Preventing NEETs During the Great Recession The Effects of a Mandatory Activation Program for Young Welfare Recipients

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1 Preventing NEETs During the Great Recession The Effects of a Mandatory Activation Program for Young Welfare Recipients Emile Cammeraat Egbert L.W. Jongen Pierre W.C. Koning January 27, 217 Abstract We study the impact of a mandatory activation program for young welfare recipients in The Netherlands. Introduced at the end of 29, the goal of the program was to prevent so-called NEETs (individuals not in employment, education or training). We use a large administrative data set for the period and employ differences-in-differences and regression discontinuity to estimate the effects of the reform. We find that the reform reduced the number of NEETs on welfare, increased the number of NEETs not on welfare, and had no effect on the overall number of NEETs. Our results contrast with previous studies, which may be due to the fact that the reform took place during a severe economic recession. JEL codes: C21, H31, J21 Keywords: NEETs, mandatory activation programs, differences-in-differences, regression discontinuity, Netherlands We are grateful to Ineke Bottelberghs, Marina Pool and Mirthe Bronsveld-de Groot of Statistics Netherlands for the data on participation in mandatory activation programs by young welfare recipients. Furthermore, we are grateful for comments and suggestions by Matz Dahlberg, Bas Jacobs, Max van Lent and participants of the IIPF 216 Doctoral School in Mannheim, the IIPF 216 Conference in South Lake Tahoe, the EALE 216 Conference in Ghent and the NED 216 in Amsterdam. Remaining errors are our own. Leiden University, Department of Economics, Steenschuur 25, 2311 ES, Leiden, The Netherlands. e.cammeraat@law.leidenuniv.nl. Corresponding author. CPB Netherlands Bureau for Economic Policy Analysis and Leiden University. e.l.w.jongen@cpb.nl. Leiden University, VU University Amsterdam, Tinbergen Institute and IZA. p.w.c.koning@law.leidenuniv.nl. 1

2 1 Introduction Individuals not in employment, education or training (NEETs) are a major policy concern, in particular during periods of recession. NEET rates have not recovered yet from the Great Recession, making them a prime concern for the European Commission (Carcillo et al., 215). Recently, President Juncker of the European Commission stated in his 216 State of the Union speech that he wants to continue to roll out the Youth Guarantee across Europe, improving the skillset of Europeans and reaching out to regions and young people most in need (European Commission, 216). This increased policy attention for reducing the number of NEETs is accompanied with a trend towards stricter conditions for receiving welfare benefits; via e.g. the imposition of job search requirements and/or by making welfare benefits receipt conditional on participation in so-called work-learn programs. These policies are mostly targeted at young unemployed individuals, prominent examples include the New Deal for Young People in the UK and the Jobs Corp in the US (Kluve, 214). Previous studies have found that stricter conditionality of welfare benefits decreases welfare claims and increases employment rates (Blundell et al., 24; Hernæs et al., 216; Dahlberg et al., 29; Bolhaar et al., 216). In this paper, we study the effects of a mandatory activation program for young individuals during a severe economic recession. Specifically, we study the WIJ (Wet Investeren in Jongeren, Work Investment Act for Young Individuals) reform, introduced in the Netherlands at the end of 29, just after the start of the Great Recession. The reform targeted individuals up to and including individuals 26 years of age. The goal of the WIJ reform was to reduce the number of young NEETs. To this end, welfare benefits were made conditional on participation in work-learn programs. We consider the effects of the WIJ reform on a large number of outcome variables: NEETs claiming welfare benefits, NEETs not claiming welfare benefits, the overall NEETs rate, the employment rate and the enrollment rate in education. We use a large administrative data set called the Labour Market Panel (Arbeidsmarktpanel) of Statistics Netherlands (215). The Labour Market Panel tracks 1.2 million individuals over the period and contains a large set of labour market outcomes and a large number of individual and household characteristics. We use differences-in-differences and regression discontinuity to estimate the causal effects of the WIJ reform. Our base treatment group consists of individuals

3 years of age, and our base control group consists of individuals years of age. A key challenge in the empirical analysis is to control for potentially different time effects, absent the reform, between the treatment and control group, due to e.g. differential trends or different business cycle responses. In our preferred specification we include demographic controls, a full set of unemployment-rate-age dummies, age-specific trends and control-specific trends. Our main findings are as follows. First, we find that the reform had a statistically significant large negative effect on the number of young NEETs claiming welfare benefits of 24%. Second, the reform had only a small statistically insignificant effect on the total number of young NEETs. The reform pushed young individuals out of welfare, but did not increase the number of young individuals in employment or education. Third, our analysis shows that it is important to control for differential trends in a differences-in-differences analysis when studying a reform that targets young individuals and using somewhat older individuals as a control group. Our paper relates to a number of studies that consider the effects of mandatory activation programs for young individuals. Blundell et al. (24) use area-based piloting and age-related eligibility rules to identify the employment impact of a mandatory job search programme, the New Deal for Young People, in the UK. They find that the program increased the probability to find employment by about five percentage points. Persson and Vikman (21) analyze entry and exit effects of a welfare reform in Sweden where city districts in Stockholm implemented mandatory activation programs at different rates. They find that the reform reduced welfare participation and increased employment rates of younger individuals, particularly those born in non-western countries. Hernæs et al. (216) exploit a geographically differentiated implementation of conditionality of welfare benefits for Norwegian youth and find that stricter conditionality reduces welfare claims and increases high school completion rates. These analyses suggest that the combination of welfare conditionality and welfare-to-work programs reduce NEETs and promote employment and enrollment in education. We make the following contributions to this literature. First, we show that stricter conditionality combined with welfare-to-work programs does not always increase employment or enrollment in education. Indeed, we find that for the WIJ reform there was no effect on the number of young NEETs. The main effect of the reform was simply to push young individuals out of welfare. This is likely to be due 3

4 to the state of the business cycle, as the reform clashed head on with the start of the Great Recession, during which it was hard for people, in particular young individuals, to find a job. Second, we consider all potential outcome states, not only NEETs on welfare but also NEETs not on welfare, and the enrollment in education next to employment. Indeed, our analysis for young individuals in the treated group shows that when looking at the effects on the employment rate, it is important to study changes in the enrollment rate in education as well. Third, we use an exceptionally large and long data set, that allows us to study and account for differential trends. The outline of the paper is as follows. Section 2 describes the institutional setting and the main features of the reform. Section 3 discusses the empirical methodology. Section 4 discusses the data set and gives descriptive statistics. In Section 5 we then present graphical evidence, the estimation results and a number of robustness checks. Section 6 concludes. 2 Institutional setting and the reform Young NEETs are a policy concern in all OECD countries. However, there is considerable variation in the share of NEETs among the young across OECD countries, and the extent to which the share of NEETs has risen (or fallen) during the Great Recession, see Table 1. The Netherlands has one of the lowest NEETs shares among OECD countries, in 215 only 8.9% of 2 24 year olds in the Netherlands were NEETs. 1 Compared to 25, there has been a moderate rise in the share of NEETs in the Netherlands. The low share of NEETs in the Netherlands is in part due to the high share of 2 24 year olds that are in education in the Netherlands (and mostly full-time), and in part due to the high share of 2 24 year olds that are employed in the Netherlands, whereas the share of unemployed 2 24 year olds is relatively low, see again Table 1. 2 In the Netherlands, welfare benefits form a safety net that is provided by municipalities to support unemployed workers who are not, or are no longer, entitled to other types of social insurance benefits like unemployment insurance. The vast 1 In 215, the only country in the OECD with a lower share of NEETs was Iceland (6.6%). 2 The shares of individuals in education and individuals in employment add up to more than 1% because individuals in education can be employed, and employed individuals can also be in education. 4

5 Table 1: NEETs - An international perspective NEETs-to- Education-to- Employment-to- Unemployment-topopulation rate population rate population rate population rate FT and PT FT only Year Continental Europe Netherlands Belgium France NA Germany Scandinavia Denmark Finland Norway Sweden Anglo-Saxon countries Australia Canada NA NA United Kingdom Unites States OECD average Source: OECD (216a), OECD (216b) and OECD (216c). All numbers refer to individuals aged 2 24 years of age. The education-to-population rate is the enrollment in education divided by the population. FT and PT is shorthand notation for full-time and part-time education, respectively. The unemployment-to-population rate is calculated as the unemployment rate multiplied by the labour force participation rate. majority of new welfare recipients consists of individuals with insufficient work history for entitlement to unemployment insurance. Indeed, in 214, only 22% of all new welfare recipients consisted of unemployed workers who exhausted their unemployment insurance benefits (UWV, 214). Welfare benefits are means-tested and assets-tested. 3 The level of welfare benefits differs across household types and age 3 For single individuals, net worth should not exceed 5,765 euro. For households with more 5

6 groups, ranging from 22 euro per month for singles of 18 2 years of age, to 1,32 euros per month for couples with children (Ministry of Social Affairs and Employment, 28). The Work Investment Act for Young Individuals (Wet Investeren in Jongeren, WIJ) came into force in October 29 as a consequence of increased policy attention for NEETs and welfare dependency. The reform was designed before the start of the Great Recession, but the implementation was after the start of the Great Recession (September 28). The WIJ reform aimed at activating the young, as well as fostering their human capital formation. The WIJ stipulated that for individuals below the age of 27, entitlement to welfare benefits was conditional on participation in a mandatory activation program. 4 These programs were defined as work-learn -offers and consisted of public employment programs, apprenticeships and internships. Any wage earnings that were made in these programs were supplemented up to the level of welfare benefits. As Figure?? shows, the WIJ increased the coverage rate of activation programs for young welfare recipients in our preferred treatment group (individuals years of age) from around 8% in January 29 to almost 9% in 211. Hence, the discretionary room of caseworkers administering welfare benefits was restricted considerably. The WIJ applied to all new entrants into welfare from October 29 onwards. However, as the enactment of the WIJ implied a substantial increase in the workload for municipalities, municipalities got nine additional months until July 21 to increase coverage of the WIJ to 1% of the pre-existing stock of welfare recipients. Figure?? suggests that in the end it took until January 211 for the WIJ to be fully implemented. 5 To get a better understanding of the implementation of the WIJ reform at the local level, we interviewed policymakers and caseworkers from the city of Amsterdam that were involved in the design and implementation of the WIJ. In Amsterdam, the majority of work-learn offers were provided by retail companies, local industries and reintegration agencies. The respondents in our interviews stressed that some aspects persons, net worth should not exceed 11,895 euro. 4 The WIJ contains many elements that are similar to the New Deal program for younger individuals in the UK (Wilkinson, 23; Blundell et al., 24; Dorsett, 26). 5 This is consistent with the numbers presented in Leenheer et al. (211), who calculate that about 7% of the WIJ applications received a work-learn offer in 21, 11% received welfare benefits without a work-learn offer, and the remaining 19% did not receive welfare benefits. 6

7 Figure 1 (a) Participation rate in activation programs by individuals on welfare (b) Number of individuals on welfare 2, 18, 16, 14, 12, 1, 8, 6, 4, 2, (c) Number of individuals in activation programs 14, 12, 1, 8, 6, 4, 2, Notes: Statistics Netherlands (personal communication).

8 of the WIJ were already common practice in Amsterdam. That is, apprenticeships, internships and public employment programs were already provided for individuals up to 23 years of age (Board of Amsterdam, 28). In effect, in Amsterdam the WIJ reform thus implied the extension of these programs to individuals with years of age, together with the imposition of welfare conditionality for all young individuals below the age of 27. In our empirical analysis, we focus on the group of individuals years of age, but we also consider the effects for younger age groups. Finally, next to the WIJ reform, there were two other reforms that are relevant for our analysis. First, in January 212 the government replaced the mandatory acceptance of work-learn offers with work-first arrangements. Specifically, the government introduced an initial one-month job-search period during which individuals younger than 27 years of age did not receive welfare benefits. This can explain the small drop in the participation rate in activation programs in January 212, and the larger drop in January 213, see Figure??. Second, also from January 212 onwards, adult children living at home were no longer eligible to welfare benefits when they lived in a household in which first-degree relatives had sufficient income or assets (the household-income test ). in the empirical analysis we also consider treatment effects by individual years, the treatment effect on the probability of being an adult child living at home and the treatment effects for the subgroup of adult children living at home. 3 Empirical methodology We use differences-in-differences (DD) and regression discontinuity to estimate the effects of the WIJ reform on a number of outcome variables. 6 In the DD approach we estimate the impact of a policy reform by taking a double difference between the treatment group and a control group in the outcome variable. First, we take the difference in the outcome variable between the treatment group and the control group after the reform. Second, we subtract the difference in the outcome variable between the treatment group and the control group before the reform. In this way we control for the time-invariant difference between the 6 For a general introduction to the differences-in-differences and regression discontinuity methodologies see e.g. Angrist and Pischke (29). 8

9 treatment and control group and for common time effects in the outcome variable. The WIJ reform targets individuals up to 27 years of age. Our preferred treatment group consists of individuals years of age and our base control group consists of individuals years of age. We also consider the treatment effects for younger individuals, but we will show that changes in the enrollment in education complicate the analysis for this group (young individuals in the treated group have a choice of staying in education, while this is hardly a choice for individuals in the control group). The age is measured on the 1st of October, and the outcome variables are averages for the month October. As outcome variables we consider the participation rate in NEETs, defined as not being in employment or education 7, the participation rate in NEETs on welfare, the participation rate in NEETs not on welfare, the participation rate in employment (employment rate) and the participation rate in education (enrollment rate in education). Together these probabilities sum to one, but we analyze them independently. We estimate a linear probability model (Angrist and Pischke, 29). Let y iat be a dummy variable that is 1 if individual i in age group a is participating in period t. In our most extensive specification, we regress the outcome variables on a set of year fixed effects (α t ), age fixed effects (β a ), age-specific trends with coefficients (γ a ), an interaction term between age and the unemployment rate (u t ) with agespecific coefficient φ a, a set of demographic controls X i (gender and ethnicity) with coefficients µ x, a set of demographic-control specific trends with coefficients ψ x, a treatment effect (DD at ) for individuals in the treatment group with age a in a given year t in the post-reform period with coefficient δ a, and an error term (ɛ iat ): y iat = α t + β a + γ a t + φ a u t + X iµ x + X iψ x t + δ a,t DD at + ɛ iat. (1) We are primarily interested in the treatment coefficients δ a,t. We include an interaction term between age and the unemployment rate to allow for different business cycle responses across age groups (Bell and Blanchflower, 211). Furthermore, we include age and demographic control specific trends to allow for trend differences (note that we have 1 years of pre-reform data to estimate the coefficients on these trends). In an extension we also include placebo treatment dummies for the pre-reform 7 Similar to the OECD, we do not observe participation in shorter training programs in our data set. 9

10 years 28 and 29. The coefficient on this placebo treatment dummy is informative about potential remaining differential time effects between the treatment and control groups, for example because of changes in group specific trends or differences in business cycle responses not captured by the age-specific unemployment terms, and also about potential anticipation effects of the reform. Finally, to allow for correlation in the error terms at a higher level of aggregation than the individual, we use clustered standard errors (Bertrand et al., 24; Donald and Lang, 27). We cluster standard errors by year of birth interacted with the region where the individuals is living, which results in 216 clusters in our base DD specification, deemed for sufficiently large by Angrist and Pischke (29) to use the large sample properties of the estimator. The RD approach identifies the labour supply response by comparing young individuals just younger than the cutoff that determines treatment by the WIJ reform with inidividuals just older than this cutoff. The idea is that in the absence of the reform, the outcome variables are a smooth function in age, and the reform introduces a discontinuity in these function. Also in the RD approach we use linear probability models. In the most elaborate specification, we regress participation status y iat on a year fixed effect (β t ), age in months (recentered) 8 a it (with coefficient β a ), (recentered) age in months squared (with coefficient β a 2), an interaction term that captures the additional effect of age when the person is younger than the cutoff a (with coefficient β a<a ) to allow for a different slope to the left of the discontinuity, a treatment effect if the age of the person is below 27 (with coefficient β RD ) capturing the discontinuity, time-varying individual and household characteristics X it and an error term ɛ it y iat = β t + β a a it + β a 2 (a it ) 2 + β a<a 1(a it < a )a it + β RD RD it + X itµ + ɛ it. (2) In the RD analysis our primary interest is in β RD. For an accurate measurement of the discontinuity it is important to get a precise estimate of the relation between age and the outcome variables around the discontinuity. In the RD analysis we therefore use month of birth relative to the discontinuity 9 as the running variable. 1 8 Age is recentered so that individuals that have turned 27 in September have a value of 1, they are the first non-treated group. 9 The exact date of birth is not available in our data set. 1 In the appendix we show that the results are similar when using quarter of birth or year of birth instead. 1

11 Also, in the RD analysis we want to account for cluster correlation of the error term over individuals and over time, and present standard errors clustered at a broader level of aggregation than the individual. Since the identification comes from differences in month of birth, we cluster standard errors by month of birth (with persons born in the same month but in different years in different clusters). This by itself generates a sufficient number of clusters, 72 in our base specification, so that in this case we do not need to interact these months of birth with province. In an extension of the RD analysis we consider what might be called a differencein-discontinuity setup, using both the pre- and post-reform data. Using observations both before and after the policy reform, we can control for a potential discontinuity before the reform, due to e.g. discontinuities in pre-existing policies. In this specification we include a treatment effect γ P RD that captures the pre-reform discontinuity, and an additional treatment effect for the post-reform discontinuity relative to the pre-reform discontinuity γ DRD (i.e. the discontinuity before the reform equals γ P RD and the discontinuity after the reform equals γ P RD + γ DRD ). Furthermore, we also allow for a different slope in age and a different slope in age left of the discontinuity in this specification. For the same reasons as in the RD analysis we use age measured in months relative to the discontinuity as the runnig variable, and we cluster the standard errors by month of birth. 4 Data set We use data from the Labour Market Panel (Arbeidsmarktpanel) of Statistics Netherlands (215). The Labour Market Panel is a large and rich household panel data set, tracking 1.2 million individuals over the period We use the years as the pre-reform years, and as the treatment years. To ensure that the treatment and control groups are sufficiently similar in their characteristics, we limit the sample to individuals years of age. Our preferred treatment group consists of individuals years of age. Our preferred control group consists of individuals years of age. We study the following outcome variables: a) the participation rate in NEETs, defined as not being in employment or education, b) the participation rate in NEETs 11 For a limited number of variables, not used in this study, the data set also contains data for

12 on welfare, c) the participation rate in NEETs not on welfare, d) the employment rate and e) the enrollment rate in education. The states a), d) and e) make up the full sample of individuals in a specific age group (they add up to 1). These outcome variables are based on the social-economic classification (SEC) variable in the Labour Market Panel. The SEC variable classifies individuals according to their main source of income, where individuals in education are always classified as being in the state of education and individuals with profit income are always classified as being self-employed (even if their wage income exceeds their profit income). According to the SEC individuals can be in the following states: 1) employee, 2) owner of closely-held company, 3) self-employed, 4) other type of employment, 5) on unemployment insurance, 6) on welfare benefits, 7) on disability or sickness benefits, 8) on retirement benefits (including benefits for orphans), 9) on other social insurance, 1) in education with income, 11) in education without income, 12) without income. We count individuals in states 1)-4) as employed, in states 1) and 11) as in education, and in states 5)-9) and 12) as NEETs. Within the state of NEETs we count individuals in state 6) as NEETs on welfare and individuals in states 5), 7)-9) and 12) as NEETs not on welfare. As demographic control variables we include gender and ethnicity (native/non-western immigrant/western immigrant). Table 2 gives the descriptive statistics for our treatment group, along with the differences and normalized differences (for the demographic control variables) with the control group in the pre- and the post-reform period. Differences in the demographic control variables gender and ethnicity are small between the treatment group and the control group, and the same is true for the so-called normalized differences (the mean differences divided by the square root of the sum of variances). Imbens and Wooldridge (29) argue that these normalized differences are an informative way to check if the treatment and control group have sufficient overlap in the covariates. As a rule of thumb they suggest that when the normalized difference exceeds a value of.25, linear regression becomes sensitive to the specification. The normalized differences for gender and ethnicity stay well below.25. Furthermore, the differences in the demographic control variables hardly change from the pre- to the post-reform period. Hence, there is no indication of differential changes in the composition of the treatment and control group. Table 2 also presents descriptive statistics for the outcome variables. The share of NEETs on welfare (in the relevant age population) in the treatment group is 12

13 Table 2: Descriptive statistics treatment and control group Treatment Group Differences Normalized differences a (pre-reform: ) (treatment control) (treatment control) Mean SD Explanatory variables Female Non-Western immigrant Western immigrant Dependent variables NEETS rate on welfare NEETs rate not on welfare Total NEETs rate Employment rate Enrollment rate education Observations : treatment group 376,83 and control group 391,627. Treatment group: individuals years of age. Control group: individuals years of age. a Normalized differences are mean differences divided by the square root of the sum of the variances (see Imbens and Wooldridge, 29). calculations using the Labour Market Panel (Statistics Netherlands). Source: Own very similar in the pre-reform period, and becomes smaller relative to the control group in the post-reform period. The share of NEETs not on welfare and the total NEETs rate are also quite similar, though somewhat smaller for the treatment group in the pre-reform period, and become somewhat bigger in the post-reform period. Furthermore, the employment rate is higher in the control group in the pre-reform period as well, and the difference in the employment rate becomes more negative in the post-reform period, suggesting a negative treatment effect on the employment rate. Finally, the enrollment rate in education shows the mirror image of the employment rate. The enrollment is higher in the treatment group than the control group in the pre-reform period, and the difference becomes bigger in the postreform period, suggesting a positive treatment effect on the enrollment in education. However, these simple treatment effects do not accounting for differential trends which will turn out to be important for some outcome variables in the empirical analysis below. 13

14 5 Results Figure 2 presents graphical evidence on the treatment effects of the reform on the outcome variables. The solid black lines denote the control group (27 28 years of age), the dashed red lines denote the treatment group (25 26 years of age) and the dotted blue lines denote the difference between the treatment group and the control group. What is clear from these graphs, is that the NEETs rate on welfare moves very much in tandem for the treatment and control group in the pre-reform period, but there are trend differences between the treatment and control group for the other outcome variables. Hence, accounting for these differential trends will be important to isolate the treatment effect of the reform. This also makes it hard to eyeball potential treatment effect from these graphs, that is why we turn to the results of a regression analysis next. Table 3 presents the base results for the different outcome variables, using a single treatment dummy for all years and both ages in the treatment group. Column (1) shows the results of the basic DD setup, where we only include year dummies, a group dummy for each individual age group and a treatment dummy for the age group This simple setup suggests a counterintuitive positive and statistically significant treatment effect on the total NEETs rate, with a smaller but statistically significant drop in the NEETs rate on welfare and a large and statistically significant rise in the NEETs rate not on welfare. The treatment effect on the employment rate is negative and large, whereas the treatment effect on the enrollment rate in education is positive and large, and both are statistically significant. Adding demographic control variables hardly affects the results, see column (2). When we add unemployment-age dummies, to capture different business cycle responses by age, the treatment effects typically become somewhat smaller in absolute terms, see column (3), but qualitatively the effects remain the same. But then, adding agespecific trends in column (4) has a big impact on the results, as suggested by the graphical analysis in Figure 2. The counterintuitive rise in the total NEETs rate becomes a small and statistically insignificant effect. The drop in the NEETs rate on welfare is quite similar, though a bit larger in absolute terms than in specification (3). The rise in the NEETs rate not on welfare is now much smaller. The negative effect on the employment rate is much, much smaller, as is the positive effect on the enrollment rate in education. Finally, adding demographic control-specific 14

15 Figure 2: DD: outcome variables treatment and control group over time (a) NEETs rate on welfare.4 Pre-reform Reform Difference (b) NEETs rate not on welfare (c) Total NEETs rate.12 Pre-reform Reform.16 Pre-reform Reform Difference Difference (d) Employment rate (e) Enrollment rate in education 1. Pre-reform Reform.12 Pre-reform Reform Difference Difference Notes: Own calculations using the Labour Market Panel (Statistics Netherlands). The solid black lines denote the control group (27 28 years of age), the dashed red lines denote the treatment group (25 26 years of age) and the dotted blue lines denote the difference between the treatment control group. NEETs rates are individuals not in employment or in education relative to the population, employment rates are individuals in employment relative to the population and enrollment rates are individuals in education relative to the population.

16 16 Table 3: DD: base results (1) (2) (3) (4) (5) NEETs rate on welfare (.15) (.15) (.17) (.23) (.21) NEETs rate not on welfare (.23) (.25) (.27) (.36) (.34) Total NEETs rate (.31) (.35) (.38) (.52) (.48) Employment rate (.55) (.48) (.52) (.67) (.66) Enrollment rate in education (.41) (.39) (.42) (.52) (.51) Demographic controls NO YES YES YES YES Unemployment-age dummies NO NO YES YES YES Age-specific trends NO NO NO YES YES Control-specific trends NO NO NO NO YES Observations 767,71 767,71 767,71 767,71 767,71 Clusters Cluster-robust standard errors in parentheses, clustered by year of birth*province (18*12=216 clusters), * denotes significant at the 1% level, ** at the 5% level and *** at the 1% level. Table 4: DD: placebo s and treatment dummies per year (1) (2) (3) (4) (5) NEETs rate NEETs rate Total Employment Enrollment rate on welfare not on welfare NEETs rate rate in education Treatment (placebo) (.28) (.58) (.73) (.91) (.61) Treatment (placebo) (.34) (.65) (.85) (.15) (.76) Treatment (.3) (.6) (.78) (.12) (.73) Treatment (.32) (.62) (.81) (.111) (.82) Treatment (.32) (.59) (.77) (.14) (.77) Observations 767,71 767,71 767,71 767,71 767,71 Clusters Cluster-robust standard errors in parentheses, clustered by year of birth*province (18*12=216 clusters), * denotes significant at the 1% level, ** at the 5% level and *** at the 1% level. All specifications include demographic controls, unemployment-age dummies, age-specific trends and control-specific trends.

17 trends in column (5) leads to results very similar to specification (4). Column (5) is our preferred specification. We find a tiny rise in the total NEETs rate of.14 percentage points. The drop in the NEETs rate on welfare is more pronounced,.45% percentage points ( 24% relative to the pre-reform year 29. There is also a marked increase in the NEETs rate not on welfare of +.59 percentage points. Finally, we find an insignificant drop in the employment rate of.23 percentage points, and a tiny increase in the enrollment rate in education of.9 percentage points. The base results suggest that the reform did not reduce the share of total NEETS, but did push NEETs out of welfare. In Table 4, we take specification (5) of Table 3 and include a placebo treatment dummy for the year 28 and 29, and also split the treatment dummy for into individual year dummies 21, 211 and 212. For the NEETs rate on welfare we find coefficients on the placebo treatment dummies that are small and insignificant. The treatment dummy for 21 is statistically significantly and more negative than the combined dummy for Indeed, the treatment effects for 211 and 212 are rather small, consistent with the pattern we see in Figure 2. Hence, the effect seems to have faded rather quickly. The coefficients on the placebo dummies are also small and insignificant for NEETs not on welfare, and most of the effect appears to be in 21. For the total NEETs rate, the coefficients on the placebo treatment dummies are small and insignificant, as are the individual year dummies in the post-reform period, and the same is true for the employment rate and the enrollment rate in education. Some further DD analyses are given in the appendix. Figures A.1-A.3 show that the control variables move quite similar both in the pre- and post-reform period for the base treatment and control group, suggesting no group specific changes in observable, and hence presumably also in unobservable, characteristics. Table A.1 shows that when we use individuals 29 3 years of age as an alternative control group, we find quite similar treatment effects for the preferred treatment group of individuals years of age, whereas placebo treatment effects for the preferred control group of individuals years of age are small and insignificant. Next, we consider extending or limiting the treatment group. Figure A.4 shows the participation rates in work-learn programs by individuals 2 26 and years of age. Hence, we also consider younger treated individuals. Figure A.6 shows that the NEETs rate on welfare still moves in tandem, but differences in levels are less 17

18 pronounced. More problematic seem the large differences in the enrollment rate in education and as a result also in the employment rate. However, regression results for the preferred specification (5) for the whole treatment group 2 26 years of age are still quite similar to the base results, see Table A.3. However, when we then run regressions with treatment effects by individuals ages, the results are more mixed, and different business cycle responses in the enrollment rate in education between the treatment group and the control group become problematic, see Table A.2. Focusing on the narrower group instead, with 26 being treatment and 27 being control, we obtain quite similar graphs as when using the base groups of and 27 28, see Figure A.4. Regression results are also quite similar to the base results, see Table A.4. Table A.5 considers the effect by level of unemployment, where we divide the regions by their pre-reform level of the unemployment rate into low and high regions. The results suggest a somewhat larger effect for regions with a high unemployment rate, but the difference with the effect for the low unemployment rate region is not statistically significant. Finally, in Table A.6 and A.7 we consider, respectively, the effect on the share of young individuals living at home with their parents, and the outcomes for young individuals living at home with their parents. Table A.6 show that in our preferred specification (5) we find essentially no effect on the share of adult children living with their parents. Table A.7 suggests a larger decline in the NEETs rate on welfare for young individuals living at home. When we use individual year treatment dummies in Table A.8, we find the largest effects for 21 and 211 indicating that it is not the 212 reform that explains this larger effect. This table also hints at a decline in the total NEETs rate for this group. Finally, Table A.9 include a placebo treatment dummy for the years to check for different business cycle responses between the treatment and control groups not captured by the age-unemployment dummies. We find very similar treatment effects, while this placebo dummy is small and statistically insignificant. For the RD analysis we also start with an eyeball test first. Figure 3 gives the outcome variables by month of birth relative to the discontinuity, where we show averages for the period The blue dots are the averages, the solid lines are predicted values for a simple RD regression with only age in months, the discontinuity and year dummies included, estimated separately on both sides of the discontinuity, and the dotted lines denote the corresponding 95% confidence interval. The graphs hint at a somewhat lower NEETs rate on welfare for individuals younger 18

19 Figure 3: RD: outcome variables relative to discontinuity (21 212) (a) NEETs rate on welfare Estimate of the discontinuity:.17 (.14) (b) NEETs rate not on welfare Estimate of the discontinuity:.4 (.29).12 (c) Total NEETs rate Estimate of the discontinuity:.23 (.32) (d) Employment rate (e) Enrollment rate in education Estimate of the discontinuity:.9 (.41) Estimate of the discontinuity:.13 (.24) Notes: Own calculations using the Labour Market Panel (Statistics Netherlands). NEETs rates are individuals not in employment or in education relative to the population, employment rates are individuals in employment relative to the population and enrollment rates are individuals in education relative to the population.

20 Figure 4: RD: pre-reform outcome variables relative to discontinuity (27 29) (a) NEETs rate on welfare Estimate of the discontinuity:.19 (.16) (b) NEETs rate not on welfare Estimate of the discontinuity:.1 (.25).12 (c) Total NEETs rate Estimate of the discontinuity:.29 (.35) (d) Employment rate (e) Enrollment rate in education Estimate of the discontinuity:.41 (.41) Estimate of the discontinuity:.12 (.22) Notes: Own calculations using the Labour Market Panel (Statistics Netherlands). NEETs rates are individuals not in employment or in education relative to the population, employment rates are the employed relative to the population and enrollment rates are individuals in education relative to the population.

21 21 Table 5: RD and DRD base results (1) (2) (3) (4) (5) NEETs rate NEETs rate Total Employment Enrollment rate on welfare not on welfare NEETs rate rate in education Panel A: RD (21 212) (.13) (.22) (.23) (.3) (.24) Observations 158, , , , ,195 Clusters Panel B: RD (27 29) (.14) (.23) (.3) (.34) (.22) Observations 157, , , , ,543 Clusters Panel C: DRD (27 212) (.2) (.31) (.38) (.46) (.3) Observations 315, , , , ,738 Clusters Cluster-robust standard errors in parentheses, clustered by month of birth (18 clusters), * denotes significant at the 1% level, ** at the 5% level and *** at the 1% level.

22 than the threshold, and a somewhat higher NEETs rate not on welfare for individuals younger than the threshold. There is no apparent discontinuity in the total NEETs rate, and the plots for the employment rate and the enrollment rate in education show that these outcome variables depend strongly on age. Figure 4 show the same outcomes, but for the pre-reform period These graphs do not hint at clear discontinuities for the outcome variables in the pre-reform period, although there are some small changes. Table A.11 gives the RD results for 6 different specifications. In the first three specifications we do not include demographic control variables, in the last three specification we do include demographic control variables. This hardly affects the results, though the estimated standard errors are somewhat smaller when we include the demographic control variables. In specification (1) and (4) we only include a dummy for the discontinuity in age. In specification (2) and (5) we also include a quadratic term in age. In specification (3) and (6) we allow for a different slope on the left-hand side of the discontinuity. Specification (6) is our preferred specification. The results are qualitatively similar to the DD results, but the effect on the NEETs rate on welfare is not statistically significant. Table A.12 gives small and insignificant treatment effects for the pre-reform period, suggesting no pre-reform discontinuity. However, when we combine the preand post-reform data in the difference-in-discontinuity setup, in Table A.14, we find results that are very similar to the DD setup. The drop in the NEETs rate on welfare is quite comparable to the DD results, although only statistically significant at the 1 percent level. The rise in the NEETs rate not on welfare is again comparable but of opposite sign when compared to the effect on the NEETs rate on welfare, as in the DD analysis, and the effect on the total NEETs rate is very small, and the effects on the employment rate and enrollment rate in education are small and statistically insignificant as well. The appendix gives additional analyses for the RD analysis as well. Figures A.8-A.13 show that there are no apparent discontinuities in the control variables around the cutoff, not in the pre-reform period and not in the post-reform period. Furthermore, we find no difference in the number of observations around the cutoff in the density figure, see Figure A.19. Figures A.14-A.18 give the relation between age and the outcome variables by individual year. Figure A.14 shows the emergence of the discontinuity in 21 for the NEETs rate on welfare, which then becomes 22

23 smaller in 211 and 212. Figure A.15 shows the opposite effect for the NEETs rate not on welfare. There are no apparent changes in the relation between age and the total NEETs rate, the employment rate and the enrollment rate in education, see Figures A.16-A.18. Table A.1 confirms this using regressions, where only the drop in the NEETs rate on welfare in 21 is statistically significantly different (at the 5% level). Table A.11 and A.12 shows that we obtain similar results for the difference in discontinuity setup when using quarter of birth or year of birth instead of month of birth, although the coefficients become statistically insignificant. Table A.13 and A.14 show that we also get similar results when we use an age range of or instead. Table A.15 shows somewhat larger effects in regions with high unemployment which is in line with the DD results. Finally, table A.16 shows no significant effect on the probability of being an adult child living at home, consistent with the DD analysis, and Table A.17 again suggests a somewhat larger effect for the subgroup of adult children living at home, again consistent with the DD analysis. 6 Conclusion In this paper we have studied the labour market effects of a Dutch mandatory activation program for individuals up to 26 years of age in The Netherlands. We used differences-in-differences and regression discontinuity, and a long and rich administrative data set to uncover the effect of the WIJ reform on the NEETs rate on welfare, the NEETs rate not on welfare, the total NEETs rate, the employment rate and the enrollment rate in education. We find that the reform did not reduce the total NEETs rate, but the number of NEETS on welfare dropped with a substantial 24% relative to the pre-reform year 29. Furthermore, the reform did not affect the employment rate and the enrollment rate in education. We also find that the effects are somewhat bigger for adult children living at home. These results are robust across the different methods we use. Our results are partly at odds with previous studies on mandatory activation programs (Blundell et al., 24; Persson and Vikman, 21; Hernæs et al., 216). Consistent with previous studies, we find a substantial negative effect on the young individuals on welfare. However, contrary to previous studies, we do not find a statistically significant effect on the employment rate or the enrollment rate in edu- 23

24 cation. A plausible explanation for this difference is the fact that the reform clashed head on with the Great Recession. The Great Recession made it more difficult for individuals, especially young individuals, to find a job. This would suggest that mandatory activation programs are less effective in stimulating employment (and education) during a recession, and other policy measures (perhaps oriented more towards the demand side) might be more effective. References Angrist, J. and Pischke, J. (29). Mostly Harmless Econometrics. Princeton University Press, Princeton. Bell, D. and Blanchflower, D. (211). Young people and the Great Recession. Oxford Review of Economic Policy, 27(2): Bertrand, M., Duflo, E., and Mullainathan, S. (24). How much should we trust differences-in-differences estimates? Quarterly Journal of Economics, 119(1): Blundell, R., Dias, M. C., Meghir, C., and Reenen, J. (24). Evaluating the employment impact of a mandatory job search program. Journal of the European economic association, 2(4): Board of Amsterdam (28). Wijziging beleidsregels re-integratieverordening wwb: stagebeleid wet werk en bijstand. Amsterdam. Bolhaar, J., Ketel, N., and Van der Klaauw, B. (216). Job-search periods for welfare applicants: Evidence from a randomized experiment. CEPR Discussion Paper No. DP11165, London. Carcillo, S., Fernández, R., and Königs, S. (215). Neet youth in the aftermath of the crisis: Challenges and policies. OECD Social, Employment and Migration Working Papers, No. 164, OECD Publishing, Paris. Dahlberg, M., Johansson, K., and Mörk, E. (29). On mandatory activation of welfare recipients. IZA Discussion Paper No. 3947, Bonn. 24

25 Donald, S. and Lang, K. (27). Inference with difference-in-differences and other panel data. Review of Economics and Statistics, 89(2): Dorsett, R. (26). The new deal for young people: effect on the labour market status of young men. Labour Economics, 13(3): European Commission (216). The youth guarantee and youth employment initiative three years on. Brussels. Hernæs, Ø., Markussen, S., and Roed, K. (216). Can welfare conditionality combat high school dropout? IZA Discussion Paper No. 9644, Bonn. Imbens, G. and Wooldridge, J. (29). Recent developments in the econometrics of program evaluation. Journal of Economic Literature, 47:5 85. Kluve, J. (214). Youth labor market interventions. IZA World of labor 214:16, Bonn. Leenheer, J., Adriaens, H., and Mulder, J. (211). Evaluatie wet investren in jongeren. CentERdata Tilburg. Ministry of Social Affairs and Employment (28). Bevordering duurzame arbeidsinschakeling jongeren tot 27 jaar (wet investeren in jongeren). Persson, A. and Vikman, U. (21). Dynamic effects of mandatory activation of welfare participants. IFAU Working Paper 21:6, Uppsala. Statistics Netherlands (215). Documentatierapport Arbeidsmarktpanel Technical report, Statistics Netherlands, Leidschenveen. Wilkinson, D. (23). New deal for young people: evaluation of unemployment flows. Policy Studies Institute, Research Discussion Paper, 15, Westminster. 25