Abstract
We use administrative data to examine the effect of a 50 percent benefit cut for young unemployed claimants in Ireland during the Great Recession. Because the cut applied only to new spells, claimants whose unemployment start dates differed by one day received very different benefits; we exploit this feature in a regression discontinuity analysis. We find that the benefit cut significantly reduced unemployment duration, with exits to training and work accounting for the majority of this effect.
I. Introduction
While no age group was spared the effects of the Great Recession, younger workers were hardest hit, with unemployment rates for 15–25-year-olds exceeding 30 percent in some OECD countries (van Ours 2015). There is strong evidence that unemployment when young has particularly adverse long-run effects, especially for disadvantaged youths (Bell and Blanchflower 2011). As a result, policies aimed at tackling youth unemployment have become a key priority of policymakers in recent years, and reforms of the unemployment benefit system have been prominent in these discussions (OECD 2010).
In this study, we examine the labor market responses of 18- and 19-year-olds to a substantial reform of unemployment assistance in Ireland during the Great Recession. For those affected, weekly benefits were cut from €204.30 to €100 (approximately US$237–US$116). To evaluate this reform, we exploit the fact that only new claimants were subject to the cut, which meant that people whose unemployment start dates differed by a matter of days were entitled to very different benefit rates.
To carry out the analysis, we use administrative data on welfare duration covering every new unemployment claim initiated between 2007 and 2014. These data provide the start and end dates of all unemployment spells commencing during this eight-year period. To identify the causal effect of the benefit cut, we use a regression discontinuity (RD) approach. The ability to combine the clean quasi-experimental nature of a substantial intervention with rich administrative data on the entire population of claimants provides a unique opportunity to identify the impact of benefit cuts on young people during a major recession.
For 18-year-olds, we find that the cut in benefits reduced average unemployment duration by more than a year, implying a significant duration elasticity with respect to the benefit rate of 1.08. The corresponding elasticity for 19-year-olds is somewhat smaller at 0.83. We provide evidence that differences in the potential duration of exposure to the cut explain the lower elasticity for 19-year-olds. The design of the cut was such that benefits were restored to the higher level once claimants reached 20 years of age. We exploit variation in month of birth to examine this and find that the impact of the benefit cut is smaller for those entering unemployment closer to their 20th birthday. We also consider the destination states of those exiting unemployment, and find that exits to both training and work are important components of the reduced durations. When we examine long-run effects, the results are mixed, with some evidence of beneficial effects for 18-year-olds but not for 19-year-olds.
These results have potential implications for benefit policy in many countries. As in several unemployment benefit systems, the Irish regime has two tiers: Jobseekers Benefit (JB) and Jobseekers Allowance (JA). The JB is a contribution-based unemployment insurance (UI) payment provided for up to nine months, whereas JA is an open-ended unemployment assistance (UA) payment paid to those who have exhausted JB or who have not accumulated sufficient contributions to be eligible for it. Similar two-tier benefit systems operate in the UK and Finland, while other countries, including Australia and New Zealand, have benefit systems that consist of the UA payment only. Despite the prevalence of UA systems, there has been little work examining the impact of changes to UA rates on unemployment duration. Walsh (2015) provides an initial evaluation of the benefit cut that we analyze. In contrast to our analysis, he has to rely on survey data that do not allow him to follow claimants over a spell, nor to directly identify claimants who were subject to the cut. Although Walsh finds no evidence of a higher rate of transition from unemployment to employment for those affected by the benefit cut, he is careful to say that the results are suggestive rather than definitive, given the limitations of the data available at that time.
While our paper is one of the first to examine the impact of UA rates on unemployment duration, we also regard the behavioral responses found in our analysis as relevant to the literature on UI. Although JA is open ended and does not require insurance contributions, in other respects it has much in common with JB. The full rates of payment of JA and JB are the same, and recipients must satisfy identical work search requirements. Moreover, although JA is means-tested, this has little bite in practice,1 so that unlike social assistance (SA), it is not specifically targeted at low-income families. It is therefore interesting to consider our results in the context of previous work on the effect of UI rates on unemployment duration. This work is summarized in surveys by Krueger and Meyer (2002), Tatsiramos and Van Ours (2014), and Schmieder and von Wachter (2016). Most of the papers cited report estimates of between 0.3 and 1.0 for the elasticity of duration with respect to UI benefit levels.
The fact that our results refer to benefit changes during a major recession provides additional policy relevance. Another paper covering the same period is Card et al. (2015), which examines the responsiveness of unemployment duration to benefit changes in the state of Missouri from 2003–2013. They find that unemployment durations became more responsive to benefit levels during the Great Recession, with an elasticity of between 0.65 and 0.9 during the recession compared to about 0.35 prerecession. The paper closest to ours is Rebollo-Sanz and Rodríguez-Planas (2020), which examines the impact of a reduction in the replacement rate in Spain in 2012. They find that the reform reduces mean unemployment duration by 5.7 weeks, implying an elasticity of 0.86. The Spanish reform differs from ours, however, in that the benefit cut only took effect after 180 days of unemployment.
Our analysis is also related, albeit to a lesser extent, to the literature on SA and labor supply. Bargain and Doorley (2011) exploit an age threshold in payments to study the effect of a French income maintenance payment on unemployment. They find significant effects for single unskilled men, with employment rates falling by seven to ten percentage points at the age threshold, but no significant effect for higher-skilled men. Fortin, Lacroix, and Drolet (2004) and Lemieux and Milligan (2008) also exploit age variation in SA eligibility to examine its effect on labor supply in Quebec. Fortin, Lacroix, and Drolet (2004) find significant results for those aged 22–29, with a duration elasticity of about 0.25, while the effect for 18–21-year-olds is not statistically significant. Lemieux and Milligan (2008) find that entitlement to the benefit reduces the probability of employment by three to five percentage points.2
We begin in the next section with a discussion of the policy change evaluated in our paper. Section III discusses the econometric specification and identification assumptions used in our analysis, and Section IV describes our data in more detail. Our main results are presented in Section V. In Section VI we examine the relative importance of alternative destination states in explaining our overall result and provide a competing risks decomposition of the total effect. In Section VII we examine the long-run effects of the benefit cut. Section VIII concludes our analysis.
II. The Irish Welfare System in the Great Recession
Ireland was one of the countries worst affected by the Great Recession (Ball 2014), with the unemployment rate rising from 4.7 percent in 2007 to 12.0 percent in 2009 and peaking at 14.7 percent in 2012.3 Youth unemployment rose from 9.1 percent in 2007 to 30.4 percent in 2012. The effects of the financial crisis felt elsewhere were compounded in Ireland by the bursting of a property bubble and the near collapse of the banking system. A combination of falling tax revenue from the construction sector and a decision to guarantee all bank liabilities resulted in the government being unable to borrow on international financial markets, which led to the introduction of severe austerity measures.4
In this paper we evaluate one such measure, a substantial reduction in JA paid to younger claimants. JA is by far the most prevalent unemployment payment to 18- and 19-year-olds, accounting for 94 percent of such payments in 2009. Prior to the benefit cut examined in this paper, all JA claimants were paid a basic rate of €204.30 a week. On April 29, 2009 claimants aged 18 and 19 had their weekly rate cut to €100.5 The stated rationale for the cut given by the government was to “ensure that young people are better off in education, employment, or training than claiming.”6 However, the necessity of cutting spending in order to reduce the government deficit also played an important role in the timing of the cut. Given that total spending on JA accounted for 3.25 percent of total public expenditure in 2009, reductions in JA had the potential to generate significant savings to the exchequer.
The cut only applied to claimants who entered unemployment after the date of the legislation, with claimants entering prior to the legislation remaining on the old rate. As a result, people whose unemployment start dates differed by a matter of days were subject to very different benefit rates. We exploit this feature of the legislation in order to identify the impact of the benefit cut.
In addition to exemptions for existing claimants, new claimants were exempted from the cut if they had a dependent child, if they had had a spell of unemployment in the previous 12 months, or if they were transferring from Disability Allowance. Given the nature of these conditions, the proportion of eligible claimants exempted from the benefit cut differed between the 18- and 19-year-olds. Moreover, the duration of the cut also differed between these age groups, as the benefit was restored to the full rate at age 20. We account for these features in our econometric analysis.
The benefit change for 18- and 19-year-olds was first announced as part of an emergency budget introduced on April 7, 2009, and the legislation putting it into effect was passed three weeks later on April 29. Because there was no discussion of the cut prior to the budget,7 and the legislation was enacted so soon after its announcement, there was little opportunity for strategic behavior. We examine this formally in Section V.
The cut in benefits outlined above is very large relative to many of those examined in previous research. For example, Carling, Holmlund, and Vejsiu (2001) examine benefit cuts of the order of 6 percent, Hunt (1995) considers cuts of 3–7 percent, and the cut analyzed in Rebollo-Sanz and Rodríguez-Planas (2020) amounted to a 17 percent reduction in the replacement rate. The cut of 51 percent implemented in Ireland during the Great Recession is much larger. The restriction of the cut to new entrants provides the quasi-experimental variation in JA rates that we exploit in order to establish the causal effect of benefits on unemployment.
III. Econometric Specification
Regression discontinuity is a well-established approach for identifying causal effects in economics (see Imbens and Lemieux 2008). In this framework, assignment to the treatment is determined either completely (sharp RD) or partly (fuzzy RD) by the value of a predictor or running variable (S) being on either side of a fixed threshold (s0). With a sharp RD design, unit i is assigned to the control group if Si < s0 and to the treatment group if Si ≥ s0. In this case, receipt of treatment is a deterministic function of the running variable. Where the running variable causes a discontinuity in the probability of receiving the treatment rather than a deterministic switch, a fuzzy RD approach is required. In this case, the running variable acts as an instrumental variable for treatment status, and the estimator is a Wald estimator in which the estimated discontinuity in outcomes at s0 is divided by the corresponding discontinuity in the probability of treatment.
The RD approach estimates the average treatment effect at the threshold:
1
where Y(1) and Y(0) denote the potential unemployment durations associated with and without treatment respectively. Following much of the literature (for example, Gelman and Imbens 2019), we estimate a using kernel-based local linear regressions on either side of the threshold.
In choosing the bandwidth for the local linear regression, there is a trade-off between bias and efficiency. In our analysis, we follow the literature in choosing a triangular kernel and the mean squared error optimal bandwidth suggested by Calonico, Cattaneo, and Titiunik (2014). We also examine the sensitivity of our results to alternative bandwidths and kernels.
The RD estimation is facilitated by two key features of our data set that make it ideal for our analysis. First, we have access to the population of claimants, resulting in a large number of observations. Second, we know the exact start date of every claim, which allows us to specify the running variable in days rather than in weeks or months. As noted by Lee and Card (2008), this can substantially reduce specification error compared to cases in which the running variable is only available in coarse intervals.
IV. Data
To carry out our analysis, we use the Jobseekers Longitudinal Database provided by the Department of Employment Affairs and Social Protection (DEASP), the government department responsible for the benefit system. This is an administrative data set that includes every claimant who received an unemployment payment from 2004.
The availability of both age and the start date of the spell allows us to identify whether an individual was in the group targeted by the benefit cut. As discussed earlier, some individuals, such as claimants with dependent children, were exempt from the benefit cut. Crucially, the data set includes an indicator of whether or not a claimant was actually subject to the cut.
For claims that have ended, we can identify the destination state, allowing us to consider competing risk explanations of our findings. We also have information on an individual’s gender, nationality, and unemployment history. In addition, the DEASP has collated some data on education, which allows us to construct an indicator of whether the claimant completed second-level schooling. We also have administrative data on annual earnings and weeks worked, taken from tax returns submitted by employers, for every year in which the individual worked.
The JA claimants in Ireland consist of two groups: those who exhaust their JB insurance and those not eligible for JB. We focus only on those who enter JA directly and exclude those who transition from JB. However, given the age groups we are analyzing, this restriction has little bite. Very few 18- and 19-year-olds have built up sufficient contributions to be eligible for JB, so the vast majority (96 percent) of these JA claimants are direct entrants.
We use data on the 17,379 claims that started six months before and after the reform to calculate bandwidths for the RD estimation procedure. Effective sample sizes, which take into account the bandwidths used, are reported in the tables alongside the main RD results.
Table 1 provides summary statistics for these data, by age and treatment status. For both age groups, about 94 percent of claimants have Irish nationality. The variable labeled “low education” denotes that the claimant did not complete second-level education. In the Irish system, approximately 15 percent of recent cohorts of school leavers do not complete second-level education. The figures in Table 1 show that for our sample of JA claimants, this number is much higher, indicating that, as expected, JA claimants are less educated than their peers. The variable labeled “no previous employment spell” denotes that the claimant had never worked prior to the unemployment spell of interest. As anticipated, the proportion with no prior work experience is higher for 18-year-olds than for 19-year-olds. The fact that those who enter unemployment later in 2009 are somewhat better educated and are more likely to have had no previous employment spell reflects both seasonal effects and the deterioration in the labor market during that year. However, as we will show later, these differences are not evident at the RD threshold and therefore do not affect the validity of the RD design. The proportion of claimants who are male ranges from 0.58 for the 19-year-old treatment group to 0.66 for the 18-year-old control group.
The treatment status variable indicates whether the claimant was subject to the legislated benefit cut. A substantial majority of 18-year-old claimants were subject to the cut. The proportion affected is lower for 19-year-olds because, as discussed earlier, older claimants are more likely to qualify for the exemptions specified in the legislation. The table also indicates that a small number of people are recorded as having their benefit cut before the legislation came into effect. This appears to be due to short delays in processing claims. Finally, the table shows the average spell duration for both groups. The length of unemployment spells during this period is notable, with an average unemployment duration of between 18 months and two years. This reflects the depressed nature of the Irish labor market at this time. It is also noteworthy that, for both age groups, average durations were shorter for those entering after the legislation, suggesting a potential effect of the cut. In the remainder of the paper, we examine whether these differences in duration represent causal effects.
V. Results
A. Main Results
Initial results for the RD analysis are shown in Figure 1 for 18- and 19-year-olds. These graphs provide a visual description of the RD design prior to the more formal analysis outlined in Section III. The figures show regression discontinuity plots for both ages, where the running variable is days before or after the introduction of the benefit cut.
Regression Discontinuity Graphs. Proportion Treated (Left) and Average Unemployment Duration (Right) for Entrants to Unemployment Six Months before and after April 29, 2009
Each panel consists of two graphs. The graphs on the left are regression discontinuity plots of treatment status, where the treatment variable takes the value one if a claimant was subject to the legislated cut and zero otherwise. The points represent the proportion treated within each of 50 equally spaced bins on either side of the threshold. We also show estimates of global fourth-order polynomials fitted to these data. These higher-order polynomials are simply an exploratory visual aid; the statistical inference conducted later follows recommended procedures, estimating the discontinuity using local linear regressions. The vertical lines on the graphs indicate the RD threshold given by the date of the legislation, April 29, 2009. Examination of these graphs allows us to explore the bite of the legislation, which provides the basis for the denominator of the fuzzy RD estimator described in Section III. The graphs on the right present RD plots of unemployment duration, with each point now representing average duration within a bin. These graphs illustrate the change in unemployment duration upon introduction of the legislation and provide the basis for the estimated numerator of the fuzzy RD estimator.
Looking first at the RD plots for treatment status, we see clear evidence of a discontinuity at the threshold for both age groups. The graphs suggest that the likelihood of treatment increased by between 60 and 70 percentage points for 18-year-olds and by about 40 percentage points for 19-year-olds. The differential bite of the treatments is taken into account in the fuzzy RD analysis, so that the estimates of all treatment effects are consistent. However, it should be noted that the weaker bite of the cut for 19-year-olds makes precise estimation of the effects for this group more difficult.
Turning to the RD plots for unemployment duration, we see that for both 18- and 19-year-olds, unemployment duration fell substantially when benefits were cut, with the effect particularly pronounced for 18-year-olds. For this group, the graph suggests a reduction in unemployment duration of about 40 weeks at the threshold.
While the RD graphs provide a useful visual presentation of the RD design, a more formal analysis is needed to establish the statistical significance of the causal effects. The results of this analysis are given in Table 2. When estimating these effects, we follow the recent literature, estimating local linear regressions to the left and right of the threshold and reporting the results for the optimal bandwidth proposed by Calonico, Cattaneo, and Titiunik (2014). For our data the optimal bandwidths are 48 days for 18-year-olds and 52 days for 19-year-olds.
The first row of Table 2 provides the estimated effect of the legislation on the likelihood of receiving a benefit. The second row provides the fuzzy RD estimates of the causal effect of the benefit cut on unemployment duration, which confirm the results of the RD graphs. There is evidence of a strong negative effect for both 18-and 19-year-olds, with unemployment durations falling by 61 weeks and 38 weeks, respectively. However, only the 18-year-old effect is statistically significant.
To check the sensitivity of our results to the choice of bandwidth, we reestimate the models using twice and half the optimal bandwidths. The results for these alternatives are given in the Panel B of Table 2. The results for 18-year-olds are very robust, with neither the point estimates nor the standard errors varying substantially across bandwidths. The results for 19-year-olds are somewhat more sensitive to the choice of bandwidth, so that the conclusion that the effect for 19-year-olds is statistically insignificant is less clear-cut.8
Panel C of Table 2 examines the sensitivity of our results to alternative kernels, namely a rectangular kernel and an Epanechnikov kernel. Once again our key findings are robust to this choice.
We can use the RD results to estimate a benefit duration elasticity for both groups. These are reported in the last row of Table 2. The fall in duration combined with the reduction in benefits imply elasticities of 1.08 and 0.83 for 18- and 19-year-olds, respectively. These estimates are consistent with the range reported in the UI literature.
As noted above, the difference between 18- and 19-year-olds may reflect differences in the relative bite of the treatment across the two groups. However, it may also reflect differences in behavior. The design of the benefit cut analyzed here was such that it applied only to 18- and 19-year-olds, with benefits restored to the higher level once claimants reached their 20th birthday. The fact that benefits would be restored sooner for 19-year-olds may explain the smaller effect of the benefit cut reported for this group. To consider this, we use the availability of data on month of birth to examine the average duration of unemployment for the treatment and control groups separately by detailed age categories. For each group, claimants are divided into 20 equally-sized bins based on their age at the start of their claim.
The results are shown in Figure 2, which plots the average duration of unemployment in each of the bins, together with 95 percent confidence intervals. The results for those entering unemployment in 2008, when there was no benefit cut, are in the left-hand panel and the results for those entering in 2009 are in the right-hand panel. Looking at the results for 2008, we see, as expected, no difference between the treatment and control groups in any of the age bins considered. On the other hand, in 2009, there is a statistically significant difference in average duration between treatment and control groups for all 18-year-olds and for all 19-year-olds up to 19.5 years of age. After this point, however, the confidence intervals overlap, implying no significant difference between treatment and control groups.
Notes: For 2008, treatment status is determined by whether entry to unemployment occurred before (control) or after (treatment) April 29, 2008.
The fact that the benefit effect is weaker for claimants who turn 20 earlier in their unemployment spell helps explains the difference between our results for 18- and 19-year-olds. The finding that a benefit cut, if perceived as temporary, has little effect on incentives has implications for the design of benefit sanctions; short-lived sanctions are unlikely to have strong effects.
There is some evidence in the literature that the labor market response to a benefit change may differ between men and women (Røed and Zhang 2003). This may be particularly important in our case, as new claimants were exempt from treatment if they had a dependent child, which is more likely to apply to women than men. To consider this issue we repeat the analysis separately for men and women. The results are given in Table 3. Panel A shows that, for this group of young claimants, there is little difference in the proportion treated by gender. The treatment effects reported in the second row indicate that, although slightly smaller for women, the estimated effects are large for both genders. As before, the significance of the 18-year-old results is robust across bandwidths for both men and women, while the insignificance of the 19-year-old results is less clear-cut.
B. Robustness Checks
We carry out a number of robustness checks to examine the validity of the RD design assumptions. The first repeats the analysis for dates at which there is no treatment. If the identification strategy is valid, we should observe no effect at other dates. A second check uses the fact that neither JB claimants nor 20-year-old JA claimants were subject to the benefit cut; therefore, we should see no significant effect at the threshold for these groups. Finally, we examine the impact of covariates for our findings, both by repeating the analysis conditioning on covariates and also by using covariates themselves as pseudo-outcomes.
For the first robustness check, we conduct a permutation test for each group, following Johnston and Mas (2018). This involves estimating a placebo treatment effect at all dates between April 1, 2008 and May 1, 2010. The distributions of the resulting 761 estimated treatment effects for 18- and 19-year-olds are shown in Figure 3, Panels A and B, respectively. For 18-year-olds, only two of the 761 dates give a bigger effect than the true treatment date of April 29, 2009. For 19-year-olds, 6 percent of alternative dates yielded bigger treatment effects than that estimated at the true threshold. These permutation tests thus indicate that our estimated treatment effects are unlikely to be chance occurrences.
Permutation Test for RD Threshold: Distribution of Estimated Benefit Effects Using All Dates Between April 1, 2008 and May 1, 2010 as the RD Threshold, 18-Year-Olds (Left) and 19-Year-Olds (Right)
The RD plots for the population of 18- and 19-year-old JB claimants in 2009 are given in the two panels of Figure 4. We see little evidence of a discontinuity in unemployment durations at the threshold. In contrast to the significant negative results for JA claimants, the estimated effect for 18-year-old JB claimants is positive. The point estimate for this group is 25.95, which is significant at the 5 percent level. However, this effect is not robust to alternative bandwidths; at twice the optimal bandwidth, the point estimate falls to 11.86, and the p-value increases to 0.15. The estimated effect for 19-year-old JB claimants is very small in magnitude and statistically insignificant; the point estimate using the optimal bandwidth is −1.71, with a p-value of 0.75. A separate analysis for 20-year-old JA claimants finds that the RD effect is neither economically nor statistically significant; the point estimate and corresponding p-value are 5.33 and 0.71, respectively. The absence of a noticeable effect for young JB claimants or 20-year-old JA claimants supports the view that the JA effects we have estimated are causal and not the result of contemporaneous labor market shocks affecting all young claimants.
Regression Discontinuity Graph of Average Unemployment Duration, 18-Year-Old (Left) and 19-Year-Old (Right) Entrants to Unemployment Six Months before and after April 29, 2009 for JB Claimants
Covariates can also play a useful role in assessing the plausibility of any RD design (Athey and Imbens 2017). First, we examine the validity of the RD identification strategy directly by examining whether the covariates are correlated with the treatment when the running variable is near the threshold. To examine this, we follow previous work and repeat the RD analysis using covariates as pseudo-outcomes. A discontinuity in a covariate at the threshold would cast doubt on the validity of the RD approach. The results from this analysis are given in Table 4. All the coefficients are small and statistically insignificant, providing no evidence of a discontinuity in any of the covariates for either 18- or 19-year-olds.
Fuzzy Regression Discontinuity Results for the Effect of Treatment on Claimant Characteristics. Standard Errors in Parentheses
Next we follow Calonico et al. (2019) and consider the impact of controlling for covariates. In particular we include nationality, previous employment, and gender in the estimated model. The results are given in Table 5. For ease of comparison we reproduce the results from Table 2 in the first and third columns.9 The similarity of the results with and without covariates shows that our key findings are not driven by compositional changes.10 These robustness checks all support the identifying assumptions underlying our RD estimation.11
C. Spillover Effects
As noted by Lalive, Landais, and Zweimüller (2015), the presence of spillovers can affect the estimation of benefit changes; with a fixed number of jobs in the economy, the reduced durations for claimants in the treatment group may be at the expense of longer durations for those in the control group. Lalive, Landais, and Zweimüller (2015) label such an effect the “rat race” effect. To examine this in our setting requires considering the extent to which the fall in unemployment durations for those affected by the benefit cut was accompanied by an increase in durations for those still in receipt of the higher benefit. Since the control group in our RD approach consists of 18-year-olds starting a spell just prior to the legislated cut on April 29, 2009, one possibility would be to compare the durations of this group to the durations for 18-year-old claimants entering unemployment during the same period a year earlier. These claimants are less likely to be affected by spillovers, as many will have completed their spell prior to the benefit cut. Since a comparison of 18-year-old claimants in 2008 and 2009 may also be affected by changing macroeconomic circumstances, we control for this by subtracting the corresponding change in duration for 25-year-olds. This latter group is less likely to be in direct competition for jobs with 18-year-olds and therefore not subject to spillover effects, but they are likely to experience similar macroeconomic shocks. In particular we estimate a simple difference-in-difference regression model
2
Age 18i is a dummy variable indicating that the claimant is aged 18 rather than 25 and D2009,i is a dummy variable indicating entry into unemployment in 2009. The parameter of interest is φ, which measures the change in the duration for 18-year-olds entering in February, March, or April 2009 as a result of the benefit cut introduced on April 29, 2009.
The results, which are given in Table 6, show no economically or statistically significant change in durations for 18-year-olds entering just prior to the benefit cut. There is no evidence that unemployment durations increased for those in our RD control group when the benefit cut was introduced.12
D. Effects at the Extensive Margin
As mentioned, one of the stated aims of the benefit cut was to ensure that young people were better off in education than in unemployment. Accordingly, it is possible that the benefit cut had an effect at the extensive margin, reducing the numbers entering unemployment by encouraging young people to stay in school. Such effects would not be picked up in the earlier duration analysis. An additional concern affecting the extensive margin is the possibility of anticipation effects; these occur when individuals initiate claims earlier than otherwise to avoid announced benefit cuts that have not yet taken effect. Given the short time period between announcement and enactment of the legislation discussed in this paper, we believe that the scope for anticipation effects is limited.
To consider effects at the extensive margin, we adjust the RD design used above, and check for discontinuities in the density of the running variable itself. If young people remained in education for longer following the reduction in benefits, we would expect fewer entries to unemployment to the right of the threshold. On the other hand, if people changed behavior in anticipation of the benefit cut, we would expect more entries to the left of the threshold. Either of these would give rise to a discontinuous fall in the density of entries to unemployment at the threshold. The estimated densities for 18- and 19-year-olds are given in Figure 5. The points represent the proportion of all claimants entering unemployment in each bin. The estimated densities are clearly continuous at the threshold, with no statistically significant change following the benefit cut.13 This shows that the benefit cut had no additional effect on unemployment over and above its effect on the duration of spells reported earlier, and also that anticipation effects were not important. As an additional check for announcement effects, we conduct an RD analysis using the date on which the cut was announced (April 7) as the threshold, and find no effect; the point estimate is positive and statistically insignificant. These results again support the validity of the RD analysis in identifying causal effects.
Regression Discontinuity Graph of Density of Entries to Unemployment, 18-Year-Old (Left Panel) and 19-Year-Old (Right Panel) Entrants to Unemployment Six Months before and after April 29, 2009
VI. Competing Risks Analysis of Exit States
In Section V, we reported robust evidence of a substantial and significant effect on unemployment durations for 18-year-old claimants, with weaker evidence for 19-year-olds. Given the depressed nature of the labor market in 2009, it may have been easier for claimants to exit to training or inactivity than to find employment. Because alternative exit states will have different policy implications, it may be important to distinguish unemployment spells ending in work from those ending in nonemployment. Previous research has examined this directly by analyzing the duration of nonemployment spells rather than the duration of unemployment spells (Card, Chetty, and Weber 2007). We cannot adopt this approach because our data do not record the time spent in states other than unemployment. We can, however, identify the exit state, so we exploit this information to conduct a competing risks decomposition of the difference in mean unemployment duration between the treatment and control groups. The competing risks approach we propose differs from the cause-specific hazard function approach that is commonly used when examining unemployment hazards. While cause-specific hazards are useful when examining the rate of occurrence of an outcome in the subset of people who are event-free, they do not identify the absolute risk of a cause-specific outcome that is of interest in our analysis (Austin and Fine 2017; O’Neill 2019).
To examine competing risks we use a version of the decomposition developed by O’Neill (2019). The difference in average duration between the treatment and control groups is given by
3
where T indicates treatment group, and C denotes control group. In the case of three exit states denoted by 1, 2, and 3, where the proportion leaving into each of the three states for group i is given by fi1, fi2, and fi3, we can write the overall difference as
4
5
where NT and NC are the total number of claimants in the treatment and control groups, respectively, NTk and NCk refer to the number exiting to state k from these groups, and 
is the average duration for those in group i who exit to state k.
Suppose we observe spells over a period of D weeks. Then we can write 
as 
, where 
is the number exiting to state k from the treatment group in week d. The overall difference can then be rewritten as
6
The terms inside the curly brackets represent the contributions of each of the exit states to the overall difference in duration. O’Neill (2019) shows that these terms can be estimated using the cumulative incidence function for exit state k at duration d (Coviello and Boggess 2004; Kalbfleisch and Prentice 2002), which measures the absolute risk associated with each exit state in the presence of competing risks.
In our data, there are 22 recorded exit states. When carrying out the decomposition, we follow DEASP guidelines and aggregate these into four categories: work, education and training (hereafter referred to as simply training), inactivity, and other.14 The results of the decompositions for both 18- and 19-year-olds are given in Table 7. The first row presents an estimate of the overall treatment effect, calculated as the difference between the average duration of those entering unemployment in the month before the legislation and those entering in the month after, rescaled using the first stage treatment effects reported in Table 2. As before, we find substantial effects on the duration of unemployment, although the simple before–after estimates reported here are somewhat smaller than those produced using the RD approach.
The remaining four rows of Table 7 report the contributions of each of the exit states. Looking at the results, we see that all exit states contribute substantially to the overall effect, with exits to work being the most important state for both 18- and 19-year-olds.15 As discussed, the government’s stated motivation for the benefit cut was to ensure that training, education, and employment were preferable to unemployment. Our results confirm that these exit states did contribute to the overall reduction in unemployment durations.
VII. Long-Run Effects
We conclude our analysis by considering the long-run effects of the benefit cut. Recent evidence in the program evaluation literature indicates that the effects of active labor market programs are strongest in the long run (Card, Kluve, and Weber 2018). The same could be true for the effects of benefit cuts—if the shorter initial durations prevent human capital depreciation, then claimants will not only find jobs more quickly but will earn higher wages and remain in employment for longer. On the other hand, the long-run effects of benefit cuts could be weaker than the short-run effects if they force people to end their job search prematurely and move into low-paying, low-quality, transitory jobs. This could lead to substantial churning between states, weakening the long-run impact of the cuts. For those entering training schemes following benefit cuts, the long-run effects will also depend on the quality of these schemes.
We examine the impact of the 2009 benefit cut on outcomes in 2014, the last year for which new unemployment spells are recorded in our data. Using RD analysis, we consider three outcomes: whether the claimant had a spell of unemployment in 2014, the total time spent unemployed in 2014, and the weekly wages reported in 2014 for those with positive earnings. The results are given in Table 8. The first row presents the average outcomes for the control group and shows that the labor market experience of this group continued to be poor in 2014. The second row presents the effect of the benefit cut on the outcomes. The results for 18-year-olds show that the benefit cut in 2009 reduced the total time spent unemployed in 2014 by more than six weeks, reduced the likelihood of having an unemployment spell five years later by 11 percentage points, and increased average weekly wages in 2014 by €5.98, although only the first of these effects is statistically significant. None of the results are statistically significant for 19-year-olds. Overall these results provide some evidence of a long-run effect of the benefit cut on employment prospects but little evidence of any effect on job quality in terms of earnings.16,17
VIII. Conclusion
This paper evaluates the impact of an unusually large cut in benefits on unemployment duration during the Great Recession. While most existing studies focus on middle-aged workers, the reform we analyze affected only 18- and 19-year-olds, and thus provides evidence on the benefit responsiveness of very young labor market participants, a group that is of particular policy interest. Our analysis is facilitated by access to high-quality administrative data on the population of claimants and by the quasi-experimental nature of the benefit cut. The design of the benefit cut resulted in claimants whose unemployment start dates differed by one day receiving very different benefits.
We find that the benefit cut substantially reduced unemployment duration for 18-year-olds. For JA claimants in this age group, who are predominantly low educated and have little previous employment experience, we estimate a significant duration elasticity of 1.08. This implies a reduction in average unemployment duration of more than a year. We find a smaller and less precisely estimated elasticity for those aged 19. We provide evidence that the difference in results for the two age groups is due to the fact that 19-year-olds are closer to their 20th birthday, at which point benefits were restored.
Our results provide clear evidence of a labor supply response to lower unemployment benefits for young claimants, even during a recession. To examine the effects of the benefit cut in more detail, we decompose the overall effect into the components due to different exit states. The motivation for the benefit cut was to ensure that employment, education, or training were preferable to unemployment. Our results confirm that these exit states all contributed to the overall reduction in unemployment durations.
Although we find some evidence that the benefit cut improved employment prospects in the long term, there is little evidence of an impact on earnings in the long run. However, the effects of the benefit cut may have been more positive had it been introduced in better labor market conditions.
While we find a significant effect of the benefit cut on unemployment duration, it is possible that a benefit cut of this magnitude had negative consequences, reducing the ability to consumption smooth and increasing claimants’ dependence on family members. This in turn may have led to increased pressure on low-income families. For those without family support, there is anecdotal evidence of an increase in homelessness affecting those whose benefits were cut. Further research is needed on these negative effects, which, when combined with the large positive incentive effects found in our paper, would provide the evidence needed to determine the appropriate benefit rates for young people.
Footnotes
The authors thank Terry Corcoran (DEASP) for providing the data used in the analysis and for many useful discussions in relation to this research. They are also grateful to Tim Callan, Chris Jepsen, John Kennan, Attila Lindner, Paul Redmond, and participants at the Labour Market Council conference on program evaluation (Dublin), the 31st Irish Economic Association Conference (Dublin), the 22nd Society of Labor Economists Conference (North Carolina), the 5th NERI Annual Labour Market Conference (Maynooth), the 31st European Society for Population Economics Annual Conference (Glasgow), the 13th IZAWorkshop on Labor Market Policy Evaluation (Bonn), the 29th European Association of Labour Economists Conference (St.Gallen), and seminar participants at Maynooth University, Queens University Belfast, and the University of Limerick for helpful comments on an earlier version of this paper. This paper uses confidential administrative data provided by the Department of Employment Affairs and Social Protection in Ireland. Those interested can contact the DEASP (http://www.welfare.ie/en/Pages/contact-us_home.aspx) directly for the data. The authors are willing to assist (donal.oneill{at}mu.ie).
Supplementary materials are freely available online at: http://uwpress.wisc.edu/journals/journals/jhr-supplementary.html
↵1. For any family circumstances, the threshold beyond which payments are reduced is above average household earnings, and for households with typical housing costs, the threshold is around the 75th percentile.
↵2. A more extensive summary of the literature discussed in this section is provided in Table A1 of Online Appendix A.
↵3. For comparison, the corresponding figures for the OECD were 5.6, 8.1, and 7.9 percent.
↵4. Ireland subsequently required a rescue package from the Troika of the EU, ECB, and IMF, but the policy measures analyzed in this paper predate this 2010 agreement.
↵5. Between 2010 and 2013, there was also a series of other cuts for those aged 20–25. However, many of the eligible pool in these age groups were exempt from the benefit cut, making it difficult to identify an effect. In addition, all the later cuts came into effect at the beginning of the year so seasonal effects specific to the Christmas period further complicate identification. Therefore, we do not analyze these cuts here.
↵6. http://www.welfare.ie/en/pressoffice/Pages/pr231013.aspx (accessed October 18, 2019).
↵7. We carried out an online search of the national newspapers for the four months prior to the emergency budget. We did not find a single article mentioning impending cuts for any claimants in the run-up to the budget. The fact that benefits had been increased in the main budget in October, 2008, just six months previously, made the cut in the emergency budget all the more surprising.
↵8. We have also estimated the models using a range of bandwidths between one month and six months; these results are available in Table A2 of Online Appendix A. Our conclusions are not affected by varying the bandwidths within this range.
↵9. To ensure comparability, we use the same bandwidths in the models including and excluding covariates.
↵10. We also conducted this analysis controlling for education as an additional covariate. Because education is only available for 90 percent of claimants, this reduced our sample sizes. The results with and without controls for this smaller sample are given in Table A3 of Online Appendix A. Again, adding covariates makes almost no difference to the estimated effects.
↵11. We have also estimated a difference-in-difference hazard model. In keeping with the RD results, we find that the benefit cut had a large significant effect on 18-year-olds and a smaller insignificant effect on 19-year-olds. Details are available in Online Appendix B.
↵12. We have also repeated this analysis for those entering in the months May, June, and July. For 18-year-olds in 2009, this corresponds to treated workers in our RD analysis. In keeping with the main results from the RD analysis, we find large significant reductions in benefit durations for those subject to the benefit cut, which supports the identification strategy used in our spillover analysis.
↵13. The t-statistics for the McCrary (2008) test of the difference in the log density on either side of the threshold are −0.002 for 18-year-olds and 0.59 for 19-year-olds.
↵14. Many of those in the “other” category were recorded as “no reason stated.” Some of these claimants had earnings records that suggested that they had exited to work. We experimented by allocating these claimants into the work category, but this had little effect on the reported results.
↵15. Given the importance of exits to employment, we have also examined post-unemployment annual earnings. In Table C1 of Online Appendix C, we provide results from a difference-in-difference wage estimation that indicates that earnings of the treatment group do not differ significantly from those of the control group. This provides suggestive evidence that reservation wages were not affected by the benefit cut.
↵16. These conclusions are not sensitive to the use of wider bandwidths.
↵17. Lalive (2007); Card, Chetty, and Weber (2007); van Ours and Vodopivec (2008); and Schmieder, von Wachter, and Bender (2016) all examine extensions to the duration ofUI benefits directly and find little evidence that extended UI duration improve subsequent job match quality, while Nekoei and Weber (2017) find some evidence that UI extensions raised wages in Austria.
- Received May 2018.
- Accepted September 2018.
