Mandatory integration agreements for unemployed job seekers: a randomized controlled field experiment in Germany

van den Berg, Gerard J.; Hofmann, Barbara; Stephan, Gesine; Uhlendorff, Arne Article — Published Version Mandatory integration agreements for unemployed job seekers: a randomized controlled field experiment in Germany International Economic Review Provided in Cooperation with: John Wiley & Sons Suggested Citation: van den Berg, Gerard J.; Hofmann, Barbara; Stephan, Gesine; Uhlendorff, Arne (2024) : Mandatory integration agreements for unemployed job seekers: a randomized controlled field experiment in Germany, International Economic Review, ISSN 1468-2354, Wiley, Hoboken, NJ, Vol. 66, Iss. 1, pp. 79-105, https://doi.org/10.1111/iere.12745 This Version is available at: https://hdl.handle.net/10419/323782 Standard-Nutzungsbedingungen: Die Dokumente auf EconStor dürfen zu eigenen wissenschaftlichen Zwecken und zum Privatgebrauch gespeichert und kopiert werden. 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If the documents have been made available under an Open Content Licence (especially Creative Commons Licences), you may exercise further usage rights as specified in the indicated licence. http://creativecommons.org/licenses/by/4.0/ INTERNATIONAL ECONOMIC REVIEW Vol. 66, No. 1, February 2025 DOI: 10.1111/iere.12745 MANDATORY INTEGRATION AGREEMENTS FOR UNEMPLOYED JOB SEEKERS: A RANDOMIZED CONTROLLED FIELD EXPERIMENT IN GERMANY∗ By Gerard J. van den Berg, Barbara Hofmann, Gesine Stephan, and Arne Uhlendorff University of Groningen, University Medical Center Groningen, Netherlands and IFAU Uppsala, Sweden; FEA Nuremberg, Germany; Institute for Employment Research (IAB Nürnberg), Friedrich-Alexander-Universität Erlangen-Nürnberg, Germany; CNRS, CREST, and IAB Nuremberg, 5, Av Henry Le Chatelier, Palaiseau 91120, France Integration agreements (IAs) are contracts between the employment agency and the unemployed, nudging the latter to comply with rules on search behavior. We designed and implemented a randomized controlled trial involving thousands of newly unemployed workers, randomizing at the individual level both the timing of the IA and whether it is announced in advance. Administrative records provide outcomes. Novel theoretical and methodological insights provide tools to detect anticipation and suggest estimation by individual baseline employability. The positive effect on entering employment is driven by individuals with adverse prospects. For them, early IA increase reemployment within a year from 53% to 61%. 1. introduction During the past decades, a view has emerged that Active Labor Market Programs (ALMP) are on average not very effective in bringing unemployed individuals back to work. Specifically, average reemployment effects of participation in training and workfare are often rather low, whereas the effectiveness of job search assistance and monitoring varies with the setting at hand and is typically low for groups with relatively bleak labor market prospects. Crépon and van den Berg (2016) and Card et al. (2018) provide recent overviews, but discouraging findings were already documented and summarized as early as Heckman et al. (1999). The evidence is of concern even in labor markets with favorable conditions, as unemployment may drive individuals out of the regular labor market and, indeed, may lead them to drift away from mainstream society. This has led to a search for different tools to support the placement of the unemployed. In this article, we evaluate one such policy, called mandatory integration agreements (IAs). An IA is a written contract that stipulates rights and obligations of an unemployment insurance (UI) recipient. The signing of this contract takes place upon entry into UI, at the end of the first meeting of the UI recipient, and his/her caseworker in the employment agency.1Both ∗Manuscript received July 2022; revised May 2024. We are grateful to the Editor Petra Todd and two anonymous Referees as well as to Bart Cockx, Bruno Crépon, Jeffrey Smith, Johan Vikström, Michael Visser and participants in conferences in Ghent, Seville, Mannheim, Bonn, Bristol, Augsburg, Groningen and Paris, seminars in Potsdam, Sheffield, Paris (CREST and DARES), Lucca and St Gallen, and a J-PAL summer school, for helpful comments. We thank Christian Rauch for enabling the project, Susanne Koch and Carina Schwarz for their cooperation in the set-up and implementation of the experiment, the “ProIAB” institutional experts of the IAB for their support in implementing the RCT on-site, and the IAB-DIM (in particular Ali Athmani, Steffen Kaimer and Markus Köhler) for their technical and data-related support. The RCT is registered in the AEA RCT registry (0006368); note that the RCT took place before this registry was formally established. We gratefully acknowledge support of DFG SFB 884. Arne Uhlendorff is grateful to Investissements d’Avenir (ANR-11-IDEX-0003/Labex Ecodec/ANR-11-LABX-0047) for financial support. Please address correspondence to: Arne Uhlendorff, CNRS, CREST, IAB Nuremberg. E-mail: [email protected]. 1For ease of exposition, we refer to “being a UI recipient” as “being unemployed.” In Section 2, we discuss subtle differences. 79 © 2024 The Author(s). International Economic Review published by Wiley Periodicals LLC on behalf of the Economics Department of the University of Pennsylvania and the Osaka University Institute of Social and Economic Research Association. This is an open access article under the terms of the Creative Commons Attribution License, which permits use, distribution and reproduction in any medium, provided the original work is properly cited. 80 van den berg et al. the UI recipient and the caseworker should sign the IA. Its content is based on a template of textual building blocks that may slightly vary across occupation and family status but in practice the template is rather uniformly specified. The template reflects existing rules and laws (see also Schütz et al., 2011; and Boockmann et al., 2013, for descriptions of the IA; see also below). Since the IA does not impose constraints that tighten the existing rules, one could argue that it is not being perceived as a monitoring device, at least as long as the unemployed individual is aware of the existing rules. Instead, the design and phrasing of the IA suggest a “nudge” character of the policy. Signing the IA, with its apparently symmetric design with rights and obligations and with its space for two signatures, may be viewed as a sort of ritual that may increase the commitment on both sides and foster a cooperative bond between the unemployed and the caseworker, effectively reducing the disutility of search as perceived by the unemployed. However, the content of the IA consists mostly of a list of obligations on the job search activities on the part of the unemployed worker, such as a minimum number of job applications per time unit. Even some of the stated rights of the unemployed can be seen as veiled threats to comply. Moreover, the caseworker may impose the IA unilaterally if the unemployed refuses to sign, and the resulting contract is legally binding. The punishment for noncompliance with aspects of IA is one-sided and involves UI benefits reductions. With all this in mind, and given the self-reported assessments of the IA by surveyed workers and caseworkers (see Section 2), it is more accurate to view the IA as a combination of a nudge and a refresher on obligations including a reminder of monitoring and potential punishments. As such, the IA may have effects similar to monitoring, where the effects may be stronger because of the nudging that may make the IA a more comprehensive experience than the alternative of a simple confrontation with a list of obligations. We employ a randomized controlled trial (RCT) with randomization at the individual level to evaluate the IA. Specifically, we randomize two aspects of the policy: the timing of the IA and the advance notification of the IA. Randomization takes place upon entry into unemployment. The timing of the IA is randomized over possible elapsed times from entry into unemployment until the IA. One treatment arm involves the IA in the first month, one involves the IA at three months, and one at six months. In addition, we randomize whether those assigned to receive the IA at three months also receive an advance notification of the timing of the future IA at three months, to be received upon entry into unemployment. In total, these constitute four possible treatment statuses, each with a 25% assignment probability. The RCT was carried out in five local labor market regions in Germany. These were chosen for reasons of representativeness but also because they are large, because no ALMP pilots or other evaluations were held there, and no reorganizations took place in the local employment agencies at the time. It was promised to the agencies that their performance ratings would not be affected by the RCT. We use a number of data sources. First, we observe the output of the randomization tool. Second, administrative data on UI recipients provide daily observations on outcomes: ALMP participation (including IA), meetings, covariates, employment spells, and past labor market outcomes. Third, we held a survey of caseworkers working in the agencies that participate in the RCT, one month before the RCT began. Fourth, we carried out a survey of UI recipients around two months after entry into UI. The nonresponse in the UI recipients’ survey was sizeable. For data protection reasons, the survey data can only be linked to the administrative data if the respondent agrees. In particular, most of the caseworkers did not allow merging of their own responses to records of their clients. For these reasons, the survey data are of limited use. We merely use them to informally gauge workers’ and caseworkers’ perceptions of the IA. Our RCT is the first causal evaluation of the IA policy. Also, it is the first large-scale RCT of ALMP in Germany with randomization at the individual level. Note that the combination of monitoring with nudging makes our evaluation potentially relevant for other policies that mandatory integration agreements for unemployed job seekers 81 combine these components, such as devices to discourage tax avoidance.2In addition, some other OECD countries have recently implemented what could be called weak versions of the IA policy (Immervoll and Knotz, 2018; Knotz, 2018), usually without the formal contractsigning ceremony and without threats of enforcement. In our view, an evaluation of the fullblown IA in Germany, with its strong legalistic tradition and adherence to the law, provides an interesting benchmark. We discuss policy differences in more detail in Subsection 2.2. The comparison of those who are notified about a future IA at three months to those who are not is an innovative feature of our study design. This feature connects our article to the literature on anticipation of future treatments (see, e.g., Black et al., 2003; and van den Berg et al., 2009).3Using a search-theoretical framework, we show that the two treatment arms lead to an observationally distinct difference in the reemployment rate around the threemonth threshold. At first sight, it may seem that inference on the latter is hampered by the challenge that randomization is lost when conditioning on survival until close to three months. However, in the article we develop a novel method to detect qualitative features of the reemployment rate that are informative on the presence of anticipation of the treatment at three months and that are preserved if randomization is lost. Clearly, this has wider relevance for the evaluation of anticipatory effects of future events.4 To investigate heterogeneity of effects, we divide the population of unemployed into two groups based on their predicted median unemployment duration until reemployment. Predictions are based on an inflow sample into unemployment from the year before our experiment, conditioning on individual labor market histories and characteristics. We show that local labor market conditions in these years are stable. We split the sample into individuals with a high (above six months) and a low (below six months) predicted median duration and perform sensitivity analyses with respect to this threshold value. We do not use in-sample observations to quantify the prediction model in order to avoid overfitting and the related risk of biased treatment effects (Abadie et al., 2018). Interestingly, our findings already led to a policy change in the use of IAs by the German Federal Employment Agency (FEA). Specifically, by now, individuals who are regarded as having favorable labor market prospects are not obliged anymore to undergo an IA during the first three months of unemployment. 2From a sociological-institutional perspective, IAs can be seen as an example of new public management strategies or new public contractualism with reconstructed citizens—in our case, job seekers—as customers (O’Flynn, 2007). In this view, contracts that define requirements, monitoring, and incentives constitute the legitimate relationship between the state as the principal and the job seeker as the agent. 3Effects of advance announcements and notifications of future treatments are hard to identify because they are often not observed and they may obliterate the very treatment they announce, if they cause an exit from the state that is the eligibility state for the treatment. Nonexperimental studies have relied on policy discontinuities (Blundell et al., 2004; De Giorgi, 2005; van den Berg et al., 2020) or on self-reported assessments of the likelihood of a treatment in the near future under unconfoundedness (van den Berg et al., 2009) or on register data with observed advance announcements in a timing-of-events model setting (Lalive et al., 2005; Crépon et al, 2018). RCTs are uniquely equipped to study anticipation effects because advance announcements are predetermined by the study design. Michalopoulos et al. (2005) find a small increase in the share of individuals who anticipate access to in-work benefits by extending their length of stay on welfare in order to become eligible for those benefits, in the context of the Canadian Self-Sufficiency Project RCT. Büttner (2008) estimates effects of the announcement of participation in a future job search assistance program. However, sample sizes are in the low 100s and he resorts to propensity score methods to deal with implementation issues. 4As indicated above, there is a large literature on effects of job search assistance, counseling and monitoring of unemployed job seekers. Some of this has studied policy measures that cannot be straightforwardly assigned to one of these standard ALMP categories, and in some cases the estimated effects shed a favorable light on their effectiveness. In general, caseworker meetings are deemed to speed up reemployment (see, e.g., Schiprowski, 2020, for a recent example). Altmann et al. (2018) and Belot et al. (2019) find that providing information to unemployed job seekers about job search and labor market opportunities may affect their job search behavior, leading to better employment prospects. Altmann et al. (2018) show that this is especially relevant for job seekers with a low predicted probability of leaving unemployment for a job. Our study extends this literature by providing additional evidence on nonstandard policy measures. Similarly, our study extends the large literature on effects of monitoring schemes (for recent evidence, see, e.g., Lachowska et al., 2015) by examining a new tool combining monitoring with nudging. 82 van den berg et al. The outline of the article is as follows: Section 2 describes the German UI benefit system and IAs. Sections 3 and 4 discuss the setup of the experiment and the data, respectively. Methodological considerations and novel methodological contributions are in Section 5. The empirical results are presented in Section 6. Section 7 concludes. 2. institutional background 2.1. UI Benefits. The German unemployment compensation system has two pillars. The first is UI. As a norm, upon inflow into unemployment, UI eligibility requires that individuals have been working and paying social security contributions for at least 12 months within the period of 24 months immediately prior to unemployment (30 months since 2020). UI benefit recipients have to be registered as unemployed at the FEA. The UI entitlement duration depends on the duration of the prior employment period and the age of the recipient. The highest possible entitlement duration for individuals below 50 years is 12 months. This increases for older individuals, up to 24 months for those aged above 58 if they were employed for at least 48 months in the five years prior to unemployment. The replacement ratio is about 67% for individuals with dependent children and about 60% for those without, with a benefits level cap that is binding for only a small percentage of newly unemployed. After expiration of UI, unemployment compensation is reduced to unemployment assistance or “welfare.” This is the second pillar of the system. Welfare is tax-financed and meanstested, and the level depends on household composition but not on former earnings. In 2012, it equaled around 345 euro per month with supplementary accommodation costs as well as support in case of specific needs. Recipients have to register and receive placement services in job centers that are partly administered by the FEA and partly by municipalities. In the article, we restrict attention to UI benefit recipients. 2.2. Integration Agreements. IAs were introduced as a policy in Germany in 2002.5Ap- pendix 2 provides an actual example of an IA for an unemployed physiotherapist, with a slightly abridged English translation. Most of its content is uniform across all IAs but a few features may vary across occupations. The latter applies in particular to the geographical range of the job search (here: nationwide), the minimum number of applications per month, the maximum time allowed for submitting a list of qualifications to successfully exert one’s occupation (typically one week), and the time until the next meeting (here: two months). As already discussed in Section 1, most of the IA text is about UI recipients’ obligations, and even some of the text on the recipients’ rights can be interpreted as a reminder of obligations or as a veiled threat in case of noncompliance (e.g., that the agency promises to make a phone call if it identifies an appropriate vacancy and in some cases may immediately send an actual job offer). As noted in Section 1, the IA is signed at the end of the first meeting of the UI recipient and his/her caseworker. Before that, the meeting covers formalities such as entering information about the client into the computer system of the FEA, and a discussion of plans for job search and future participation in ALMP. This includes the information on occupation, qualifications, and household status that may affect the few open details of the IA to be signed. According to our survey among caseworkers (see Subsection 2.3), the first meeting usually takes about 50 minutes, and of these, about 15 minutes are used for the IA. Regarding the timing of the first meeting, we should point out that individuals are required to register as a job seeker three months before unemployment entry or—if they do not know about this three months in advance—as soon as they receive a dismissal note. As a result, the first meeting with a caseworker can take place before the actual unemployment entry as well. (In our RCT, however, 5The law covering the policy throughout the 2010s is written in the Social Code II Section 15 and the Social Code III Section 37. mandatory integration agreements for unemployed job seekers 83 all caseworkers were instructed to conclude the first IA only after the actual unemployment entry; see Section 3.) The assignment of caseworkers to clients is quasi random and is typically governed by the first letter of the last name of the client, by the first or last digits of various codes that the individual bears, and by who is the first available caseworker when the client enters the agency for the first meeting. As a rule, the client keeps the same caseworker throughout his/her UI spell. There is no space for discretionary behavior by the caseworker regarding the contents of the IA. However, it is possible that the individual impact of the IA depends on the caseworker’s behavior. We return to this in the results section. After the first meeting, the caseworker only updates the IA if strictly necessary, for example, if the unemployed hands in a disability note. Apart from this, the IA is typically updated after at least six months (for those aged 25+), to take changing circumstances and completed ALMP participation into account.6 If the UI recipient is found not to comply with the obligations and guidelines on search behavior and ALMP participation, whether they are mentioned in detail in the IA or not, then (s)he may receive a punishment in the form of a benefits reduction (i.e., a sanction). These are relatively severe, typically involving a full benefits withdrawal for at least one week, where the length of the period depends on the type of violation. A second detected violation may lead to a complete UI benefits withdrawal for more weeks. Various countries have adopted policies that share features with the IA policy. In 2016, the Council of the EU issued guidelines to the member states on the policy mix to integrate the long-term unemployed into the labor market (EU, 2016). One aspect of this concerned “job integration agreements,” which should define goals and obligations of the unemployed person and the counseling, help, and support measures by the service provider. A recent critical interim assessment (EU, 2021) observes that countries have taken varied approaches and complains that many countries are actually slow to implement it and many do not have a full-blown system. Often, the “job integration agreements” in place only prescribe counseling, assistance, training, and the provision of information to the unemployed, sometimes complemented with advice on childcare services, health services, and debt counseling (see also European Commission, 2019). The German IA policy is praised as a policy that fulfills the original EU guidelines. In this sense, our evaluation provides valuable insights for the other EU countries. 2.3. Self-Reported Perceptions of IA among Caseworkers. To gauge caseworkers’ perceptions and assessments of the IA for UI recipients, we held a short survey in June 2012, that is, one month before the RCT began, among caseworkers in the participating agencies.7Unit nonresponse was 28% and there was also substantial item nonresponse, resulting in a total of 159 respondents who answered each question used in this subsection. The survey was set up as a list of statements for each of which the caseworker could indicate his or her agreement. We observe that 16% of the respondents agree mostly or fully with the statement that IAs are supportive for the job seekers in their search for work. Next, 19% agree mostly or fully with the statement that IAs help the job seekers to claim their rights. Conversely, 74% state that they use the IA at least to some extent to control the effort by the job seeker (i.e., to monitor the job seeker). These numbers confirm the descriptions of the nature of the IA in Section 1 and Subsection 2.2. Regarding the contents of the IA agreement, the caseworkers’ responses support our above descriptions as well. The survey also reveals that caseworkers envisage IA effect heterogeneity. On average, they believe that IAs do not increase the reemployment probability of individuals who have a good connection to the labor market and who can be expected to find work on their own within half 6Before or after the IA is signed, caseworkers may profile their clients according to their assessment of the support they need. These are not in the data used in this article but our extended analysis allows effects to differ by an index of individual characteristics and labor market history. 7Preliminary findings from this survey were reported in German in van den Berg et al. (2014). 84 van den berg et al. a year. They tend to view IAs as more useful for individuals who in their view need to be activated and/or receive job search assistance or training. Of course, it is not clear whether the views on the usefulness of such support precede the views on the usefulness of an IA. But it appears that the usefulness of an IA is regarded to be higher if the individual does not have excellent prospects. We also conducted a short survey among a sample of participants in the experiment. Again, the unit and item nonresponse was sizeable. More importantly, unit nonresponse was not balanced across treatment groups,8which is why we mostly do not use the survey responses. The survey was again set up as a list of statements for each of which the respondent could indicate his or her agreement. The survey was held around 1.5 months after unemployment entry and the questions relating to the IA were only put forward to respondents who (and were assigned to have) received the IA in the first month. In the resulting small subsample of 127 individuals, less than half (44%) agree mostly or fully that IAs are supportive in their search for work. However, a much larger fraction (80%) feels that the IA serves as a reminder of their obligations during their search for work. And 78% agrees with the statement that the IA is a tool with which the caseworker can control the individual (i.e., to monitor the job seeker). Here, it should be kept in mind that the respondents are informed that the survey is carried out by the Institute for Employment Research (IAB, which is the main research and data institute of the FEA) among employment agency clients. Although they are also informed that responses are strictly confidential, some may have given answers that they deem to be desired by the FEA, so that the actual assessment of IAs may be even more tilted toward monitoring and away from counseling. 3. experimental design 3.1. Treatment Arms. We randomize two aspects of the policy: the timing of the IA and the advance notification of the IA. Randomization takes place at the individual level upon entry into unemployment. We allow for four treatment arms. In treatment arm A, the IA is supposed to be signed in the first month of unemployment. In treatment arms B and C, this is supposed to occur three months after entry (if the individual is still unemployed), and in treatment arm D the signing is supposed to take place for the first time six months after entry (again conditional on unemployment). Treatment arms C and D do not include an advance notification of the future IA. In contrast, treatment arm B involves the receipt of a written announcement during the first meeting with the caseworker, informing the individual about the requirement to sign an IA in the third month of unemployment. This includes a detailed description of the typical content of IAs. In addition to that, it states that noncompliance with the content of the IA may lead to a sanction in the form of benefits cuts (see Appendix 3 for the exact wording of the announcement). In other words, treatment arm B provides an advance announcement that the rules the individual will have to comply with will be announced and fixed within an IA in around three months. Table 1 summarizes the treatment arms. Each of the four possible treatment statuses in the RCT is given a 25% assignment probability. The Social Code legal framework does not allow for an RCT with a treatment arm in which the individual is never confronted with an IA. Similarly, it was not possible to randomize parts of the contents of the IA, so we could not introduce random variation, for example, in the number applications per week or in the highest commuting time deemed acceptable for offers provided to the individual. Note, however, that this would have increased the number of treatment arms considerably, which would be impractical and would lead to underpowered inference at given sample sizes. However, 8Replication of the estimation of treatment effects based on the subset of the administrative data that exclusively contains the potentially selective sample of survey respondents leads to results that are qualitatively different from those based on the full sample. Several of the estimates (but not all) are outside the confidence intervals of the estimates based on the main sample. mandatory integration agreements for unemployed job seekers 85 Table 1 experimental design Group IA in Month IA Announced A1 No B3 Yes C3 No D6 No Note: IA: integration agreement. IA announced: written announcement on IA handed out in the first month of unemployment. these policy variations represent compelling candidates for future field experiments that could enhance our understanding of how different components of the IA impact employment outcomes. 3.2. Implementation of the RCT. We set up the experiment in five regional employment agencies out of a total of around 180 nationwide.9The agencies were selected on the following criteria. First, during the time of the experiment (2012–13), they hosted no other pilot projects, for example, for the evaluation of other active labor market policies. Second, during this time, they did not face any other organizational changes, restructurings, or mergers. Third, the regions they served should not be too small in terms of population, to safeguard the sample size. In June 2012, around 2.8% of all unemployed individuals in Germany were registered at one of the five agencies. Fourth, they had to be dispersed across East and West Germany and across rural and urban regions, jointly creating some representativeness. The unemployment rate averaged across the five agencies does not differ from the national average (6.7% vs. 6.8%; both measured in June 2012). However, unemployment rates range from 2.5% in a Bavarian agency to 12.0% in an East German agency in the RCT. The agencies were informed by the FEA that they were selected to participate in the RCT. To prevent that the agencies’ performance ratings would be affected by the work for the RCT or by the outcomes of clients involved in the RCT, it was communicated that RCT participation would not affect their performance goals.10 At each of the five agencies, two representatives of the FEA and of the research team presented the RCT to the agency head. FEA experts conducted instruction lessons with team leaders of caseworker teams in participating agencies before the project started (teams usually consist of 5 up to 15 caseworkers). The caseworker team leaders, in turn, instructed single caseworkers. The research team designed instruction material consisting of a presentation, a FAQ list, and a two-sided plastic slide summarizing the experimental design which was meant to be placed on each caseworker’s desk throughout the experiment. The presentation highlighted the importance of the research question and why it could only be answered by means of an RCT. The material included verbal and graphical descriptions of the treatment arms. The target population was described and it was emphasized that other elements of the placement process were not supposed to differ across treatment groups, and in particular that all groups should have the same degree of access to ALMP instruments. Follow-up information was made available by e-mail and telephone. The target population of the experiment is the full set of new entries into unemployment in the five employment agencies between July 2012 and January 2013. Individuals who were 9The RCT design was approved after an internal review by the IAB Project Approval board and after a critical review by the legal department of the FEA, without the imposition of any additional constraints on the proposed design. 10 Each year, the FEA headquarters agrees on targets for the regional directorates through framework agreements with the Federal Ministry of Labor and Social Affairs. The regional directorates then agree on corresponding targets with their local employment agencies. These targets cover aspects such as the share of integrations into employment and the average duration of unemployment (Kaltenborn et al., 2010). If the local units do not meet targets, regional directorates may suggest measures for improvement (Kaltenborn et al., 2010). 86 van den berg et al. eligible for UI were supposed to participate in the trial, where those aged below 25 or registered as unemployed anytime in the quarter prior to the current unemployment spell were excluded. This is because those categories faced different institutional environments and/or placement processes. We also exclude females because parental leave is not observable in the data and cannot be identified as distinct from unemployment. Parental leave spells can take up to three years and are usually taken up by the mother of the child instead of the father.11 In the first meeting between the caseworker12 and a newly unemployed individual in the target population, the latter was randomly assigned with equal 25% probabilities to one of the four treatment arms.13 The randomization is triggered by the caseworker during the meeting. The caseworker had to open an app and enter the client’s identification number, name, and date of birth into a computer system. Both the app and the system were developed by the FEA for evaluation studies. The system generates a random number (not based on above characteristics) which then determines the assigned treatment status. In the RCT, the assigned status was immediately displayed in the caseworker app and the caseworker had to acknowledge it by entering it into the usual placement software program. This stores the time and the randomization outcome as well as anonymized identifiers of the client and the caseworker. Caseworkers were not able to manipulate the randomization, for example by rerunning the randomization. Importantly, the unemployed individuals were not informed about the RCT.14 It is also important to note that the protocol specified that the content of the IAs cannot be influenced by the randomized treatment. However, it is possible that the content of the IAs that were signed in later months (typically six months or later after inflow) systematically differs from the content of earlier IAs. We regard such potential differences as part of the treatment. It is also possible that the treatment assignment influenced the frequency of subsequent meetings between the unemployed and the caseworker or that it influenced ALMP access. We will address this aspect in more detail below. 4. data 4.1. Administrative Databases. The empirical analysis uses administrative data of the IAB of the FEA.15 These consist of individual records for the full labor force, notably from the so-called IEB. The IEB contains sociodemographic individual characteristics and detailed employment and unemployment histories, including daily earnings, transfer payments, and participation in ALMP, sanctions, and meetings with caseworkers. The IEB does not contain detailed information about working hours and self-employment but we observe self- 11 Schönberg (2009) develops an algorithm for detecting maternal leave in the same IEB (integrated employment history register) data that we use as well, but this presupposes that the mother is in an employment relationship at the onset of the leave period, whereas in our setting the leave period would start during an unemployment spell. Note that even in the absence of these issues, the sample size for women would be substantially smaller than the size of our sample of men, causing any analysis of the former to be underpowered. 12 In our experiment, all caseworkers were instructed to deal with the IA and IA-related issues only after the actual unemployment entry. 13 In an additional fifth group, the unemployed were assigned to be treated “as usual” with respect to the IA. Adding this group was a request of the involved department at FEA headquarters. The treatment “as usual” typically corresponds to an early IA during the first meeting with the caseworker. There were no clear instructions for the caseworkers for this group, so it is hard to interpret findings for this group, and, indeed, the outcomes for this group may be affected by the ongoing RCT. Therefore, we exclude this group from the analysis. However, we include a brief presentation of our findings for this group in a sensitivity analysis in Subsection 6.3. 14 In such evaluation designs at the FEA, the default would be to obtain informed consent. This can be disposed of if this would plausibly induce selection and if there is no convincing prior evidence that a participant will be worse off because of participation. If consent is not required, informing the participants about the experiment can be disposed of if the latter would plausibly induce changes in behavior and could thus invalidate the RCT. 15 We use databases called IEB version V12.01.00 and ASU-EEI version V06.09.00-201604. These are social data with administrative origin which are processed and kept by IAB according to Social Code III. The data contain sensitive information and therefore are subject to the confidentiality regulations of the German Social Code (Book I, Section 35, Paragraph 1). mandatory integration agreements for unemployed job seekers 93 0.00 0.25 0.50 0.75 1.00 0 100 200 300 400 500 600 700 Unemployment duration in days Kaplan–Meier survival estimates Notes: Solid: IA in month 1 (Group A), long dash: IA in month 3 with announcement (Group B), dot: IA in month 3 without announcement (Group C), dash dot: IA in month 6 (Group D). Number of observations: 4,163. Figure 2 kaplan–meier estimates of the survival function until exit to work edge this benefit of nudging in advance then, before τ, this would make the future event less unattractive in the eyes of individuals in group B. This could mitigate the size of the differences between the effects of B and C before τ. Second, individuals in C may expect the IA event to occur at some rate η, in which case the IA has a so-called ex ante effect. This also tends to mitigate the size of the differences between B and C. Third, note that up to τ,the groups C and D behave identically on average, so for the above purposes D may be added to C on that time interval. 6. results 6.1. Average Effects. Figure 2 shows Kaplan–Meier estimates of the survival function until exit to employment, that is, estimates of the probability of having found a job as a function of the time tsince the start of the unemployment spell. Note that we do not censor observations if they leave registered unemployment without entering employment directly. Therefore, the estimated survival rate at a duration tsimply equals the ratio of the number of individuals at risk (i.e., who have not found a job yet) divided by the size of the corresponding treatment group. We discuss standard errors of estimated effects in binary-outcome analyses below, so the discussion of the estimated functions is brief. The estimated functions for the four groups are virtually indistinguishable in the first 120 days after unemployment entry. This suggests that signing an IA very early has on average no short-term impact on the probability of getting a job. At higher durations (around the median of about 200 days) individuals assigned to group D have a lower probability of having entered employment. There seem to be no systematic differences between groups A, B, and C. Next, we estimate linear probability models. In what follows, we take treatment arm D (not-previously announced IA at six months) to be the reference category. The outcome yit is 94 van den berg et al. Table 3 exit to work within 90,180,270,and365 days after unemployment entry Until Day:90 180 270 365 Coef. S.E. Coef. S.E. Coef. S.E. Coef. S.E. A 0.007 (0.019) 0.022 (0.021) 0.027 (0.020) 0.041** (0.019) B−0.010 (0.019) 0.001 (0.021) 0.021 (0.020) 0.033*(0.020) C−0.003 (0.019) 0.022 (0.021) 0.024 (0.020) 0.047** (0.019) Mean D 0.254 0.474 0.589 0.650 Note: Linear probability models. Dependent variable is one if an individual has found a job within 90/180/270/365 days after unemployment entry. Number of observations: 4163. Group A: IA in month 1. Group B: IA in month 3 with announcement at first meeting. Group C: IA in month 3 without announcement. Reference group is D: IA in month 6. Significance levels: *10%, **5%, ***1%. Individual controls included but not shown: age, nationality, education, previous wage, handicap, and previous employment history. a binary indicator which is one iff an individual imoved to subsidized or unsubsidized work before t, and Ai=1iffiis assigned to group A, etc. yit =β0+AiδA+BiδB+CiδC+εit .(4) We also estimate versions including a vector xicontaining individual characteristics like age, nationality, education, last observed daily earnings, and other labor market history indicators. Table 3 reports the latter results, for tequal to 90, 180, 270, and 365 days. Not surprisingly, the results without xiare virtually identical to those in the table. The coefficients for A, B, and C are close to zero and insignificant at 90 days after entry into unemployment. At t=180 and t=270, the differences are not statistically significant either. The point estimates for effects at 270 days are around 2–3 percentage points for A, B, and C as compared to D. At one year, the effect estimates range from 3 to 5 percentage points; these are statistically significant at the 5% level for A and C and at the 10% level for B. Thus, on average, being assigned to a late IA reduces the probability of reemployment within a year by about 4 percentage points, from 69% to 65%, and it commensurately increases the probability of long-term unemployment. On average, it does not matter at any twhether the IA is signed immediately or after three months. None of these results suggests that it matters much whether the IA at three months is announced in advance or not. To scrutinize this in more detail, we use information in the data on the exit rate to work around t=90 for groups B and C. In line with the approach proposed in Subsection 5.2, we examine the steepness of the slopes of the empirical hazard rates around three months. Figure 3 displays kernel hazard estimates for B and C for durations up to six months.22 This figure indicates that the hazard rate for B increases less steeply than for C, around 90 days, although the difference is not overwhelming. The result fits the theoretical prediction and thus supports the notion of anticipatory behavior. Individuals who are not informed in advance about the IA adjust their behavior more abruptly upon the signing of the IA, leading to a larger increase of the exit rate to work than among those who are informed in advance. However, this is not a quantitatively important phenomenon, as we do not find evidence of a larger reemployment probability for B at 90 days (or beyond) in Table 3. 22 The bandwidth is 14 days. In our data, the usual starting day of a new job is a Monday. For this reason, the bandwidth should be a multiple of seven days. Furthermore, in any given month, there are two moments where reemployment is much more frequent than at other moments: at the beginning of the month and in the middle of the month. Specifically, in our data, around 39% of the employment spells start in the first three days of a calendar month, and around 12% start at day 13, 14, or 15. This implies that a two-week bandwidth is more appropriate than a one-week bandwidth. A bandwidth of three or more weeks is too large in comparison to the 13 weeks that span the period from entry until the moment where the treatment groups B and C receive their IA. Indeed, according to graphical inspection, a bandwidth of three or more weeks leads to oversmoothing of the hazard rates around 13 weeks. mandatory integration agreements for unemployed job seekers 95 0.002 0.003 0.004 0.005 0.006 30 60 90 120 150 180 analysis time treatment = B treatment = C Smoothed hazard estimates Notes: Epanechnikov Kernel estimates for exit rate to work, with a bandwidth of 14 days. Solid: IA in month 3 with announcement (Group B), dashed: IA in month 3 without announcement (Group C). N: 2,081. Figure 3 kernel hazard estimates for treatment groups b and c 6.2. Heterogeneous Effects. Employability For policy reasons, it is interesting to know if there are certain identifiable types of individuals whose reemployment benefits strongly or does not benefit at all from the timing and/or prior announcement of IAs. A key result from the theoretical analysis in Subsection 5.2 is that an individual’s employability is the prime candidate for the study of heterogeneous treatment effects, in particular when comparing treatment arms B and C.23 The caseworker survey (see Subsection 2.2) suggests that caseworkers often do not regard IAs as useful for the reemployment chances of individuals who are thought to find work on their own within half a year. In contrast, they see more potential for IAs in the case of individuals expected to need some help to bring them back to work. This also points at effect variation by employability. We do not directly observe individual employability or caseworkers’ expectations on employability in our sample. However, we may obtain an indicator of individual employability by predicting individual unemployment durations in terms of individual characteristics and labor market history. Instead of considering many possible employability types, we consider a binary classification. For this, we estimate a duration model on a different but similar sample. The estimated duration model is then used to classify individuals according to whether the predicted median duration exceeds six months or not.24,25 23 More generally, the behavior of individuals with low employability may be more restricted by the controlling aspects of IA. 24 This approach can be seen as a profiling exercise. In practice, caseworkers themselves may profile their clients into one of a few categories. Such profiling is soft in the sense that it does not rely on an algorithm but on the caseworker’s observation of the client’s characteristics and history, the caseworker’s subjective impressions, and the caseworker’s assessment of the support that the client may need most. Clearly, the resulting category is related to whether the caseworker expects the unemployed individual to return to employment on his or her own within six months. At the macro level, about half of the inflow of unemployed is classified as being able to return on his or her own within six months. The data set we use for the present article does not contain comprehensive and directly usable information on profiling outcomes. Note that profiling classifications after the IA may have been made in response to the assigned treatment. 25 A standard approach in the literature is to use the control group and to regress the outcome variable on a set of baseline characteristics and then to use this model to predict the potential outcomes for the full experimental sample. Based on that one can stratify the sample into groups with different levels of expected outcomes. Abadie et al. (2018) 96 van den berg et al. Specifically, we estimate a descriptive Weibull proportional hazard model for the duration until employment given individual characteristics and labor market history x, so in obvious notation, θ(t|x)=αtα−1exp(xβ). The median m(T|x)ofTgiven xis then equal to m(T|x)=(log 2)1 αexp(−xβ α). It is not difficult to show that in this model, E(T|x)=m(T|x)·γfor some γ>0 that does not depend on xor β. Thus, a low median is equivalent to a low expected duration. Note that the individual predicted median duration m(T|x) is a monotonic function of the single index xβ, so the binary outcome I(m≷6) should give an employability classification that is relatively robust to misspecifications of the prediction model and to changes of the threshold value. We estimate the prediction model with data we obtained covering all inflows into unemployment in the same regions in the year 2011, that is, from before the RCT. This is motivated by the fact that 2011 and 2012 are comparable years in terms of labor market conditions and in terms of absolute levels of flows into and out of UI among individuals aged 25-64 in the five regions (see Statistics of the FEA, 2019). Conditions in these two years 2011 and 2012 were slightly more favorable than in the surrounding years. Indeed, along the above dimensions, 2011 and 2012 are more similar to each other than to any of the surrounding years since 2009. The year 2011 was slightly more favorable than 2012, but the relevant flows differ only up to about 5% between the two years. Even when considering regions and 10-year age groups separately, differences in relevant flows between the two years do not exceed 10% in any subgroup. The 2011 sample consists of 55,545 men aged 25–64. This is substantially larger than our RCT sample, because it covers a larger inflow window but also because the 2011 sampling design does not exclude some types of individuals or spells that would not be eligible for inclusion in the RCT, such as spells of individuals who had been unemployed at some point in the three months prior to the onset of the spell, or spells with meeting timing sequences deemed inadmissible for the RCT, or spells where individuals moved to work before the IA.26 Table A.2 gives the estimation results for the prediction model.27 Using the estimated prediction model, around 40% of our RCT sample are predicted to have a median duration below six months. (The next subsection contains sensitivity analyses regarding the six-month threshold value.) Table A.3 describes mean differences between covariates in the ensuing low- and highemployability groups in the RCT sample. The low-employability group with predicted medians above six months does not primarily consist of young unskilled workers but actually contains many older workers with higher previous wages and long previous employment spells, possibly with obsolete skills and coming from sectors in decline. Some further comments are in order regarding the usage of the prediction model. First, spells that start in 2011 may be ongoing during the RCT, meaning that they may be affected by the execution of the RCT, even though the RCT is designed to avoid such externalities. More generally, it is undesirable if the prediction model is affected by outliers in the spell lengths. We investigate this empirically by artificially right-censoring spells at various points in time when estimating the prediction model. Second, the predicted employability should relate to the views of the caseworkers in the RCT regarding employability because it reflects the experiences that the caseworkers accumulated before the RCT. The spells starting in 2011 were subject to the standard IA regime, point out that this endogenous stratification can lead to substantial biases. Moreover, our sample sizes are modest, and, in fact, in our regions there is no natural control group during the RCT. 26 Also, recall that the RCT sample excluded 20% of the inflow as they were randomized to not be in one of the four treatment arms. 27 In the 2011 sample, we predict for 87% of the individuals who experienced a duration of more than six months that their predicted median is above six months. For 47% of those with a completed duration less than six months, it is predicted that the median is below six months. The latter result may reflect the restrictiveness of the Weibull model, which may lead to a slight underestimation of the prevalence of short durations. mandatory integration agreements for unemployed job seekers 97 0.00 0.25 0.50 0.75 1.00 0 100 200 300 400 500 600 700 Unemployment duration in days 0.00 0.25 0.50 0.75 1.00 0 100 200 300 400 500 600 700 Unemployment duration in days Low expected UE duration High expected UE duration Notes: Individuals with predicted median unemployment duration ⩽6 months on the left (n=1,688) and individuals with predicted median unemployment duration >6 months on the right (n=2,475). Solid: IA in month 1 (Group A), long dash: IA in month 3 with announcement (Group B), dot: IA in month 3 without announcement (Group C), dash dot: IA in month 6 (Group D). Figure 4 kaplan–meier estimates of the survival function until exit to work—depending on predicted unemployment-to-employment duration meaning that the IA usually occurs during the first meeting. In a different regime (e.g., where everybody only receives an IA after six months), individual employability may change and caseworkers may respond to this. Whether such an equilibrium policy effect is quantitatively important depends on whether the regime affects the ranking of individuals in terms of their employability index. Results by employability Figure 4 shows Kaplan–Meier estimates of the survival functions until exit to work. Among those with high employability, the estimated functions for the four treatment groups are very close. This suggests that, among them, signing an IA very early has on average no impact on their probability of getting a job. In contrast, among those with low employability, the survival function for group D is markedly different from the functions for groups A, B, and C, where the latter three are virtually equal. In particular, beyond 150 days group D displays a lower probability of having entered employment. Table 4 presents estimation results for the regressions by employability. Among those with high employability, we do not find any statistically significant difference between treatment groups, regardless of the elapsed duration. The coefficients in the table have a negative sign, meaning that the probability of returning to work within a certain amount of time is highest for group D. Thus, early IAs are obviously not an effective tool to speed up reemployment for individuals with good labor market prospects. The same applies to the early notification of IAs. This is different for those with lower employability. Here, early IAs in the first or third month of unemployment have statistically significant positive and quantitatively relevant effects on reemployment within nine months, as compared to having a later IA. For treatment groups A and C, the difference with D is even statistically significant at an elapsed duration as low as six months. One year after entry into unemployment, the differences between A, B, and C on the one hand and D on the other hand range from 6 to 9 percentage points; these differences are all statistically significant. Thus, on average, among those with low employability, being assigned to a late IA reduces the probability of reemployment within a year by 98 van den berg et al. Table 4 exit to work within 90,180,270,and365 days after unemployment entry—heterogeneous effects depending on predicted unemployment duration Until Day:90 180 270 365 Coef. S.E. Coef. S.E. Coef. S.E. Coef. S.E. Predicted Median Unemployment Duration ⩽6 Monthsa A−0.024 (0.032) −0.011 (0.032) −0.021 (0.029) −0.006 (0.026) B−0.027 (0.033) −0.045 (0.033) −0.025 (0.029) −0.002 (0.026) C−0.032 (0.032) −0.021 (0.033) −0.040 (0.029) −0.020 (0.027) Mean D 0.344 0.642 0.771 0.823 Predicted Median Unemployment Duration >6 monthsb A 0.030 (0.023) 0.046*(0.027) 0.061** (0.028) 0.075*** (0.027) B 0.006 (0.023) 0.036 (0.027) 0.054*(0.028) 0.060** (0.027) C 0.019 (0.022) 0.049*(0.027) 0.064** (0.027) 0.091*** (0.027) Mean D 0.191 0.357 0.462 0.530 Note: Linear probability models. Dependent variable is one if an individual has found a job within 90/180/270/365 days after unemployment entry. Predicted median unemployment duration is based on the coefficients of a hazard rate model estimated on an inflow sample into unemployment in the year before the experiment. Number of observations: aN: 1,688, bN: 2,475. Group A: IA in month 1. Group B: IA in month 3 with announcement at first meeting. Group C: IA in month 3 without announcement. Reference group is D: IA in month 6. Significance levels: *10%, **5%, ***1%. Individual controls included but not shown: age, nationality, education, previous wage, handicap, and previous employment history. 0.003 0.004 0.005 0.006 0.007 0.008 30 60 90 120 150 180 analysis time treatment = B treatment = C Smoothed hazard estimates 0.002 0.0025 0.003 0.0035 0.004 30 60 90 120 150 180 analysis time treatment = B treatment = C Smoothed hazard estimates Notes: Epanechnikov Kernel estimates for exit rate to work, with a bandwidth of 14 days. Solid: IA in month 3 with announcement (Group B), dashed: IA in month 3 without announcement (Group C). Left panel: sample of individuals with predicted median unemployment duration ⩽6 months (N=838). Right panel: individuals with predicted median unemployment duration >6 months (N=1,243). Figure 5 kernel hazard estimates for treatment groups b and c by degree of employability about 8 percentage points, from 61% to 53%. This is a substantial effect. For this, it does not matter whether an IA is signed immediately or after three months. The results also indicate that it is not quantitatively relevant whether the IA is announced in advance. To examine this in more depth, Figure 5 presents the equivalent of Figure 3 for each of the two employability groups. Each panel in the figure displays kernel hazard estimates for B and C for durations up to six months (bandwidths equal 14 days). Note that the vertical axis of the left panel (high employability) is more compressed than the vertical axis of the right panel.28 Among high-employability individuals, we find a marked difference in 28 Also note that the horizontal axis only covers the early stages of the spells. After 180 days the hazards decrease substantially. mandatory integration agreements for unemployed job seekers 99 the increase of the hazard rate around 90 days, with C displaying a much stronger increase than B (this is robust with respect to the bandwidth choice). According to the theoretical analysis, this means that individuals with treatment status B anticipate the IA at three months and modify their behavior before the IA in response to that. However, as in the full sample, this does not lead to a difference between B and C in the unconditional average reemployment probabilities at 90 days, so the anticipation is quantitatively unimportant. Among lowemployability individuals, the hazard rates around 90 days are remarkably similar for B and C, and this does not provide much evidence of anticipatory behavior. Tables A.4 and A.5 illustrate that the results do not change much when we decrease the right-censoring time point applied to the prediction sample. Caseworker identifier As an additional heterogeneity analysis we interact the treatment effects with the caseworker identifier. Such an investigation can only have a limited scope due to (i) the large number of caseworkers and (ii) the fact that, although caseworker assignment is arguably quasi random, we were not able to randomize it within our RCT. However, interaction effects may be informative on the presence of heterogeneity in the extent to which a caseworker is able to put the IA to good use. If such heterogeneity is indeed present then this provides an incentive for the employment agency to let less-effective caseworkers learn from more-effective caseworkers. In the data used for the above results, there are 13 caseworkers with each over 50 clients in the RCT. We estimate regression models in which the treatment effects are interacted with 13 corresponding binary caseworker indicators and where these indicators are also included as additive regressors, using the same data. Clients of caseworkers who had 50 or less clients in the RCT are the baseline category in these regression models. Among low-employability clients, we find strong evidence of effect heterogeneity according to an F-test (p-value is 0.041).29 The standard deviations across the estimated treatment effects correspond to 0.42 for treatment A, 0.40 for treatment B, and 0.36 for treatment C, again suggesting a substantial amount of effect heterogeneity. The results are robust with respect to small changes in the threshold value of 50 clients per caseworker. For the reasons mentioned above, we do not zoom in further on sources of effect heterogeneity by caseworker. However, the results motivate further research to identify whether caseworkers can increase the reemployment effect of early IAs among low-employability clients by adopting the work practice used by the caseworkers whose clients display the largest effects. 6.3. Additional Outcome Variables and Sensitivity Analyses. Wage-related outcomes Recall from Subsection 5.1 that inference of average treatment effects on initial wages in accepted jobs is not possible due to right-censoring of unemployment spells at the end of the observation window. With this in mind, Figure A.2 compares kernel density estimates for the initial wage (per day) in accepted jobs, measured at various duration endpoints. This does not suggest any large or systematic differences across the treatment groups.30 Stratification by employability is not informative, as the degree of right-censoring differs starkly between the two subsamples. Moreover, it is not clear how to interpret wage effects by an employability measure based not on wages but on durations. As mentioned in Sub- 29 In the subsample of clients with high employability, we do not find evidence of effect heterogeneity (p-value 0.65). Note that in this subsample we do not find an effect in a homogeneous specification either. 30 The survey that was held among a subsample of RCT participants about 1.5 months after entry (Subsection 2.3) includes a question about the lowest acceptable wage (i.e., the reservation wage) for those still unemployed. It is difficult to use this information. As discussed in Subsection 2.3, the sample of respondents is nonbalanced. Moreover, the reservation wage is a determinant of being unemployed at 1.5 months. With these caveats in mind, we find no evidence that the observed reservation wages early in the spell are systematically different across treatment groups (see Table A.6). This is consistent with the absence of differences in accepted wages. 100 van den berg et al. Table 5 active labor market policy participation, invitations to meetings and vacancy referrals Predicted Median Duration ⩽6 MonthsaPredicted Median Duration >6 Monthsb Until Day 90 180 365 90 180 365 Participation in ALMP A−0.000 (0.011) −0.009 (0.012) −0.008 (0.012) 0.004 (0.011) 0.007 (0.011) 0.003 (0.010) B−0.005 (0.011) −0.010 (0.012) −0.009 (0.012) 0.001 (0.011) 0.002 (0.011) 0.002 (0.010) C 0.018 (0.013) 0.009 (0.013) 0.007 (0.013) −0.003 (0.010) −0.003 (0.010) 0.000 (0.010) Mean D 0.052 0.071 0.080 0.056 0.063 0.066 Invitations to Meeting A 0.000 (0.001) 0.000 (0.001) −0.000 (0.001) 0.000 (0.001) −0.000 (0.001) −0.000 (0.001) B−0.000 (0.001) −0.000 (0.001) −0.000 (0.001) 0.000 (0.001) 0.000 (0.001) 0.000 (0.001) C 0.001 (0.002) 0.001 (0.002) 0.001 (0.002) 0.001 (0.001) 0.000 (0.001) 0.000 (0.001) Mean D 0.013 0.013 0.013 0.011 0.011 0.011 Vacancy Referrals A 0.003 (0.005) 0.003 (0.005) 0.003 (0.005) −0.003 (0.003) −0.003 (0.003) −0.003 (0.003) B 0.007 (0.005) 0.006 (0.005) 0.006 (0.005) −0.002 (0.004) −0.001 (0.004) −0.001 (0.004) C−0.004 (0.005) −0.004 (0.004) −0.005 (0.004) −0.002 (0.003) −0.001 (0.003) −0.000 (0.003) Mean D 0.054 0.050 0.050 0.036 0.032 0.031 Note: OLS regressions. Outcome variables: sum of days in ALMP participation/sum of invitations/sum of vacancy referrals, each divided by the number of days spent in unemployment, by employability indicator. In the latter, the predicted median unemployment duration is based on the coefficients of a hazard rate model estimated on an inflow sample into unemployment in the year before the experiment. Number of observations: aN: 1,688, bN: 2,475. Group A: IA in month 1. Group B: IA in month 3 with announcement at first meeting. Group C: IA in month 3 without announcement. Reference group: IA in month 6. Significance levels: *10%, **5%, ***1%. Individual controls included but not shown: age, nationality, education, previous wage, handicap, and previous employment history. section 6.2, the preunemployment wage is negatively correlated to the employability measure in the RCT sample. Next, we consider effects on cumulative earnings. The average effects are reported in Table A.7. It turns out that we do not find any statistically significant impact on cumulative labor earnings or on the sum of cumulative labor earnings and UI benefits, measured at 180 or 365 days after entry into unemployment. Turning to heterogeneous treatment effects, our point estimates are more positive for unemployed with a rather long expected unemployment duration (see Table A.8). Whereas the estimates for treatment arms A and B are not statistically significant, the effect of receiving an IA in month 3 without previous announcement is statistically significant suggesting that cumulative labor earnings after a year are increased by around €1,240. When we consider the cumulative sum of labor earnings and UI benefits, the estimated effect of treatment C drops to around €926 after a year, which is still sizeable but is not statistically significant anymore. Overall, the effects are estimated with relatively low precision. Usage of ALMPs According to the experimental protocol, caseworkers should not allow the assigned IA treatment to affect the frequency of meetings with the unemployed or their access to ALMPs. To verify this, we examine whether these are associated with each other, using the detailed information on meetings and ALMP participation in the data. Such analyses are descriptive as the observation of meetings and ALMP participation is restricted by the realized duration outcome. We regress the number of days spent in ALMP and the number of invitations divided by the days spent in unemployment on indicators for being assigned to treatment A, B, or C, controlling for observed background characteristics x. Analogously, we investigate whether the treatment groups differ in the probability of receiving vacancy referrals from the employment agency. Table 5 contains results by employability. None of the coef- mandatory integration agreements for unemployed job seekers 101 ficients is significantly different from zero. This suggests that our main findings are not driven by differences in the access to ALMP, the receipt of vacancy referrals or the number of meetings with the caseworkers.31 Moreover, we obtain qualitatively similar results when only considering transitions into unsubsidized jobs as transitions into employment, or when considering subsidized selfemployment as part of regular employment (see Tables A.9 and A.10). We also investigate whether the probability of a recall is affected by the treatment. It turns out that recall differences across treatment groups are small and typically statistically nonsignificant (see Table A.11). What the results in this subsection suggest is that IAs do not work by way of participation in other ALMPs. Also, the usage of other ALMPs does not seem to depend on the timing or advance notification of the IA. IAs thus appear to operate independently of other policy measures. IA effects can therefore be seen as policy effects that are separate from any effects of other ALMPs. Treatment “as usual” Whereas our original research design consists of the comparison of four different treatment arms, the involved department of the FEA headquarters has implemented a fifth arm described as “the usual IA regime.” This should correspond to signing an IA early in the unemployment spell. In fact, there were some degrees of freedom in the organization of this fifth arm and there were no unified instructions across the involved local agencies. Therefore, we do not include this treatment arm in our main analysis. Tables A.12 and A.13 report results including this additional treatment “E.” We find, on average, a positive but statistically insignificant effect on the probability of leaving unemployment for a job. When we consider heterogeneous treatment effects, we find that the “treatment as usual” tends to have negative but statistically insignificant effects for those unemployed with a short expected unemployment duration, whereas it has a positive and statistically significant effect for lowemployability individuals. Overall, the effects do not contradict the main results. Alternative (sub)sampling criteria Next, we take a predicted median duration of seven months instead of six months as threshold for splitting the sample into two groups. The results are robust with respect to this (Table A.14). We additionally examine whether the results change when omitting individuals with a predicted median duration of more than three years until employment. It turns out that most point estimates are close to those for our main specification (see Table A.15). Finally, as a sensitivity analysis, we omit all clients of caseworkers with relatively many extreme scheduling deviations.32 The results are qualitatively the same (see Table A.16). 7. conclusions Signing an IA in the first or third month of unemployment (as opposed to later, in the sixth month) has on average a positive effect on entering employment within a year. More specifically, a late IA reduces the average probability of reemployment within a year by about 4 percentage points, from 69% to 65%, and it commensurately increases the probability of longterm unemployment. For this, it does not matter whether the IA is signed immediately or after three months. 31 In Table 5, we focus on the number of days spent in any ALMP. The overall share of days spent in ALMP is rather low (around 7%). The conclusions obtained for the aggregate measure do not change when we instead focus on the largest ALMP, which is the default training program. 32 For this purpose, we define that a caseworker deviates from the schedule if (i) a client in treatment group A is unemployed for 60 days or more and does not sign an IA before 60 days of unemployment, (ii) a client in treatment group B or C signs an IA before day 60 or after 135 days of unemployment, or (iii) a client in treatment group D signs an IA before day 135 or after day 245. In the sensitivity analysis, we exclude caseworkers who deviate in more than 40% of their cases. 102 van den berg et al. A theoretical analysis based on job search models suggests that an individual’s employability is the prime candidate for the study of effect heterogeneneity, and this is corroborated by caseworker survey responses. It turns out that among those with high employability, the timing of the IA does not affect the probability of returning to work within any amount of time. If anything, early IAs have a negative effect on exits to work. Thus, early IAs are not an effective tool to speed up reemployment for individuals with good labor market prospects. This is different for those with lower employability. Here, early IAs in the first or third month of unemployment have significantly positive and quantitatively relevant effects on reemployment within 9 months and within 12 months, as compared to having a later IA. The differences are sometimes even statistically significant at an elapsed duration as low as six months. On average, among those with low employability, being assigned to an early IA increases the probability of reemployment within a year by about 8 percentage points, from 53% to 61% (so the relative increase is 15%). This is a substantial effect. For this, it does not matter whether an IA is signed immediately or after three months. Note that the positive overall effects of early IAs are exclusively driven by the lower-employability group. We conclude from this that the IA is a valuable policy tool, especially for newly unemployed individuals with adverse labor market prospects, as it strongly reduces their probability of long-term unemployment. It is interesting to view this in the light of the existing evidence on the limited effectiveness of more traditional ALMP that, after all, often target those with adverse prospects. Our results suggest that the IA is an interesting new addition to the set of policies for this group. Apparently, an approach in which monitoring is presented in a rather neutral and formal fashion delivers desirable outcomes. Our article contains a detailed theoretical analysis of anticipatory effects of advance announcements of the IA, and we develop an innovative econometric approach to detect such announcement effects. The corresponding empirical findings suggest anticipatory behavior in response to the advance announcement of an IA at three months. Upon the signing of the IA, individuals who are not informed in advance adjust their behavior more abruptly, as witnessed by a larger increase of their exit rate to work, than those who are informed in advance. However, this is not a quantitatively important phenomenon, as we do not find evidence of announcement effects on unconditional reemployment probabilities at any elapsed duration. We also examine interaction effects with caseworker identifiers. Among low-employability clients, we find statistical evidence of effect heterogeneity. In our view, this motivates further research to identify whether early IAs for low-employability clients can be put to better use by adopting work practices used by the most effective caseworkers. According to the experimental protocol, caseworkers should not allow the assigned IA treatment to affect the frequency of meetings with the unemployed or their access to ALMPs. We verified that this was indeed the case (and this also applies to the frequency of vacancy referrals), so that effects cannot be attributed to differential usage of other policy instruments. Also, results are robust with respect to the usage of wage subsidies or self-employment subsidies. All in all, IA effects appear to operate independently of other policy measures. We do not find effects on recalls or on accepted wages, where it should be kept in mind that the latter are only observed for uncensored unemployment spells. First findings from our study were presented to the governing board of the German FEA. This led the FEA to implement a major modification of the usage of IAs in the UI system. Caseworkers conduct a soft profiling for individuals entering unemployment, distinguishing between unemployed persons who are considered to be able to find work by themselves within six months and those who are not. Job seekers profiled as part of the former group are now not exposed anymore to a mandatory IA in the first three months of unemployment. In the absence of aggregate numbers on the fraction of newly unemployed UI recipients with this subjective reemployment characteristic, we cannot quantify the number of individuals who directly benefit from this policy change. A crude indication could be based on the