Abstract

We exploit two Norwegian parental leave reforms to investigate their effects on adolescents' household work. The main reform increased the parental leave time by 7 weeks, 4 of which were reserved for the father, while the second reform raised only the general parental leave time by 3 weeks. We find a robust and substantial effect of the main reform implying that adolescent girls born immediately after the reform are less likely to do household work. By analyzing the two parental leave reforms together, we show that the father quota drives the results.

Introduction

Whether family policies change gender relations in society is an important question, but credible evidence is largely lacking. Cross-national differences in to what degree men participate in housework co-vary with family policy differences across countries (e.g., Fuwa and Cohen 2007; Hook 2006, 2010; Ruppander 2010), but a causal interpretation of this correlation is problematic. Since countries do not implement parental leave arrangements randomly, we should worry that other differences between the countries drive both patterns of household work and leave regulations, and that the patterns in household work we are trying to explain drives the leave regulations we are proposing to be a causal factor. In the present study, we instead analyze differences in household work across people within the same country, where the only plausible difference is exposure to different parental leave rules.

Paternal involvement in childrearing is increasing (Hook 2010), and several countries have policies to increase it by means of father quotas, i.e., weeks of parental leave reserved for the father. Yet only a few studies have investigated the effects of these reforms, and most of them study labor market outcomes of parents (Cools, Fiva and Kirkebøen 2011; Johansson 2010; Kotsadam et al. 2011; Rege and Solli 2010). However, Ekberg, Eriksson and Friebel (2006) and Kotsadam and Finseraas (2011) examine the effects of paternity leave on household division of labor. Although Ekberg, Eriksson and Friebel (2006) find no effects of the first Swedish daddy month in 1994 on subsequent leave taken for sick children, Kotsadam and Finseraas (2011) find an effect of the first Norwegian daddy month in 1993 on the division of household labor 13 years later. More specifically, Kotsadam and Finseraas (2011) find that couples with children born after the reform have fewer conflicts about household work and that they share household tasks more equally.1

As among adults, female teenagers do more household work than their male counterparts (Brannen 1995; Gager, Cooney and Call 1999; Dodson and Dickert 2004). The family is important in shaping these conditions, partly as children inherit social norms and cultural beliefs from their parents (e.g., Farré and Vella 2007; Fernández 2007a; Guiso, Sapienza and Zingales 2006; McHale, Crouter and Tucker 1999). It is frequently argued that family policies have important consequences for family decisions (Dauphin et al. 2011), which are essential for the degree of gender equality (e.g., Sullivan et al. 2009). Consequently, researchers have begun to study the effect of parental leave on children (Baker and Milligan 2010, 2011; Cools, Fiva and Kirkebøen 2011; Dustmann and Schonberg 2008). Only one study (Cools, Fiva and Kirkebøen 2011) has investigated the effects of paternity leave on children.

In the present study, we ask whether parental leave shapes the decision to conduct household work and the amount of household work conducted by adolescents. We exploit a Norwegian parental leave reform in 1993, which increased the parental leave time by 7 weeks, 4 of which were reserved for the father, to evaluate the long-term effects on the affected children's household work.

We build on a simple model contrasting within-family socialization with the parents' need for help to derive testable hypotheses on the mechanisms for how paternity leave can influence the amount of household work conducted by adolescents. In accordance with empirical findings (Kotsadam and Finseraas 2011), we believe that the paternity leave reform equalized the division of household work between the mother and the father. If the more equal division of household work is being transmitted to the next generation as parents transfer their norms and practices to their children, then we would expect that the parental leave reform has gendered effects. More specifically that it decreases girls' household work, increases boys' household work, or both. If, however, the more equal division of parents' work simply reduced the need for children's work, then we would expect a similar decrease in household work for both boys and girls.

The 1993 reform not only implemented a father's quota but also extended the total parental leave time. To isolate the effects of paternity leave from the effects of a general increase in parental leave, we also investigate the effects of a parental leave reform in 1992. The 1992 reform increased the general parental leave by 3 weeks, without any reservation for the father. Because the 1992 reform increased mothers' time at home, we expect opposite effects of the 1992 parental leave reform compared with the 1993 paternity leave reform.

We find a robust and substantive effect of the 1993 reform, implying that adolescent girls born immediately after the reform are less likely to be involved in household work. The results regarding the amount of household work point in the same direction, but are less precisely estimated. Our analysis of the 1992 reform indicate that the general increase in parental leave reduces the amount of household work conducted by boys, and the difference-in-differences estimation of the two reforms together makes us more confident that the decrease in the probability of conducting household work among girls are driven by the daddy quota. Our results indicate that the socialization and need mechanisms interact, as the gendered nature of the effects gives support for the socialization mechanism, while the reduction of the total amount of children's household work gives support to the need mechanism.

The Reform and Testable Hypotheses

The Norwegian Parental Leave Scheme and the Two Reforms

Norway, like the other Scandinavian countries, has for decades operated what has been labeled a women-friendly welfare state (Hernes 1987) where equal opportunities in employment and domestic work have been important goals. Paid parental leave has a long history in Norway (NOU 1996). A 6-week paid maternity leave was introduced as far back as in 1909. In 1956, sickness insurance became compulsory for all employed citizens, and thus a 12-week paid maternity leave became available to all working women. The parental leave system was first justified based on mothers' health-related necessity to be absent from work, and to compensate for lost income in connection with pregnancy and care for small children. In the late 1960s, the public debate turned to concerns about equal rights in the labor market. In 1977, fathers gained the right to use parental leave when the leave was expanded to 18 weeks with 6 weeks after the birth reserved for mothers. The right to take paid parental leave was gradually extended during the 1980s and early 1990s. Most notably, on April 1, 1992, the paid parental leave was expanded from 32 to 35 weeks.

For policymakers it was disappointing to observe that an overwhelming majority of the parental leave was taken up by mothers (NOU 1995). To increase fathers' take-up rates, Norway was the first country in the world to introduce a “daddy quota” on April 1, 1993, where fathers to children born at or after this date got an independent right to parental leave. The reform extended the parental leave from 35 to 42 weeks with full earnings compensation,2 4 of which were reserved for the father.3 At this time, paid paternity leave was contingent on both parents working at least 50 percent before the child was born, and the payment to fathers was reduced if the mother did not work full time. In addition, fathers were not eligible for paid parental leave unless they had worked at least 6 of the last 10 months. Fathers were entitled to use the daddy quota up until the child turned 3 years old, although 95 percent of those taking leave in 1993-1995 did so during the child's first year (Rege and Solli 2010).

Inducing fathers to take more responsibility for childrearing was seen as an important step on the way to equal division of labor and toward reducing the gender wage gap. The political arguments to earmark some of the parental leave for fathers were threesome: first, this policy implementation gives a strong signal as well as possibilities to be more actively involved in child rearing and hence to challenge norms of male breadwinning (Leira 1998). Second, an independent right to parental leave gives fathers an advantage when parents discuss the distribution of the parental leave between them. Third, the law strengthens fathers' argument for parental leave when dealing with reluctant employers.

The reform led to a sharp increase in the take-up rate from less than 4 percent in March 1993 to 39 percent in April 1993 and is now over 80 percent (Cools, Fiva and Kirkebøen 2011). The average paternity leave taken by fathers to children born right after the reform was 5 weeks, the vast majority took exactly 4 weeks. On average, the fathers started their leave when the child was 9 months old. There was no obligation for the mother to return to work when the father was home on parental leave, and a survey conducted in 1995 shows that 35 percent of the mothers were home (for instance, by taking vacation from work) during the father's leave period (Brandt and Øverli 1998).

Parental Leave, the Need for Household Work and the within-Family Socialization of Gender Roles

The main aim of the article is to test whether parental leave reforms, and in particular a daddy quota, affect children's household work. To understand why and how this may happen, we build on a simple model which contrasts within-family socialization of gender roles with the need for household work to derive testable hypotheses for the mechanisms of how parental leave might influence adolescents' household work.

Blair (1992) highlights two reasons for why children do household work, namely, socialization and need. Parents may assign household work to children as a socializing experience to promote responsibility or important gendered tasks. Alternatively, parents may use children as a labor source and assign household tasks to them because the available time the parents themselves are able or willing to allocate to household tasks is not sufficient to cover the need. These two motivations may differ across households and need not be mutually exclusive even within the same household. Nonetheless, they are the two most likely mechanisms for how changes in household work of children may appear and they both explain why the effects may be durable. As we will show, the two mechanisms yield different predictions of how the reforms might influence adolescents' household work.

The first step in our model regards the effect of parental leave on the adolescents' parents. In essence, the introduction of a daddy quota challenges norms of male breadwinning (Gornick and Meyers 2008; Hook 2006, 2010). Within the family, the daddy quota effectively increases the time fathers' spend with the child during the child's first years and improves the father-child relationship. Beyond the quota's effect on the father-child-relationship, we argue that the quota had an effect on the division of household work between the mother and the father. The quota improves the bonding between father and child, which could affect attitudes toward activities traditionally performed by women, and men who are exposed to nontraditional experiences are more likely to change their views on gender equality (Klein 1987:35). Even though the paternity leave covers only a short period, it intervenes at a critical time for renegotiating household work (e.g., Hook 2010). Fathers are expected to do more household work during the leave and arguments of returning to traditional gender roles after the leave are therefore less credible. Kotsadam and Finseraas (2011) find, in line with our argument, survey data evidence of more equal sharing of household tasks when comparing the division of household work of parents with access to the daddy quota (i.e., with children born right after the implementation of the reform) and parents without this access (i.e., children born right before the reform).

The second step in our theoretical argument regards the effect on the children. One mechanism for how paternity leave may affect children's household work is if the father's increase in household work substitutes for children's household work. A testable hypothesis derived from this mechanism is whether the total amount of household work reduces for the children as a result of the daddy quota.

A second mechanism is that the paternity leave affects the gender socialization of children. It has been argued that children's participation in household work is particularly important to study as it is one area where gender roles are clearly spelled out and visible across social classes (Raley and Bianchi 2006:406). The family is probably the most important area for social learning, and we may expect that the more equal division of household work among parents with access to the daddy quota is being transmitted from one generation to the next (see, e.g., Farré and Vella [2007] and McHale, Crouter and Tucker [1999] for similar arguments). The socialization is likely to occur if the parents transfer their own gender practices to their children by making boys conduct more household work or making girls conduct less. A testable hypothesis derived from this mechanism is therefore whether we observe a less gendered pattern of children's household work in families where the parents had access to the daddy quota.

To differentiate between the two main mechanisms for household work of the adolescents we test the following two hypotheses:

(1. The daddy quota reduces children's household work similarly for both sexes.

(2. The daddy quota affects the gendered pattern of children's household work without affecting the total amount.

As these two mechanisms are not mutually exclusive a third hypothesis is that they work together, leading to the following hypothesis:

(3. The daddy quota reduces children's household work and this decline follows the gendered dimensions outlined above.

To be even more specific, we may expect the two features of the 1993 reform, i.e., the more general parental leave and the daddy quota, to work in opposite directions. When more general time is given to parents, it has been the case that the extended time is used by the mother. When mothers' increase their relative time at home, we expect a reinforcement of the existing gendered patterns of household work. On the other hand, by increasing the time fathers stay at home, we expect traditional gender roles to be challenged.

We expect the daddy quota aspect of the reform to be more important for gender roles than the general increase in parental leave. The marginal effect of increasing the general parental leave by 3 weeks from 35 weeks is likely to be smaller than increasing fathers' time at home from a modal zero to a modal of 4 weeks (Cools, Fiva and Kirkebøen 2011). Still, we also analyze the effects of the 1992 reform, which increased only the general parental leave. A corollary expectation is that this reform has less effect, and in the opposite direction, than the father's quota.

Theoretical models of gender socialization give prominence to the family setting, and while no one is arguing that the family is the only arena for socialization, the family is considered central (see Owen Blakemore and Hill 2008 for an overview). Hence, we assume that the family is one important area of socialization of household work, which is in fact sufficient for our mechanisms to come into play. Of course, children with parents having access to the daddy quota will mix and interact with children socialized in families without daddy quota experience, and their parents will also interact. Attitudes and practices can therefore spread from one group to the other. This implies that we investigate whether the reform creates a change in gender roles over and above the possible effects of the reform on gender roles in the total population, i.e., in addition to peer effects and other societal changes. Hence, the total effects of the reform are likely to be even larger than what we identify here.

There is no denying that the causal chain we propose is long, involving changes among the parents in practices and attitudes, which in turn affect their children. The empirical analysis is, however, in “reduced form,” in the sense that irrespective of the large and complex chain of events, we are able to credibly assess whether there is any effect of the reform. This assessment is a crucial first step. The nature of the empirical analysis implies that we do not establish the exact mechanism linking the reform to children's household work. Nonetheless, by using the hypotheses above we are able to speak to the two most likely reasons that the reform would have an effect and see whether one of these two mechanisms work in isolation, or whether they work together to produce results with a high level of internal validity.

Data and Descriptive Statistics

We rely on data from the 2010 edition of the Young in Norway study, which is a cross-sectional study of students in elementary school, junior high school and senior high school. In total, 11,659 students aged 12-19 years participated, with a response rate of 73 percent. Because we are mainly interested in the 1992 and 1993 year cohorts, we rely mostly on data from the senior high schools, for which the response rate was 84 percent. The questionnaires were completed from January to March 201.

The most important feature of this dataset is that we have access to exact birthdates of the respondents so that we are able to construct treatment and control groups based on when the child was born. Those born on or after April 1st are the treatment group because the parents of these students were treated by the reform. Those born before April 1st compose the control group because the parents of these students were not treated by the reform. To our knowledge, this dataset is the only available dataset that allows us to investigate the effects of parental leave on children's participation in household work.

Our main variable of interest is a survey question that asks how many times in the last 7 days the respondent did household work. The question included three examples of such tasks, namely, washing, cleaning and shoveling snow (the survey was distributed during winter). We recode this variable into two dependent variables, first, a binary recoding of those who report that they did household work in the last 7 days (household_work = 1) against those who report that they did not (household_work =0). Second, we analyze the logged number of times the respondent did household work (nr_of_times) in the last 7 days.4 It would have been preferable to have a household work variable that separates the different types of household work, in particular because the specific tasks are gendered. This lack of separation does not affect the identification of causal effects of parental leave, as it is the same question for treatment and control groups, but it would be useful in terms of identifying the mechanisms.

Ideally, we would have preferred a measure of the amount of time spent on housework as a complement to the number of times the respondent did household work. Unfortunately we do not, and this is the only dataset we know of that includes exact birthdates of children born around the reform date. Although we readily acknowledge that more specific outcome variables would be preferred, the ability to credibly assess the causal effects makes using this dataset strictly advantageous to using other datasets. Table 1 presents the mean values of our dependent variables for the group affected by the 1993 policy and for the control group. The numbers for number of times are presented in unlogged form to ease the interpretation.

Table 1:

Mean Values of the Dependent Variables for the Treatment and Control Groups

Treatment Group
 
Control Group
 
3 Months
 
3 Months
 
Variable Mean Standard Deviation Variable Mean Standard Deviation 
household_work .820** .385 316 household_work .898 .303 304 
nr_of_times 2.326 2.151 316 nr_of_times 2.536 2.560 304 
1 Month 1 Month 
Variable Mean Standard Deviation Variable Mean Standard Deviation 
household_work .740*** .441 104 household_work .925 .264 120 
nr_of_times 2.106** 2.310 104 nr_of_times 2.833 2.772 120 
2 Weeks 2 Weeks 
Variable Mean Standard Deviation Variable Mean Standard Deviation 
household_work .768** .426 56 household_work .953 .213 43 
nr_of_times 1.946* 2.203 56 nr_of_times 2.791 2.054 43 
Treatment Group
 
Control Group
 
3 Months
 
3 Months
 
Variable Mean Standard Deviation Variable Mean Standard Deviation 
household_work .820** .385 316 household_work .898 .303 304 
nr_of_times 2.326 2.151 316 nr_of_times 2.536 2.560 304 
1 Month 1 Month 
Variable Mean Standard Deviation Variable Mean Standard Deviation 
household_work .740*** .441 104 household_work .925 .264 120 
nr_of_times 2.106** 2.310 104 nr_of_times 2.833 2.772 120 
2 Weeks 2 Weeks 
Variable Mean Standard Deviation Variable Mean Standard Deviation 
household_work .768** .426 56 household_work .953 .213 43 
nr_of_times 1.946* 2.203 56 nr_of_times 2.791 2.054 43 

*** p < .01 ** p < .05 * p < .1 (p-values in two-sided t tests of the difference between treatment and control groups)

We focus on three different time windows to show the robustness of the results. The first time window is 3 months before and after April 1st (n = 620). This is our longest possible time window (because we want the respondents to be in the same school year). We also present results from two shorter time windows, namely, 1 month before and after April 1st (n = 224) and 2 weeks before and after April 1st (n = 99).

Our first finding is that a lower proportion of respondents in the treatment group report that they conducted household work in the last 7 days. This is the case in all time windows. We also find that respondents in the treatment group do household work less frequently, although this difference is not statistically significant in the 3-month sample.

Table 2 presents descriptive statistics of other variables by treatment/control group (3-month window). These variables are the gender of the respondents and characteristics of their parents. The variables are described in the online appendix. Reassuringly, we find no significant or substantial differences between the groups in the mean values of these variables. Nonetheless, below we present results both with and without these variables as control variables to show the robustness of the results.

Table 2:

Differences in Control Variables between Treated and Control Respondents

Treatment Group
 
Control Group
 
3 Months
 
3 Months
 
Variable Mean Standard Deviation Variable Mean Standard Deviation 
Boy .50 .50 337 boy .53 .50 324 
mother_foreign .06 .24 338 mother_foreign .06 .24 326 
father_foreign .06 .25 339 father_foreign .07 .26 326 
father_fulltime .81 .39 339 father_fulltime .78 .42 327 
mother_fulltime .68 .47 339 mother_fulltime .68 .47 327 
father_parttime .08 .27 339 father_parttime .09 .28 327 
mother_parttime .18 .38 339 mother_parttime .19 .39 327 
father_unemployed .02 .15 339 father_unemployed .01 .11 327 
mother_unemployed .03 .16 339 mother_unemployed .02 .14 327 
father_home .03 .16 339 father_home .03 .18 327 
mother_home .05 .21 339 mother_home .07 .26 327 
father_dead .01 .08 339 father_dead .003 .06 327 
mother_dead .01 .11 339 mother_dead .003 .06 327 
father_university .41 .49 315 father_university .45 .50 306 
mother_university .46 .50 313 mother_university .48 .50 308 
good_income .71 .46 328 good_income .76 .43 317 
Treatment Group
 
Control Group
 
3 Months
 
3 Months
 
Variable Mean Standard Deviation Variable Mean Standard Deviation 
Boy .50 .50 337 boy .53 .50 324 
mother_foreign .06 .24 338 mother_foreign .06 .24 326 
father_foreign .06 .25 339 father_foreign .07 .26 326 
father_fulltime .81 .39 339 father_fulltime .78 .42 327 
mother_fulltime .68 .47 339 mother_fulltime .68 .47 327 
father_parttime .08 .27 339 father_parttime .09 .28 327 
mother_parttime .18 .38 339 mother_parttime .19 .39 327 
father_unemployed .02 .15 339 father_unemployed .01 .11 327 
mother_unemployed .03 .16 339 mother_unemployed .02 .14 327 
father_home .03 .16 339 father_home .03 .18 327 
mother_home .05 .21 339 mother_home .07 .26 327 
father_dead .01 .08 339 father_dead .003 .06 327 
mother_dead .01 .11 339 mother_dead .003 .06 327 
father_university .41 .49 315 father_university .45 .50 306 
mother_university .46 .50 313 mother_university .48 .50 308 
good_income .71 .46 328 good_income .76 .43 317 

To establish which variables are important predictors of our dependent variables, we conducted a series of regression models including all the control variables for the largest possible sample of students with equal regulation of parental leave (children born 1994-1997). The results are presented in the online appendix (Section B, Table B1). Two findings are of particular importance. First, the gender difference is robust to the inclusion of the control variables. Second, and most important, age is not statistically significantly correlated with our dependent variables––neither in years nor in months.5 Because we compare people born in the second quarter of the year to those born in the first quarter, we also investigate whether there are any differences between those born in these two quarters when they have equal parental leave regulation. We fail to reject that quarter of birth does not have an effect on our dependent variables (columns 3 and 6 in Table B1); thus, we are more confident that age differences or birth months are not driving the difference between the treatment and the control group.

Empirical Strategy

We exploit the paternity leave reform as a natural experiment where the treatment consists of having parents affected by the new paternity leave reform, i.e., having children born on or after April 1, 1993. Because all children born after the reform date were treated by the reform and no children born before the reform date were treated, we are able to compare the two groups of children in an attempt to identify the causal effects of the policy. The credibility with regard to identifying causal effects is strengthened by the fast policy process, which implies that parents giving birth around the reform threshold could not have known about the reform at the time of conception. The specific design of the reform, including April 1, 1993, as the day of implementation, was proposed on December 1, 1992, and decided in parliament on January 22, 1993.6

We do not have information on actual take-up of parental leave. However, the main point of our empirical strategy is to exploit the exogenous variation induced by the reform, implying that we do not need to condition our analysis on actual take-up of parental leave. This allows us to estimate the intention-to-treat effect of the reform. If we had access to take-up at the individual level, then we could have estimated the treatment effect of actually using the daddy quota using an instrumental variables approach. Yet for policymakers, the intention-to-treat effect is probably more relevant as it identifies the total effects of the reform. In the online appendix, we also present the setup and results of a regression discontinuity analysis that yield the same qualitative conclusions as those presented in the main text of the article.

Local Regressions

We start by running ordinary least squares (OLS) regressions of the dependent variables on an indicator variable that equals 1 for children born just after the reform in 1993 (Treatment) and on a vector of control variables. We rely on an OLS specification even though the dependent variable (household_work) is binary. This specification gives us the linear probability model, which has the advantage that the interaction terms are easy to interpret. Furthermore, as all our covariates are discrete and the model is fully saturated in most specifications, the linear probability model is as appropriate for limited dependent variables as OLS is for continuous dependent variables (Angrist 2001).7 We also run all regressions using a probit model, which yields the same conclusions as below (results available upon request).

Following Angrist (2001), we choose an OLS specification also for our second dependent variable, nr_of_times, which is the log of number of times the respondent did household work plus 1 to retain the zeros. One alternative is to estimate a Tobit model, but we want to avoid assumptions of an underlying continuously distributed latent variable. A second alternative is to estimate the outcome only for individuals doing some amount of household work. Such conditional-on-positive effects are harder to interpret, as they are not necessarily causal effects on the number of times housework is conducted for the subset of individuals that would have done household work irrespective of the reform. If the reform affects participation, we do not identify an effect among children that do household work, even if we condition on positive effects, as the composition of this group changes. Rather, the identified effect would then be a combination of selection effects from those who would not have participated if not for the reform, and increases in the amount of household work for participants.

We always limit the sample so that we compare children born just before and just after the reform and within the same school year. The sample windows presented in the main analyses are 3 months, 1 month and 2 weeks. The 2-week sample has been argued to be a random sample (e.g., Ekberg, Eriksson and Friebel 2006). Using this sample corresponds well with what Rosenzweig and Wolpin (2000) label a “natural” natural experiment in which nature determines the institutional setting the parents end up in, and thus allocation to either treatment or control group. There are several arguments to support this reasoning. First, it is not possible for parents to completely control the date of conception (Eriksson 2005; Lalive and Zweimüller 2009).

Second, a pregnancy takes an average of 40 weeks, and the duration is normally distributed with a standard deviation of 2 weeks (Ekberg, Eriksson and Friebel 2006; Eriksson 2005). Most important, however, none of the parents knew that they would be treated at the time of conception. Thus, it seems reasonable that the reform creates exogenous variation in own and spousal parental leave, and long-run differences in outcomes can plausibly be attributed to the change in legislation (cf. Kluve and Tamm 2009; Lalive and Zweimüller 2009). Births cannot be postponed and the studied reform is strictly favorable for parents, so triggering of birth by medical means such as by a cesarean section (see Johansson 2010) should not be a problem. A problem may occur, however, if triggering of births is postponed by the reform. In fact, Cools, Fiva and Kirkebøen (2011) show that about 5.7 percent of the births that were predicted to occur in late March instead occurred in early April. We address this potential problem in the same vein as Cools, Fiva and Kirkebøen (2011), by excluding births around the last 2 weeks of March and the first 2 weeks of April 1993 as yet another robustness check.

Difference in Differences

Next, we present difference-in-differences estimations with children born on the same calendar dates in 1994 and 1995. Taking the amount of household work variable with the difference-in-differences estimation using the 1994 cohort as an illustrative example, we estimate the following regression model:  

formula
where the subscript c accounts for different cohorts (1993, 1994, 1995) and the subscript m refers to month of birth (January-March or April-June). Treatment_months equals one for those born in the months after the reform and zero for those born in the months before the reform. Treatment_cohort equals one for those born in 1993 and zero for those born in 1994. χ is our parameter of main interest, as Treatment equals one for those being exposed to the reform in 1993. Note that this variable is implicitly an interaction term between Treatment_months and Treatment_cohort. The advantage of the difference-in-differences estimation is that it eliminates the within-year differences in age between treatment and control individuals since the difference between treated and control children is compared with the difference of children with the same age difference in other years.

Finally, we also analyze the 1992 reform, which increased the general parental leave by 3 weeks. First, we examine the effects of the 1992 reform in a set of local regressions as with the 1993 reform. We then proceed to use the two reforms in a difference-in-differences estimation. Remember, in contrast to the 1993 reform—which increased the parental leave by a total of 7 weeks, but tied 4 weeks to the father—the 1992 reform added 3 weeks of general parental leave, but did not entail any daddy quota. We can therefore use the two reforms to cancel out the general increase in parental leave, and the remaining difference pertains to the 4 weeks of paternity leave (see Cools, Fiva and Kirkebøen 2011 for a similar strategy). A crucial assumption in order for this strategy to identify the causal effect of the daddy quota is that there are no other differences between the children born after and before the reform in 1993 that do not appear in 1992 as well.8

Results

We now proceed to present the results. The section follows the same disposition as the Empirical Strategy section. Because of space restrictions, we do not present the coefficients for the control variables, but they are reported in the online appendix, section B.

Results from the Local Regression Analysis

Table 3, panel A, presents the OLS results with the indicator of whether the respondent did any household work (household_work) as the dependent variable. The first column includes the treatment status as the only independent variable, and shows that individuals in the treatment group are about eight percentage points less likely to report that they conducted any household work in the last 7 days.

Table 3:

OLS Regressions

Panel A. Dependent Variable household_work; OLS Regressions
 
 (1) (2) (3) (4) (5) (6) (7) (8) (9) (10) 
Variables Basic By Gender Exogenous All Controls 1 Month By Gender 2 Weeks By Gender Reduced By Gender 
Treatment -.078*** -.123*** -.128*** -.120*** -.185*** -.192*** -.186*** -.240*** -.058* -.102** 
 (.028) (.038) (.038) (.040) (.049) (.069) (.066) (.087) (.030) (.042) 
Boy  -.056 -.055 -.077**  -.044  -.095  -.048 
  (.035) (.035) (.037)  (.048)  (.065)  (.039) 
Treatment*Boy  .089 .100* .113**  .016  .109  .089 
  (.056) (.056) (.058)  (.099)  (.133)  (.061) 
Constant .898*** .926*** .936*** .854*** .925*** .947*** .953*** 1.000 .889*** .913*** 
 (.017) (.022) (.023) (.076) (.024) (.030) (.032) (.) (.019) (.025) 
Observations 620 616 615 579 224 223 99 99 521 517 
R-squared .013 .017 .028 .043 .063 .065 .066 .074 .007 .011 
Panel B. Dependent Variable, nr_of_times; OLS Regressions 
 (1) (2) (3) (4) (5) (6) (7) (8) (9) (10) 
Variables Basic By Gender Exogenous All Controls 1 Month By Gender 2 weeks By Gender Reduced By Gender 
Treatment -.066 -.063 -.070 -.077 -.250*** -.163 -.326*** -.310* -.016 -.019 
 (.049) (.067) (.067) (.069) (.086) (.121) (.116) (.161) (.054) (.073) 
Boy  -.023 -.020 -.063  -.002  -.109  -.006 
  (.068) (.069) (.073)  (.110)  (.161)  (.075) 
Treatment*Boy  -.012 .002 .040  -.166  -.017  .002 
  (.099) (.099) (.104)  (.172)  (.237)  (.108) 
Constant 1.076*** 1.089*** 1.099*** 1.063*** 1.155*** 1.157*** 1.201*** 1.254*** 1.056*** 1.060*** 
 (.034) (.043) (.044) (.131) (.055) (.068) (.080) (.084) (.037) (.048) 
Observations 620 616 615 579 224 223 99 99 521 517 
R-squared .003 .004 .012 .018 .037 .045 .072 .082 .000 .000 
Panel A. Dependent Variable household_work; OLS Regressions
 
 (1) (2) (3) (4) (5) (6) (7) (8) (9) (10) 
Variables Basic By Gender Exogenous All Controls 1 Month By Gender 2 Weeks By Gender Reduced By Gender 
Treatment -.078*** -.123*** -.128*** -.120*** -.185*** -.192*** -.186*** -.240*** -.058* -.102** 
 (.028) (.038) (.038) (.040) (.049) (.069) (.066) (.087) (.030) (.042) 
Boy  -.056 -.055 -.077**  -.044  -.095  -.048 
  (.035) (.035) (.037)  (.048)  (.065)  (.039) 
Treatment*Boy  .089 .100* .113**  .016  .109  .089 
  (.056) (.056) (.058)  (.099)  (.133)  (.061) 
Constant .898*** .926*** .936*** .854*** .925*** .947*** .953*** 1.000 .889*** .913*** 
 (.017) (.022) (.023) (.076) (.024) (.030) (.032) (.) (.019) (.025) 
Observations 620 616 615 579 224 223 99 99 521 517 
R-squared .013 .017 .028 .043 .063 .065 .066 .074 .007 .011 
Panel B. Dependent Variable, nr_of_times; OLS Regressions 
 (1) (2) (3) (4) (5) (6) (7) (8) (9) (10) 
Variables Basic By Gender Exogenous All Controls 1 Month By Gender 2 weeks By Gender Reduced By Gender 
Treatment -.066 -.063 -.070 -.077 -.250*** -.163 -.326*** -.310* -.016 -.019 
 (.049) (.067) (.067) (.069) (.086) (.121) (.116) (.161) (.054) (.073) 
Boy  -.023 -.020 -.063  -.002  -.109  -.006 
  (.068) (.069) (.073)  (.110)  (.161)  (.075) 
Treatment*Boy  -.012 .002 .040  -.166  -.017  .002 
  (.099) (.099) (.104)  (.172)  (.237)  (.108) 
Constant 1.076*** 1.089*** 1.099*** 1.063*** 1.155*** 1.157*** 1.201*** 1.254*** 1.056*** 1.060*** 
 (.034) (.043) (.044) (.131) (.055) (.068) (.080) (.084) (.037) (.048) 
Observations 620 616 615 579 224 223 99 99 521 517 
R-squared .003 .004 .012 .018 .037 .045 .072 .082 .000 .000 

*** p < .01 ** p < .05 * p < .1

Note: Robust standard errors in parentheses; column 1 presents the basic regression with a time window of 3 months before and after the reform. In column 2 we let the treatment effect vary by gender by interacting the treatment variable with an indicator variable for being a boy. In column 3 we include controls for mother_foreign, father_foreign, father_dead and mother_dead. In Column 4 we add the additional control variables. In column 5 the time window is +/- 1 month around April 1st. In column 7 the time window is +/- 2 weeks around April 1st. In column 9 we repeat the basic regression in the 3-month sample, but exclude individuals born in the last 2 weeks of March or the first 2 weeks of April. Columns 6, 8 and 10 allow for gender differences by interacting Boy with Treatment.

In column 2 we add gender (Boy = 1) and its interaction with treatment status. The results show that girls in the treatment group are about 12 percentage points less likely to report doing housework compared with girls in the control group, a difference that is strongly statistically significant. The treatment effect differs between boys and girls by nine percentage points, but this difference is only statistically significant when adding control variables (and only marginally so). In fact, boys in the treatment group are only about three percentage points less likely to report doing housework compared with boys in the control group, a difference that is not statistically significant.9 In other words, the reform appears to have reduced the probability of doing housework among girls, and yet this decrease is not matched by an increase among boys. This finding supports the socialization theory as the results are gendered, but it also supports the need theory as the total probability of doing household work is lower in the treatment group. Thus, the results support the hypothesis that the mechanisms work together.

The coefficients do not change much when we add a vector of plausibly exogenous control variables (column 3) or the full set of control variables (column 4),10 while columns 5 and 7 show that the treatment effect becomes even more negative when we decrease the time window to 1 month and 2 weeks, respectively. In column 9 we exclude the 2 weeks around the reform date, which are potentially polluted because of strategic birth planning (Cools, Fiva and Kirkebøen 2011). When excluding these weeks, the treatment effect is somewhat smaller compared with what we find in the main window (and substantially smaller compared with the smaller windows), and only statistically significant at the 10 percent level. The effect by gender in the smaller samples (in columns 6, 8 and 10) show a similar pattern as in the 3-month sample.

Panel B of Table 3 shows the OLS regression results for the logged number of times household work was conducted in the last week (nr_of_times). The results point in the same direction as the results on the probability of doing household work, but the coefficients are imprecisely estimated and often not statistically significant.

One potential problem for the identification of causal effects of the reform is that children born after the reform are slightly younger than children born before the reform, and perhaps do less housework because they are younger. Thus, it is very important to make sure that our treatment effect is not biased by a spurious age effect. Reassuringly, we find no statistically significant age differences on household work (see previous discussion in the Data and Descriptive Statistics section). In addition, we conduct placebo analyses where we “pretend” that the reform was introduced at times when there were no changes in parental leave legislation. We pretend that the reform happened 1 month before, 1 month after, 1 year after and 2 years after April 1, 1993. If the results are merely driven by age differences, then we expect to find similar results in these placebo regressions because the two groups then face identical parental leave regulations. The placebo regressions in 1994 and 1995 furthermore account for possible biological or social differences between children born in the first versus the second quarter of the year. Because of space constraints we report the full results in the online appendix. The placebo regressions produce insignificant treatment effects, which strengthen our confidence in the validity of the estimation strategy.

Results from the Difference-in-Differences Analyses

Table 4 presents the difference-in-differences estimations with data on children born around April 1, 1993 (i.e., the cohort including the treated children), and children born on the same calendar dates in 1994 and 1995. These regressions eliminate the within-year differences in age between treatment and control individuals, because the difference between children in the treatment and control group is compared with the corresponding difference in other years. Thus, we further reduce the worry that age differences between the groups drive the results.

Table 4:

Difference-in-Differences Regressions Comparing the Difference in 1993 to the Difference in 1994 (Columns 1 to 4) and 1995 (Columns 5 to 8); Dependent Variables household_work (OLS) and nr_of_times (OLS)

 Difference-in-Differences with the 1994 Cohort
 
Difference-in-Differences with the 1995 Cohort
 
 household_work
 
nr_of_times
 
household_work
 
nr_of_times
 
 (1) (2) (3) (4) (5) (6) (7) (8) 
Variables Basic. Gender. Basic. Gender. Basic Gender Basic Gender 
Treatment -.026 -.102* -.002 -.030 -.111*** -.197*** -.092 -.133 
 (.046) (.058) (.084) (.103) (.040) (.048) (.077) (.093) 
Boy*Treatment  .154*  .051  .188***  .094 
  (.079)  (.144)  (.068)  (.129) 
Treatment_months -.052 -.022 -.064 -.032 .033 .073** .026 .071 
 (.037) (.044) (.068) (.078) (.029) (.029) (.060) (.065) 
Treatment_cohort .041 .069** -.051 -.033 .022 .045 -.048 -.040 
 (.029) (.032) (.056) (.062) (.028) (.031) (.056) (.062) 
Boy*Treatment_months  -.065  -.062  -.099**  -.105 
  (.056)  (.104)  (.039)  (.082) 
Boy*Treatment_cohort  -.056  -.023  -.056  -.023 
  (.035)  (.068)  (.035)  (.068) 
Constant .857*** .856*** 1.127*** 1.123*** .876*** .880*** 1.124*** 1.129*** 
 (.024) (.024) (.044) (.045) (.022) (.022) (.044) (.044) 
Observations 1,042 1,035 1,042 1,035 1,079 1,072 1,079 1,072 
R-squared .010 .015 .004 .005 .012 .020 .007 .010 
 Difference-in-Differences with the 1994 Cohort
 
Difference-in-Differences with the 1995 Cohort
 
 household_work
 
nr_of_times
 
household_work
 
nr_of_times
 
 (1) (2) (3) (4) (5) (6) (7) (8) 
Variables Basic. Gender. Basic. Gender. Basic Gender Basic Gender 
Treatment -.026 -.102* -.002 -.030 -.111*** -.197*** -.092 -.133 
 (.046) (.058) (.084) (.103) (.040) (.048) (.077) (.093) 
Boy*Treatment  .154*  .051  .188***  .094 
  (.079)  (.144)  (.068)  (.129) 
Treatment_months -.052 -.022 -.064 -.032 .033 .073** .026 .071 
 (.037) (.044) (.068) (.078) (.029) (.029) (.060) (.065) 
Treatment_cohort .041 .069** -.051 -.033 .022 .045 -.048 -.040 
 (.029) (.032) (.056) (.062) (.028) (.031) (.056) (.062) 
Boy*Treatment_months  -.065  -.062  -.099**  -.105 
  (.056)  (.104)  (.039)  (.082) 
Boy*Treatment_cohort  -.056  -.023  -.056  -.023 
  (.035)  (.068)  (.035)  (.068) 
Constant .857*** .856*** 1.127*** 1.123*** .876*** .880*** 1.124*** 1.129*** 
 (.024) (.024) (.044) (.045) (.022) (.022) (.044) (.044) 
Observations 1,042 1,035 1,042 1,035 1,079 1,072 1,079 1,072 
R-squared .010 .015 .004 .005 .012 .020 .007 .010 

*** p < .01 ** p < .05, * p < .1

Note: Robust standard errors in parentheses; all results are based on the +/- 3 months sample. The 1993 cohort is the reform cohort and is contrasted to the 1994 cohort (columns 1 to 4) or the 1995 cohort (columns 5 to 8).

Starting with an estimation using those born in 1994 as a counterfactual group, we see a negative treatment effect on the indicator of doing any household work, but the effect is not statistically significant in the basic regression (column 1). Analyzing the effects by gender of the child in column 2, we again note a negative treatment effect on girls (Treatment) and a difference between the effects for girls and boys (Treatment*Boys). These coefficients are only statistically significant at the 10 percent level, however.

As for the amount of household work, we find a negative, albeit statistically insignificant, treatment effect in column 3 and a corresponding statistically insignificant gender difference in column 4. We see a similar pattern when using the 1995 cohort as a counterfactual group, with the difference that the treatment effects in the household_work regressions are more robust and larger in magnitude. These results increase the confidence in the previous estimations. In particular, they suggest that the differences in the probability of doing household work between treatment and control respondents in the 1993 cohort are not driven by age differences or some spurious calendar effects.

To sum up, those with parents affected by the 1993 reform are less likely to do household work. When disentangling the effects by gender, we find that the reform affected girls more than boys. We find similar, but less robust, results when studying the amount of household work conducted.

The results so far constitute the composite causal effects of the two components of the 1993 reform, the extended parental leave and the daddy quota. Thus, to conclude that these results are an effect of the daddy quota, we need to disentangle the causal effect of the daddy quota from the causal effect of extending the general parental leave. We therefore analyze the 1992 reform, which increased the general parental leave by 3 weeks, but did not implement a daddy quota.

Table 5 presents the results using a sample of respondents born 3 months before and after April 1, 1992, which is the date of the implementation. The treatment effects on the probability of doing household work (columns 1 and 2) are not statistically significant. Furthermore, we see that there is a difference in the treatment effect for boys and girls in the amount of household work done. The treatment effect is statistically significant for boys. Boys do household work less frequently if they are born after the parental leave reform in 1992. As these results are not accompanied by a total decline in household work, they suggest that it is the socialization mechanism that drives the results, i.e., that the increase in general parental leave reinforces traditional gender norms and propagates them across generations.

Table 5:

Effects of the 1992 Reform: Dependent Variables household_work (OLS, Columns 1 and 2) and nr_of_times (OLS, Columns 3 and 4)

 (1) (2) (3) (4) 
Variables household_work basic household_work by gender nr_of_times basic nr_of_times by gender 
Treatment .003 .032 -.023 .131 
 (.035) (.050) (.060) (.085) 
Boy  .013 -.028 .122 
  (.050) (.060) (.084) 
Treatment*Boy  -.065  -.300** 
  (.071)  (.120) 
Constant .816*** .812*** 1.036*** .960*** 
 (.025) (.036) (.050) (.056) 
Observations 482 477 477 477 
R-squared .000 .002 .001 .014 
 (1) (2) (3) (4) 
Variables household_work basic household_work by gender nr_of_times basic nr_of_times by gender 
Treatment .003 .032 -.023 .131 
 (.035) (.050) (.060) (.085) 
Boy  .013 -.028 .122 
  (.050) (.060) (.084) 
Treatment*Boy  -.065  -.300** 
  (.071)  (.120) 
Constant .816*** .812*** 1.036*** .960*** 
 (.025) (.036) (.050) (.056) 
Observations 482 477 477 477 
R-squared .000 .002 .001 .014 

*** p < .01 ** p < .05 * p < .1

Note: Robust standard errors in parentheses; all results are based on a +/- 3 months sample.

Finally, and in order to purge away the effects of the general parental leave increase from the effects of the 1993 daddy quota reform, we use the two reforms in a difference-in-differences estimation. Table 6 presents the results. Again we find a negative treatment effect on girls (column 2), as indicated by the Treatment-coefficient. The results suggest that girls in the treatment group are about 15 percentage points less likely to do household work. The positive interaction term for Boy*Treatment implies that the treatment effect is significantly (although at the 10% level in terms of statistical significance) smaller for boys than for girls, while the total treatment effect for boys is insignificant. The effect of the daddy quota on the amount of household work points in the same direction (columns 3 and 4), but the effect is not statistically significant.

Table 6:

Difference-in-Differences Regressions Comparing the Difference in 1993 to the Difference in 1992: Dependent Variables household_work (Columns 1 and 2, OLS) and nr_of_times (Columns 3 and 4, OLS)

 (1) (2) (3) (4) 
Variables household_work household_work by gender nr_of_times nr_of_times by gender 
Treatment -.081* -.148*** -.048 -.132 
 (.045) (.057) (.077) (.102) 
Boy* Treatment  .140*  .166 
  (.075)  (.131) 
Treatment_months .003 .025 -.018 .069 
 (.035) (.042) (.060) (.077) 
Treatment_cohort .082*** .107*** .059 .068 
 (.031) (.033) (.054) (.060) 
Boy* Treatment_months  -.051  -.177** 
  (.050)  (.086) 
Boy* Treatment_cohort  -.056  -.023 
  (.035)  (.068) 
Constant .816*** .819*** 1.018*** 1.022*** 
 (.025) (.025) (.042) (.042) 
Observations 1,102 1,093 1,102 1,093 
R-squared .009 .013 .002 .007 
 (1) (2) (3) (4) 
Variables household_work household_work by gender nr_of_times nr_of_times by gender 
Treatment -.081* -.148*** -.048 -.132 
 (.045) (.057) (.077) (.102) 
Boy* Treatment  .140*  .166 
  (.075)  (.131) 
Treatment_months .003 .025 -.018 .069 
 (.035) (.042) (.060) (.077) 
Treatment_cohort .082*** .107*** .059 .068 
 (.031) (.033) (.054) (.060) 
Boy* Treatment_months  -.051  -.177** 
  (.050)  (.086) 
Boy* Treatment_cohort  -.056  -.023 
  (.035)  (.068) 
Constant .816*** .819*** 1.018*** 1.022*** 
 (.025) (.025) (.042) (.042) 
Observations 1,102 1,093 1,102 1,093 
R-squared .009 .013 .002 .007 

*** p < .01 ** p < .05 * p < .1

Note: Robust standard errors in parentheses; all results are based on the +/- 3 months sample. The 1993 cohort is the reform cohort and is contrasted to the 1992 cohort. The first two columns present results after OLS regressions for the dependent variable household_work.

Conclusion

Gender inequalities in household work are a persistent feature across societies, even as women have dramatically increased their participation in the labor market. At the same time, there are cross-cultural differences, and over time, men have become more involved in household work and childrearing (Hook 2006). An important question is whether family policies affect the distribution of household work and thus partly explain the pattern of change over time. Furthermore, becuase gender attitudes are products of childhood socialization (McHale, Crouter and Tucker 1999), it is important to investigate the effects of family policy on children.

We exploit two Norwegian parental leave reforms to investigate their effects on adolescents' household work. Thus, we examine the long-run effects of the reforms on an important aspect of social change. In particular, we examine the effects of a parental leave reform that increased the parental leave time by 7 weeks, 4 of which were reserved for the father. This reform has been shown to equalize the distribution of household work between parents (Kotsadam and Finseraas 2011).

The nature of the reforms together with the specifics our data allows us to examine whether the reforms have a causal effect on household work. Building on a model contrasting within-family socialization of gender roles with the need for household work we are able to highlight some of the pathways for how and why these long-term effects may be observed. In particular we hypothesize that the more equal division of household work is being transmitted to the next generation as parents either transfer their norms and practices to their children, thus reducing the gender gap in household work among adolescents, or that the need for children's household work is reduced as the father now does more or both. Hence, the degree to which the effects of the reform are gendered allows us to draw conclusions about the mechanisms.

We find a robust and substantial effect of the daddy quota reform in 1993. Girls born immediately after the reform are less likely to be involved in household work. For boys we find either a much less pronounced effect or no statistically significant effect. We reveal a similar, although not statistically significant, effect on the number of times household work was conducted in the previous 7-day period.

When analyzing the 1992 reform—which increased the parental leave period, but did not include a daddy quota—we find no effects on the probability of doing household work, and yet we do find that boys do household work less frequently if born just after the reform. Thus, the gendered pattern of household work was strengthened, which is to be expected because the reform reinforced traditional gender roles by increasing the time mothers spend at home.

By using a difference-in-differences estimation strategy where we analyze the effects of the two reforms simultaneously, we are able to isolate the effects of the daddy quota from the coinciding increase in the parental leave period. The results strongly suggest that the introduction of the daddy quota lowered the probability of girls doing household work. At the same time, we find no effects of the daddy quota on the frequency of household work.

Together, the results suggest that the daddy quota equalizes the probability of doing household work between the genders, while the effect on the number of times per week that boys do household work is uncertain. Regarding mechanisms, the results therefore indicate that the need for housework theory and the socialization theory combined best explain the observed pattern. The results further indicate that the daddy quota is most affecting households where the parents have a low propensity to ask adolescents to do housework at all. One possible interpretation of this finding is that it indicates heterogeneity in the treatment effect between socioeconomic groups, but our small sample size impedes us from analyzing this possibility further.

In the causal inference terminology, our estimates are “intention to treat” estimates and are thus measures of the total direct effects of the policy. Hence, the estimates do not give us the effects of parents taking out more leave; rather they show the effects of parents being offered more leave. Because the policy changes induced parents, and in particular fathers, to take more parental leave, the estimates show the average effects of such incentivizing, taking into account that not all people respond to such incentives equally. In addition to the direct effects induced by the policies, it is likely that the reforms affected both children born before and after the policy changes, as well as their parents. In particular, the policies are normative and signal what society thinks is right. As the parents and children in the treatment and control group interact across the groups, the practices induced by the reform might spread from one group to the other. The total direct and indirect effects of the policies are therefore likely to be even larger than what is captured here.

The article contributes to several different academic literatures. First, our results speak to the large sociological literature on the effects of parental leave on gender equality (e.g., Fuwa and Cohen 2007; Gornick and Meyers 2008; Hook 2006, 2010; Ruppander, 2010) by identifying a causal effect of paternity leave on the gender gap in adolescents' household work. Second, the results contribute to a small but growing literature investigating children's household work (e.g., Dauphin et al. 2011; Salman Rizavi and Sofer 2010) by illustrating the importance of public policy. Third, the article identifies a long-run effect of parental leave. Although previous studies using parental leave reforms have focused on cognitive effects on the children (Baker and Milligan 2010, 2011; Cools, Fiva and Kirkebøen 2011; Dustmann and Schonberg 2008), our study extends the outcome set of interest to also include social variables.

Fourth, our results indicate that policy changes can have intergenerational effects. Intergenerational transmission of values and attitudes has been argued to be important in explaining fertility patterns and the increasing labor market participation of women (e.g., Blau et al. 2008; Blau, Kahn and Papps 2011; Fernández 2007a, 2007b; Fernández and Fogli 2006, 2009; Fernández, Fogli and Olivetti 2004). Finally, the article shows that policy may affect cultural change and is in fact susceptible to rather small policy changes.

Future studies are needed to show under which contexts and policies transformative effects are most likely to occur. Other outcome variables, such as attitudes, should also be investigated to grasp the total societal effects of the reforms. Furthermore, our evidence regarding mechanisms is admittedly somewhat indirect, and our sample size restricts us from conducting rigid analyses of heterogeneity in treatment effects across groups. In particular, it would have been useful to have more information on the parents than we have in our data. To gain greater knowledge about the mechanisms, we urge researchers to collect data that include information on both parents and children (containing their exact birth dates), their attitudes and actual behavior.

Notes

1
A plausible interpretation of the different findings is that although Kotsadam and Finseraas (2011) rely on survey data on household division of labor, Ekberg, Eriksson and Friebel's (2006) proxy for household work—leave to take care of sick children—also involves a relationship with employers.
2
Income compensation had a ceiling of six times the so-called base amount of the Norwegian social insurance system. The base amount is adjusted on a yearly basis and was 36,167 NOK (about 6,300 USD) in 1992. Most employers compensate for the amount above the ceiling.
3
Parents could choose to either take the 42 weeks with full compensation or 52 weeks with 80 percent earnings compensation.
4
Recoding the amount of household work into a categorical variable (none, low amount, high amount) produces similar results.
5
The conclusions remain if we include age squared. The same is true if we include flexible specifications for age in days and birth month fixed effects (results are available upon request).
6
The Norwegian Government first proposed introducing a daddy quota of 4 weeks in the state budget for 1993, which was accepted by the parliament on November 4, 1992 (Budsjett-innst. S. nr.2 1992-1993). At this time, however, the exact date of implementation was not known.
7
In some specifications, the full vector of controls is included and the model is then not fully saturated (as we do not include all possible interaction terms). However, as identification is not based on the conditional independence assumption, these results are only included to show the robustness of the results.
8
Similar to the daddy quota reform, the 1992 reform was announced very close to its implementation (it became publicly known in October 1991). Hence, the children born around the reform date were already in utero at the time of the announcement.
9
Keep in mind that the difference between treated boys and boys in the control group, and the accompanying significance test, is not directly observable in Table 4. We have therefore re-estimated the model with boys in the control group as the reference category to get a direct estimate of this difference. The resulting table is available upon request.
10
The number of observations drops slightly when we include the full set of control variables. All substantive conclusions remain if we impute missing data to avoid the potential bias from Listwise deletion of missing data (results available upon request).

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Author notes

The paper has benefited from comments by seminar participants at Stockholm University, University of Oslo, the Institute for Social Research and the 2011 national conference for Swedish economists at Uppsala University. In addition, we thank Jon-Ivar Elstad, Niklas Jakobsson, Edwin Leuven, Mette Lovgren and Viggo Nordvik for useful comments, and Kieu Thanh Thi Do for excellent research assistance.

Supplementary data