Abstract

Previous research examining the impact of unilateral divorce law (UDL) on the prevalence of divorce has provided mixed results. Studies based on cross-sectional cross-country/cross-state survey data have received criticism for disregarding unobserved heterogeneity across countries, as have studies using country-level panel data for failing to account for possible mediating mechanisms at the micro level. We seek to overcome both shortcomings by using individual-level event-history data from 11 European countries (SHARELIFE) and controlling for unobserved heterogeneity over countries and cohorts. We find that UDL in total increased the incidence of marital breakdown by about 20 %. This finding, however, neglects potential selection effects into marriage. Accordingly, the estimated effect of unilateral divorce laws becomes much larger when we control for age at marriage, which is used as indicator for match quality. Moreover, we find that UDL particularly affects marital stability in the presence of children.

Introduction

European countries, like many other developed nations, have faced a persistent increase in divorce rates over the last four decades. The rise in divorce rates has accompanied several changes in divorce law, particularly the introduction of “unilateral divorce law” (UDL), which permits divorce without the consent of both spouses. Whether UDL has increased divorce rates remains disputed (for an overview, see Allen 2002). The empirical evidence so far is based either on cross-sectional survey data or on country-level panel data. Although both methods have their advantages, each also has some drawbacks. Studies based on cross-sectional surveys, which exploit differences in divorce law across states or countries, are not able to account for country/state heterogeneity. On the other hand, studies using country-level panel data fail to account for possible mediating mechanisms at the micro level. The aim of our study is to combine the advantages of both approaches by examining the impact of the introduction of unilateral divorce, using event history data from 11 European countries. This allows us to account for unobserved time trends affecting all European countries, country heterogeneity, and mechanisms at the micro level. Specifically, this article addresses the question of whether the establishment of unilateral divorce has had an impact on the incidence of marital breakdown and whether such an effect, if it exists, has been more direct or more mediated by changing patterns in marriage, female labor force participation, or fertility.

Divorce laws have undergone several changes in Europe over approximately the last century. Historically, the first, and perhaps most significant, change was the introduction of divorce as a legal act, which occurred quite early in most countries. A second major change was the introduction of “no-fault” grounds for divorce. By the middle of the twentieth century, the majority of countries had adopted them; the remainder followed during the second half of the century. No-fault grounds were sometimes intended as additional to fault grounds, but most countries eventually installed them in replacement thereof. Moreover, where fault grounds have been kept, they have been decreasingly used and usually do not affect the question of alimony payments (Goode 1993:32). The third change has been a shift from divorce legislation requiring mutual consent to laws permitting unilateral divorce. Apart from a few outliers, this change mainly took place in the 1970s and early 1980s. Although the shift from mutual-consent to unilateral law is often confused with a shift from fault to no-fault law in the literature (perhaps because of the historical concurrence of their introductions in many legislatures), they are conceptually distinct. Theoretically, the shift to unilateral law is of primary interest here because it affects the assignment of the right to remarry to spouses and thus their relative bargaining power. Whereas the right to remarry is held by the partner with the least interest in divorce under mutual consent law, it is assigned to the partner with the least interest in maintaining the marriage under UDL. Consequently, this specific time-variant characteristic of the legal setting constitutes the key explanatory variable of our analyses.

Theoretical Background and Previous Research

Direct Effects: Bargaining in the Shadow of the Law

One apparent theoretical conclusion regarding the impact of UDL on the incidence of divorce is that it alters marriage from a social relation whose maintenance involves one party to one whose maintenance involves both parties. According to Becker (1981), however, UDL should have no effect on divorce rates. His argument makes use of the Coase theorem, and the question of whether the introduction of UDL might affect divorce rates is thus often seen as concerning its applicability to marital relations. The Coase theorem essentially states that interdependent actors will, under certain conditions, come to efficient (i.e., jointly favorable) outcomes, regardless of the initial allocation of property (Coase 1960).

In Becker’s model, both spouses stay married if they are better off married than separated and possibly remarried. Marriages generate some surplus for the couple, and divorce should occur only if there is no way to make both partners better off within marriage through side payments (Becker et al. 1977; Landes 1978). Becker argued that the introduction of UDL did not affect the marriage surplus. Instead, this reform only reassigned the right to remarry after a separation and hence should not affect divorce rates.

This reasoning, however, applies only if side payments are possible within a marriage and the consent either to maintain or to terminate the relation can be “bought.” The rationale behind this hypothesis is as follows: under mutual-consent law, the spouse who wants to divorce must “bribe” the spouse who wants to stay married in order to convince him/her to agree to the divorce (e.g., by ceding the house, car, and pets to the latter). Under UDL, the spouse wishing to remain in marriage must bribe the spouse who wants to get out (e.g., by increasing his/her own share of household duties).

From the economist’s perspective, the application of the Coase theorem to marital bargaining is, however, questionable. First, information asymmetries with respect to spouses’ divorce opportunities are in conflict with the notion of renegotiation and utility transferability (Peters 1986). Second, the public-good character of marital assets, particularly of children, violates the assumption of well-defined property rights (Allen 2002; Chiappori et al. 2007; Zelder 1993). Because of the joint consumption of public goods, gains to marriage will not be fully transferrable from one spouse to the other. Third, although bargaining costs should be relatively small in marital relations, they may be not negligible, especially in the presence of domestic violence (Stevenson and Wolfers 2006). These transaction costs may therefore impede a redistribution of assets. Information asymmetry and transaction costs arguments are rather general objections, and there is no argument why these assumptions should be particularly violated in marital relationships. Yet, the opposite is true for the public-goods argument. This leads to the testable hypothesis that the divorce regime should, for the most part, affect marital stability in the presence of children.

Indirect Effects

Identifying the direct effect of UDL is thus arguably a test of the applicability of the Coase theorem to bargaining over divorce, but we must also take indirect effects on marital stability into account. Even if the Coase theorem is applicable to existing marriages with given marital investments, one might still find a significant total effect of UDL. Likewise, if it is not applicable, one might find no total effect. This is because UDL could trigger changes in marriage-specific investment behavior, investments in marketable human capital, or spousal selection (with respect to match quality). Unilateral law may lead to an underproduction of marriage-specific capital in favor of higher labor market participation rates, particularly among women, perhaps because of a lack of compensation at divorce for marriage-specific investments (Peters 1986) or a lack of compensation for reduced human capital (Parkman 1992), respectively. Mutual-consent law, in contrast, enforces such compensations in cases when the affected spouse might otherwise withhold his/her consent to divorce. For example, given that female labor force participation (e.g., Booth et al. 1984; Rogers 2004; South 2001) and the absence of children (e.g., Brüderl and Kalter 2001; Lillard and Waite 1993; Wagner and Weiss 2006) have been found to be associated with marital instability, changes in divorce law that affect either or both will also affect divorce rates.

Finally, making divorce less restrictive may affect which people enter into marriage and thus, in the medium run, divorce rates. Whether allowing unilateral divorce leads to an increase or to a decrease in marriage rates, however, remains an open question. Rasul (2005) argued that gains from marriage are reduced under unilateral divorce regimes because the provision of insurance and risk sharing in marriage declines. In consequence, reduced gains from specialization in home and market production will result in a decline of marriage rates. According to his findings, the observed decrease in U.S. marriage rates can to some extent be attributed to the introduction of UDL. If individuals are willing to enter only marriages of potentially higher quality, match quality within the married population will rise after the introduction of unilateral divorce. Alesina and Giuliano (2007), on the other hand, concluded that UDL raises marriage rates. Their explanation is that reduced exit costs facilitate rash marriages. Hence, unilateral divorce laws could likewise lead to a lower average match quality.

State of Research

Previous research on the effect of unilateral law on divorce has led to somewhat mixed results (Allen 2002; Friedberg 1998; Gallagher 1973; Goddard 1972; González and Viitanen 2009; Kneip and Bauer 2009; Marvell 1989; Nakonezny et al. 1995; Peters 1986; Schoen et al. 1975; Wolfers 2006; Wright and Stetson 1978). Moreover, because of the varying empirical approaches employed, findings are hardly cumulative. One of the first studies using advanced statistical modeling and large data sets was that of Peters (1986). Using U.S. micro data from a special 1979 Current Population Survey (CPS), Peters found no effect of unilateral law on divorce probabilities. On the other hand, Allen (1992), using the same data as Peters, detected an impact. Friedberg (1998) traced this discrepancy to the fact that the studies differed in whether they considered controls for geographic differences in divorce propensities. Friedberg therefore proposed a model exploiting state-level panel data to control for state and year fixed effects, as well as for state-specific time trends. Her model thus controlled for various sources of state heterogeneity, without being specific about them, and revealed an effect of UDL on divorce. Wolfers (2006) introduced an extension to Friedberg’s model by accounting for the potential dynamics of a policy shock and found no long-run effect for the United States. However, applying Wolfers’ model, Kneip and Bauer (2009), as well as González and Viitanen (2009), found a sustainable effect in Europe. These differences in results between Europe and the United States could be to the result of differences in the processes of deciding whether to marry (and hence average match quality) and how these processes responded to changes in divorce laws. For the United States, there is a mixed picture of whether UDLs have improved match quality (Alesina and Giuliano 2007; Rasul 2005).

Our article adds to this literature in several ways. First, because we know whether the couple got married under mutual consent or unilateral divorce law, we can assess the importance of the composition of the pool of married couples with regard to match quality for the estimated effect on divorce. If UDL has an effect only on couples who were surprised by the introduction of UDL, we would expect that after a while, there are no apparent effects of this reform anymore. In a similar vein, we can assess whether UDL has affected the search behavior by investigating whether age at first marriage has stayed constant. This is related to whether and how match quality has changed, and we provide the first evidence for this for Europe. In addition, we also present evidence for the effect of UDL on labor force participation and fertility, which are potentially important mediators of a UDL effect. Using microdata also allows a more thorough investigation of the applicability of the Coase theorem. For instance, we expect that in the presence of public goods, such as children, the UDL effect will be stronger.

Method

Data

We used data from the SHARELIFE study, which was part of the Survey of Health, Ageing and Retirement in Europe (SHARE) conducted in 13 European countries between October 2008 and September 2009.1 The study’s main objective was to gather retrospective biographic information as a supplement to the regular panel waves. Using these data has several advantages but also disadvantages. A sample of European countries, for instance, will unfortunately likely be less homogeneous than U.S. federal states. This “disadvantage” is at the same time a significant advantage, though: in Europe, one cannot easily flee an initially responsible jurisdiction through migration, so there is less concern than in the United States that those seeking divorce may take residence in jurisdictions with more favorable divorce laws. Still, in order to avoid too much cultural heterogeneity in the sample of countries considered, we excluded the former communist countries Poland and the Czech Republic, leaving 11 countries in our analytic sample. For the same reason, we also omitted persons who had lived in the German Democratic Republic (GDR) prior to 1989 from the German sample.

Despite these concerns, and although not primarily designed to study divorce, these data seemed particularly appropriate for our research question for several reasons. First, they contain the necessary biographic information on marriages, births, job episodes, and separations over the course of life. Second, the cross-national design provides a variation in the timing of divorce law changes necessary to isolate the effect of UDL. Third, with a target population of people aged 50 or older, the cohort structure of the sample leads to a favorable distribution of respondents under applicable divorce laws during the course of marriage. We observed a substantial share of marriages that started under mutual consent law and experienced no shifts as long as they lasted (16.62 %), marriages that outlasted the shift to a UDL (60.27 %), as well as marriages that started under unilateral law (23.11 %). The variation in distributions across countries is in Table 1, together with the year unilateral divorce was enacted.

Analytic Strategy

With respect to marital breakdown, marriage, and fertility as dependent variables, we apply and estimate Cox duration models of the following form:
formula

where α gives the effect of the introduction of unilateral divorce (uni =1).2 We control for country fixed effects (c), cohort fixed effects (b), as well as linear (l) and quadratic (l2) country-specific cohort trends.3 This eliminates unobserved heterogeneity in divorce (marriage, childbearing) propensities across countries and cohorts from the model without being specific about the driving factors. These may include different levels or trends in, for example, wealth, education, religiosity, marriage market opportunities, or any other factors that may affect the outcome of interest. Essentially, the model fits country-specific/cohort-specific trends in a transition risk and assesses whether a significant discontinuity in the trend occurred at the time when unilateral law was enacted. With respect to female labor force participation as the dependent variable, we run a two-period fixed-effects ordinary least squares (OLS) regression model, taking into account the periods shortly before and after marriage and considering the same controls as in the Cox duration models. Without further controls, we obtain the total UDL effect. We are, however, also interested in determining the direct effect in order to assess the applicability of the Coase theorem. To do so, we include possible individual-level mediators xi (age at marriage, labor force status, and presence of children) in the model that might otherwise be partly absorbed by the unilateral law effect.

Measures

Our main dependent variable is duration of marriage until marital breakdown. We consider separation rather than divorce because uncontrolled features of the processes of family law (e.g., the mere duration of court and administrative proceedings) affect the time lag between separation and actual divorce.

The main independent variable—unilateral law—is a time-variant variable, with a value of 0 prior to the date of de facto unilateral divorce’s introduction in a given country, and a value of 1 thereafter. We apply the same coding of this variable as that which Kneip and Bauer (2009) employed, focusing on de facto unilateral divorce regimes. Such a regime is defined as one in which it is possible to file for divorce without the consent of one’s spouse or invoking fault. However, a spouse’s wish to divorce does not need to be sufficient to obtain divorce. Instead, it will typically be granted by judicial verdict based on the grounds of irretrievable breakdown if certain requirements are fulfilled. Regimes are coded as de facto unilateral if the period of separation required to get divorced is one year or less. To date the introduction of de facto UDL, we use the date of coming into effect of the respective law.4

“Age at first marriage” gives the age of the respondent when entering his/her first marriage (centered on the mean over all countries). It serves as an indicator of match quality because persons who marry at relatively young ages spend less time searching for a partner in order to obtain optimal matches and are thus more likely to accept less advantageous marriages. They are less informed about themselves, their mates, and the marriage market, all of which increase the probability of a mismatch (Becker et al. 1977; Oppenheimer 1988). Empirically, age at marriage has been widely used as an indicator for match quality and has been found to be one of the strongest predictors of marital stability (Brüderl and Kalter 2001; White 1990). By using this indicator, we are necessarily restricted to analyzing first marriages.

“Employment” is a time-variant categorical variable capturing the respondent’s employment status as full-time employed, part-time employed, or not employed, where the last serves as a reference category. We interpret (female) labor force participation as an indicator of investment in individual bargaining power resulting from increased outside options. When employment is used as a dependent variable, it gives the average workload over the three consecutive years before and following marriage, respectively; full-time is coded as 1, part-time is coded as 0.5, and not employed is coded as 0 in every year. The resulting variable thus ranges from 0 to 1, with a mean of 0.69.

“Common child(ren)” is a time-variant variable that takes the value 0 before the first common child is born and switches to 1 after the birth of the first common child. We interpret the existence of common children as an indicator of marriage-specific investments.

“Family intact when 10” is a dummy variable indicating whether the respondent, at age 10, was living with both his/her parents (1) or not (0). This variable serves as a control for the stability of the parents’ marriage, which is known to affect divorce propensities of offspring (Diekmann and Engelhardt 1999; Wagner and Weiss 2006).

“Female” takes the value 1 if the respondent is female and 0 if he is male. This variable serves as a mere control variable and is, for example, necessary to interpret the age-of-marriage effect, given the average difference in this trait between men and women. However, it can also be interpreted substantively in interaction with labor force participation.

Results

The structure of the results section is as follows. We start by focusing on the model selection with respect to the parameterization of country-specific trends and report the total effect of UDL on the risk of marital breakdown. We would expect this to mirror previous findings (particularly Kneip and Bauer 2009) based on country-level analyses. Next, we strive to identify the direct effect of UDL by controlling age at marriage, female labor force participation, the presence of children as indicators for selection into marriage, investments in marketable capital, and marriage-specific investment behavior, respectively. For each of these potential mediators, we look at how UDL influences them as well as how their inclusion in the model affects the UDL effect on marital stability. We conclude this section with a detailed note on conducted robustness checks.

Model Setup and Total Effects

Table 2 shows the effects of the introduction of unilateral divorce laws on the risk of marital breakdown for different specifications of country-specific cohort trends. Specification 1 includes only country and cohort fixed effects but no trends. Models 2–4 consecutively introduce linear, quadratic, and cubic trends. The UDL effect is strikingly robust with respect to the different model specifications. This demonstrates that our estimates are not mere artifacts of the selected trend parameterization, which is about 19 % in magnitude and significant at the 10 % level using clustered standard errors (N = 11 countries). For further analyses, we use specification 3, including linear and quadratic trends, because it fits the data best. Further, including a cubic trend does not significantly improve the model’s explanatory power.

Besides demonstrating the robustness of our model with respect to trend specification, Table 2 also yields our first substantive result. Based on the selected model specification, the unilateral law coefficient can be interpreted as the total effect on the risk of marital breakdown. Thus, the divorce rate has risen by about 20 % because of the introduction of UDL when country and cohort differences are accounted for. The preceding analysis mirrors what can be done with country-level data. It is noteworthy that our estimation is quite consistent with the findings from Kneip and Bauer (2009), who also attributed about 20 % of the rise in divorce rates between 1960 and 2003 to the introduction of UDL. This is the starting point for the following analyses in which we try to decompose the resultant total effect according to possible mediating pathways.

Selection Into Marriage

The first intervening mechanism we consider is a change in individuals’ entering into marriage. Specifically, we investigate whether the introduction of UDL has affected individuals’ chances and timing in marriage and whether controlling for age at marriage alters the estimated UDL effect. Table 3 reports effects on the transition to first marriage (panel a) as well as on marital disruption when controlling for age at marriage (panels b and c). All models account for country differences and cohort trends as specified earlier. We look at the transition to first marriage in two ways: (1) how the introduction of UDL affects the chance of marrying; and (2) how the timing of marriage shifts for those who do marry. As the Cox model in the first column reveals, the chance of getting married is reduced by about 40 % under unilateral law. Given the proportional hazard constraint of the model, this reduction can be interpreted as an average effect and does not reflect potential shifts in the timing of marriage. The latter is addressed in the log-logistic model, which shows that for those who did marry, the age at which they did so increased by about 8 %. Thus, for example, if the average age at first marriage had been 25 years before the introduction of UDL, about eight months of the subsequent increase in age at marriage could be attributable to the change in divorce laws.

Panels b and c look at how age at first marriage may have mediated the effect of unilateral law on marital instability. Results in panel b show that a higher age at marriage reduces divorce risks by roughly 4 % per year delay. More interestingly, the UDL effect rises to about 1.4 and is now significant at the 1 % level. However, the apparent doubling of the effect size (as compared with Table 2, specification 3) may not be interpreted as mediator effect given that we would expect a mediation only in the case of persons not married prior to the divorce law transition. Panel c thus reports separate UDL coefficients for persons married versus unmarried at the time unilateral divorce was established. As can be seen in the basic model, the estimated effect for those who married only under unilateral law is virtually 0. Adding age at marriage to the model raises the hazard ratio to 1.56, which is now significant. Surprisingly, the unilateral coefficient for the previously married also rises, perhaps hinting that age at marriage also captures some other confounding factors. However, comparing coefficients across nested nonlinear models is not directly feasible (Winship and Mare 1984). Assessing the actual change in coefficients based on the (“KHB”) method proposed by Karlson et al. (2012) reveals that there is a significant mediation only for those who married under UDL.5 Respective coefficients and test statistics are given in Table 6 in the appendix.

Taking these findings together, we can state that a change in age at first marriage suppresses the divorce law effect. UDL has triggered a postponement of first marriages that we interpret as an indicator for match quality. The resulting gradual quality shift in the sample of married couples compensated for part of the effect that divorce law changes would have had if age at first marriage had remained constant. The estimated UDL effect then always reflects the ratio of couples married before versus after the law transition. Flexible trends at the country level do not seem to account sufficiently for this process, and the actual (direct) impact of unilateral law is strongly underestimated.

Female Labor Force Participation

We have argued that a switch to unilateral divorce laws might affect investments in marketable human capital vis-à-vis marriage-specific assets. The next analyses scrutinize how female labor force participation could possibly mediate the effect of UDL on the rate of marital disruption. Again, we first examine how unilateral law affects female labor force participation.

The models shown in panel a of Table 4 compare individuals with the same marital status within countries and cohorts in which marriage is entered under either mutual consent or unilateral law. For this, we used OLS regression, pooling the two periods shortly before and after marriage, in which each period comprises workload averaged over three consecutive years. As the dependent variable is normalized, coefficients can be interpreted in percentages of full-time work equivalence. The basic model shows that UDL has no significant effect on overall labor supply. This is not surprising given that a general extension or reduction of labor demand should be captured by the controls in the model. However, as revealed by the interaction in column 2, this is attributable to different effects on men and women that cancel each other out. In fact, we observe that relative female labor force participation increased in response to unilateral divorce laws. Further, as shown in column 3, this change occurs not only after marriage but also and mainly prior to it. According to our findings, the typical reduction of female labor supply subsequent to marriage has somewhat diminished under unilateral law, but the triple interaction is not significant. Given that labor supply largely depends on educational decisions made prior to marriage, this is what one would expect to find. Women who have completed their educational career, married under mutual consent law, and engaged in housekeeping and childcare duties might want to increase their labor supply after a transition to unilateral law but may simply be inhibited by their low human-capital endowment.

The reported effects are also illustrated in Fig. 1, where men’s and women’s average workload shortly before and after marriage is depicted relative to the workload of unmarried men under mutual consent law. Again, these effects are net of country-specific trends in labor force participation. Moreover, by including age at marriage in the labor force models, we effectively control for period effects as well. The analysis replicates three well-known findings: (1) the men’s average workload is higher than women’s; (2) men increase their workload after marriage; and (3) women reduce labor force participation, which is a pattern reflecting the gendered division of labor (for an overview, see Baxter et al. 2008; Shelton and John 1996; South and Spitze 1994). The figure also shows that the relative workload of women as compared with men has strongly converged under UDL. In effect, the increased female labor force participation triggered by unilateral law offsets the still persisting effect of a gendered division of labor within marriage. As a result, gender differences in labor market participation are reduced for couples married under unilateral law.

Panel b of Table 4 shows how female labor force participation affects marital stability and to what extent it mediates the unilateral law effect. First, the analysis confirms well-known results from previous research: full-time employment of women raises divorce propensities, as does part-time employment of men. When we account for labor force participation, the UDL coefficient reduces slightly to about 1.18 (as compared with 1.19 in Table 2, spec. 3). Although the effect is no longer significant, with respect to point estimates, the reduction is only of small size. Similarly, when we include age at marriage in the model, there is hardly any difference (compared with the estimated effect from Table 3, panel b). Applying the KHB method confirms that there is no significant mediation by labor force participation (see Table 6). Put another way, excluding female labor force participation from the model hardly alters the estimated effect of unilateral law when we account for country and cohort differences as well as the process of opting into marriage.

Common Children

The next analyses consider common children as a factor possibly mediating or even moderating the effect of unilateral divorce on divorce propensities. Panel a of Table 5 shows how the introduction of UDL has affected the transition to parenthood. According to the basic model, it reduces the frequency of having a first child by about 20 %. The negative UDL effect on fertility disappears, however, when we take age at marriage into account. A higher age at marriage is not only an indicator of match quality but also reflects the reduced time available for begetting children. A plausible interpretation of this finding may therefore be that unilateral law has reduced the chances of entering parenthood by reducing fertile time in marriage.6

With respect to marital stability, panel b of Table 5 reveals a pattern quite similar to our findings for the effect of female labor force participation. The presence of children reduces the risk of marital breakdown by about 40 %. Including this variable in the model leads to a reduction of the UDL effect to about 1.15, which is no longer significant. When we include age at first marriage, the estimated effect is 1.4, which is essentially the same as the effect when we remove children from the model. Again, applying the KHB method confirms that there is no significant mediation by having children (see Table 6).

The third column from Table 5, panel b displays the test of the hypothesis that unilateral law particularly affects marital stability in the presence of children because they constitute a public good and this constrains the possibility of side payments. As the interaction effect reveals, we can confirm this hypothesis. As long as no children are present, the UDL effect reduces to about 16 % and is no longer significant. A possible explanation is that Coasian bargaining is more likely when few public goods, children, are involved. Yet, it also follows that children lose part of their stabilizing effect on marriage when unilateral divorce laws are installed. Finally, the last model from panel b of Table 5 simultaneously addresses the mediating effects of common children and female labor force participation. The interaction effect between unilateral law and common children is not included in the final model in order to estimate the average effect of UDL on couples’ divorce risks, irrespective of parenthood. We find that the effect of common children does not change substantially after we control for the mediation of UDL by female labor force participation. Likewise, effects of labor force participation (compared with panel b of Table 4, column 2) are only a bit weaker when the model accounts for common children.7

Robustness of Findings

Robustness of findings is always a critical issue, especially when the statistical models applied include control terms for unspecified sources of heterogeneity (Lee and Solon 2011), or when there is a possible selection bias in the analytic sample. We therefore ran a number of robustness checks to ensure that our findings are not mere coincidence. The first, and perhaps most crucial, which we present at the beginning of the empirical section, concerns the model’s calibration with respect to the inclusion of control trends. Although we based the ex ante decision regarding the highest polynomial degree included on baseline model fit, we also replicated the full models with respect to all dependent variables (final column in Table 5, panel b) including either linear trends only or up to a cubic trend. All models appear to be very robust. As in the baseline models, the estimated UDL effects hardly differ at all (see Fig. 2).

A related, additional check was the inclusion of period effects in addition to cohort trends. We did this because our model assumes that the cohort effects capture all unobserved heterogeneity in divorce propensity over time. However, allowing for country-specific period trends does not alter the UDL coefficient significantly. Figure 2 reports the unilateral law effect when we use a linear specification of the period trend. Adding polynomials of a higher degree does not significantly improve the model.

Our second set of robustness checks involved including lags and leads. If including leads had affected the results, this could have hinted at the law transition being endogenous with respect to the dependent variable (“endogenous legislation”) and thus to biased estimates. However, introducing leads into the model had no significant impact (χ2(5) = 4.77), and the coefficient for unilateral law remained stable and significant. Taking these findings together, we would argue that our results are reasonably robust regarding model calibration. We also checked the effect of including lags on our estimation, mainly because of the problem of pinpointing the actual switch to de facto unilateral divorce. Although we consider the date a de facto unilateral law was enacted, the transition in reality sometimes involved a gradual change in standards set by the courts (by means of statutory interpretation). One could thus expect a swelling UDL effect until the new standards became fully operative. In fact, this pattern is apparent when lags are introduced into the model. Overall, however, including lags similarly has no significant impact (χ2(5) = 6.51), and the estimate for the sustainable UDL effect does not significantly differ from our original estimate.

Another robustness check was necessary due to the manner of sampling in SHARELIFE. Respondents consisted of target persons aged 50 years or older and their current spouses regardless of age. Thus, our analytic sample contains spouses who may, or who may not, be in their first marriage. Although these “double counts” of marriages do not generate a problem of deflated standard errors when one uses clustered standard errors, it may lead to some bias. However, the direction of this bias is not clear ex ante. On one hand, the sample may be biased toward persons with a reduced divorce risk (due to persistent first marriage); on the other, it may be biased toward divorced persons (due to higher-order marriages). To eliminate double counts, we reran the full model on divorce with a sample of females only. Again, results are only slightly different. The UDL effect rose by 5 percentage points to 1.45, indicating that the overall sample may be only slightly biased toward lower-risk persons.

Because our analyses are based on retrospective life history information from elderly respondents, recall bias is an issue we must address, although Garrouste and Paccagnella (2011) found that the possible recall bias in the data employed was only modest. We used an interviewer rating on the perceived reliability of answers to eliminate those respondents who seemed almost never to understand the questions correctly (N = 318). We found that recall bias seems to be of no great importance in this case given that all coefficients remain quite stable.

We also must discuss the calculation method of the reported standard errors. Because the regressor of interest—“unilateral”—is measured only at the country level, there are good a priori reasons to cluster standard errors on the country level. However, given that there are only 11 countries in our analytic sample, we may run into problems resulting from the low number of clusters because the resulting standard errors may be biased downward. We address this problem by calculating standard errors assuming no clustering with and without heteroskedasticity and then comparing the standard errors to choose the most conservative ones. By doing so, we use a guideline similar to the one Angrist and Pischke (2009) suggested when choosing among standard errors under the assumption of homoskedasticity with heteroskedasticity-robust standard errors; they found that this approach worked well in their simulations. In our application, clustered standard errors are always the largest, and therefore we stick with them.

We have argued in favor of using separation rather than divorce as an outcome variable. It nevertheless seems reasonable to cross-check our findings by looking at divorce. Because unilateral separation was also possible under mutual-consent law, we might have generated downward-biased estimates when looking at separation. As shown in Fig. 2, replacing separation with divorce does not alter the previous finding significantly. The point estimate is even slightly lower for divorce.

A further issue to address is that we used a linear specification of age at marriage to capture match quality, although the theoretical link could be U-shaped because individuals (especially women) might settle for poorer matches as they hear their biological clock ticking. Actually, Becker et al. (1977) and, more recently, Lehrer (2008) found support for a nonlinearity. When including a quadratic term in the model, we can replicate that finding. For simplicity, we use the linear term because this issue is not crucial to the argument and, as shown in Fig. 2, does not affect the unilateral law estimate.

A potential problem might arise from using age at marriage as an indicator for the length of the search phase: couples might in fact have ended the search phase much earlier, when they started the relationship. The effect of age at marriage thus confounds the effects of searching and relationship duration. However, both are expected to be related to higher match quality (Brüderl and Kalter 2001). Because we are not primarily interested in disentangling the two different channels, age at marriage is still likely to be an appropriate indicator for match quality. To make sure, we ran a model substituting age at relationship formation for age at marriage and, consequently, left-truncating at the time of entering the population at risk. As depicted in Fig. 2, this does not affect the UDL estimator. Additionally, controlling for relationship duration (not shown) yields the expected negative effect, but neither the UDL effect nor the effect of age at union formation is affected.

Throughout this article, our focus has been on de facto unilateral divorce. However, we were also able to assess the effect of introducing de jure law (i.e., a legal claim to divorce upon unilateral filing) and to see whether we could replicate the aggregate finding that it has had no additional long-term effect (Kneip and Bauer 2009). Again, the de facto effect is completely unaffected by including de jure law into the model. As for the de jure effect, we indeed cannot reject the hypothesis of a null effect, suggesting that there is no sustainable direct effect of de jure over de facto unilateral law (see Fig. 2).

A final aspect concerns the sensitivity of our findings with respect to the countries included in the sample and thus the degree to which our findings are generalizable. We tested this through case-by-case omission of countries from the analytic sample. We found that the UDL coefficients are fairly stable, ranging from 1.32 to 1.47 and always remaining significant (see Fig. 3). We also replicated the analysis including Poland, the Czech Republic, and the respondents from the former GDR, which we have argued to be a possibly inappropriate comparison group. However, the estimated UDL effect on divorce is only little affected (1.34). Likewise, analyses on marriage, labor force participation, and transition to parenthood yield very similar results. Overall, our findings are fairly robust with regard to country selection.

Conclusion

This article has scrutinized the effects of the presence of unilateral divorce law on the incidence of marital breakdown and possible mediating mechanisms. We find that UDL increases the divorce risk by 20 %. This is in line with previous findings for Europe (González and Viitanen 2009; Kneip and Bauer 2009). However, unilateral divorce is also associated with an increased age at marriage, raising the average match quality for married couples. Taking this into account reveals a stronger and significant direct effect of UDL on divorce, which is also robust against various model specifications. Neglecting this mediating pathway thus leads to biased estimates. Our main finding is that the UDL effect is overshadowed by the fact that the married population changes over time in response to the legal transition. Thus, the overall impact of unilateral law on divorce rates also diminishes over time. Analyses based on country-level/state-level aggregate data cannot disentangle these processes, but because the risk pool of the married population has improved over time, it should be harder to detect a significant total effect of unilateral divorce law. Our findings imply that the estimated UDL effect becomes smaller as the fraction of couples that have married after the UDL transition becomes larger. Likewise, effect size will diminish over time as unilaterally married couples are gradually replacing those married under mutual consent law (Kneip and Bauer 2009). Although this holds for Europe, future research will need to address whether the same mechanism also applies to the United States and whether the suppressor effect is of comparable size.

Our results yield less support for the notion that UDLs affect divorce rates through their effect on marital investments. We find that UDL stimulated increased female labor force participation. This applies not only to reducing labor supply to a lesser extent subsequent to marriage but also to increased labor force participation prior to marriage. Although female labor force participation is affected by the introduction of unilateral divorce law and is also found to increase the risk of divorce, its mediating effect is rather small and insignificant. With respect to investments in children, we find no direct UDL effect and thus no mediation of the effect on marital stability. However, children are found to moderate the unilateral law effect. A possible explanation is that children constitute public goods within marriage that impede full utility transferability and thereby Coasian bargaining. Again, it is an open question whether the mediating role of investment behavior is similar in the United States or other societies.

How do our findings contribute to an assessment of the impact of the transition to UDL on spousal welfare and child development? Our results suggest a positive sorting into marriage that results in higher-quality matches. In addition, evidence from previous research suggests that the introduction of unilateral law has reduced domestic violence (Stevenson and Wolfers 2006). On the other hand, we find that more couples postpone marriage or do not get married at all. To the extent that marriages provide additional benefits to couples, this results in welfare losses. At the same time, the risk of divorce has increased after the unilateral law transition. If separation costs are higher among married couples, this also leads to welfare losses under the new divorce regime. The net effect is not clear, however, and we are thus unable to draw any conclusion about the total effect on the welfare of the adult population.

With respect to child development, there are also counterbalancing effects. Experiencing divorce has been shown to be unfavorable for children (Amato 2001; Amato and Keith 1991). Because unilateral law has increased the risk of marital breakdown, particularly in the presence of children, the likelihood of children experiencing parental divorce has increased under the new law. Moreover, match quality has risen in reaction to UDL. Thus, children will more often experience the benefits of high-quality marriages (including the reduced incidence of domestic violence) but will also more often be affected by divorce in relatively intact marriages. Whereas children’s well-being might even increase following divorce at levels of high parental conflict, they suffer particularly when marital quality was rather high (Amato et al. 1995). Previous research has also shown that the introduction of unilateral law has had adverse long-term effects on children by changing intrafamily bargaining in intact marriages (Gruber 2004; Reinhold et al. 2013). Additionally, children raised out of wedlock have to be taken into account, and there is evidence that their share is increasing while the stability of their parents’ unions is decreasing (Bumpass and Lu 2000; Raley 2001).

Although unilateral law itself is not at stake in Europe, our findings bear some clear relevance to policy. The introduction of unilateral divorce has had some demonstrably negative effects that were unintended by its originators.

Acknowledgments

This article uses data from SHARELIFE release 1, as of November 24, 2010; or SHARE release 2.5.0, as of May 24, 2011. The SHARE data collection has been primarily funded by the European Commission through the fifth framework program (project QLK6-CT-2001-00360 in the thematic program Quality of Life), through the sixth framework program (projects SHARE-I3, RII-CT- 2006-062193, COMPARE, CIT5-CT-2005-028857, and SHARELIFE, CIT4-CT-2006-028812), and through the seventh framework program (SHARE-PREP, 211909 and SHARE-LEAP, 227822). Additional funding from the U.S. National Institute on Aging (U01 AG09740-13S2, P01 AG005842, P01 AG08291, P30 AG12815, Y1-AG-4553-01 and OGHA 04-064, IAG BSR06-11, R21 AG025169), as well as from various national sources, is gratefully acknowledged (see http://www.share-project.org for a full list of funding institutions). We thank Henning Best, Martina Brandt, Josef Brüderl, Tabea Bucher-Koenen, Andrew Cherlin, and Stefania Marcassa for valuable comments.

Appendix

Notes

1

For details on the SHARE data, see Börsch-Supan et al. (2013). Methodological issues of the SHARELIFE survey are addressed in Schröder (2011).

2

The analytic sample is restricted to respondents aged 50–90 with nonmissing information on all covariates. Time at risk is defined from marriage to divorce or censoring (interview, widowhood), from age 16 to first marriage or censoring, or from marriage to first child born in wedlock or censoring (interview, divorce, or death), respectively.

3

Technically, fixed effects enter into the model as country and cohort dummy variables, where cohorts are defined by year of birth. Country-specific trends are modeled as interaction terms of country dummy variables × cohort (linear) and country dummy variables × cohort (quadratic), respectively. This specification implies that countries never observed to change their divorce regime contribute to the estimation by affecting the specification of cohort effects.

4

For a detailed discussion on unilateral divorce in Europe, also see the results of an extensive expert survey among European family law researchers in Boele-Woelki et al. (2003, 2004) as well as the national reports of the European expert group on family law available online (http://www.ceflonline.net). The divorce law coding of Kneip and Bauer (2009) and González and Viitanen (2009) relies on these sources.

5

Mediator effects are obtained using the khb.ado Stata command, as described in Kohler et al. (2011). Because the KHB method cannot be used with Cox regression, we instead ran discrete-time models, which are technically logit models. The (generalized form of the) sickle function, which has been shown to be appropriate in the case of divorce (cf. Diekmann and Mitter 1983, 1984), was chosen as parameterization of the hazard rate. Obtained estimates are virtually identical to those from Cox regression (i.e., coefficients usually do not differ to the second decimal place).

6

We have focused on the transition to parenthood, which is likely to be the most crucial investment decision. Analyses on higher-order transitions (not shown) reveal that the negative UDL effect becomes even stronger with increasing parity. Moreover, transition rates to a second and third child decrease significantly under UDL even when we control for age at marriage.

7

Estimates of the UDL effect remain stable over all models from panel b when number of children is included as a measure of specific capital. The interaction effect of UDL and children slightly rises with increasing parity, with a pronounced jump in the presence of one child.

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