Evaluating the Dynamic Employment Effects of Training Programs in East Germany Using Conditional Difference in Differences

Evaluating the Dynamic Employment Effects of Training Programs in East Germany

Using Conditional Difference–in–Differences

Annette Bergemann ⁺ , Bernd Fitzenberger ^§ , Stefan Speckesser ^&

Long Version – April 2008

Abstract: This study analyzes the employment effects of training in East Ger- many. We propose and apply an extension of the widely used conditional difference- in-differences estimator. Focusing on transition rates between nonemployment and employment, we take into account that employment is a state and duration depen- dent process. Our results show that using transition rates is more informative than using unconditional employment rates as commonly done in the literature. More- over, the results indicate that due to the labor market turbulence during the East German transformation process, the focus on labor market dynamics is important.

Training as a first participation in a program of Active Labor Market Policies shows zero to positive effects both on reemployment probabilities and on probabilities of remaining employed with notable variation over the different start dates of the pro- gram.

Keywords: Evaluation of active labor market policy in East Germany, transition rates, employment dynamics, Ashenfelter’s Dip, nonparametric matching, condi- tional difference–in–differences, bootstrap

JEL classification: C 14, C 23, H 43, J 64, J 68

∗ This is the unabridged version of our paper which is forthcoming in the Journal of Applied Econometrics. We especially thank Gerard van den Berg, Ed Vytlacil, three anonymous referees, and the editor for their very helpful comments. We are grateful for numerous helpful comments received in numerous seminars at various universities and at various conferences. Thanks goes also to Thomas Ketzmerick of the ZSH for the provision and help with the data. Annette Bergemann acknowledges the support by a Marie Curie Fellowship of the European Community Programme

‘EU Training and Mobility of Researcher’ under contract number HPMF-CT-2002-02047. The usual disclaimer applies.

Corresponding Author: Bernd Fitzenberger, Department of Economics, Albert Ludwigs-University Freiburg, 79085 Freiburg, Germany, Email: [email protected]

+ Free University Amsterdam and IZA ^§ Albert Ludwigs-University Freiburg, ZEW, IZA, and

IFS ^& Westminster Business School, University of Westminster, London

1 Introduction

After the formation of the German “Social and Economic Union” in 1990, the East German economy underwent enormous changes. It had to transform from a com- mand driven backward economy to a market economy at an unprecedented speed.

The transformation process brought about high unemployment in East Germany.

To increase the employment chances of the unemployed, the German government decided to provide on a high scale Active Labor Market Policies (ALMP) in East Germany. These programs mainly consisted of training and temporary employment schemes. Fifteen years after the reunification, the German Federal Employment Ser- vice still spends around e 10 Billion for ALMP (Bundesanstalt f¨ur Arbeit, 2005).

About 50% of this budget is spent in East Germany with a labor force less than one sixth of Germany as a whole. Quite a significant share of the labor force in East Germany has been participating in programs of ALMP since 1990.

During the last decade, there were a lot of pessimistic assessments regarding the usefulness of public sector sponsored training programs in raising employment chances of the unemployed (see the surveys in Fay, 1996; Heckman et al., 1999;

Martin and Grubb, 2001; Kluve and Schmidt, 2002). These studies doubt that large scale training programs, which are not well targeted, are successful in raising employment. However, evidence for Eastern European transition economies (other than East Germany) has often shown positive effects (Kluve et al., 1999 and 2004;

Lubyova and Van Ours, 1999; Puhani, 1999). ¹

For East Germany, appropriate data for an evaluation of public sector sponsored training were not available for a long time and, until recently, the available evidence has been quite mixed. ² Most studies suffer from data limitations, either from a small number of participants (e.g. Lechner, 2000, using the German Socio-Economic

1 Another exception consists of training programs for prime–aged women in countries with a relatively low female labor force participation (see the survey by Bergemann and Van den Berg, 2007).

2 See Bergemann et al. (2004), Fitzenberger and Prey (2000), Kraus et al. (1999), or Lechner

(2000) for exemplary studies based on survey data. Hagen and Steiner (2000), Speckesser (2004,

chapter 1) and Wunsch (2006, section 6.5) provide comprehensive surveys of this literature, which

is not reviewed here for the sake of brevity, and discuss critically the data used.

Panel) or from the data being limited to the early 1990s and lacking the employment history on a monthly basis (e.g. Fitzenberger and Prey, 2000, using the Labor Mar- ket Monitor for East Germany). Recently, administrative data brought about more evidence on the effectiveness of further training indicating short-term reductions in the employment outcomes of participants relative to non-participation, but signifi- cantly positive effects of ALMP in the medium and long-run, see Fitzenberger and Speckesser (2007) and Lechner et al. (2008). While studies based on administra- tive data only estimate the effects on employment subject to the mandatory social insurance system our analysis applying employment outcomes reported by survey participants can also consider self-employment or public sector employment, which usually remains unrecorded in administrative data. Lechner et al. (2008) evaluate effects of training programs on employment. They find strong evidence that, on av- erage, most training programs under investigation increase long–term employment prospects. Fitzenberger and Speckesser (2007) estimate the employment effects of one major training program (Provision of Specific Professional Skills and Techniques, SPST) against nonparticipation in SPST for 36 months after the beginning of the treatment. The analysis is performed only for the 1993 inflow sample into unemploy- ment. The analysis finds positive medium–run employment effects. These studies are based on administrative data since 1992 and they only analyze training programs starting in 1993 or later, because there are no administrative data available for the time shortly after the reunification.

We focus on the employment effect of public sector sponsored training programs in East Germany starting with the reunification for the group of individuals who belonged to the active labor force in 1990. This group was fully hit by the transfor- mation shock. In the early 90s, training was often considered to be the most effective among the ALMP programs as it was supposed to provide skills that were in de- mand in a market economy but not in sufficient supply due to the former educational system. ³ Training was in term of participants the largest ALMP program.

3 Forecasts of the future labor demand in the early 1990s for both East and West Germany (e.g.

Prognos 1993) usually indicated a severe shortage especially for service sector skills in the East if

catching up to the economic situation of the West. Human capital transformation was believed to

satisfy the changing labor demand and at the same time to reduce unemployment (OECD 1994).

We implement a semiparametric conditional difference–in–differences estimator (CDiD) (Heckman, Ichimura, Smith and Todd, 1998). We extend the CDiD ap- proach to using transition rates between different labor market states as outcome variables instead of exclusively using employment rates in levels as is often done in the literature. The focus on transition rates is able to take into account the special economic situation of East Germany that was characterized by a labor market that was in a major restructuring process. An approach that only uses employment rates might not capture sufficiently that the labor market is in a dynamic adjustment process. ⁴ As two benchmarks to estimate the treatment effects on unconditional employment rates, we also implement a matching estimator, which matches on em- ployment history, and a CDiD estimator. Additionally, we also use the matching estimator in order to estimate effects on earnings.

We apply propensity score matching in the first stage and then estimate average effects of treatment on the treated. The analysis matches treated individuals to non- participants using local linear matching to account for selection on observables. We consider selection on time invariant unobservable characteristics by implementing a conditional difference–in–differences estimator in matched samples. Our inference uses a bootstrap approach taking account of the estimation error in the propensity score.

Our results indicate that modeling transition rates is more appropriate than using unconditional employment rates in the given labor market situation and the data at hand. Moreover, the approach is more informative, as we can determine whether ALMP programs help workers to find a job and/or whether they stabilize employment. We find zero to positive employment effects. Depending on the start date of the program we find significant variation concerning job finding rates and employment stability.

Next to the extension of the CDiD to using transition rates as outcome variables, our paper involves two further methodological innovations: First, anticipation effects

4 See also Kluve et al. (1999) who use conditional probabilities for the analysis of ALMP effects

in Poland. However, they apply a pure matching approach and define the conditional probabilities

over several yearly quarters.

regarding future participation or eligibility criteria (Ashenfelter’s Dip) requiring a certain elapsed duration of unemployment for participation can affect the results of difference–in–differences estimator (Heckman and Smith, 1999). Using institutional knowledge and data inspection to bound the start of Ashenfelter’s Dip, we suggest for our context a long–run difference–in–differences estimator to take account of possible effects of anticipation and participation rules which might otherwise contaminate the estimation results. Second, we suggest a heuristic cross–validation procedure for the bandwidth choice that is well suited to the estimation of conditional expectations for counterfactual variables.

Some recent publications propose a number of extensions to the standard static evaluation approaches to consider dynamic selection issues involved here: Similar to our paper, the timing–of–events approach (Abbring and Van den Berg, 2003;

Fredriksson and Johanson, 2003) focuses on transition rates from unemployment to employment by modeling the duration of unemployment as outcome. Sianesi (2004) emphasizes that treatment differs by the elapsed duration of unemployment at the beginning of the program and that future program participants should be used in the comparison group for earlier treatments. We estimate the treatment effects during two time periods and we do not evaluate the effect of training now versus waiting where the latter may include the possibility of training in the future during the same time period.

Also, our analysis goes beyond the aforementioned studies in two respects: We model the effects of treatment on both the probability of leaving nonemployment and of remaining employed. Extending the standard CDiD estimator, we allow for unobserved, state dependent individual specific fixed effects.

The paper is organized as follows: Section 2 gives a short description of economic development in East Germany. Section 3 summarizes the institutional settings of training. Section 4 proceeds to the microeconomic evaluation approach used here.

Section 5 describes the data set used and compares participants and nonparticipants.

Section 6 shows the implementation of the estimation approaches and discusses the

empirical results. Section 7 concludes. The appendix includes detailed descriptive

evidence and results.

2 The Economic Development in East Germany

During reunification in 1990, the East German economy underwent unprecedented changes. It was rapidly transformed from a command driven backward economy to a market economy facing competition from Western economies.

The economic situation in the last years of the socialistic German Democratic Republic was shaped by stagnation, an obsolete capital stock, and production pro- cesses which were highly overstaffed. This resulted in high employment rates and a productivity level that fell substantially short of West European standards. Al- though formally highly qualified, the workforce lacked specific skills necessary in a competitive environment. Moreover, compared to modern market economies, the production structure was heavily biased towards manufacturing goods. ⁵

Following July 01, 1990, the Economic, Monetary and Social Union transferred the West German legal, social and economic regulation to East Germany together with an exchange rate highly overvaluing the East German currency. Furthermore, in 1991 trade union and employer representatives agreed on a wage path quickly converging to West German levels in 1991, which stood in sharp contrast to the productivity level in East Germany. In 1993, however, the idea of a fast wage convergence was abandoned.

Production collapsed during the first two years after the reunification. Produc- tion in 1991 only reached 2/3 of its 1989 level. Afterwards, real GDP was growing rapidly with annual growth rates between 7.7% and 11.9%. But since 1995, eco- nomic growth has ebbed off with growth rates between 1.6 and -0.2%. At the same time, labor productivity increased from 51.2% in 1991 of the West German level to 74.2% in 2004. However, wage increases were even larger. Wages in 1991 amounted to 56.1% of the West German level in 1991 and increased to 81.5% in 2004.

The labor market suffered from a dramatic disequilibrium. In 1989 close to 9.6 million individuals were employed. This figure dropped sharply to 6.5 million in 1997 and remained fairly constant since then. To fight the resulting high unemploy-

5 Unless indicated otherwise, the following overview is based on Akerlof, Rose, Yellen and Hesse-

nius (1991), Bundesministerium f¨ ur Verkehr, Bau und Stadtentwicklung (2005), Hunt (2006), van

Hagen and Strauch (2001), and Wurzel (2001).

ment, active and passive labor market policies were heavily used in East Germany (see figure 1). These programs should also provide an immediate cushion for the un- employed and support the goal that the standard of living in East Germany should converge quickly to Western levels in order to avoid large scale outmigration and to foster political stability.

Although the composition and scale changed markedly over time, training pro- grams played a central role during the 1990’s. It was strongly believed that training programs were important as the East German workforce lacked skills which are nec- essary in a competitive environment, especially in the light of the likely changes or the sectoral production composition. Compared to modern market economies, production related services were for example strongly under-represented in the pre–

reunification period (Prognos, 1993; OECD, 1994; Bundesanstalt f¨ur Arbeit, 1991).

Shortly after reunification, early retirement programs and short-time work pro- grams were heavily used in order to reduce - at least in the short run - open un- employment (see figure 1). In ALMP, training programs and job creation schemes dominated. In addition to the main objective of increasing the re–employment probability, especially job creation schemes were also regarded as social measures.

Participation in ALMP peaked in 1992 with over 800.000 individuals participating on average in full time programs. From 1993 onwards budget constraints forced the labor offices to reduce the number of participants. Open unemployment increased from 1 million in 1991 to 1.6 million individuals in 2005.

From 1989 to 1991 migration from East to West Germany was substantial. In

1991, the net migration amounted to 171.000 individuals. However, after uncertainty

concerning the political and economic situation disappeared, migration ebbed away

and was increasingly matched by migration in the opposite direction. In 1996, net

migration to the West reached its minimum with 26.000. Before 1997 net outflow

was confined to lower and medium qualified labor. Since 1997, however, the net

flow has increased again and the net outflow is highest for highly qualified labor (see

Kempe 2001).

3 Training in East Germany

3.1 Institutional Background

Between 1969 and 1997, training as part of Active Labor Market Policy in Germany was regulated by the Labor Promotion Act (Arbeitsf¨orderungsgesetz, AFG). Despite a number of changes in the regulation over this time period, the basic design of training programs remained almost unchanged until the AFG was replaced by the new Social Law Book (Sozialgesetzbuch, SGB) III in 1998. The German Federal Labor Office (Bundesanstalt f¨ur Arbeit, BA) was in charge of implementing these programs in addition to being responsible for job placement and for granting un- employment benefits. In the course of German reunification, these programs were extended to East Germany (§ 249 AFG).

Training programs under the AFG legislation consist of the following two types:

Further Vocational Training (Fortbildung) and Re–training (Umschulung). ⁶

Further vocational training includes mainly courses for the assessment, main- tenance, and extension of skills. The duration of these courses depends on the characteristics of the participants and varies between 2 and 8 months. The courses are mainly offered by private sector training companies. Under the heading of fur- ther vocational training also Short–term training courses were implemented. These are courses that provide skill assessment, orientation, and guidance. The courses are intended to increase the placement rate of the unemployed. Mostly, they do not provide occupational skills but aim at maintaining search intensity and increasing the hiring chances. The courses usually last from two weeks to two months.

Re–training enables vocational re–orientation if no adequate employment can be found because of skill obsolescence. Re–training is supported by the BA for a period up to 2 years and aims at providing a new certified vocational training degree.

Participation in training is basically voluntary. Individuals face a variety of incentives to participate. Next to the potential benefits in terms of increase of the employment chances, participation can also offer some instantaneous utility,

6 By law, also so called Integration Subsidies are part of the the array of training programs, but

in reality these programs are closer to wage subsidies and therefore not part of this analysis.

especially in this time with high uncertainty (being together with other job seekers, the learning experience, motivation, etc.).

Enrollment into training is also attractive from a financial point of view. First of all, participants can be granted an income maintenance payment (Unterhalts- geld). The time of participation in the training program does not count towards the limited time of the unemployment benefits. Second, under certain conditions the participants can re–qualify for, or prolong their eligibility period for unemployment benefits. Third, the refusal of participation in a training program despite the recom- mendation of a caseworker can lead to the imposition of a sanction, which basically meant that their benefit payments would stop completely for between six weeks and three months.

3.2 Changing Incentives for Participation

Initiated after 20 years of an unprecedented economic growth in post–war West Ger- many, the 1969 legislation of Active Labor Market Policies and training programs in particular was fairly generous. The design of these programs provided institu- tionally built–in incentives to participate because participants benefited from rather long-term programs, offering high levels of benefit and post-participation advantages such as renewed unemployment benefits after participation. As often observed in European welfare states (e.g. Calmfors 1994), the institutional incentives for par- ticipation were probably as important as the objective of re-integration into the labor market through human capital investment. As a consequence, the program intake consisted of heterogeneous participants: On the one hand, participants with good prospects might have started training in order to get a decent job. On the other hand, job seekers might have started the program because of the institutional incentives even though the program was not effective to achieve the objective of reintegration into the labor market.

With the changing economic situation in the 1990’s, following the German reuni-

fication a number of changes concerning the institutional settings of training took

place affecting also strongly the incentives to participate. The most important ones

are the following:

1. Change in provision of training: Shortly after the reunification, training pro- grams were massively supplied. However, mainly due to tighter public budgets, the number of courses provided declined strongly after 1992.

2. Short–term training programs were formally abolished in 1992. In 1993, a new program with the same purpose was established, but participants were no longer considered as taking part in training programs. Before 1993 pro- gram participants were not required to prove active job search and job place- ment while on the program. After 1993, participants in the new program remained openly unemployed, including the requirement for a job seeker on unemployment benefit to continue active job search and to start employment immediately when offered a job corresponding to their previous occupation.

3. Change in income maintenance payments: Participants in training might have been either recipients of unemployment benefit (i.e. those with unemployment of less than one year) or of unemployment assistance (long–term unemployed, receiving lower means–tested benefits). During the early 1990’s, participants, who previously had received unemployment benefits, received income main- tenance payments exceeding the standard unemployment benefits by 3 per- centage points, while participants entering the program from means–tested benefits continued to receive benefits at the level of 58% of previous net earn- ings. Legislation reduced the benefits for participants starting training after unemployment benefit in 1994. Since then, the level of income maintenance payments of 67% of previous net earnings for participants with children and 60% for participants without children matches the level of unemployment ben- efits. This decline in the income maintenance payment for the most important group of participants reduced institutional incentives of participating in train- ing programs (see Eichler/Lechner 2001, 221).

4. Change in eligibility rules for participation: Originally, participation in a train-

ing program was open to participants who had not been unemployed before as

long as the case worker deemed participation in training as “advisable”. This

type of training intended to prevent future unemployment, to increase the la-

bor market prospects in the future, or to foster re–integration of individuals returning to the labor market. In 1994, a reform restricted access to individu- als fulfilling the criteria for “necessary” training, i.e. to formerly unemployed participants. However, especially in East Germany, participation under the weak criterion of “being threatened by unemployment” was still possible.

These four major changes over the period of investigation of our study reduced both the overall program intake as well as the participation due to institutional incentives. One can expect the outcomes of training programs to be different for the later years compared to the early 1990’s, as the mix of participants in training programs changed particularly following the 1994 reform. We conclude that a cred- ible evaluation strategy has to account for this and our empirical analysis considers both periods separately.

The reduction in program intake mainly affected the selection of participants (more targeted towards special problem groups). The end of explicit short–term training programs made the programs longer and more expensive. Hence, we expect the program mix to have become less focused on immediate placement of partici- pants. After the change, there is a stronger focus on providing additional skills and helping participants to signal their skills. On the one hand, these changes result in stronger incentives to participate than before the reform. This and the knowledge, that ALMP would be a permanent feature of the East German labor market, were likely to cause unemployed individuals to decrease their search effort for a new job in anticipation of participation. On the other hand, training programs become less attractive, especially for workers who are still employed. Over time, a change in the selection of the program group occurs, with training increasingly targeting problem groups with a priori significantly lower employment chances.

3.3 Aggregate Participation

Training programs were implemented in East Germany immediately after unification

(see figure 2): 94,000 persons started to participate during the last three months of

1990. In 1992, the maximum was reached with 774,000 entries. Between 1993 and

1997 the number declined considerably to 155,000 in 1997. Afterwards participation

recovered to a level slightly above 180,000 reflecting the ongoing importance of these programs in East Germany. The share of entries into re–training as a percentage of total training varies between 15% in 1991 and 28% in 1993. Separate figures for the subprograms are not available for the time after 1997 due to the change in the regulation.

Stocks of participants show a similar pattern (see figure 3). The maximum was reached in 1992, amounting to 492,000 participants on average. Participation has been declining afterwards (2000: 139,700, 2002: 129,000 participants). The trends for the subprograms (not reported in figure 3) are analogous.

Direct costs for participation (see figure 3, right axis) – income maintenance, course fees, travel costs etc. – increased continuously over time. In 1991, when short–

term training programs still existed, annual costs were at e 8,000 per participant.

These cost increased to e 14,600 in 1995 and to e 20,600 in 2002.

4 Evaluation Approach

Our empirical analysis is based on the potential outcome approach to causality (Roy, 1951, Rubin, 1974), see the survey Heckman, LaLonde, and Smith (1999).

We focus on estimating the average causal effect of treatment on the treated (TT) in the binary treatment case. ⁷ TT is given by E(Y ¹ |D = 1) − E(Y ⁰ |D = 1), where the treatment outcome Y ¹ and the nontreatment outcome Y ⁰ are the two potential outcomes and D denotes the treatment dummy. Our outcome variable of interest Y is an employment dummy, in our preferred approach conditional on the

7 The framework can be extended to allow for multiple, exclusive treatments. Imbens (2000) and

Lechner (2001) show the extension of the standard propensity score matching estimators for this

purpose. Although this would be a natural extension in our application, we do not think that our

data are sufficiently rich enough for this purpose. Our analysis is very demanding since we argue

that matching on observable covariates will not suffice to control for selection bias and since we

model the effects on transition rates between different labor market states. Therefore, we restrict

ourselves to estimating TT for training where the comparison group is the group of all individuals

who either do not participate in any program or who only participate in other programs where the

latter two are weighted by their sample frequencies.

employment status in the previous month resulting in a transition dummy. ⁸ The observed outcome Y is given by Y = DY ¹ + (1 − D)Y ⁰ .

The evaluation problem for estimating the TT consists of estimating the counter- factual outcome in the nonparticipation situation for the participating individuals (D = 1). Identifying assumptions are needed to estimate the counterfactual based on the outcomes for nonparticipants (D = 0).

One important aspect for the implementation of a treatment effect estimator in our context is connected with the observation that training in East Germany is associated with a disproportionate decline in employment rates shortly before the start of the treatment, as it is typical for training among the unemployed. A similar finding termed Ashenfelter’s Dip was first discovered when evaluating the treatment effects on earnings (Ashenfelter, 1978). Later research demonstrated that the same phenomenon can also occur regarding employment, see Heckman, LaLonde and Smith (1999), Heckman and Smith - henceforth HS -, 1999, and Fitzenberger and Prey (2000). We argue that in our context the decline in employment is caused by participation rules or anticipation effects (HS) and we implement our estimators to allow for this relationship.

Regarding participation rules, the target group of public sector sponsored train- ing are the unemployed and employees with a high risk of unemployment. Antici- pation effects arise because unemployed individuals and employees with a high risk of losing their jobs reduce their search effort, because they know about the avail- ability of a training program in the near future. Analogous to the finding in the US literature (Ashenfelter and Card, 1985, Heckman, Ichimura, Smith, and Todd - henceforth HIST - , 1999, HS) that earnings decline before training starts, we denote the decline in employment as Ashenfelter’s Dip (or the preprogram dip) in employment. The problem that Ashenfelter’s Dip imposes for evaluation studies is mostly discussed in the context of conditional Difference–in–Difference estimators (henceforth CDiD). HIST and HS for example, emphasize that CDiD estimators are quite sensitive with regard to Ashenfelter’s Dip, a problem which is also summa- rized under the heading of the “fallacy of alignment” (see Heckman, LaLonde and

8 For the evaluation approach with respect to the outcome variable earnings see section 4.4.

Smith, 1999). On the one hand, if the decline in employment before treatment is transient then contrasting the before–after difference in employment for the treated with that of the nontreated will overstate the treatment effect. On the other hand, if the decline in employment is persistent then DiD based on a longer preprogram period will underestimate the treatment effect. This is analogous to the discussion in HS, p. 317, for the dip in earnings.

For US data, HS show that the short–run dynamics in unemployment are an important determinant of treatment and that the preprogram dip in earnings is transitory. Matching on the earnings history does not allow to take account of the dip. Rather it proves important to match on the short–run dynamics in unem- ployment which HIST and HS include as determinants of the propensity score. To account for the dynamics in earnings shortly before and shortly after treatment, the CDiD estimators in HIST and HS are based on before–after differences which are symmetric in time before and after treatment start. This builds on the iden- tifying assumption that the selection bias after matching on the propensity score is the same symmetrically around the treatment start. This approach proves use- ful to reduce considerably the bias in nonexperimental TT estimates as shown by HIST and HS who have experimental estimates as a benchmark. We think that such a symmetry assumption is not warranted in our application because there is no reason to believe that in the East German context the selection bias in the em- ployment recovery for the time shortly after participation is a mirror image to the preprogram dip in employment. In fact, since HIST and HS match on short–run preprogram unemployment dynamics, such an assumption would not even be jus- tifiable for employment in their case. We will suggest a CDiD estimator based on long–run preprogram differences that lie before the time period of the preprogram dip.

This paper discusses and implements three different estimators. First, as a bench-

mark approach, we introduce a matching estimator for the effects on employment

rates and earnings. With respect to matching on the labor force history, it appears

naturally to only match on the long–run preprogram history in order to circum-

vent potential problems with respect to Ashenfelter’s Dip. This comes at the cost

of ignoring the short–run preprogram history for the selection into the program.

Note that simply matching on the short–run preprogram history would be incorrect resulting in a fallacy of alignment.

As the second approach, we consider a static CDiD estimator (henceforth CDiDS) in order to estimate the effect on employment rates that is based on the long–run preprogram differences. Similar to the approach in HIST and HS, the CDiDS estimator takes account of the link between the treatment start and the short–run preprogram employment history by matching on the employment status in the month before program start for those who are nonemployed in that month.

This way, the matched nontreated individuals are at similar risk of participating in training, which is necessary for an appropriate control group. As becomes ev- ident below, matching on the employment status in the month before treatment start should not be necessary for those who are employed in that month. ⁹ Note that the short–run preprogram employment history does not enter the before–after differences used for CDiDS estimation. However, this approach requires a stable long–run pre–program difference in employment rates between treated and matched controls, which we do not achieve in our application.

Our third preferred estimator uses CDiD in employment rates conditional upon employment state in the previous month (discrete transition rates or ’hazard rates’) and conditional upon duration dependence (henceforth CDiDHR). We develop this estimator on the basis of an employment model with state dependent transition rates, duration dependence, additive unobserved heterogeneity, and heterogeneous treatment effects. CDiDHR is a natural extension of the CDiDS. CDiDHR takes ac- count of short–run dynamics in two ways: First, by conditioning on the employment state in the previous month and on the time in the current employment state, we automatically account for the short–run dynamics in employment when matching treated and nontreated individuals at the time of evaluation. Second, we match on the employment status in the month before program start for those who are nonem-

9 In East Germany there were a number of transitions from employment to training without an

intervening spell of nonemployment. Apparently, these participants are less selective because in

the transition process a large fraction of the East German employees workforce was at the risk of

becoming unemployed.

ployed. With this approach we are able to achieve parallel long–run preprogram differences between treated and matched non–treated.

In the following, we develop the three estimation approaches more formally and we provide implementation details. In particular, we develop a new cross–validation rule to choose bandwidths for kernel matching. Last, we discuss applying the cross–

sectional matching estimator also for the TT effects of training on earnings taking account of the fact that earnings are only observed in the last three years of our observation period.

4.1 Matching on Employment History and CDiDS

Building on the Conditional Mean Independence Assumption (CIA), a standard matching estimator would involve matching the employment history and the relevant characteristics X to contrast the post treatment employment rates for treated and matched nontreated (see Heckman, LaLonde, and Smith, 1999). To account for the preprogram employment dip, it would seem advisable to match on the long–run preprogram employment history, i.e. for a time before Ashenfelter’s Dip starts. We specify the start of Ashenfelter’s Dip conservatively and we let it vary over time (see section 6.2 and 6.4). Shortly after the German reunification individuals could not have expected the huge supply of training programs. Thus, anticipation of program participation could only occur shortly before the beginning of the participation.

Likewise, participation rules were only applied in very lax way in 1990 and 1991.

With the reduction of supply of training courses, participation rules became stricter but at the same time it became obvious that training courses would be a permanent feature of the labor market. Consequently, we let the time of Ashenfelter’s Dip increase during early 1990’s.

We implement the cross–sectional matching estimator as benchmark approach.

To estimate the expected nonparticipation outcome for the participants with observ-

able characteristics X, it suffices to take the average outcome for nonparticipants

with the same X and the same long–run preprogram employment history. Based

on the CIA, the expected nontreatment outcome for a participant i is estimated by

the fitted value of a nonparametric regression in the sample of nonparticipants at

point X and at the employment history. This is implemented by a bivariate kernel regression on the propensity score and on the employment history. Differences in the long–run preprogram employment history are summarized by the Mahalanobis distance. The nonparametric regression can be represented by a weight function w

(i, j) that gives a higher weight to nonparticipants j the stronger his similarity to participant i in terms of X and the employment history using a product ker- nel. For each i, these weights sum up to one over j ( ^P _j∈{D=0} w

(i, j) = 1). The estimated TT is then

1 N 1

X

i∈{D=1}

 

 Y _i ¹ − ^X

j∈{D=0}

w

(i, j) Y _j ⁰

 

 , (1)

with N ₀ the number of nonparticipants j and N ₁ the number of participants i. We use local linear matching for the propensity score and the employment history. The product kernel is given by (for ease of notation, we omit the index N ₀ )

K(i, j) = φ

à p _i − p _j h _p

!

· exp

Ã

−

"

mdist(i, j) h ² _m

#!

(2)

where p _i , p _j are the estimated propensity scores for individuals i, j, mdist(i, j) is the Mahalanobis distance in the employment history (difference in vector of monthly employment dummies), h _p , h _m are the two bandwidths, and φ is the Gaussian kernel. The weights are given by w

(i, j) = K(i, j)/ ^P _j∈{D=0} K(i, j).

As a simple alternative to the matching estimator discussed so far, CDiDS takes account of the short–run dynamics in the selection into training and accounts for time–invariant, additively separable selection bias due to unobserved characteristics.

For instance, unobserved characteristics could be due to differences in the motivation of participants or could reflect that programs are targeted to individuals with some particular problems in the labor market. The CDiDS estimator analyzes the before–

after change in in employment rate instead of its level in equation (1).

Following the approach in HIST, ¹⁰ we use local linear matching based on the estimated propensity score to match participants i and nonparticipants j in the same time period. In addition, we also match on being nonemployed in the month

10 See also Blundell, Costa Dias, Meghir and Van Reenen (2004) for an application of the CDiD,

where age eligibility rules and regional variation in the provision of program are used to take

account of selection effects.

before treatment start using a product kernel analogous to equation (2), where the distance in the employment status in the month before treatment (only for those participants who are nonemployed in the month before) is used as a one–dimensional Mahalanobis distance.

For treatment in period τ , i.e. conditional on τ _i = τ (τ _i is the random time individual i first enrolls in training), the simple CDiDS–estimator for the treatment effect on the employment rate in period t = t1 + τ is given by

1 N 1

N

X

i=1



 Y _{i,τ +t1} ¹ − Y _{i,τ +t0} ⁰ − ^X

j

w _i,j (Y _{j,τ +t1} ⁰ − Y _{j,τ +t0} ⁰ )



(3) 

where period τ + t1 (t1 > 0) lies after and τ + t0 (t0 < 0) before treatment. t1 and t0 are defined relative to the actual beginning of the treatment τ . N 1 is the number of participants i for whom the (t1, t0) difference can be determined. Note that we only match comparison individuals j who do not receive treatment during the observation period under consideration.

We implement the CDiDS using long–run preprogram differences in the outcome variable after matching to control for remaining unobservable differences. Therefore, t0 must lie before −ad, the start of Ashenfelter’s Dip. ¹¹ This is parallel to the matching approach where the existence of the preprogram employment dip precludes that we use the short–run preprogram dynamics in employment to match. For the CDIDS, the preprogram employment dip does not allow the use of the short–run dynamics for the before–after differences. Using the short–run preprogram dynamics in either way would result in a fallacy of alignment.

4.2 Conditional Difference–in–Differences in Hazard Rates (CDiDHR)

4.2.1 Employment Model and Ashenfelter’s Dip

We specify an econometric model for employment in order to develop and discuss the the estimator for the effects on transition rates. The model takes account of

11 As discussed below (footnote 15) in greater detail, we do not take symmetric differences t0 =

−t1, in contrast to HS. We do not think the employment recovery after the beginning of treatment

is likely to be symmetric to the decline in employment before treatment.

important features of employment dynamics such as state dependence and duration dependence. The model represents a nonparametric version of a linear probability regression specification for employment probability with a fixed effect. This model allows for a CDiD estimation of the treatment effects on state specific employment rates.

As the we allow for state dependency in the employment Y _it of individual i in month t and we distinguish between two different labor market states, notably employment and nonemployment, we specify two separate outcome equations de- pending on the state in the previous month. ¹²

Employed in t − 1:

Y _it = a ^e (X _i , t, E _i,t−1 ) + δ _i,t,E ^e

(τ _i ) + c ^e _i + u ^e _i,t for Y _i,t−1 = 1 (4)

Not employed in t − 1:

Y _it = a ⁿ (X _i , t, N _i,t−1 ) + δ _i,t,N ⁿ

(τ _i ) + c ⁿ _i + u ⁿ _i,t for Y _i,t−1 = 0 (5)

Duration dependence enters equation (4) through E _i,t−1 , the elapsed employ- ment duration in t − 1, and equation (5) through N _i,t−1 , the elapsed nonemployment duration in t − 1. a ^e (X _i , t, E _i,t−1 ), a ⁿ (X _i , t, N _i,t−1 ) are functions describing the state dependent employment probabilities as a flexible function of observed time invari- ant characteristics X _i , month t, and elapsed durations E _i,t−1 , N _i,t−1 . c ^e _i , c ⁿ _i are state dependent permanent individual specific effects, and u ^e _i,t , u ⁿ _i,t are the idiosyncratic, period specific effects which are conditionally heteroscedastic. Our estimation ap- proach hinges critically on the assumption of additive fixed effects.

τ _i is the actual (random) time individual i first enrolls in a training program with τ _i > ¯ T for nonparticipants and ¯ T being the end of the time period analyzed.

δ ^e _i,t,E

(τ _i ), δ _i,t,N ⁿ

(τ _i ) are the individual specific, state dependent effects of treat- ment on the individual employment probabilities and represent potential treatment effects of different τ _i . ¹³ We estimate averages of the employment effects in period t, δ ^e _i,t,E

(τ ), δ _i,t,N ⁿ

(τ ), conditional on receiving treatment in some period τ , i.e.

12 In this subsection, the index i denotes any individual whereas in the remainder of the paper i applies only to treated individuals.

13 The link between actual treatment effects operating for treated individual i and potential

τ _i = τ where τ is some fixed time, and conditional on the employment status in the previous period t − 1. Furthermore, we assume that the effect of treatment occurs after treatment, i.e. δ _i,t,E ^e

(τ _i ) = 0 and δ ⁿ _i,t,N

(τ _i ) = 0 for t < τ _i . ¹⁴ The as- sumption implies the absence of deterrence effects, which is plausible since training programs are not mandatory. Next to state and duration dependence, we allow the individual potential treatment effects δ ^e _i,t,E

(τ ) and δ _i,t,N ⁿ

(τ ) (see footnote 13) to depend upon observed characteristics X _i and the individual specific effects c ^k _i . They are also allowed to vary by i, t, and τ conditional upon X _i and c ^k _i .

Regarding the selection into treatment, the evaluation approach allows treat- ment time τ _i to be affected by the observed covariates X _i , by the treatment effects δ ^e _i,t,E

(τ _i ), δ _i,t,N ⁿ

(τ _i ) , and by the individual specific effects c ^e _i , c ⁿ _i . Furthermore, we impose little functional form restrictions on a ^e (X _i , t,E _i,t−1 ) and a ⁿ (X _i , t, N _i,t−1 ).

However, we choose a parametric model to estimate the propensity score. For the id- iosyncratic error terms, we assume that u ^e _i,t , u ⁿ _i,t are conditionally mean independent of treatment in the past.

Ashenfelter’s Dip in employment (the preprogram employment dip) links treat- ment and the idiosyncratic error terms u ^e _i,t , u ⁿ _i,t shortly before treatment. Formally, the preprogram employment dip can be described by E(u ^k _i,t−s |τ _i = t) < 0 for (k = e, n) and s = 1, . . . , ad, where ad denotes the beginning of Ashenfelter’s Dip.

We assume that both anticipation effects and participation rules do not affect the idiosyncratic error term after treatment. Therefore, the preprogram effects are not linked to the outcome variable once treatment has started, i.e. u ^k _i,t−s (k = e, n) are not correlated with u ^k _i,t+l with s, l ≥ 1 and conditional on τ _i = t. ¹⁵ Note that

treatment effects is given by δ ⁿ _i,t,N

(τ i ) = P

τ δ ⁿ _i,t,N

(τ )I(τ i = τ ), where I(τ i = τ ) is a dummy variable which is equal to one iff τ i = τ .

14 This assumption is similar to the timing–of–events approach (Abbring and Van den Berg, 2003).

15 This is in contrast to HS who model earnings in the recovery process to be expected (based on

nontreatment outcomes) after the treatment being symmetric to the deterioration during Ashen-

felter’s Dip. HS show empirically that such a pattern holds based on experimental data. In our

context, state dependence in employment results in a sluggish recovery process without treatment

which in general is not symmetric around Ashenfelter’s Dip. Analyzing transition rates allows us

to take account of the sluggishness of recovery.

the preprogram employment dip as a temporary shock nevertheless would affect nontreatment outcomes through the state dependence of the employment process.

In our empirical analysis, we allow for a maximum length of time (ad months) for Ashenfelter’s Dip (see section 4.1).

4.2.2 Implementation of CDiDHR

Based on the employment model in equations (4) and (5), the following Conditional Difference–in–Differences in Hazard Rates (CDiDHR) estimator arises naturally as an extension of a CDiD estimator to a state dependent employment process with duration dependence. We simply estimate the treatment effect on the employment probability via CDiD as in equation (3) conditional on employment status in the previous month and conditional on dummy variables for duration dependence E _i,t−1 or N _i,t−1 . The estimator is calculated for the set of observations N ^l instead of all treated individuals {D = 1} where l denotes the employment status in the previous month (l = 1 if previously employed and l = 0 if previously nonemployed). N ^l is then the set of treated individuals for whom Y _{i,τ +t1−1} = Y _{i,τ +t0−1} = l, where period t1 lies after and t0 before treatment for individual i. N ₁ in equation (3) is replaced by N ^l , the number of individuals in the set N ^l . Also the weights are normalized accordingly based on this set. Similar to the previous section, we use the average individual employment rate Y _{m,τ +t0} (m = i, j) in the time period before the preprogram employment dip conditional on the employment status in the month before. Thus, we use individual average observable transition rates for alignment in the preprogram period. Only nonparticipants j for whom Y _{j,τ +t1−1} = Y _{j,τ +t0−1} = l and who fall into the same duration categories are matched, i.e. can have a non zero weight w _i,j . For l = 0 and l = 1, we estimate the reemployment probability and the probability of remaining employed, respectively.

When calculating the expression in equation (3), the set N ^l changes over the

time periods (t ₁ , t ₀ ) considered since different sets of individuals are employed or

non–employed in the previous month. For some individuals, there exists no pair

of time periods in the ’pre’ and ’post’ intervals where they are employed or not

employed. Effectively, there is a sorting process in either employment state which

respect to observed and unobserved characteristics. Our estimated treatment effect averages over the different set of individuals across time. This implies that we do not estimate the TT for all treated individuals but just the TT for those treated individuals who happen to be in the employment state of interest in the months after treatment start. This way we focus on the effects for those settings which are observed. There is no ready procedure to estimate the unconditional TT by also integrating out both observed and unobserved individual specific effects without imposing further stringent assumptions.

To properly account for selection bias in the nonparticipation outcome, CDiDHR only requires the mean difference in the idiosyncratic error terms conditional on D _i = 1 and DT _i = 0 (both also conditional on X _i ) to coincide, i.e. E(u ^k _{i,τ +t1} |D _i = 1, X _i ) − E(u ^k _{i,τ +t0} |D _i = 1, X _i ) = E(u ^k _{i,τ +t1} |DT _i = 0, X _i ) − E(u ^k _{i,τ +t0} |DT _i = 0, X _i ) for k =e,n , t1 ≥ τ , and t0 < −ad, where D _i ≡ D(τ _i = τ ) (dummy for treatment in period τ ) and DT _i ≡ D(T ≤ τ _i < T ) (dummy for treatment during observation period [T , T ]). The individual specific effects c ^l _i do not have to be conditionally mean independent of treatment status and covariates X _i . Also for CDiDHR, we require that t0 lies before −ad, i.e. before anticipation and participation rules can take effect. ¹⁶

We estimate the TT over the sample distribution of lagged employment status and elapsed (non)employment durations. The state dependent specification allows for a sluggish recovery in employment rates in the nontreatment state as a bench- mark. In light of our employment model in equations (4) and (5), our CDiDHR estimator is robust against the preprogram dip in employment provided average long–run employment differences before treatment do not change before the start of the dip (parallel pretreatment outcomes). As in the case of CDiDS, CDiDHR can be modified to account for the dependence of treatment participation and treat- ment effect on the employment dynamics in the short run before the start of the

16 If the timing of treatment τ i is independent of the person specific gains δ _i,. ^k (k = e, n) conditional

on the unobserved heterogeneity terms, then the estimated treatment effect for some τ is the

average effect of treatment on the treated for the entire treated sample in the observation period

conditional on the employment state in the previous month. However, the latter condition may

not be justifiable in our application.

treatment. Indeed, the dynamics shortly before treatment appear to be decisive for participation. We find that we need to match on the employment state in the month before treatment for those who are then nonemployed in order to stabilize the average long–run employment differences. Only this way, we obtain the neces- sary parallel average long–run preprogram outcomes which are required for CDiD (see Abadie, 2005). Note that despite matching on the short–run preprogram dy- namics, our CDiDHR estimator is not invalidated by the preprogram employment dip. The only purpose is to match nontreated individuals who have a similar risk of participating in training as the treated individuals.

4.3 Implementation Details

Following HIST and HS, we use a local linear matching in the propensity score, i.e. we run a local linear kernel regression in the dimension of the propensity score, see Pagan and Ullah (1999). ¹⁷ A kernel function with unbounded support avoids some of the problems involved with local linear kernel regression, namely, that the variance can be extremely high in areas where there is not a lot of data, see Seifert and Gasser (1996) and Fr¨olich (2004) for a critical assessment of local linear kernel regression.

We take account of the sampling variability in the estimated propensity score by applying a bootstrap method to construct the standard errors of the estimated treatment effects. To account for autocorrelation over time, we use the entire time path for each individual as the block resampling unit. All the bootstrap results reported in this paper are based on 200 resamples.

For the local linear kernel regression in the sample of nonparticipants, we use the Gaussian kernel, see Pagan and Ullah (1999). Standard bandwidth choices (e.g. rules

17 Local linear matching has a number of theoretical advantages compared to the widely used

nearest neighbor matching. The asymptotic properties of kernel based methods are straightforward

to analyze and it has been shown that bootstrapping provides a consistent estimator of the sampling

variability of the estimator in (1) even if matching is based on closeness in the estimated propensity

score, see HIST or Ichimura and Linton (2001) for an asymptotic analysis of kernel based treatment

estimators. Abadie and Imbens (2006) show that the bootstrap is in general not valid for nearest

neighbor matching due its extreme nonsmoothness.

of thumb) for pointwise estimation are not advisable here because the estimation of the treatment effect is based on the average expected nonparticipation outcome for the group of participants, possibly after conditioning on some information to capture the heterogeneity of treatment effects. Since averaging pointwise estimates reduces the variance, it is clear that the asymptotically optimal bandwidth should go to zero faster than an optimal bandwidth for a pointwise estimate, see Ichimura and Linton (2001) on such results for a different estimator of treatment effects. ¹⁸

To choose the bandwidths h _p and h _m , we suggest the following heuristic leave–

one–out cross–validation procedure which mimics the estimation of the average ex- pected nonparticipation outcome for each period. First, for each participant i, we identify the nearest neighbor nn(i) in the sample of nonparticipants, i.e. the non- participant whose propensity score is closest to that of i, and we also assign the start of treatment τ _i for i as the fictitious start for nn(i). Second, we choose the bandwidths h _p and h _m to minimize the sum of the period–wise squared prediction errors

T −1 X

t=0



 1 N _1,t

N X

i=1



 Y _nn(i),τ ⁰

_+t − ^X

j∈{D=0}\nn(i)

w i,j Y _j,τ ⁰

_+t









2

where the prediction of employment status for nn(i) is not based on the nearest neighbor nn(i) himself and t = 1, ..., T denotes the month (T = 36 for our data) in the calendar months after the beginning for treatment for treated individual i himself. The optimal bandwidths affecting the weights w _i,j are determined by numerical optimization. In some cases, we find a very large value for h p which means that the matching on the propensity score does not have much influence on the results. Since our method for the bandwidth choice is computationally quite expensive, it is not possible to bootstrap it. Instead, we use the bandwidth found for the sample in all resamples.

4.4 Effects on Earnings

We also attempt to estimate the TT effects of training on earnings. For earnings as outcome variable, we can only provide cross–sectional matching estimates because

18 This is also the rationale for researchers using nearest neighbor matching with just the closest

neighbor thus focusing on minimizing the bias.

earnings are only observed for the last three years of the data 1997 to 1999. Since we analyze training in the years 1990 to 1999, data availability precludes a CDiD estimator. We report an estimate of the treatment effects on earnings by matching on the long run employment history before treatment, analogous to what we do for employment effects, and then we control for the time passed since the beginning of treatment.

5 Data

Our analysis uses the Labor Market Monitor Sachsen–Anhalt ¹⁹ (Arbeitsmarktmoni- tor Sachsen–Anhalt, LMM–SA) for the years 1997, 1998, and 1999. The LMM–SA is a panel survey of the working–age population of the state (Bundesland) of Sachsen–

Anhalt with 7,100 participants in 1997, 5,800 in 1998, and 4,760 in 1999. 1999 is the last year in which the survey was conducted. Only in the three years used, ret- rospective questionnaires on the monthly employment status between 1990 and the interview date were included, covering employment, unemployment, or participation in a program of ALMP, as well as periods in the education system, inactivity, or in the military. Individuals who did not participate in the 1998 survey are recorded until at least September 1997, those who dropped out in 1999 at least until October 1998. ²⁰

19 Our data refer to the state of Sachsen–Anhalt, which experienced a slightly worse economic development after 1990 than the average of East Germany (see Eichler and Lechner, 2002). How- ever, the regional economic situation varies within this state and we control for these differences between treated and matched control observations in our matching approach. Therefore, the esti- mated effect should reflect an uncontaminated microeconomic effect that accounts for differences in the economic situation within the state. Since we focus on the employment effect as an effect of treatment–on–the–treated for a particular cohort on the East German labor market, the results are therefore likely to hold for similar cohorts in other East German areas. Further information on the data set can be found in Ketzmerik (2001).

20 Recall error is unlikely to be of particular importance for these data, see the discussion in the

Appendix.

5.1 Selection of Sample

Unfortunately, in the three survey years used the categories of the labor market status information differ. For compatibility, the data set also includes a combined monthly calendar for the three survey years. This calendar distinguishes the follow- ing categories: Education, full–time employed, part–time employed, unemployed, job creation scheme, training, retirement, pregnancy/maternity leave, not in active workforce.

Additional information on the individuals that goes beyond the monthly labor market status since 1990 can be retrieved from the cross–sectional dimension of the survey for the years 1997 to 1999. We use static individual characteristics, such as education, area of residence at the time of the interview, and year of birth.

As an additional outcome variable, next to employment, we consider monthly net income at the time of the interviews in 1997 to 1999, in case an individual is defined as employed. When nonemployed, we set this outcome variable to zero. Thus, we basically consider monthly earnings because nonlabor income is likely to be negligible in East Germany among employees.

We only consider individuals with uninterrupted information on their labor mar- ket history between January 1990 and at least September 1997 (i.e. individuals who completed the retrospective question in 1997). ²¹ The individuals are between 25 and 50 years old in January 1990 and employed before the start of the “Economic and Social Union” in June 1990. This way, only individuals are included who belonged to the active labor force of the GDR, who therefore are fully hit by the transfor- mation shock, and who are not too close to retirement. Individuals who are later on in education, on maternity leave or retired are excluded completely from the analysis. The goal is to construct a consistent data base excluding individuals who have left the labor market completely. In addition, we exclude a small number of individuals without valid information on those individual characteristics, on which we build our matching estimator. We aggregate the remaining labor market states to the five categories employment, which comprises part– and full–time employment,

21 See table 1 for the number of observations dropped from the sample for each of the reasons

described here.

unemployment, out of the labor force, training, and job creation.

Our outcome variable employment is defined as a binary outcome variable with nonemployment as comprehensive alternative including participation in ALMP.

Modeling transitions between unemployment and being out of the labor force is an impossible task. People move occasionally back and forth between the two states in the data and it is not obvious whether the individuals precisely distinguish be- tween unemployment and being out of labor force, since no formal definition of unemployment is given in the questionnaire.

The resulting sample consists of 5,165 individuals, involving both participants and nonparticipants in ALMP. Table 2 summarizes participation in ALMP based on our data. The two most important programs, Training (TR) and Job Creation Schemes (JC), were implemented on a large scale. In total, 27% of our sample participated at least once in one of the two programs. 13% (689 cases) participated at least once in JC, however, TR was by far the most important program with a rate of 20% (1,021 cases). ²² Multiple participation is quite common in East Germany.

After a first TR, a second treatment in TR or JC occurred in 326 cases, i.e. in more than 36 % of the 889 cases in a first treatment in TR. ²³ Here we focus on TR as the first treatment in ALMP. We observe 9.8% (495 cases) of our sample to participate in a first TR during the first period from 1990 to 1993 and 7.6% (394 cases) to participate during the second period from 1994 to 1999. Note, that our data do not distinguish between further training and retraining. Therefore, the estimated treatment effects represent an average of the two programs.

22 The question in the LMM–SA on training also includes privately financed training. However, calculations based on the German Socioeconomic Panel for East Germany show that a very high share of training is in fact public sector sponsored training (in 1993 more than 88%).

23 In the working paper version Bergemann, Fitzenberger and Speckesser (2005), we estimate

effects both for a first and second treatment. We evaluated sequences or increments of multiple

treatments using a specific variant of the evaluation approach suggested under section 4.