Experimental Evidence from the Great Recession

Working Paper 06-2015

Are Reemployment Services Effective? Experimental Evidence from the Great Recession

Marios Michaelides and Peter Mueser

Department of Economics, University of Cyprus, P.O. Box 20537, 1678 Nicosia, Cyprus Tel.: +357-22893700, Fax: +357-22895028, Web site: http://www.ucy.ac.cy/econ/en

Are Reemployment Services Effective? Experimental Evidence from the Great Recession†

Marios Michaelides (University of Cyprus) Peter Mueser (University of Missouri)

June 2017

Abstract We report the results of a random assignment study of a reemployment program implemented in the United States during the Great Recession which required Unemployment Insurance (UI) recipients to undergo an eligibility review and receive comprehensive job-counseling services. The program expedited participant exit from UI, produced substantial UI savings, and improved participant employment rates and earnings. These effects are associated with: (1) increased participant UI exit up to the time of services receipt, indicating an effect due to participant efforts to avoid program activities or failure to meet UI eligibility requirements; and (2) greater exit subsequent to services receipt, implying that the services themselves helped participants conduct an effective job search. Our findings provide compelling evidence that reemployment programs can be effective during recessions.

JEL Classifications: J6, H4. Keywords: Great Recession, job search services, unemployment, Unemployment Insurance, program evaluation. † This paper is based on data collected by IMPAQ International, LLC (IMPAQ) as part of a study funded by the U.S. Department of Labor, Employment and Training Administration (DOL/ETA). The authors are grateful to the European Research Council (ERC) for financial support provided through the Marie Curie fellowship program. The views expressed in this paper are those of the authors and should not be attributed to ERC, DOL/ETA, or IMPAQ, nor does mention of trade names, commercial products, or organizations imply endorsement of the same by the European Commission, the U.S. government, or IMPAQ. The authors would like to thank a number of people who contributed to this paper, including: Eileen Poe-Yamagata, Jacob Benus, and Goska Grodsky of IMPAQ; Jonathan Simonetta, Wayne Gordon, and Richard Mueller of the U.S. Department of Labor; Kim Morigau of the Nevada Department of Employment, Training, and Rehabilitation; and Ariana Matsa for excellent research assistance. Author contact information: Marios Michaelides ([email protected]); Peter Mueser ([email protected]).

INTRODUCTION In the past 25 years, policymakers in the United States and Europe have put much emphasis on programs that require unemployed workers to participate in reemployment services as a condition for collecting unemployment benefits (Wandner, 2010; OECD, 2013). Funding for these programs grew dramatically during the Great Recession in the U.S., when the federal government made substantial investments to enhance the capacity of public employment offices to offer services to jobseekers (Wandner and Eberts, 2014). Despite this growing interest, there is no recent evidence on the effectiveness of U.S. reemployment programs, with the most recent studies examining programs implemented more than a decade before the start of the Great Recession (Decker et al., 2000; Klepinger et al., 2002; Black et al., 2003). Although there are many recent studies of such programs in Europe, evaluations are generally in the context of relatively strong labor markets (e.g., Gorter and Kalb, 1996; Graversen and van Ours, 2008; Hägglund, 2011; Dolton and O’Neill, 2002). Economic conditions may play a significant role in the potential benefits of reemployment programs, as the structure of job matching and the composition of the unemployed varies greatly over the business cycle (Elsby et al., 2010; Hobijn and Sahin, 2013), with layoffs affecting a broader population of workers during a recession. This is particularly true for the Great Recession, when the unemployed population included more high-skill workers than usual, such as collegeeducated, experienced, and white-collar workers (Michaelides and Mueser, 2012). These workers may have had limited job-search experience prior to the recession, and it is possible that services to help make the best use of their skills would be particularly valuable (Jacobson and Petta, 2000; Jacobson et al., 2004; Barnichon et al., 2012). On the other hand, the benefits of improved job search might well be reduced during a recession in reflection of a decline in available jobs. The lack of evidence on the effectiveness of reemployment programs during downturns is a Page 1

conspicuous gap, considering that interest in these programs peaks when the labor market is weak. In addition, existing studies provide very little evidence on the mechanisms underlying observed program effects. U.S. studies find that program effects are largely attributable to participants’ response prior to service receipt, implying that the primary response is the “threat” of the services, and that the services themselves are not of importance (Decker et al., 2000; Black et al., 2003). While this may be true for the particular programs evaluated, the conclusion that services are generally of little value may be premature, as these studies examine programs providing services to only a small share of participants. Although European programs provided extensive job-search services, studies of these programs do not allow us to identify the value of services (e.g., Gorter and Kalb, 1996; Graversen and van Ours, 2008; Hägglund, 2011). Thus, while the literature consensus is that reemployment programs are effective in inducing participants to exit prior to services engagement, there is little evidence that the services offered by these programs help participants to improve their job search. This paper examines a reemployment program implemented in the state of Nevada that targeted workers who started collecting Unemployment Insurance (UI) benefits in the second half of 2009. During this period, the Nevada unemployment rate averaged over 12 percent, reaching a peak near 14 percent in the subsequent 15 months, the highest in the state in 25 years and among the highest in the U.S. In addition to the fact that the program was implemented during a recession, two key features make this case study compelling. First, Nevada used random assignment at the start of the UI spell to determine which eligible UI recipients would be required to participate in the program (treatment group) and which would not be required to participate (control group).

This experimental design yields reliable

counterfactual outcomes against which to measure the outcomes of the treated cases. Second, the

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program required participants to receive more extensive services than previous U.S programs studied to date. Participants were required to attend a one-on-one meeting with program staff in the early stages of their UI spell in which they: (1) underwent an eligibility review to confirm they were indeed qualified for benefits and were actively searching for a job; and, if determined eligible, (2) were provided services designed to enhance their job search based on individual needs, including direct referrals to job openings. None of the U.S. programs studied to date have included an eligibility review or provided participants with the level of services that the Nevada program provided to its participants. Our data confirm that a large majority of treatment cases attended the assigned meeting and fulfilled program requirements, and that the program substantially increased receipt of job-search services. The analyses presented here rely on administrative UI claims data, UI wage records, and employment services data for all workers who started collecting UI in Nevada from July 2009 through December 2009 and were eligible for participation in the reemployment program and thus subject to random assignment. The UI claims data report: (1) the total number of regular UI benefit weeks and dollar amounts each recipient collected under the UI claim; and (2) the total benefit weeks and amounts collected under the Emergency Unemployment Compensation (EUC) program, available to recipients who exhausted their regular UI entitlement. UI wage records report quarterly earnings in each of the six calendar quarters after the start of the UI claim when random assignment was done. The employment services data report for treatment cases when meetings were scheduled, whether participants attended, and whether they were disqualified for findings of ineligibility during the meeting or for failure to attend the meeting. The data also report the specific job-search services received by both treatment and control cases. Our analysis begins with an examination of the characteristics of UI recipients who were

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eligible for random assignment for participation in the reemployment program and the job-search services they received during their UI claim. We confirm that random assignment was successful in assuring that the treatment and control groups were comparable. We also report on program participation measures for the treatment group and show that treatment cases obtained much more extensive job-search services than the control group. We then undertake analyses of the program effects, showing that the program was successful in reducing UI spells and payments, and in increasing quarterly employment and earnings in the six-quarter period after program entry. The fact that program requirements were scheduled at the beginning of participants’ UI spells enables us to shed light on the underlying mechanisms that led to program effects. In particular, we attempt to identify the relative importance of: (1) moral hazard effects, reflecting voluntary exit of participants to avoid program requirements and disqualifications of participants who were found ineligible during the review or failed to undergo the review, and (2) services effects, reflecting the value of services in helping participants to conduct a more effective job search. To do so, we identify which treatment cases are likely to be subject to each effect based on the timing of their involvement in the program. Our general assumption is that moral hazard effects are most relevant for treatment cases before completion of program requirements and that services effects are most relevant for treatment cases after completion of program requirements. Our analyses show that program effects were partly realized in the initial stages of the UI spell, suggesting the role of moral hazard effects. However, a substantial portion of program effects on UI exit occurred in the period after participants had received services and their interactions with the program had ended, suggesting that the actual services provided by the program led to improved job-search outcomes. Although exit at later points in the UI spell could be influenced by selection, we show that selection cannot explain the program effects estimated in later points

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in the spells. Overall, these findings provide evidence that programs requiring UI recipients to undergo an eligibility review and receive job-search services can be effective during a recession, and that both moral hazard and services effects play an important role in program effects.

BACKGROUND U.S. Reemployment Policy Since the early 1990s, U.S. policymakers have focused substantial attention on promoting the exposure of UI recipients to reemployment services. Although not all unemployed workers receive UI benefits, among displaced workers, most earnings losses occur for this group (Couch and Placzek, 2010). In 1993, Congress enacted the Worker Profiling and Reemployment Services (WPRS) program, which required state UI agencies to establish a system to identify which new UI recipients were most likely to exhaust benefits and refer them to reemployment services (Wandner, 2010). The recommendation to states was to provide WPRS-referred recipients with the full range of services offered at public employment offices, including: (1) group orientations to learn about available services; (2) registration in automated job banks to connect to available jobs; (3) workshops to improve job-search skills to aid in preparation of application materials and to improve interview performance; and (4) individual job counseling, including skills assessment, development of a work search plan, and job referrals (Dickinson et al., 1999). According to the U.S. Department of Labor, from 1997, when WPRS became fully operational, until 2007, 11.5 million UI recipients were referred to services – 6.3 million attended the orientation, 3.9 million participated in workshops, and 1.6 million received counseling.1 Services were funded under the Wagner-Peyser Act, which established the national employment system 1

See Worker Profiling and Reemployment Service Activity (http://workforcesecurity.doleta.gov/unemploy/profile.asp). Page 5

and is the funding authority for state reemployment services, providing support to the states averaging $766 million annually (Wandner, 2010, Table 6.1, page 197). At the end of 2007, the U.S. economy entered its worst recession since the Great Depression, with the unemployment rate increasing from 5 percent in December 2007 to a peak of around 10 percent by the end of 2009. To facilitate the economic recovery, the American Recovery and Reinvestment Act of 2009 (ARRA) authorized $400 million – in addition to $1.4 billion provided under Wagner-Peyser in 2009 and 2010 – to enhance the capacity of states to provide reemployment services. Using these funds, states increased the number of UI recipients referred to services by WPRS from 1.2 million in 2008 to 1.9 million in 2009 and to 2.1 million in 2010.

Effectiveness of U.S. Reemployment Programs The most recent experimental studies of U.S. reemployment programs examine programs implemented in the mid-1990s, more than a decade before the start of the recession and in a period when the average unemployment rate was between 5 and 6 percent. Decker et al. (2000) present experimental evidence on the Florida and Washington, DC Job Search Assistance demonstration programs, which required UI recipients to attend a group orientation to obtain information on services, with referrals to employment workshops and job counseling. Although 71 percent of participants attended the orientation, only 16 percent received services. The study finds that the program reduced UI duration by up to 1.1 weeks and UI benefits collected by up to $182, but produces mixed evidence of program effects on earnings. Treatment-control comparisons of UI exit rates show that the program’s entire effect occurred around the time participants were notified of program requirements, prior to services participation. This result leads the authors to conclude that program effects were attributable to the threat of sanctions or the expected cost of meeting the

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program’s requirements – what we refer to as moral hazard effects – rather than any benefits of services. Black et al. (2003) present experimental estimates of the effects of the Kentucky WPRS program in the period October 1994 through June 1996. The study finds that the program reduced UI duration by 2.2 weeks and benefit amounts collected by $143. The program had small positive effects on earnings in quarters 1-2 after program entry, but no impacts in quarters 3-6. Analysis of UI exit rates show that the only statistically significant effects occurred in weeks 1-2, the period when the notification letter was sent and prior to services receipt. Although effects were generally positive in subsequent weeks, they were substantively small, and effects in weeks 3-12 were responsible for only a quarter of the overall program effect. Thus, the study argues that program effects were attributable largely to moral hazard and not to the effectiveness of services. This conclusion is consistent with the fact that most participants received no services. A governmentfunded study of WPRS (Dickinson et al., 1999) reports that from July 1995 through December 1996, a period that largely overlaps the Black et al. (2003) study period, only 2 percent of Kentucky WPRS-referred recipients participated in individual job-counseling services. Klepinger et al. (2002) use data from an experimental program implemented in Maryland to examine the effects of imposing alternative work search requirements on UI recipients. The study examines three treatments: (1) remind participants that their records of employer contacts may be reviewed for verification; (2) increase the required weekly number of employer contacts to four instead of two; and (3) refer participants to employment workshops. Based on comparisons to the control condition, the study finds that these treatments reduced UI spells by 0.6 to 0.9 weeks and benefit amounts by $75 to $116, but found no effects on employment and earnings. The entire effect on UI was realized in the first two weeks of the UI spell – when treatment cases were notified

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of program requirements – and the authors conclude that effects were entirely due to the added burden imposed by the program. The above studies provide little evidence on whether services can help UI recipients to conduct a more effective job search. While not definitive, a few studies suggest that job-counseling and related services may be valuable for certain groups of disadvantaged workers.

A random

assignment study of a job-training program in the early 2000s finds that structured job counseling led to positive long-run effects on reemployment rates for the most disadvantaged workers but not for others (Perez-Johnson et al., 2011). Similarly, a study of Social Security disability insurance beneficiaries in 2007-2009 finds that those randomly assigned to receive medical care management and job-counseling services had greater labor market success than those assigned to a control group that did not have such services (Weathers and Bailey, 2014).

Effectiveness of European Reemployment Programs Over the past 25 years, many European countries have put into effect programs designed to ensure that unemployed workers who collect unemployment benefits are actively searching for jobs and have access to services offered by public employment offices. Referred to as activation programs, they typically feature a combination of job-search services to help the unemployed connect to suitable jobs, monitoring to confirm that they are conducting an active job search, and benefit sanctions when program participation and work search requirements are not met. For an overview of programs in European and other developed countries, see OECD (2007, 2013).2 The effects of European programs have been examined extensively. An experimental study

2

Services to job seekers in many European countries are integrated with extensive job training programs, which are often required for some benefit recipients. We limit our focus here to programs focusing on job search requirements and related services. Such government-supported active labor market programs are generally more extensive in Europe than in the U.S. (see Kahn, 2012). Page 8

shows that requiring unemployed workers in the Netherlands to receive job-counseling services at the start of their UI spell and to attend work search monitoring meetings every four weeks thereafter led to an 11 percent increase in job finding rates (Gorter and Kalb, 1996). Also based on experimental evidence, Graversen and van Ours (2008) find that requiring unemployed workers in Denmark to participate in a two-week workshop and attend subsequent monitoring meetings reduced average unemployment duration by 2.5 weeks. An experimental study of Swedish activation programs (Hägglund, 2011) finds that combined mandatory monitoring and job-search assistance increased reemployment rates up to 51 percent. Additional experimental studies in Denmark (Pedersen et al., forthcoming), France (Behaghel et al., 2012), Germany (Krug and Stephan, 2013) and the United Kingdom (Dolton and O’Neill, 2002), and non-experimental studies in Belgium (Cockx and Dejemeppe, 2012), Denmark (Geerdsen, 2006), the Netherlands (Abbring et al., 2005), the United Kingdom (Blundell et al., 2004), and Portugal (Centeno et al., 2009) confirm that programs that combine continued work search monitoring and job-search services are successful in increasing unemployment exits and promoting the reemployment of unemployed workers.3

Gaps in the Literature Reemployment programs may produce a moral hazard effect because program requirements push participants to exit unemployment before they receive any actual services. These programs may also produce a services effect because actual services are successful in enhancing participants’ job-search skills. For instance, directly referring jobseekers to employers or registering them in automated job banks where they can easily access information about available jobs may reduce

3

These studies do not provide estimates of program effects on earnings. Page 9

search costs and increase job applications (Jacobson and Petta, 2000). Individual job counseling may help participants to recognize their skills and focus their search on jobs that are suitable to those skills and are likely to offer them acceptable compensation (Jacobson et al., 2004; Wandner, 2008). Employment workshops may improve participants’ basic job-search skills, including application and interview skills, making them more attractive to employers (Balducci et al., 1997; O’Leary, 2006). Some combination of these services may help reduce search costs and enhance search intensity, particularly for those with limited job-search experience, reducing the amount of time they remain unemployed. With the partial exceptions noted above, existing studies provide little basis for separating the effects of services from moral hazard effects. A common theme in U.S. studies is that they examine programs in which very few participants received any actual services. The vast majority of participants in programs studied by Decker et al. (2000) Black et al. (2003) and Klepinger et al. (2002) did not participate in services. Given the low level of services receipt, we believe that these studies cannot be used to infer whether services are of value. Most European programs required participants to receive services on a regular basis throughout their UI spells, so it is difficult to distinguish effects resulting from the burden associated with this requirement and the effects of actual services. Many studies focus explicitly on moral hazard effects, examining responses to information about program requirements prior to initial services receipt, excluding any impact of the services themselves. Another important gap in the literature is that existing studies examine program efficacy during periods of moderate unemployment; thus, we can only speculate whether their results are generalizable to the Great Recession or other economic downturns. The most recent U.S. studies examine programs implemented from 1994 through 1997, at least a decade before the start of the

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Great Recession, when the U.S. unemployment rate was between 5 and 6 percent. Similarly, with the exception of Martins and Pessoa e Costa (2014),4 recent European studies examine programs implemented during relatively strong labor markets. Hence we have little knowledge about the value of job search during those times when the need is greatest. Existing work provides no evidence on the size of moral hazard effects during a recession. Although moral hazard may be of little importance for workers with very poor job prospects, the availability of UI benefits for extended periods may increase moral hazard for those whose employment likelihood is sensitive to their search effort. In addition, subsidies may interact with behavioral problems, lulling workers into inaction; if so, the shock effect of program requirements could be particularly valuable during the recession in pushing workers to find employment. Conversely, the growing prospect of long-term unemployment and attendant difficulties brought on by the recession may have served as a spur to search activity, thus reducing the importance of moral hazard effects. There is uncertainty as to whether reemployment services would be more or less valuable during a recession. The Great Recession substantially reduced employment opportunities, and insofar as search activities exhausted available job vacancies, the return to job search and services to support search may well have declined. At the same time, we know that the job matching process was particularly slow during the recession, as evidenced by a disproportionately small decline in unemployment associated with each additional job opening and by high long-term unemployment (Elsby et al., 2010; Barnichon et al., 2012; Hobijn and Sahin, 2013). This is partly attributable to a decline in the intensity with which employers recruited workers, as measured by advertising of job vacancies, speed of processing applications, and attractiveness of compensation 4

Using a fuzzy regression discontinuity design, they find that a job search support program implemented in Portugal in 2010 during a period of high unemployment doubled participants’ likelihood of finding employment. Page 11

packages (Davis et al., 2012; Ravenna and Walsch, 2012; Sedlacek, 2014). In the face of such changes, the value of more intensive job-search activities may have either increased or decreased. Several observations suggest the recession could increase the value of services. First, the profile of the average jobseeker changed substantially in the Great Recession, when the proportions of male, older, high-education, and white-collar workers reached their highest levels in 20 years (Michaelides and Mueser, 2012). The increase in unemployment and subsequent shortfall of vacancies was more pronounced for certain sectors, including construction, manufacturing, trade, and leisure and hospitality (Barnichon et al., 2012; Davis et al., 2012). These imply that the recession may have disproportionately affected workers who would not have employability issues under normal circumstances. Job-search support may have been more valuable insofar as they lacked the skills to conduct an effective job search. Second, there is a growing literature arguing that strategic provision of information may improve individual decision making, reducing procrastination and other behavioral biases that cause recipients of public assistance to fail to take necessary actions to improve their circumstances (Thaler and Sunstein, 2009; Babcock et al., 2012; Cockx et al., 2014). During recessions, limited job options and the prospect of long-term unemployment may exacerbate these problems, and thus make unemployed workers more responsive to services. Our study addresses the gaps in the existing literature, by providing evidence on both the relative importance of moral hazard effects and the value of job-search services during one of the most important recessions since the 1930s.

THE NEVADA PROGRAM In 2009, Nevada implemented a new program that required UI recipients to undergo an inperson eligibility review and receive staff-assisted reemployment services near the start of their UI Page 12

spells. This program was created in response to the federal Reemployment and Eligibility Assessment (REA) initiative, which provided states with grants to implement in-person eligibility reviews of UI recipients (Poe-Yamagata et al., 2012). Nevada replaced its existing WPRS program with the new program in the workforce regions covering the two large metropolitan areas in the state (Las Vegas-Henderson-Paradise and Reno). 5 Workforce regions in the rest of the state, serving mostly rural counties, were not affected by the new program. Nevada used REA funding together with Wagner-Peyser and ARRA funds to assure that each participant in the new program would attend an in-person meeting with program staff in which the participant underwent the REAmandated review and received staff-assisted services.

Nevada used random assignment to

determine which recipients would be required to participate in the new program. The Nevada selection process was as follows. Once an unemployed worker filed a UI claim and was deemed eligible for benefits,6 the individual was scheduled to start collecting weekly UI payments after a one-week waiting period. During that waiting period, Nevada UI agency staff determined if the worker was eligible for the program. Similar to U.S. programs evaluated in previous studies, and in compliance with WPRS and REA directives, the Nevada program included all new UI recipients, except those on temporary layoff, those attached to a union hiring hall, and those who were active in training programs. Each week, the pool of program-eligible UI recipients was placed in an interface that allowed random assignment to the treatment group (subject to program requirements) or to the control group (no program requirements). Once treatment cases were identified, they were sent letters notifying them that they had been

5

These workforce areas covered 87 percent of the unemployed population in Nevada in 2009, per tabulations of the American Community Survey. 6 UI claimants had to meet the following criteria to qualify for benefits: (1) lost their jobs through no fault of their own; (2) were willing and able to start a new job; and (3) earned at least $600 during the base period (the first four of the five calendar quarters prior to the UI claim date) and at least $400 during the quarter in the base period with the highest earnings. For details, see http://www.ows.doleta.gov/unemploy/uilawcompar/2009/comparison2009.asp. Page 13

randomly selected to attend a UI eligibility assessment meeting at a specified public employment office. Letters were sent around the time treatment cases received their first weekly UI payment (week 1 of their UI spell), informing them that the purpose of the meeting was to assist them in planning their job search and reduce the amount of time they would remain unemployed. The letter also indicated the exact date/time of the meeting, typically scheduled in weeks 2-4 of the UI spell,7 and explicitly stated that the meeting was mandatory and that failure to attend would cause loss of benefits. Treatment cases that failed to attend or reschedule the meeting and did not meet the above conditions, were disqualified from collecting additional UI benefits. Although not stated in the letter, according to program rules, treatment cases that, by the time of the meeting, had participated in job-search services, found a job, or enrolled in training were not subject to disqualification because of failure to attend the meeting. Control cases had no requirements under the reemployment program to retain their UI eligibility. They received no program letter and had no requirement to meet with program staff, undergo an eligibility review, or receive services, but were subject to the usual UI rules.8 The meeting between each participant and program staff comprised two components: the eligibility review and provision of staff-assisted job-counseling services. In the eligibility review portion of the meeting, program staff reviewed agency records of the participant’s employment history to confirm that the participant was indeed eligible for benefits. Program staff also questioned the participant to determine if he or she was conducting an active job search while collecting benefits, in accordance with state law. Participants deemed ineligible for benefits or non-compliant with work-search requirements were disqualified from receiving UI payments.

7

As we will see later, some treatment cases rescheduled their meetings. Nonetheless, the final schedule that included appointments after postponements placed 95 percent of all meetings in weeks 2-6. 8 The law specifies that all UI recipients in Nevada are required to be able to work, be actively searching for a job, and not reject suitable employment. Page 14

Participants who passed the review were offered job-counseling services during the same meeting. Program staff assessed participant occupational skills and work experience and, based on the results, helped the participant to produce a professional resume if appropriate. Program staff also worked with participants to develop a work search plan designed to focus their search efforts on jobs that matched their skills and experience. A key part of this process was that participants were directly referred to employers with job openings that suited their skills. Notably, participants were offered services based on their needs, and they did not necessarily receive the entire range of services offered by the program. Although there is no data on the length of these meetings, the letter sent to treatment cases indicated that the meeting would take about one hour, which was consistent with the estimate of program administrators we interviewed. Importantly, participants were informed during the meeting that this meeting was the only requirement and that they were not required to participate in additional services or meetings. We show below that nearly 80 percent of treatment cases attended the scheduled meeting and thus fulfilled program requirements. We also show that a majority of treatment cases received assistance to formulate a work search plan, nearly a quarter received a job referral, and substantial numbers received other services. Overall, more than two-thirds of treatment cases received at least one service. In contrast, although control cases were free to obtain such services, only about 10 percent received any service in the claim’s benefit year. The requirements of the Nevada program are a departure from U.S. programs examined by previous work. The programs examined by Decker et al. (2000) did not include an eligibility review and participation in job counseling was not enforced, so only 16 percent of participants received services, which was much lower than the Nevada services take-up rate. Similarly, the Kentucky WPRS program studied by Black et al. (2003) did not include an eligibility review and

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did not enforce participation in counseling; as a result, only 2 percent of participants met with a job counselor. None of the treatments tested in the Klepinger et al. (2002) study included an eligibility review, and although one of the conditions formally required that participants attend an employment workshop, only 30 percent of those assigned to this condition actually attended. To the extent that the eligibility review and job-search services are effective in facilitating the exit of participants from UI and improving reemployment outcomes, we would expect the Nevada program to have greater effects than the programs studied to date. The Nevada program requirements are similar to those of many of the European programs cited above, with the distinction that those programs required participants to receive services on a continuing basis, not just at the start of their UI spell. This feature makes it difficult for studies to explore whether the effects of these programs were solely attributable to moral hazard effects, or whether counseling services were themselves effective.

Finally, according to the Nevada

Department of Employment, Training, and Rehabilitation, the state spent $2,191,905 in 2009 to provide services to 10,905 participants, implying an estimated cost per participant of about $201. This amount covered all costs associated with program implementation, including the costs of identifying eligible recipients, the referral process, staff salaries, and related office expenses. It did not, however, cover costs of providing services not directly associated with the program. As noted below, a substantial minority of program participants obtained services following the week of their required meeting, and insofar as the costs of these services exceed those for the control group, this measure underestimates average program expenses.

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DATA UI Claims Data We use Nevada UI claims data, which provide information on the entire population of unemployed workers who started collecting UI benefits from July 2009 through December 2009 and were eligible for random assignment and participation in the reemployment program. Our sample includes: (1) all new UI recipients who were assigned to the treatment group (received the letter and were subject to program requirements); and (2) all new UI recipients who were assigned to the control group (did not receive the letter and did not face these requirements). The UI claims data provide information on recipient characteristics at program entry (i.e., when they applied for UI, about a week prior to random assignment) and treatment/control status for the reemployment program. To determine UI eligibility, the Nevada UI agency used information on prior employment and earnings to determine the number of regular UI weeks, weekly benefit amount (WBA), and cumulative benefit entitlement (the maximum total payment the recipient was eligible to collect during the claim’s benefit year).9 Nevada’s unemployment rate during the study period exceeded the thresholds for activating the Emergency Unemployment Compensation (EUC) and Extended Benefits (EB) programs. Thus, treatment and control cases in our sample that exhausted their regular UI benefits (12-26 weeks) and had at least 20 weeks of employment in the base period, could apply to receive up to an additional 53 weeks of EUC benefits.10 Moreover, those who exhausted EUC could apply to collect up to an additional 20 weeks of EB.11 The WBA for EUC and EB was identical to that under regular UI. The UI data used in this study report the number of regular UI benefit weeks and cumulative

9

The WBA was equal to 1/25 of earnings in the quarter with the highest earnings during the base period, subject to a $16 minimum and a $393 maximum. Weeks of eligibility were equal to one third of the benefit year earnings divided by the WBA, with a 12-week minimum and a 26-week maximum. The cumulative entitlement is equal to WBA times weeks of eligibility. The benefit year lasted 365 days from the date the claim was filed. Page 17

benefit amount each recipient was entitled to collect during the claim’s benefit year for all treatment and control cases. The data also provide information that we used to calculate each recipient’s EUC and EB entitlements, which measure the additional benefit weeks and amounts each recipient would be eligible to collect after exhausting regular UI benefits. Importantly, the data provide the total number of regular UI and EUC benefit weeks and amounts actually collected by each recipient. The data do not provide information on benefits collected under EB, an omission reflecting an early data management decision. The omission of EB data has two implications: (1) we cannot calculate the full UI spells for individuals who exhausted both regular UI and EUC benefits;12 and (2) to the extent that the program was effective, we underestimate program effects on total UI spells and benefit amounts collected. Using UI claims data, we find that, during the study period, 31,793 unemployed workers started collecting UI in Nevada and were deemed eligible for the program.13 Of these, 4,673 (15 percent) were randomly assigned to the treatment group and the remaining 27,120 (85 percent) to the control group. Table 1 presents sample proportions for measures of individual characteristics derived from UI claims data and means and standard deviations of prior earnings from UI wage records. Also, to check if random assignment produced a balance in the characteristics of treatment and control group members, the right column of Table 1 presents treatment-control differences in

10

Recipients who exhausted regular UI, applied for EUC, and had at least 20 weeks of prior employment were eligible for: (1) up to 20 weeks of EUC tier 1 benefits (lesser of 80 percent of regular UI and 20 weeks); (2) up to 14 weeks of EUC tier 2 benefits (lesser of 50 percent of regular UI and 13 weeks, plus one week); (3) up to 13 weeks of EUC tier 3 benefits (lesser of 50 percent of regular UI and 13 weeks); and (4) up to 6 weeks of EUC tier 4 benefits (lesser of 25 percent of regular UI and 6 weeks). 11 Recipients who exhausted EUC were eligible for up to 20 weeks of EB (lesser of 80 percent of regular UI or 20 weeks). 12 During the study period, 16.2 percent of the treatment and 19.1 percent of the control group exhausted regular UI and EUC, and thus were eligible for EB. 13 Workers who had Nevada earnings but were not residing in Nevada and who therefore filed UI claims in other states were not included. Page 18

means and t-tests to assess their statistical significance. The table provides no surprises. For both treatment and control cases, just over two-fifths were women and a fifth were Hispanic, with relatively low proportions under age 25 and over age 55. The occupational distribution, based on the occupation associated with the most recent job held, shows that the low-skill white-collar group was the largest, reflecting the dominance of Nevada’s service industry. Information on industry of prior employment was not available in the data. The bottom panel of Table 1 reports average quarterly earnings in the four-quarter period prior to UI entry based on UI wage records.14 As expected, UI recipients experienced a slight decline in average earnings over the year prior to the time they filed their UI claims. T-tests reveal no statistically significant treatment-control differences in characteristics and prior earnings. Table 2 presents means and standard deviations of regular UI eligibility measures. Individuals in the sample were eligible for about 23 weeks of regular UI, with just over $7,000 in cumulative benefit entitlements. Separate analyses show that regular UI weeks of eligibility ranged from 1226 weeks, with nearly 60 percent of recipients eligible for the maximum 26 weeks. Table 2 shows that treatment and control cases that exhausted regular UI were entitled to about 46-47 weeks of EUC benefits, and an additional 18 weeks of EB after they exhausted EUC. Separate analyses show that EUC eligibility ranged from 25 to 53 weeks, with 58 percent of recipients eligible for the full 53 weeks, and that EB eligibility ranged from 9 to 20 weeks, with 61 percent of recipients eligible for the full 20 weeks. Overall, treatment and control cases in our sample were eligible for an average 87 weeks in total benefits (regular UI, EUC, and EB), with an average total cumulative entitlement of nearly $27,000. Total benefit eligibility ranged from 46 to 99 weeks, with nearly 58 percent of recipients entitled to the full 99 weeks. T-tests in Table 2 show no significant 14

Individuals with no reported earnings in a quarter are included with a value of zero. Further information on our earnings measures is provided in the next section. Page 19

treatment-control differences in entitlements which, combined with the Table 1, confirms that random assignment was successful in balancing the samples to within statistical expectation. Under random assignment, treatment-control differences in subsequent outcomes provide unbiased estimates of program effects. We also used Nevada UI claims data to construct benefit receipt measures, including whether recipients exhausted regular UI benefits, whether they collected EUC after exhausting regular UI, benefit weeks collected (regular UI and EUC), and benefit amounts collected (regular UI and EUC). Table 3 shows that treatment cases had lower regular UI exhaustion and EUC collection probabilities than control cases. As a result, treatment cases collected fewer weeks and lower amounts of regular UI, EUC, and total benefits (regular UI plus EUC) than control cases. 15 Treatment cases were less likely to exhaust EUC benefits, suggesting that they were less likely to collect EB (information on EB collection was not reported in our data). Thus, if the program reduced UI duration, the reported average treatment effects below underestimate the program’s effect on total UI duration and benefits collected (including regular UI, EUC, and EB).

UI Wage Records Our second data source derives from Nevada UI wage records, which provide calendar-quarter earnings within Nevada for all treatment and control cases in our sample in each of the four quarters prior to and in each of the six quarters following the start of the UI claim. We use these data to identify employment and total earnings in each quarter. The data do not report the exact date the recipient started and/or stopped working within the quarter, and thus, they cannot be used

15

Note that the proportion exhausting regular UI benefits is about 10 percentage points greater than the proportion collecting EUC benefits. This difference is likely attributable to the fact that some recipients did not apply for EUC after exhausting regular UI, while others who applied for EUC did not have the required 20 weeks of employment in the claim’s base period. Page 20

to determine length of employment or hourly wages. Also, the data do not include earnings from employment in other states, an omission that could potentially affect our results. If more treatment cases were able to find jobs in other states relative to control cases, then treatment-control differences in employment and earnings would understate the true effects of the program.

In

contrast, if control cases were more likely to migrate because of lack of available jobs in their state, then treatment-control differences would overestimate the program’s effects. Notwithstanding these omissions, it has been suggested that program effects on employment and earnings based on wage records are generally comparable to those obtained in surveys, at least in the context of worker training programs (Kornfeld and Bloom, 1999) and welfare programs (Wallace and Haveman, 2007). In fact, wage records have been used extensively in studies that assess the effects of reemployment programs in lieu of survey data, including the aforementioned U.S. studies (Decker et al., 2000; Klepinger et al., 2000; Black et al., 2003). We use these data to construct two measures of quarterly earnings outcomes in each of the six calendar quarters following the start of the UI claim. First, positive earnings in a calendar quarter provide our measure of employment, indicating whether the individual was employed at any point during a quarter. Second, we measure the total earnings in a quarter for each individual; those with no Nevada earnings records were included with values of zero. As seen in Table 4, treatment cases had higher employment probabilities and earnings than control cases over the entire sixquarter follow-up period.

Employment Service Data The third data source used here derive from employment service records, which provide the exact scheduled date of the required program meetings for the 4,673 treatment cases, indicate

Page 21

whether they attended the meeting, and report whether they were disqualified because of findings of ineligibility or failure to attend the meeting. Table 5 presents the final REA meeting schedule, which reflects any postponements of an originally scheduled meeting; we do not have information on original meeting dates. As shown in Table 5, the vast majority of treatment cases (4,446 or 95 percent) were scheduled to have their meeting in weeks 2-6. Overall, 3,717 (80 percent) of treatment group members attended the meeting. The employment service data provide an account of the specific services received by all treatment and control cases in our sample. Table 6 provides information on staff-assisted services received during the UI claim’s benefit year.16 We see that 68.4 percent of treatment cases and only 9.7 percent of control cases received any listed services. The most common service was aid in developing a work search plan, with more than 55 percent of treatment cases served, as compared with only about 6 percent of control cases. As might be expected, treatment cases were much more likely to receive staff-assisted services offered during the meeting, such as resume assistance and job referrals. In fact, about 21 percent of treatment cases were referred to specific jobs, compared with only 4 percent of control cases. For other types of services, between a fifth and a third of treatment cases are coded as receiving the service, as compared with less than 4 percent of control cases. Combining the information on the meeting and services received, we find that of the 4,673 treatment cases: (1) 3,717 (80 percent) attended the meeting; (2) 491 (11 percent) did not attend the meeting but received at least one service; and (3) 465 (10 percent) did not attend the meeting or receive any services. Under program rules, those who attended the meeting and passed the

16

As noted below, we do not have information on the date of the service for most of the listed services. The services tabulated in Table 6 are those that are associated with the indicated claim. For services where we do have dates, 99 percent were received within the claim’s benefit year (i.e., within 365 days of the claim date). Page 22

eligibility review were not subject to any further requirements. Those who did not attend the meeting but received at least one service were not subject to disqualification because they missed the meeting, although it is not clear most participants were informed of this provision. Our data confirm that none of the participants who missed their meeting but participated in job-search services were identified as terminated. Treatment cases that did not attend the meeting and did not receive any services were subject to disqualification for failure to attend the meeting, but program rules specify that if participants reported that they had found a job (presumably implying they would soon exit UI) or were participating in training, they were excused from attending the meeting, exemptions that are not identified in our data. Overall, 0.7 percent of treatment cases were disqualified because of eligibility issues and 1.1 percent because of failure to undergo the review.17 We also have dates when services were received for about 40 percent of cases, although even when a date for the service is provided, except for job referrals, only the most recent date of that service is reported. Table 7 provides tabulations based on available information. In each line, the first count is the number of individuals who received at least one service and the second count is the number of individuals with information on the most recent date of service receipt. The three remaining columns report the proportion of individuals with date information receiving services before, during, or after the week of the meeting. For the lines identifying categories that include more than one service or for the job referrals category, the totals add to more than the number of

17

Of the 3,717 cases that underwent the review, 34 were disqualified due to eligibility issues identified in the review, and, of the 465 cases that did not attend the meeting and did not receive any services, 52 were disqualified for failure to attend the meeting. The timing of disqualifications is summarized in appendix Table A1, which shows that exits from UI due to disqualifications occurred only in the first eight weeks of the of the UI spell. Separate tabulations show that all disqualifications produced exits that occurred within two weeks of the meeting. Specifically, of the 34 cases that were disqualified because of findings of ineligibility, 26 exited the week of the meeting and 8 in the subsequent week; of the 52 cases that were disqualified for not completing the meeting, 22 exited the week of the meeting and the remaining cases in the subsequent two weeks. Page 23

individuals, since an individual can be coded as receiving services at multiple times. The first line indicates that, for the 1,296 treatment cases that received services and for which a date is available, 80 percent received a service in the week of the meeting. This is consistent with the program’s reported structure, in which services were provided during the meeting. In addition, some 27 percent received a service before the week of the meeting and 24 percent received a service following the week of the meeting. Looking at individual services, although most individuals received services during the week of the meeting, in each case, some are accessing services subsequent to the meeting. Hence, it appears that the program was successful in inducing some participants to undertake activities beyond those that were strictly required. Insofar as these services were of value, they could increase program effects.

METHODS Effects on UI Receipt, Employment, and Earnings Comparisons of means for measures of UI receipt, employment, and earnings between treatment and control cases, presented in Table 3, provide unbiased estimates of program average treatment effects. To improve statistical power, we used linear regression models to estimate program effects, controlling for characteristics and prior earnings, as follows: [1]

𝑌𝑖 = 𝑎 + 𝑏 ∙ 𝑇𝑖 + 𝑋𝑖 ∙ 𝑐 + 𝑢𝑖

The dependent variable (𝑌𝑖 ) is the outcome for individual i. The treatment indicator (𝑇𝑖 ) equals 1 if the individual was in the treatment group and 0 otherwise. The vector of control variables (𝑋𝑖 ) includes individual characteristics at program entry and prior earnings (as seen in Table 1), fixed effects capturing the number of regular UI weeks for which the individual is eligible, the logarithm of the regular UI benefit entitlement, and fixed effects for week of UI entry. Estimated parameters Page 24

include a constant term (a), a vector of coefficients for control variables (c), and a zero-mean disturbance term (𝑢𝑖 ). The estimation sample includes all treatment and control cases during the study period; thus, the fitted parameter 𝑏 provides an unbiased estimate of the program’s average treatment effect. To examine program effects on UI use, we estimate equation [1] taking as dependent variables measures of UI exhaustion, number of weeks of receipt, and the value of benefits received (see Table 3). To examine the labor market effects of the program we estimate the same equation taking employment and earnings as dependent variables.

While employment and earnings

measures are available for all treatment and control cases, they derive from wage records, so they cover a slightly different period than UI claims data. One concern with programs that facilitate UI exit, especially during high-unemployment periods, is that they may force treatment cases to take jobs that are poor matches for their skills. In this case, positive effects on employment may be more than compensated for by lower earnings of those with jobs. However, if effects on total earnings are positive, we can assure that any decline in match quality is compensated by increased earnings for those employed. Even if the program has positive effects on earnings, it is still possible that the effects are driven solely by effects on employment and that treatment cases were placed in jobs with lower earnings. To illustrate this point, the program’s average treatment effect on earnings can be expressed as: [2] 𝑌𝑇 − 𝑌𝐶 = 𝐸𝑇 ∙ 𝑊𝑇 − 𝐸𝐶 ∙ 𝑊𝐶 = (𝐸𝑇 − 𝐸𝐶 ) ∙ 𝑊𝑇 + 𝐸𝐶 ∙ (𝑊𝑇 − 𝑊𝐶 ) In the above, 𝑌𝑇 and 𝑌𝐶 are the average earnings for treatment and control cases, respectively, in a particular quarter; 𝐸𝑇 and 𝐸𝐶 are the employment probabilities; and 𝑊𝑇 and 𝑊𝐶 are the

Page 25

average earnings conditional on employment. 18 The program’s effect on earnings can be decomposed into: (1) the employment component, (𝐸𝑇 − 𝐸𝐶 ) ∙ 𝑊𝑇 , due to the greater levels of employment among the treated and (2) the conditional earnings component, 𝐸𝐶 ∙ (𝑊𝑇 − 𝑊𝐶 ), the treatment-control difference in earnings, conditional on employment. If the program’s effect is primarily due to pressure to accept employment and it forces individuals with poor labor market prospects to accept jobs, we may expect earnings for employed treatment cases to be lower, reflecting in a negative earnings component.

Effects on UI Exit Likelihood Program effects on UI receipt, employment, and earnings may be due to: (1) moral hazard effects, caused by participant disqualifications and participant voluntary withdrawal from UI to avoid program requirements; and (2) reemployment services effects, caused by the effectiveness of the services themselves in helping the remaining participants to improve their job-search outcomes. We expect moral hazard effects to occur between receipt of the letter informing treatment group members of the date for their required meeting and the week they actually met with counselors. Hence, such effects would likely occur in weeks 1-6 of the UI spell, the timeframe during which almost all participants were scheduled to attend the meeting. Services effects may occur because the job-search services provided by the program helped participants who fulfilled program requirements to conduct a more effective job search. Since the program informed participants who attended the meeting that they were not required to receive additional services after the meeting, moral hazard effects would be more limited after that point, but we expect

18

Wage records are used to measure earnings but not to measure length of employment or hourly wages in a given quarter. Thus, any treatment-control differences in average quarterly earnings, conditional on employment in the quarter, may be attributed both to differences in hourly wages and number of hours worked during the quarter. Page 26

services effects to be of primary importance subsequent to the meeting. Thus, services effects are expected to be dominant in week 7 or later, after the interactions of the vast majority of participants with the program had ended. Table 5 above indicates that 95 percent of treatment cases had a scheduled meeting in weeks 2-6 of their UI spell and that approximately 80 percent of these attended the meeting, fulfilling program requirements. To provide a more precise indicator of the relatively importance of moral hazard effects as compared to services effects in each week, we divided the sample of treatment cases that are in the risk set for exiting UI in each week into three groups. Group A for a particular week t consists of treatment cases that: (1) were scheduled for the meeting in week t or later; (2) did not show up for their scheduled meeting prior to week t and were not coded as receiving any job-search services; or (3) attended the meeting prior to week t and were disqualified because of findings of ineligibility. We assume that these treatment cases are subject to moral hazard effects, stemming from voluntary UI exit to avoid program requirements or from disqualification for failure to meet requirements.19 It is unlikely that services effects are relevant for these cases. Group B consists of treatment cases that missed their scheduled meeting prior to week t, but had received job-search services. According to program rules, these individuals were not subject to disqualification because of failure to show up for the meeting, because their services receipt was taken as indication that they were searching for a job. Using the information for treatment cases for which the timing of services is available, we find that the vast majority received services prior to or at the time their meeting was scheduled.20 Thus, we assume that, for many in this group, both

19

Data show that, of treatment cases that were still receiving UI in a given week, about 0.2–0.5 percent were disqualified in weeks 2-8 (see Appendix A). There were no disqualifications in week 1 or after week 8. 20 A total of 485 treatment cases did not complete their required meeting but received services, with service dates information available for 129 of these cases. Of these, 110 (85 percent) had received services prior to or at the week when the REA was scheduled. Page 27

moral hazard and services effects are likely to be relevant. Moral hazard effects may occur because these participants are unaware that they are exempt from the meeting because they received services, so some may drop out of UI to avoid program requirements. Services effects may occur because they had already received services. Finally, Group C comprises those that attended the meeting and passed the eligibility review, and thus fulfilled program requirements, prior to week t. Given that these individuals were informed that they had satisfied program requirements, we expect that services effects are most likely to be relevant. Figure 1 identifies the relative sizes of these groups as a function of the time since the start of their UI spell. In weeks 1-2, all individuals are in Group A, since no meetings occurred prior to that point. With many treatment cases attending scheduled meetings in weeks 2–5, the proportion in Group A declines to less than half by week 4 and to only about 18 percent by week 6. During this period, Group B is relatively small, remaining under 9 percent. Because many treatment cases attended meetings in weeks 2-4, starting in week 5, the majority of the at-risk participants consists of those in Group C. In week 6, after the period when the majority of meetings were scheduled, Group C accounts for about 73 percent of the at-risk group. The Group C proportion increases steadily over time thereafter, approaching a maximum of over 85 percent in week 11. These figures suggest that the timing of program effects on the likelihood of exiting UI, conditional on having not exited in a prior week,21 can be used to assess the relative importance of moral hazard and services effects. Any program effects on UI exit in weeks 1-3 would be primarily attributable to moral hazard, while any effects in weeks 4-5 are likely attributable to both moral hazard and services. Any effects on UI exit in week 6 or later, after the interactions of most

21

In the discussion that follows, our reference to the likelihood of exit, or simply UI exit, will refer to the probability of exiting in a given week, conditional on not having exited in a prior week. This probability is a good approximation to the continuous-time hazard for small probabilities. Page 28

participants with the program had ended, would most likely reflect services effects. To identify the importance of moral hazard and services, we estimate treatment-control differences in the likelihood of exiting UI in each week, conditional on having not exited in prior weeks. Although random assignment assures that initial treatment-control differences in UI exit are due to program participation, differences for subsequent weeks may reflect both program effects and dynamic selection, especially if a larger share of treated cases discontinued UI receipt early in the UI spell. The possibility of such selection effects has been recognized in previous work (e.g., Black et al, 2003; Geerdsen, 2006; and Graversen and van Ours, 2008). Where such selection is based on measured variables, accounting for selection requires that we control for the impact of these measures on the hazard at each point in time. We adopt a very general structure, taking the UI exit likelihood in week t for individual i (Hti) as a function of program assignment (𝑇𝑖 ), measured characteristics (𝑋𝑖 ), with parameters (𝑎𝑡 , 𝑏𝑡 , 𝑐𝑡 ): [3]

𝐻𝑡𝑖 = 𝑎𝑡 + 𝑏𝑡 ∙ 𝑇𝑖 + 𝑋𝑖 ∙ 𝑐𝑡

Central to this specification is that we allow the program effect (𝑏𝑡 ) to change over time, which is consistent with the view that program effects are likely to vary between early in the UI spell, when moral hazard effects would predominate, and subsequently, when services effects would be operable. Our model also allows for the possibility of selection on measured characteristics and that measured characteristics have differing impacts over time, as reflected in the vector of parameters 𝑐𝑡 . This accounts for potential heterogeneity of effects in measured characteristics without making strong assumptions about the structure of the relationship between observables and the UI exit likelihood. In our analysis, the time period will be a week, and the dependent variable will be a dichotomous measure indicating exit from UI during that week, with the sample

Page 29

limited to those who had not exited in prior weeks.22 Our approach is much more flexible than previous studies that estimate UI exit assuming program effects and/or the effects of observed characteristics are constant over time and affect the exit likelihood proportionally (e.g., Gorter and Kalb, 1996; Abbring et al., 2005; Hägglund, 2011) Our specification does not account for unobserved heterogeneity across individuals, which could cause bias if selection occurred early in the spell on unmeasured factors that influence UI exit. Adjusting for such heterogeneity requires that the model distinguish between unobserved heterogeneity and duration dependence, which must be based on functional form assumptions, given that we have information on only one spell per person (Wooldridge, 2010). Studies that model unobserved heterogeneity in estimating reemployment program effects assume that dynamic selection downwardly biases program effect estimates later in a spell.

Such an

assumption implies that our program effects in later weeks would be underestimated, which is consistent with the view that, since the burden of program participation occurs early in a spell, those with the longest expected spells are less likely to exit UI early in response to program demands.

Graverson and van Ours (2008) report that failing to allow for unmeasured

heterogeneity understates program effects by about 25 percent, but their data are limited to a single spell per individual. Geerdsen (2006) uses multiple spells to identify heterogeneity and reports that estimated program effects do not change substantially when heterogeneity is permitted.23 Although we know of no estimated models that allow for unmeasured heterogeneity where dynamic selection causes program effect estimates to be upwardly biased later in a spell, this is a

22

This model was estimated using a linear probability model; we also estimated this model using probit, but results were essentially identical. 23 In examining employment transitions following a training program, Ham and LaLonde (1996) and Eberwein et al. (1997) develop models allowing for unmeasured heterogeneity across multiple spells. In common with the aforementioned studies, their models imply that such heterogeneity causes exit likelihood differentials to understate program effects at longer spell durations. Page 30

theoretical possibility. For example, Black et al. (2003) observe “that persons with low hazard rates in the treatment group [could] exit UI in the first few weeks at higher rates than similar persons in the control group,” which would cause the treatment-control difference in the observed exit likelihoods to overestimate the treatment’s causal impact (p. 1322). In terms of the Nevada program, if the eligibility review – or the prospect of an eligibility review – was particularly likely to induce exit for those who expected to receive UI for an extended period, perhaps because they had no intention of undertaking meaningful job search, this would lead to an upward bias in estimated effects later in the spell. Following presentation of our main results below, we present a formal model to examine the potential effects of selection and undertake analyses showing that selection is not large enough to explain the patterns of our estimated program effects over time.

RESULTS Effects on UI Receipt Table 8 presents the average treatment effect for UI receipt outcomes based on equation [1], along with the effect as a percentage of the control group mean. The program led to a 10.4 percentage-point reduction in the likelihood of exhausting regular UI, which means that, compared to the control group mean, the program reduced regular UI exhaustion by 15 percent. This effect translates into a 16 percent reduction in the likelihood of EUC receipt. The program also had substantial effects on UI duration, reducing regular UI spells by 1.9 weeks and EUC spells by 2.5 weeks. The program is estimated to reduce total UI duration (regular UI plus EUC) by 4.4 weeks, implying that treatment cases collected 12 percent fewer benefit weeks than control cases. As a result, the program led to a $520 reduction in regular UI and a $625 reduction in EUC, for a $1,145 reduction in benefits collected. Thus, the average UI savings per treatment case were nearly six times the estimated average program cost of $201. Page 31

Finally, the program reduced the likelihood of EUC exhaustion by 2.8 percentage points, a 15percent reduction over the control group mean. This result suggests that the reported program effects on total UI duration and benefits collected under the regular UI and EUC programs almost surely underestimate effects on UI receipt outcomes that also include EB. We can obtain a rough estimate of the potential bias under the assumption that, for those who exhausted EUC, the program had no effect on the likelihood of or length of time collecting EB, and that all individuals used their entire EB entitlement. The bias is obtained by multiplying the treatment-control difference in the likelihood of exhausting EUC (2.8 percentage points) times the average EB entitlement. In this case, we underestimate program effects on total UI spells by .5 weeks and on total benefit collected by $151. Although other assumptions would produce somewhat different estimates, it is nonetheless clear that omission of EB does not substantively change our findings.

Effects on Employment and Earnings We next turn to effects on the level of employment and earnings receipt. Table 9 shows that treatment cases were 7.0 and 8.2 percentage points more likely to be employed in quarters 1 and 2, respectively, than control cases. The program’s effect on employment gradually declined over time, but remained positive and statistically significant through quarter 6, the last quarter for which we have employment data. As noted, even with a positive impact on employment, if the program pushed participants into inferior jobs, lower earnings in such jobs might more than compensate for the higher employment rates. We do not find, however, evidence supporting such concerns since the program had positive and statistically significant effects on earnings in each quarter over our follow-up period. Over the entire six-quarter period following UI entry, treatment cases had $2,607 (18 percent) higher earnings than control cases.

Page 32

Based on equation [2], we decompose the treatment-control difference in average earnings into two components – the first due to greater employment likelihood in a quarter, and the second due to higher earnings, conditional on employment in a quarter. In Figure 2, the lower portion of the bar area is the contribution of the employment component and the upper area is the conditional earnings component. Both components contributed positively to program effects, reflecting greater levels of employment within a quarter for the treatment cases but also higher average earnings for those employed. In the first two quarters, over 80 percent of the effect on earnings is attributed to the employment component (86 and 83 percent, respectively). In quarters 3-6, 70-73 percent of the effect is attributable to the employment component, with the remaining attributable to the conditional earnings component.24 Thus, although program effects on earnings are largely due to greater levels of employment, a portion of the effects, particularly in quarters 3-6, is due to higher earnings conditional on employment. These results suggest that the Nevada program was indeed effective in facilitating UI exit and reemployment of recipients. The fact that participants had higher earnings relative to nonparticipants conditional on employment suggests the possibility that the program is placing them in jobs that offered higher hourly wages and/or more hours of employment than the jobs they would have obtained in the absence of the program, consistent with the view that services provided by the program were responsible for an improvement in job matches. Alternatively, the program may have facilitated or encouraged employment for those able to obtain higher wages once employed. Our analyses do not distinguish between these alternatives, but in either case, the program clearly led to an improvement in labor market outcomes.

24

An alternative way of decomposing the earnings effects is to use the conditional earnings of the control group in the employment component, and the probability of employment for the treatment group in the earnings component: 𝑌𝑇 − 𝑌𝐶 = (𝐸𝑇 − 𝐸𝐶 ) ∙ 𝑊𝐶 + 𝐸𝑇 ∙ (𝑊𝑇 − 𝑊𝐶 ). This decomposition yields similar results, with the employment component accounting for 83, 79, 65, 69, 83, and 67 percent of the effect in Quarters 1-6, respectively. Page 33

Previous studies produced mixed evidence that programs improved earnings and no evidence that earnings contingent on employment were increased. Black et al. (2003) found that the program’s moral hazard effect led to small effects on earnings in the first two quarters but not in subsequent quarters, while Decker et al. (2000) found small effects in Washington, DC and no effects in Florida. Klepinger et al. (2002) did not find any earnings effects, whereas most of the aforementioned European studies did not estimate effects on earnings. The fact that we find positive effects for up to six quarters after entry and higher earnings contingent on employment suggests that the mechanism underlying our results may differ from those of other programs.

Effects on UI Exit Likelihood Figure 3 presents estimated program effects on the UI exit likelihood based on equation [3] for weeks 1 through 25, as well as each parameter’s .05 confidence interval. For example, the figure shows that, in week 2, for those who had not exited in week 1, treatment cases were 1.8 percentage points more likely to exit than control cases. Treatment-control differences in the initial weeks are positive and statistically significant and, although there is a generally declining trend, with the exception of week 10, the estimates are statistically significant through week 15. Overall, the UI exit likelihood by week 15 is estimated to be 31.5 percent for control cases and 40.6 percent for treatment cases, which means that program participation increased UI exit in the first 15 weeks by 9.1 percentage points (29 percent).25 A portion of this effect was realized in weeks 1-5, when the cumulative UI exit likelihood was 15.6 percent for the treatment and 9.8 percent for the control group, a 5.8 percentage-point difference. In week 1, the program increased UI exit by 0.7 percentage points, an effect that is 25

Throughout this section, the exit rates for program participants are based on the regression adjustment obtained from equation [3]. Page 34

entirely due to moral hazard because none of the at-risk population was scheduled to undergo the review prior to week 1. In each subsequent week, the proportion of the at-risk sample subject to moral hazard effects declined, as more treatment cases attended the meeting and fulfilled program requirements. Still, the observed effects in weeks 2-5 – ranging from 1.1 to 1.8 percentage points – could be primarily attributable to moral hazard. These effects reflect the fact that 0.2 to 0.5 percent of treatment cases were disqualified in weeks 2-5 either because they did not attend or reschedule the meeting, or because of findings of ineligibility during the review (see appendix Table A1). The remaining effect in this period is primarily attributable to treatment cases that discontinued UI voluntarily to avoid program requirements and, possibly, to a lesser extent, to services effects for cases that had completed program requirements. The key finding here is that a substantial portion of program effects occurred in week 6 or later, when moral hazard effects due to voluntary exit or disqualifications are less likely and services effects are expected to be important. In week 6, for example, the proportion of the at-risk population subject primarily to services effects (Group C) was about 73 percent, increasing over time and approaching 85 percent by week 10. Among those who had not exited by week 5, we find that the UI exit likelihood in weeks 6-15 was 29.6 percent for treatment and 24.1 percent for control cases. Thus, program participation is associated with a 5.5 percentage-point (23 percent) increase in UI exit in weeks 6-15.26 In contrast, Black et al. (2003) report that three-quarters of program effects occurred in weeks 1 and 2 of the 12-week period in which positive effects were observed, while estimated effects in weeks 3-12 were not statistically significant. We therefore conclude that, although our results confirm that moral hazard plays an important role in explaining program effects, the substantial effects occurring after weeks 5 or 6 are most likely attributable to

26

Only 0.6 percentage points (13 percent) of this effect is attributable to disqualifications occurring in weeks 6-8. Page 35

services.

Robustness Tests In this section, we focus on differences in the time patterns of UI exit between treatment and control cases to investigate potential sources of bias caused by weaknesses in our design. We begin by considering how dynamic selection may influence estimated program effects later in the UI spell, with the result that estimates may misrepresent the program’s causal impacts. We then turn to the question of the relative importance of moral hazard and service effects, providing a detailed analysis of the timing of scheduled meetings and the pattern of UI exit. We also discuss the possibility that participants may respond to implicit program imperatives even after program requirements have been met, implying that our approach overstates services effects. Finally, we comment on general equilibrium effects, which may cause our estimates to overstate realized impacts if the program were to be widely implemented. We first turn to the concern that, because the program induces some participants to exit near the beginning of the UI spell, selection may alter the composition of treatment and control groups, inducing bias in estimated program effects in later weeks. Although we cannot directly measure such selection effects, we can characterize the potential bias for the estimated effect in any given week since it is a function of the size of prior treatment effects. In particular, consider the observed probability in week t>1 that a control case exits, conditional on it not having exited prior to t, as 𝐻𝑡𝑐 . Denote the proportion of cases that have not exited from the control and treatment groups prior to t as 𝑆𝑡𝑐 and 𝑆𝑡𝑝 , respectively (these are the proportions of the original samples in the risk sets in week t). As observed in our analysis, treatment cases are induced to exit the program at a higher rate prior to week t, that is 𝑆𝑡𝑐 > 𝑆𝑡𝑝 . We assume that treatment cases that are in the risk

Page 36

set in week t would have been in the risk set if they had been assigned to the control. In contrast, some individuals assigned to the control group who are in the risk set at time t would have exited in a prior week if they had been in the treatment. Denote the UI exit likelihood of this group in week t as 𝐻𝑡𝑐−𝑝 . Under the assumption that the treatment has no effect at time t, we may write the observed UI exit likelihood for the treatment group as: [4]

𝑆𝑐

𝑆𝑐

𝑡

𝑡

𝐻𝑡𝑝∗ = (𝑆𝑡𝑝 ) 𝐻𝑡𝑐 − (𝑆𝑡𝑝 − 1) 𝐻𝑡𝑐−𝑝

The asterisk indicates that the exit likelihood is calculated under the assumption that there is no treatment effect at time t. Equation [4] provides a measure of the bias in the estimate, indicating how the estimated exit likelihood for the treatment group at time t is affected by selection due to program effects in prior weeks.27 The bias is increasing with the proportion of cases that exited due to the program in prior weeks. If those in the control group who would be omitted by the treatment prior to t are more likely than others to exit at time t (𝐻𝑡𝑐−𝑝 > 𝐻𝑡𝑐 ), the treatment estimate is downwardly biased. As we note above, this is the assumption implicit in most formal models. No bias occurs if the exit rate for omitted individuals is the same as those in the treatment risk set in week t. Our concern focuses on the case where the program culls out those who are less likely to exit later (𝐻𝑡𝑐−𝑝 < 𝐻𝑡𝑐 ), inducing a positive bias. To determine whether such bias could be large enough that observed estimates are wholly spurious, we make the extreme assumption that those who exited in prior weeks would have had no chance of exiting in week t, that is, we assume that 𝐻𝑡𝑐−𝑝 = 0. This assumption implies that, for such individuals, the program effect during week t is

27

To derive this expression, note that, if there is no treatment effect in week t, the exit hazard for the control group is just the weighted average of the exit hazard for the treated group in the risk set in week t and the exit hazard for those 𝑝

𝑆𝑡𝑐 −𝑆𝑡

who exited previously due to the treatment: 𝐻𝑡𝑐 = (

𝑆𝑡𝑐

𝑐−𝑝

) 𝐻𝑡

Page 37

𝑆

𝑝

𝑝∗

+ ( 𝑡𝑐 ) 𝐻𝑡 𝑆𝑡

the opposite of the program effect in prior weeks. Not only is this a very conservative assumption for the first few weeks of the UI spell, but it would appear highly unlikely in later weeks, implying that the actual bias is likely to be much smaller than this measure implies. Our analyses show that this measure of potential bias is modest throughout weeks 1-25. For weeks 2-6, the measure of potential bias ranges from .0001 to .0011, accounting for less than 12 percent of the estimated effect in any week.28 In weeks 7-11, the potential bias ranges between .0013 and .0016, whereas the average treatment effect is over .006. After adjusting for the subgroup that is eligible for exactly the specified number of weeks, the measure of the maximum potential bias in weeks 12-25 is between .0017 and .0030, in all cases less than the average effect of .004. 29 Given that our selection assumption is clearly extreme, these results suggest that selection effects could play at most a limited role in explaining program results in later weeks, when services effects are likely to be important. We next consider the relative importance of moral hazard and services effects in explaining the treatment-control differences in UI exit. As noted above, any program effects on individuals who have not attended the meeting and have not received job-search services (Group A) must be attributable to moral hazard. Similarly, effects for those who have missed their scheduled meeting but received services (Group B) may reflect moral hazard effects implicit in uncertain future program requirements, in addition to services effects. In contrast, those who have completed their meeting (Group C) no longer face program requirements, so program effects on UI exit are likely to reflect the value of services. In the prior section, we argued that effects in week 6 or after, when

28

𝑝∗

We estimate the bias as 𝐻𝑡 − 𝐻𝑡𝑐 = (

𝑆𝑡𝑐

𝑝

𝑆𝑡

𝑐−𝑝

− 1)𝐻𝑡𝑐 , based on Equation [4] and the assumption that 𝐻𝑡

29

= 0.

Note that, beginning in week 12, cases that exit include those eligible for exactly that number of weeks. After week 11, we adjust the bias estimate in each week to omit cases that are not eligible for additional weeks of UI. Note, our estimates of program effect also control for weeks of eligibility, so this adjustment is implicit in reported estimates. Page 38

Group C predominates, are likely to be due largely to service effects. The analysis here provides a more detailed examination of these effects based on observed exit probabilities for each group. For each of these three groups, we observe the likelihood of exiting in the specified week, but we cannot estimate separate program effects because we cannot determine what the exit likelihood would have been for each group in the absence of the program. However, we can calculate bounds for the treatment effects for groups based on various assumptions. For this analysis, we combine Groups A and B, the two groups for which moral hazard effects are expected to be important, and denote the proportion of the at-risk population in week t made up of this combined group as 𝑄𝑡𝑇 and the proportion made up of Group C, for which only services are likely important, as 𝑄𝑡𝑆 = 1 − 𝑄𝑡𝑇 . As above, denote 𝐻𝑡𝑘 the exit likelihood for treatment status k (k=p for treatment, k=c for control), and 𝐻𝑡𝑘𝑅 as the exit likelihood for treatment status k and group R (R=T for those in Groups A and B, and so subject to moral hazard effects; R=S for those in Group C, subject to service effects). The program’s effect in week t for Group C may be written as:30 [5]

𝑄𝑇

𝐻𝑡𝑝𝑆 − 𝐻𝑡𝑐𝑆 = (𝐻𝑡𝑝 − 𝐻𝑡𝑐 ) + 𝑄𝑡𝑆 [(𝐻𝑡𝑃 − 𝐻𝑡𝑐 ) − (𝐻𝑡𝑝𝑇 − 𝐻𝑡𝑐𝑇 )] 𝑡

The first term on the right-hand side is the estimated overall program effect (𝐻𝑡𝑝 − 𝐻𝑡𝑐 ) and the remaining expression indicates how this must be adjusted to identify the effect for Group C. The 𝑄𝑇

adjustment is a function of the relative size of the two groups in the risk set in week t (𝑄𝑡𝑆 ) and the 𝑡

extent to which the program effect for the moral hazard group differs from the overall estimate. If the program effect is the same for both groups, the overall effect estimate 𝐻𝑡𝑝 − 𝐻𝑡𝑐 is a valid

𝑝

𝑝𝑆

𝑝𝑇

This expression is based on the observation that 𝐻𝑡 = 𝑄𝑡𝑆 𝐻𝑡 + 𝑄𝑡𝑇 𝐻𝑡 and 𝐻𝑡𝑐 = 𝑄𝑡𝑆 𝐻𝑡𝑐𝑆 + 𝑄𝑡𝑇 𝐻𝑡𝑐𝑇 . Possible selection effects prior to week t are ignored, so that sample proportions are taken to be the same in the treatment and control group. Differences in exit probabilities between treatment and control groups identify program effects. 30

Page 39

estimate of the program effect for both groups. Our primary concern focuses on the possibility that the correction term is negative, so that a positive overall program effect may result entirely from a strong moral hazard effect, i.e., overall program effects reflect the effects on Groups A and B, while there is little or no effect for Group C. The data provide us with estimates for all terms on the right-hand side of this equation except for 𝐻𝑡𝑐𝑇 , the exit likelihood in the absence of the program for those assigned to the program and subject to moral hazard effects (Groups A and B). Among our robustness tests, we consider the size of the adjustment for alternative values of 𝐻𝑡𝑐𝑇 . One possibility is that 𝐻𝑡𝑝𝑇 − 𝐻𝑡𝑐𝑇 = 𝐻𝑡𝑝𝑆 − 𝐻𝑡𝑐𝑆 , meaning that the program’s effect on Group C is the same as the combined effect for Groups A and B. Alternatively, we consider the possibility that 𝐻𝑡𝑐𝑇 = 𝐻𝑡𝑐𝑆 , meaning that, in the absence of the program, the exit likelihood for Group C would be the same as the exit likelihood for the combined Groups A and B. Figure 4 presents estimated program effects for Group C under these assumptions. The solid black line reproduces the estimates in Figure 3; as indicated in Equation [5], if the moral hazard effect is equal to the services effect, the estimated overall program effect is the appropriate estimate both for service and moral hazard effects. Since the observed UI exit rate for Groups A and B generally exceeds that for Group C, this assumption implies the Groups A and B would have had a higher exit likelihood even in the absence of the program. This is consistent with the view that those expecting to exit UI sooner would have more limited incentives to attend the meeting. In the extreme, those expecting jobs to begin in the week or two following the meeting, a group very likely to exit in the absence of the program, would have had minimal incentives to attend the meeting.

Page 40

In order to get a plausible upper bound for the potential bias in the estimated effect of services, we calculate the service effect under the assumption that the combined exit likelihood for those who had not met program requirements (Groups A and B) would have been the same as those who attended the meeting (Group C), if they had all been assigned to the control group. In other words, we assume that those subject to moral hazard effects would have been no more likely to exit UI in a given week in the absence of the program than those subject to service effects. The dashed line in Figure 4 provides an estimate of the program effect for Group C under this assumption. (Since no individuals completed meetings prior to week 2, there is no estimate of the service effect in weeks 1-2.) This estimate is positive in all but one of the weeks up to week 17. Our best guess of the likely service effect is between these two estimates. If one believes that those who fail to meet program requirements would be no more likely to exit in the absence of the program than those who go through with the required meeting, then the dashed line would be the most reasonable estimate. However, the large negative estimate in weeks 23-25 under this assumption suggests that it is too extreme. Such large negative program effects many weeks following the meeting when participants completed program requirements seem highly implausible. If one suspects that those who missed their scheduled meeting would have been more likely to exit in the absence of the program than those who at met requirements, the best estimate would be above the dashed line.31 We interpret our results to imply that services play a substantial role in explaining program effects based on the assumption that, after completing the scheduled meeting, participants no longer felt pressure to exit UI, due either to anticipated monitoring burdens or program

31

We also considered the extreme assumption that the exit likelihood in the absence of the program for those who had not yet met program requirements (Groups A and B) would have been zero in the absence of the program. Under this assumption, the service effects on UI exit were strongly negative in weeks 1-4, and negative in weeks 14-25, clearly implausible results, leading us to reject this assumption. These results are available upon request. Page 41

requirements. If this assumption is false, despite the statement to participants that program requirements had been met, moral hazard effects could be partly responsible for observed effects even in later weeks. Note, however that previous U.S. studies found strong moral hazard effects but little evidence that such effects persisted after the period when participants completed program requirements. The Nevada program produced large cumulative effects after the period when participants were exposed to the intervention, which is consistent with the view that the services provided by the program were effective. Nonetheless, we cannot rule out the possibility that, by providing more extensive job-search services, counselors imposed implicit pressure on participants to undertake more intense job search. If this was the case, the program would appear to have been more successful than prior programs partly because it activated increased search efforts. We should note that the size of the moral hazard effect partly depends on the perceived burden of the program. It is possible that if the program were in place for an extended period, participants would realize that the program’s requirements were less onerous than participants in the study believed them to be. In this case, if the program was implemented over the long-term, the moral hazard effect would be reduced. The effects of job-search services might be expected to survive even in the long-term if they reflected the direct service benefits, although, if participants’ jobsearch effort reflected a concern with anticipated sanctions, our measure of service effects could be reduced as well. Finally, we should note that, in common with other experimental studies of reemployment programs, our results identify program effects for participants as compared to a control group, which may not be the same as effects of the program if it were implemented for the full population. As Graversen and van Ours (2008) observe, where the treatment group is small relative to the

Page 42

control, as is the case in our study, it is unlikely that results will be biased by spillover effects altering control outcomes. However, it is still possible that participants may displace nonparticipants searching for jobs, so that estimated effects would be larger than the general equilibrium effects that would occur if the program were widely implemented. During a recession, with the number of jobs limited, one might assume that such displacement would be particularly likely. In fact, the evidence on this issue is mixed. Some studies find substantial evidence of displacement effects, particularly among the long-term unemployed youth (Feracci et al., 2010; Gautier et al., 2012; Crepon et al., 2013). Toohey (2015) finds that increased job-search efforts due to state rules have only modest effects on unemployment spells, especially during downturns, and he suggests that this is due to displacement (see also Lise et al., 2004). In contrast, Martins and Possoa e Costa (2014) conclude that displacement is not important and that targeted groups who benefited from the reemployment program they examined did not do so at the expense of other groups. Other studies find that job-search assistance and employment subsidies have substantial positive impacts even when they are provided to a large share of unemployed workers in particular geographic areas, suggesting the displacement effects are minor (Blundell et al., 2004; De Giorgi, 2005).

CONCLUSION AND DISCUSSION This paper examined the effectiveness of a program implemented in the United States during the Great Recession that required new UI recipients to undergo an eligibility review and receive job-search services at the early stages of their UI spells. Our analyses show that the program reduced average UI duration by nearly 4.4 weeks and average total benefits collected by $1,145, with UI savings exceeding average program costs by nearly six times. These effects are partly

Page 43

attributable to moral hazard, given that the program pushed some participants to exit UI during the timeframe in which participants received notification of their assignment to the program and were required to attend a meeting and pass an eligibility review to continue collecting benefits. But a substantial increase in UI exits occurred in the 10-week period after the interactions of most participants with the program had ended, when services effects were likely to have been important. We show that these effects cannot be attributed to dynamic selection because of the program’s early moral hazard effects. Our findings suggest that the services offered to participants were effective in enhancing their job-search skills or motivating them to pursue a more intensive job search. The plausibility of the view that the value of services contributed to program success is supported by our finding that the program had substantial positive effects on both employment and earnings throughout the entire six-quarter follow-up period, leading to an increase in earnings of $2,607 (18 percent) over that period. Since the program is also associated with increased earnings conditional on employment, it does not appear that the program produced average earnings increases by pushing unprepared workers into the labor market. The findings of this paper confirm those of recent U.S. and European studies that reemployment program requirements increase the cost of collecting UI, pushing participants who are job-ready or noncompliant with work-search requirements to exit unemployment. Our findings show that such moral hazard effects may occur during a recession when jobseekers have fewer job options and are eligible for unemployment benefits for extended periods. Our findings also show that, in addition to moral hazard effects, a program requiring participants to receive comprehensive jobcounseling services may have services effects. Services may provide direct aid to participant jobsearch efforts, facilitating their UI exit and movement into employment and helping them to achieve higher earnings. These findings are in contrast to those of recent studies of U.S. programs,

Page 44

which provided participants with less substantial interventions and had limited effects on participant employment and earnings. Our findings suggest that programs requiring participation in job-counseling services may be successful in part because participants benefit from job-search services but would not seek them out in the absence of a program requirement. Another possible interpretation is that provision of services may indirectly influence the behavior of participants, encouraging them to conduct a more intensive job search after program requirements are satisfied. Regardless of the actual mechanism underlying program effects, our findings suggest that providing direct services may be valuable. Thus, European programs that provide a combination of job-counseling services and work search monitoring may influence participants beyond the incentive effects that previous studies have focused on. In conclusion, our results lend support to the view that reemployment services programs may be valuable during a recession, when the need is greatest.

Although identifying general

equilibrium effects is beyond the scope of this study, the results point to the possibility that, in the face of a weak labor market, government-sponsored reemployment programs – which combine mandatory monitoring activities and job-search services participation – may provide an effective strategy to both reduce the moral hazard of UI and help unemployed workers to conduct more effective job search.

Page 45

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Table 1: Treatment and Control Group Characteristics Treatment

Control

Sample Size

4,673

27,120

Female

.422

.433

-.011 [.008]

Hispanic

.211

.202

.010 [.006]

No High School Diploma

.164

.163

.001 [.006]

High School Diploma

.426

.435

-.009 [.008]

Some College

.288

.283

.005 [.007]

College Degree

.122

.119

.003 [.005]

Less than 25 Years

.123

.127

-.003 [.005]

25-34 Years

.257

.249

.008 [.007]

35-44 Years

.221

.229

-.007 [.007]

45-54 Years

.227

.218

.009 [.007]

55-64 Years

.128

.130

-.002 [.005]

65+ Years

.043

.047

-.004 [.003]

U.S. Citizen

.900

.899

.001 [.005]

Disabled

.050

.046

.004 [.003]

White Collar, High Skill

.192

.191

.001 [.006]

White Collar, Low Skill

.319

.320

-.001 [.007]

Blue Collar, High Skill

.233

.224

.009 [.007]

Blue Collar, Low Skill

.256

.265

-.009 [.007]

Prior Quarter 1 Earnings

7,073 (7,186)

7,078 (6,829)

-5 [113]

Prior Quarter 2 Earnings

7,132 (6,573)

7,310 (9,224)

-178 [111]

Prior Quarter 3 Earnings

7,398 (7,362)

7,445 (7,256)

-47 [116]

Prior Quarter 4 Earnings

7,585 (7,008)

7,488 (8,312)

97 [114]

Difference

Note: The treatment and control columns report the sample means for dichotomous measures and the sample means with standard deviations in parentheses for non-dichotomous measures. The difference column reports the treatmentcontrol differences in means with standard errors in brackets. Source: Nevada UI claims data (individual characteristics); Nevada UI wage records (prior earnings).

Page 50

Table 2: Treatment and Control Group Benefit Entitlements

Regular UI Weeks Eligibility Regular UI Cumulative Entitlement ($) EUC Weeks Eligibility EUC Cumulative Entitlement ($) EB Weeks Eligibility EB Cumulative Entitlement ($) Total Weeks Eligibility Total Cumulative Entitlement ($)

Treatment

Control

Difference

22.8 (4.6)

22.9 (4.5)

-.1 [.07]

7,075 (3,046)

7,056 (3,033)

19 [48]

46.3 (9.4)

46.6 (9.2)

-.3 [.2]

14,271 (6,084)

14,238 (6,057)

33 [96]

17.6 (3.5)

17.7 (3.5)

-.1 [.1]

5,410 (2,296)

5,396 (2,284)

13 [36]

86.7 (17.6)

87.2 (17.3)

-.5 [.3]

26,756 (11,603)

26,690 (11,556)

66 [183]

Note: The treatment group and control group columns report the sample means with standard deviations in parentheses. The difference column reports the treatment-control differences in means with standard errors in brackets. Source: Nevada UI claims data.

Table 3: Unemployment Insurance Receipt Outcomes Treatment

Control

Exhausted Regular UI Benefits

.604

.710

Collected EUC Benefits

.500

.599

Exhausted EUC Benefits

.162

.191

Regular UI

17.1 (8.5)

19.0 (7.9)

EUC

14.9 (18.9)

17.5 (19.2)

Total

32.0 (24.4)

36.5 (23.6)

Regular UI

5,352 (3,498)

5,863 (3,416)

EUC

4.621 (5,258)

5,258 (6,274)

Total

9,973 (8.749)

11,119 (8,535)

Weeks Collected

Benefits Amounts Collected ($)

Note: The treatment and control columns report sample means for dichotomous outcomes and the sample means with standard deviations in parentheses for non-dichotomous measures. Source: Nevada UI claims data.

Page 51

Table 4: Employment and Earnings Outcomes Treatment

Control

Quarter 1

.476

.406

Quarter 2

.498

.414

Quarter 3

.526

.458

Quarter 4

.551

.487

Quarter 5

.539

.487

Quarter 6

.548

.500

Quarter 1

1,848 (3,659)

1,529 (3,247)

Quarter 2

2,479 (4,176)

1,977 (3,726)

Quarter 3

3,028 (4,715)

2,475 (4,347)

Quarter 4

3,188 (4,885)

2,674 (4,528)

Quarter 5

3,174 (4,967)

2,811 (5,338)

Quarter 6

3,405 (5,172)

2,987 (4,888)

17,122 (22,570)

14,453 (21,065)

Employed

Earnings ($)

Total, Quarters 1-6

Note: The treatment and control columns report the sample means for dichotomous outcomes and the sample means with standard deviations in parentheses for non-dichotomous measures. Source: Nevada UI claims data.

Page 52

Table 5: Meeting Scheduling and Completion Rates Meetings Scheduled [sample proportion]

Completers

4,673 [1.000]

3,717 (80%)

1

--

--

2

993 [.212]

796 (80%)

3

1,563 [.334]

1,227 (79%)

4

997 [.213]

773 (78%)

5

602 [.129]

482 (80%)

6

291 [.062]

242 (83%)

7

107 [.023]

95 (89%)

8+

120 [.026]

102 (85%)

Week

Note: The first data column reports the distribution of meetings scheduled by week with sample proportions in brackets. The rightmost column reports the number and proportion of treatment cases that completed the meeting, as scheduled, in the specified week. Source: Nevada employment service data.

Table 6: Service Take-Up Rates, Treatment vs. Control Group Treatment

Control

Difference

Any Staff-Assisted Services

.684

.097

.587 [.005]**

Work Search Plan

.555

.061

.494 [.005]**

Resume Assistance

.257

.025

.231 [.004]**

Job Referral

.214

.042

.172 [.004]**

Group Orientation

.315

.035

.279 [.004]**

Individual Needs Assessment

.326

.039

.286 [.040]**

Employment Workshops

.138

.015

.122 [.003]**

Number of Job Referrals

.31 (.87)

.11 (.68)

.21 [.01]**

Note: Staff-assisted services include: work search plan, resume assistance, job referrals, group orientation, individual needs assessment, and employment workshops. They do not include the eligibility review. ** = treatment-control difference is statistically significant at the 1 percent level. Source: Nevada employment service data.

Page 53

Table 7: Timing of Services, Treatment Group Date of Service Available

Received Service

Individuals with Service Dates

Before Meeting

At Meeting

After Meeting

Staff-Assisted Services*

3,195

1,296

346 (27%)

1,037 (80%)

307 (24%)

Work Search Plan**

2,593

1,085

189 (17%)

824 (76%)

72 (7%)

Resume Assistance**

1,200

504

86 (17%)

374 (74%)

44 (9%)

Job Referral*

1,002

424

74 (17%)

224 (53%)

200 (47%)

Group Orientation**

1,470

607

144 (24%)

393 (65%)

70 (12%)

Individual Needs Assessment**

1,522

634

78 (12%)

456 (72%)

100 (16%)

644

270

57 (21%)

144 (53%)

69 (26%)

Employment Workshop**

Note: The first data column reports the number of treatment cases that received services and the second data column the number of treatment cases that received services for which service dates are available. The three right columns identify for the latter group whether participants received services before, during, or after the week when the meeting was scheduled. *= Individuals may have received more than one service and thus before/at/after meeting proportions may add to more than 100 percent. **= Only last date of service is observed and thus before/at/after meeting proportions add to 100 percent. Source: Nevada employment service data.

Page 54

Table 8: Average Treatment Effects, UI Receipt Average Treatment Effect

Percentage of Control Group Mean

Exhausted Regular UI Benefits

-.104 (.007)**

-15

Collected EUC Benefits

-.097 (.008)**

-16

Exhausted EUC Benefits

-.028 (.006)**

-15

Regular

-1.9 (.1)**

-10

EUC

-2.5 (.3)**

-14

Regular + EUC

-4.4 (.4)**

-12

Regular

-520 (38)**

-9

EUC

-625 (96)**

-12

-1,145 (120)**

-10

Weeks on UI

UI Benefits Collected ($)

Regular + EUC

Note: The left data column reports average treatment effects, with standard errors in parentheses; the right column reports each average treatment effect as a percentage of the control group mean. **= statistically significant at the 1 percent level.

Page 55

Table 9: Average Treatment Effects, Employment and Earnings

Employed Quarter 1 Quarter 2 Quarter 3 Quarter 4 Quarter 5 Quarter 6 Earnings ($) Quarter 1 Quarter 2 Quarter 3 Quarter 4 Quarter 5 Quarter 6 Total, Quarters 1-6

Average Treatment Effect

Percentage of Control Group Mean

.070 (.008)** .082 (.008)** .066 (.008)** .063 (.008)** .052 (.008)** .046 (.008)**

17 20 14 13 11 9

315 (51)** 493 (59)** 542 (68)** 504 (70)** 348 (81)** 404 (75)** 2,607 (322)**

21 25 22 19 12 14 18

Note: The left column reports the average treatment effects with standard errors in parentheses; the right column reports each average treatment effect as percentage of the control group mean. **= statistically significant at the 1 percent level.

Page 56

Figure 1: Treatment Cases, Classified by Meeting and Services Receipt

Note: Proportion of at-risk treatment cases in each week for Groups A, B and C. Group A = treatment cases scheduled for the meeting in current or subsequent week; missed their meeting and did not receive services; or were disqualified for failure to attend meeting or for findings of ineligibility. Group B = treatment cases that missed scheduled meeting but received services. Group C = treatment cases that attended the scheduled meeting and passed the eligibility review.

Page 57

Figure 2: Decomposition of Average Treatment Effects on Quarterly Earnings Program ATE on Quarterly Earnings $600 $500 $400 $300 $200

86%

83%

70%

72%

73%

70%

Q1

Q2

Q3

Q4

Q5

Q6

$100 $0 Employment Component

Conditional Earnings Component

Note: The full bar height indicates the program’s average treatment effect on quarterly earnings. The dark grey area is the portion of the effect attributed to the employment component (percentage of total effect reported) and the light grey area is the portion of the effect attributed to the conditional earnings component.

Figure 3: Regression-Adjusted Treatment-Control Group Difference in UI Exit Likelihood

Note: Black line presents regression-adjusted treatment-control differences in UI exit likelihood. The grey dotted lines encompass the 95 percent confidence interval. Estimates based on equation [3]. Page 58

Figure 4: Program Effect of Services under Alternative Assumptions

Note: Black line presents regression-adjusted treatment-control differences in the UI exit likelihood reproduced from Figure 3. This is equal to the service effect if program effects are the same for those who have completed program requirements and for those who have yet done so or have missed their scheduled appointment. The dashed line presents the effect of program services under the assumption that the exit likelihood in the absence of the program would have been the same for these two groups, so the unobserved exit likelihood does not differ by whether treatment cases had completed required meetings. Calculations are based on equation [5].

Page 59

APPENDIX Table A1: Program Disqualifications Disqualifications (proportion of at-risk population)

Week of UI Spell

Population At-Risk for Exit [sample proportion]

No Shows

Ineligibles

Total

1

4,673 [1.000]

0 (.000)

0 (.000)

0 (.000)

2

4,534 [.970]

5 (.001)

3 (.001)

8 (.002)

3

4,350 [.931]

10 (.002)

10 (.002)

20 (.004)

4

4,197 [.898]

9 (.002)

11 (.003)

20 (.005)

5

4,077 [.872]

6 (.001)

11 (.003)

17 (.004)

6

3,948 [.845]

2 (.001)

8 (.002)

10 (.003)

7

3,834 [.820]

1 (.000)

7 (.002)

8 (.002)

8

3,738 [.800]

1 (.000)

2 (.001)

3 (.001)

34

52

86

Total

Note: The first data column reports the number of treatment cases at risk of exiting in each week with sample proportion in brackets. No shows = number of treatment cases disqualified for failure to show up or reschedule the meeting with the proportion of at-risk population in parenthesis. Ineligibles = number of at-risk treatment cases who were disqualified for findings of ineligibility during the meeting with the proportion of at-risk population in parenthesis. Source: Nevada employment service data.

Page 60

Table A2: Regression Results, Likelihood of UI Exit Likelihood of UI Exit, Conditional on No Exit in Prior Weeks Week 1

Week 4

Week 7

Week 10

.007 (.002)**

.011 (.002)**

.010 (.002)**

.003 (.002)

.001 (.002)

.003 (.002)

.003 (.002)

-.001 (.002)

.017 (.002)**

.002 (.002)

.003 (.002)

-.001 (.002)

--

--

--

--

High School Diploma

-.010 (.003)**

-.002 (.002)

.003 (.002)

-.002 (.002)

Some College

-.013 (.003)**

.001 (.003)

.003 (.003)

-.000 (.003)

-.007 (.004)

.006 (.003)

.005 (.003)

.003 (.003)

--

--

--

--

25-34 Years

.001 (.003)

-.000 (.003)

-.001 (.003)

-.004 (.003)

35-44 Years

-.000 (.003)

-.002 (.003)

-.003 (.003)

-.009 (.003)

45-54 Years

-.002 (.003)

-.001 (.003)

-.004 (.003)

-.010 (.003)**

55-64 Years

-.008 (.004)*

-.009 (.003)**

-.011 (.003)**

-.010 (.003)**

65+ Years

-.013 (.005)**

-.012 (.004)**

-.010 (.004)*

-.012 (.004)*

U.S. Citizen

-.007 (.003)*

-.007 (.003)*

-.011 (.003)**

-.005 (.003)*

Disabled

-.004 (.004)

-.005 (.004)

-.005 (.004)

-.005 (.003)

White Collar, High Skill

--

--

--

--

White Collar, Low Skill

.001 (.003)

.004 (.002)

.003 (.002)

-.001 (.002)

Blue Collar, High Skill

.011 (.003)**

.009 (.003)**

.006 (.003)**

.008 (.003)**

Blue Collar, Low Skill

.021 (.003)**

.009 (.003)**

.000 (.003)

.004 (.003)

-.002 (.002)

-.002 (.002)

-.001 (.002)

-.003 (.002)

Prior Earnings, Quarter 1 (in $000s)

-.00019 (.00018)

-.00001 (.00017)

-.00011 (.00016)

.00011 (.00016)

Prior Earnings, Quarter 2 (in $000s)

.00001 (.00021)

.00012 (.00012)

.00002 (.00011)

-.00002 (.00011)

Prior Earnings, Quarter 3 (in $000s)

-.00012 (.00021)

-.00028 (.00019)

-.00012 (.00018)

.00019 (.00018)

Prior Earnings, Quarter 4 (in $000s)

-.00018 (.00016)

.00008 (.00015)

-.00005 (.00014)

-.00024 (.00013)

Treatment Female Hispanic No High School Diploma

College Degree Less than 25 Years

Log Cumulative Entitlement

(continues on next page)

Page 61

(continued from previous page) Regular UI Weeks Allowed 12 weeks

--

--

--

--

13 weeks

-.001 (.007)

.003 (.007)

-.001 (.006)

.004 (.006)

14 weeks

-.007 (.007)

.011 (.007)

.003 (.006)

-.002 (.006)

15 weeks

.003 (.007)

-.001 (.006)

.001 (.006)

-.002 (.006)

16 weeks

-.004 (.007)

.004 (.006)

.006 (.006)

-.002 (.006)

17 weeks

.002 (.007)

.007 (.007)

.004 (.006)

-.004 (.006)

18 weeks

-.003 (.007)

.003 (.007)

-.002 (.007)

.006 (.006)

19 weeks

-.001 (.007)

.011 (.007)

.002 (.006)

-.003 (.006)

20 weeks

-.002 (007)

.014 (.007)*

-.001 (.007)

.002 (.006)

21 weeks

.002 (.007)

.013 (.007)

.019 (.006)**

-.002 (.006)

22 weeks

.001 (.007)

.017 (.007)*

.009 (.007)

.008 (.006)

23 weeks

.004 (.007)

.020 (.007)**

.004 (.006)

.013 (.006)*

24 weeks

.005 (.007)

.014 (.007)*

.007 (.007)

.006 (.006)

25 weeks

.012 (.073)

.013 (.007)

.010 (.007)

.018 (.006)**

26 weeks

.014 (.006)*

.014 (.005)**

.007 (.005)_

.008 (.005)

.037 (.019)

.066 (.019)**

.027 (.018)

.070 (.018)**

Observations

31,793

29,558

27,908

26,758

R-Squared

.0018

.0037

.0036

.0035

Constant

Note: Estimated parameters based on equation [3]. **, * = statistically significant at the 1 percent, 5 percent level.

Page 62

Table A3: Regression Results, Likelihood of UI Exit Likelihood of UI Exit, Conditional on No Exit in Prior Weeks Week 13

Week 16

Week 19

Week 22

.010 (.002)**

.004 (.002)

.006 (.003)*

.004 (.003)

Female

-.002 (.002)

-.001 (.002)

-.002 (.002)

-.002 (.002)

Hispanic

-.003 (.002)

-.001 (.002)

.000 (.002)

.001 (.002)

--

--

--

--

High School Diploma

.000 (.002)

.004 (.002)

.002 (.003)

.001 (.003)

Some College

.003 (.003)

.003 (.003)

.001 (.003)

.004 (.003)

College Degree

.004 (.003)

.006 (.003)*

.007 (.004)

.007 (.004)

--

--

--

--

25-34 Years

-.011 (.003)**

-.005 (.003)

-.001 (.003)

.001 (.003)

35-44 Years

-.012 (.003)

-.006 (.003)*

-.002 (.003)

-.007 (.004)*

45-54 Years

-.010 (.003)**

-.007 (.003)*

-001 (.003)

-.007 (.004)*

55-64 Years

-.010 (.003)**

-.013 (.003)**

-.007 (.004)

-.009 (.004)*

65+ Years

-.012 (.004)*

-.010 (.004)*

-.014 (.005)**

-.008 (.005)

U.S. Citizen

-.005 (.003)*

-.002 (.003)

-.003 (.003)

.001 (.003)

Disabled

-.005 (.003)

-.004 (.004)

-.001 (.004)

-.001 (.004)

White Collar, High Skill

--

--

--

--

White Collar, Low Skill

-.001 (.002)

-.002 (.002)

-.004 (.003)

-.001 (.002)

Blue Collar, High Skill

.008 (.003)**

.004 (.003)

-.002 (.003)

.005 (.003)

Blue Collar, Low Skill

.004 (.003)

.000 (.003)

-.002 (.003)

.001 (.003)

Log Cumulative Entitlement

-.003 (.002)

.000 (.002)

-.003 (.003)

-.003 (.003)

Prior Earnings, Quarter 1 (in $000s)

.00006 (.00016)

.00023 (.00016)

.00021 (.00017)

.00025 (.00016)

Prior Earnings, Quarter 2 (in $000s)

-.00003 (.00011)

.00001 (.00010)

.00001 (.00011)

-.00006 (.00010)

Prior Earnings, Quarter 3 (in $000s)

.00001 (.00018)

-.00025 (.00017)

-.00015 (.00019)

.00003 (.00018)

Prior Earnings, Quarter 4 (in $000s)

-.00009 (.00013)

.00002 (.00013)

-.00009 (.00014)

-.00001 (.00013)

Treatment

No High School Diploma

Less than 25 Years

(continues on next page)

Page 63

(continued from previous page) Regular UI Weeks Allowed 12 weeks

--

--

--

--

13 weeks

.979 (.005)**

--

--

--

14 weeks

-.003 (.007)

--

--

--

15 weeks

-.002 (.005)

--

--

--

16 weeks

-.005 (.004)

.988 (.004)**

--

--

17 weeks

-.009 (.005)

.002 (.005)

--

--

18 weeks

-.006 (.005)

.010 (.005)

--

--

19 weeks

-.003 (.005)

.001 (.005)

.984 (.005)**

--

20 weeks

-.002 (.005)

.001 (.005)

.002 (.005)

--

21 weeks

.001 (.005)

.007 (.004)

.002 (.005)

--

22 weeks

.011 (.004)

.018 (.004)**

.008 (.005)

.989 (.005)**

23 weeks

-.006 (.004)

.011 (.004)**

.007 (.005)

.004 (.004)

24 weeks

.006 (.005)

.007 (.004)

-.001 (.005)

.006 (.005)

25 weeks

.006 (.004)

.001 (.004)

.005 (.005)

.011 (.004)*

26 weeks

--

--

--

--

.070 (.018)**

.025 (.019)

.043 (.023)

.044 (.025)

Observations

24,646

21,324

18,317

15,621

R-Squared

.6584

.7478

.7201

.7600

Constant

Note: Estimated parameters based on equation [3]. **, * = statistically significant at the 1 percent, 5 percent level.

Page 64