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Keywords:

  • Offer rejection;
  • sanction;
  • search effort;
  • unemployment duration;
  • wage;
  • C21;
  • C41;
  • D83;
  • E65;
  • H75;
  • J30;
  • J31;
  • J44;
  • J62;
  • J64;
  • J65;
  • J68;
  • K42

Abstract

  1. Top of page
  2. Abstract
  3. I. Introduction
  4. II. Unemployment Insurance
  5. III. Theoretical Insights
  6. IV. Data
  7. V. Empirical Model
  8. VI. Results
  9. VII. Displaced Workers
  10. VIII. An Assessment of the Design of the Monitoring Policy
  11. IX. Conclusions
  12. References

Unemployment insurance systems include the monitoring of unemployed workers and punitive sanctions if job search requirements are violated. We analyze the causal effect of sanctions on the ensuing job quality, notably on wages and occupational level. We use Swedish data and estimate duration models dealing with selection on unobservables. We also develop a theoretical job search model that monitors job offer rejection versus job search effort. The empirical results show that, after a sanction, the wage rate is lower and individuals move more often to a part-time job and a lower occupational level, incurring human capital losses.

I. Introduction

  1. Top of page
  2. Abstract
  3. I. Introduction
  4. II. Unemployment Insurance
  5. III. Theoretical Insights
  6. IV. Data
  7. V. Empirical Model
  8. VI. Results
  9. VII. Displaced Workers
  10. VIII. An Assessment of the Design of the Monitoring Policy
  11. IX. Conclusions
  12. References

Unemployment insurance (UI) systems typically include the monitoring of unemployed workers and punitive sanctions for those who do not comply with job search requirements (for an overview, see, for example, OECD, 2000). Van den Berg et al. (2004) were the first to publish a study of the causal effect of a punitive sanction on the transition rate from unemployment to employment. Since then, a range of similar studies have been carried out for different countries and time periods (for overviews, see Van den Berg and Van der Klaauw, 2005, 2006). However, these studies do not consider the effect of a sanction on the type of job accepted. From a welfare point of view as well from the point of view of the unemployed individual, such effects are important. If the job accepted after a sanction is often worse than the job accepted in the counterfactual situation of no sanction, then severe sanctions and intensive monitoring adversely affect the individual beyond the time in unemployment. This relates to the more general issue of how steeply benefits should decline as a function of the elapsed unemployment duration, to balance moral hazard with the likelihood that unemployed individuals are driven into suboptimal job matches (e.g., Acemoglu and Shimer, 2000).

In this paper, we address the effects of sanctions on the quality of the job that is accepted. We distinguish between the effects on the wage and on working hours (specifically, full-time versus part-time). Wages and hours are potentially relevant margins along which unemployed individuals make job acceptance decisions. We use register data covering the full Swedish population over the period 1999–2004. This includes several hundreds of thousands of unemployment spells. The register data also include information on a large range of background characteristics of the individual, his/her household, and his/her local labor-market conditions. If a spell is observed to end in a transition to work, then in many cases we observe the above-mentioned job characteristics. Note that the observation of a wage rate is very unusual in register data on employment. Such data typically only record annual income or annual earnings, which are composite measures based on both wages and hours worked. Our data enable us to distinguish between the effects on wages and the effects on hours.

It can be argued that any adverse effects on characteristics of the first accepted job after unemployment fade away swiftly because individuals have the opportunity to search on the job and to make transitions to jobs with better characteristics. We investigate this by examining the individual labor-market outcomes that prevail several years after the sanction. Moreover, we examine to what extent the job acceptance decisions lead to irreversible skill losses. We observe the occupation of the accepted job, and we observe to what extent this differs from the occupation of the pre-unemployment job. On average, the acceptance of a job with a lower occupational level involves a larger loss of human capital than the acceptance of a job in the same occupation. This loss becomes irreversible as human capital depreciates over time. Therefore, it might be more difficult for the individual to move out of an adverse job match if the job has a lower occupational level. This makes it important to know whether sanctions often lead to a match in a lower occupational level. By measuring the required number of years of education for each occupation, we can quantify the human capital loss as a result of the occupational downgrading caused by a sanction. Because of the existence of separate educational tracks, this is likely to be a lower bound of the true loss.

The empirical analyses are based on the “Timing of Events” approach to the identification of treatment effects if the treatment is characterized by the moment in time at which it occurs (e.g., Abbring and Van den Berg, 2003). This takes into account the fact that treatment assignment can be selective in that the durations might be affected by related unobserved determinants. Note that “conditional independence” assumptions, stating that treatment and potential outcomes are independent conditional on observed individual characteristics, are almost certainly invalid if the treatment is punitive. This is because individuals can only logically display inadmissible behavior if this behavior or its determinants are not directly observable in registers used by the monitoring agency. By including post-duration outcomes, such as post-unemployment wages, it becomes a necessity to deal with dynamic selection because of unobserved heterogeneity, even if the assignment is randomized (see Ham and LaLonde, 1996; Abbring and Van den Berg, 2005).

We make some additional contributions. To introduce these, we point out that in the Swedish UI monitoring system, after inflow into UI, monitoring focuses exclusively on job offer decisions, in the sense that unemployed individuals are not supposed to reject suitable job offers. This contrasts with the monitoring carried out in other countries, which typically focuses on search effort, as measured by the number of applications sent out or by indicators of the willingness to adhere to guidelines on search effort. The monitoring of offer decisions increases the relevance of studying the effects on job quality, because rejected offers concern jobs with a low job quality. In this paper, we develop and analyze a theoretical job search model with monitoring of job offer rejection decisions in the presence of wage variation. The theoretical predictions can be contrasted with those from a model with monitoring of job search effort or search intensity. We find a number of qualitative differences. Our estimation results can be understood in the light of this theoretical model framework. In effect, the theoretical analysis provides a contribution to our policy recommendations.

Our study focuses extensively on the behavior and outcomes of displaced workers. The stereotypical displaced worker has worked for a long time in a manufacturing job with skills that are highly job-specific, before becoming unemployed because of a mass lay-off or plant closure. As argued by Ljungqvist and Sargent (1997), such workers are likely to become long-term unemployed. Upon entry to unemployment, they might overestimate the market value of their skills and therefore reject a suboptimally large number of job offers. Generous UI benefits exacerbate this, until the point in time where their skills have become fully obsolete; see Pavoni (2009) for an analysis of optimal UI with skill depreciation during unemployment. It has been argued that a sanction can act as a “wake-up call” for displaced workers, signaling that they have misperceived their chances in the labor market, and inducing them to accept low wage offers (e.g., Department of Health and Human Services, 1999). We formalize this line of reasoning within the setting of our theoretical job search model, and we examine to what extent our empirical model specification can capture this. The wake-up call hypothesis is an alternative explanation for the main empirical results if the displacement status is not properly controlled for. Therefore, we estimate models that condition on displacement status, using a range of displacement indicators. For this, we extend our dataset by adding a matched employer–employee register, enabling us to observe pre-unemployment conditions at the establishment level. We also examine how strongly represented the displaced workers are among the sanctioned.

In a parallel paper, Arni et al. (2013) use Swiss data to study effects of UI benefit sanctions on post-unemployment earnings. They do not distinguish between wages and hours worked, and they do not consider how sanctions affect the occupational level. Other differences are that we focus on effects by displacement status and that we integrate the empirical analysis into a theoretical analysis of monitoring systems.

The outline of the paper is as follows. In Section 'Unemployment Insurance', we present the institutional setting. We discuss the Swedish UI system and the role of monitoring and sanctions in that system. In Section 'Theoretical Insights', we provide the theoretical job search framework and derive theoretical predictions. In Section 'Data', we describe the data and consider an attempt to reform the monitoring policy. In Section 'Empirical Model', we discuss the empirical approach. Note that we observe the full population, while only a small fraction is sanctioned. Therefore, we estimate the models with endogenously stratified samples, using weighted exogenous sampling maximum likelihood (WESML). In Section 'Results', we present the empirical results, and in Section 'Displaced Workers', we consider the extent to which the displacement status of unemployed individuals determines the results. We conclude in Section 'An Assessment of the Design of the Monitoring Policy'.

II. Unemployment Insurance

  1. Top of page
  2. Abstract
  3. I. Introduction
  4. II. Unemployment Insurance
  5. III. Theoretical Insights
  6. IV. Data
  7. V. Empirical Model
  8. VI. Results
  9. VII. Displaced Workers
  10. VIII. An Assessment of the Design of the Monitoring Policy
  11. IX. Conclusions
  12. References

Unemployment Insurance Entitlement

A newly unemployed individual in Sweden is entitled to UI benefits if a range of conditions are fulfilled. First, the individual must have been member of a UI fund for at least 12 months and should have had a job for at least six months in the past 12 months. Second, he needs to be registered at the public employment service (PES) and has to be able and willing to work at least three hours a day and at least 17 hours per week. Further, he must state that he is actively searching for employment.

Those who fulfill these conditions are entitled to UI benefits. In our observation window, these amounted to 80 percent of the average earnings during the latest six months of employment, with a floor and a ceiling. At the beginning of 2001, these were SEK 270 (≈ €25) and SEK 580 (≈ €55) per day. An individual who has not been a member of an UI fund for at least 12 months might qualify for the Unemployment Assistance (UA) system. Compensation in UA is unrelated to previous earnings and its generosity is much lower than UI. In our analysis, we restrict attention to UI recipients. To retain UI during a spell of unemployment, the individual needs to remain eligible.

In 2001, the maximum entitlement duration of UI benefits was 300 days for everyone. The benefits can be collected with or without interruptions. If the individual finds a job and retains it for six months, then he qualifies for a new entitlement period. The individual also continues to collect UI benefits while being enrolled in specific labor-market programs.1 UI benefits are mainly financed by proportional pay-roll taxes.

Monitoring and Sanctions

The monitoring of an unemployed individual is carried out by the case worker of the PES office. This is the same person as the case worker who provides job search assistance to the individual. Indeed, the case worker's primary task is to help the unemployed to find a job. As a rule, the case worker's identity does not change during the unemployment spell.

The case worker is supposed to examine whether the individual's job search behavior is in accordance with the UI guidelines. Specifically, this means verifying that the individual has not rejected suitable job offers.2 A sanction is a benefits reduction for a limited period of time, as a punishment for violation of the guidelines. The case worker is the only person who can take the initiative to give a sanction. For first-time offenders, a sanction is a reduction of 25 percent of benefits for a period of 40 days. For second-time offenders, the sanction is 50 percent for 40 days. A third violation during the same UI entitlement period entails a full loss of benefits until new employment has been found. The case worker is also supposed to verify, during the course of an unemployment spell, that the unemployed individual does not violate the UI entitlement conditions in the first place. This concerns, for example, unreported employment. If the individual is deemed non-eligible, then he is no longer registered as being unemployed. Moreover, his UI benefits payment is terminated for an indefinite period of time.3

The assignment of a sanction starts with the case worker at the PES office observing an infringement. The case worker then informs the UI fund about the infringement. In practice, case workers contact the individual immediately prior to contacting the UI fund, to rule out the possibility that the apparent infringement was the result of a misunderstanding. In the third stage, a decision about the sanction is made by the UI fund, and a motivation is provided. In more than 85 percent of cases, the UI fund approves a sanction (see IAF, 2007, 2009). In a fourth stage, there might be an appeal to revert the decision. However, of all decisions, only a negligible fraction (2 percent) are partially or fully reversed. Subsequently, it is possible to appeal against a sanction at the county administrative court.

Several events in this process are not fully predictable. Most importantly, the case worker does not always observe that an individual has turned down a job offer. The case worker also has substantial discretionary power in his or her daily work, and whether the UI fund is informed about an apparent infringement depends on the attitude of the case worker. Overview studies in Swedish, such as IAF (2006), state that case workers themselves report that there are differences in the interpretation of the regulations between counties and employment offices, and between individual case workers working at the same employment office. The decision on a benefit sanction might depend on the board members attending the UI fund meeting. All this makes it unlikely that UI claimants anticipate the imposition of the sanction with great accuracy before they receive information that an apparent infringement has been detected.

The time interval between the moment that the case worker informs the UI fund about the infringement and the moment that the UI fund makes its decision is short. Over the period 2004–2009, the median duration of this interval was less than four weeks. Information on the years prior to 2004 is not available, but the procedure has not changed, so we suspect that the time intervals had roughly the same length. This means that once the unemployed individual receives the signal that he will most likely receive a sanction, it only takes a few weeks before this sanction is imposed.

The number of sanctions issued in Sweden per year is low in comparison to other countries. Figure 1 displays this number per month, between January 1999 and November 2004. In 2000, about 3,000 sanctions were issued, on an average stock of 210,000 full-time unemployed UI recipients. In the ranking of countries by sanction occurrence by Gray (2003) – which, roughly speaking, is defined as number of sanctions in 1997 divided by the number of unemployed in 1997 – Sweden is the lowest among the nine European countries considered (see Table 1). For the Netherlands in 1993, Abbring et al. (2005) report that around 3 percent of the inflow of UI recipients receive a sanction during the UI spell. In non-European OECD countries, the occurrence rates are also typically higher than in Sweden. Furthermore, contrary to Sweden, a number of countries, including Germany, the Netherlands, and Denmark, have witnessed strong absolute increases in the occurrence of sanctions since the early 2000s (e.g., Schneider, 2008; Svarer, 2011). In the other social insurance programs and unemployment benefits programs in Sweden, sanctions are also rare.

image

Figure 1. Monthly number of sanctions 1999–2004

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Table 1. Sanction occurrence by country and by reason (1997–1998)
CountryTotalReason: offer rejectionReason: lack of effort
Notes
  1. Numbers of sanctions divided by the average annual stock of beneficiaries, in percentages. Sanctions upon entry into unemployment are not considered. The underlying UI systems and the methods to classify the reason for the sanction differ greatly across countries. See Gray (2003) for detailed comments for each country. In the case of Sweden, both of the sanction categories include cases where the UI eligibility conditions were violated and the individual was actually deregistered as unemployed. (In particular, the category of sanctions “Reason: lack of effort” contains such cases, which formally are not sanctions at all.)

Australia14.710.3314.38
Belgium4.200.024.18
Canada0.130.080.06
Czech Republic14.70??
Denmark4.300.573.73
Finland10.192.697.5
Germany1.140.640.50
Japan0.020.000.02
Sweden0.790.610.17
Switzerland40.2913.2327.06
New Zealand0.370.010.36
Norway10.845.015.83
United Kingdom10.301.239.07
USA56.971.9055.07

The Swedish UI monitoring system is also different from the systems in other countries. First, in Sweden, monitoring and job search assistance are carried out by the same case worker. In other countries, monitoring is often carried out by agencies that are distinct from the agencies providing job search assistance. Second, after inflow into UI, monitoring restricts attention to job offer rejections. Other countries focus primarily on search effort as captured by the number of applications sent out or by indicators of the time spent searching for a job. Grubb (2000) has provided a comprehensive and systematic overview by country.4 The final two columns of Table 1 display the occurrence of the two main types of sanctions: (i) those given because of job refusals; (ii) those given because of insufficient job search activity or because of insufficient performance in active labor-market policy (ALMP) programs and contacts with the PES.

Raw differences between sanction occurrence rates are not readily interpretable in terms of policy parameters. The occurrence of a sanction is right-censored by the exit to work, and if monitoring is very stringent, then this can lead to a low occurrence of violations that are actually detected by the monitoring. Nevertheless, as can be seen in the following, the low overall occurrence of Swedish sanctions can be explained by the institutional features of the monitoring system.

III. Theoretical Insights

  1. Top of page
  2. Abstract
  3. I. Introduction
  4. II. Unemployment Insurance
  5. III. Theoretical Insights
  6. IV. Data
  7. V. Empirical Model
  8. VI. Results
  9. VII. Displaced Workers
  10. VIII. An Assessment of the Design of the Monitoring Policy
  11. IX. Conclusions
  12. References

A Job Search Model with Monitoring of Job Offer Decisions

In this subsection, we present a job search model of unemployed individuals with a monitoring system in which job offer decisions are monitored and sanctions can be imposed. This model takes the distinguishing features of the Swedish UI monitoring system into account and has not been analyzed in the literature. The model helps us to understand the effects of such a system on individual behavior. It also provides insights into the determinants of the rates at which jobs are found and the rate at which sanctions are imposed and the relationship between these rates.

First, consider an unemployed individual who searches sequentially for a job in a world without monitoring. Job offers arrive according to the rate λ. Offers are random drawings from a wage offer distribution inline image. Every time an offer arrives, the decision has to be made whether to accept it, or to reject it and search further. During unemployment, a flow of benefits b is received, possibly including a non-pecuniary utility of being unemployed. The individual aims at maximization of the expected present value of income over an infinite horizon. For expositional convenience, in this subsection, we take the wage as the only possible job characteristic and we assume that once a job is accepted it will be held forever at the same wage.

It is well known that under some regularity conditions, the optimal strategy of unemployed individuals can be characterized by a reservation wage ϕ, giving the minimal acceptable wage offer. The transition rate to work equals inline image.

Now let us introduce monitoring in this framework. We assume that the case worker scrutinizes a fraction p of all the rejected job offers, and that, on average, a fraction q of these rejected offers are deemed to be sufficiently suitable for the unemployed worker. Accordingly, if the unemployed individual's optimal strategy is characterized by reservation wage ϕ, the sanction rate equals inline image. If inline image, then all offers are monitored, and if inline image, then each rejected offer entails a sanction. For given p and q, we assume that the individual does not know which rejected offers are sampled or which are deemed acceptable by the case worker, but that he does know the values of p and q. In practice, case workers might be more concerned about the rejection of reasonably good job offers than about the rejection of very unattractive offers. This can be formalized by allowing q to be an increasing function of the offered wage w. We return to this model extension in the next subsection.

Some individuals will be more willing to take the risk of being given a sanction than others (e.g., because they have a higher non-pecuniary utility of being unemployed). Obviously, if inline image and the punishment is sufficiently severe, then all job offers are always accepted and sanctions are never given. To proceed, we have to be specific about what occurs after the imposition of a sanction. First of all, benefits (b) are reduced substantially. Second, p is likely to increase. If the individual again violates the rules concerning job offer decisions, and this is observed by the case worker, then additional reductions in benefits are imposed. We assume that the punishment for such repeat offences is so severe that the individual will avoid this at all costs, so we assume that all offers are accepted after the imposition of a sanction. This implies that sanctions are imposed at most once in a given spell of unemployment. (A strategy in which individuals take a job upon imposition of a sanction, and quit immediately in order to make a “fresh start” in UI, would not be optimal. UI would be reduced again immediately after quitting because of “insufficient effort to prevent job loss”; see Section 'Unemployment Insurance'.)

For simplicity, we assume that the parameters b1 (which is the benefits level before a sanction is imposed), F, λ, p, q, and the discount rate ρ are constant as a function of unemployment duration. Upon imposition of a sanction, b is permanently reduced from b1 to b2, with b2 constant as a function of unemployment duration. As a consequence, both within the time interval before a sanction and within the time interval after a sanction, the expected present value of income and the optimal strategy are constant over time.

Let R1 and R2 denote the expected present value of income before and after the imposition of a sanction, respectively, and let ϕ1 denote the reservation wage before the sanction. We find that

  • display math(1)

and

  • display math(2)

with

  • display math(3)

These equations follow from the Bellman equations in which R1 and R2, at a given point in time, are expressed in terms of events that might occur in a short time interval with length inline image right after this point in time. For R2, this Bellman equation states that

  • display math

This can be understood as follows. Within inline image, the flow of benefits equals inline image. If this is paid at the end of inline image, then this flow is discounted by inline image. With probability inline image, a job offer arises within inline image. This offer must be accepted, and the expected return at the end of the interval equals the expected value of inline image over F. With probability inline image, no offer arises in inline image, and the ensuing expected return at the end of the interval equals R2 again. Multiple offers in inline image arise with probability inline image. By elaborating on this equation and letting inline image, we obtain equation (2).

Likewise, equation (1) follows from the Bellman equation

  • display math(4)

The main difference with the Bellman equation for R2 concerns the second term on the right-hand side. In equation (4), the mean over F of the expected return of a wage offer w takes into account the fact that an offer might be rejected, in which case there is a probability inline image that one is caught, with associated present value R2, and a probability inline image that one is not caught, with present value R1. It is optimal to accept an offer if and only if inline image. Hence, the reservation wage ϕ1 satisfies equation (3).

Note that with the strictest possible monitoring (i.e., inline image), the outside option when considering an offer is equal to a certain punishment, so then inline image. This implies that extreme monitoring does not necessarily entail the absence of punishments. Given certain model parameter values, it is optimal for an individual to prefer a sanction and a forced future job offer acceptance over a current low offer. This is particularly likely if the offer under consideration is much lower than the average offer and if the punishment inline image is small.

It is also interesting to consider the expected present value inline image and optimal reservation wage inline image in the absence of a monitoring system,

  • display math(5)

By elaborating on equations (1) and (2), we obtain the following expression for ϕ1,

  • display math

which has a similar structure as the reservation wage equation in a standard job search model. Clearly, the latter is obtained by imposing inline image. For general inline image, the reservation wage is a weighted average of the reservation wage without monitoring and the present value flow after punishment.

Using obvious notation, the transition rates from unemployment to employment before and after the imposition of a sanction equal

  • display math(6)

For a system with given p and q, the probability that a sanction occurs before a job exit is equal to inline image. This can be seen by noting that a newly unemployed individual faces competing risks (a sanction and exit to work) with constant rates inline image and inline image, respectively.

Theoretical Predictions Concerning the Effects of Sanctions and Monitoring

In the model, the proportionate effect of the sanction on the exit-to-work rate equals inline image. This effect corresponds to a parameter of the empirical model specification (see Section 'Empirical Model'). The additive effect on the exit-to-work rate equals inline image. The additive effect on the mean accepted wage equals inline image. The empirical model contains a parameter that captures the additive effect on the mean log accepted wage inline image. These empirical parameters are likely to vary across individuals, because they depend on the characteristics of the individual and his labor-market segment. Of course, the empirical parameters are not constrained to have a particular sign.

The model also generates a number of implications of the monitoring scheme as such. Consider the general case where the model parameters are such that inline image: the reservation wage before a sanction is imposed exceeds the lowest possible wage offer in the market. This is a necessary condition to observe sanctions at all. It is clear that inline image, and consequently inline image. From the point of view of the individual, monitoring reduces the expected present value, and so does an actual punishment in a world with monitoring. By implication, inline image and inline image are both larger than the transition rate in a world without monitoring. Consequently, monitoring affects the transition rate of all individuals (except for those who have a low reservation wage inline image anyway). This is the ex ante effect of the monitoring system, as opposed to the ex post effect resulting from the imposition of a sanction.

With monitoring, if inline image, then the individual probability of job acceptance is equal to one, so there will not be any sanctions. If the case worker is very lenient (inline image), then the sanction rate is also zero. Conversely, we have seen that in the strictest possible monitoring system (inline image), an individual might still prefer to reject a low-wage offer in favor of a sanction. This reflects a first fundamental difference with monitoring schemes that target an endogenously chosen level of search effort by the individual (for a theoretical analysis, see Abbring et al., 2005). In the latter scheme, perfect monitoring leads to the absence of sanctions, even if the punitive reduction in benefits is small. This is because perfect monitoring of search effort is instantaneous and uninterrupted over time, and the effort constraint is strictly enforced after a violation. Perfect monitoring of offers only takes place upon offer rejections but not in-between rejections, and a rejection followed by a sanction might be worthwhile if it is followed by a high wage offer at a later point in time.

It is interesting to consider the ex post effect and the occurrence of sanctions for different subgroups of individuals. First, consider individuals for whom inline image is small. Because inline image, this means that their expected present value of unemployment after rejection of an offer is low. For example, R1 and R2 might be low because of a low job offer arrival rate λ and R1 might be low because of low benefits b1. These individuals are unlikely to reject an offer and are therefore unlikely to receive a sanction. Their sanction effect is also small. Note that for moderate values of inline image, the probability inline image that a sanction occurs before exit to work can still be extremely small if q is very small, but in that case the sanction effect is not necessarily extremely small.

Second, consider the opposite case where inline image is large (i.e., close to one). Such individuals face a high sanction rate and their sanction effect is large. For such individuals, it is particularly interesting to examine optimal behavior if they can optimally choose their search effort s as well. Let the job offer arrival rate now be specified as inline image, and let the search cost flow inline image be a convex increasing function of s with inline image, such that the instantaneous income flow before a sanction equals inline image. The optimal value of s before a sanction follows from maximization of the right-hand side of the suitably adjusted equation (1), leading to

  • display math

If ϕ1 is at the upper bound of the support of F, then the integral in the above expression vanishes, implying that inline image. The same result follows for values of ϕ1 close to the upper bound. If the monitoring regime is stringent, then the last term on the right-hand side increases, so the reduction of optimal search effort is exacerbated. In summary, when these individuals can choose their level of search effort, then monitoring of offer decisions will be counteracted by a reduction of search effort. To put it bluntly, monitoring of job offer decisions means that individuals with high benefits (or a high utility flow of being unemployed) adjust their behavior so that they never receive a job offer. The ex ante effect of monitoring is then perverse: more monitoring implies a lower exit-to-work rate. So, in contrast to the monitoring of job search effort, the monitoring of job offer decisions does not always generate a positive ex ante effect.

In reality, the difference between the monitoring regimes might be smaller than described. For one thing, the potential perverse ex ante effect of monitoring job offer decisions with optimally chosen search effort might be mitigated by the assignment of job offers by case workers to unemployed individuals. Such job offers do not require any search effort on the part of the unemployed worker, and the offer decision is easily monitored. Job offer assignments are a feature of many monitoring systems (Grubb, 2000). At the same time, monitoring of job search effort can be sabotaged by unemployed individuals making so-called fake applications. These are viewed as serious applications by the monitoring agency and, as such, they are accepted as evidence of search effort. However, the applications might contain some subtle signal, inducing the employer to reject the application.

Another difference between the monitoring regimes concerns post-unemployment outcomes, and this is perhaps the most important difference for our study. As already mentioned in the introduction of the paper, with the monitoring of search effort, the adverse effects on post-unemployment outcomes might be smaller than with the monitoring of job offer decisions. Perfect monitoring after a sanction implies full compliance after the sanction. With the monitoring of job offer decisions, this means that compared to the situation before a sanction, punished individuals now also have to accept all offers of jobs with the lowest wages. With the monitoring of search effort, however, full compliance means that punished individuals have to search harder for any possible job. The latter includes both high-wage and low-wage jobs.

All results in this section generalize to job characteristics other than wages. Basically, if the individual's utility flow function depends on the wage and on other characteristics, then the role of the income flow variables in the present section is replaced by the corresponding utility flows.

We finish this section by briefly mentioning some implications of the theoretical analysis for the specification of the empirical model, assuming that inline image. The empirical model is a reduced-form model in which hazard rates and post-unemployment outcomes are allowed to vary over time and across observed and unobserved individual characteristics (rejected offers are not observed). The first implication is that at the individual level, the transition rate from unemployment to employment makes a discrete upward jump upon imposition of a sanction. Furthermore, the individual's expected accepted wage makes a discrete downward jump upon imposition of a sanction, with similar effects on other post-unemployment outcomes. If individuals and their environments are homogeneous, then the sizes of these jumps, which are the causal effects of the sanction treatment, can be estimated from a joint model of unemployment durations and post-unemployment outcomes in which the moment at which a sanction occurs is a time-varying exogenous covariate. However, all outcomes and the rate at which a sanction arrives depend on all the variables that the individual uses to determine his strategy. This is because all depend on ϕ1. In reality, individuals are heterogeneous with respect to determinants of search behavior. Suppose that the individuals know their own value of some characteristic but that these values are not observed in the data. As argued in Section 'Theoretical Insights', such a setting is plausible with punitive treatments. Then, the outcomes and the rate at which a sanction is imposed depend on this unobserved characteristic. This creates a spurious relation between the duration until a sanction is imposed and the outcomes. Note that a similar spurious relation is created if the policy parameters p and q of the sanction rate itself differ across individuals in a way that is not observed by the researcher.

Biased Wage Offer Expectations among Displaced Workers

Consider the prototype displaced workers, as described in Section 'Theoretical Insights'. Upon their involuntary transition into unemployment, such individuals might overestimate their market value. Their skills might have become obsolete, and most offers they receive concern jobs with wages that are low compared to their pre-unemployment wage. In the job search model of Section 'Theoretical Insights', this can be captured by the fact that their perceived wage offer distribution inline image is a location shift of the true wage offer distribution, so inline image with inline image. From standard comparative statics results for job search models (e.g., Mortensen, 1986), it follows that the actual reservation wage ϕ1 used, based on inline image used before a sanction, is suboptimally high. Therefore, displaced workers reject a suboptimally large number of job offers after entry into unemployment. With generous UI benefits for displaced workers, the level b1 is a relatively high fraction of the previous wage, and this pushes ϕ1 up further. All this implies that the pre-sanction exit-to-work rate inline image is relatively low and that the sanction rate inline image is relatively high.

As noted in Section 'Theoretical Insights', a sanction can act as a wake-up call for such a worker, signaling that he has misperceived his chances in the labor market. The individual might realize this by himself at the moment at which the sanction is imposed, but it might also be induced by information from the employment office, which accompanies the sanction. The sanction effect now has three aspects. As in Section 'Theoretical Insights', we find that (i) b reduces to b2 and (ii) repeat offences are sufficiently unattractive to induce full compliance. However, now we also find that (iii) the individual takes F instead of inline image as the perceived wage offer distribution. The ex post sanction effects are as in Section 'Theoretical Insights': the exit-to-work rate and the mean accepted wage jump upwards and downwards, respectively.

From a welfare point of view, it is important to distinguish the adjustment in expectations (iii) from the institutional aspects (i) and (ii) of the sanction. We have seen that the institutional aspects create a welfare loss on the part of the unemployed workers, in the sense that their expected present values are lower in a system with monitoring and sanctions. The welfare effect of the adjustment in expectations is more subtle. If the displaced worker is provided with more accurate information about labor-market opportunities, then he can adjust his search strategy towards a strategy that is optimal in the light of accurate information. Without this information, the worker might have felt even better off, but this would not be sustainable indefinitely. If the information only arrives after a long time in unemployment, then the displaced worker's skills might have deteriorated so strongly that any chance to find a job might have dissipated.

This also leads to a reassessment of the post-unemployment wage effects of a sanction. This is most clearly seen in the extreme case where the sanction effect aspects (i) and (ii) are not relevant in practice (e.g., because the drop in benefits inline image is small and the punishment for re-offence is not large). In this case, the fact that displaced workers accept lower wages after a sanction than otherwise is because the sanction makes them realize that their market value is lower than they expected. However, that market value already fell at the moment of displacement – not at the moment of the sanction. In this case, therefore, the negative effect of a sanction on the post-unemployment wage captures the displacement wage effect, and such a long-run effect should not be interpreted as a long-run component of a punishment for violating job search requirements.

All this makes it interesting to empirically study the fate of displaced (versus non-displaced) workers after a sanction. In Section 'Displaced Workers', we examine suitable model specifications and we provide estimation results for given displacement statuses.

IV. Data

  1. Top of page
  2. Abstract
  3. I. Introduction
  4. II. Unemployment Insurance
  5. III. Theoretical Insights
  6. IV. Data
  7. V. Empirical Model
  8. VI. Results
  9. VII. Displaced Workers
  10. VIII. An Assessment of the Design of the Monitoring Policy
  11. IX. Conclusions
  12. References

Data Sources

Our data are taken from a combination of four Swedish population register datasets and one large-scale annual employer survey. The first register, called Händel (from the employment offices), covers all registered unemployed persons. It contains day-by-day information on the unemployment status. This includes UI eligibility, entries into and exits from ALMP programs, and the reason for the unemployment spell to end (as a rule, this is re-employment, but occasionally it is a transition into education, social assistance, or other insurance schemes). Händel also includes a number of personal characteristics recorded at the beginning of the unemployment spell. The second register, ASTAT (from the unemployment insurance fund), provides information on sanctions, including the timing, the main reason, and the size of the benefit reduction.

Our observation window runs from January 1, 1999 until December 31, 2003. An individual becomes unemployed at the first date at which he registers at the employment office as being “openly” unemployed. Concerning re-employment, we require employment (full-time or part-time) to be retained for at least 10 days. UI spells that terminate for other reasons than re-employment are considered to be right-censored durations until re-employment. We stop time during the period in which the individual is enrolled into an ALMP program. The reason for this is that the re-employment rate during program participation is low and that sanctions are not given during program participation. In sensitivity analyses, we examine the robustness of the results with respect to this. Spells that are ongoing at the end of the observation window are right-censored.

We restrict our analysis to everyone who was between 25 and 55 and who was covered by UI at the time of entry into unemployment. We exclude unemployment spells occurring after a spell during which a sanction was given to the individual. This is because we exploit multiple spells to enhance the quality of the results, and we cannot rule out that a sanction also affects future subsequent spells.

The sanction and unemployment data are combined with survey data on wages and hours worked, collected by Statistics Sweden with the purpose to publish wage statistics. These data provide us with wages per time unit and hours worked per week. The survey is conducted annually (during the fall) among employers, by Statistics Sweden in cooperation with employer organizations. It covers the whole public sector, all large private firms and a random sample of small firms (about 50 percent of all private-sector employees), and it provides the relevant variables for all employees working at the sampled firms at the moment of the survey. Note that the wages are not derived from annual earnings and some measurement of hours worked. They are recorded as monthly full-time equivalents. If we observe a wage within one year after exit to employment, then we take this wage as the post-unemployment outcome; otherwise, the latter is a missing observation. The information on hours worked is used to construct an indicator variable for full-time employment, defined as working 34 hours or more a week.

The survey data also record individual occupations. These are classified using SSYK-96, which closely follows the international standard ISCO-88. Each occupation is classified into 355 separate subgroups of occupations (four digits). The first digit classifies occupations by the general qualifications required to perform the tasks associated with each occupation. It divides the occupations into four levels: the occupations in group 1 normally require no or limited education, level 2 occupations require high-school competence, level 3 occupations require short university education, and the occupations at level 4 require longer university education (three to four years or more). Subsequent digits capture the specialization skills associated with the occupation. We use a third register (“Louise”) and the survey of 2001 to translate the occupational level into average years of education. “Louise” contains both variables as well as a range of yearly economic outcomes for each adult member of the full population. We perform this translation in three different ways, using one, two or three occupational digits. With one digit, the average number of years of education ranges from 10.5 to 14.4. This difference is rather small because of the existence of parallel educational tracks.

It can be argued that the observation of the wage variable is selective because the sampling frame depends on the firm size, and small firms tend to pay lower wages than large firms. If this is ignored and if individuals who are sanctioned accept lower wages, on average, then this can lead to an underestimate in absolute terms of any negative effect of sanctions on wages. In the next subsection, we provide some insight into the extent that this selection issue poses a problem.5 In addition, we deal with this issue by using post-unemployment annual labor earnings data in the “Louise” register for the individuals in our sample. Specifically, we select the annual labor earnings in the first calendar year after entry into employment. The labor earnings information in “Louise” is taken from the income tax register, so it is observed for the full adult population. Earnings only capture income from actual employment. If the analysis with the employer survey data is correct then the effect on log earnings should not be completely out of line with the sum of the effects on log wages and on log hours worked.

Recall that we have a particular interest in the effects on workers who were displaced at the moment of entry into unemployment. To identify these individuals, we follow two alternative approaches. First, we use information on previous unemployment experiences. The Händel register enables the reconstruction of the unemployment history several years back in time. From this, we obtain the cumulative number of days in unemployment in the year (or the two years, three years and so on) before the start of the unemployment spell. The second approach uses a fourth register (ANST), which is a matched employer–employee population database containing earnings from each employer, establishment identifiers, and employee identifiers. From this, we reconstruct the employment history of each individual back to 1990, and we summarize this in a number of measures, including (i) the amount of time spent at the firm from which the individual enters unemployment, (ii) the amount of time in the sector from which unemployment is entered, (iii) whether entry into unemployment was a result of plant closures, and (iv) whether it was because of a mass lay-off. An establishment is considered to be closed down if it disappears in a given year and if not more than 50 percent of the employees at that establishment all switch to a given employer in the next year (these individuals should also constitute more than 50 percent of the employees in the new firm). The 50 percent threshold is imposed in order to filter out changes in ownership. If more than 30 percent of the workforce leaves an establishment in a given year, and if the 50 percent threshold is not violated, then we define this as a mass lay-off. We only construct these variables for workplaces with more than 10 employees. The use of register data to identify plant closures and mass lay-offs by way of 30 and 50 percent workforce exit thresholds is common in the literature; see, for example, Jacobson et al. (1993), Sullivan and Von Wachter (2009) and, using Swedish data, Eliason and Storrie (2006, 2009a, 2009b).

Descriptive Statistics

In Section 'Empirical Model', we explain that we estimate models with a stratified sample taken from the inflow population into unemployment. This sample consists of all sanctioned individuals plus a random sample of non-sanctioned individuals. We provide descriptives for the population (or full sample) as well as the stratified sample. Table 2 reports statistics on the unemployment spells and the duration until a sanction. Clearly, sanctions are rare. In the population sample, 0.4 percent of the individuals experience a sanction. Almost half of the sanctions are imposed during the first 100 days of unemployment, whereas about 16 percent are imposed after 300 days or more in unemployment. Because of censoring, the latter figure underestimates the incidence of sanctions and the elapsed duration at which these are imposed. Sanctions to recidivists are not used in our analyses, but these are rare anyway (less than 10 percent of first-time offenders).

Table 2. Sample statistics for duration in unemployment and duration until a sanction
 Full sampleStratified sample
Notes
  1. The time is in units of days, ts is time until the sanction, and te is time in unemployment. Standard deviations are given in parentheses. The full sample is the full sample of all unemployment spells; the stratified sample is described in the data section.

Regardless of treatment
Number of individuals827,07416,941
Number of spells1,665,42035,055
Percent with exactly one spell48.749.4
Percent with exactly two spells24.224.0
Percent with more than two spells7.17.0
Percent of spells with ts observed0.188.4
Percent of te observed65.765.2
Average observed te104.4 (112.4)114.5 (122.9)
Median observed te6874
Concerning spells with sanction observed
Number of spells2,9412,941
Percent of te observed56.156.1
Average observed ts240.2 (174.0)240.2 (174.0)
Median observed ts193193
Average observed te140.6 (134.0)140.6 (134.0)
Median observed te9696
Percent ts in 0–50 days27.127.1
Percent ts in 50–100 days19.719.7
Percent ts in 100–150 days12.312.3
Percent ts in 150–200 days10.610.6
Percent ts in 200–250 days7.57.5
Percent ts in 250–300 days6.16.1
Percent ts in 300 days16.616.6
Type of sanctions  
Percent consisting of 100 percent reduction for 60 days32.032.0
Percent consisting of 25 percent reduction for 40 days68.068.0

Table 3 reports statistics on the characteristics of the accepted job. For about 35 percent of the spells for which we observe an exit to employment, we observe the wage within one year after the exit. If the wage is not observed, this could be because the individual is employed in a small private firm or has left employment before the survey date. Because the wage survey is conducted annually, the mean time from the exit to employment to the time of the wage survey is about half a year (179 days). Because the survey is mainly conducted during the autumn and because there is seasonal variation in exits into employment, the time from the exit to the survey is not uniformly distributed over one to twelve months. The mean observed monthly wage is about SEK 17,840. About 57 percent of these observations are in full-time employment. Furthermore, 57 percent have a job in the public sector, 25 percent in a private firm with at least 200 employees, and 18 percent in a smaller firm. Table 4 presents statistics by sanction status in the stratified sample.

Table 3. Sample statistics for wages and hours worked
 Full sampleStratified sample
Notes
  1. Wage is the first observed (within one year) after the exit from unemployment. Time of inflow is defined as the calendar year in which the unemployment spell starts. Full sample is the full sample of all unemployment spells, and the stratified sample is described in the data section. Standard deviations are given in parentheses.

Wage data  
Percent exit to employment observed65.765.2
of which:  
Observe wage (percent)36.535.1
Observe hours worked (percent)30.429.2
Public sector employment (percent)55.957.2
Private sector firm ⩾200 workers26.025.3
Private sector firm <200 workers18.117.5
Monthly wage in SEK17,941 (4,371)17,843 (4,446)
Full time (⩾34 hours a week) percent58.757.0
Average time between exit and wage survey179.5 (107.6)178.9 (108.3)
Median time between exit and wage survey161161
Time between exit and wage survey  
0–60 days13.714.5
61–120 days22.321.8
121–180 days18.719.0
181–240 days13.713.4
241–300 days14.614.0
301+ days17.017.4
Individual  
Male (percent)50.252.2
Education in occupation (percent)64.665.5
Experience in occupation (percent)39.639.7
Needs guidance (percent)22.823.2
Age36.4 (8.14)36.4 (8.11)
North (percent)22.122.3
Central (percent)37.536.9
South (percent)40.440.8
Less than high school (percent)20.321.3
High-school education (percent)54.355.3
University education (percent)25.423.4
Local unemployment (percent)5.15 (1.53)5.14 (1.54)
Time of inflow  
199921.921.9
200020.020.4
200119.019.6
200219.419.6
200319.718.5
Table 4. Sample statistics sanctioned and non-sanctioned in stratified sample
VariableNo sanctionSanction
Notes
  1. Standard deviations are given in parentheses.

Number of observations32,1142,941
Male (percent)51.757.7
Age36.4 (8.1)37.0
Education in occupation (percent)65.763.3
Experience in occupation (percent)40.333.9
Needs guidance (percent)23.420.7
High-school education (percent)55.354.4
University education (percent)24.118.7
North (percent)22.718.1
South (percent)40.840.7
Local unemployment5.1 (1.55)4.91 (1.40)
Wage after unemployment17,873 (4,514)17,402 (3,359)
Wage before unemployment17,014 (4,087)16,503 (3,647)
Earnings after unemployment (SEK)148,806 (90,683)130,218 (79,125)
Earnings before unemployment (SEK)129,903 (100,224)123,508 (86,230)

As argued in the previous subsection, the wage data might not be missing at random. To shed some light on the role of firm size in the survey sampling scheme, we estimate a logit model for the choice between public-sector versus private-sector employment and, given the choice for the private sector, a logit model for the choice between a large firm versus a small firm. In both cases, we control for covariates, such as sex, age, level of education, time of inflow into unemployment, regional variables, level of education, the type of profession the unemployed individual is searching for, and whether the unemployed individual has education and previous experience in that occupation. We estimate the logit specifications jointly. This exercise show no evidence of a sanction-induced selection into small private firms.

We also examine whether the so-called common support condition is satisfied for the evaluation of sanction effects. That is, we compare the empirical distributions of the vector of observed explanatory variables x among those who are observed to receive a sanction and among those who are not. If there are subsets of the population for whom no sanctions are observed, then it might make sense to omit those subsets from the data. However, it turns out that the two distributions are very similar. The joint empirical distribution of the elements of x in the subsample of sanctioned workers contains some empty cells, but for each element separately we observe sanctions for each possible value of the element. In our empirical analysis, we also allow for selection on unobservables, and obviously we cannot observe whether the latter have common support across treated and non-treated. We return to this issue in Section 'Displaced Workers' when we focus on displaced workers.

An Attempt to Tighten the Monitoring System

Early on in our observation window, some parameters of the sanction system were changed. Specifically, as of February 5, 2001, the size of the sanction and the length of the sanction period were set at the values mentioned in Section 'Unemployment Insurance'. Before this date, the only possible sanction was a 100 percent reduction of the benefits level for a period of 60 days.6 The underlying motivation for this change was that the personal connection between the case worker and the individual he/she was helping made it difficult for the former to propose a punishment that amounted to the full withdrawal of the latter's income. (Recall that helping the unemployed worker is the primary objective of the case worker.) This could prevent case workers from reporting violations. It was felt that more modest sanctions would be easier to give, so that the threat of sanctions would become more credible, leading to an increase in the threat effect. Governmental documents in Swedish substantiate this description of the motivation behind the policy change. At the time, many other countries already had policies where sanctions were smaller than 100 percent of the UI level. The decision to change the policy was made on December 21, 2000 – 1.5 months before enforcement.

It is interesting to examine this change more closely because it might provide information on the effects of monitoring and sanctions. Figure 1 displays the number of sanctions per month over the observation window. Clearly, the reform did not lead to a substantial increase in the number of sanctions issued. Apart from seasonal fluctuations, this number has been increasing very slowly over time, and there is no jump in February 2001. In the short run after February 2001, the absence of a response in the number of sanctions can be attributed to the slow implementation of the policy change at the level of the case worker. After the policy change, the employment office arranged regional meetings to inform the case workers about the policy change. These were held until May 2001. Case workers stated that after these meetings, certain details of the new policy regime were still unclear to them (personal communications). However, even in the long run, the occurrence of sanctions remains low by any standard.

The absence of a response in the observed number of sanctions can be explained in two ways. First, the case workers might have decided not to act on the policy change but instead to continue to ignore violations, because they might find a 25 percent reduction in benefits still too severe. From an international perspective, 25 percent reductions for first-time offenders are substantial. Concern for the living conditions of punished individuals is also present in countries where sanctions are less severe and monitoring is carried out by different individuals than the case workers, as in the Netherlands. There, individuals who carry out the monitoring state that they are less likely to issue a sanction if they feel that the unemployed individual faces adverse labor-market conditions (see Van den Berg and Van der Klaauw, 2006). In agreement to this, studies using Dutch data find that individual characteristics that are associated with a low exit-to-work rate are also associated with a low sanction rate.

The second explanation is that the threat of sanctions has become credible and that this motivates individuals to avoid violations at all costs. That is, the policy change induced a strong ex ante effect, such that the resulting occurrence of sanctions remains low. In terms of our theoretical model, the policy change is then represented by an increase of q, which leads to a decrease of ϕ1, such that virtually all offers are accepted.7inline image8

To distinguish between these explanations, we can compare the unemployment duration outcomes before and after the policy change. This effectively amounts to detecting changes in the size of the ex ante threat effect. The first explanation implies that the exit-to-work rate θe, 1 does not change upon the policy change. The second explanation implies that the exit-to-work rate increases after the policy change. It turns out that the empirical evidence supports the first explanation (see Section 'Results'). In summary, (i) the policy change was ineffective because case workers shun away from issuing sanctions more frequently, (ii) the low occurrence of sanctions can be explained by a low effective level of monitoring, and (iii) there is no strong ex ante threat effect of sanctions. This means that the ex post effects that we estimate below capture the causal effects of a sanction as compared to the outcomes in a labor market without monitoring (Abbring and Van den Berg, 2005).

V. Empirical Model

  1. Top of page
  2. Abstract
  3. I. Introduction
  4. II. Unemployment Insurance
  5. III. Theoretical Insights
  6. IV. Data
  7. V. Empirical Model
  8. VI. Results
  9. VII. Displaced Workers
  10. VIII. An Assessment of the Design of the Monitoring Policy
  11. IX. Conclusions
  12. References

Bivariate Duration Model

In this section, we present our empirical model. We start off with a model for the effect of sanctions on the unemployment duration. This is a necessary ingredient for the study of sanction effects on post-unemployment outcomes, if only because the unemployment duration determines whether the post-unemployment outcome is observed, and both the duration and the post-duration outcomes depend on unobserved characteristics (see Ham and LaLonde, 1996; Abbring and Van den Berg, 2005). In the next subsection, we extend the model by incorporating job characteristics as additional outcomes.

Because the outcome is a duration variable and the sanction treatment exerts its causal effect from the moment the sanction is given onwards, it makes sense to characterize the treatment by the elapsed unemployment duration at which it is given. Because of imperfections in the monitoring and because of the randomness of the process generating job offers, the elapsed duration at which the sanction is given is a random variable at the individual level. As argued in Section 'Theoretical Insights', the sanction assignment is selective in that the unemployment duration and the duration until the sanction are most likely affected by common unobserved determinants. Together, this gives rise to a bivariate duration model for the actual moment at which a sanction is given and the actual unemployment duration, with a causal effect as well as correlated unobserved heterogeneity. Such models have been used in studies of the effect of sanctions on the exit-to-work rate (see Van den Berg et al., 2004). Abbring and Van den Berg (2003) express these models in a potential-outcome framework. Eberwein et al. (1997) were the first to use a bivariate duration model with unobserved heterogeneity in order to estimate the causal effect of a randomly timed treatment on the exit-to-work rate. They used a randomized intention to treat as an instrumental variable to achieve identification of the causal effect. Instead, we rely on the “Timing of Events” approach to the identification of treatment effects when treatments are characterized by the moment in time at which they occur (Abbring and Van den Berg, 2003). In the following, we discuss the underlying assumptions.

The individual exit-to-work rate θe and the sanction rate θs both depend on the elapsed unemployment duration t and on observed individual characteristics x, and they depend on unobserved individual characteristics Ve and Vs, respectively. Moreover, θe depends on whether a sanction has been imposed before t. Specifically, we adopt mixed proportional hazard (MPH) specifications for inline image and inline image, where ts is the actual moment at which the sanction is given:

  • display math(7)
  • display math(8)

Here, I(.) is an indicator function taking the value of one if the argument is true, and zero otherwise. The function inline image represents the sanction effect, which we allow to depend on the time since the imposition of the sanction and on observed individual characteristics. Note that λe and λs capture dependence on the time since inflow into unemployment whereas, in Section 'Theoretical Insights', λ was the job offer arrival rate.

Let G denote the joint distribution of inline image in the inflow into unemployment. Abbring and Van den Berg (2003) have shown that all components of this model, including δ and G, are identified, provided we make assumptions similar to those usually made in standard univariate MPH models with exogenous regressors. Identification is semi-parametric in the sense that, given the MPH structure, it does not require any parametric assumptions on the components of the model.

As in virtually every conceivable evaluation of treatment effects, we need to assume that treatment effects do not occur before the treatment is realized (i.e., distributions of potential outcomes are the same before the corresponding treatments are realized). This no-anticipation assumption is often tacitly made. As explained in Section 'Unemployment Insurance', there are several sources of unpredictability in the process leading to job offer decisions and sanctions, making it even unlikely that UI claimants anticipate the precise timing of the sanction. Indeed, with punitive treatments, such as sanctions, the moment at which an individual is caught is, by definition, unanticipated by the individual. Moreover, the time interval between the moment that the individual hears from the case worker that he will most likely receive a sanction and the moment of the imposition of the sanction only covers a few weeks. This is too short to induce a strong response before the end of the interval. Note that all of this does not preclude ex ante threat effects of the system, because such threat effects do not require or depend on private knowledge of the precise future moment of the realization of the sanction.

Identification with single-spell data requires the random-effects assumption that x, on the one hand, and Ve and Vs, on the other hand, are independent in the inflow into unemployment. However, with multiple unemployment spells for a given individual, as we often observe, this random-effects assumption is not necessary for identification (see Abbring and Van den Berg, 2003). In that case, multiple spells for an individual have to be statistically independent of each other, conditional on all observed and unobserved covariates inline image, the unobservables Ve and Vs must be constant across spells, and the length of intervening spells between any two unemployment spells of a single individual must be independent of Ve and Vs. If these conditions are satisfied, then the estimation results are not critically dependent on the random-effects assumption.

The identification does not rely on an exclusion restriction on the effect of x on θe. This is important, because the theoretical analysis predicts that all systematic determinants of the sanction rate that are observable also affect the exit-to-work rate. Instead, what drives the identification of the sanction effect is the variation in the moment of a sanction and the moment of exit to work. If a sanction is closely followed by exit to employment, no matter how long the elapsed unemployment duration before the sanction, then this is evidence of a causal effect of a sanction. Any spurious selection effects due to dependence of Vs and Ve leads to a second relation between the two duration variables, but that relation does not give rise to the same type of quick succession of events (Abbring and Van den Berg, 2003). The Monte Carlo simulations in Gaure et al. (2007) support the use of this approach by showing that the estimates of the parameters of interest are robust with respect to functional form assumptions.

Extension to Post-Unemployment Outcomes

In the baseline analysis of the effects on post-unemployment outcomes, we capture job quality by the wage rate w and by the hours worked per week inline image at the start of the new job, where inline image is summarized by whether the accepted job is full-time or part-time. These outcomes can be expected to depend on unobserved factors that are related to the unobserved determinants of the exit-to-work rate and the sanction rate. For instance, ability most likely affects all these outcomes. In order to identify the causal effect of a sanction on w and inline image we need to impose some structure. We assume that the sanction and the unobserved factors only affect the mean values of inline image and inline image, and not any higher moments, and we assume that these effects are additive. Specifically,

  • display math(9)

and

  • display math(10)

where inline image means that the accepted job is a full-time job, inline image and inline image are the sanction effects, inline image and inline image are unobserved individual characteristics, and inline image and inline image reflect random variation. We assume that inline image is normally distributed with mean zero and variance inline image while inline image has a standard logistic distribution.

Note that equation (9) describes the distribution of the accepted wage and not the wage offer distribution denoted by F in the theoretical model. From the theoretical analysis, it follows that the distribution of characteristics of the accepted job is the offer distribution truncated from below by the minimum acceptable combination of characteristics, where after a sanction every offer has to be accepted. We do not impose such theoretical restrictions. In effect, the empirical model assumes that the individual distribution of wage offers that are acceptable has a log-normal distribution with inline image being additive in x and inline image as well as in whether a sanction has occurred, with a similar assumption for the fraction of full-time jobs among acceptable offers.

We acknowledge the connection between the unobserved determinants of the distribution of the two job characteristics, on the one hand, and the unobserved effects in the sanction rate and exit-to-work rate, on the other hand. We take a simple linear form for this relation,

  • display math(11)

and

  • display math(12)

Note that this allows for an association between observations of w and h conditional on x.

The joint distribution of observed outcomes follows from equations (7), (8), (9), and (10), where non-informative censoring of outcomes can be taken into account. This can be used to estimate the effects on the post-unemployment outcomes using likelihood-based estimation methods. Intuitively, the duration model embedded in the full model identifies G as well as the distribution of inline image. Given this, the only unknowns in the distributions of inline image and inline image are inline image, and inline image. The latter parameters capture the selection process in the decisions concerning acceptable job characteristics.

Parametrizations and Estimation Method

We take flexible specifications of both the duration dependence functions and the bivariate unobserved heterogeneity distribution. We take both inline image and inline image to have a series representation (inline image). With a high polynomial degree, any duration dependence pattern can be approximated closely. We take seventh degree polynomials for the exit-to-work rate and third degree polynomials for the sanction rate. For G, we use a bivariate discrete distribution with unrestricted mass point locations. This is flexible as well as computationally feasible. In fact, we take Ve and Vs to have two points of support each, which is common in this type of model (Van den Berg, 2001). We have experimented with both higher and lower degree polynomials, and with additional mass points. The results are insensitive to such changes, unless the degree of the polynomials for θe and θs is less than 4 and 2, respectively. We exclude a constant from the vector x and one category from each set of binary indicators in x. We further normalize the two constants αs0 and αe0 to 1.

Because sanctions are rare, a random sample needs to include many individuals in order to obtain a sufficient number of spells in which a sanction is observed. However, straightforward maximum likelihood estimation with very large samples is computationally demanding. In our population sample of 827,000 individuals with unemployment spells, we observe less than 3,000 unemployment spells with sanctions. Therefore, we use an endogenously stratified sample in which spells with sanctions are oversampled. Accordingly, we use the weighted exogenous sampling maximum likelihood (WESML) estimation method developed by Manski and Lerman (1977). WESML provides a consistent estimator if each observation is weighted with the ratio between the population fraction and the sample fraction of the stratum to which it belongs. Inference on precision has to be adjusted; the appropriate covariance matrix is a sandwich estimator; see Ridder and Moffitt (2007) for a detailed econometric overview, and see Ridder (1986) and Amemiya and Yu (2006) for applications in the case of duration analysis. We sample all individuals who experience at least one sanction in the observation window, and take a smaller random sample (14,000) of individuals who do not experience a sanction during this window. This leaves us with about 35,000 spells.

VI. Results

  1. Top of page
  2. Abstract
  3. I. Introduction
  4. II. Unemployment Insurance
  5. III. Theoretical Insights
  6. IV. Data
  7. V. Empirical Model
  8. VI. Results
  9. VII. Displaced Workers
  10. VIII. An Assessment of the Design of the Monitoring Policy
  11. IX. Conclusions
  12. References

Effect of Sanctions on the Exit Rate to Work

Here, we present the estimation results for the duration model in which the only outcome of interest is exit to work. In the following subsections, we examine the effects on post-unemployment outcomes and their implications. The estimates are obtained using WESML with robust standard errors.

Table 5 presents the parameter estimates of the duration model with a sanction effect that is constant over the population and over time. The covariates x contain the characteristics listed in Table 3 and a set of inflow year indicators. The estimate of the sanction effect δ is positive and significant at the 1 percent level. It implies that a sanction increases the transition rate to work by 23 percent. Compared to other studies of UI sanctions effects on the exit-to-work rate, this is rather small. For the Netherlands, Abbring et al. (2005) have found that a sanction doubles the exit-to-work rate. For Switzerland, Lalive et al. (2005) have estimated that the exit-to-work rate increases by about 25 percent if a warning is issued, and by another 25 percent if a sanction is actually imposed. For Denmark, Svarer (2007) has estimated increases of about 50 percent for men and 100 percent for women. This difference with other studies can be explained by the institutional features of the Swedish system. A system of monitoring job offer decisions places a natural upper bound on the sanction effect. This is because even if all offers are accepted, the exit-to-work rate is bounded from above, by the job offer arrival rate evaluated at the optimal search effort in the regime where all offers are accepted. A system where a minimum search effort is imposed after a sanction does not give rise to such an upper bound. Depending on the matching technology, the job offer arrival rate after a sanction might be driven up to high values by increasing the mandatory minimum search effort. Moreover, as we have seen, after a sanction, unemployed workers in Sweden can reduce their effort to zero in order to prevent further job offers and therefore additional punishments.

Table 5. Estimates of duration model for the exit-to-work rate and the sanction rate
 Exit-to-work rateSanction rate
 Est.S.E.Est.S.E.
Notes
  1. The omitted category is individuals living in the central parts of Sweden with less than high-school education who entered unemployment in 1999. Local unemployment is the regional unemployment in percent at the time of inflow.

Sanction effect δ0.2050.035  
Unobserved heterogeneity
v1 and v3−4.6460.151−5.6305.003
v2 and v4−3.3620.153−5.8601.268
inline image0.005   
inline image0.610   
inline image0.248   
inline image0.136   
Individual    
Male−0.0840.0170.0750.039
Education in occupation0.2310.0180.0690.041
Experience in occupation0.0140.018−0.0600.044
Needs guidance−0.0060.0190.0110.049
Log age−0.3730.039−0.4050.088
North0.2320.026−0.0990.059
South−0.0070.019−0.1910.043
High-school education0.1230.021−0.1310.047
University education0.0680.026−0.6320.062
Local unemployment−0.0250.007−0.1000.017
Inflow time    
20000.0150.0250.1650.067
2001−0.0450.0280.1470.074
2002−0.1040.0300.3770.075
2003−0.2500.0280.5000.074
Duration dependence polynomial coefficients
α1inline imageinline imageinline imageinline image
α2inline imageinline imageinline imageinline image
α3inline imageinline imageinline imageinline image
α4inline imageinline image  
α5inline imageinline image  
α6inline imageinline image  
α7inline imageinline image  
Number of individuals16,491   
Number of spells35,055   
Log likelihood−175,709   

Table 5 also reports the estimates for the duration dependence of θe and θs, as sets of coefficients of polynomials. Graphical representations are given in Figures 2 and 3. The exit-to-work rate initially increases, but after about 150 days of unemployment it starts to decrease. After 600 days in unemployment, it is about 30 percent of the value upon inflow. The sanction rate gradually rises with time spent in unemployment. At around 300 days, it attains its maximum value, and after this it is constant. This is, of course, consistent with the fact that sanctions that are imposed because of some violation during an unemployment spell cannot be given at the start of that spell.

image

Figure 2. Estimated duration dependence of the exit-to-work rate

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image

Figure 3. Estimated duration dependence of the sanction rate

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In extended analyses, we allow for temporal and cross-sectional variation in δ. First, we specify δ as inline image. Because the number of observed sanctions is limited, we only include a limited number of variables in x. The results presented in Table 6 show some evidence of heterogeneous effects by gender and age (the other coefficients are very similar to those in the basic duration model, and are therefore not reported). We also interact the regional occurrence of sanctions (the number of sanctions divided by the number of unemployed) with the sanction effect. If stigma is an important part of the sanction effect, the sanction effect might be lower in regions where sanctions are more common. However, we find no such differences. In Section 'Displaced Workers', we report on the heterogeneity of effects by displacement status.

Table 6. Estimates of heterogeneous sanction effect
 Exit-to-work rate
 EstimateStd error
Notes
  1. The model also controls for observed and unobserved explanatory variables. The corresponding parameter estimates are available upon request. Local unemployment is the regional unemployment in percent at the time of inflow. Regional sanction occurrence is the ratio of the annual number of sanctions in the region and the annual mean stock of unemployed in the region, times 1000.

General0.2920.142
Male−0.2020.057
Log (age)−0.3060.129
High-school education−0.0680.069
University education0.0660.085
Local unemployment−0.0170.021
New system0.2220.070
Regional sanction occurrence−0.0330.107
Number of individuals16,491 
Number of spells35,055 
Log likelihood−175,695 

The effect of the sanctions might depend on the elapsed time since imposition. To investigate this, we estimate the specification inline image. If δ2 is negative, then this means that the sanction effect decreases over time. Table 7 reports the estimates of δ1 and δ2. These indicate a persistent effect. The sanction effect on the exit-to-work rate 100 days after imposition equals about 20 percent, compared to 23 percent directly after imposition. This confirms that individuals who have experienced a sanction expect intensified monitoring from the case workers. In addition, second-time offenders are punished harder, increasing the incentive to avoid a violation.

Table 7. Estimates of time-varying sanction effect
 Exit-to-work rate
 EstimateStd error
Notes
  1. Estimates of the other parameters are available upon request.

δ1: instantaneous effect0.2040.043
δ2: dependence on inline image−0.000310.00026
Number of individuals16,491 
Number of spells35,055 
Log likelihood−175,695 

Effects of Sanctions on the Re-Employment Wages and Hours Worked

Table 8 presents the estimates of the model including wage and hours outcomes. The parameters of interest are inline image and inline image, the sanction effect on the wage and hours worked, respectively. Our estimates show negative and significant (at the 1 percent level) sanction effects, both on the wage and on hours worked. A sanction decreases the accepted wage by 3.8 percent. We measure hours worked using an indicator variable taking the value of one for full-time employment, and zero otherwise. Recalculated into marginal effects, this amounts to an increase of the probability to accept part-time work by about 10.3 percentage points, or 15 percent. With a full-time job of 40 hours and a part-time job of 20 hours per week, this implies a mean difference of approximately two hours per week.

Table 8. Estimates of the full model
 Exit-to-work rateSanction rateWageHours worked
 Est.S.E.Est.S.E.Est.S.E.Est.S.E.
Notes
  1. Wage is the full-time monthly wage in SEK, and hours worked is an indicator variable taking the value of one if it is full-time employment, and zero otherwise. Local unemployment is the regional unemployment in percent at the time of inflow.

Sanction effect0.2220.030  −0.0380.007−0.4250.105
Unobserved heterogeneity        
v1 and v3−4.6530.146−5.7260.345    
v2and v4−3.4430.147−5.9120.338    
Prinline image0.041       
Prinline image0.594       
Prinline image0.062       
Prinline image0.303       
inline image and inline image    −0.0730.003−0.3060.080
inline image and inline image    3.3491.5973.2711.656
Individual        
Male−0.0900.0170.0750.0380.0710.0031.5070.050
Education in occupation0.2270.0180.0700.0410.0260.0030.1450.052
Experience in occupation0.0090.018−0.0630.044−0.0040.003−0.0520.054
Needs guidance−0.0170.0190.0140.048−0.0060.003−0.1080.059
Log(age)−0.3580.037−0.4140.0870.0130.006−0.3540.107
North0.2300.025−0.0990.059−0.0130.004−0.1030.066
South−0.0020.019−0.1890.042−0.0160.003−0.0510.052
High-school education0.1220.021−0.1330.0460.0170.003−0.0980.068
University education0.0610.025−0.6320.0590.1130.0040.3920.074
Local unemployment−0.0240.007−0.0990.017−0.0440.001−0.0150.020
Inflow time        
20000.0110.0240.1750.066−0.0090.006−0.3230.108
2001−0.0500.0280.1560.072−0.0220.008−0.3010.154
2002−0.1080.0290.3870.071−0.0090.010−0.4730.178
2003−0.2520.0280.5080.0670.0050.011−0.6040.203
Observation time        
2000    0.0330.0060.7130.111
2001    0.0720.0070.3650.147
2002    0.1100.0090.5200.172
2003    0.1470.0100.7260.195
2004    0.1730.0110.9300.219
2005    0.1880.0191.5210.416
Constant    9.6240.0220.9810.416
σ    0.1330.001  
Duration dependence polynomial coefficients      
α1inline imageinline imageinline imageinline image    
α2inline imageinline imageinline imageinline image    
α3inline imageinline imageinline imageinline image    
α4inline imageinline image      
α5inline imageinline image      
α6inline imageinline image      
α7inline imageinline image      
Number of individuals16,491       
Number of spells35,055       
Log likelihood−176,592       

The signs of the covariate effects on the wage and on hours worked are as expected. Previously unemployed individuals with high-school education have a wage that is, on average, 2 percent higher than if they had less than high-school education. The corresponding number for university graduates is 11 percent.9 Males, highly educated, and unemployed in low employment areas, tend to find full-time employment to a higher degree. This confirms that wage and full-time employment are both perceived as attractive job characteristics.

As discussed in Section 'Data', we also perform analyses with annual labor earnings as post-unemployment outcome. To this end, we replace the wage and hour equations with a single equation for log labor earnings, which is essentially specified like the wage equation. The effect on earnings captures the joint effect on the wage rate and on the intensive and extensive employment margins. Table 9 presents the estimated causal sanction effects in the earnings model. The effect on earnings is significant and indicates that a sanction reduces annual earnings by about 7 percent. This is in line with the sum of the relative effects on wages and hours. This, in turn, confirms that the sample of individuals for whom post-unemployment wages and hours are observed is not selective.

Table 9. Estimates of full model with annual labor earnings
 Exit-to-work rateLog earnings
 EstimateStd errorEstimateStd error
Notes
  1. Estimates of the other parameters are available upon request. The model also includes an equation for the sanction rate.

Sanction effect0.2210.028−0.0670.021

Long-Run Effects of Sanctions

To assess the welfare implications of a sanction and the full magnitude of the punishment, we also need to consider the effects on outcomes after re-employment. We have seen that individuals who have been punished, on average, accept jobs with relatively adverse characteristics. If on-the-job search is inexpensive and job-to-job transitions are frequent, then individuals might be able to move swiftly to attractive jobs, and any systematic difference in characteristics of the first job after unemployment might quickly disappear. Alternatively, a first job with adverse characteristics might cause the individual to spiral into a cycle of frequent job loss and low-wage employment. We investigate this by examining individual labor-market outcomes that prevail several years after re-employment.

First, we estimate three model versions in which the post-unemployment outcomes are the wage and hours worked after two, three, and four years, respectively. Otherwise, the specification is as in the previous subsection. Table 10 presents the estimated sanction effects. We find that sanctions have persistent effects. The estimated average causal effects on wages are −3.4, −4.3, and −4.7 percent when evaluated two, three, and four years after re-employment, respectively (recall that the estimated instantaneous effect is −3.8 percent). These estimates are all significantly different from zero. We find similar negative and significant effects on the long-run probability of full-time work. We conclude that those who have received a sanction do not catch up quickly.

Table 10. Estimates of long-run sanction effects on wages and hours
 Exit-to-work rateWageHours worked
 Est.S.E.Est.S.E.Est.S.E.
Notes
  1. Each panel (one, two, and three years) represents different models. Wage one year after exit is the full-time monthly wage in SEK, and hours worked is an indicator variable taking the value of one if it is full-time employment and zero otherwise, one to two years after the exit from unemployment, and so on. Each model also includes controls for observed and unobserved variables. The models also include equations for the sanction rate. Estimates of the other parameters are available upon request.

One year later0.1360.035−0.0340.010−0.7090.146
Log likelihood−167,440    
Two years later0.2140.030−0.0430.010−0.7780.158
Log likelihood−167,336    
Three years later0.2080.034−0.0470.017−0.5300.197
Log likelihood−176,429    

In these analyses, we right-censor individuals at the moment that they exit from their employment spell into unemployment or non-participation. However, those are relevant events in their own right. Therefore, we also examine empirically whether the occurrence of a sanction affects such events. The outcomes that we consider are, as measured from re-employment, (i) the duration until subsequent unemployment, and (ii) the duration of the non-interrupted employment spell. In addition, we consider (iii) the duration until the individual leaves the firm where the re-employment occurs. The third outcome is informative on the job duration, and hence on the relevance of on-the-job search and job-to-job transitions. To simplify the analysis, we estimate proportional hazard models for these outcomes. The results in Table 11 show that sanctions do not affect these outcome measures. This suggests that transitions between jobs and between labor-market states do not mitigate or enhance the effect of sanctions. The persistency of the sanction effect is propagated by the wage and the working time factor within employment. Clearly, additional years of data would enable a more comprehensive analysis of long-run effects across consecutive individual labor-market states and transitions.

Table 11. Estimates of the effect of a sanction on the time in employment
 Estimated hazard rateS.E.
Notes
  1. Re-unemployment time is the time from the end of the unemployment spell and the start of a new unemployment spell. All models estimated using the Cox proportional hazard model with control for gender, education and experience in occupation, whether guidance is needed, age, residence area, year when the unemployment spell starts, level of education, and local unemployment rate. All variables are measured at the start of the first unemployment spell.

Model 1: Re-unemployment time  
Sanction effect−0.02710.032
Model 2: Time in employment  
Sanction effect0.04480.0353
Model 3: Time in the same firm  
Sanction effect0.03720.0349

Next to wages, hours, and employment, another relevant long-run outcome is the type of occupation in which the individual ends up. Ending up in a job with a lower occupational level might have more adverse long-run implications than ending up in a job with a lower wage in the pre-unemployment occupation. In an occupation that requires fewer skills, the individual might not fully exploit his education and experience, entailing a loss of human capital. This loss becomes irreversible because human capital depreciates over time. Therefore, it might be more difficult for the individual to move out of a bad job match if the job has a lower occupational level. This makes it important to know whether sanctions more often lead to a job with a lower occupational level.

Thus, we extend the model framework by including occupations as outcomes. We allow the selection into occupations to be driven by observed and unobserved explanatory variables, as well as by whether a sanction has been received. We distinguish between an ordered logit specification for the occupational level (four ordered values) and a linear specification for the mean number of years of schooling for the occupation. In both cases, the specification are analogous for those in equations (9) and (10), with normally distributed error terms. The unobserved determinants are assumed to satisfy inline image.

Table 12 presents the estimation results. The upper panel displays the results for the four ordered levels, while the lower panel displays results for the years of education corresponding to the occupation. For brevity, we only report the sanction effects. All models indicate a negative effect of a sanction on the qualification level. The effect on the ordered levels is not significant. Most likely, this is because these groups are broadly defined. For the other approach, we find significant effects. A sanction causes unemployed individuals to accept employment within an occupation that, on average, requires 0.04 to 0.05 fewer years of schooling. In other words, unemployed individuals who experience a sanction, on average, switch into a slightly less qualified occupation, resulting in a loss of human capital. Because of the existence of separate educational tracks, this is likely to be a lower bound of the true loss.

Table 12. Estimates of sanction effect on type of occupation
 Exit-to-work rateOccupation level
 Est.S.E.Est.S.E.
Notes
  1. The four categories represent different sets of results. The four-level official classification is an ordered logit specification for the official SSYK classification of the occupations. Classification by years of schooling classifies the occupations by the mean years of schooling among all employed in that group of occupations, at the one-, two-, or three-digit level. Each model also includes controls for observed and unobserved variables. Estimates of the other parameters are available upon request.

Four-level official classification   
Sanction effect0.1360.032−0.0300.177
Log likelihood−182,041  
Classification by years of schooling   
One-digit occupation: sanction effect0.2560.030−0.0360.016
Log likelihood−183,391  
Two-digit occupation: sanction effect0.1510.029−0.0380.020
Log likelihood−175,157  
Three-digit occupation: sanction effect0.1960.028−0.0470.026
Log likelihood−182,041  

Sensitivity Analyses

As a first sensitivity analysis, we aim to inquire whether the estimated sanction effects are sensitive to our decision to halt time during participation in an ALMP program. If we take the opposite approach (i.e., treating program participation as regular unemployment), then measured unemployment durations increase, and the estimated mean level of the exit rate into work becomes lower. The estimated sanction rate is not affected much because 79 percent of those sanctioned have not had any ALMP experience before the imposition of the sanction. More importantly, the estimated sanction effect on the exit-to-work rate increases from 0.222 to 0.304 (standard error of 0.03 in each case). The increase occurs because those who are not sanctioned at, say, an elapsed duration t are more likely to spend some time in ALMP after t. For post-unemployment outcomes, the estimates are smaller than those in the previous subsections. The sanction effects on the wage and on hours go from −0.038 to −0.019 and from −0.425 to −0.270, respectively, with standard errors similar to before, so that the effects are still significantly negative. We conjecture that these alternative estimates are less likely to be correct than those in the previous subsections, because exit to work and sanctions basically do not occur during ALMP participation.

If the estimated sanction effects on a particular post-unemployment outcome (e.g., the wage) depend on whether the model also includes other post-unemployment outcomes (e.g., hours), then this indicates that the model specification is too restrictive. This does not occur in our analyses. For example, if the hours equation is omitted from the full model, then the estimated inline image equals −0.035, rather than −0.038 in Table 8. The estimate remains significantly different from zero.

Recall that the addition of mass points in the heterogeneity distribution does not improve the fit of the model. We also estimate the full model without unobserved heterogeneity, to study the robustness of the results with respect to this. As is common in the comparison of estimates of MPH model versions with and without unobserved heterogeneity, the covariate effects in θe are larger for the former version, while their relative sizes, signs, and p-values are similar (see Van den Berg, 2001). In accordance with this, the estimated sanction effect on the exit-to-work rate in the absence of unobserved heterogeneity is smaller than in Tables 5 and 8, but it is still significantly positive (estimate 0.13, standard error 0.03). The estimates for θs are almost the same as before, which is not surprising either, given the small amount of unobserved heterogeneity in θs in Tables 5 and 8. The estimates of the sanction effects on the wage and hours outcomes are larger than those for the model with unobserved heterogeneity (−0.047 and −0.47, with standard errors 0.007 and 0.11, respectively). According to a likelihood ratio test, the exclusion of unobserved heterogeneity does lead to a strongly significant deterioration of the fit of the model.

VII. Displaced Workers

  1. Top of page
  2. Abstract
  3. I. Introduction
  4. II. Unemployment Insurance
  5. III. Theoretical Insights
  6. IV. Data
  7. V. Empirical Model
  8. VI. Results
  9. VII. Displaced Workers
  10. VIII. An Assessment of the Design of the Monitoring Policy
  11. IX. Conclusions
  12. References

Empirical Specifications

We have argued that sanction effects on wages can be interpreted in a different way, and can have different magnitudes for displaced workers compared to non-displaced unemployed workers. Suppose that sanctions are mostly given to displaced workers, that displaced workers tend to remain unemployed if they do not receive a sanction, and that their sanction effects are larger than for others. A simple comparison of accepted wages of sanctioned and non-sanctioned individuals might then give biased results because this effectively amounts to the comparison of accepted wages of displaced and non-displaced workers.

The empirical model of Section 'Empirical Model' allows for systematic unobserved heterogeneity, and in principle it can deal with the presence of different types of individuals who have systematically different sanction rates, exit-to-work rates, post-unemployment outcomes, and sanction effects, even if we do not observe to which type a sample member belongs. However, estimation of the empirical model does not allow for boundary cases where all sanctions are only given to displaced workers, and the results might be unreliable in the neighborhood of such boundary cases. Moreover, it is questionable whether a discrete distribution with a small number of mass points for inline image is sufficiently flexible to capture the heterogeneity due to the displacement status. Last but not least, it is interesting in itself to know how the model parameters depend on the displacement status of the individual. Therefore, we proceed to estimate the empirical model conditional on displacement status, by including the displacement indicators described in Section 'Data' as additional elements of x and as determinants of the sanction effects.

Empirical Findings

Recall that the displacement indicators consist of summary measures of the individual unemployment history, the fate of the firm around the time of the transition from unemployment to employment, and the individual labor-market history of this employer and its sector. Table 13 presents descriptive statistics for those who are observed to receive a sanction and those who are not. The two groups are remarkably similar in terms of the distributions of the displacement indicators as well as in terms of important socioeconomic characteristics. This is a first indication that sanctions are not predominantly given to displaced workers. Note also that the newly unemployed workers do not commonly come from firms experiencing a plant closure or a mass lay-off. This precludes the estimation of separate models for those categories of workers.

Table 13. Sample statistics of displacement indicators by sanction status
VariableNo sanctionSanction
Notes
  1. Sector is defined at the two-digit level. Standard deviations are given in parentheses.

Number of observations32,1142,941
Displacement status
Firm with more than 10 employees (percent)83.785.2
of which  
Plant closure (percent)2.01.7
Mass lay-off 75–99 percent (percent)1.61.7
Mass lay-off 50–75 percent (percent)1.81.8
Mass lay-off 30–50 percent (percent)3.63.5
Unemployment history: days in unemployment
One year before start of spell96.7 (113.8)115.3 (127.3)
Two years before start of spell203.3 (211.8)233.9 (233.9)
Three years before start of spell317.8 (307.6)366.2 (337.0)
Four years before start of spell437.7 (402.7)501.6 (437.3)
Five years before start of spell561.2 (494.4)641.0 (535.3)
Six years before start of spell684.0 (580.8)778.7 (628.1)
Time between previous and current unemployment spells
0–100 days (percent)24.130.4
101–365 days (percent)37.932.3
366–730 days (percent)12.113.3
731–1,095 days (percent)5.64.6
1,096–1,460 days (percent)3.53.6
1,461–1,825 days (percent)2.62.5
1,826+ days (percent)14.313.3
Time employed in the same firm
One year before start of spell (percent)54.451.6
Two years before start of spell (percent)18.919.9
Three years before start of spell (percent)9.18.6
Four years before start of spell (percent)5.56.6
Five to six years before start of spell (percent)5.55.6
Seven+ years before start of spell (percent)6.77.7
Time employed in the same sector
One year before start of spell (percent)31.926.1
Two years before start of spell (percent)24.923.9
Three years before start of spell (percent)20.324.5
Four years before start of spell (percent)5.35.3
Five to six years before start of spell (percent)6.26.6
Seven+ years before start of spell (percent)11.513.5

Table 14 presents estimates for models in which the displacement indicators are included. We allow heterogeneity by displacement status in the sanction effects on the exit-to-work rate, the wage rate, and hours worked. Note that the model specifications do not condition on the pre-unemployment wage,10 and the average estimated effects of the displacement indicators on post-unemployment outcomes might reflect this. In any case, we do not find the sanction effects to be strongly heterogeneous by displacement status. In addition, displaced workers have significantly lower sanction rates. We deduce from all this that sanctions are not primarily used to serve as a wake-up call for displaced workers. Furthermore, at least in most cases, the long-run adverse effects of sanctions are a consequence of the punishment itself rather than a consequence of the job loss leading to the unemployment. The estimates of the model parameters not listed in Table 14 are virtually equal to those in Table 8 for the main specification.

Table 14. Estimates for models controlling for the displacement status of the worker
 Exit-to-work rateSanction rateWageHours
Notes
  1. All models also control for observed and unobserved explanatory variables. The estimates of the other parameters are available upon request. Standard errors are given in parentheses.

Model 1: displacement = plant closure or mass lay-off 
General sanction effect0.223 −0.034−0.626
 (0.031) (0.0077)(0.112)
Sanction * displaced−0.0013 −0.0480.252
 (0.089) (0.026)(0.419)
Displaced0.039−0.1670.0280.310
 (0.025)(0.062)(0.005)(0.098)
Model 2: unemployment during year before start of spell 
General0.283 −0.043−0.432
 (0.037) (0.0092)(0.137)
Sanction * days/100−0.045 0.0056−0.170
 (0.022) (0.0062)(0.099)
Days/100−0.0800.087−0.019−0.024
 (0.0068)(0.015)(0.0016)(0.027)
Model 3: unemployment during 0–6 years before start of spell 
General0.261 −0.052−0.367
 (0.044) (0.011)(0.171)
Sanction * days/100−0.0042 0.0024−0.031
 (0.0045) (0.0013)(0.020)
Days/100−0.0210.0017−0.0044−0.014
 (0.0014)(0.0031)(0.00032)(0.0051)
Model 4: tenure in the firm before unemployment 
General0.200 −0.036−0.498
 (0.033) (0.0085)(0.126)
Sanction * (>2 years)0.059 −0.0084−0.283
 (0.061) (0.0177)(0.235)
(>2 years)−0.127−0.0620.0014−0.077
 (0.0174)(0.042)(0.0041)(0.061)
Model 5: uninterrupted employment in the sector before unemployment 
General0.255 −0.037−0.548
 (0.032) (0.0084)(0.120)
Sanction * (>3 years)−0.135 −0.0032−0.086
 (0.067) (0.019)(0.260)
(>3 years)−0.128−0.085−0.0093−0.197
 (0.019)(0.044)(0.0043)(0.065)

We also consider the role of displacement in sanctions effects on post-unemployment log annual labor earnings. This enables the use of a larger sample. We focus on the displacement indicator based on plant closures and mass lay-offs. The point estimate of the coefficient for the displacement interaction term in the sanction effect on earnings equals −0.0041 and is insignificantly different from zero (standard error 0.062). This confirms the results in Table 14.

A limitation of the estimated models with displacement indicators is that they do not distinguish between older and younger displaced workers. Displacement might be a stronger determinant of behavior if the individual is relatively old, because in that case it is many years ago since general education was received, and it is many years ago since the moment of entry into the labor market and the corresponding assessment of the market value. Table 15 presents estimates for models in which the role of the displacement status in the sanction effects might depend on age. The estimates clearly indicate that there is no strong evidence of such interactions with age.

Table 15. Estimates for models where the sanction effects for displaced workers depend on their age
 Exit-to-work rateSanction rateWageHours
Notes
  1. All models also control for observed and unobserved explanatory variables. The corresponding parameter estimates are available upon request. Standard errors are given in parentheses.

Model 1: displacement = plant closure or mass lay-off 
General sanction effect0.222 −0.033−0.624
 (0.031) (0.0077)(0.112)
Sanction * displaced0.012 −0.0500.274
 (0.0084) (0.029)(0.537)
Sanction * displaced * (age >35)−0.030 0.00840.014
 (0.17) (0.058)(0.80)
Displaced0.039−0.1670.0280.311
 (0.025)(0.062)(0.005)(0.098)
Model 2: unemployment during year before start of spell 
General0.281 −0.0421−0.438
 (0.037) (0.0093)(0.137)
Sanction * days/100−0.016 0.0018−0.21
 (0.030) (0.0085)(0.136)
Sanction * days * (age > 35)/100−0.047 0.0061−0.255
 (0.033) (0.0094)(0.156)
Days/100−0.0800.086−0.019−0.024
 (0.0069)(0.015)(0.0017)(0.027)
Model 3: unemployment during 0–6 years before start of spell 
General0.261 −0.052−0.366
 (0.044) (0.011)(0.172)
Sanction * days/1000.004 0.0021−0.029
 (0.035) (0.0017)(0.026)
Sanction * days * (age > 35)/1000.017 −0.0045−0.014
 (0.0014) (0.032)(0.0051)
Days/100−0.0084−0.0210.035−0.341
 (0.0056)(0.0032)(0.168)(0.251)
Model 4: tenure in the firm before unemployment 
General0.210 −0.035−0.500
 (0.033) (0.0082)(0.126)
Sanction * (> 2 years)0.071 −0.0068−0.283
 (0.089) (0.025)(0.345)
Sanction * (> 2 years) * (age > 35)−0.023−0.060−0.0035−0.0042
 (0.104)(0.042)(0.030)(0.040)
(>2 years)−0.123 0.0014−0.077
 (0.017) (0.0039)(0.061)
Model 5: uninterrupted employment in the sector before unemployment 
General0.258 −0.037−0.547
 (0.032) (0.0083)(0.120)
Sanction * (>2 years)−0.132 −0.0055−0.082
 (0.095) (0.028)(0.393)
Sanction * (>2 years)*(age > 35)−0.00660.0850.0062−0.018
 (0.12)(0.044)(0.033)(0.470)
(>2 years)−0.127 −0.0094−0.197
 (0.019) (0.0042)(0.065)

We also performed some sensitivity analyses with respect to our definition of a mass lay-off and a plant closure. Specifically, we vary the threshold percentages of the workforce leaving the firm in the year in which the worker enters unemployment. Recall that our default percentage values, taken from the displacement literature, result in small subsamples of displaced workers, so we merely consider a reduction of the mass lay-off threshold from 30 percent to 20 percent of the firm's workforce. This does not lead to major changes in the above results. The interaction coefficients in the sanction effects in Model 1 in Table 14 change marginally, from −0.0013 to 0.0018 (in δ), −0.048 to −0.042 (in inline image), and 0.252 to 0.253 (in inline image). They remain insignificantly different from zero, with the exception of inline image (standard error 0.20). This means that under this wider displacement definition, individuals who are displaced face a larger wage loss upon a sanction than other unemployed individuals. This, in turn, suggests that sanctions for displaced workers do have the characteristic of a wake-up call. The sanction wage effect for displaced workers is roughly twice as large as the effect for non-displaced workers. According to our theoretical insights, this difference reflects a loss in market value upon displacement. This result suggests that sanctions might be a useful policy instrument to influence unemployed displaced workers. In our empirical setting, this is not a quantitatively important phenomenon, because (i) displacement is not common among the unemployed, and (ii) the displaced face a lower sanction rate than the non-displaced. Moreover, the sanction re-employment effect does not empirically vary with the displacement status. All this suggests that an important topic for further research would be to examine the effects of monitoring and sanctions on the jobs accepted by displaced workers.

VIII. An Assessment of the Design of the Monitoring Policy

  1. Top of page
  2. Abstract
  3. I. Introduction
  4. II. Unemployment Insurance
  5. III. Theoretical Insights
  6. IV. Data
  7. V. Empirical Model
  8. VI. Results
  9. VII. Displaced Workers
  10. VIII. An Assessment of the Design of the Monitoring Policy
  11. IX. Conclusions
  12. References

The results lead to a re-assessment of the Swedish system of monitoring and sanctions in UI. We have seen that sanctions upon the rejection of job offers are severe, in the sense that punished individuals end up in significantly less attractive jobs than unpunished individuals. This difference is persistent up to the end of the observation window, which can be as much as five years after unemployment. Basically, every monitoring system has sanctions that involve a negative income effect. Thus, in that sense, we can expect adverse effects of sanctions on post-unemployment outcomes in any system. However, the theoretical results imply that the size of these adverse effects is larger in a system with monitoring of job offer decisions than in a system with monitoring of search effort. With full compliance after a realized punishment, the system with monitoring of job offer decisions entails that punished individuals now have to accept jobs with the least attractive characteristics, whereas the other system entails that punished individuals have to search harder for any possible job.

An additional problem with the monitoring of job offer decisions is that it can create an incentive for certain unemployed individuals to prevent sanctions by reducing their search effort to zero. Such a problem does not exist in systems with monitoring of search effort. All this suggests that the Swedish system could improve if monitoring were focused on job search effort instead of job offer decisions. In addition, the system would benefit if monitoring were carried out by a different individual than the case worker who provides job search assistance. Recall from Section 'Data' that sanctions do not exert a strong ex ante threat effect because of the reluctance of case workers to report violations. It is plausible that a policy change where the focus on monitoring switches to search effort and where the monitoring is no longer performed by the case worker would create a threat effect that increases the exit-to-work rate before punishment, and as such would lead to a reduction of unemployment. This is both because the moral dilemmas that the case workers currently face would be avoided, and because the unemployed would not reduce their ex ante search effort to zero in order to avoid sanctions.

To assess such a policy change, it is also important to gauge the direct monitoring costs of the policies. Unfortunately, no information is available on the costs of the current regime, let alone of counterfactual regimes. Currently, monitoring is a side activity of the case worker who primarily tries to help the unemployed individual with his or her job search. To assume that the monitoring costs equal a fraction, say 20 percent, of the case worker's salary would probably grossly overestimate the true costs. At the same time, more effective monitoring of job search effort is not necessarily expensive either. Van den Berg and Van der Klaauw (2006) have considered, in the Netherlands, the monitoring of search effort performed by separate UI agencies who do not act as intermediaries between unemployed workers and firms with vacancies. The monitoring mainly consists of monthly evaluation meetings at the agency. The cost of monitoring up to a maximum of six months is about 150 euros in total, which is less than 10 percent of the monthly UI benefits level in their sample. Other existing evaluation studies of sanctions and monitoring do not include cost–benefit analyses.

IX. Conclusions

  1. Top of page
  2. Abstract
  3. I. Introduction
  4. II. Unemployment Insurance
  5. III. Theoretical Insights
  6. IV. Data
  7. V. Empirical Model
  8. VI. Results
  9. VII. Displaced Workers
  10. VIII. An Assessment of the Design of the Monitoring Policy
  11. IX. Conclusions
  12. References

We find that sanctions have adverse effects on post-unemployment outcomes. On average, they cause individuals to accept jobs with a lower hourly wage and fewer working hours per week. The estimated average reduction in the accepted wage is 4 percent. The probability to move into full-time employment decreases by about 15 percent. Furthermore, post-unemployment outcomes are also affected in the long run. Sanctions causally increase the likelihood of the acceptance of a job at a lower occupational level. Such decisions are to some extent irreversible, in which case they involve a permanent loss of human capital. Indeed, job-to-job transitions do not mitigate the long-run effects. From a present-value point of view, this means that sanctions entail a substantial welfare loss for at least some of those who have been punished.

Concerning the effects of sanctions on the transition rate into work, we find a significant positive effect. On average, this involves a 23 percent increase. Compared to estimates for the exit-to-work rate in other studies, this is a small effect. At the same time, the Swedish UI sanction rate is much smaller than in most OECD countries.

We explain our findings by additional empirical and theoretical analyses, and we combine the evidence in order to assess the current Swedish monitoring system. Our theoretical analysis derives implications from the fact that Swedish monitoring is primarily focusedon the prevention of job offer rejections. Such a policy has particularly adverse effects on post-unemployment outcomes. Its emphasis on the acceptance of all job offers means that individuals are pushed to modify their behavior towards an acceptance of low-quality jobs. In addition, such a policy might induce certain individuals to reduce their search effort in order to avoid receiving job offers at all. The ex ante effect of monitoring is then perverse for some individuals, with more monitoring implying a lower exit-to-work rate. We view this as a potentially important insight.

We contrast the system with monitoring of job offer decisions to the alternative and more common system with monitoring of job search effort. The adverse effects of sanctions on post-unemployment outcomes might be smaller with monitoring of search effort, because it pushes individuals to search harder for any possible job and not just low-quality jobs. Moreover, the monitoring of search effort is not compatible with the perverse ex ante effect mentioned above.

Our empirical analyses lead us to conclude that case workers use their substantial discretionary power to keep sanction rates low because they feel uncomfortable initiating punishments to their clients. This finding shows how difficult it is to implement monitoring policies if those who carry out the day-to-day monitoring have discretionary power and have personal contacts with the individuals to whom they are supposed to issue punishments. In our case, the findings imply that across our observation window, the monitoring regime does not exert a strong ex ante (or threat) effect.

All this suggests that it is worth considering a switch to a system in which (i) monitoring focuses on job search effort instead of job offer decisions, and (ii) monitoring is carried out by different individuals than the case worker who provides job search assistance. Such a system might lead to a larger threat effect and a smaller ex post effect on post-unemployment outcomes. Obviously, a larger threat effect could lead to lower unemployment durations for many individuals. It would be interesting to shed some more light on these issues by studying spatial and temporal variations in institutions and outcomes in more detail, but the low occurrence of sanctions precludes this avenue. We should note that, in recent years, the Swedish system has gradually adopted the features of monitoring search effort (OECD, 2007).

It is important to point out that the policy changes suggested above cannot be expected to completely rule out adverse effects on post-unemployment outcomes. After all, if those effects are adverse in a system with monitoring of job offer decisions, then they will also be adverse in the other system. This is because in both systems, the sanction involves a negative income effect.

The finding that individuals move more often to a lower occupational level after a sanction might have implications for the more general issue of how steeply benefits should decline as a function of the elapsed unemployment duration. Theoretical studies of optimal UI design do not distinguish between jobs in the same occupation (with opportunities to mitigate the low starting wage through job-to-job transitions) and jobs with a lower occupational level (where long-run opportunities might be less abundant). Such a distinction can shed new light on the optimal balance between moral hazard and the likelihood that unemployed individuals are driven into suboptimal job matches. We leave this as a topic for further research.

In this paper, we have argued that for displaced workers, sanction effects on wages can be explained in an alternative way. Specifically, they might reflect a “wake-up call” effect, signaling to the worker that his subjective assessment of labor-market opportunities after displacement is too optimistic. We show that this leads to a reassessment of the welfare implications of long-run sanction effects. We estimate models controlling for the individual displacement status, and this leads to the following conclusions. First, sanctions are not predominantly given to displaced workers. Second, we do not find strong evidence that the sanction effects are heterogeneous by displacement status. We deduce from this that sanctions are not primarily used as a wake-up call for displaced workers, and in most cases, the long-run adverse effects of sanctions are a consequence of the punishment itself rather than a consequence of the job loss leading to the unemployment. However, in a sensitivity analysis, we do find that displaced workers face a larger wage loss upon a sanction than other unemployed individuals. This suggests that sanctions for displaced workers are a potentially useful policy instrument to activate unemployed displaced workers.

  1. 1

    The case worker assesses the need for program participation if the individual is close to the end of the entitlement period. As a rule, the individual is then assigned to the “activity guarantee”, which includes monitoring activities that are different from those in open unemployment.

  2. 2

    In addition to this, UI benefits can be reduced upon inflow into unemployment, if the individual has left employment without a valid reason or because of improper behavior at the work floor. UI is then suspended for a maximum of 45 days. We do not analyze this type of reduction in temporary benefits because our data do not allow for a distinction between causal effects and selection effects of treatments that start at the beginning of a spell.

  3. 3

    In addition, eligibility is terminated if the individual sabotages cooperation with the employment office, for example by refusing to follow an individualized pathway back to work, possibly with participation in an active labor-market program. In accordance with the definition of unemployment, we regard such eligibility losses as exits from the state of unemployment.

  4. 4

    See also Gray (2003), Abbring et al. (2005), Hofmann (2008), and the US Department of Labor Comparison of State Unemployment Insurance Laws for supplementary information on details for specific countries and states.

  5. 5

    A similar issue arises because we do not observe the wage in the first job for individuals who move into a second job or into non-participation or unemployment in the time period between the end of the unemployment spell of interest and the survey date. Notably, if there is a negative effect of a sanction on the security of the accepted job, then relatively more individuals with sanctions move into unemployment before the date of the wage survey. As these individuals can be expected to have been in the lower end of the wage distribution, this will also cause a bias towards zero in any estimated negative effect of sanctions on wages. If unemployed with sanctions move relatively fast into a second job, with a higher wage, then this also biases the estimate towards zero.

  6. 6

    The sanction period could be shorter, depending on the (subjectively assessed) expected remaining duration of unemployment. However, in practice, only a period of 60 days was used.

  7. 7

    In Section 'Theoretical Insights', we have shown that an increase of q can lead to a reduction of search effort to zero, such that no offers are generated in the first place, and consequently sanctions do not occur. This is potentially only relevant for a subset of individuals whose benefits are high compared to the wages they might earn. Obviously, a zero effort gives rise to extremely long unemployment spells, which is not what we observe after the policy change. Moreover, the estimated ex post causal effect of a sanction does not decrease after the policy change (Section 'Results'), which is hard to reconcile with a strategic reduction of search effort in response to the increased monitoring after a violation.

  8. 8

    A third explanation is that monitoring was virtually perfect in both regimes, but this seems borne out by the motivation for the policy change as well as by the variation in enforcement across case workers. A fourth explanation is that there exists a different policy that has such a strong ex ante threat effect that virtually all workers accept the first offer they receive or leave the labor market to avoid the threat. A candidate could be the participation in an ALMP program after 300 days in order to obtain an extension of UI benefits entitlement (see Black et al., 2003). However, Hägglund (2006), who examines the ex ante effects of ALMP programs in Sweden using social experiments, does not find any strong effects, and in some cases he reports that such effects are totally absent. From our data description, it follows that most unemployed individuals leave unemployment much earlier than at 300 days, and there does not seem to be a large spike of the exit rate out of the labor force just before 300 days. This suggests that this fourth explanation is not the driving force behind our finding either.

  9. 9

    The literature confirms the low returns to education in Sweden; see, for example, Psacharopoulos and Patrinos (2004) and, citing more recent OECD studies, the survey overview by Björklund et al. (2010). Isacsson (2004) has found that compared to pre-high-school education, the returns to high-school education are 26 percent and the returns to university education are 43 percent, which is low by international standards. Wage differences by education directly after unemployment are likely to be smaller than the overall rates of returns to education, for at least two reasons. First, low-educated unemployed workers might have used previous work experience to make up for the difference in initial education. This is confirmed by the finding in Albrecht et al. (2009) that the observed cross-sectional median wage rates among “less than high-school” educated and “high-school” educated employed workers in Sweden differ by approximately 10 percent. Second, the highly educated who are unemployed are most likely a highly selective subset of the highly educated in general.

  10. 10

    This is to maintain a reasonable sample size of sanctioned workers. Displaced newly unemployed workers, on average, do have higher pre-unemployment wages than non-displaced newly unemployed workers.

References

  1. Top of page
  2. Abstract
  3. I. Introduction
  4. II. Unemployment Insurance
  5. III. Theoretical Insights
  6. IV. Data
  7. V. Empirical Model
  8. VI. Results
  9. VII. Displaced Workers
  10. VIII. An Assessment of the Design of the Monitoring Policy
  11. IX. Conclusions
  12. References
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