of falling wages.

In the first panel of Figure 2, we separate wage patterns by age at marriage. Table 3 presents numerical results and indicates the significance of hypothesis tests for both within-group wage patterns and between-group differences in these patterns. Men who marry after age 26 (the top third of the distribution) experience no unusual wage gains prior to or during marriage: in other words, wage growth among men who marry after age 26 is entirely explained by the control variables, and we cannot reject the null hypothesis that all the marriage terms are jointly zero. In contrast, men who marry at younger ages experience faster-than-expected wage growth leading up to marriage and through the first several years of their marriages, and we can reject the null hypothesis that all the marriage terms are jointly zero for both of the younger groups. For these men, the years immediately prior to marriage are the late teens and early 20s, a time when we might expect the most rapid wage changes. Men who marry at age 27 or later are more likely to be approaching marriage after their improvements in wages have stabilized and are well-captured by our controls. Descriptively, unexplained premarital wage gains are larger for the younger two groups, but the confidence intervals are wide and the differences are not statically significant. However, we can reject the joint null hypothesis that the three overall trajectories are equal, and specifically that they have equal slopes in the two years surrounding entry into marriage: the rate of wage growth for men marrying later is slower during this period than for the other two groups.

Figure 2.

Heterogeneous wage patterns: Anticipation of marriage or a transition to adulthood?

Note: Models are fixed-effects models analogous to the spline models in Figure 1. The analysis by age at marriage begins at 3 years before marriage because many men who marry at age 22 or younger do not have valid wage observations more years prior to marriage. Models are estimated separately within subgroups defined by terciles of the age at first marriage distribution (left figure) and by whether the marriage was a shotgun marriage, defined as a marriage followed by a first birth within 7 months (right figure). Tests of the significance of differences between slopes are provided in Tables 3 and 4. Full results are available in the online supplement, Table A3.

Table 3.

Heterogeneity in wage trajectories by age at marriage

	(1)	(2)	(3)	(4)
	Marries at age 22 and under	Marries at ages 23–26	Marries at age 27+	H0: (1) = (2) = (3)
A. Pre-marriage slope (−3, −1)	0.044 (0.026)	0.042** (0.015)	0.010 (0.009)	ns
	eβ = 1.045	eβ= 1.043	eβ= 1.011
B. During-marriage slope (−1, 1)	0.059*** (0.017)	0.025* (0.013)	−0.004 (0.009)	**
	eβ= 1.061	eβ= 1.025	eβ= 0.996
H0: (A) = (B)	ns	ns	ns	-
C. Immediate post-marriage slope (1, 5)	0.018 (0.010)	0.010 (0.009)	0.002 (0.006)	ns
	eβ= 1.018	eβ= 1.010	eβ= 1.002
H0: (B) = (C)	**	ns	ns	-
D. Long-term post-marriage slope (5, 10+)	0.010 (0.008)	0.005 (0.009)	−0.000 (0.006)	ns
	eβ= 1.010	eβ= 1.005	eβ= 1.000
H0: (C) = (D)	ns	ns	ns	-
Joint test of linearity	**	*	ns	-
H0: (A) = (B) = (C) = (D)
Joint test of 0 growth	**	*	ns	-
H0: (A) = (B) = (C) = (D) = 0
N	1,545	1,301	1,372

Note: Models are fixed-effects models analogous to the spline models in Figure 1. Models are estimated separately within subgroups defined by terciles of the age at first marriage distribution. Trajectories begin 3 years before marriage because many men who marry at age 22 or younger do not have valid wage observations more years prior to marriage. We can reject the null hypothesis that trajectories are equal across age at marriage groups. Full results are available in the online supplement, Table A3.

These results are consistent with the claim that marriage is associated with wage gains simply because the timing of marriage is correlated with the transition to adulthood. It may also be consistent with delay of marriage until financial thresholds are met, which may especially affect younger men, who have lower average wages.

In the second panel of Figure 2, we test whether the premarital increase in wages is shared by men who enter shotgun marriages, which are likely to be less deliberately timed and anticipated. Table 4 presents numerical results and indicates the significance of hypothesis tests, again making both within- and between-group comparisons. Men entering shotgun marriages experience premarital wage gains similar to other grooms, and we cannot reject the null hypothesis that the two trajectories are equal. The lack of support for causal anticipation is not only due to wide confidence intervals; the point estimates for premarital wage gains are actually greater among men experiencing a shotgun marriage, despite their marriages being less likely to be deliberately timed. Again, the results cast doubt on the claim that premarital wage gains are due to anticipation of entering marriage. Since premarital conceptions may also lead couples to marry under less than ideal financial circumstances, the results also suggest that the premarital increase in wages is not entirely due to men delaying marriage until financial thresholds are met. Instead, premarital wage gains shared by husbands with anticipated and less-anticipated marriages are most consistent with marriage often occurring during the transition to adulthood, when wages are rapidly growing.

Table 4.

Heterogeneity in wage trajectories by shotgun marriage

	(1)	(2)	(3)
	Non-shotgun marriage	Shotgun marriage	H0: (1) = (2)
A. Pre-marriage slope (−5, −1)	0.002 (0.005)	0.023 (0.014)	ns
	eβ= 1.002	eβ= 1.023
B. During-marriage slope (−1, 1)	0.018** (0.007)	−0.009 (0.020)	ns
	eβ= 1.018	eβ= 0.991
H0: (A) = (B)	ns	ns	-
C. Immediate post-marriage slope (1, 5)	0.002 (0.004)	0.013 (0.012)	ns
	eβ= 1.002	eβ= 1.013
H0: (B) = (C)	ns	ns	-
D. Long-term post-marriage slope (5, 10+)	0.001 (0.004)	−0.008 (0.010)	ns
	eβ= 1.001	eβ= 0.992
H0: (C) = (D)	ns	ns	-
Joint test of linearity	ns	ns	-
(A) = (B) = (C) = (D)
Joint test of 0 growth	ns	ns	-
(A) = (B) = (C) = (D) = 0
N	2,761	556

Note: Models are fixed-effects models analogous to the spline models in Figure 1. Models are estimated separately by whether the marriage was a shotgun marriage, defined as a marriage followed by a first birth within 7 months. We cannot reject the null hypothesis that the trajectories are equal by shotgun marriage. Full results are available in the online supplement, Table A3.

Supplementary models

To test the robustness of our results, we estimated a variety of supplementary models. The online supplement describes these models in more detail and shows their results.

Heterogeneous Effects by Subgroup

Even if marriage has no average effect on the wages of men who marry, it might benefit some subgroups of men, including men who did not marry but would have benefited from marriage. We found no statistically significant variation in wage patterns in the years surrounding marriage by race, education, AFQT score groups, wife’s employment status at the start of marriage, or gender role attitudes.

We estimated men’s probability of marriage based on family background, race, AFQT score, health, and marital, employment, and educational expectations in 1979 (for more detail, see the online supplement) and stratified respondents by the predicted probability (see the methodology and discussion in Brand and Xie 2010). We found no evidence of a larger wage premium for men less likely to marry; in fact, those less likely to marry had less favorable wage trajectories in the years surrounding marriage. These results cast doubt on the hypothesis that men who do not marry would benefit if they did, assuming that men with lower probabilities of marriage are more similar to men who never marry than are men with higher likelihoods of marriage.

We also matched married men to similar men observed through age 40 who never married. For each matched pair, we assigned the never-married man the hypothetical age of marriage observed in his matched counterpart. We find that men who married experienced significantly more rapid wage growth between one and five years after marriage than matched men at the same ages who did not marry, which might suggest that men who did not marry would have benefited from marriage. However, they may also have missed or not yet experienced the latent maturation process that spurred both wage growth and marriage for their peers.

Our analyses, therefore, do not lead to firm conclusions about possible wage gains from marriage for the unmarried. We caution that the men in the NLSY79 who did not marry are a subgroup likely to be particularly disadvantaged in the labor force: 31 percent are black, compared to 12 percent in the married sample, 19 percent lack a high school degree at age 25, compared to 12 percent among those who marry, and they average about a decile lower on the AFQT. Our subgroup analyses do not suggest that these traits lead to larger wage gains from marriage. Furthermore, given the distinctiveness of the unmarried group on observed characteristics, they may differ on unobserved traits as well, and we hesitate to speculate about the likely wage outcomes of these men, were they to marry.

Of course, the absence of statistically significant group differences does not rule out the possibility that subgroups may have true differences in wage patterns or that subgroups of men not identified by our analyses may experience a causal marriage premium. Descriptively, we observe somewhat more rapid wage growth throughout the years surrounding marriage (including before marriage) for men with more traditional gender role attitudes, and more rapid wage growth following marriage for men with the highest probabilities of marriage. Future research is needed to further investigate potential heterogeneity in the causal effect of marriage on men’s wages.

Alternative Measures of Anticipation

In 1979 and 1982, respondents were asked questions about whether they expected to marry in a given time frame in the future. We found that men who expected to marry yet did not experienced wage trajectories that were not statistically distinguishable from those who followed through on the marriage. Using a similar approach, we examined the wage trajectories of men who married during this period, stratified by whether they expected it. Here, we find some statistically significant differences in overall wage trajectories, but they are inconsistent in direction and do not occur during the premarital period. We find no statistically significant differences in wage patterns. Sample sizes are small and confidence intervals wide, but, minimally, we find no strong evidence to counteract our conclusions from the main analyses that anticipation of marriage is not driving the premarital increase in wages, since wage gains in the years surrounding marriage are shared regardless of whether marriage was expected, and that being married has no additional effect on wages, since men “left at the altar” experience similar wage outcomes as men who actually marry.

A More Recent Cohort

Using traditional fixed-effects models and data from the National Longitudinal Survey of Youth 1997 cohort (NLSY97) (Bureau of Labor Statistics 2016b), Budig and Lim (2016) find that men born 1980–1984 receive a marriage premium. Furthermore, among those marrying 2004–2010 (the group with the relevant data available), the premium was larger for men in male-breadwinner marriages (husband but not wife employed full-time, full-year) than dual-earner marriages. This finding raises two questions: whether our results are particular to the NLSY79 cohort and whether the marriage premium requires household specialization. We replicated our analyses on the NLSY97 cohort and, as in the NLSY79, found no evidence in favor of a causal marriage premium. Descriptively, as in the NLSY79, wages rise beginning prior to marriage and do not accelerate following marriage, while wages begin to decline prior to divorce. For this cohort, we do find significant variation in wage trajectories across specialization categories. Men with non-employed wives have the fastest wage growth one year before to one year after marriage, but then their wage growth changes significantly to a slight decline in the post-marriage period. This trajectory is the opposite of the prediction one would make based on a specialization argument (full results are available in the online supplement). We caution that the NLSY97 cohort remains young (ages 28–34 in 2013), so conclusions remain tentative and estimates imprecise. Future research is needed to investigate the experiences of the NLSY97 cohort as they age.

Alternative measures of wages and events

We estimated models that (1) imputed in various ways wages for men who were not employed, (2) described wage patterns relative to the start of a first coresidential partnership (either marriage or cohabitation), and (3) did not censor individuals at divorce in the marriage model or at marriage and remarriage in the divorce model. In each case, we found results very similar to those in the main models.

We also examined transitions to second marriages. The estimates are less precise because of the smaller sample size, but, if anything, suggest a drift upward in wages that predates the marriage itself, similar to first marriages.

Conclusion

Recent research on the marriage wage premium has identified that men’s wages begin to grow at accelerated rates at least several years prior to marriage (Cheng 2016, Dougherty 2006), inconsistent with the claim that the marriage premium is driven by household specialization or employer discrimination. However, the premarital increase in wages may be interpreted either as evidence of no causal effect of marriage on wages (Dougherty 2006) or as a real effect of marriage that predates the marriage itself (Cheng 2016). In this paper, we bring together three related but largely independent lines of research in an attempt to adjudicate between these interpretations: the effect of marriage on men’s wages, the economic determinants of marriage, and the transition to adulthood.

We show that divorce penalties estimated by conventional fixed-effects models in fact predate divorce, suggesting that prior evidence of a divorce wage penalty is likely due to failure to account for this reverse causality. Thus, we find no evidence that staying married has a causal wage benefit for men.

Next, we performed two analyses to evaluate whether the premarital run-up in men’s wages is likely to be due to a causal anticipation of marriage, versus either timing marriage to follow wage gains or an unobserved latent maturation process that leads to rapid wage gains around the same time as marriage. We find that men who marry after age 26 do not experience any unusual wage growth in the years surrounding marriage: their wages grow as predicted by other characteristics. By contrast, younger grooms experience more rapid wage gains than expected in the years leading up to and through their entrance into marriage. It is possible that anticipation of marriage acts to “settle down” young men, while by the late 20s men experience this transition in work regardless of marital status. In this case, marriage might shift men’s period of wage growth earlier, while their peers catch up later. Likewise, it is possible that reverse causality only occurs among younger grooms, whose earnings are more likely to be below a normative threshold, while older grooms do not need to wait for wage growth before marriage. However, such an interpretation is difficult to reconcile with the lack of variation in trajectories by other wage-relevant traits, including race, education, and AFQT score. We believe that the observed variation by age at marriage is most consistent with the transition to adulthood argument, which suggests that the spurious association between marriage and rapid wage growth is particularly likely for men marrying in the late teens and early 20s. Men who marry later are more likely to have already experienced that period of rapid wage gain prior to their approach to marriage.

This interpretation is reinforced by our finding that the premarital increase in wages is shared by men who enter shotgun marriages and men whose marriages are not as rapidly followed by a birth. If the period of rapid wage increases before marriage is due to anticipation, we would not expect that men with less anticipated marriages would share fully in these anticipatory effects. Furthermore, we would not expect that men entering shotgun marriages have as much discretion as other men about delaying marriage until financial thresholds are met. Our results thus cast doubt on the explanation that the premarital increase in wages is due to marriage being timed to follow economic improvements.

Of course, our analyses have limitations. Due to sample size, we are limited in our ability to test the effects of rarer transitions (such as to second marriages) and to estimate longer-term trends (such as more than a decade after marriage). When we are unable to reject null hypotheses of linear wage trends through the years surrounding marriage or similar wage patterns between groups, this may be because of low statistical power rather than truly similar patterns between groups. This challenge is heightened in models that allow greater flexibility in the estimated wage patterns surrounding marriage, providing a richer picture but decreasing the precision of estimates. For example, in the pooled marriage model, wage gains are descriptively faster in the year just before and just after marriage, which could be interpreted as a wage premium of about 2 to 3 percent at the time of marriage, although we believe that our later results are less consistent with this interpretation than with a spurious maturation process driving wage gains in the years surrounding marriage.

We recognize that it is impossible to establish causal effects with complete certainty in the absence of random assignment. In a theoretical piece outlining the challenges of causal inference based on fixed-effects estimates of the male marriage premium, Sobel (2012) argues that current panel datasets do not include information on relevant time-varying confounders, such as mental health and substance abuse. Furthermore, for scholars interested in studying the wage effects of an entire marital history, he notes that alternative methods, such as marginal structural models, are needed to account for the fact that marital status follows a dynamic selection process—factors such as occupation and work experience may be predictors of marital status in one period and its outcomes in the next. Rather than attempt to perfectly identify the effect of marriage on wages, we present a set of empirical analyses that provide evidence that is consistent to different degrees with various theoretically informed perspectives on the appropriate interpretation of men’s observed wage trajectories at marriage and divorce.

Our analyses support the argument that men simply tend to marry at times when wages are already increasing particularly rapidly. For each result, it is possible to tell an alternative story of how the observed pattern is consistent with a causal effect of marriage, although that effect may be limited to particular years or particular subgroups. Taking the findings together, however, shows how complicated and limited such a causal story would have to be to be consistent with our results. Because our main focus is questioning whether marriage affects wages, we are less concerned with adjudicating between the reverse causality and transition to adulthood perspectives. We believe that our results favor the transition to adulthood interpretation for marriage and the reverse causality perspective for divorce, but our core claim—that there is no population-average causal effect of anticipating, getting, or staying married on men’s wages—does not depend on which alternative process is at work.

While we find no individual-level effect of marriage on men’s wages, we are unable to evaluate the effect of “marriage culture” on all men’s wages, regardless of whether they personally marry. For example, if wage-earning is normative for husbands, it may also become a more general expectation of adult masculinity, particularly if most men expect to marry and therefore perceive themselves as potential future husbands, regardless of whether they eventually marry. Because 96 percent of the men in our sample expect to marry, we cannot separately identify the effects of marital expectations on men’s wages, or what men’s wages would be if the marriage rate were substantially lower.

Our results have implications for research on the economic determinants of marriage. If wages rise prior to marriage for spurious reasons, positive associations between men’s current economic circumstances and marriage in the next year may be biased just as the wage premium is. Alternatively, if men time marriage in response to changes in financial circumstances, more research is needed to understand which aspects of financial change and achievement, or which financial thresholds, are particularly relevant to enabling marriage, and whether these thresholds vary by subgroup. Although we cannot provide definitive evidence that marriage does not benefit men’s wages, our analyses show that the empirical patterns of men’s wage changes in the years surrounding marriage are entirely consistent with an alternative explanation: men marry during a transition to adulthood when their wages are already improving, and they tend to divorce after their wages are already declining.