Are temporary work agencies stepping stones into regular employment?

3.1 Differences-in-Differences

Here, T is getting treatment, X is a set of confounders, and Y _0i the potential outcome if not taking treatment. Having a rich set of observables is, as previously stated, crucial for being able to claim that the CIA holds and thus that the conditional differences- in-differences (cDiD) is valid. More specifically, observables such as previous labor market performance prior to treatment might control for the unobservable characteristics that cause a selection bias. One way of applying the matching approach is to weight the most crucial variables in the estimation in order to balance the two groups so that they look very similar along observable dimensions. This can be done by coarsened exact matching (CEM) where the reweighing is done individually on the different confounders depending on relevance¹⁰.

Here, α is the intercept, the a _i are the individual dummies, γ _t is a set of time dummies, X _i,t is a set of confounders, ν _i,t is the error term, T _i,ρ  = 1[if will be getting treatment], and T _i,τ  = 1[if treated]. Given that there are no anticipation effects (by construction impossible in this setting) the coefficient of the leads (δ _ρ ) should be zero (i.e., parallel trends) strengthening our causal link hypothesis. Since the matching is performed before estimating the equation, we omit any treatment group dummy in Equation (3) since its coefficient will be zero if the matching was successful. Including a group dummy would, in that case, only inflate the standard errors while not contributing to the model. The timing of the treatment is chosen to be 2002 to ensure a long follow-up.

Joining a TWA after the treatment year by either the control or treatment group is permitted and thus selection is orthogonal to future outcomes. Violating this and in effect conditioning on future outcomes would lead to a bias of the estimated effect (Fredriksson and Johansson 2003).

Both groups are identified by being unemployed in 2001, thus a form of matching on pre-treatment labor market outcomes is already performed here. The control group is defined as not joining a TWA in 2002 and instead engaging in something else or staying unemployed. The counterfactual path is then, e.g., taking up studies, dropping out of the labor force, taking a regular job, etc. No restrictions were put on any outcomes from 2003 to 2008.

The reason for using both iDiD and cDiD (to be described in the following section) is that we can expect iDiD to give more precise estimates by construction, compared to a regular DiD by controlling for individual effects rather than two group effects. Also, controlling for unobserved and observed heterogeneity with fixed effects does not prune out observations like coarsened exact matching (CEM)¹⁴ does: CEM might result in very few observations. On the other hand, cDiD can, by balancing the two groups, mitigate the bias occurring when, for instance, the two groups have different age compositions, something which can give rise to diverging income progressions (steeper for younger people). Using well-balanced groups it is also more convincing to point at the control groups’ outcome as the actual counterfactual outcomes since they are the same in all observed aspects. The drawback then is of course the low number of observations that arise due to tight matching criteria. Contrasting these two methods with each other will also give the reader a feel for how big the self-selection bias might be in this application.

3.2 Matching

Matching is a technique to overcome the selection bias threatening causal inference. The approach is, however, not uncontroversial. Evidence pointing in favor of the technique comes from, e.g., (Dehejia and Wahba 1999), who report a successful non-experimental analysis on the data in (LaLonde 1986): using matching, they replicate the experimental impact estimates. (Smith and Todd 2005) criticizes (Dehejia and Wahba 1999), but conclude that the matching technique is best put in a DiD-design, which is what is done in the present paper (conditional DiD). A principle conceptual difference between regular regression estimations and matching estimation is that the latter gives the researcher greater flexibility in choosing how to aggregate heterogeneous effects, especially when using the specific technique coarsened exact matching. Since previous work has shown that the impact TWAs have on individuals differ greatly among groups, this is of great importance. Due to the explicit and easily manipulated weighting procedure, which is in the hands of the researcher instead of implicitly in the estimator (as in OLS), matching makes it easier to estimate the interesting parameters such as the ATT in a stratified way (Cobb-Clark and Crossley 2003).

Matching estimations rely on the CIA as discussed earlier. Furthermore, (Rosenbaum and Rubin 1983) noted that an additional condition was needed, common support: If we define P(x) as being the probability of getting treatment (T) for an individual with characteristics x, then the common support condition requires 0 < P(x) < 1, ∀x. This is also called the overlap condition and it rules out the perfect predictability of T given x; without this assumption, we have no information to construct our counterfactuals. CEM takes care of this by construction.

Coarsened exact matching is a member of the Monotonic Imbalance Bounding (MIB) class of matching methods (further described in (Iacus et al. 2008)). It is a method of pre-processing data which deals with the 'curse of dimensionality’¹⁵ by coarsening continuous data into bins where the researcher by in-depth knowledge of the variables at hand can determine the size of the bins to preserve information and maximize the number of matches. When the continuous variable is coarsened into bins, matching will take place on the respective strata and then observations are finally re-weighted according to the size of their strata. The bin width can be constant (ε _j ) within the variable j or it can vary within each variable, ${\epsilon }_j^v$, where the v are the cut-off points. Then basically any type of regression can be performed while including the new weights on the uncoarsened data. If the matching is exact in a variable—which is done for, e.g., the educational level—then this confounder is not needed in the regression since the balancing is perfect, unless the variable is time varying. If the matching is exact only on the coarsened values and/or is time varying, then the confounder should be included in the regression to control for the within-bin correlation which most likely will be very small if the bin width (ε _j ) is tightly defined.

The rationale for using CEM instead of, e.g., propensity score matching, is because this technique is more transparent, straightforward, by construction deals with the common support, gives priority to balancing (thus reducing bias and model dependence) to variance (high precision), meets the congruence principle, is computationally efficient, and reduces the sensitivity to measurement error (which would lead to biased estimates of the ATT, see (Iacus et al. 2008)). In Figures 5 and 6 in the Appendix, two kernel density plots over aggregated days in unemployment from 1998 to 2001 and two histograms over age are graphed before and after matching to give a visual representation of what is going on in the matching process. The treatment group has a higher density over the left region of days in unemployment and vice versa over the right region, this skewness is adjusted through the matching. A similar adjustment takes place in the variable age, where the treatment group has a lower density in the left region and vice versa in the right. Notably the sample under study becomes a quite young sample compared with the population. Since balancing the two groups to each other changes the average sample characteristics compared to the population, we in effect measure the sample average treatment effect on the treated (SATT) when applying CEM. Matching was performed exactly in 2001—unless otherwise is specified—on gender, level of education, and marital status; coarsened exact matching on aggregate days in unemployment from 1998 to 2001¹⁶ (ε _{u n e m p.} = 2 days), age (ε _age = 5 years), annual earnings in 2000 (${\epsilon }_{\mathit{\text{earnings}}}^v$ where v = [0, 5000, 10,000, 15,000, 20,000, 25,000, 30,000, 35,000, 40,000, 60,000, 100,000, 200,000]). For non-western immigrants, the income distribution was completely different and the following break points were chosen to get a sufficient number of matches: v = [0, 3000, 10,000, 50,000]. The number of children over age groups (${\epsilon }_{{\mathit{\text{children}}}_{\mathit{\text{age}}}}^v$ where v = [0.5, 1.5, 2.5] and age = [0–3, 4–6, 7–10, 11–15, 16–17, 18+]). When matching the non-western sample, marital status was not included since it reduced the number of matches and did not help to establish parallel trends. Region of birth was not included since it reduced the number of matches severely: if region of birth were included in the regression, the F-test would not be able to reject the hypothesis that the coefficients are zero (at the 5% significance level)¹⁷.

4.1 Unmatched results

Here, Y is either regularly employed, unemployed or employed. Thus each line of Table 7 in the Appendix is a separate regression measuring the effect of joining a TWA in year 2002 on subsequent labor market outcomes.

The estimates in Table 7 in the Appendix hint at a locking-in effect during the first years, which fades away and becomes insignificant in 2006 and 2007 though still negative. For unemployment, we find the same mechanical decrease of unemployment in the first year. Those who joined a TWA have a risk of unemployment in 2003 that is 6.3 percentage points lower, but already in 2004 the estimate becomes insignificant. In 2006 and 2007 the estimates once again turn significant. It would, however, be quite a stretch to draw any inference about that, since the earlier insignificant estimates suggest that we are most likely picking up something unobserved systematic, e.g., the business cycle. The overall probability of employment rises by 0.22 and then hovers around 0.10, implying that treatment raises the participants’ overall employment rate. The non-western immigrants section of the table show similar results but with more unfavorable figures compared to the full sample in all aspects. These results will be contrasted against the more causally robust cDiD and iDiD estimates.

Making use of the individual DiD design, we estimate the equation for the full sample and the subsample non-western immigrants¹⁸. The estimated coefficients, i.e., the average treatment effects on the treated (ATT), are seen in Table 8 in the Appendix¹⁹. The estimates exhibit a similar pattern as in Table 7 in the Appendix but overall they are more unfavorable for the stepping stone hypothesis. The results hardly vary when conditioning on non-western immigrants, though one could argue that they do not suffer any TWA stigma²⁰(or, at least, suffer less of a TWA stigma) since the post-treatment estimates on regular employment are lower than for the full sample and revert back to insignificance more quickly. When performing the individual DiD estimation on income, the parallel trends assumption is in the danger zone. Figure 2 suggests a small diverging trend from 1998 to 2001; the individual FE:s do not control for the differences in the pre-existing trend. This is picked up by the iDiD estimator in Figure 8 in the Appendix and suggests that the estimates are unreliable. In the following section, matching will prove itself useful compared to fixed effects in mitigating these sorts of problems.

4.2 Matched results

where k is the number of dimensions (or variables), f is the treated, g is the control, and ℓ is the variable imbalance. $f_{{\ell }_1\cdots {\ell }_k}$ is then the k-dimensional relative frequency for the treated. ${\mathcal{ℒ}}_1=0$ means perfect balance and ${\mathcal{ℒ}}_1=1$ means perfect imbalance. The measure by itself is not that informative but computing the pre-matching ${\mathcal{ℒ}}_1$ and comparing it to the post-matching ${\mathcal{ℒ}}_1$ will show if the matching was successful.

The first balancing is done on the full sample where pre-matching ${\mathcal{ℒ}}_1=0.99$ and post-matching ${\mathcal{ℒ}}_1=0.86$. The summary statistics reported in Table 5 in the Appendix exhibit a clear improvement relative to Table 2. Since matching on aggregate days in unemployment was performed at two-day precision—and not in the intervals specified in the table—the balanced result cannot be entirely visible in the table (though it can be viewed in Figure 5 in the Appendix. Country of birth is not perfectly balanced since no matching was made on that variable. Still, improvement has been made; only the Nordic countries are unbalanced in the treatment group’s favor (2 percentage points more in the treatment group). The fact that balancing on some variables gives rise to balancing on other observable variables adds to the plausibility of the CIA assumption, since it is not unreasonable to believe that unobserved characteristics also might become balanced. The post balancing results for the subsample non-western immigrants are shown in Table 6 in the Appendix. The balance is not perfect in the mean Aggregate days in unemployment but the difference is insignificant. Balancing had not been performed on country of birth or year of arrival, yet they still balanced after matching. The ${\mathcal{ℒ}}_1$ statistic equals 1.0 for pre-matching and 0.8 post-matching, an even better improvement than for the full sample matching. If we compare the ${\mathcal{ℒ}}_1$ statistics and the matched tables to the unmatched, it is clear that improvements have been made. However, the common support condition implies a substantial reduction in the number of observations, which affects the precision of the estimates.

Figure 3 compares the iDiD and the cDiD estimates of the probability of being regularly employed for the non-western immigrants and the full sample. In Figure 3 the different sample average effects on the treated (SATT) for the outcome employment are plotted over time, the estimates for all labor market outcomes are displayed in Table 3. For the full sample, the probability of regular employment is not significantly different from zero in 2007 while the iDiD estimates were always significantly negative²². Stratification on gender shows that women endure negative regular employment estimates until 2006 while men’s estimates only remain significant until 2004, see Figure 7 in the Appendix. Another change that has taken place—compared to the iDiD estimates—is in the regular employment probability for non-western immigrants, where there is no evidence of a negative significant effect, which is in line with the theory of a more favorable subsequent labor market outcome for immigrants than for natives. However, this is rather an absence of adverse effects than a prevailing positive effect. Notably, the standard errors are large and the estimated insignificant effect for 2003 might just be due to imprecisions caused by the reduced number of observations.

The estimates for unemployment (Table 3) are in agreement with the overall employment results, by never getting anywhere near significantly positive. The cyclical pattern of unemployment exhibited in the iDiD estimates has been reduced by the matching process, thus showing a favorable image for TWA’s effect on the transition out of unemployment. Apart from 2005, until 2007 all estimates are significantly negative, hovering around 0.04 to 0.08.

For instance, joining a TWA in 2002 reduced the probability of getting unemployed by 4 percentage points in 2004. Compared to the iDiD estimates where the unemployment significantly fluctuated around zero, the cDiD estimates do not. If negative self-selection was the reason for the cyclical pattern then it seems likely that the matching has mitigated the problem, making these estimates more reliable. The unemployment estimates for non-western immigrants exhibit an insignificant positive trend before taking treatment, the in-treatment effect is then significantly negative, followed by four consecutive years of negative insignificant estimates and then two years of significantly negative estimates. The pattern displayed in the unemployment column for non-western immigrants is similar to the full sample unemployment column even though—maybe due to imprecision—more estimates are insignificant and also the impact is larger. For instance: in 2007 taking treatment lead to a 15.4 percentage points drop in the probability of being unemployed for non-western immigrants and 8.7 percentage points for the full sample.

The overall employment has also changed significantly from the unmatched estimates. The iDiD estimates where significant at the 5%-level for only two years whereas the cDiD estimates never go insignificant. The employment columns in Table 3 shows clear cut evidence of a long-run change in the probability of employment for both the full sample and the immigrant subset. Given that the matching successfully eliminated the self-selection bias, we can causally interpret this as joining a TWA increases one’s probability of employment in the long run by approximately 7 to 9 percent points in general and 12 to 15 percent points for non-western immigrants.

Given the effect on employment probability it might also be interesting to take a closer look at the income progression that one would expect from joining a TWA. Previous studies usually show that the working conditions in TWAs are worse and that the salaries are lower than those in regular employment contracts (Jahn 2008). The coarsened exact matching technique showed itself useful in the income equation where the process purged out individuals with diverging pre-treatment income trends and reduced the standard errors. A time trend has also been included in the earnings regression apart from the other confounders included in the employment status cDiD. Figure 4 and Table 10 in the Appendix report the estimates. There are no subsequent adverse earnings effects from joining a TWA. In fact the income progression seem to benefit from TWA employment, supporting the descriptive results in Figure 2. When stratifying on gender (Figure 4 and Table 10 in the Appendix), it seems as though the effect is mostly driven by women. Since the parallel trends assumption cannot be empirically supported in the non-western immigrants sample, the estimates are unreliable.

This means that the treatment group on average increased their annual earnings by 9% in 2008 compared to those not taking treatment when accounting for employment effects. How much of this that is an effect of increased working hours rather than a wage increase is unfortunately not possible to determine with the available data, but presumably the hours effect dominates. One has to keep this equation in mind when interpreting the plots.

4.3 Robustness check

To make sure the results do not hinge on the specific timing of treatment (2002) a type of robustness check was performed: All equations were re-estimated with 2004 as treatment year instead of 2002. Neither the iDiD nor the cDiD estimator showed a sensitivity to the treatment timing. The overall pattern was unchanged in all estimations. Two changes are worth noting though: the unemployment estimates for the cDiD shifted down a few points, making the estimates significant at all post-treatment years. Secondly, the earnings estimates shifted upwards, resulting in significantly positive estimates for all panels in the post-treatment years.

By this I conclude that the reported results most likely are robust since the pattern and the estimates barely varied when switching treatment year.