Table 3 presents ordinary least squares (OLS) estimates of the DD coefficients (η
). Standard errors (in parentheses) are corrected for heteroskedasticity and nonindependence of residuals across fathers’ earnings observed at different points in time, using the “robust cluster (.)” option in Stata. Year and age fixed effects, as well as relevant control variables for parents and child, are included in the model.
The table reveals a stepwise pattern in incremental effects on log earnings for treated fathers consistent with the shading in Fig. 2. In particular, the DD coefficients of children born after 1994 (treated children) are significant and negative in all years and for all ages of the child. The DD coefficients for fathers of children born in 1993 or 1994 (treated during phase-in period) are negative but are small and are significant only when the child is aged 1–3, which corresponds well with the phase-in period of the uptake documented in Fig. 1. Apart from 2-year-olds in 1994, the DD coefficients are small and not significantly different from zero for children born prior to 1993. This finding is consistent with our identifying assumption that time trends in earnings are similar for fathers of children of various ages absent the reform.
In Fig. 3, we present the estimated treatment effects from Table 3 graphically. The figure plots the treatment effects on earnings (vertical axis) for different age levels. The horizontal axis denotes the child cohort. For the fully treated cohorts (from 1995), we can see negative effects for all ages. Moreover, for the nontreated cohorts (prior to 1992), no systematic effects seem to be present.
As noted earlier, 95 % of all fathers who exercised their right to paternity leave took leave in conjunction with the mothers’ leave during the child’s first year of life—that is, either during the year the baby was born or the year the baby turned 1 year old. As such, the estimated treatment effect on fathers of 1-year-olds (first row in Table 3) can be partly explained by less than 100 % earnings compensation when being on leave.Footnote 11 The focus in this article is the estimated treatment effects on fathers of children older than age 1 (second through sixth row in Table 3), which reflects treatment effects of the paternity-leave quota on future earnings. We can see that for a father of a given cohort, the treatment effect decreases somewhat as the child becomes older—that is, diagonally in the matrix—but is still significant when the child is 5 years old. Larger incremental earnings drop for fathers of younger cohorts can be explained largely by the increase in uptake of the reform. Adjusting for this, the earnings drop remains fairly stable across cohorts.
The validity of our identifying assumption is supported by the fact that we do not observe significant DD effects on earnings prior to the reform in Table 3. However, this matrix provides limited evidence on pre-reform trends because it includes only a few pre-reform cohorts. In Table 4, we extend the analysis six years back in time. The structure of the regression we run in Table 4 is identical to Table 3, with some few exceptions because of data limitations: for the period 1986–1991, we have only earnings data and therefore cannot include any control variables in the regression. Moreover, instead of restricting the sample to fathers working full-time, we restrict the sample to fathers with earnings above a certain threshold, below which full-time employment can be ruled out. This threshold is defined as four times the annually adjusted basic amount in the Norwegian pension system (which is equivalent to NOK 337,000 and $58,000 in 2013).
Table 4 shows that time trends in earnings for fathers of children of various ages were similar until the introduction of the paternity-leave quota, supporting the validity of our identifying assumption. The stepwise pattern in earnings effects for the treated and those treated in the phase-in period is similar as in Table 3. The effects are somewhat smaller (and insignificant for the 1995 cohort) in Table 4, likely because we are unable to restrict the sample to fathers who are the most likely to be eligible for the paternity-leave quota when we observe only earnings.
Specifically, a concern with our empirical strategy is that our estimate may be biased by several extensions in the parental leave legislation during our period of study, as discussed earlier. In particular, general parental leave increased by three weeks in 1993, in addition to the four weeks designated to the father (see Fig. 2). Table 4 provides no evidence that fathers are responding to the gradual extensions from 18 to 35 weeks of parental leave prior to 1993. If fathers responded, we should have seen significant estimates for some cohorts born prior to 1993 in Table 4. In contrast, time trends in earnings are similar for fathers of these cohorts. Moreover, the general parental-leave extensions prior to the introduction of the paternity-leave quota also did not have a negative short-term effect on father’s earnings: none of the estimates for 1-year-olds in the period 1987–1992 are negative and significant. We conclude that our estimates do not seem to be biased by the general parental leave extensions. In particular, a response to the 1993 extension in general leave rights seems unlikely because fathers’ earnings have not been affected by general extensions in parental leave rights prior to 1993.
Earlier we noted that the introduction of a cash-for-care subsidy in 1998 had a substantial impact on mothers’ but no effect on fathers’ labor supply. Consistent with Drange (2012), Table 4 suggests that the cash-for-care subsidy had no effect on fathers’ labor force participation. If the subsidy had an effect, we would expect to see a change in the DD coefficients for the fathers of 1-year-old and 2-year-old children starting in 1998.
Even if Table 4 provides evidence that pre-reform trends in earnings are similar for fathers of children of various ages, our estimates may still be biased by changes in characteristics that are discontinuous, are child cohort–specific, and occurred at the time of implementation of the paternity-leave quota and had an effect on earnings. In the following discussion, we investigate such possible sources of bias by exploring how our estimates are sensitive to the inclusion of different covariates and different sample restrictions.
We conduct our specification analyses by collapsing all treatment variables of fathers of children born after 1994 (after the phase-in period) to one treatment variable, and all the treatment variables of fathers of children born in 1993 and 1994 (during the phase-in period) to one phase-in-treatment variable. The comparison group consists of fathers of children born before the paternity-leave quota was introduced in 1993. Observations of fathers of 1-year-old children are excluded from the analysis because any treatment effect on these fathers can be partly explained by less than 100 % earnings compensation when being on leave. Figure 2 illustrates the nature of the experiment: darkly shaded cells are collapsed to form the treatment group, and white cells are collapsed to form the comparison group. Lightly shaded cells represent those treated during the phase-in period. All observations from the first row have been dropped.
The results are reported in Table 5. All models include year and age fixed effects. Models 1–5 add covariates stepwise for characteristics of the child, mother, and father as well as municipality fixed effects. We can see that the additional covariates increase the explanatory power of our model (adjusted R
2). However, the treatment estimates remain at around 1.3 % across the different model specifications, suggesting that the treatment effect is not biased by any cohort specific and discontinuous changes in observable characteristics. The corresponding TOT estimate, resting on the assumption that the treatment effect is generated only by fathers actually taking leave, ranges from 2.0 % to 2.2 %. Fathers treated in the phase-in period face, on average, a 0.5 % decrease in earnings.
Models 6 and 7 investigate how the treatment estimate is affected by different sample restrictions. In Model 6, we relax the age restriction that both parents should be older than 25 when the child was born. When including all parents older than 21, the estimated treatment effect drops to 1.0 %. In Model 7, we can see that when we tighten the age restriction to parents who were older than 27 when the child was born, the estimated treatment effect increases to 1.7 %.
One possible concern is that the paternity-leave quota affected fertility. In particular, if the reform increases father involvement, this may motivate couples to have another child that they otherwise would not have had. This, in turn, could have an impact on our estimates of treatment effects because a selected sample of fathers of older children will exit our sample and enter with a younger child. We address this concern in Model 8 by restricting our sample to fathers of one child. The estimated treatment effect remains basically the same. Ideally, we would investigate effects on fertility utilizing a similar framework as in our main analysis investigating effects on fathers’ earnings. However, our DD approach rests on the assumption that trends in the outcome variable are similar for fathers of children of various ages, which does not hold for trends in fertility.
We have limited our sample to full-time employed fathers. As discussed earlier, this restriction is problematic if the reform had an impact on the fathers’ decision to be employed full-time. We investigate this assertion in Table 6. In this table, we drop the sample restriction of full-time employment, and the dependent variable is a dummy variable indicating whether the father is full-time employed. Apart from these changes, Models 1 and 2 correspond to Models 1 and 4, respectively, in Table 5. We can see in both specifications a small and insignificant relationship between the treatment variables and full-time employment.Footnote 12 This is consistent with the hypothesis that the reform did not have an effect on the fathers’ decision to be full-time employed.
We also investigate whether the paternity-leave quota affected mothers’ labor market participation.Footnote 13 The analysis is designed in accordance with the analysis reported in Table 3. The DD coefficients of this analysis (available from authors on request) do not show a stepwise pattern that corresponds to the changes in fathers’ earnings reported in Table 3. We can see a strong decrease in labor supply for mothers of 1-year-olds in 1995, most likely because of the extended job protection implemented the same year. As expected, the table also shows that the cash-for-care subsidy implemented in 1998 decreased the labor supply of women with 1-year-olds (from 1998) and 2-year-olds (from 1999). However, the table does not show that the paternity-leave quota affected mothers’ labor supply.
Subsample Analyses: Father’s Education Level
In Table 7, we investigate the variation in responses to the paternity-leave quota across different levels of education. We use the same collapsed-form specification as Model 4 in Table 5. Comparing across Models 1–3 in Table 7, we can see that the negative response in earnings is significantly larger for fathers with no college degree compared with fathers with a college degree.Footnote 14 Moreover, the effect for university graduates is not statistically significant.
Because uptake rates vary between subgroups, we also report the corresponding TOT estimates, resting on the assumption that the treatment effect is generated only by fathers who actually took leave. Adjusting for relevant uptake rates amplifies the differences and gives us a TOT effect of a 3.3 % drop in earnings for fathers who have not completed high school, compared with 2.7 % for high school graduates and 1.1 % for university graduates. Some studies suggest that less-educated fathers are less involved with their children (Yeung et al. 2001), and our findings may reflect that the paternity-leave quota has a stronger effect on the group where the potential increase in involvement is largest. Alternatively, our findings may reflect that highly educated fathers have a higher opportunity cost of spending more time at home and are consequently less responsive to the paternity-leave quota. Empirical findings on the association between education level and father involvement are inconclusive (see, e.g., Yeung et al. (2001) for an overview of the literature).