Quasi-Natural Experiment.

Transcription

1 Increasing the Mandatory Retirement Age: Lessons from a Quasi-Natural Experiment. Pedro Martins Queen Mary, University of London & IZA p.martins@qmul.ac.uk Álvaro A. Novo Banco de Portugal & ISEGI - U. Nova anovo@bportugal.pt Pedro Portugal Banco de Portugal & U. Nova de Lisboa pportugal@bportugal.pt March 8, 2007 Abstract In this study we analyse the impact of a legislative increase in the women s legal retirement age (LRA) introduced in 1994 by the Portuguese government. In a 6-year period, the women s LRA increased from 62 to 65 years old, equalizing men and women retirement ages. This reform affected both the labor supply by directly postponing inactivity, but it also had the potential to indirect effects on labor demand. Although the success of increasing the legal retiremen age is essentially determined at the labour market, our paper is the first to examine how firms adjust their personnel policies when forced to retain their older workers longer than initially expected. We present quasi-experimental evidence about such response. Using detailed matched employer-employee panel data and difference-in-differences matching methods, we compare firms that, before the law was announced, employed women old enough to be soon affected by the new law with firms that did not employ such women. After checking that firms did indeed comply with the law, we find that, while employment and wage levels were virtually unchanged, treated firms did significantly reduce their worker flows (hirings and separations). The last result suggests that the contribution of higher retirement ages to the sustainability of pensions appear to be much weaker than previously assumed. Keywords: Retirement age; worker flows; matching estimators JEL Codes: J14, J26, J38 Opinions expressed herein do not necessarily reflect the views of the Banco de Portugal. All remaining errors are of our responsability. 1

2 1 Introduction Most of the public pension systems in the developed countries are under severe financial stress, primarily due to the pressure arising from increased life expectancy of individuals coupled with low fertility rates. A number of countries has already decided to increase the legal retirement age (e.g., Germany and the United Kingdom) whereas other countries linked the mandatory retirement age to the evolution of the life expectancy of their citizens (e.g., Sweden, Netherlands, and Portugal). Despite its policy relevance, very little is known about the economic implications of changing the legal age of retirement. This holds not only for the recent trend of increasing the age of retirement, but also for the old fashioned early retirement policies that were popular among developed countries, in the eighties. The evidence on the economic consequences of increasing the mandatory retirement age is indeed rather sparse. Ichino et al. (2006) argue that increasing retirement age helps solving pension problems only if employment prospects of the elderly remain intact. They find that displaced elderly workers initially lose out in terms of employment chances, but eventually there are no differences with respect to displaced prime-age workers. Meghir & Whitehouse (1997) find that increased earnings in work delay job exit while increased social security benefits delay the return to work. In conjunction, the two effects imply that setting the correct economic incentives is important to determinane the retirement age. Changing the legal retirement age has obvious public finance implications. The long-term financial sustainability has been the main concern of the reform of the public pension systems. Less attention has been devoted to the labor market implications of such policy changes. It is clear, however, that postponing the retirement age impacts not only on labor supply decisions of the workers but also on labor demand decisions by the firms. In essence, increasing the legal retirement age affects negatively the worker intertemporal labor income stream and imposes, in general, larger labor costs to the firm. The legislative change in the Portuguese pension system that occurred in 1994 offers a useful quasi-experiment which will allow us to evaluate, under nearly ideal conditions, the labor market implications of an increase in the legal age of retirement. In fact, the Portuguese parliament decided to change the legal retirement age of women from 62 to 65 years. This 2

3 change was made effective gradually, increasing the retirement age by six months every year, starting in What makes our inquiry particularly enlightening is the ability to follow the affected individuals and their firms through time. Since we have access to all wage earners in the private sector we can also construct a suitable comparison group of individuals and firms that can be followed through time. Using treatment effects methods, most notably the difference-in-differences and the matching approaches, we analyze to what extent the extension of the legal retirement age impacted on the employment status, the hours worked, and the wages of women affected by legislative change. At the firm level, we study, using similar methods, the effect of postponing the legal retirement age on the hiring and firing policies of the firms. Proceeding this way one should be able to track the influence of the policy change of net job flows, and, by implication, on the level of employments. Before proceeding with the estimation of the treatment effect, we checked that firms did indeed comply with the law. Thus, we find that employment and wage levels were virtually unchanged. We observed, however, that treated firms did significantly reduce their worker flows, both in terms of hirings and separations. Generally, the results indicate that firms hire approximately one fewer worker for each older worker that is retained due to the higher legal retirement age. From a public policy point of view, the latter result suggests that the contribution of higher retirement ages to the financial sustainability of pensions may be weaker than previously assumed. The paper is organized as follows. Section 2 sketches the new Portuguese retirement legislation for women. The econometric methodologies, including the construction of treatment and control groups, are described in section 3. We present the data in section 4. We measure the compliance with the new law in section 5. The final sections present the results and the conclusions. 2 Brief characterization of the retirement law reform When in 1993 the Portuguese government decided to adjust the retirement rules, most of the arguments then put forward to justify it are still valid in today s discussion of the ailments of 3

4 social security systems. Indeed, the ageing population (higher life expectancy combined with lower fertility rates) and the decreasing ratio of active to retired were the main driving forces. We will focus on the new legal retirement age for women, but the diploma also increased from 10 to 15 years of past contributions the pension eligibility criterium and changed the financial generosity of the pension system. We will focus our evaluation exercise on the increased legal retirement age, noticing however that neither of the other changes hinders the evaluation proposed because they were across the border changes. The legislation was first approved by in July 1993, later promulgated in September, but it came into effect only on January 1, This difference between public discussion of the topic and the time it is legally binding may have anticipation effects in both the behavior of future retirees and employers. To avoid this effects, we will use the year of 1992 rather than 1993, as the before period in the difference-in-differences estimator. Another important feature of the new law is its phased implementation. Rather than equalize women s LRA with men s in a single year, the legislator chose to increase women s LRA by 6 months per year. Thus, from 1994 to 1999, the women s LRA increased gradually from 62 to 65 years (see Table 1). 3 Identification and estimation methods Given the non-experimental feature of the legislative change, the feasibility of any evaluation exercise depends crucially on the ability that researchers have to generate counterfactual groups from the data available on the legislative change. Typical methodologies proposed to tackle non-experimental settings issues include: difference-in-differences (see Meyer (1995) and the recent discussion in Abadie (2005)) and matching methods (Rubin 1977, Rosenbaum & Rubin 1983). The difference-in-differences matching estimator was proposed by Heckman et al. (1997) and Heckman et al. (1998) as a combination of the two former methods. It was recently reviewed and compared with the other methods by Smith & Todd (2005) and has the potential benefit of eliminating some sources of bias present in non-experimental settings, improving the quality of evaluation results significantly. We take advantage of the characteristics of the dataset and of the new legal setup to construct treatment and control groups. In particular, we explore (i) the existence of data for the pre- and post-law periods, and (ii) the source of variation that the gender specific law 4

5 introduced. The dataset characteristics are also important in trying to meet the fundamental requirements for the success of our evaluation exercise, namely choosing a comparison group from the same local labor market and with comparable measures from a common data source, as put forward by Heckman et al. (1997) and Heckman et al. (1998) 1. The latter requirement is clearly satisfied in our evaluation exercise as all information as a common questionnaire recorded in a common dataset (see section 4). We will focus on the first argument, usually identified as the main source of bias in this evaluation exercises (Michalopoulos et al. 2004). 3.1 The treatment and control groups The conditions to evaluate the impact of the policy change in such a setting are not as perfect as in experimental settings, requiring stronger conditons to identify the treatment effect. In fact, the counterfactual must in our case be drawn from a different group in the same labor market. We will take this into account when discussing identification, and will try to circumvent the possible sources of bias still remaining in our quasi-experimental setting through the choice of the adequate estimation methods. We also add layers of robustness checks to our identifying assumptions. The new retirement law affected all women under the age of 62. Nonetheless, there is a group of women who seems to be more prone to react to or to be affected by the firms reactions to the new legal retirement age (LRA), namely, those who would have reached the legal retirement age in year t + 1 had the LRA remained at its value of year t. For instance, those aged [61, 61,5) at the end of 1993 would have retired during 1994 under the previous age limit (62), but due to the extension to 62 1 / 2 years they (have to) postpone their retirement to We identify these women with the treatment group. It is a simple age criterium: women aged 62 to 65 years old during the law s phased implementation period, 1994 through The top panel of Table 1 summarizes the construction of the treatment group through the implementation period. Since we do not have a natural experimental setting, we need to pay particular attention to the choice of the control group. Upon it will hinge the validity of our causal inference evaluation strategy. We will argue in favor of a difference-in-differences (D-in-D) evaluation 1 The availability of a rich set of covariates, usually from the pre-treatment period, is also stressed for a good performance of some of the methods. We will address this aspect later. 5

6 strategy, eventually combined with matching (see e.g. Smith & Todd (2005)). As such, besides the choice of the non-experimental control group, we also need to decide on the before period. For the latter task, we have two choices: a single (and always the same) year or the year before the new retirement age comes into effect. 2 For the first hypothesis, we have as obvious candidate 1992 and The choice of 1993 as the before period has the disadvantage that since there some for of pre-announcement of the new law, the individuals and firms had time to react in anticipation. On the other hand, in 1992 the government policy was unknow and, therefore, it does not suffer from the anticipation pitfalls. So, we will consider 1992 as the before period. Thus, the treatment group in the before period includes all women aged [57.5, 60.5) or firm with women in this age range (see first column in Table 1). The second alternative considers the year immediately before, providing more up-to-date information, which in later years might have incorporated all the effects (anticipation) that the new law had (see Table 1, bottom panel, for details on the before and after age groups). We will entertain both hypotheses. Regarding the non-experimental control group, we consider the group formed by men in the same age group as the women included in the treatment group. Men s LRA was already 65 years when the new law came into effect in the 1994 to 1999 period. Therefore, in this agerelated dimension we can construct comparable control groups. Of course that this control group raises gender-related issues. These are, however, mitigated if we are willing to accept the time-invariance hypothesis of the D-in-D estimator. That is, if the gender gap is constant over the analysis period, using men as control for women is less of an issue. Indeed, Figure?? shows for total income and working hours that the time invariance hypothesis is supported by the evidence collected for the 1990 to 1992 period. Besides any gender related issues that may arise, the non-compulsory nature of the experiment raises issues of selection into treatment status. These, as far as imputable to observables, can be handled by the matching causal inference methodology (Rubin 1979). To address differences between the two groups due to non-observable factors, we combine both strategies, as suggested by Heckman et al. (1997) and Heckman et al. (1998), the so called D-in-D matching estimator (see Smith & Todd (2005) for a thorough discussion of matching, D-in-D and D-in-D matching estimator). 2 Recall that, starting in 1994, the women s new LRA was increased each year by 6 months until it reached (the men s LRA of) 65 years in So, for example, we may consider 1995 as the before period for

7 For the cases where the treatment unit is not the worker (women), but the firm we define our treatment and control groups in a similar fashion, though. For instance, we considered treatment units all firms that have women affected (in a particular age group) by the new law, and as control group all firms that only have men affected by the new law (i.e., in similar age groups). 3.2 Econometric implementation Let Y D it be the potential outcome of interest for individual i at time t had (s)he been in state D, where D = 1 if exposed to the program and 0 otherwise. Let treatment take place at time t. The fundamental identification problem lies in the fact that we do not observe, at time t, individual i in both states. Therefore, we cannot compute the individual treatment effect, Y 1 it Y it 0. One can, however, if provided with a convenient control group, estimate the average effect of the treatment on the treated. The method we will use to uncover this estimate is labelled difference-in-differences (D-in-D) and compares the average behavior before and after the program for the treatment group with the before and after outcomes for the comparison group (see Blundell & Costa Dias (2000)). The idea behind a D-in-D estimator is that we can use an untreated comparison group to identify temporal variation in the outcome that is not due to the treatment. However, in order to achieve identification of the general D-in-D estimator we need to assume that the average outcomes for treated and controls would have followed parallel paths over time. This is known as the time invariance assumption: E[Yit 0 Y 0 0 D = 1] = E[Yit Y 0 D = 0], (1) it where t is a time period before the program implementation. The assumption states that the over time the outcome variable of treated individuals (D = 1), in the event that they had not been exposed to the treatment, would have evolve in the same fashion as the actually observed for the individuals not exposed to the treatment (D = 0). If the assumption expressed in (1) holds, the D-in-D estimate of the average treatment effect on the treated can be obtained by the sample analogs of it 7

8 α D-in-D = {E[Y it D = 1] E[Y it D = 0]} {E[Y it D = 1] E[Y it D = 0]}. (2) It simply states that the impact of the program is given by the difference between participants and nonparticipants in the before-after difference in outcomes. The estimator uses both pre- and post-1994 law data (periods t and t) on D = 1 and D = 0 observations. The time invariance assumption can be too stringent if the treated and control groups are not balanced in covariates that are believed to be associated with the outcome variable (a common problem referred to as the Ashenfelter s dip, after Ashenfelter (1978)). The D-in-D setup can be extended to accommodate a set of covariates and this is usually done in a linear way, which takes into account eligibility specific effects and time/aggregate effects. In the following model, α D corresponds to the D-in-D estimate obtained on a sample of treatment and control units: Y it = λd + τ t + θ Z it + α D Dτ t + ε it, (3) where D is as before and represents the eligibility specific intercept, defined over age and gender according to treatment rules, τ t captures time/aggregate effects and equals 0 for the before period and 1 for the after period, and Z is a vector of covariates included to correct for differences in observed characteristics between individuals in treatment and control groups. This estimator controls for both differences in the Z s and for time specific effects, but it does not allow α D to depend on Z and it does not impose common support on the distribution of the Z s across the cells defined by the D-in-D approach (namely, before and after; treatment and control). Additionally, this procedure might be inappropriate if the treatment has different effects for different groups in the population (Meyer 1995). These pitfalls can be relaxed by supplementing the D-in-D estimates with propensity score matching (Smith & Todd 2005). The difference-in-differences matching (DDM) estimator (Heckman et al. 1997, 1998), adds to the simple D-in-D estimator the comparability on the observable covariates that characterizes the propensity score matching estimator. The feasibility of the matching strategy relies on a rich set of observable individual characteristics, X, to guarantee that the distribution of the individual characteristics important to 8

9 each evaluation exercise is the same in the difference-in-differences cells. 3 The matching process models the probability of participation and matches individuals with similar propensity scores. The time invariance assumption for the DDM estimator is E[Yit 0 Y 0 0 p, D = 1] = E[Yit Y 0 p, D = 0], (4) it where p = Pr (D = 1 X) is the propensity score. When estimating the mean impact of the treatment on the treated the matching estimator requires a conditional mean independence assumption it E ( Y 0 it X, D = 1 ) = E ( Y 0 it X, D = 0 ) = E ( Y 0 it X ) (5) and also requires that there is a nonparticipant analogue for each participant which means that Pr(D = 1 X) < 1. The DDM estimator takes two forms, depending on the nature of the data, namely, balanced panel data or repeated cross-section. For the former case, the estimator is computed by first calculating the differences over time for each individual and then match treatment and control units using propensity score estimates. Formally, [ α DDM = E (Yt 1 Yt 1 ) Ê ( Yt 0 Yt 0 P )], (6) where Ê (Y P ) represents the expected outcome of individuals in the control group matched with those in the treatment group. In the case of the repeated cross-section, the DDM takes the form of: [ α DDM = E Yt 1 Ê ( Yt 0 P )] [ E Yt 1 Ê ( Yt 0 P )], (7) where all variables are as above. In practice, for each time period, treatment and control units are matched and then the average treatment effects are computed. Finally, the before estimate is subtracted from after estimate to yield the DDM estimate of the average treatment effect on the treated. Our definition of treatment unit in the case of the firms motivates the estimation of the 3 This set of variables X does necessarily coincide with the set Z. The included X s should influence both selection into treatment and the outcome variable. 9

10 propensity score using Poisson regression rather than the ubiquitous probit or logit models. Indeed, recall that the treatment unit is defined if the firm has 1 or more women affected by the new legislation. Poisson regression allows us to capture this wealth of information with some advantages. It handles oversampling of zeros yielding more robust estimates of the propensity scores. Secondly, it allows us to match firms with a similar number of treatment (old age women) and control (old age men) units without performing (pre-estimation) exact matching on this univariate dimension. Thus, in practice, we apply the matching algorithm both to the probability that there are at least one elder woman or man in the firm (the standard definition of propensity score), but also to the estimated expected value of elder women and men in the each firm (observation unit). The Poisson regression specifies that y i is drawn from a Poisson distribution with parameter λ i, which in turn is a function of regressors x i. Formally, Pr(Y i = y i ) = e λ i λ y i i, y i = 0, 1, 2,..., (8) y i! where the λ i is typically specified as log(λ i ) = β x i. Estimation of the Poisson regression is achieved by maximum likelihood, where the log-likelihood function is given by log L = n λ i + y i β x i log(y i!). (9) i=1 4 Data We use two datasets in our analysis. To study the issues of labor income, working hours and job flows, we use Quadros de Pessoal, a employee-employer matched dataset. The impact on labor market transitions are analyzed with a quarterly employment survey, Inquérito ao Emprego. 4.1 Quadros de Pessoal Quadros de Pessoal (QP) is a longitudinal dataset matching firms and workers in the Portuguese economy. The data are gathered every year by the Ministry of Employment and Social Security, based on an inquiry that every establishment with wage-earners is legally obliged to fill in. Reported data cover all the personnel working for the establishment in a reference 10

11 week, in October of every year. The personnel on short leave (such as sickness, maternity, strike or holidays) is included, whereas personnel on long-term leave (such as military service) is not reported. Civil servants and domestic service are not covered, and the coverage of agriculture is low given its low share of wage-earners. Reported data include the firm s location, industry, employment, sales, ownership, legal setting, and the worker s gender, age, skill, occupation, schooling, admission date, earnings, duration of work, as well as the mechanism of wage bargaining. The mandatory nature of the survey leads to an extremely high response rate, and in fact the population of firms with wage-earners in manufacturing and the services private sector is covered. Given the nature of the dataset, which covers not just every company with wageearners, but also all of its workers, problems commonly faced by panel data sets, such as under- or over-sampling of certain groups and panel attrition, are thus reduced. A detailed analysis of the representativeness of this data set has been performed by Cardoso (1997), focusing on manufacturing and relying on the Census of Manufacturing, whose exhaustive nature is stressed by INE, the national statistical office. Comparison of the coverage of QP and the Census indicated that QP provides a wider coverage of the population of wage-earners than the explicit attempt on the part of the INE to exhaustively capture every firm in the economy when making interviews for the Census. Also, employer-reported wage information is known to be subject to less measurement error than worker reported data. Moreover, the legal request to publicly display in the establishment the reported data contributes to its reliability, reducing measurement errors. Each firm entering the database is assigned a unique identifying number and it can thus be followed over time. The Ministry implements several checks to ensure that a firm that has already reported to the database is not assigned a different identification number. The worker code results from a transformation of the Social Security number and it has been considered eligible for matching across years if: (i) it presented the number of digits declared valid by the Social Security Office; (ii) it was not repeated within a year. In the period under analysis, percent of the workers had a code that could be matched across years. Moreover, we were able to overcome the lack of information on this code for some workers simply by using information on the date of birth, the gender, the date of admission into the firm, and the firm identification number. 11

12 4.2 Inquérito ao Emprego Our data are taken from the nationally representative Portuguese quarterly employment surveys Inquérito ao Emprego for the period 1992(2)-2000(4), conducted by the Instituto Nacional de Estatística (INE). The quarterly employment survey has a quasi longitudinal capacity. One sixth of the sample rotate out of the sample each quarter, so that we can track transitions from employment for up to five quarters, and hence pursue the conditional approach. Transition rates are then obtained simply by identifying those employed individuals in the survey, who move out of employment over the subsequent quarter. For the present purposes, we shall distinguish between two: unemployment and economic inactivity (i.e., withdrawal from the labor force). The employment survey contains in addition to the employment status, information on the individual s age, gender, and SIC codes, inter al. The main restrictions placed on the data were that the individual be employed at the time of the survey, aged older than 55, and resident in mainland Portugal. Finally, in recognition of potential sample attrition, we ensured that individuals appearing in contiguous surveys with the same identifier were in fact the same individual. The resulting sample size is individuals. Among them we were able to spot transintions from employment into inactivity over the course of the (six quarter) survey. 5 Measuring compliance with the new law A common concern with the measurement of treatment effects is the effectiveness of the quasiexperiment. In other words, one needs to know how far reaching is the impact of the legislative change. In order to evaluate the effect of the new law on the labor force status of affected women we assembled microdata from the Portuguese employment household survey (Inquérito ao Emprego), from the first quarter of 1992 until the fourth quarter of With this information, we specified conventional logit models to estimate the probability of being employed and the probability of being inactive. Based on time of the survey and on the age and gender of the individuals we defined a dummy variable identifying the women likely to be affected by the change in the legislation. More specifically, this variable takes the value one for women aged between 62 and 62 and a half during 1994, for women aged between 62 and 63 during 12

13 1995, etc. Clearly, after 1999 the dummy is one for women aged between 62 and 65. We called this variable Treatment Group. The estimation results are provided in Table 2 where it can be seen that the probability of being employed for the treated group of women increased sizably. According to the logit estimates the odds ratio associated with the treatment group is 1.313, meaning that it is 31.3 percent more likely for a women affected by the increase of the retirement to be employed. Symmetrically, the probability of being inactive decreased significantly among the treated women, where the decline is estimated to be around 27.9 percent. The overall picture from these two logit regressions is that the new retirement age rules had a visible impact in the labor force status of affected women. We can give a more complete picture of the labor market changes that emerges from postponing the retirement age by looking at transitions out of employment. Since the Portuguese employment survey has a quasi/longitudinal capacity, one can track transitions among labor market states for about five sixths of the sample. In particular, one can spot transitions from employment into inactivity among individuals who are old enough to consider retirement. Based on the age of the individuals, one should expect to see an increase in the hazard rate for women affected by the change in the legislation. And this is indeed what is extracted from the estimation of a Cox proportional hazards model, where the time of the efficacy of the new law (the After variable in the specification) is treated as a time-varying covariate. The indication provided in table 3 is that the hazard rate more than tripled among the affected women. 6 Results Our estimates of the average treatment effect on the treated are based on the class of differencein-differences estimators, which as argued earlier are the most appropriate to handle the issues related with our specific non-experimental setting. 6.1 Impact on women s labor income, working hours, and work absence In Table 4, we present a set of D-in-D estimates for the effect of the treatment on the treated for total income, working hours, and the probability of absence. The general idea that emerges is that the impacts on these women s labor market outcomes are negligible. If income is not 13

14 affected, working hours might have decreased by at most 3 percent in addition to any other non-treatment related variation in the period. Also, the probability that a women is an absentee, which could admittedly increase by requiring women to stay employed beyond their initial expectations, is not affected. Before we discuss in more detail the DDM estimates, we shift our focus to the choice of the covariates used in the estimation of the propensity score and also to the plausibility of the assumption underlying the matching estimator. This is particularly important in nonexperimental settings, as it is our case, which is aggravated by the fact that there are gender composition differences between the two groups. The choice of the variables in the specification of the probit model observed the basic principle that they should influence both the selection-into-treatment (remain on the job) and the outcome variables. Thus, Table 5 includes potential experience and current job tenure with the respective quadratic terms, year dummies and (log) sales to control for economy-wide shocks and firm-specific, education level dummies, and sector of activity and regional dummies. 4 While the latter two variables might influence more the outcome variable, clearly the other variables are simultaneously important in determining the decision to remain employed (maintain the job) and the outcome variable. The focus of Table 5 is, however, on the balancing properties of the matching procedure. For that purpose, we present a plethora of statistics, namely, the mean for the treatment and control groups for the unmatched and matched samples, the standardized bias measure suggested by Rosenbaum & Rubin (1985), and the joint significance tests and pseudo-r 2 of the propensity score (probit model) estimation following Sianesi (2004). This table illustrates the importance of matching and how successful it is. While before the kernel-based matching procedure, the treatment and control groups presented average differences, e.g. tenure differed by about 2 years, after matching they are reduced to statistically insignificant departures from each other. This is also confirmed by the reduction obtained in the standardized bias and, finally, by the joint statistical significance of the covariates and by the pseudo-r 2 of the propensity score in the unmatched and matched samples estimation procedures. As it can be seen in the last two rows of Table 5, the pseudo-r 2 in the propensity score estimation that used only the treated units and the matched control units falls to values close to zero. The F -test complements this information, 4 This table refers only to the propensity score matching procedure for the after period. Similar testing schemes were conducted for the other components of the DDM estimator with overall results qualitatively identical to the reported ones. The full set of results is available from the authors upon request. 14

15 corroborating the view that matching has successfully eliminated any systematic observable differences between the treated and control groups. With regards to the DDM estimates, we present two estimates, depending on the use of unbalanced panel data (which we treat as repeated cross section) or balanced panel data. The researcher has typically these two options, and the choice of one over the other is dependent on the question to be answered. In the present case, women had access to rather generous early retirement schemes. Therefore, one cannot exclude the possibility that faced with unexpected extensions of their careers, some of them opted for such retirement schemes. Thus, by opting for the balanced panel data, we are in fact looking exclusively over time at those that, as expected by the legislator, extended their careers. For the present case, the two estimates are statistically not different from zero. But if we are allowed to entertain the differences between the two estimates, we observe that the impact is larger for the case of the balanced panel, which might be interpreted as suggesting that those women who decided to remain employed did so because they expected higher returns than those that abandoned the labor force. 6.2 Impact on firms personnel policy We consider three different matching variables: propensity scores, predicted number of women affected by the new legislation (from a Poisson regression), and the estimated probability that a firm employed at least one woman affected (again, from a Poisson regression). The matching method is the nearest neighbour. (We have checked the robustness of the results using kernel matching and the results available upon request are virtually the same.) We also impose the common support. The propensity score is estimated using a large number of variables: a cubic in firm size (measured in terms of workers), a quadratic in the share of women in the workforce, a cubic in the average total pay, a cubic in the average total number of hours worked, a quadratic in the percentage of workers that are men aged 60 or more, a cubic in the year in which the firm was set up, the shares of equity held by domestic and foreign investors, 57 industry dummies and 29 region dummies. We assess the treatment effect in terms of three different labour market variables: hirings, separations and net job creation. Net job creation is constructed from the difference in the total number of workers from year to year in each firm. Hirings are defined as the number of 15

16 workers that are present in one year but not in the previous year; these workers are identified as those whose date of entry into the firm is subsequent to the previous census month in the QP data (March up to 1993 and October from 1994). Finally, separations are defined as the difference between hirings and net job creation. Table 6 present the results concerning the impact of the higher LRA in terms of firm-level job and worker flows. As mentioned before, we consider three different matching variables. Moreover, we consider models with firm fixed effects. Finally, we consider two different sample definitions: all firms present in 1992 and in subsequent years up to 1999 (implying a decreasing sample size over time, due to firm turnover) and only firms present in each one of all years from 1992 to The resulting 6 sets of results are presented in Tables 6 and 7 (each Table then presents the results for each flow variable Hirings, Separations and Net Job Creation in each year from 1995 to 1999.) 5 The general pattern that emerges from these results is that hirings and separations fall significantly for the treated firms. ( The only exceptions to this pattern come from the specifications using the propensity score, fixed effects, and the same firms from 1992 to 1999.) For instance, when considering the Pr(t 1) matching variable with fixed effects, the impact of the introduction of the reform ranges from -1 to -5, regardless whether considering only the same firms or all firms present in each year. Other combinations result in similar patterns. The ATT values described in the Tables are not cumulative: they result from comparing the flow rate of each year (and the flow rate of 1992, in the case of models with fixed effects). The decline in hirings tends to increase from 1995 to 1997 and then to decline up to This is in line with the range of ages we consider when establishing the treatment and control groups. The results about hirings and separations tend to be statistically significant. Another important result is that the declines of hirings and of separations tend to be similar, so that that there is typically no effect upon net job creation. We also calculated the impact of the new law in terms of the ratio of the change in hirings (and separations), as indicated by our estimates of the average treatment effect, with respect to the number of women affected, as indicated by the average percentage of women aged in the size of each firms workforce in We find that that ratio tends to vary between -1 and -3. We also find evidence (available upon request) that most of the impact of the higher LRA 5 We checked the balancing of covariates was satisfactory (results available upon request). 16

17 in terms of the reduction of hirings was felt upon younger workers and, in particular, on younger female workers. 7 Conclusion Increasing the legal retirement age has been considered as the most influential policy dealing with the financial sustainability difficulties of pay-as-you-go pension systems brought about by population ageing. Although the success of such policy is essentially determined in the labor market, our paper is the first to examine how firms adjust their personnel policies when forced to retain their older workers longer than initially expected. We present quasi-experimental evidence about such response, by examining the impact of a 1994 Portuguese law that increased the retirement age of women while leaving unchanged the retirement age of men. Using matched employer-employee panel data and difference-indifferences matching methods, we compare firms that, before the law was announced, employed women old enough to be soon affected by the new law with firms that did not employ such women. After checking that firms did indeed comply with the law, we find that employment and wage levels were virtually unchanged. Moreover, we also find that treated firms did significantly reduce their worker flows (hirings and separations). In our preferred specifications, the results indicate that firms hire approximately one fewer worker for each older worker that is retained due to the higher legal retirement age. The last result suggests that the contribution of higher retirement ages to the sustainability of pensions may be much weaker than previously assumed. References Abadie, A. (2005), Semiparametric difference-in-differences estimators, Review of Economic Studies 72(1), Ashenfelter, O. (1978), Estimating the effect of training programs on earnings, Review of Economic and Statistics 60, Blundell, R. & Costa Dias, M. (2000), Evaluation methods for non-experimental data, Fiscal Studies 21(4),

18 Heckman, J., Ichimura, H., Smith, J. & Todd, P. (1998), Characterizing selection bias using experimental data, Econometrica 66(5), Heckman, J., Ichimura, H. & Todd, P. (1997), Matching as an econometric evaluation estimator: Evidence from evaluating a job training programme, The Review of Economic Studies 64(4), Ichino, A., Schwerdt, G., Winter-Ebmer, R. & Zweimuller, J. (2006), Too old to work, too young to retire?, Economics Department, European University Institute. Meghir, C. & Whitehouse, E. (1997), Labour market transitions and retirement of men in the UK, Journal of Econometrics 79(2), Meyer, B. D. (1995), Natural and quasi-experiments in economics, Journal of Business & Economic Statistics 13, Michalopoulos, C., Bloom, H. & Hill, C. (2004), Can propensity-score methods match the findings from a random assignment evaluation of mandatory welfare-to-work programs?, The Review of Economics and Statistics 86(1), Rosenbaum, P. & Rubin, D. (1983), The central role of the propensity score in observational studies for causal effects, Biometrika 70, Rosenbaum, P. & Rubin, D. (1985), Constructing a control group using multivariate matched sampling methods that incorporate the propensity score, The American Statistician 39(1), Rubin, D. (1977), Assignment to a treatment group on the basis of a covariate, Journal of Educational Statistics 2, Rubin, D. (1979), Using multivariate matched sampling and regression adjustment to control for bias in observational studies, Journal of the American Statistical Association 74, Sianesi, B. (2004), An evaluation of the Swedish system of active labor market programs in the 1990s, Review of Economics and Statistics 86(1), Smith, J. & Todd, P. (2005), Does matching overcome LaLonde s critique of nonexperimental estimators?, Journal of Econometrics 125(1-2),

19 Table 1: Treatment groups: Before and after the new retirement age Treatment groups by age sets (Before=1992) Year: LRA: [57.5, 58) [64.5, 65) [58, 58.5) [64, 64.5) [58.5, 59) [63.5, 64) [59, 59.5) [63, 63.5) [59.5, 60) [62.5, 63) [60, 60.5) [62, 62.5) Treatment groups by age sets (Before = Year t 1) Year: LRA: Before After [63.5, 64) [64.5, 65) Before After [63, 63.5) [64, 64.5) Before After [62.5, 63) [63.5, 64) Before After [62, 62.5) [63, 63.5) Before After [61.5, 62) [62.5, 63) Before After [60, 60.5) [62, 62.5) Notes: (1) Treatment group: The set of individuals (women) who would have retired in year t if the legal retirement age (LRA) had remained at its value of year t 1. For example, women in the age group [60, 60.5) in 1992 would have retired in 1994 if the LRA had remained at 62 years. (2) Before period: (i) In the top panel, the before is always set to 1992, when the women s LRA was 62 years and no legislative change was expected; (ii) In the bottom panel, we slide the before period along with the after period. In particular, the before period is set to the year before the after period, with the exception of the first case, which has 1992 as before and 1994 as after. Table 2: Labor Force Status Before and After the Change in the Legislation (Logit results) Labor Force Status: Employment Inactivity Regressor Gender (Male=1) (0.005) (0.005) Age Group (0.028) (0.028) Treated Group (0.031) (0.031) Number of observations 229, ,066 Wald test 28, ,942.3 Source: Inquérito ao Emprego. The specification includes 17 age and 8 year dummies. Standard errors in parenthesis. 19

20 Table 3: Transition from Employment into Inactivity (Cox Hazard Model with Time-Varying Covariates) Regressor Gender (Male=1) (0.069) Age Group (0.298) Age Group Female (0.177) Age Group After (0.210) Age Group After Female (0.309) Number of observations 1,167 Wald test 47.3 Source: Inquérito ao Emprego. The specification includes 8 year dummies. Standard errors in parenthesis. 20

21 Table 4: Labor market outcomes: Impact on postponed women retirees total income, working hours and probability of working Before period: 1992 Before Period: y t 1 D-in-D D-in-D Matching Matching Variable unrest. (1) rest. (2) c. section (3) panel (4) unrest. (1) rest. (2) c. section (3) panel (4) Log earnings (0.013) (0.010) (0.015) (0.011) (0.014) (0.012) (0.016) (0.008) 52,120 52,120 53,570 10,204 37,661 37,661 39,076 12, Log hours (0.007) (0.007) (0.010) (0.009) (0.008) (0.008) (0.012) (0.007) 50,628 50,628 52,166 9,823 37,069 37,069 38,571 12, Pr(Absentee) (5) (0.009) (0.010) , , Notes: The values reported for each pair variable and estimator are point estimate, standard error, number of observations and R 2. (1) The D-in-D unrestricted estimator does not control for confounding factors; (2) The OLS D-in-D restricted estimator is based on a linear specification, controlling for observable characteristics; (3) DDM estimator with kernel matching on the propensity score with repeated cross-section data; (4) DDM estimator with kernel matching on the propensity score with balanced panel data. The set of variables used with the estimation of the propensity score and in the restricted OLS D-in-D estimator are reported in??. (5) It refers to the probability that a employee although registered in QP is reported as having worked zero hours, and (s)he is taken as absentee. 21

22 Table 5: Balancing properties of the kernel based propensity score matching for the unbalanced panel data in the after period Unbalanced panel data (as repeated cross-section) After Mean t-test Reduction Variable Sample Treated Control p-value (1) % bias (2) bias Experience Unmatched Matched Experience 2 Unmatched Matched Tenure Unmatched Matched Tenure 2 Unmatched Matched Total sales Unmatched Matched Education: High school Unmatched Matched College Unmatched Matched Year dummies: 1994 Unmatched Matched Unmatched Matched Unmatched Matched Unmatched Matched Unmatched Matched Unmatched Matched Observations: Off common support 4,324 13,259 On common support 12 0 Unmatched Matched Bias summary statistics: Mean Std. Dev Maximum Minimum Pseudo R 2(3) Joint F -test, p-value Notes: The table does not exhaustively list all variables included in the probit model used to estimate the propensity scores; we omit from the table the balancing property of sector of activity and regional dummy variables. (1) The p-value of the t-test for the equality of means in the treated and control groups, both before and after matching. (2) Bias is the standardized bias as suggested by Rosenbaum & Rubin (1985) reported together with the achieved percentage reduction in bias. (3) Pseudo R 2 from the probit model estimation of the propensity scores, including all variables reported above, before and after the matching process (Sianesi 2004). 22

23 Table 6: Average treatment effect on hiring, separtion and net job flows Matching on: Number of women Pr(t 1 woman) Propensity score Hirings ATE SE ATE SE ATE SE Separations Net Job Flows Notes: Source: Quadros de Pessoal. ATE refers to the average treatment effect in terms of the worker flow considered and at the year under analysis. SE denotes analytical standard errors. Estimation is done using by fixed effects where estimates are based on the difference in the level of the worker flows between the year under analysis and the base year, The matching variable number of women is the predicted number of affected women from a Poisson regression; Pr(t 1 woman) is equivalent to the propensity score but the estimates are obtained from the Poisson regression; propensity score refers to the conventional propensity score method. 23

24 Table 7: Average treatment effect on hiring, separtion and net job flows (continuing firms Matching on: Number of women Pr(t 1 woman) Propensity score Hirings ATE SE ATE SE ATE SE Separations Net Job Flows Notes: Source: Quadros de Pessoal. ATE refers to the average treatment effect in terms of the worker flow considered and at the year under analysis. SE denotes analytical standard errors. Estimation is done using by fixed effects where estimates are based on the difference in the level of the worker flows between the year under analysis and the base year, Continuing firms refer to an analysis in which only firms present all year between 1992 and 1999 are considered. The matching variable number of women is the predicted number of affected women from a Poisson regression; Pr(t 1 woman) is equivalent to the propensity score but the estimates are obtained from the Poisson regression; propensity score refers to the conventional propensity score method. 24