Marco Caliendo
email: caliendo@iza.org.

Katharina Wrohlich
email: kwrohlich@diw.de.

Silke Anger

Peter Haan

Benjamin Price

Jürgen Schupp

Viktor Steiner

Evaluating the German "Mini-Job" Reform Using a Natural Experiment

Keywords: Evaluation, Natural Experiment, Difference-in-Differences, Marginal Employment Evaluation, Natural Experiment, Difference-in-Differences, Marginal Employment. JEL Classification: C25, H31, J68

Evaluating the German "Mini-Job" Reform Using a

Natural Experiment

Introduction

As a response to persistently high unemployment rates, especially of low-skilled people, wage subsidies have been intensively discussed in European countries. Following the example of the Earned Income Tax Credit (EITC) introduced in the 70s in the US (see, e.g., [START_REF] Scholz | In-Work Benefits in the United States: The Earned Income Tax Credit[END_REF], several European countries have introduced in-work benefits, tax credits, or subsidies to social security contributions (SSC) for working individuals. Examples are the Working Family Tax Credit (WFTC) in the UK (see, e.g., [START_REF] Blundell | The Labour Market impact of the Working Families Tax Credit[END_REF] and the French Prime Pour l'Emploi (see, e.g., Stancanelli, 2005). 1 The "Mini-Job" reform introduced in Germany in 2003 had a similar motivation. The main objective of this reform was to provide positive work incentives for people with low earnings potential by subsidising social security contributions. The government expected to achieve that goal by exempting labour income up to 400 euro from employees' SSC and introducing a degressive subsidy for earnings between 401 and 800 euro. To be specific, this reform included three major changes compared to pre-reform regulations. First, the maximum amount for earnings exempted from SSC was increased from 325 to 400 euro. Jobs with earnings less than this threshold (marginal employment) are from then on labeled mini-jobs. Second, the previous maximum hours restriction (15 hours per week) was abolished. Third, income up to 400 euro per month from a mini-job held as a secondary job, which was fully taxable before the reform, is now exempted from SSC and income tax. 2 The expected labour supply effects of wage subsidies, which consist of the effect on the participation as well as on the hours worked, depend on the design of the policy instrument and on various other institutional and economic factors (see, e.g., [START_REF] Blundell | Work Initiatives and 'in-work' Benefit Reforms: A Review[END_REF], or Moffit, 2003). The expectation of unambiguously positive effects on labour force participation is based on two conditions. First, the subsidies have to be targeted at individual income rather than household income, and second, the reform has to change the incentives to take up work for recipients of unemployment benefits or other social transfers. The subsidies under the German "Mini-Job" reform are indeed targeted at the individual level; however, the budget constraint for recipients of social transfers hardly changes due to strict withdrawal of earnings, as is shown in Steiner 1 For a detailed overview of recent European "Making Work Pay" policy reforms, see [START_REF] Orsini | Tax-Benefit Reform and the Labor Market: Evidence from Belgium and other EU countries[END_REF]. 2 See Steiner and Wrohlich (2005) for a more detailed description of the reform. Note that the reform did not change employers' SSC except for mini-jobs in private households. Hence, there is no reason for a marked increase in the overall demand for marginal employment. and Wrohlich (2005). Additionally, it should be noted, that without a minimum hours restriction, the reform provides subsidies for all kinds of low-earnings jobs, whether low earnings result from low wages or short working hours. Hence, the reform cannot be directly compared to programmes such as the WFTC. The differences between the "Mini-Job" reform and the other mentioned reforms are even more pronounced when one looks at the incentives to take up a secondary job. After the reform, earnings from a secondary job-defined as a job which is held in addition to a primary job bound to social security contributions-are not only exempted from social security contributions but also from the income tax. Thus, incentives to take up such a job have markedly increased.

Already very shortly after its introduction, the "Mini-Job" reform was portrayed by different official sources as quite successful in generating new employment. The Federal Ministry of Health and Social Affairs stated in July 2003 that three months after the reform, 930,000 new jobs had been created. 3 These numbers were corrected by the Federal Employment Agency in November 2003, who stated that one month after the reform, there was an increase in marginal employment of as high as 79,000 individuals and an increase of secondary jobs by 580,000. However, it is not clear whether this increase is causally related to the reform, since based on the theoretical reasoning above-if at all-only small effects can be expected. Hence, an ex-post evaluation is called for. This is an especially difficult task here, since from 2004 onwards various other legal changes have been introduced which might affect labour supply decisions of individuals simultaneously. Therefore, it should be obvious that a comparison of the mini-jobs realised in 2004 with pre-reform numbers will not reveal the true effect of the reform. Furthermore, in contrast to other evaluation studies of labour market policies, the distinction between control and treatment groups is not initially clear, since the reform is relevant for the whole population. A thorough evaluation has to take these points into consideration and should be based on a credible identification strategy. We will do so by using the exogenous variation in the interview date of the German Socio-Economic Panel (SOEP). The interviews are conducted between January and October in each year. Since the reform was introduced on April 1, 2003, we observe some people who are interviewed before the reform and others interviewed after the new legislation was implemented. This allows us to estimate the immediate short-run effect of the reform. To account for seasonal variation, we additionally use a difference-in-differences approach.

Our results show that, although there has been a rise in marginal employment after the introduction of the "Mini-Job" reform, this rise cannot be causally related to the reform. In the short run, we do not find a significant effect of the reform on marginal employment. However, we do find evidence for a positive effect on secondary job-holding for single men. We will explain our identification strategy in more detail in Section 2, where we will also describe the data used for the analysis. Section 3 contains the estimation results, before Section 4 concludes.

Evaluation Strategy and Data

Our empirical analysis is based on the German Socio-Economic Panel (SOEP), a sample gathering socio-demographic and financial information about 12,000 representative households each year. We will use the waves for the years 2002 and 2003. The individuals are interviewed in person from January until October each year. 4 Our identification of the treatment effect of the reform will be based on this exogenous variation in the interview month.

Evaluation Design

As already mentioned we want to evaluate the effects of the reform on some outcome Y , for example, the probability of beginning a mini-job for certain groups of the population. In the usual microeconometric evaluation framework (the "potential outcome approach", most commonly called the [START_REF] Roy | Some Thoughts on the Distribution of Earnings[END_REF][START_REF] Rubin | Estimating Causal Effects to Treatments in Randomised and Nonrandomised Studies[END_REF] The "Mini-Job" reform was introduced on April 1, 2003, and applies to the whole population. Hence, we have no direct treatment group which has received the treatment and whose outcome we could compare with a control group who did not receive the treatment. 5 The whole population before April 1, 2003, was not affected by the reform, while the whole population after April 1, 2003, was affected by it. It should also be noted that the whole population was (not) affected by the reform in 2004 (2002).

Comparing the outcomes between these two years (Y 1 2004 -Y 0 2002 ) will not give us the actual treatment effect, since other regulations were also changed. Most significant of these were changes in the income tax as part of the German Tax Reform. From 2003 to 2004, the basic allowance was increased from 7,235 to 7,664 euro per year, the tax rate of the first tax bracket was reduced from 19.9 to 16.0 percent, and the top tax rate was reduced from 48.5 to 45.0 percent. Clearly, this reform also affected labour supply decisions of individuals with low earnings. 6

However, the timing of the SOEP interviews gives us an opportunity to identify the true treatment effect. As mentioned above, the SOEP interviews are conducted between January and October of each year. We argue that the random variation of the interviews mimics a natural experiment, where we can compare the effects for the group of participants, i.e. the people who were interviewed when the reform was already implemented in t 2003 , with the group of controls, i.e. the people who were interviewed before the reform was implemented in t 2003 7 :

∆ = Y 1 2003 -Y 0 2003 . (1)
Most of the interviews are accomplished within the first quarter. In fact, by default households are contacted by the interviewers in the first quarter of each year. If this contact is not successful, whether because no one is at home or the household has moved to another address, households are contacted again in the second quarter of the 5 Recent examples for evaluation studies with a 'classical' distinction between treatment and control groups can be found in [START_REF] Andren | Assessing the employment effects of vocational training using a one-factor model[END_REF], [START_REF] Fertig | The effectiveness of qualification measures for employed workers -an evaluation study for Saxony[END_REF] or [START_REF] Caliendo | Identifying Effect Heterogeneity to Improve the Efficiency of Job Creation Schemes in Germany[END_REF].

6 For a detailed description and an estimation of labour supply reactions to this tax reform see [START_REF] Haan | Distributional Effects of the German Tax Reform 2000 -A Behavioral Microsimulation Analysis[END_REF]. They show that total hours worked increase by about 1% due to this reform.

7 The superscript behind year information indicates the first quarter of the year, year information without superscript indicates quarters 2-4. A problem which might arise with this approach are potential differences in unobserved characteristics (UC) between individuals interviewed before April and those interviewed after April as well as seasonal employment effects (SEE). If employment in the mini-job sector varies heavily within a year or if the two groups differ in unobserved characteristics the above-mentioned approach becomes invalid since

Y 1 2003 -Y 0 2003 = ∆ + SEE + U C. (2)
To account for these potential sources of bias, we apply a control mechanism based on the difference-in-differences (DID) approach9 , using the seasonal variation and un- The treatment effect is then given by (see also Figure 1):

∆ = (Y 1 2003 -Y 0 2003 ) -(Y 0 2002 -Y 0 2002 ). ( 3
)
Since we are using cross-sectional information from two waves of the SOEP, the populations in 2002 and 2003 as well as the populations in the first and subsequent quarters might not be the same. To account for variations in observable characteristics, we specify the outcome variable Y in a parametric way and estimate the effect on the whole sample with interaction effects.

The equation we will estimate can be specified as

y * i = β 1 * d2003 i + β 2 * af ter i + β 3 * d2003 × af ter i + γ X i + ε i , (4)
where y * i is a latent variable such as the propensity to be marginally employed or to hold a secondary job (the outcome variables will be specified in more detail in Section

1.4 1.1 1.1 1.1 2003 SOEP-Interview Month 0 2003' Y 0 2002 Y 0 2002' Y 1 2003 Y 2.2), d2003 i is a dummy variable indicating whether individual i is observed in 2003,
af ter is a dummy variable indicating whether individual i is observed after the first quarter of a year, and d2003 × af ter is an interaction term of these two variables.

Vector X i summarises control variables such as age, education, family status, number of children, health status, etc., and ε i is an unobserved error term. The βs and the vector γ include the respective coefficients. We are particularly interested in β 3 , which yields the causal effect of the reform. Since we do not observe the latent variable y * i , but the binary outcome variables y i , we will estimate equation ( 4) using a probit model. The marginal effect corresponding to the coefficient β 3 can thus be interpreted as change in the probability of the outcome variable (e.g. marginal employment) due to the reform.

It might be argued that this evaluation design leads to a downward bias of our results since the "Mini-Job" reform has been announced a few months before its introduction. Thus, individuals might have started to search for a job already before April 2003. We argue, though, that even if people started to search for a job before April 2003 there was no incentive to start the job before April 1st under the old legislation.

Thus, when asked about their employment status, we do not expect an effect for those individuals interviewed before April 1st, 2003. We are interested in two outcome variables, namely the probability of being in marginal employment ("geringfügige Beschäftigung") and the probability of having a secondary job ("Nebenerwerbstätigkeit"), since the incentives to take up these two types of jobs have been changed by the "Mini-Job" reform. Examining the effects on secondary job holding seems to be especially relevant, since there is evidence that the strong increase in mini-jobs after the introduction of the reform was not caused by new jobs taken up by individuals who were previously not employed. Instead it is likely that a share of the new mini-jobs were jobs taken up by individuals who had already been working.11 Thus, in addition to the analysis of marginal employment, we are particularly interested in the effect of the reform on secondary job holding. Furthermore, we also analyse the effect on the labour supply of students. This group was even more affected by the reform, because the SSC-exemption threshold is at the same time the exemption limit of earned income for recipients of student aid. 12In the SOEP data, there are several questions containing information about employment status, working hours, earnings, and job characteristics. We use the following definitions for the two outcome variables of interest. An individual is defined to be in marginal employment if -the answer to employment status is "marginally employed", or -the answer to employment status is "part-time employed" and gross monthly earnings are reported to be less than 400 euro, or -the answer to job characteristics is "this job is a 325 euro/400 euro Job", or -the answer to employment status is "not working" and the individual reports having a secondary job with gross monthly earnings less than 400 euro.

Note that we use the post-reform threshold of 400 euro for all individuals (interviewed before and after the reform), since we are not interested in redefinitions of already existing jobs. Relating to the second outcome variable, we define an individual as holding a secondary job if -the answer to employment status is "full-time employed" or "part-time employed" and the individual reports gross monthly earnings from regular or irregular secondary jobs less than 400 euro.

Table 1 shows the total number of observations in the four subsamples, interviewed before and after April 1st in 2002 and 2003, respectively. To analyse the changes with respect to marginal employment we look at the whole population, whereas we focus on individuals who are full-or part-time employed to analyse secondary job-holding.

For both analyses we focus on individuals aged between 16 and 70 years.

Results of several ex-ante evaluation studies (see [START_REF] Haan | Distributional Effects of the German Tax Reform 2000 -A Behavioral Microsimulation Analysis[END_REF]Wrohlich, 2005, or Bargain, Caliendo, Haan, and[START_REF] Orsini | Tax-Benefit Reform and the Labor Market: Evidence from Belgium and other EU countries[END_REF] have shown that the reaction to the reform differs between population subgroups. For example, women in couple households have been shown to adjust their labour supply to a greater extent than men. Therefore, we differentiate between several subgroups in our analysis. In particular, we run separate estimations for men, women and students and include interaction terms for individuals living in single and couple households. women than men, whereas the opposite is true for secondary job holding. Additionally, marginal employment is higher in the second and third quarter of both years when compared to the first quarter. Furthermore, it is interesting to note that we observe an increase in marginal employment from the first quarter of 2002 to the first quarter of 2003.

Before we turn to the estimation results, we look at some descriptives of the covariates used in the estimations. Thereby we differentiate the four subsamples under consideration. As can be seen from Table 1, there are far fewer observations in the two subsamples "interviewed after April 1st", which is due to the interview routine of the SOEP already described. Therefore, the group of individuals interviewed after April 1st might be systematically different from those interviewed in the first three months.

0 : (X 2003 -X 2003 )-(X 2002 -X 2002 ) = 0.
Note that-as already discussed-even if the "after" groups differ systematically from the "before" groups with respect to unobservable characteristics, this does not flaw our results as long as we assume that the differences are the same in 2002 and 2003. The only assumption that needs to be valid for our study is that the interview month of the 2003 wave is independent of the introduction of the "Mini-Job" reform on April 1, 2003. We tested the significance of the differences across the four subsamples using a t-test of mean equality. Thereby we tested the hypothesis that the difference-indifferences of the covariates equals zero, i.e., H 0 : 2 shows that the differences are in fact not different from zero for most of the variables. Exceptions (at the 5%-significance level) are the marital status, living in East Germany 13 and children under 15. To take care of these small remaining differences, we control for the covariates in the parametric estimation of the treatment effect in the next section.

(X 2003 -X 2003 )-(X 2002 -X 2002 ) = 0.

Results

Since we expect different effects for men and women as well as for students, we perform separate analyses for these groups. For men and women, we run estimations for two outcome variables, namely marginal employment (Section 3.1) and secondary job holding (Section 3.2). For students we combine these two outcome variables into one due to the limited number of observations (Section 3.3). For all subgroups and outcome variables, we run three probit estimations, respectively. The first estimation is only for the year 2003, and includes a dummy indicating "interviewed after April 1st" as a single explanatory variable. This corresponds to the "raw" effect of the reform, without controlling for potential seasonal effects or possible differences in observable or unobservable characteristics between individuals interviewed in and after the first quarter of 2003. In the second estimation, we control for differences in observable characteristics by including a set of control variables such as age, educational variables, regional variables, marital status, and number of children. Finally, in the third estimation we pool data from 2002 and 2003, and include two more variables, a dummy indicating the year 2003 and an interaction term between this year dummy and the "interviewed after April 1st" dummy (see equation 4). Note that this variable measures the effect that the "Mini-Job" reform had on the outcome variable, controlling for seasonal effects, observable and time-invariant unobservable characteristics that differ between the groups interviewed in and after the first quarter of each year.

13 Given the differences in this variable, we have also performed the analysis separately for East and West Germany, which did not yield different results from the ones we will present in the next section.

Effects on Marginal Employment

Table 3 shows a short summary of the estimation results for marginal employment, where we have displayed marginal effects. Full estimation results, including the coefficients and standard errors of the control variables, can be found in Table A.1 in the Appendix. For men, the first model indicates that the "raw" effect of the reform is positive, i.e. in the second and third quarter of 2003 we observe more men in marginal employment than in the first quarter of 2003. This is still true if we control for differences in observable characteristics, as can be seen from column 2. This is in line with the descriptive statistics showing a post-reform increase in marginal employment.

However, to answer the question whether this increase is causally related to the reform we have to look at the third column. The third column shows the estimation of the pooled sample of 2002 and 2003 including a dummy variable indicating the year 2003, and an interaction term of this dummy with the dummy indicating "interviewed after the reform". We further interacted this variable with the "single" dummy, because ex-ante studies have shown different reactions to the reform by singles and individuals living with a partner. Doing so allows us to calculate marginal effects for singles and couples separately. 14 Our results show, that as far as the probability of being marginally employed is concerned, neither single men nor men living in couples react to the reform.

Similar to what we observe for men, we find a positive and significant "raw" effect of the reform for women (see column 4). This effect disappears, however, once we control for socio-demographics (column 5) and for differences in seasonal employment effects and unobservable characteristics between the "before" and "after" samples (column 6). Note that in the full model presented in column 6, the coefficients of the variables af ter and d2003 are positive and significant, indicating that for women the probability of being marginally employed is higher in the second and third quarter of each year, and that this probability is also higher in 2003. However, there is no causal effect of the reform, which would be caught by the effect of the variables af ter × 2003 and 14 Note that the marginal effect of the interaction term is not equal to the magnitude of the interaction effect in non-linear models (see [START_REF] Ai | Interaction terms in logit and probit models[END_REF]. In order to calculate the absolute treatment effect for couples and singles, we use the following formula: Φ(

β af ter + β 2003 + β af ter2003 + γ X) -Φ( β af ter + γ X) -Φ( β 2003 + γ X) + Φ( γ X)
where Φ is the cdf of the normal distribution. For singles, the marginal effect corresponds to Φ( af ter × 2003 × single (see Table A.1 in the Appendix). To check whether certain subgroups of the population were particularly affected by the reform, we have, for example, also included interaction terms of af ter × 2003 and low -skilled in separate estimations. However, we did not find any significant effects. 15 Moreover, we evaluated the marginal effects not only at the sample mean, but also for several subgroups (e.g.

β af ter + β 2003 + β single + β af ter2003 + β af ter2003single + γ X) -Φ( β af ter + β single + γ X) -Φ( β 2003 + β single + γ X) + Φ( β single + γ X).
with respect to education, marital status and number of children) which did not change our results.

Thus, our first conclusion is that in the short-run (defined as about two months after the reform), there has not been a significant change in marginal employment that could be causally related to the legislation introduced on April 1st, 2003. However, at least for women, marginal employment seems to be higher in the summer months than in winter and higher in 2003 than in 2002.

Effects on Secondary Job Holding

Let us now turn to the analysis of the probability of holding a secondary job. As already explained above, for these estimations we focus on the sample of full-time or 15 These estimation results are available on request from the authors. 4 (column 1) shows, there seems to be no significant "raw" effect of the reform for men, as the share of men holding a secondary job does not differ between the first and the subsequent quarters of 2003. 16 This is also true if we control for differences in observed characteristics (column 2) and for differences in seasonal employment effects and time-invariant unobserved characteristics (column 3). However, as the results of this estimation show (see Table A.2 in the Appendix), we do find a positive effect for single men that is significant at the 10 percent level. The marginal effect corresponding to this coefficient amounts to 0.031. This implies that for single men, the probability of having a secondary job increases by 3.1 percentage points. Since the probability of holding a secondary job before the reform for single men is 3.7 percent, this effect almost implies a doubling of secondary employment in this group. However, the standard error of the marginal effect amounts to 0.0198. 17

The marginal effect is thus not significant at the 10 percent level, the empirical significance level amounting to 11.5%. Given the economic significance of the effect and the 16 Full estimation results can be found in Table A.2 in the Appendix. 17 Statistical (non)significance of the estimated coefficient of the interaction term does not necessarily imply (non)significance of the marginal effect of this variable in non-linear models (see [START_REF] Ai | Interaction terms in logit and probit models[END_REF]. relatively limited number of observations, we would not conclude from the standard error that the reform did not affect this group, but rather that there is evidence for a positive effect on secondary employment of single men. As columns 4 to 6 of Table 4 show, we do not find a corresponding effect for women. 18

Effects for Students

The estimation results for students can be found in Table 5. 19 Similar to what we found for women with respect to marginal employment, for students there is a positive and significant "raw" effect of the reform. Students in the second and third quarter of 2003 are more likely to be observed in marginal employment or holding a secondary job than in the first quarter of 2003. This is still true once we control for socio-demographic characteristics. The differencein-differences model, however, shows that there is no causal effect of the reform, even

18 Once again we evaluated the marginal effects also for several subgroups. In none of these cases we could find a significant effect.

19 Table A.3 in the Appendix contains the total number of observations for this group as well as the numbers on being marginally employed and/or holding a secondary job. Due to the limited number of observations we pooled male and female observations and included a control variable for gender. Full estimation results can be found in Table A.4 in the Appendix. To sum up, we find that in the short run, there is evidence that the reform had a causal effect for single men, whose probability of having a secondary job increases by about three percent. According to our estimation results, the reform had no causal effect on marginal employment in any of the subgroups, although we do find a general rise in marginal employment in the second quarter of 2003 as compared to previous periods.

Conclusions

The aim of this paper was to evaluate the causal effect of the German "Mini-Job" reform from 2003 on the probabilities of being in marginal employment or of having a secondary job. Based on our identification strategy, we were able to identify the shortrun effects of the reform. Disentangling seasonal or cyclical trends from causal effects is a major requirement in order to draw policy-relevant conclusions. For example, we find that for women and students marginal employment is higher in the summer months (compared to the first quarter) and in the year 2003 (compared to the year 2002). This increase might have been reflected in the numbers-a short-run increase of 79,000 jobs-reported by the Federal Employment Agency. However, we show that this increase can not be causally related to the reform. As far as secondary jobs are concerned, our results differ to a much larger extent from the numbers published by the Federal Employment Agency. We only find evidence for a positive reaction to the reform among single men, whose probability of having a secondary job increases. However, this can not explain the total increase of 580,000 secondary jobs stated above. We believe that a large fraction of these "new" jobs are actually redefinitions of previously fake/false self-employment, i.e., a situation where a self-employed individual is actually dependent on one company for (most of) her income. This effect cannot be identified with the SOEP data. The same is true for turning illegal jobs into legal employment (see also [START_REF] Schupp | Kleine Beschäftigungverhältnisse: Kein Jobwunder[END_REF]. All ex-ante evaluation studies using behavioural microsimulation models predict similar effects from the "Mini-Job" reform suggesting only very moderate participation effects and even negative effects on working hours. 21 They do find a small yet significant effect on the labour force participation of women living in couple households. As described above, we do not find a significant effect on the participation in marginal employment in the short-run. However, since the effects that are calculated with ex-ante microsimulation techniques correspond to long-term effects, our results need not necessarily be a contradiction to this literature.

Even though our results only reflect the short-run effects of the "Mini-Job" reform, they are in line with what could be expected according to its set-up. As we have pointed out, the reform was not explicitly targeted to subsidize employment in the low-wage sector since there is no minimum hours restriction. Moreover, working incentives for individuals receiving unemployment benefits or social assistance have hardly been changed due to the strict withdrawal rate of earnings. The largest change was actually the exemption from income taxation for earnings up to 400 Euro from a secondary job.

Hence, it is also questionable whether the reform will achieve its objective-to provide positive work incentives for people with low earnings potential-in the long-run.

21 See e.g. Steiner and Wrohlich (2005), [START_REF] Arntz | Die Arbeitsangebotseffekte der neuen Mini-und Midijobs -eine Ex-Ante Evaluation[END_REF] or [START_REF] Bargain | Making Work Pay' in a Rationed Labour Market[END_REF].

Reply to the comments on "Evaluating the German Mini-Job Reform Using a Natural Experiment"

First of all, we would like to thank the referee for his/her valuable comments which helped to improve the paper. We will explain below in details how we incorporated the suggestions or indicate why we did not do so.

Major Comments

(1) Given the setup of the reform, one of its main effects should be that all existing employment contracts are changed and split in two parts, with a small part of 400 Euros being freed of income and social security taxes. This is not discussed (though briefly mentioned on the bottom of p.8) nor analyzed in the paper. Why not?

We discuss that now in more detail on page 8f. In fact, our analysis of secondary job holding is especially designed to detect such effects.

(2) The authors' conclusions are predominantly based on observations in month 1 and 2 after the reform. It seems questionable that the effects of the reform are realized this fast given search, information, and administrative requirements connected to hiring. Are there any institutional reasons for not looking at the evidence of 2004? this might be a valuable addition.

Unfortunately, we cannot use information from the year 2004 for our analysis, since from 2004 onwards various other legal changes have been introduced which might affect labour supply decisions of individuals simultaneously. Most significant of these were changes in the income tax as part of the German Tax Reform, increasing the basic allowance and decreasing the initial tax rate (see page 5 for more details).

(3) If individuals who cannot be interviewed in the first quarter of the year systematically and in unobservable ways differ from others and if these differences are correlated to their response to the reform, the estimates are biased. The authors should explicitly state their assumption that the reform effect is identical for all, once the quarter of observation is conditioned out. Particularly in this application this assumption might matter, as those working on second jobs should be less likely to be met at home by interviewers. It is therefore not certain that the variation of interview months is random, as stated on p.5.

We discuss that in detail on page 6f. "A problem which might arise with this approach are potential differences in unobserved characteristics (UC) between individuals interviewed before April and those interviewed after April […]". To account for these differences we apply a control mechanism based on the difference-in-differences (DID) approach. "Clearly, this assumption is only valid if both patterns have not changed over the two years, such that SEE2003 = SEE2002 and UC2003 = UC2002".

(4) The treatment of single vs. married vs. couple status of individuals is confusing. (a) Table 2 might present the test of mean equality also for the omitted category.

We present that now, see page 10. (b) The estimations use one omitted category for the level effects and a different one for the treatment effects. The discussion covers absolute effects without referring to reference groups. It should be clarified wether the estimates show the difference between singles and non-married couples or whether they discuss the absolute level of effects for singles. The marginal effects presented in Table 3 refer to absolute effects for singles and couples, as we explain in footnote 14. (c) It might be of interest to -at least in a footnote -present the joint treatment effect (for singles and couples) and its significance instead of only presenting model 3.

We present the joint treatment effect now in the tablenotes to Tables 3 and4. It is insignificant in both cases. (5) The authors should explain their computation of the marginal effect as presented in footnote 13 (e.g. by referring to equation 3). [START_REF] Ai | Interaction terms in logit and probit models[END_REF] show, that the magnitude of the interaction effect in non-linear models does not equal the marginal effect of the interaction term. Thus, we calculate the interaction effect using the formula stated in footnote 14 (formerly 13). We have clarified that in this footnote, see page 12.

Minor Comments

(1) Some references to the German institutional background are difficult to understand: explain "fake self-employment" (p.16).

We have rephrased that. (2) Is the Orsini 2006 reference cited in the paper?

Yes, in footnote 1 on page 1. (3) Some typos -middle of p2 "maximum hours restriction" -top of p5 "groups which" -top of p8 "the strong increase ... was"

We have corrected all typos.

  model), the treatment effect ∆ is given by a comparison of the treatment outcome (Y 1 ) with a hypothetical situation where the same individual does not receive treatment (Y 0 ), i.e.: ∆ = Y 1 -Y 0 . The fundamental evaluation problem arises because we can never observe both potential outcomes for the same individual at the same time. A simple comparison between outcomes of treated and untreated individuals is not possible if they are selective groups, that is when the condition E(Y 0 | D = 1) = E(Y 0 | D = 0) , where D is a binary treatment indicator. Let us transfer this general framework to our evaluation question, before we present our identification strategy.

  on. Since on average most of the post-reform interviews are completed by May 2003 8 , it should also be clear that we are only able to estimate the immediate short-run effects of the reform.

  observed differences in the year 2002 to account for the seasonal variation and unobserved differences in 2003. Clearly, this assumption is only valid if both patterns have not changed over the two years, such that SEE 2003 = SEE 2002 and U C 2003 = U C 2002 . 10

Figure 1 :

 1 Figure 1: Definition of the Subsamples According to the SOEP Interview Month

  Variables, Subgroups and Some Descriptive Statistics

  Looking at the p-values in column 5 of Table

  The corresponding standard errors are calculated using the Delta method.

  employed individuals only. As Table

  of being marginally employed or holding a secondary job is higher in 2003 and in the second and third quarter of each year.20

Table 1 :

 1 Number of Observations, Marginal and Secondary Employment in the Subsamples

	Marginal	Secondary

Source: SOEP, waves 2002 and[START_REF] Moffitt | Welfare Program and Labor Supply[END_REF]

Table 2 :

 2 Some Descriptive Statistics -Differentiated by Interview Date

		2002		2003		Test of
		Before	After	Before	After	mean equality 1
		April 1st April 1st April 1st April 1st	(p-value)
	Age	43.62	41.22	43.64	41.61	0.088
	Female	0.512	0.518	0.515	0.515	0.323
	No Educational Degree	0.017	0.026	0.018	0.024	0.205
	High School Degree	0.201	0.240	0.207	0.243	0.327
	Vocational Training	0.658	0.618	0.657	0.615	0.389
	Academic	0.170	0.191	0.172	0.186	0.197
	Disabled	0.096	0.074	0.095	0.078	0.204
	Married	0.640	0.613	0.623	0.625	0.000
	Single	0.170	0.183	0.175	0.178	0.087
	Cohabiting Couple	0.203	0.223	0.214	0.219	?!?
	German	0.919	0.864	0.923	0.862	0.176
	Living in East Germany	0.285	0.139	0.290	0.105	0.000
	Children under 15	0.329	0.357	0.318	0.361	0.046

Source: SOEP, waves 2002 and 2003. 1 p-values refer to a test of the following hypothesis: H

Table 3 :

 3 Estimation Results (Marginal Effects) -Marginal Employment Model 3 has also been estimated without the interaction term 'after×2003 (Singles)'. The marginal effect for men is 0.0084 (s.e. 0.0065), for women -0.0105 (s.e. 0.0094). Covariates include: age, age 2 , no education, high school degree, vocational training, academic, disabled, married, single, german, number of children in different age classes, and a dummy for living in East Germany. See also Table A.1.

	Variable		Men			Women
		Model 1 Model 2 Model 3 (a) Model 1 Model 2	Model 3 (a)
	after	0.0108* 0.0132**	0.0036 0.0246***	0.0062	0.0171**
		(0.0059) (0.0055) (0.0045)	(0.0093) (0.0087)	(0.0080)
	d2003			0.0045*			0.0195***
				(0.0024)			(0.0041)
	after×2003 (Couples)			0.0090			-0.0092
				(0.0067)			(0.0108)
	after×2003 (Singles)			0.0145			-0.0158
				(0.0135)			(0.0247)
	Controlled for Covariates	no	yes	yes	no	yes	yes
	Log-Likelihood	-1666.813	-1529.5	-2919.3	-3829.5	-3664.7	-7183.4
	Observations	8,907	8,907	18,154	9,444	9,444	19,215
	Note: ***/**/* indicates significance at the 1%/5%/10% level. Standard errors (in parentheses) correct
	for correlation across repeated observations of individuals.
	(a)

Source: Estimations based on SOEP, waves 2002 and 2003.

Table 4 :

 4 Estimation Results (Marginal Effects) -Secondary Employment

	Variable		Men			Women
		Model 1 Model 2 Model 3 (a) Model 1 Model 2 Model 3 (a)
	after	0.0058	0.0051	0.0012	0.0030	0.0004	0.0001
		(0.0066) (0.0062) (0.0054) (0.0068) (0.0062) (0.0057)
	d2003			0.0017			-0.0009
				(0.0030)			(0.0033)
	after×2003 (Couples)			-0.0015			0.0017
				(0.0072)			(0.0087)
	after×2003 (Singles)			0.0311			-0.0023
				(0.0198)			(0.0207)
	Controlled for Covariates	no	yes	yes	no	yes	yes
	Log-Likelihood	-929.1	-891.6	-1794.2	-665.8	-644.4	-1324.8
	Observations	5,564	5,564	11,466	4,447	4,447	9,047
	(a) Model 3 has also been estimated without the interaction term 'after×2003 (Singles)'. The
	marginal effect for men is 0.0031 (s.e. 0.0072), for women 0.0009 (s.e. 0.0078).

Note: ***/**/* indicates significance at the 1%/5%/10% level. Standard errors (in parentheses) correct for correlation across repeated observations of individuals. Covariates include: age, age 2 , no education, high school degree, vocational training, academic, disabled, married, single, german, number of children in different age classes, a dummy for living in East Germany, industry class, full-time employment dummy, and overtime. See also Table A.2. Source: Estimations based on SOEP, waves 2002 and 2003.

Table 5 :

 5 Estimation Results (Marginal Effects) -Marginal and/or Secondary Employment for Students

	Variable		Students
		Model 1 Model 2	Model 3
	after	0.0639*** 0.0500**	0.0465**
		(0.0220) (0.0220)	(0.0193)
	d2003			0.0379***
				(0.0112)
	after×2003			0.0042
				(0.0267)
	Controlled for Covariates	no	yes	yes
	Log-Likelihhod	-1161.7	-1134.1	-2197.5
	Observations	2,295	2,295	4,703
	Note: ***/**/* indicates significance at the 1%/5%/10% level.
	Standard errors (in parentheses) correct for correlation across re-
	peated observations of individuals.
	Covariates include: age, age 2 , no education, high school degree,
	vocational training, academic, disabled, married, single, german,
	number of children in different age classes, and a dummy for living
	in East Germany. See also Table A.4.
	Source: Estimations based on SOEP, waves 2002 and 2003.

Page 17 of 25 Editorial Office, Dept of Economics, Warwick University, Coventry CV4 7AL, UK

  Stancanelli, E. (2005): "Evaluating the Impact of the French Tax Credit Programme, "La Prime Pour L'Emploi": A Difference in Difference Model," Working Paper, OFCE. Steiner, V., and K. Wrohlich (2005): "Work Incentives and Labour Supply Effects of the Mini-Jobs Reform in Germany," Empirica, 32, 91-116.

			Submitted Manuscript
	Appendix -Tables
	Table A.2: Estimation Results (Coefficients) for Men and Women -Secondary
	Employment -Full Model
	Table A.1: Estimation Results (Coefficients) for Men and Women -Marginal Em-Variable Men Women ployment -Full Model Model 1 Model 2 Model 3 Model 1 Model 2 Model 3 Table A.2 continued.
	Variable after Variable	0.066	Men 0.065 Men	0.015	0.038	Women 0.006 Women	0.001
		Model 1 (0.072) Model 1	Model 2 (0.076) Model 2	Model 3 (0.071) Model 3	Model 1 (0.086) Model 1	Model 2 (0.090) Model 2	Model 3 (0.081) Model 3
	after d2003 overtime (< 3h)	0.106*	0.148** -0.056	0.05 0.023 0.027	0.107***		0.029 0.105	0.083** -0.012 0.123*
		(0.055)	(0.059) (0.087)	(0.058) (0.039) (0.067)	(0.039)		(0.04) (0.087)	(0.038) (0.047) (0.064)
	d2003 after×2003 overtime (≥ 3h)		0.147**	0.062* -0.02 0.163***			-0.024	0.097*** 0.024 0.007
			(0.075)	(0.032) (0.096) (0.059)			(0.109)	(0.020) (0.122) (0.077)
	after×2003 after×2003×single full-time employed		0.095 0.320* -0.507*** -0.560***			-0.069	-0.05 -0.041 -0.148**
			(0.140)	(0.081) (0.172) (0.109)			(0.085)	(0.051) (0.179) (0.068)
	after×2003×single age constant	0.029 0.043** -1.769*** -1.930*** -2.348*** -1.828*** -1.693*** -1.797*** -0.021 0.02 0.001 0.003
		(0.035	(0.025) (0.502)	(0.132) (0.021) (0.402)	(0.041		(0.027) (0.532)	(0.099) (0.020) (0.397)
	age age squared Log-Likelihood	-929.1	-0.121*** -0.119*** -0.000 -0.001** -891.6 -1794.2	-665.8		0.025*** -0.000 -644.4	0.018** -0.000 -1324.8
	F o r P e e r F o r P e e r F o r P e e r (0.011) (0.009) 0.001*** 0.001*** (0.000) (0.000) -0.293 -0.225 (0.228) (0.163) high-school degree age squared no education 0.392*** 0.349*** (0.065) (0.057) vocational training -0.026 -0.057 (0.062) (0.049) academic -0.221*** -0.258*** (0.080) (0.075) disabled -0.029 0.041 (0.084) (0.073) single -0.006 -0.022 F o r P e e r (0.000) (0.000) no education -0.058 -0.404 (0.415) (0.387) vocational training 0.234*** 0.113 (0.087) (0.07) academic 0.108 0.091 Observations 5564 5564 11466 F Note: ***/**/* indicates significance at the 1%/5%/10% level. Standard errors (in paren-(0.009) (0.007) -0.000*** -0.000*** (0.000) (0.000) -0.202 -0.215* (0.131) (0.120) 0.067 0.021 (0.048) (0.043) -0.156*** -0.163*** (0.039) (0.034) -0.358*** -0.364*** (0.058) (0.054) -0.307*** -0.234*** (0.075) (0.06) -0.013 0.01 (0.000) (0.000) 0.506* 0.38 (0.294) (0.251) -0.013 -0.059 (0.092) (0.074) 0.185* 4447 4447 9047 theses) are corrected for correlation across repeated observations of individuals. o All variables except age and age squared are dummy variables, taking the value 1 if the r condition is fulfilled. 0.195** (0.084) (0.07) (0.099) disabled 0.067 0.072 -0.154 0.046 (0.144) (0.116) (0.203) (0.140) married 0.131 0.077 -0.124 -0.038 (0.098) (0.082) (0.107) single 0.117 -0.028 0.163 0.242*** (0.103) (0.096) (0.107) german 0.164 0.166 -0.096 0.027 r (0.083) e (0.085) e P (0.081) Source: Estimations based on SOEP, waves 2002 and 2003.
	married german children under 15 children under 1 children under 7 children between 8-15 children under 15 children under 1 children between 8-15 east german civil servant self-employed	R e v i e w R e v i e w R e v i e w (0.073) (0.062) -0.222*** -0.206*** (0.079) (0.063) -0.033 0.014 (0.093) (0.077) -0.033 -0.056 (0.065) (0.052) R e v i e w (0.133) (0.112) -0.08 -0.059 (0.079) R (0.065) e v -0.121 -0.142** (0.082) (0.070) 0.119 0.084 (0.116) (0.099) -0.377*** -0.293*** i e w	(0.055) 0.195*** (0.053) 0.184*** (0.062) -0.234** -0.199*** (0.047) 0.220*** (0.043) 0.219*** (0.055) (0.099) (0.074) 0.069 0.058 (0.048) (0.039) 0.185*** 0.202*** (0.143) (0.120) -0.072 -0.100 (0.123) (0.097) -0.137 -0.108 (0.098) (0.075) -0.156 -0.122 (0.097) (0.076) -0.320* -0.320** (0.180) (0.134) -0.18 -0.255
			(0.138)	(0.110)			(0.040) (0.184)	(0.033) (0.163)
	east german industry class. 2		0.039 -0.107	0.032 -0.057			-0.309*** -0.344*** 0.046 -0.066
			(0.057) (0.108)	(0.049) (0.093)			(0.043) (0.176)	(0.037) (0.166)
	constant industry class. 3	-1.705***	0.598*** 0.031	0.486*** -1.101*** -1.493*** -1.495*** 0.124 -0.101 -0.148
		(0.026)	(0.218) (0.122)	(0.182) (0.099)	(0.018)		(0.168) (0.142)	(0.139) (0.112)
	Log-Likelihood industry class. 4	-1666.8	-1529.5 -0.181	-2919.3 -0.165	-3829.5		-3664.7 -0.326	-7183.4 -0.264
	Observations	8,907	8,907 (0.160)	18,154 (0.126)	9,444		9,444 (0.296)	19,215 (0.248)
	industry class. 5 Note: ***/**/* indicates significance at the 1%/5%/10% level. Standard errors (in parenthe-0.184** 0.231*** 0.169 0.134 (0.093) (0.079) (0.107) (0.090) ses) are corrected for correlation across repeated observations of individuals. industry class. 6 0.109 0.196** -0.112 -0.020 All variables except age and age squared are dummy variables, taking the value 1 if the con-(0.119) (0.099) (0.155) (0.116) dition is fulfilled. industry class. 7 0.16 0.139 0.275* 0.257**
	Source: Estimations based on SOEP, waves 2002 and 2003. (0.139) (0.115)		(0.151)	(0.124)
					Continued on next page.

Table A

 A

	Table A.4: Estimation Results (Coefficients) for
	Students -Marginal and/or Secondary Employ-
	ment -Full Model
	Variable		Students
		Model 1	Model 2	Model 3
	after	0.214***	0.160**	0.159**
		(0.071)	(0.073)	(0.068)
	d2003			0.145***
				(0.043)
	after×2003			-0.005
				(0.093)
	age		0.060***	0.048***
	F o r female age squared no education F o r		(0.021) 0.204*** (0.061) -0.001** (0.000)	(0.018) 0.229*** (0.049) -0.001** (0.000)
	P high-school degree P e e r vocational training e academic disabled e r	-0.239** -0.247*** (0.096) (0.077) -0.514 -0.331
	.3: Number of Observations, Marginal and/or Secondary Employment for Students in the Subsamples Marg. or Secon. Employment Subsample Obs. abs. before 1778 274 2002 after April 1st 630 132 before 1819 350 2003 after 476 122 1%/5%/10% level. Standard errors (in parentheses) 0.1324 Note: ***/**/* indicates significance at the April 1st 0.0808 Observations 2,295 2,295 4,703 0.0873 Log-Likelihhod -1161.7 -1134.1 -2197.5 0.0574 (0.034 (0.342) (0.285) in % R e v i e w (0.314) (0.207) single 0.033 0.083 (0.075) (0.060) married -0.388*** -0.351*** (0.136) (0.105) german 0.283** 0.178* (0.126) R e v (0.102) children under 15 -0.134* -0.06 (0.071) (0.055) east german i e -0.224*** -0.246*** (0.071) (0.058) constant -0.869*** -2.025*** -1.889*** w
	Note: High income sample of the SOEP is not in-are corrected for correlation across repeated observa-
	cluded, since this entire group was interviewed after tions of individuals.
	April in the 2003 wave. Numbers refer to the popula-All variables except age and age squared are dummy
	tion in "Ausbildung". variables, taking the value 1 if the condition is fulfilled.
	Source: SOEP, waves 2002 and 2003. Source: Estimations based on SOEP, waves 2002 and
	2003.

For a detailed description of the data, see Haisken[START_REF] De-New | Desktop Compendium to The German Socio-Economic Panel Study[END_REF].

In 2003 80% of interviews were conducted in the first quarter, 8% in April, 5% in May, 4% in June and the rest (3%) between July and October.

See, for example, Heckman, LaLonde, and Smith (1999) for an overview.

Looking at the GDP growth between 2002 and[START_REF] Moffitt | Welfare Program and Labor Supply[END_REF] shows that there has been only a small change of 0.8% between these two years. More importantly, the change between the first and second quarter in both years was about 2%.

For details see Bundesagentur fürArbeit (2003).

Note that jobs with a monthly income between 400 and 800 Euro might become more attractive under the reform as well. However, in this paper we only look at "marginal employment", which refers to jobs with an income up to 400 Euro per month.

Editorial Office, Dept of Economics, Warwick University, Coventry CV4 7AL, UK Submitted Manuscript

We also ran the same model including the variable af ter2003 × single, which did not change the results.

Foundation (DFG) under the research program "Flexibilisierungspotenziale bei heterogenen Arbeitsmärkten" (project STE 681/5-1) is gratefully acknowledged. † Marco Caliendo (Corresponding author) is Senior Research Associate at the Institute for the Study of Labor (IZA) in Bonn and Research Fellow of the IAB, Nuremberg,


Inmaculada García

Jose-Alberto A Molina
email: jamolina@unizar.es

Maria Navarro

The effects of education on spouses' satisfaction in Europe

Keywords: Education, Spouses, Income satisfaction, Europe JEL classification: I20, I31, D10

This paper identifies the effects of both own and spouse's education levels on individual economic satisfaction for European households. To that end, it estimates several specifications based on the family collective approach, for each of the 14 EU countries, by using the eight waves of the European Community Household Panel-ECHP (1994)(1995)(1996)(1997)(1998)(1999)(2000)(2001). After demonstrating that the IV Hausman-Taylor procedure is the selected estimation method in the majority of cases, the empirical results show that male and female income satisfaction significantly increases when the husband achieves higher education qualifications in the majority of European countries. However, the positive effect of the wife's higher education on female income satisfaction only appears in a very limited number of countries. Additionally, increases in individual wage and non-wage incomes generally lead to higher satisfaction levels.

I. INTRODUCTION

The existing state of research on individual satisfaction suggests that reported subjective wellbeing is a satisfactory empirical approximation of individual utility, that can be applied in socio-economic research [START_REF] Oswald | Happiness and Economic Performance[END_REF][START_REF] Easterlin | Happiness in Economics[END_REF][START_REF] Frey | What can Economists Learn from Happiness Research[END_REF][START_REF] Hamermesh | Subjective outcomes in economics[END_REF]. The evidence adduced to date has shown that education appears to have a significant impact on the different satisfaction domains of individuals. For example, Van Praag et al., (2003) conclude that individuals with higher education are significantly more satisfied with their health, thus indicating that more highly educated individuals enjoy a healthier life style. [START_REF] Belfield | How well do theories of job matching explain variations in job satisfaction across education levels? Evidence for UK graduates[END_REF], [START_REF] Gazioglu | Job satisfaction in Britain: individual and job related factors[END_REF] and [START_REF] Fleming | I'm too clever for this job: a bivariate probit analysis on overeducation and job satisfaction in Australia[END_REF] also find a significant relationship between satisfaction and educational level. For their part, Clark and[START_REF] Clark | Unhappiness and unemployment[END_REF]1996) and Clark et al. (1996) observe that highly educated people are less content with respect to their job satisfaction when other factors (income, etc.) are controlled for. The possible explanation here is that this low level of contentment might result from the significant reduction in income of those with lower qualifications. [START_REF] Ferrer-I-Carbonell | Income Satisfaction Inequality and its Causes[END_REF] produce ambiguous evidence for income satisfaction in Germany. On the one hand, they find that more education leads to more efficient consumption, which would appear to point to a positive effect on income satisfaction; on the other hand, more education widens the individual's horizon, thereby giving rise to increased expectations, which carries with it a negative effect as anticipated by neoclassical economic theory.

Despite the clear relevance of the evidence, the effects of education on satisfaction have usually been studied in a way that does not reflect the fact that the household is composed of interdependent spouses. The literature reflects only a limited number of exceptions to this approach. Thus, [START_REF] Schwarze | Living Conditions of Children and Parental Well-being: Evidence from German Data on Life Satisfaction[END_REF] finds that parental life satisfaction increases with a child's Health and education can serve as an approximation of income or future earnings, as has been confirmed in [START_REF] Blanchflower | Well-being over Time in Britain and the USA[END_REF]. In this way, if parents make some level of investment in their children's education while the children are still young, they can expect some returns when they become older. Thus, a positive impact of children's education on parental life satisfaction can also be driven by an exchange motive. Within couples, [START_REF] Groot | Age and education differences in marriages and their effects on life satisfaction[END_REF] study the effect of age and education differences between spouses on happiness, finding that female life satisfaction increases if the education gap between husband and wife is smaller.

In this line of modelling individual satisfaction within the household, as a fully interdependent process, this paper assumes the collective approach, in which one spouse's satisfaction not only depends on his/her own determinants, but also on the other spouse's variables, in order to model the effects of both own and spouse's education levels on individual economic satisfaction [START_REF] Chiappori | Rational household labour supply[END_REF][START_REF] Chiappori | Collective labour supply and welfare[END_REF][START_REF] Browning | Efficient intra-household allocations: a general characterization and empirical tests[END_REF][START_REF] Chiappori | Divorce legislation and household labour supply[END_REF]. Additionally, we also consider the influence of other individual and economic variables, such as age, the number of children, wages and non-wage incomes. The collective approach adopted in this paper makes it possible to derive some stochastic formulations which are then estimated for 14 EU countries, using the panel structure which results from the eight waves of the European Community Household Panel-ECHP (1994)(1995)(1996)(1997)(1998)(1999)(2000)(2001).

With respect to the estimation strategy, this takes the form of four consecutive estimations, namely pool, fixed effects, random effects and efficient generalized instrumental variables. The fixed or random effects methods correct the heterogeneity bias that appears when the use of subjective variables could imply that some people look at life either pessimistically or optimistically, even though there is "really" no difference in their level of well-being [START_REF] Clark | A simple statistical method for measuring how life events affect happiness[END_REF][START_REF] Ferrer-I-Carbonell | How Important is Methodology for the Estimates of the determinants of Happiness[END_REF][START_REF] Senik | Relativizing relative income[END_REF]. 3 Moreover, it is well known that individual behaviour is oriented towards achieving higher satisfaction levels. As a consequence, all the variables which can be chosen by individuals will be endogenous in the satisfaction regression, in such a way that the majority of estimated parameters obtained by standard regressions are likely to be underestimated. A standard solution to this endogeneity bias, which depends on the degree that individuals can choose their actions in order to be better off, is to use instrumental variables [START_REF] Powdthavee | Mental risk-sharing in marriage: evidence from panel data[END_REF][START_REF] Schwarze | Living Conditions of Children and Parental Well-being: Evidence from German Data on Life Satisfaction[END_REF]. After carrying out all these estimations, the strategy selects the one that is statistically most appropriate in every case, by using the LM value, as well as two Hausman tests [START_REF] Baltagi | Fixed effects, random effects or Hausman-Taylor? A pretest estimator[END_REF].

The rest of the paper is organized as follows. In the following section we describe the data. Next section is dedicated to the stochastic formulation. The following section is devoted to the empirical results and, finally, we close the paper with a summary of the most relevant conclusions.

II. DATA

Bearing in mind that the purpose of the study is to study the effects of both own and spouse's education levels on individual economic satisfaction, for individuals who work as wage earners, the data used in this work comes from the eight waves of the ECHP (1994ECHP ( -2001) ) for each of the 14 sample EU countries. 1 In our study, households have been selected in which both spouses are aged between 16 and 65 years old. Individuals both with and without children have been included in these households. Those households lacking the required information have been excluded, resulting in two sub-samples, male wage earners and female 1 The ECHP is an extensive, sample-based panel survey in which the same households and individuals are interviewed annually. The data come from a standardised questionnaire and are designed to be cross-nationally comparable [START_REF] Peracchi | The European Community Household Panel: a review[END_REF]. The ECHP includes questions about several subjective aspects of well-being, enquiring into the level of satisfaction that individuals reach with respect to different aspects, such as their income. The specific question this paper is interested in is: "How satisfied are you with your financial situation?". Each of these responses takes values from 1 to 6, moving from not satisfied at all (1) to completely satisfied (6). This satisfaction question is based on individuals' own perception, in such a way that Table 1 begins by showing the simple means which are comparable across the populations, after assuming linearity across responses.

Table 1 shows the mean and standard deviation of the dependent variables used in the analysis. The dependent variables are husband and wife income satisfaction (HusbSatisf, WifeSatisf). Starting with the male sample, it can be appreciated that for male wage earners, these generally declare higher satisfaction levels than their respective wives in the majority of the sample countries, namely Austria, Belgium, Denmark, Finland, Germany, Greece, Italy, Portugal and Spain. With respect to the female sample, it emerges that female wage earners report higher satisfaction levels than their respective husbands, this being the case for all sample countries, save Portugal.

(Table 1) With respect to the exogenous variables, the study includes both own and spouse's education levels (HusbPrimEduc, HusbSeconEduc, HusbHighEduc, WifePrimEduc, WifeSeconEduc, WifeHighEduc), as well as a number of individual characteristics and several economic variables. As regards individual characteristics, they include the age of the spouses (HusbAge, WifeAge), the age difference between the spouses (AgeDifference), as well as two other variables which refer to the presence of children in the household: a dummy variable indicating if there is a child under 12 in the household (Children<12), and another indicating the number of children under 16 (Children<16). Additionally, we include the percentages of self-employed and wage-earning wives in the husband's sample (WifeWage-Earner, WifeSelf-Employed), and the percentage of self-employed and wage-earning husbands in the wife's sample (HusbSelf-Employed, HusbWage-Earner). With respect to the variables which refer to the economic situation of the household, these include the wages of both spouses (HusbWage, WifeWage), as well as the annual non-wage incomes of both the husband and the wife (HusbNon-WageInc, WifeNon-WageInc), and the wife's participation in the household income (WifeParticipation).

Table 2 shows the mean and the standard deviation of each of the exogenous variables used in the analysis. As regards the education level, it can be noted in the majority of countries, and for both samples of wage-earners, that wives generally show a higher percentage than husbands for the primary education level. By contrast, the percentage of husbands who have attained higher education levels is generally greater than that corresponding to wives, with this evidence appearing generally in the male sample, but not at all in the female sample. The percentage of husbands who have secondary education is higher than that corresponding to wives who have attained this level, this being the case in both samples of male and female wage-earners, with the exceptions only of Germany and Ireland.

(Table 2) In every sample country analysed, the age of the husband is greater than that of the wife in both samples of males and females. The age difference is greater for the female sample, with the highest mean value corresponding to Greece in both sample groups, where this age difference reaches 4.6 years. With respect to the variables that refer to the presence of children in the household, note that the percentages are higher in the male sample (where wives can be either wage-earners or self-employed) in the majority of the countries, namely in Austria, Denmark, Finland, France, Germany, Greece, Ireland, Italy, Luxembourg, the Netherlands, Spain and the United Kingdom, with the highest values corresponding to Austria. However, there appears to be clear evidence that the mean number of children under 16 is higher for the sample of male wage-earners than for the female sample, this being the case in every sample country.

From this simple descriptive analysis it also emerges that the husband's mean income per hour is higher than that of the wife's for both male and female wage-earners in every sample country. We can further note the smaller wage gap in the sample of female wageearners, and the highest values being reached for the male sample in Finland and Luxembourg. With respect to non-wage annual incomes, the wife's non-wage income is higher than that of the husband's in Austria, Belgium, Denmark, Finland, Germany, Greece, Ireland and the United Kingdom in the male wage earner sample. However, in the female wage-earner sample, the husband's non wage income is higher than that of the wife in every country, save Belgium and Denmark. Finally, note the higher percentage of wage-earner wives, as compared to self-employed wives, in the sample of male wage-earners and of female wage-earners, respectively, in all EU sample countries.

III. THE MODEL

This section develops the model specification and its estimation procedure. In order to describe the empirical specification to model the effects of both own and spouse's education levels on individual economic satisfaction, we first adopt the family collective approach. On the basis of the assumption that intra-household decisions are Pareto-efficient, this approach considers that the household consists of two working-age individuals, A = husband and B = wife, whose rational preferences could be represented by indirect utility functions, defined in Moreover, the panel data structure provided by the ECHP permits the application of techniques that help to control for unobservable heterogeneity. On these theoretical and empirical bases, the stochastic formulation underlying the observed subjective well-being responses takes the form of linear functions:

I I A A B B A A B B A A B B A A B B I I it it 1 it 2 it 3 it 4 it 1 it 2 it 3 it 4 it i it v ED ED z z w w y y e µ = + + + + + + + + + + i =1, …, N; t =1, …, T ; I =A,B (1)
where v it corresponds to the income subjective satisfaction of the individual i in period t, with this t being the current period, whereas an individual can be in the sample a maximum of T periods. This dependent variable, v it,, is explained, according to the collective framework, by a number of exogenous variables. Thus, it ED and it z represent the education and other sociodemographic characteristics, respectively; it w and it y are wages and non-labour incomes; the parameters and represent the coefficients; µ and are constant terms, with µ being the average population and the individual deviation with respect to this average; and, finally, e are the error terms that are supposed to be independent, with null mean and constant variance.

These equations are estimated independently for both spouses, in such a way that N is the number of households in the sample.

The estimation strategy follows these steps. 2 First, each equation is estimated separately, considering the aggregated data, that is to say, a pool estimation is carried out. A panel data structure is then used in order to estimate functions, considering individual effects, both fixed and random. As is well known, the difference between the two lies in the fact that, while, in

2 Given the ordinal nature of the dependent variable on individual satisfaction, an appropriate regression model would be an ordered probit. However, while a random-effects ordered probit model is available in standard statistical software packages [START_REF] Ferrer-I-Carbonell | Income Satisfaction Inequality and its Causes[END_REF][START_REF] Schwarze | Living Conditions of Children and Parental Well-being: Evidence from German Data on Life Satisfaction[END_REF][START_REF] Winkelmann | Subjective well-being and the family: results from an ordered probit model with multiple random effects[END_REF], the fixed-effects ordered probit estimator is not. This is why the present paper uses as approximations both randomeffects and fixed-effects regression models, which are perfectly comparable by using habitual tests (D' Ambrosio and Frick, 2004;[START_REF] Ferrer-I-Carbonell | How Important is Methodology for the Estimates of the determinants of Happiness[END_REF][START_REF] Graham | Does happiness pay? An exploration based on panel data from Russia[END_REF]. Consideration is also given to an alternative estimation procedure suggested in the literature, namely the Efficient Generalized Instrumental Variables (EGIV), proposed by [START_REF] Hausman | Panel data and unobservable individual effects[END_REF]. 3 The method followed in this paper uses as instruments the individual time averages of the variables (the individual's own wage, the presence of children under 12, the number of children under 16, the spouse's own wage, male and female nonlabour income, the wife's participation in household income, own age and a dummy that indicates if the individual is self-employed) for the time-invariant variables that are correlated with the individual effects (the age difference between the spouses, the individual's own education levels, and the spouse's higher education level). Thus, this procedure allows for the simultaneous control of the correlation between regressors and unobserved individual effects, by using instruments. Similarly, it permits the identification of the estimates of the timeinvariant covariates, such as education. Moreover, it avoids the insecurity associated with the choice of suitable instruments, since the individual means over time of all the included regressors can serve as valid instruments. Additionally, the variance-covariance structure can be taken into account so as to obtain more efficient estimators.

This EGIV method is implemented in the following steps. First, equations (1) are estimated by pooled Two Stage Least Squares (2SLS), where the set of variables mentioned above act as instruments. Second, the pooled 2SLS residuals are used to construct the weights for a Feasible Generalized Least Squares estimator. Third, these weights are used to transform (by quasi-time demeaning) all the dependent variables, explanatory variables and instrumental 3 The recent work by [START_REF] Baltagi | Fixed effects, random effects or Hausman-Taylor? A pretest estimator[END_REF] provides information on the suitability of the Hausman-Taylor procedure in a general framework where panel data is available and some regressors are correlated with the individual effects. After estimating the four alternative specifications, some appropriate econometric tests allow for the best formulation to be selected in every case. In particular, an LM test indicates if a panel or a pool estimation is preferred. If a panel estimation is selected, then a choice must be made from among the three alternative specifications, with two Hausman tests allowing the best panel estimation to be selected [START_REF] Hausman | Specification tests in econometrics[END_REF]. 4 The first Hausman test (Hausman-1) is the standard to distinguish between the random and fixed effects estimators, and the second (Hausman-2) tests the Hausman-Taylor against the fixed effects model. 5

IV. EMPIRICAL RESULTS

Table 3 includes the empirical results for both sub-samples, male wage earners and female wage earners. We begin with a brief description of the test results that allows us to select a particular estimation procedure for each sample country. First, the LM tests indicate that the pool estimation is not selected in any sample country. Second, Hausman-1 tests reveal that the fixed effects estimation is preferred over random effects and, third, Hausman-2 tests indicate that, for all cases, save for male wage earners in Austria, the Hausman-Taylor estimation is preferred over the fixed effects.

(Table 3) 4 See, for details, [START_REF] Hausman | Panel data and unobservable individual effects[END_REF], [START_REF] Wooldridge | Econometric Analysis of Cross-Section and Panel Data[END_REF] and [START_REF] Baltagi | Fixed effects, random effects or Hausman-Taylor? A pretest estimator[END_REF]. 5 The 8.0 version of Stata includes the Hausman-Taylor procedure and is used to obtain the estimates presented in this paper (2004). As regards the effect of a wife's higher education on her husband's income satisfaction, this appears to increase in France, which can be interpreted as that the wife can better appreciate the necessary effort of her husband to reach a certain level of income and, therefore, according to the cooperative nature of the relationship between spouses, this assessment increases the husband's satisfaction with respect to his level of income. By contrast, the effect decreases in Finland and Germany, where the wife's higher education does not imply a higher assessment of her spouse's effort to reach a certain level of income.

Wives' higher education increases income satisfaction of wives in Greece, Ireland and

Portugal. The wife is affected more than the husband by the spouse's education level, in such a way that income satisfaction is increased when the husband has received higher education, in the cases of Austria, Belgium, Denmark, the Netherlands, Portugal and the United Kingdom. Groot and Maasen Van Den Brink (2002) find that husbands typically tend to be older and higher educated than their wives. Education differences between spouses can effect marital stability and divorce rates, in such a way that life satisfaction increases when the education gap is smaller. This is also the case of Finland and Germany, where we can note that the effect of the wife's education on the husband's satisfaction runs in the opposite direction.

Additionally, we can observe that the effect of age is significantly positive for male wage earners in the majority of countries, namely Austria, Belgium, Finland, France, Greece, Ireland, Luxembourg, the Netherlands, Portugal and Spain. This same result appears for the wife's age in the female samples of Belgium, Denmark, Finland, France, Greece, Ireland, The Netherlands, Spain and the United Kingdom. Groot and Maasen Van Den Brink (2002) find that a positive age gap between husband and wife increases both male and female satisfaction, and we find an increase in female satisfaction in Finland and Greece. The effects of the presence of children vary across countries, also depending on age. Thus, we find that if the child is under 12, then the effect is positive in Spain and negative in Austria, Denmark,

France and the Netherlands for male wage earners. For the female sample, we can observe the same result and, in addition, a negative effect in Italy and the United Kingdom, but a positive effect in Greece. Moreover, if the age is less than 16 years, then the effect is positive for male wage-earners in France and Luxembourg, and negative in Belgium, Denmark, Germany, Greece, Italy, Spain and the United Kingdom. For the female sample, it is similarly negative in Denmark, Greece, Ireland and the United Kingdom, but positive in France.

Turning to the economic variables, it can be observed that increases in the husband's wage has, according to the normality assumption, a highly significant positive impact on male satisfaction for the majority of cases, particularly for both samples in Austria, France, Germany, Greece, Italy, Portugal and Spain. Moreover, this same positive effect from the wife's wage is also observable for both samples in France, Greece and Portugal. For their part, Belgium, France, Greece, Italy, Portugal and Spain show altruistic behaviour with respect to wage incomes, in such a way that male satisfaction positively depends on female wages, and female satisfaction on male wages. By contrast, all male workers in Austria, Finland, Germany, Ireland, Luxembourg and the United Kingdom exhibit egoistic behaviour, with their utilities remaining indifferent to changes in their wives' labour incomes. With respect to non-wage incomes, the husband's variable has a clearly positive effect on male and female income satisfaction in Greece and Portugal. Finally, it can be noted that increases in

V. CONCLUSIONS

This paper has analysed the effects of both own and spouse's education levels, as well as other individual and economic variables, on economic satisfaction for the case of European households. To that end, we have assumed a collective family model framework, whose empirical specifications (pool, fixed effects, random effects and efficient generalized instrumental variables) have been estimated using the eight waves of the ECHP (1994)(1995)(1996)(1997)(1998)(1999)(2000)(2001).

With respect to the selected formulation, the empirical results show that the IV Hausman-Taylor estimator has been selected in the majority of cases. As regards the relevant variables for this article, male income satisfaction significantly increases when the husband achieves higher education qualifications in Finland, Germany, Greece, Italy, The Netherlands, Portugal, Spain and the United Kingdom. Female income satisfaction is positively related to her education level in Greece, Ireland and Portugal; and, additionally, to the husband's education level in Austria, Belgium, Denmark, Finland, Germany, the Netherlands, Portugal and the United Kingdom.

As regards other determinants, age has a significantly positive impact on income satisfaction for wage earners in the majority of countries. With respect to the economic variables, it first appears that increases in individual wage and non-wage incomes lead to higher satisfaction levels. Moreover, with respect to interrelations between spouses, our results reveal that in France, Greece and Portugal, all workers, whether male or female, show 13 altruistic behaviour with respect to wage incomes, while in Finland, both male and female workers exhibit egoistic behaviour.

An understanding of individual satisfaction derived from income within the household could be particularly useful for policy-makers in evaluating socio-economic policies. Thus, the empirical conclusions drawn from this study will hopefully assist in the drafting of such policies, that have the objective of increasing the satisfaction levels reported by the spouses within the household.

There appears to be support for such policies, e.g. the reduction in class sizes, that has been shown to improve children's education outcomes [START_REF] Bingley | The effects of school resources on participation in post-compulsory education: Danish quasi-experimental evidence, and evidence that controls for family, school and neighbourhood effects[END_REF]. Moreover, while it is clear that both genders have benefited from progress in the sphere of education, these advances have failed to eradicate the gender gap. Compulsory education laws are not sufficient to equalize attendance rates, so special policies should be enacted aimed at increasing the number of women benefiting from education, such as building more schools in remote rural areas, or providing correspondence courses. However, the costs associated with school attendance, as well as opportunity costs, are high and the perceived benefit of formal education for girls is low, which could reduce the demand for education on the part of some groups in certain developing countries.

F

  with the number of observations ranging from France (17,623 husbands and 13,589 wives) to Luxembourg (1,288 husbands and 774 wives).

  own exogenous variables, as well as in terms of the other member's variables.

  fixed effects, the coefficients are considered as fixed values for each individual, in the specification of random effects, the specific aspects of each spouse are taken as independent random variables.

  , the transformed regression is again estimated by pooled 2SLS, where the individual means over time of the time-varying regressors, and the exogenous time-invariant regressors, are the instruments. Under the full set of assumptions, this Hausman and Taylor estimator coincides with the efficient GMM estimator.

  the education variables, we show that income satisfaction significantly increases when husbands achieve higher education qualifications, with this result appearing in a significant number of cases, particularly Finland, Germany, Greece, Italy, Portugal, Spain, the Netherlands and the United Kingdom. Similar results have been obtained in[START_REF] Ferrer-I-Carbonell | Income Satisfaction Inequality and its Causes[END_REF];[START_REF] Van Praag | The Anatomy of subjective wellbeing[END_REF] andFrijters, Haisken-DeNew and Shields

  s share of household income increases male income satisfaction in Finland, Ireland, Luxembourg and the Netherlands, and decreases it in Belgium and the United Kingdom. Finally, note that when the wife's participation in household income increases, so her satisfaction increases in the cases of Italy, Portugal and the United Kingdom.

Table 1 .

 1 comments made by the participants, particularly those of Ian Walker, being highly appreciated. Moreover, the authors would like to express their thanks to one anonymous referee for helpful comments and suggestions. Thanks are due also for the financial support provided by the Spanish Ministry of Education and Science and FEDER (Project SEC2005-06522), by the BBVA Foundation and the DGA. The usual disclaimer applies. Mean and std. dev of dependent variables of husbands and wives

	o r
	P
	e
	e r
	R e v
	i e
	w

Editorial Office, Dept of Economics, Warwick University, Coventry CV4 7AL, UK

Table 2 .

 2 Mean and std. dev of exogenous variables of husbands and wives

							Submitted Manuscript						Page 20 of 23
		Austria	Belgium	Denmark	Finland	France	Germany	Greece	Ireland	Italy	Luxembourg	The Netherlands	Portugal	Spain	United-Kingdom
	Husbands
	HusbPrimEduc	0.123 (0.33)	0.227 (0.42)	0.190 (0.39)	0.188 (0.39)	0.272 (0.44)	0.175 (0.38)	0.428 (0.49)	0.391 (0.49)	0.486 (0.50)	0.484 (0.50)	0.213 (0.41)	0.823 (0.38)	0.579 (0.49)	0.354 (0.48)
	HusbSeconEduc	0.780 (0.41)	0.324 (0.47)	0.426 (0.49)	0.447 (0.50)	0.434 (0.50)	0.493 (0.50)	0.281 (0.45)	0.371 (0.48)	0.379 (0.49)	0.286 (0.45)	0.527 (0.50)	0.102 (0.30)	0.174 (0.38)	0.226 (0.42)
	HusbHighEduc	0.089 (0.29)	0.369 (0.48)	0.378 (0.48)	0.360 (0.48)	0.235 (0.42)	0.331 (0.47)	0.287 (0.45)	0.227 (0.42)	0.107 (0.31)	0.228 (0.42)	0.242 (0.43)	0.063 (0.24)	0.247 (0.43)	0.404 (0.49)
	WifePrimEduc	0.271 (0.44)	0.243 (0.43)	0.216 (0.41)	0.183 (0.39)	0.315 (0.46)	0.307 (0.46)	0.520 (0.50)	0.392 (0.49)	0.508 (0.50)	0.595 (0.49)	0.294 (0.46)	0.806 (0.40)	0.635 (0.48)	0.446 (0.50)
	WifeSeconEduc	0.631 (0.48)	0.299 (0.46)	0.399 (0.49)	0.381 (0.49)	0.375 (0.48)	0.551 (0.50)	0.243 (0.43)	0.430 (0.50)	0.374 (0.48)	0.282 (0.45)	0.517 (0.50)	0.099 (0.30)	0.170 (0.38)	0.243 (0.43)
	WifeHighEduc	0.084 (0.28)	0.393 (0.49)	0.378 (0.48)	0.433 (0.50)	0.241 (0.43)	0.139 (0.35)	0.235 (0.42)	0.167 (0.37)	0.088 (0.28)	0.119 (0.32)	0.176 (0.38)	0.064 (0.24)	0.195 (0.40)	0.303 (0.46)
	HusbAge	41.602 (9.56)	41.095 (9.04)	41.893 (11.14)	41.394 (9.97)	40.685 (9.53)	43.079 (10.15)	43.163 (9.66)	43.310 (10.19)	43.082 (9.29)	39.958 (9.03)	41.769 (9.33)	42.187 (11.48)	42.015 (9.87)	41.614 (10.97)
	WifeAge	39.127 (9.53)	39.038 (9.23)	39.621 (10.99)	39.761 (10.11)	38.580 (9.69)	40.534 (10.01)	38.690 (9.71)	41.323 (10.04)	39.945 (9.23)	37.231 (8.84)	39.468 (9.41)	39.563 (11.33)	39.561 (9.71)	39.669 (10.98)
	AgeDifference	2.489 (4.15)	2.057 (3.84)	2.264 (4.22)	1.629 (3.76)	2.110 (4.30)	2.547 (3.94)	4.664 (4.25)	1.989 (3.60)	3.154 (3.64)	2.742 (4.16)	2.296 (3.71)	2.614 (4.42)	2.493 (3.56)	1.962 (4.63)
	Children< 12	0.476 (0.50)	0.354 (0.48)	0.363 (0.48)	0.450 (0.50)	0.428 (0.49)	0.272 (0.45)	0.413 (0.49)	0.432 (0.50)	0.412 (0.49)	0.367 (0.48)	0.374 (0.48)	0.401 (0.49)	0.401 (0.49)	0.333 (0.47)
	Children < 16	0.978 (1.01)	1.117 (1.12)	0.914 (1.04)	1.082 (1.17)	1.092 (1.11)	0.899 (1.03)	1.060 (0.96)	1.471 (1.34)	0.930 (0.91)	1.203 (1.08)	1.006 (1.11)	0.971 (1.04)	0.958 (0.95)	0.920 (1.06)
	WifeSelf-Employed	0.064 (0.25)	0.054 (0.23)	0.025 (0.16)	0.047 (0.21)	0.026 (0.16)	0.028 (0.17)	0.080 (0.27)	0.030 (0.17)	0.037 (0.19)	0.027 (0.16)	0.027 (0.16)	0.070 (0.26)	0.039 (0.19)	0.039 (0.19)
	WifeWage-Earner	0.565 (0.50)	0.655 (0.48)	0.786 (0.41)	0.738 (0.44)	0.609 (0.49)	0.624 (0.48)	0.356 (0.48)	0.501 (0.50)	0.417 (0.49)	0.500 (0.50)	0.649 (0.48)	0.557 (0.50)	0.343 (0.47)	0.710 (0.45)
	HusbWage	10.046 (5.17)	9.854 (4.80)	10.833 (6.17)	14.039 (8.92)	9.657 (8.68)	10.733 (6.25)	5.281 (3.51)	9.997 (11.903)	0.007 (0.00)	14.296 (7.13)	10.546 (14.68)	3.808 (3.04)	6.421 (4.22)	7.638 (6.28)
	WifeWage	4.165 (5.67)	5.560 (5.19)	7.269 (5.41)	8.020 (10.12)	4.857 (6.69)	4.255 (6.32)	1.728 (2.93)	3.766 (6.521)	0.003 (0.00)	5.664 (8.31)	5.348 (8.12)	1.902 (2.66)	1.957 (3.64)	4.307 (6.80)
	HusbNon-WageInc	2025.505 1855.242 1347.727 1777.939 (4271.17) (5086.61) (3456.13) (4912.63) (3898.42) (3195.05) (1327.78) (1920.66) 2212.050 1169.542 414.627 614.436	0.597 (2.53)	3616.738 (6378.44)	1640.062 (3351.43)	432.686 (2051.76) (1657.48) (2637.27) 533.796 860.891
	WifeNon-WageInc	2400.428 3406.671 3907.233 4483.919 (4826.48) (5045.16) (4870.13) (7621.38) (3203.06) (2618.47) (1426.85) (1232.95) 1563.077 1680.182 440.924 869.619	0.514 (2.10)	1944.135 (4034.56)	732.279 (2068.92)	342.062 (1398.80) (1247.23) (1943.32) 348.595 1191.522
	WifeParticipation	0.267 (0.20)	0.347 (0.18)	0.428 (0.12)	0.402 (0.14)	0.310 (0.19)	0.263 (0.19)	0.205 (0.22)	0.228 (0.20)	0.212 (0.22)	0.229 (0.21)	0.230 (0.20)	0.271 (0.22)	0.175 (0.22)	0.318 (0.18)
	Number of observations	7615	8284	8356	6280	17623	5764	8814	5295	17344	1288	16442	13612	15524	8427

Editorial Office, Dept of Economics, Warwick University, Coventry CV4 7AL, UK

Table 3 .

 3 Husband's and wife's income satisfaction

															Page
		Austria	Belgium	Denmark	Finland	France	Germany	Greece	Ireland	Italy	Luxembourg	The Netherlands	Portugal	Spain	United-Kingdom
	Husbands
	HusbSeconEduc		0.518 (0.11)	-0.426 (-0.25)	2.466** (2.04)	-2.604** (-3.78)	1.398 (0.34)	2.277 (1.42)	7.247* (1.75)	0.705 (0.70)	4.551 (1.09)	-0.561** (-2.74)	1.128 (0.47)	6.602 (1.42)	-3.559* (-1.82)
	HusbHighEduc		2.244 (1.26)	1.819 (1.31)	4.774** (3.45)	0.464 (0.80)	9.578** (2.66)	3.541** (2.18)	3.280 (1.36)	2.341* (1.70)	3.599 (1.35)	1.129** (3.48)	2.211** (3.92)	2.508** (2.05)	1.602** (3.39)
	WifeHighEduc		-0.598 (-1.50)	-0.632 (-0.89)	-2.641** (-2.17)	1.816** (3.83)	-3.151** (-2.02)	-1.620 (-1.15)	-1.872 (-0.72)	-0.976 (-0.56)	-0.003 (-0.00)	0.261 (0.90)	-0.469 (-0.22)	-1.798 (-1.10)	0.068 (0.17)
	HusbAge	0.021**	0.011**	0.003	0.024**	0.030**	-0.043**	0.025**	0.064**	-0.010**	0.033**	0.018**	0.007**	0.028**	0.008
		(4.80)	(3.07)	(1.26)	(4.12)	(10.28)	(-4.92)	(7.28)	(8.59)	(-2.67)	(2.31)	(6.14)	(4.20)	(8.90)	(1.33)
	AgeDifference		-0.022	-0.003	0.009	-0.026**	-0.008	-0.001	-0.004	0.004	-0.048	-0.007	0.004	0.013	-0.005
			(-0.76)	(-0.23)	(0.58)	(-2.72)	(-0.29)	(-0.05)	(-0.10)	(0.37)	(-1.23)	(-1.50)	(0.53)	(0.67)	(-0.72)
	Children < 12	-0.103**	-0.017	-0.057*	-0.052	-0.096**	-0.013	0.010	-0.067	-0.047	-0.071	-0.075**	-0.002	0.060**	0.019
		(-2.20)	(-0.72)	(-1.90)	(-0.93)	(-4.30)	(-0.37)	(0.31)	(-1.54)	(-1.35)	(-1.28)	(-3.45)	(-0.11)	(2.25)	(0.55)
	Children< 16	0.012	-0.050**	-0.120**	-0.018	0.072**	-0.135**	-0.071**	-0.035	-0.066**	0.141*	-0.011	-0.021	-0.095**	-0.087**
		(0.40)	(-2.40)	(-5.81)	(-0.55)	(4.69)	(-2.88)	(-3.24)	(-1.18)	(-2.42)	(1.79)	(-0.74)	(-1.41)	(-4.76)	(-2.49)
	HusbWage	0.087**	0.032**	0.020	0.188**	0.011*	0.055*	0.105**	0.010	0.307**	0.037	0.003	0.037**	0.037**	0.022
		(3.69)	(2.66)	(1.46)	(3.84)	(1.90)	(1.93)	(7.53)	(0.23)	(4.83)	(0.83)	(0.16)	(4.35)	(3.76)	(0.68)
	WifeWage	0.014	0.019**	0.033**	-0.032	0.016**	-0.010	0.030**	0.018	0.099*	0.006	0.038**	0.016**	0.028**	0.035
		(1.32)	(2.73)	(3.84)	(-0.98)	(2.63)	(-0.54)	(4.45)	(0.49)	(1.85)	(0.29)	(4.01)	(3.46)	(4.51)	(1.48)
	HusbNon-WageInc	0.241	-0.166**	-0.577	0.869	0.590	0.631	0.104**	-6.686	-0.949	0.005	-4.158**	0.040**	-0.086**	0.748
		(1.01)	(-2.95)	(-1.17)	(1.25)	(1.58)	(0.25)	(3.94)	(-0.51)	(-0.50)	(0.04)	(-3.11)	(2.46)	(-2.23)	(0.14)
	WifeNon-WageInc	0.034	0.116*	0.902**	-0.420	-1.556**	0.612	0.039	-27.193	2.385	-0.367*	-0.459	0.044	-0.008	1.340
		(0.13)	(1.90)	(2.36)	(-0.88)	(-3.49)	(0.17)	(1.28)	(-1.39)	(0.68)	(-1.86)	(-0.22)	(1.50)	(-0.15)	(0.17)
	WifeParticipation	-0.083	-0.248**	-0.206	0.908**	0.085	0.173	-0.177	0.387*	-0.221	0.749**	0.207**	-0.073	0.034	-0.294*
		(-0.56)	(-2.09)	(-1.55)	(2.88)	(1.07)	(1.06)	(-1.62)	(1.66)	(-0.82)	(2.41)	(2.55)	(-1.04)	(0.34)	(-1.84)
	LM	3051.17 (0.0000)	5198.11 (0.0000)	2883.17 (0.0000)	1176.81 (0.0000)	8369.92 (0.0000)	902.67 (0.0000)	1307.60 (0.0000)	1277.06 (0.0000)	2132.94 (0.0000)	246.20 (0.0000)	6668.60 (0.0000)	5873.75 (0.0000)	3354.24 (0.0000)	1408.33 (0.0000)
	Hausman 1	63.29 (0.0000)	41.32 (0.0000)	93.74 (0.0000)	70.50 (0.0000)	240.28 (0.0000)	193.94 (0.0000)	111.38 (0.0000)	135.69 (0.0000)	57.81 (0.0000)	45.46 (0.0000)	212.57 (0.0000)	137.24 (0.0000)	214.70 (0.0000)	125.96 (0.0000)
	Hausman 2	0.54 (0.0003)	0.23 (1.0000)	6.20 (0.6246)	0.68 (0.9996)	2.30 (0.9703)	4.89 (0.7688)	0.18 (1.0000)	0.33 (1.0000)	1.72 (0.9885)	0.53 (0.9998)	2.90 (0.9406)	1.32 (0.9953)	0.18 (1.0000)	1.05 (0.9979)
	Selected estimation	FE	HT	HT	HT	HT	HT	HT	HT	HT	HT	HT	HT	HT	HT
	Number of observations	7615	8284	8356	4615	17622	5764	8814	5295	7303	1288	16442	13612	15524	8427

22 of 23 Editorial Office, Dept of Economics, Warwick University, Coventry CV4 7AL, UK

						Submitted Manuscript
	Wives
	WifeSeconEduc	-2.173 (-1.08)	1.398 (1.09)	-0.964 (-1.57)	1.744 (2.18)	-4.233 (-0.80)	-10.376** (-2.78)	1.517 (1.09)	0.734 (0.94)	0.780** (2.10)	-2.785 (-1.37)	-1.824** (-2.57)	-0.123 (-0.20)	4.594** (3.18)	1.429 (1.27)
	HusbHighEduc	5.188* (1.86)	1.584** (2.76)	1.233** (2.67)	1.674** (2.84)	1.964 (0.70)	3.534* (1.74)	-0.842 (-0.46)	0.125 (0.25)	0.734 (0.91)	1.049 (0.39)	2.201** (2.00)	1.094* (1.74)	0.424 (0.51)	1.878** (5.65)
	WifeHighEduc	1.422 (0.77)	0.327 (0.58)	0.066 (0.14)	0.476 (0.81)	2.153 (1.32)	-2.697 (-1.56)	4.177** (2.29)	1.271** (2.51)	0.291 (0.25)	0.287 (0.08)	0.965 (1.31)	1.875** (3.20)	1.109 (1.53)	0.410 (1.17)
	WifeAge AgeDifference Children < 12 Children< 16 HusbWage WifeWage HusbNon-WageInc WifeNon-WageInc WifeParticipation LM Hausman 1	0.001 (0.12) 0.010 (0.50) -0.124** (-2.16) 0.010 (0.26) 0.051** (3.39) 0.005 (0.36) 0.459 (1.56) -0.492 (-1.59) 0.062 (0.42) 1992.82 (0.0000) 57.56 (0.0000)	0.014** (3.01) -0.007 (-0.70) -0.045 (-1.57) -0.011 (-0.47) 0.016 (1.45) 0.010 (0.95) 0.009 (0.36) -0.073 (-1.13) -0.013 (-0.10) 3054.99 (0.0000) 38.68 (0.0000)	0.010** (3.16) 0.011 (1.30) -0.129** (-3.85) -0.089** (-3.83) 0.056** (4.85) -0.001 (-0.08) -1.300** (-2.82) -0.798 (-1.63) 0.088 (0.61) 2499.05 (0.0000) F o r P e e r R e v i e w 0.028** 0.028** -0.055** 0.026** 0.028** -0.002 (5.17) (8.89) (-3.22) (4.15) (4.04) (-0.38) 0.020* 0.018 -0.064* 0.032* 0.002 -0.002 (1.82) (0.44) (-1.85) (1.85) (0.15) (-0.19) -0.082 -0.095** -0.030 0.087* -0.065 -0.058* (-1.54) (-3.95) (-0.54) (1.90) (-1.22) (-1.65) -0.015 0.060** -0.098 -0.090** -0.088** -0.000 (-0.46) (3.52) (-1.40) (-2.86) (-2.56) (-0.01) 0.028 0.014** 0.069** 0.020** 0.268** 0.262** 0.078** -0.011 (-0.56) 0.005 (0.20) -0.026 (-0.28) 0.139 (1.16) (0.65) (2.36) (2.29) (1.97) (5.92) (4.99) (2.02) -0.004 0.017** 0.002 0.031** 0.041 0.053 -0.059 (-0.12) (2.57) (0.08) (2.42) (0.87) (1.03) (-1.64) 0.659* 0.660** -1.274 0.075** 6.870 3.473** -0.383* (1.89) (2.11) (-0.43) (3.04) (0.60) (1.98) (-1.83) -2.529** -1.085** -3.990 -0.057 29.381 -0.914 -0.021 (-2.97) (-1.97) (-0.80) (-1.15) (1.19) (-0.28) (-0.09) -0.301 -0.034 0.238 0.008 0.215 0.786** 0.536 (-1.13) (-0.42) (1.18) (0.05) (0.89) (3.20) (1.22) 1391.77 5514.11 603.45 799.41 944.91 2461.96 133.32 (0.0000) (0.0000) (0.0000) (0.0000) (0.0000) (0.0000) (0.0000) 100.95 52.46 148.29 86.84 132.36 21.15 71.86 15.99 (0.0000) (0.0000) (0.0000) (0.0000) (0.0000) (0.0068) (0.0000) (0.0425)	0.022** (6.94) 0.015 (1.20) -0.093** (-3.68) -0.017 (-1.03) 0.101** (7.32) -0.006 (-0.49) -0.770 (-0.56) -15.854** (-5.52) 0.102 (1.24) 4175.75 (0.0000) 94.71 (0.0000)	-0.000 (-0.01) 0.007 (1.32) 0.017 (0.68) -0.032 (-1.61) 0.036** (6.12) 0.021** (2.44) 0.038** (2.64) -0.014 (-0.21) 0.219** (2.75) 4105.12 (0.0000) 91.59 (0.0000)	0.043** (7.76) 0.014 (0.98) -0.040 (-0.96) 0.014 (0.44) 0.054** (6.18) 0.003 (0.31) -0.008 (-0.21) -0.011 (-0.16) 0.125 (1.01) 1257.95 (0.0000) 127.35 (0.0000)	0.024** (4.56) 0.002 (0.31) -0.104** (-3.04) -0.105** (-3.22) 0.168** (7.31) -0.097** (-3.79) 9.967** (2.26) -2.975 (-0.43) 0.456** (3.60) 994.30 (0.0000) 121.99 (0.0000)
	Hausman 2	0.82 (0.9991)	2.01 (0.9806)	9.08 (0.3353)	2.16 (0.9756)	0.00 (1.0000)	0.08 (1.0000)	1.23 (0.9963)	4.72 (0.7876)	2.07 (0.9787)	0.07 (1.0000)	0.31 (1.0000)	0.03 (1.0000)	0.45 (0.9999)	0.17 (1.0000)
	Selected estimation	HT	HT	HT	HT	HT	HT	HT	HT	HT	HT	HT	HT	HT	HT
	Number of observations	5523	6604	7790	5187	13589	4399	4884	3800	8317	774	12218	10271	7600	7839
							21

Editorial Office, Dept of Economics, Warwick University, Coventry CV4 7AL, UK Submitted Manuscript

ACKNOWLEDGEMENTS

This paper was partially written while José Alberto Molina was Visiting Fellow at the Department of Economics of the University of Warwick (UK), to which he would like to express his thanks for the hospitality and facilities provided. An earlier version of this paper has been presented at the Spanish Economic Analysis Meeting-2004 (Pamplona, Spain), as well as at the Department of Economics of the University of Warwick-2005 (Warwick, UK),

I20 -General < I2 -Education < I -Health, Education, and Welfare, I31 -General Welfare|Basic Needs|Living Standards|Quality of Life < I3 -Welfare and Poverty < I -Health, Education, and Welfare, D10 -General < D1 -Household Behavior and Family Economics < D -Microeconomics

Editorial Office, Dept of Economics, Warwick University, Coventry CV4 7AL, UK Submitted Manuscript