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 Germany. We propose and apply an extension of the widely used conditional differencein-differences estimator. Focusing on transition rates between nonemployment and
employment, we take into account that employment is a state and duration dependent process. Our results show that using transition rates is more informative than
using unconditional employment rates as commonly done in the literature. Moreover, 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 program.
Keywords: Evaluation of active labor market policy in East Germany, transition
rates, employment dynamics, Ashenfelter’s Dip, nonparametric matching, conditional 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 command 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 Service still spends around e 10 Billion for ALMP (Bundesanstalt für 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.
1
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 Market 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 significantly positive effects of ALMP in the medium and long-run, see Fitzenberger and
Speckesser (2007) and Lechner et al. (2008). While studies based on administrative 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 average, 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 unemployment. 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 transformation 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 demand 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).
2
We implement a semiparametric conditional difference–in–differences estimator
(CDiD) (Heckman, Ichimura, Smith and Todd, 1998). We extend the CDiD approach 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 employment 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 nonparticipants 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.
3
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.
4
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 processes which were highly overstaffed. This resulted in high employment rates and
a productivity level that fell substantially short of West European standards. Although 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. Production 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, economic 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 unemploy5
Unless indicated otherwise, the following overview is based on Akerlof, Rose, Yellen and Hesse-
nius (1991), Bundesministerium für Verkehr, Bau und Stadtentwicklung (2005), Hunt (2006), van
Hagen and Strauch (2001), and Wurzel (2001).
5
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 unemployed 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 programs 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 necessary 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 für Arbeit, 1991).
Shortly after reunification, early retirement programs and short-time work programs were heavily used in order to reduce - at least in the short run - open unemployment (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).
6
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 (Arbeitsförderungsgesetz, 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 für Arbeit, BA) was in charge of implementing these
programs in addition to being responsible for job placement and for granting unemployment 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, maintenance, 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 further 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.
7
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 (Unterhaltsgeld ). 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 recommendation 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 Germany, the 1969 legislation of Active Labor Market Policies and training programs
in particular was fairly generous. The design of these programs provided institutionally 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 participation 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 reunification 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:
8
1. Change in provision of training: Shortly after the reunification, training programs 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 program participants were not required to prove active job search and job placement 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 maintenance payments exceeding the standard unemployment benefits by 3 percentage points, while participants entering the program from means–tested
benefits continued to receive benefits at the level of 58% of previous net earnings. 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 benefits. This decline in the income maintenance payment for the most important
group of participants reduced institutional incentives of participating in training programs (see Eichler/Lechner 2001, 221).
4. Change in eligibility rules for participation: Originally, participation in a training 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 la9
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 individuals 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 credible 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 participants. 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
10
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.
11
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 counterfactual 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 training are the unemployed and employees with a high risk of unemployment. Anticipation effects arise because unemployed individuals and employees with a high risk
of losing their jobs reduce their search effort, because they know about the availability 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 summarized 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.
12
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 unemployment 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 identifying assumption that the selection bias after matching on the propensity score
is the same symmetrically around the treatment start. This approach proves useful 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 employment 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 justifiable 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 benchmark 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 circumvent potential problems with respect to Ashenfelter’s Dip. This comes at the cost
13
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 evident 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 account 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 nonem9
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.
14
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 observable 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
15
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
wN0 (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 kerP
nel. For each i, these weights sum up to one over j (
j∈{D=0}
wN0 (i, j) = 1). The
estimated TT is then
(1)
1
N1


X
i∈{D=1}



X
Yi1 −
j∈{D=0}
wN0 (i, j) Yj0  ,
with N0 the number of nonparticipants j and N1 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 N0 )
Ã
(2)
pi − pj
K(i, j) = φ
hp
!
Ã
"
mdist(i, j)
· exp −
h2m
#!
where pi , pj 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), hp , hm are the two bandwidths, and φ is the Gaussian
kernel. The weights are given by wN0 (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.
16
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 τi = τ (τi 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


N1
X
1 X
0
0
0
Y 1

−
Y
−
wi,j (Yj,τ
i,τ +t0
+t1 − Yj,τ +t0 )
N1 i=1 i,τ +t1
j
(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 . N1 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.
17
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 Yit 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 depending on the state in the previous month.12
Employed in t − 1:
(4)
e
Yit = ae (Xi , t, Ei,t−1 ) + δi,t,E
(τi ) + cei + uei,t
i,t−1
for Yi,t−1 = 1
Not employed in t − 1:
(5)
n
Yit = an (Xi , t, Ni,t−1 ) + δi,t,N
(τi ) + cni + uni,t
i,t−1
for Yi,t−1 = 0
Duration dependence enters equation (4) through Ei,t−1 , the elapsed employment duration in t − 1, and equation (5) through Ni,t−1 , the elapsed nonemployment
duration in t − 1. ae (Xi , t, Ei,t−1 ), an (Xi , t, Ni,t−1 ) are functions describing the state
dependent employment probabilities as a flexible function of observed time invariant characteristics Xi , month t, and elapsed durations Ei,t−1 , Ni,t−1 . cei , cni are state
dependent permanent individual specific effects, and uei,t , uni,t are the idiosyncratic,
period specific effects which are conditionally heteroscedastic. Our estimation approach hinges critically on the assumption of additive fixed effects.
τi is the actual (random) time individual i first enrolls in a training program
with τi > T̄ for nonparticipants and T̄ being the end of the time period analyzed.
e
n
δi,t,E
(τi ), δi,t,N
(τi ) are the individual specific, state dependent effects of treati,t−1
i,t−1
ment on the individual employment probabilities and represent potential treatment
effects of different τi .13 We estimate averages of the employment effects in period
e
n
t, δi,t,E
(τ ), δi,t,N
(τ ), conditional on receiving treatment in some period τ , i.e.
i,t−1
i,t−1
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
18
τi = 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
e
n
after treatment, i.e. δi,t,E
(τi ) = 0 and δi,t,N
(τi ) = 0 for t < τi .14 The asi,t−1
i,t−1
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
e
n
individual potential treatment effects δi,t,E
(τ ) and δi,t,N
(τ ) (see footnote 13)
i,t−1
i,t−1
to depend upon observed characteristics Xi and the individual specific effects cki .
They are also allowed to vary by i, t, and τ conditional upon Xi and cki .
Regarding the selection into treatment, the evaluation approach allows treatment time τi to be affected by the observed covariates Xi , by the treatment effects
e
n
δi,t,E
(τi ), δi,t,N
(τi ) , and by the individual specific effects cei , cni . Furthermore,
i,t−1
i,t−1
we impose little functional form restrictions on ae (Xi , t,Ei,t−1 ) and an (Xi , t, Ni,t−1 ).
However, we choose a parametric model to estimate the propensity score. For the idiosyncratic error terms, we assume that uei,t , uni,t are conditionally mean independent
of treatment in the past.
Ashenfelter’s Dip in employment (the preprogram employment dip) links treatment and the idiosyncratic error terms uei,t , uni,t shortly before treatment. Formally,
the preprogram employment dip can be described by E(uki,t−s |τi = 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. uki,t−s (k = e, n)
are not correlated with uki,t+l with s, l ≥ 1 and conditional on τi = t.15 Note that
n
treatment effects is given by δi,t,N
(τi ) =
i,t−1
P
τ
n
δi,t,N
(τ )I(τi = τ ), where I(τi = τ ) is a
i,t−1
dummy variable which is equal to one iff τi = 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 Ashenfelter’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.
19
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 Ei,t−1
or Ni,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 Yi,τ +t1−1 = Yi,τ +t0−1 = l, where
period t1 lies after and t0 before treatment for individual i. N1 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 Ym,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 Yj,τ +t1−1 = Yj,τ +t0−1 = l
and who fall into the same duration categories are matched, i.e. can have a non zero
weight wi,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 (t1 , t0 ) 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
20
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
Di = 1 and DTi = 0 (both also conditional on Xi ) to coincide, i.e. E(uki,τ +t1 |Di =
1, Xi ) − E(uki,τ +t0 |Di = 1, Xi ) = E(uki,τ +t1 |DTi = 0, Xi ) − E(uki,τ +t0 |DTi = 0, Xi )
for k =e,n , t1 ≥ τ , and t0 < −ad, where Di ≡ D(τi = τ ) (dummy for treatment
in period τ ) and DTi ≡ D(T ≤ τi < T ) (dummy for treatment during observation
period [T , T ]). The individual specific effects cli do not have to be conditionally
mean independent of treatment status and covariates Xi . 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 benchmark. 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 treatment effect on the employment dynamics in the short run before the start of the
16
k
If the timing of treatment τi is independent of the person specific gains δi,.
(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.
21
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 necessary parallel average long–run preprogram outcomes which are required for CDiD
(see Abadie, 2005). Note that despite matching on the short–run preprogram dynamics, 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 Frölich (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.
22
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 hp and hm , we suggest the following heuristic leave–
one–out cross–validation procedure which mimics the estimation of the average expected 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 nonparticipant whose propensity score is closest to that of i, and we also assign the
start of treatment τi for i as the fictitious start for nn(i). Second, we choose the
bandwidths hp and hm to minimize the sum of the period–wise squared prediction
errors


2
N1,t
X
1 X
0
Y 0


wi,j Yj,τ
nn(i),τi +t −
i +t
t=0 N1,t i=1
j∈{D=0}\nn(i)
TX
−1
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 wi,j are determined by
numerical optimization. In some cases, we find a very large value for hp 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.
23
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–Anhalt19 (Arbeitsmarktmonitor 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, retrospective 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). However, 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 estimated 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.
24
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 following 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 market 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 transformation 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.
25
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 between 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.
26
5.2
Descriptive Analysis of Participants and Non-participants
Since our analysis estimates the effects of TR participation for a period up to 36
months after the beginning of the participation, only a small number of observations
might remain in the sample for outcomes late in the 1990’s. Whereas attrition is
absent for TR programs that started in our first observation period from 1990 to
1993, because of the retrospective sampling procedure, there might be a problem
for training in the second period for 1994 to 1999. Table 3 shows for the first
period that all monthly status information until 36 months after the beginning of
the program can be retrieved from the data, both for the treated and the nontreated
individuals. Attrition matters for the second period (see table 4), i.e. participation
occurs between 1994 and 1999. There is no longer information on the labour market
status for every treated individual for 36 months after the beginning of the treatment.
The decreasing numbers result mainly from persons surveyed in the years 1997 and
1998 that were participating relatively late in the 1990’s. We lose about one third
of the treated individuals after 24 months and about 50% after 36 months. There
is considerably less attrition in the control group (based both on the evolution of
the kernel weights used for the CDiDS estimator, whose results are described below,
and the actual number of nonparticipants), see columns 3 and 4 of table 4 and the
detailed explanations at the bottom of table 3. Thus, there is still a very substantial
share of both the treated and the untreated persons available until 36 months after
beginning of the treatment. In order to keep a sufficiently large sample size, we
use the unbalanced sample for the evaluation analysis. This approach can also be
justified based on existing evidence in the literature that attrition from a survey does
not influence the results concerning the determinants of labor market transition rates
(Van den Berg et al., 1994; Van den Berg and Lindeboom, 1998).
Based on the sample selection outlined above, our descriptive analysis shows a
stark contrast in the labor market participation of participants in a first TR and
non-participants. Figure 4 shows the monthly employment status by participation
status. Conditioning on employment in June 1990, we observe only few nonparticipants to leave employment until the end of 1990. Even until two years after, there
is still an employment rate of 91.2% in June 1992 and remains relatively stable until
27
the mid 1990’s, when still more than 90% of the original cohort is in employment.
After 1995, the unemployment rate of the original cohort doubles to almost 15%,
and participation in JC increases. Employment falls steadily to 82.7% of the total population of non-participants at the end of the millennium. Ten years after
unification, the share of our sample leaving the labor force remains low with less
0.5%.24
In contrast, the participants in a first TR experience an earlier and more dramatic reduction in their employment rates. Two years after the economic and social
union, the employment share of the formerly fully employed cohort is already reduced to as low as 56.6%. Since then, the participants showed relatively stable
employment rates, reaching still 53.3% at the end of 1999. The massive decline in
employment not only resulted in participation in TR, but also in higher participation in JC and higher unemployment. With 16%, open unemployment was already
three times the share as for non-participants in December 1992 when the public
programs peaked with a participation of 31.8% in either TR or JC. Since then, the
participation in programs declined to 15%. Simultaneously, the unemployment rate
among participants increased to more than 30%. As for the non-participants, there
is not much drop out, eventually reaching 1% at the end of 1999.
A closer look into the dynamics of transitions in and out of employment reveals
that the dynamics were completely different for participants and non-participants
(see figures 5-6). In 1991, 45% of the first cohort of TR participants left employment
for at least one month. Since then, exits to nonemployment declined to around 6%.
On the other hand entries into employment reached a maximum of 19% in 1993
and declined thereafter, being, however, on average by 2 percentage points higher
than exits from employment. Non–participants show a very different pattern. Exit
rates from employment for the first cohort of non–participants fluctuates around 7%
points, whereas entry rates to employment are around 2 percentage points lower.
With respect to the second training period, the exits from employment for the
24
Note that a small fraction of the non-participants also shows participation in public sector
sponsored further training. These are participants in a training program after an earlier participation in a public job creation program and thus are not subject to our evaluation of training as
the first program.
28
participants increased until 1993 and remained with about 21% on a relatively high
level until 1997. Entries into employment fluctuated until 1994 around 3% and
increased thereafter to 19% in 1998, dominating exits from employment for the
first time. The second cohort of non–participants display exit rates from employment of around 6% (with the exception of 1991), being mainly one percentage point
lower than entry rates. These differences between participants and non–participants
suggest that an analysis that only controls for the high static differences in nonemployment would be insufficient. Therefore, our CDiDHR estimator introduced in
section 4 controls for the differences in the underlying dynamics of participants and
nonparticipants.
6
6.1
Empirical Analysis
Propensity Score and Matched Samples
The goal is to estimate the effect for participation in training as the first program.
The treatment probability (propensity score) is estimated by a parametric probit
model. Since the data do not provide time–varying information (except for the
labor market status), the regressors are the static observable characteristics education, occupational degree, gender, age, residence (at the time of the survey), and
interactions of gender and education or occupational degree. We estimate two different probit models one for participating in a first TR during the time 1990 to
1993 and a second for participating in a first TR during the time 1994 to 1999.
The group of “nonparticipants” represents the entire sample of individuals who are
not participating in a first treatment program in the time period consider but who
might be a participant in another program or in another time period. The results
of the probit estimate for the propensity score are reported in table 5 and 6. In
addition to the propensity score we also match either on the labor force dynamics
in the long–run pre–program time period or, in another version of our estimators,
on the employment status in the month before treatment starts for those who are
non–employed in this month. We only present the evaluation results jointly for men
and women. In our case separate estimations of the program effects did not show
29
significant differences by gender.25 Using a bootstrap estimator for the covariance
matrix of the estimated treatment effects, we capture the estimation error in the
propensity score.
The post-program evaluation period starts with the beginning of the participation in training. This approach views treatment as one realization of the nonemployment state with the treated searching for a job. Since the participant might
be enrolled in training for a duration of several months up to two years, the effects
after program beginning include a lock–in effect caused by the program itself, i.e.
the time spent in the program is likely to cause an increase of the nonemployment
probability for the treatment group in the early months of our outcome period. The
start of the evaluation period depends upon the outcome variables considered. For
employment rates and reemployment probabilities, the evaluation period starts one
month after the first month of the treatment. For probabilities of remaining employed, the evaluation period starts one month later than for the other two outcome
variables, since we first have to observe employed former participants. We choose
the length of the evaluation period to be 36 months (as far as being observed in the
data set – otherwise set to missing). With respect to earnings we can not construct
such a stringent evaluation period, as we only have earnings information for the
time period from 1997 to 1999. However, when estimating earnings effects, we take
the elapsed time period since start of training into consideration. For the alignment
of the CDiD estimators in the preprogram period, we start 18 months before the
beginning of the treatment (excluding Ashenfelter’s Dip).
Based on the estimated propensity score and the preprogram employment history, we construct matched samples of participants and comparable “nonparticipants”. Alignment occurs in the same calendar month, i.e. we match individuals in
the same calendar month in order to eliminate common time effects. The characteristics and outcomes of matched nonparticipants are the fitted values obtained by
the local linear kernel regression of characteristics and outcomes, respectively, in the
sample of nonparticipants as a whole. Note that the results of our cross validation
procedure for the bandwidth choice involve a bandwidth hp for the propensity score
25
The results of these estimations are available upon request.
30
growing to infinity in all settings for participation in the first time period 1990 to
1993. In contrast, we obtain a finite hp for the second time period 1994 to 1999.
When matching on the employment history, we obtained a finite bandwidth hm in all
cases. Thus, for the first time period, it turns out that it is not necessary to match
upon the propensity score – and therefore not on the observable time–invariant
covariates. This is important to keep in mind.
Table 7 and 8 provide evidence on the balancing properties in the matched
samples when taking account of state and duration dependence. The first column
shows the average characteristics in the whole sample. The remaining columns show
the average characteristics conditional upon employment state in the previous month
during the time period under consideration. For example, when calculating the
average characteristics for the previously nonemployed, the individual contribution
to the mean characteristics is weighted by the number of months the individual’s
state was nonemployment during the time period under consideration.
Table 7 and 8 show that participants are younger than the nonparticipants.
Higher skilled individuals are more likely to participate in the training period 1990
to 1993 than lower skilled. Similarly women are likely to receive training than men
in this time period. There are no clear pattern with respect to skills and gender for
training in the time from 1994 to 1999. The matching process balances reasonably
well the characteristics of the participants and the matched nonparticipants conditional on state and duration dependence. The balancing works especially well with
respect to the short run employment dynamics before training in the second period.
For example the employment probability for those nonparticipants who were previously nonemployed is 16%, whereas matching reduces the employment probability
of to 3%. This is very close to the employment probability of 2% of the previously
nonemployed participants.
Balancing also works well with respect to age for the second training period and
conditional on being previously nonemployed. Also, the regions seem fairly well
balanced. However, the category skilled worker does not seem so well balanced as
well as the employment probability in the month before (potential) participation
during 1990 to 1993 for those who are previously nonemployed.
31
Furthermore, table 7 and 8 sheds some light on the differences in characteristics
across employment states in the previous month. Male participants are more likely
to belong to the group of previously employed participants than women. The skill
distribution or participants in TR in 1990 to 1993 is quite different depending on
whether they are previously employed or nonemployed. Previously employed participants have on average a higher education. Furthermore, previously employed
participants in TR in 1994 to 1999 are younger than previously nonemployed.
We conclude that our matching approach balances participants and nonparticipants fairly well. This holds even for the first period where the results of our
cross–validation procedure implies that matching of the time–invariant covariates is
not necessary.
6.2
Specification of Outcome Equation
In the matched samples, the CDiDS estimators are based on a flexible linear model
for the employment dummy as outcome variable. For CDiDHR, the model is estimated separately depending on the employment state in the month before, thus
modeling transition rates. The state of nonemployment includes the participation
in ALMP programs so that previous and subsequent participation in a program are
both accounted for as nonemployment. We estimate an average employment effect
of a program relative to all possible nonemployment states for the treated individuals thus estimating TT (with CDiDHR conditioned on the employment status in
the previous month).
We assume that participant i starts treatment in period τi and, in the following,
we will omit the index i for ease of notation. We consider the employment outcome Y
during the evaluation period t1 = 1, . . . , 36. The definition of t1 depends on the success criterion. For the unconditional employment probability or the reemployment
probability being the outcome variable, the evaluation starts with the beginning of
the program, t1 is measured relative to τ , e.g. t1 = 1 corresponds to month τ + 1
and t1 = −1 corresponds to τ − 1. For the probability of remaining employed, t1 is
measured relative to τ + 1 during the evaluation period. The following estimators
are applied separately for the two training periods 1990 to 1993 and 1994 to 1999.
32
The matching estimator, which matches on the long–run preprogram employment history, is implemented in the following way:
1
Yi,τ
+t1 −
(6)
X
0
wi,j Yj,τ
+t1 =
36
X
δs I(t1 = s) + νi,τ +t1
s=1
j
where I(.) denotes the indicator function and νi,τ +t1 is the error term. For the first
time period, we also add dummies indicating the exact start year of the training as
additional regressor in equation (i.e. we let the treatment effect vary by τ ), when
the employment rate is the outcome variable. For earnings as outcome variable, we
can only implement the matching estimator as in equation (6) just accounting for
the years s (instead of months) since the start of the treatment.
For CDiDS (sample of all participants) and CDiDHR (separately for the two
employment states in the previous month), we estimate the following three steps
(only for employment as outcome variable):
1. We calculate the average long–run preprogram difference between participant
i (treatment starts in τ ) and comparable nonparticipants as
âi,τ =
1
18 − ad(τ )
−ad(τ )−1
X
0
(Yi,τ
+t0 −
t0=−18
X
0
wi,j Yj,τ
+t0 ) .
j
2. Then, âi,τ is subtracted from the difference during the evaluation period resulting in the following model to estimate the treatment effects
(7)
1
Yi,τ
+t1 −
X
0
wi,j Yj,τ
+t1 − âi,τ =
36
X
δs I(t1 = s) + νi,τ +t1
s=1
j
Analogous to the matching estimator, we add dummies indicating the exact
start year of the training as additional regressor in equation (7) for the first
training period.
3. We also report the averages over the long–run preprogram difference âi,τ separately for different training periods to illustrate how the average long–run
preprogram differences (≡ residual selection effect due to permanent individual specific effects) between participants and nonparticipants after matching
depend upon the timing of the program.
33
We define:
ad(τ )
month before the beginning of the program when Ashenfelter’s Dip starts depending upon τ ,
δs
coefficients modeling the TT effect relative to the time since
treatment started (s), and
wi,j
weights implementing local linear kernel regression on the
estimated propensity score and, depending on the type of
estimator, depending on the short–run or long–run preprogram employment history (see section 4).
All three estimators take account of the possibility that the effect of the program
depend upon the time since treatment (t1 > 0) and the beginning of the program
τ . On the one hand, we estimate the effect δs separately for each month s since
treatment. On the other hand, we allow the effect to to depend in a flexible way upon
τ , by separately estimating the effects for the two training periods and including
yearly dummies for effect estimates for training in the first time period.
The length of Ashenfelter’s Dip, ad(τ ), (the preprogram dip in employment) is
allowed to depend upon the time when the program starts. During the period shortly
after unification, it is likely that the dip is fairly short because program participation
could not have been anticipated long before and participation rules were not applied
in a strict way. This changed with the occurrence of high unemployment in the mid
90’s. A visual inspection of the average employment differences between treated and
matched controls before and after the program as a function of the time when the
program starts indicates that the dip lasted at least one to two months in 90/91
and increases over time to at least six months for training. Before November 90, we
set ad(τ ) = −1. Between November 1990 and July 1994, ad(τ ) increases linearly in
absolute value from 2 months to 6 months, where ad(τ ) is rounded to the nearest
integer. After July 1994, ad(τ ) remains constant. In order to avoid a potential
’Fallacy of alignment’, we are conservative and take Ashenfelter’s Dip as fairly long.
Our subsequent results imply that our approach to account for Ashenfelter’s Dip
does not work in a satisfactory way for the matching estimator and the CDiDS
estimator of employment effects. In contrast, as we argue in section 4, the CDiDHR
estimates seem more credible in light of Ashenfelter’s Dip.
34
6.3
Employment Differences in Matched Samples
Next, we discuss the employment differences in the matched samples for the two
different CDiD estimators in order to investigate whether the long–run preprogram
differences are fairly stable. The results for the time of Ashenfelter’s Dip are left
out because this is excluded for CDiD. Also estimates that are based on less than
20 observations are explicitly discarded (this applies to the lower panel in figure 9).
Figure 7 shows the average differences in employment rates for the matched
samples that build the basis for CDiDS, separately for the two different training
periods. Time relative to the start of TR is depicted at the horizontal axis. Right
after the beginning of treatment, employment rates of the participants are between
45 and 25 percentage points (ppoints) lower than for comparable nonparticipants.
There is a noticeable recovery for the participants afterwards – basically the time
path reflects the changes for participants since employment rates for nonparticipants
change fairly little in comparison – but the difference comes nowhere close to zero
except at the end of the evaluation period for TR after 1993. For the first period
1990 to 1993, the long–run preprogram differences are slightly below 10 ppoints and
fairly stable. For the second period after 1993, they decline considerably from 40
ppoints at month -18 to 20 ppoints at month -7. Thus, for the second period, we do
not find parallel long–run preprogram differences which would be a prerequisite for
the CDiDS estimator. This suggests that CDiDS estimates for the second period
are not valid. It is evident that the CDiDS estimates will imply strong negative
employment effects (as we will see in the following). The continuous decline before
the program in the first period and the recovery process after the program suggest
that employment rates do not adjust instantaneously, suggesting that employment
dynamics play an important role.
In contrast to the employment rates for the second period, the differences in
the transition rates in figures 8 and 9 do not display a trend for the long–run
preprogram differences (excluding the period of Ashenfelter’s Dip). The differences
in the matched samples for both outcomes, the reemployment probability and the
probability of remaining employed, fluctuates around a stable average preprogram
difference, indicating that our CDiDHR approach with alignment on an average pre35
program difference is valid. Furthermore, these long–run preprogram differences in
transition rates are very small in comparison to the differences in employment levels.
6.4
Estimated Treatment Effects
First, we discuss the employment and earnings effects estimated by the matching
estimator. We then proceed to the CDiD estimates where the outcome variable
consists of either the employment rate (CDiDS) or the transition rates (CDiDHR).
We mainly rely on graphical illustrations and we report only point estimates representing at least 20 observations. Further detailed results are available upon request.
6.4.1
Matching Estimator for Employment and Earnings
Figure 10 depicts the estimated employment effects based on the matching estimator. This estimator matches on the long–run preprogram employment history. The
graphs show a thick line representing the estimated effects on the employment probability. The surrounding dotted lines around this line represent the 95%–confidence
interval that is based on bootstrap covariance estimates.26
In both the early as well as the later 1990’s, the employment effects of training prove significantly negative. However, the negative employment effects became
weaker over time, whereby the recovery is stronger for training starting in the first
period. While in both periods the employment effects are about -70 ppoints in the
first months after training started, the effect is less negative at the end of the first
period (-18 ppoint) than at the end of the second period (-35 ppoint). All this would
imply that training results in a considerable reduction in employment rates, which
is a common result found in the literature using survey data when matching is based
on observable characteristics (see the survey in Speckesser 2004, chapter 1).
Table 9 reports the estimated earnings effects pooled for 1997 to 1999 by the
time since the beginning of the treatment based on the matching estimator. Again,
we find also negative point estimates up to eight years after the beginning of the
26
When comparing the bootstrap standard errors to conventional heteroscedasticity consistent
standard errors, we find that bootstrap standard errors are higher. This is also the case for the
CDiDS and CDiDHR estimates.
36
treatment which are significant in most years. The negative effects are reduced
over time, but we can not say whether this is due to a recovery process or whether
the effects differ by the time of the treatment. Unfortunately our data set does
not allow us to distinguish the two. The results based on the matching estimator
suggest negative earnings effects which is in line with the estimated employment
effects. However, the estimates are subject to the same criticism as the matching
estimator for employment because both ignore the dynamics in employment and
earnings.
6.4.2
CDiDS Results for Employment
Figure 11 displays the CDiDS employment effects. This estimator is able to take
account of selection on the basis of unobserved characteristics (see section 4.1). The
labor market dynamics are recognized by matching on the nonemployment status
in the month before training starts. Figure 11 depicts next to the treatment effect
also α, the average long–run preprogram differences. As could be expected from the
discussion on the employment differences in the matched sample for CDiDS, α turns
out to be positive and the effect estimates negative. If compared to the estimates
of the matching approach, the CDiDS effects are similar in two aspect: they are
always significantly negative and display a similar recovery process. They differ,
however, slightly in the strength of the negative effect. The CDiDS estimates are
not as negative as the results received by matching. However, the qualitative nature
of results is the same.
6.4.3
CDiDHR Results for Transition Rates
The CDiDHR estimates explicitly take into account the state dependence and duration dependence in the employment process. The outcome variable used is either
the probability of exiting nonemployment for the previously nonemployed or the
probability of remaining employed for the previously employed.
Figure 12 illustrate the estimated TT for the reemployment probability. We
show employment effects separately for three different time periods in order to give
additional insides into possible changes of treatment effect. We distinguish programs
37
that start 1) between 1990 and 1991, 2) in 1993, and 3) after 1993. For 1990 and
1991, we find positive employment effects during the evaluation period, which are
mostly significant. For example, one year after the program start the participants
have a 5 ppoints higher reemployment probability than they would have had, had
they not participated. These positive effects of the participation in training vanish
for programs starting after 1993. In the second training period after 1993, the effect
sometimes takes negative values, which are significant shortly after the program
started. This is not too surprising because one would expect a reduced search
effort when the program has just started (lock–in effect). The long–run preprogram
difference is significantly negative shortly after reunification (-5 ppoints), becomes
less negative over time, and is effectively zero after 1993. This is in contrast to the
CDiDS results where the long–run preprogram differences increase from the first to
the second period.
Figure 13 provides results for the probability of remaining employed where the
evaluation period starts two months after the beginning of the program. The estimated effect is close to zero for programs that start between 1990 and 1991. However, for 1994 to 1999, the effect becomes significantly positive in some cases. For
example, one year after the program started the probability of remaining employed
increases by approximately 6 ppoints. Shortly after reunification, the long–run preprogram difference is slightly negative and significant. It becomes more negative in
later periods (-7 ppoints for programs that started in December 1996).
The CDiDHR estimates differ strongly from the results for the matching estimator and the CDiDS estimator. The latter ignore the state dependence and the
duration dependence of employment and therefore, they do not capture the fact that
even without any treatment effect a sluggish employment recovery would have to
be expected after the start of training. There is also evidence that the selectivity of
the treated individuals regarding permanent differences across individuals differs by
employment state. Also this aspect can not be captured by the matching estimator
and by the CDiDS estimator. Thus, we conclude that the CDiDHR results are our
preferred estimates. Furthermore, these consideration also cast some doubts on the
validity of the estimate of the earnings effects of training.
38
Why do the CDiDHR results differ between the two transition rates? This could
be driven by changes in the content of the training programs over time. Shortly
after unification a large part of training consisted of short courses mainly aiming at increasing the participant’s placement potential, as described in section 3.2.
This could be an explanation for the positive effect on the reemployment probability. However, later on, the composition of training courses changed towards longer
courses intended to provide substantive skills. These additional skills could improve
the quality of the match between participants and employers, thus increasing the
employment stability, once a participant finds a job. However, these additional skills
do not seem to help in finding a job at a faster rate.
Also, changes in the search behavior of East Germans due to a better understanding of the labor market and the benefit system in unified Germany might play
a role in the differences. Shortly after unification, unemployed East Germans, not
being used to a labor market in a market economy, probably tended to accept new
jobs quickly with little regard to the quality of the job (f.e. job stability). As a
result, a positive effect of training programs might show up in an increase in their
reemployment probability rather than in an increase of the probability of remaining
employed. Later on, individuals searching for a job perhaps became more aware of
the importance of finding a ‘good’ job, which is not only important for their job
stability, but also for the level of potential future unemployment benefits, which
depend on the earnings in the last job. In addition, the entitlement for transfer
payments is prolonged by taking part in a training program for some time after the
program, lowering the opportunity costs of job search for participants compared to
other unemployed individuals. Thus, participants tended to search longer to find
a ‘better’ job match resulting in a positive effect on the probability of remaining
employed.
Another feature of the results which should be explained are the changes in the
long–run preprogram differences. The CDiDHR estimator matches participants and
nonparticipants month by month conditional on having the same employment status
in the previous month. Shortly after unification the labor market was quite turbulent. Everybody faced a high unemployment risk , resulting in a relatively small
39
long–run preprogram difference in the probability of remaining employed. However,
some individuals quickly found another job and did not participate in a training
program, leading to a large long–run preprogram difference in the reemployment
probability at the begin of the 90’s. Later on, unemployment became more persistent. The difference in transitions out of nonemployment between participants and
nonparticipants became less pronounced.27 The change in the long–run preprogram
differences in the probability of remaining employed could reflect the stricter targeting of labor market policy on individuals with previous unemployment experience.
Our CDiDHR results are mostly in line with the results in Fitzenberger and Prey
(2000) for East Germany in the early 1990’s. The latter study analyzes the effects
of training on state dependent employment rates based on a completely parametric
model. Recent studies for East Germany using administrative data (Fitzenberger
and Speckesser, 2007; Lechner et al., 2008) use matching estimators for the effects
of training on employment rates after treatment had started. These studies do not
distinguish state dependent transition rates. They estimate employment effects of
training for an inflow sample into unemployment in 1993 and 1994 conditional on
having been unemployed for a certain time. These analyses capture the employment
dynamics before treatment start in a careful way but the studies do not address
the issue of Ashenfelter’s dip explicitly. Both studies find a negative lock–in effect,
which also involves the recovery period to be expected, and mostly positive long–run
employment effects afterwards. The latter are consistent with our positive effects
on the probability of remaining employed. Focussing on transition rates allows
decomposing the effect on employment directly and seems appropriate in light of
the strong labor market dynamics in East Germany, especially in the early 1990’s.
Both studies do not provide special treatment for the case that program participants
move directly from employment to training and, due to data limitations, they do
not analyze training programs starting before 1993.
27
Note that this explanation of the changes in the long–run preprogram difference does not
violate the assumption of permanent fixed effects since participants change over time.
40
7
Conclusions
This paper investigates the employment effects of first participation in Public
Sponsored Training in East Germany after the German reunification. Our study
makes methodological progress, particularly regarding modeling the dynamic employment process in the context of program evaluation. Modeling employment as
a state–dependent outcome variable, we develop a new semiparametric conditional
difference–in–differences estimator for the treatment effect. We use the transition
rates between employment and nonemployment as outcome variables. We account
for Ashenfelter’s Dip caused by anticipation effects and institutional program participation rules.
To start with, we find negative effects of training on unconditional employment
rates. However, taking account of state dependency in employment, training shows
zero or positive effects. Concerning training programs which took place shortly after
reunification, we find positive program effects on the reemployment probability. For
programs starting in the mid 1990s, we find some positive program effects on the
probability of remaining employed. Our results indicate that modeling transition
rates is more appropriate and more informative than using unconditional employment rates in such a turbulent economic environment as in East Germany shortly
after reunification. Using only employment rates as an outcome might result in misleading conclusions concerning the effectiveness of ALMP programs. We also find
some differences in treatment effects on the probability of remaining employed and
on the reemployment probability depending upon the time period under investigation, probably as a result of institutional changes during the 1990s.
Overall, our results are more positive than previous results in the literature and
it is unlikely that training on average reduces the future employment chances of
participants.
Unfortunately, we can not assess to what extent general equilibrium effects influence our results. Our partial estimates represent average treatment effects for a
randomly selected individual in the treatment group holding treatment status of all
others constant. General equilibrium effects (or macro effects) may arise because
programs have indirect effects on both participants and nonparticipants (Calmfors,
41
1994). Participation in training programs was very different in the two time periods
considered, possibly resulting in diminishing returns in program effects after a time
of high participation. The differences in targeting over time changed the group of
nonparticipants most affected via substitution effects. In addition to having access
to cost data, which we do not have, the knowledge of equilibrium effects is necessary to investigate whether training programs are cost effective (efficient). Albrecht
et al. (2008) find for a large adult education program in Sweden that equilibrium
effect work in favor of the participants, i.e. the fraction of vacancies tailored toward
the medium–skilled workers increased almost one–to–one. In contrast, results for
make–work–pay programs in Canada are much less favorable (Lise et al., 2005).
Clearly, in a case as ours, where training programs were implemented at a large
scale, additional research on general equilibrium effects would be very rewarding,
especially regarding policy advice. However, typically the investigation of general
equilibrium effects requires the use of structural models which is a challenging task
because of the rapidly changing economic environment in East Germany. This important task is left for future research.
42
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46
Appendix
Table 1: Sample Selection
Selection Criteria
Resulting Number
of Observations
Fully observed labor market history and year of birth
10,715
Aged between 25 and 50 years in January 1990
6,088
Employed in June 1990
5,529
Not in Education after June 1990
5,480
Not in Maternity Leave after June 1990
5,334
Not retired after June 1990
5,224
Final sample: with valid information on relevant covariates
5,165
Table 2: Program Participation in the LMM–SA during 1990 and 1999a
One Program
At least once
As first program
As first program
Job Creation Scheme Training
13.3 (689)
19.8 (1,021)
9.4 (484)
17.2 (889)
Training in 1990-1993 Training in 1994-1999
9.8 (495)
7.6 (394)
a The
numbers represent the participation rates and in brackets the absolute number of
observation.
47
Table 3: Attrition of participation group and naı̈ve control group Period 1990-93
Time
relative
to beginning of
treatment
1
2
3
4
5
6
7
8
9
10
11
12
13
14
15
16
17
18
19
20
21
22
23
24
25
26
27
28
29
30
31
32
33
34
35
36
Number of par- % participants Average % of
ticipants
relative to t1=1 kernel
weight
relative to t1=1a
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
482
100%
100%
Average % size
of control relative to t1=1b
100%
100%
100%
100%
100%
100%
100%
100%
100%
100%
100%
100%
100%
100%
100%
100%
100%
100%
100%
100%
100%
100%
100%
100%
100%
100%
100%
100%
100%
100%
100%
100%
100%
100%
100%
100%
a: This column describes the share of the sum of the kernel weights for matching which are
available after the beginning of treatment relative to the total sum of kernel weights available at
t1 = 1 (≡the beginning). This sum of kernel weights for CDiDS across all nonparticipants j is
P P
calculated separately for all treated individuals i as i j∈{D6=1} Kij (t1) · Ij (t1) at time t1 since
the beginning of treatment, where Ij (t) is a dummy variable for individual j being still observed
in the data at t1.
b: This column describes the attrition in the actual number of nonparticipants to match with.
48
Table 4: Attrition of participation group and naı̈ve control group Period 1994-99
Time
relative
to beginning of
treatment
1
2
3
4
5
6
7
8
9
10
11
12
13
14
15
16
17
18
19
20
21
22
23
24
25
26
27
28
29
30
31
32
33
34
35
36
Number of par- % participants Average % of
ticipants
relative to t1=1 kernel
weight
relative to t1=1a
385
100%
100%
381
99%
100%
376
98%
99%
370
96%
99%
368
96%
99%
368
96%
98%
363
94%
97%
359
93%
97%
351
91%
95%
350
91%
95%
346
90%
94%
336
87%
93%
332
86%
92%
325
84%
91%
322
84%
91%
319
83%
91%
314
82%
90%
310
81%
89%
305
79%
88%
297
77%
88%
290
75%
87%
282
73%
87%
273
71%
87%
266
69%
86%
264
69%
84%
255
66%
84%
248
64%
84%
246
64%
84%
242
63%
83%
238
62%
83%
231
60%
81%
223
58%
80%
210
55%
80%
202
52%
79%
197
51%
78%
188
49%
78%
a, b: see table 3.
49
Average % size
of control relative to t1=1b
100%
100%
99%
99%
99%
98%
97%
96%
95%
94%
94%
93%
91%
90%
90%
90%
90%
89%
88%
87%
86%
86%
86%
86%
84%
83%
84%
83%
82%
82%
81%
80%
79%
79%
78%
77%
Table 5: Propensity Score Estimation
Variable
Participation in Training as a
First Program in ALMP during 1990-1993
Coef. (s.e.)
mean num.
derivative
Constant
-1.302 ( 0.197 )
Age in 1990: Age 25–34 is omitted category
Age 35–44
-0.151 ( 0.055 )
-0.027
Age 45–50
-0.396 ( 0.071 )
-0.061
Labor Market Region: Dessau is missing category
Halberstadt
-0.228 ( 0.106 )
-0.041
Halle
-0.346 ( 0.090 )
-0.058
Magdeburg
-0.219 ( 0.083 )
-0.039
Merseburg
-0.172 ( 0.094 )
-0.032
Sangerhausen
-0.107 ( 0.101 )
-0.021
Stendal
-0.187 ( 0.109 )
-0.034
Wittenberg
-0.135 ( 0.125 )
-0.026
Professional education (all): Unskilled, semi–skilled or other skills
are missing category
Skilled Worker
0.028 ( 0.194 )
0.004
Craftsman
-0.164 ( 0.226 )
-0.021
Technical college
0.234 ( 0.214 )
0.039
University education 0.217 ( 0.196 )
0.035
Professional education (women)
Skilled worker
0.559 ( 0.076 )
0.093
Craftswoman
0.998 ( 0.215 )
0.174
Technical college
0.169 ( 0.125 )
0.028
University education 0.270 ( 0.094 )
0.047
50
Table 6: Propensity Score Estimation
Variable
Participation in Training as a
First Program in ALMP during 1994-1999
Coef. (s.e.)
mean num.
derivative
Constant
-1.622 ( 0.198 )
Age in 1990: Age 25–34 is omitted category
Age 35–44
0.012 ( 0.059 )
0.002
Age 45–50
-0.095 ( 0.071 )
-0.013
Labor Market Region: Dessau is missing category
Halberstadt
0.083 ( 0.114 )
0.012
Halle
0.107 ( 0.097 )
0.015
Magdeburg
0.046 ( 0.094 )
0.006
Merseburg
0.022 ( 0.106 )
0.003
Sangerhausen
0.150 ( 0.110 )
0.022
Stendal
-0.163 ( 0.130 )
-0.019
Wittenberg
-0.102 ( 0.147 )
-0.013
Professional education (all): Unskilled, semi–skilled or other skills
are missing category
Skilled Worker
0.121 ( 0.189 )
0.016
Craftsman
0.088 ( 0.210 )
0.011
Technical college
0.209 ( 0.210 )
0.029
University education 0.115 ( 0.193 )
0.015
Professional education (women)
Skilled worker
0.237 ( 0.076 )
0.140
Craftswoman
0.326 ( 0.224 )
0.053
Technical college
-0.137 ( 0.129 )
-0.019
University education -0.098 ( 0.108 )
-0.012
51
Table 7: Balancing Properties of Matching for CDiDHR with
respect to Participation in Training during 1990-1993
Variable
Age 25–34
Age 35–44
Age 45–50
Dessau
Halberstadt
Halle
Magdeburg
Merseburg
Sangerhausen
Stendal
Wittenberg
Unskilled, semi–skilled
and other skills
Skilled Worker
Craftsman
Technical college
University education
Female
Female unskilled worker
Female skilled worker
Female Craftsman
Female and technical college
Female and university education
Employment probability before
(potential) participation
Means of Variable in Subgroups
All
Nonpar– Parti– Matched Nonpar– Parti– Matched
ticipants cipants Nonpart. ticipants cipants Nonpart.
uncond.
averaged over prev–
averaged over prev–
iously nonemployed
iously employed
0.37
0.33
0.51
0.43
0.37
0.45
0.44
0.40
0.38
0.37
0.39
0.40
0.43
0.41
0.23
0.28
0.13
0.19
0.23
0.13
0.17
0.12
0.13
0.13
0.17
0.11
0.16
0.15
0.09
0.08
0.13
0.06
0.09
0.08
0.08
0.19
0.17
0.09
0.13
0.20
0.15
0.15
0.24
0.23
0.19
0.21
0.24
0.23
0.24
0.13
0.15
0.18
0.17
0.13
0.15
0.14
0.10
0.10
0.10
0.13
0.09
0.10
0.11
0.08
0.09
0.10
0.09
0.08
0.08
0.08
0.05
0.05
0.08
0.05
0.05
0.04
0.06
0.02
0.43
0.08
0.19
0.27
0.48
0.01
0.21
0.01
0.13
0.11
0.09
0.53
0.08
0.15
0.16
0.60
0.06
0.35
0.02
0.10
0.07
0.03
0.47
0.05
0.27
0.17
0.75
0.02
0.39
0.03
0.20
0.11
0.05
0.60
0.05
0.16
0.16
0.74
0.03
0.50
0.03
0.11
0.10
0.02
0.44
0.08
0.19
0.27
0.44
0.01
0.19
0.01
0.12
0.10
0.01
0.43
0.05
0.19
0.32
0.56
0.00
0.25
0.02
0.14
0.14
0.02
0.48
0.06
0.19
0.26
0.59
0.01
0.32
0.02
0.13
0.13
n.a.
0.32
0.03
0.31
0.92
0.52
0.65
52
Table 8: Balancing Properties of Matching for CDiDHR with
respect to Participation in Training during 1994-1999
Variable
Age 25–34
Age 35–44
Age 45–50
Dessau
Halberstadt
Halle
Magdeburg
Merseburg
Sangerhausen
Stendal
Wittenberg
Unskilled, semi–skilled
and other education
Skilled Worker
Craftsman
Technical College
University Education
Female
Female unskilled worker
Female skilled worker
Female Craftsman
Female and technical college
Female and university education
Employment probability before
(potential) participation
Means of Variable in Subgroups
All
Nonpar– Parti– Matched Nonpar– Parti– Matched
ticipants cipants Nonpart. ticipants cipants Nonpart.
averaged over prev–
averaged over prev–
uncond.
iously nonemployed
iously employed
0.37
0.29
0.29
0.30
0.41
0.50
0.40
0.40
0.38
0.42
0.40
0.39
0.40
0.39
0.23
0.33
0.29
0.30
0.21
0.10
0.22
0.12
0.13
0.13
0.13
0.12
0.10
0.12
0.09
0.07
0.12
0.07
0.09
0.08
0.08
0.19
0.15
0.20
0.16
0.20
0.17
0.19
0.24
0.23
0.21
0.22
0.24
0.28
0.25
0.13
0.16
0.13
0.16
0.14
0.12
0.14
0.10
0.11
0.11
0.13
0.11
0.15
0.11
0.08
0.09
0.08
0.08
0.07
0.04
0.07
0.05
0.06
0.03
0.05
0.04
0.06
0.04
0.02
0.43
0.08
0.19
0.27
0.48
0.01
0.21
0.01
0.13
0.11
0.06
0.50
0.06
0.18
0.19
0.60
0.04
0.33
0.02
0.12
0.09
0.02
0.58
0.06
0.12
0.22
0.58
0.01
0.39
0.03
0.07
0.07
0.06
0.58
0.06
0.15
0.16
0.68
0.04
0.45
0.03
0.10
0.08
0.02
0.45
0.08
0.19
0.27
0.44
0.01
0.19
0.01
0.12
0.10
0.01
0.46
0.08
0.21
0.23
0.42
0.00
0.21
0.01
0.13
0.08
0.03
0.51
0.08
0.17
0.22
0.49
0.02
0.27
0.02
0.10
0.09
n.a.
0.16
0.02
0.03
0.67
0.30
0.29
53
Table 9: Earnings Effects of TR 1997 to 1999 by Time since Beginning of Treatment
(Matching on Long–run Preprogram Employment History) – Monthly Net Earnings
as Outcome Variable
Years since beginning of
treatment (t1)
0 < t1 ≤ 1
1 < t1 ≤ 2
2 < t1 ≤ 3
3 < t1 ≤ 4
4 < t1 ≤ 5
5 < t1 ≤ 6
6 < t1 ≤ 7
7 < t1 ≤ 8
8 < t1 ≤ 9
TT Estimatea (Standard Error) No. of casesb
-831
-784
-438
-139
-526
-243
-332
-230
379
(174)
(167)
(153)
(150)
(92)
(108)
(128)
(127)
(366)
49
52
56
62
123
136
129
91
14
The estimates are pooled across the years 1997 to 1999. Earnings are set to zero when nonemployed.
a: Average earnings differences in matched sample by year since beginning of treatment.
b: Number of cases in matched sample.
Figure 1: Unemployment and Labor Market Policies in East Germany, in 1000’s∗
∗
Note: after 2002 data for West-Berlin is included. Source: Institute (2003), Bundesanstalt für
Arbeit (2002, 2005), own calculations.
54
Figure 2: Entries into Training in East Germany, Annual Totals
∗
In 1990, training programs took place only in October, November, and December. Following
the 1998 reform, training can no longer be subdivided into the categories Further Training and
Re-Training. Source: Bundesanstalt für Arbeit (1993, 1997, 2001, 2003), own calculations
30
400
20
200
10
Average participant stocks (1000)
600
0
0
1990*
1992
1994
Participant stocks
1996
1998
2000
Costs per participants-year (1000 €)
Figure 3: Participation Stocks in Training and Expenditure per Participant / Year,
Annual Average
2002
Expenditure (€ per participants-year)
∗
For 1990 no annual stock can be calculated. Source: Bundesanstalt für Arbeit (1993, 1997,
2001, 2003), own calculations
55
Figure 4: Labor Force Status by Treatment Status
Labour force status of non-participants, 1990-99
Percenatges of all valid cases
100%
80%
60%
Out of labour force
Public Job Creation Program
40%
Public sector sponsored training
Unemployed
Working PT
20%
Working FT
Dez 99
Jun 99
Dez 98
Jun 98
Dez 97
Jun 97
Dez 96
Jun 96
Dez 95
Jun 95
Dez 94
Jun 94
Dez 93
Jun 93
Dez 92
Jun 92
Dez 91
Jun 91
Dez 90
Jun 90
0%
Calendar time
Labour force status of participants, 1990-99
80%
60%
Out of labour force
Public Job Creation Program
40%
Public sector sponsored training
Unemployed
Working PT
20%
Working FT
Calendar time
56
Dez 99
Jun 99
Dez 98
Jun 98
Dez 97
Jun 97
Dez 96
Jun 96
Dez 95
Jun 95
Dez 94
Jun 94
Dez 93
Jun 93
Dez 92
Jun 92
Dez 91
Jun 91
Dez 90
0%
Jun 90
Percenatges of all valid cases
100%
Figure 5: Mobility Pattern for Training Period 1990–1993
57
Figure 6: Mobility Pattern for Training Period 1994–1999
58
Figure 7: Differences in the Outcome Variable in the Matched Sample for CDiDS
Estimator with Matching on Nonemployment in Month before Start of Training –
Employment Probability as Outcome
59
Figure 8: Differences in the Outcome Variable in the Matched Sample for CDiDHR
Estimator with Matching on Nonemployment in Month before Start of Training –
Probability of Exiting Nonemployment as Outcome
60
Figure 9: Differences in the Outcome Variable in the Matched Sample for CDiDHR
Estimator with Matching on Nonemployment in Month before Start of Training –
Probability of Remaining Employed as Outcome
61
Figure 10: Employment Effects of TR (Matching on Long–run Preprogram Employment History) - Employment Probability as Outcome
62
Figure 11: Employment Effects of TR (CDiDS with Matching on Nonemployment
in Month before Start of Training) - Employment Probability as Outcome
63
Figure 12: Employment Effects of TR (CDiDHR with Matching on Nonemployment
in Month before Start of Training) – Probability of Exiting Nonemployment as
Outcome
64
Figure 13: Employment Effects of TR (CDiDHR with Matching on Nonemployment
in Month before Start of Training) – Probability of Remaining Employed as Outcome
65
Discussion on Recall Error in LMM–SA
Retrospective data, which in our case covers at least 8 years, entails the danger of
recall errors. In the following, we will argue that recall errors are less problematic in our
analysis than is typically the case with retrospective data.
First of all, note that the individuals were asked about their employment history starting with the year 1990. This year constitutes a turning point in the biography of East
Germans, as the political and economic system changed dramatically. The connection
of biographic events with historic events, as done here, typically improves the validity of
recall data (Loftus/Marburger, 1983, Robinson, 1986). Additionally, starting with the
salient year 1990 the individuals had to answer in chronological order, which is now commonly viewed as the best technique in collecting life history data in a single survey (Sudman/Bradburn, 1987). Second, our broad definition of employment states circumvents
some of the recall errors which are present when analyzing more than two labor market
states. It helps especially to merge the states unemployment and out of the labor force.
For instance, after some time in unemployment, women tend to label this as having been
out of the labor force (Dex/McCulloch, 1998). Third, our evaluation design (CDiDHR
estimator) allows for recall errors occurring in the same fashion among treatment and
matched comparison group. In particular, if both groups forget to mention transitions in
a similar way then the errors simply cancel out.
Thus, recall errors in our analysis might only increase the standard errors of our
estimates. However, if we were estimating individual labor market flows, recall errors
would be more worrying (Paull, 2002) and it might be useful to change the methodological
approach (e.g. following Magnac/Visser, 1999).
References
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Magnac, T. and M. Visser (1999). “Transition Models with Measurement Errors.” Review of Economics and Statistics 81:466-474.
Paull, G. (2002). “Biases in the Reporting of Labor Market Dynamics.” The Institute
for Fiscal Studies Working Paper 02/10. London: The Institute for Fiscal Studies.
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