Bridging Towards Medicare

Transcription

1 Bridging Towards Medicare: Evidence from Massachusetts Hongming Wang Department of Economics, University of Southern California October 31, 2015 Abstract There is extensive evidence in the health and labor literature that workers in their early 60s have incentive to stay employed so that they retain affordable coverage from employers until eligible for Medicare at age 65. The 2006 reform in Massachusetts, widely regarded as the precursor of the subsequent national reform of ACA, unties insurance affordability from employment, and partly offsets the incentive to bridge towards Medicare. Basing identification on insurance discontinuity at age 65, I document large pull-back from labor force among subsidy eligible workers in age 60-64, for whom retirement propensity is higher the closer to Medicare, and social security onset is more likely at age 62. I argue in a social insurance model that welfare gain of premium subsidy is limited by the degree of moral hazard distortion, which in turn is exacerbated by public program crowding out private insurance. Both effects I estimate using simulated subsidy rate as instrument. I find subsidy induces larger reduction in participation among near-retirement workers and longer unemployment duration among entering workers, whereas crowd-out is mostly concentrated at younger ages. Welfare calculation suggests current subsidy rate is higher than the optimal, especially for older workers. Keywords: Massachusetts Health Care Reform; Health Insurance; Health; Retirement; Labor Supply; Social Security. Address: KAP 300, 3620 South Vermont Ave., Los Angeles, CA 90007, USA, [email protected]. 1

2 1 Introduction The Patient Protection and Affordable Care Act, signed into law by President Obama in March, 2010, is the most comprehensive national health care reform currently underway in the US. Central to the reform is the individual mandate that requires all legal residents to obtain eligible health insurance or face a tax penalty. The goal is to bring affordable coverage to the 50 million (2010, Census Bureau) uninsured Americans through a combination of policy instruments including Medicaid expansion, premium subsidy administered on the Exchanges, and regulation of the individual insurance market. The implication of the mandate is far-reaching. Most primarily, it reduces adverse selection and lowers the average coverage cost of enrollees. Using the precursor of ACA in Massachusetts in 2006, Hackmann et al.(2014) finds lower premium rate among unsubsidized individual plans in the first few years following the reform, and calculates a welfare improvement of 4.1% per person attributable to reduction in adverse selection. Less obvious is the general equilibrium consequences of the mandate on the labor market, and its implication for other social safety net programs such as Medicare and Social Security. Because most of the working age population is left out of the public insurance program and instead obtain coverage through employer group plans, economists have long been wary of the labor market implications of insurance availability. A large literature has documented the job-lock effect of employer plans (Madrian, 1994, Gruber & Madrian, 1994, 1997, 2004, Gilleskie & Lutz, 2002, and Dey & Flinn, 2005 for a theoretical motivation). This literature suggests there is high degree of self-selection into jobs of different insurance status, and those with insurance tied to their jobs are less likely to switch jobs. In the case of retirement, joblock is more appropriately termed as employment lock (Garthwaite et al., 2014), since transition is more likely to occur on the extensive margin rather than between jobs (Gruber & Madrian, 1995, Blau & Gilleskie, 2001, 2006, 2008). Gruber & Madrian (2004) gives an excellent survey on this topic. The incentive of retaining affordable source of insurance is also complicated by the type of coverage agent is entitled to. Coverage from a public source is probably more susceptible to moral hazard distortion than private coverage either from work or from spouse, especially among means-tested public programs. Utilizing state expansion in Medicaid, previous research generally finds reduced labor supply after public insurance expansion, although the magnitude seems to differ from experiment to experiment. Baicker et al.(2014) does not find economically significant effect on labor supply in the case of Oregon Medicaid expansion, whereas Dague et al.(2013) finds positive evidence of reduced labor supply among new Medicaid enrollees in Wisconsin Garthwaite et al.(2014) instead looks at Medicaid contraction in Tennessee that disenrolled childless adults from its Medicaid program in 2005, and finds swift substitution into employer group plans and increased labor supply among the disenrollees. Closely related is the question whether government in-kind transfers simply crowd out private transfers already in place in the economy. Cutler & Gruber(1996) pioneered and spawned an ever growing literature quantifying crowd-out in state insurance programs, with the findings critically assessed and updated in Gruber & Simon(2008). By and large, the crowd-out estimate seems to be robust at 0.5 across a wide variety of studies. Because the reduction in uninsurance tends to be lower than the increase in public coverage, the 2

3 presence of crowd-out limits the gain of public intervention, and may in fact worsen welfare if both crowd-out and labor supply disincentives are strong. Chetty & Saez(2010) shows theoretically how public transfer can exacerbate moral hazard in the private market and how omitting crowd-out can overstate the benefit of public expansions. Taking into account both effects, they argue that the current Medicaid program is very close to the optimal level. In light of the recent health care reform, the case of retirement combines elements from all three strands of literature. With rising health expenditures and uncertainty at older ages (Hartman et al., 2015), value of health insurance is higher among older workers, and the effect of job lock should be most salient among near-retirement workers. Medicare, on the other hand, creates sharp discontinuity in insurance coverage and large substitution into public coverage at age 65, with drastically different labor supply implications just below and above the threshold: whereas coverage is independent of employment status for the elderly, pre- Medicare workers have incentive to stay employed full-time to bridge towards Medicare. Finally, the reform smooths out the insurance discontinuity facing the old age group and as the previously insurance-constrained types substitute into publicly-subsidized plans and retire early, will likely generate large crowd-out of private insurance before Medicare, and eliminate the bunching in retirement at Medicare. The degree to which post reform transition into retirement is more likely to peak right before than after 65, more evenly spaced over the range 60-70, and more likely to occur at younger ages of 60-64, gives causal identification of insurance availability on retirement. This paper advances the previous literature in several ways. Unlike previous research on job lock, where identification often comes from selected subgroups such as workers enrolled in employer plans, covered by spousal insurance, or veterans, this paper utilizes a natural experiment that alters the insurance incentive for the entire population, and gives clear transition patterns into retirement at the population and subgroup levels that are not available in the previous literature. Moreover, I contribute to the understanding of one particular aspect of the reform, premium subsidy extended to the poor, and causally estimate the degree of crowd-out and moral hazard distortion traceable to the price variation induced by subsidy schemes. I also add to the literature on insurance demand by estimating the demand elasticity of premium subsidy. These estimates I argue are key to the welfare analysis of the social provision of insurance, and I quantify the welfare loss of one more dollar of premium subsidy at 0.12 dollar for the average population, and 0.30 dollar for nearretirement workers. Finally, to the best of my knowledge, this paper is also the first to note the policy complementarity between insurance reform and social security benefit claiming. Because most low income households may be dually eligible for both, a better understanding of how programs interact can inform policy design and budgeting. This paper share a similar topic as Heim & Lin(2014), but the content and motivation differ drastically. Heim & Lin(2014) focuses on the age group and estimates average treatment effect for this group in a standard before-after cross-state comparison. My paper centers around the hypothesis that agents might bridge towards Medicare and therefore more closely looks at transition behavior immediately before Medicare versus after. To do this I use much richer empirical strategies than simple differences, and extend the analysis to study welfare and crowd-out, elements that are absent in Heim & Lin(2014). With respect to the difference models employed in both papers, identification in Heim & Lin(2014) would require cross-state time trend for the given age group to be parallel, which I show below 3

4 is hardly satisfied in pre-reform years, let alone in post-reform years complicated by the recession. My identification instead stems from the differential behavioral patterns of the below age group (60-64) versus the above age group (65-69) within any state-year pair. In my main triple difference specification, this requires that recession does not differentially affect age groups after controlling for all two-way fixed effects, which is much weaker than what Heim & Lin(2014) needs to invoke in a single age group differences-in-differences setup. In terms of outcome, I find much larger increase in early retirement rate, 3.9% as opposed to 0.6% in Heim & Lin(2014). The magnitude differs hugely enough that they carry completely different policy weights, and suggests proper defense against confounds and other threats to identification can be crucial for studies using Massachusetts experience as crystal ball that prophets the national impact of ACA (Gruber, 2013). I begin with a difference-in-differences specification comparing within-state age group, applied to Massachusetts and all other Northeastern states. Estimates from the treatment state is potentially biased due to neglected regional shocks and common demographic shifters, and estimates from the control states constitute natural placebo tests for an erroneous treatment effect. I pay special attention to the complication of the recession: if the concurrent recession affects Massachusetts age group differentially, then the effect of the insurance reform cannot be identified in difference-in-differences. Using other Northeastern states as proxies, I present clear graphical evidence that below and above age groups exhibit identical trends over the period for my main outcome variables. More rigorously, I open a two year window around the onset of recession (December 2007, NBER) and apply the same differences-in-differences strategy to pooled control states. The result shows that conditional on state-year fixed effects, recession does not appear to affect retirement transition differentially across age groups. I then progress to the triple difference model that additionally compares the age group differential across treatment and control states. This extra layer of difference sweeps out any common regional shocks and changes in cohort-specific demographics, sources of biases in the within-state analysis. Inclusion of all two-way fixed effects accounts for differential trending that does not vary at the state-year-age-group level, and importantly absorbs any confounding effect by recession. The remaining variation in the triple interaction term is attributed to the insurance reform. I find strong disincentivizing effect on labor supply of the below group compared to the above group, and the effect is larger among low income households eligible for premium subsidy. The reduction in labor supply is mostly on the extensive margin, in particular direct transition into retirement from full-time work, with little evidence of reduced hours on the intensive margin. The main findings are robust to using only aggregated variables, different computations of clustered standard error, and a spatial discontinuity design where I compare age group differentials within paired contiguous border areas. Disaggregating by age, I show larger effects at policy cut-off ages of 62 (social security early retirement) and 65 (Medicare). To get at the treatment effect at precisely the cut-off, I extend the basic regression discontinuity design and nest it within a difference-in-differences setup. Essentially I compare the discrete change in retirement behavior at cut-off ages across states and over time. Similar to the triple difference design, the double difference takes care of both time-invariant and time-varying confounds that may contribute to retirement discontinuity at the cut-off, including, for instance, recession and cohort-specific variables such as formal retirement age. 4

5 I prove that coefficient before the triple interaction term in the modified design identifies the average treatment effect at the cut-off among the treated states. Applying the specification at early retirement and Medicare age, I show the insurance reform eliminates the bunching in retirement in the first year of Medicare, and sees larger decline in participation right before Medicare rather than after. At early retirement age, workers are more likely to quit working, reduce hours, and initiate old age benefit. In both cases the effect is overwhelmingly driven by the low income group eligible for premium subsidy. The overall age profile of retirement transition differs starkly by income. Effect on higher income workers is modest and peaks at early retirement age for most outcomes. For low income workers eligible for subsidy, however, effect on transition is emphatically larger, nearly monotone over age, and culminates right before Medicare at age 65. In other words, the necessity of bridging towards Medicare is especially relevant for the low income population for whom the employment lock binds more tightly the closer to Medicare. Interestingly, in contrast to their progressive retirement transition, social security onset among the lower income group bunches heavily at age 62. The policy message is that, while most low income workers do not quit working altogether at early retirement age, they do seem to start benefit the moment it becomes available. For future generations fully anticipating and internalizing the policy incentives, early retirement rate may well exhibit the same hump-shaped pattern for the low income group. As a robustness check, I apply the synthetic control approach proposed by Abadie & Gardeazabal(2003) to my setting. This method does not rely on the common trend assumption underlying differencing, but instead constructs a weighted average of control states that best mimics the treatment state in terms of pre-treatment outcomes and key characteristics. The method is equivalent to a differences-in-differences model with time varying fixed effects in the form of multiplicative factors (Abadie et al., 2010). Since my triple difference strategy allows for two-way fixed effects that similarly capture these time varying shocks, the result from the two approaches are comparable. One additional insight is the machine selected set of covariates that best predicts pre-treatment outcome. It is reassuring to find measure of job lock, next to macroeconomic variables, receives high weight in predicting age group differentials in retirement rate. Welfare analysis of the Massachusetts reform benefits from the readiness of post reform data. Previous work includes Hackmann et al.(2014), who focuses on the efficiency gain of mandate in minimizing adverse selection, and Kolstad & Kowalski(2012), who argues employer mandate reduces welfare loss relative to an alternative insurance program funded completely by tax. The second point partially justifies the long tradition of employmentbased insurance system in the US, and the deviation from that paradigm towards a more tax-based, publicly financed insurance system raises natural question as to the labor market repercussions of the reform and the associated welfare loss. However, few paper has directly linked the two together in the insurance context, and hence it remains unknown to what extent is the reduction in labor supply induced by the public provision of insurance, and how does welfare correspond with different level of subsidies. Such knowledge is valuable not only because premium assistance is what practically makes insurance affordable to the otherwise uninsured, but also because it is a policy instrument directly controllable by the policy maker. To get at these questions, I turn to post-reform Massachusetts for an empirical characterization of the mandate economy in practice. 5

6 I build up a social insurance model (Baily, 1978, Chetty, 2006b, 2009) that incorporates key institutional elements of the reform: individual mandate and premium subsidy on the Exchange applied to those not offered employer sponsored insurance. Subsidy is funded by lump-sum tax on the working, creating moral hazard disincentive on labor supply. Higher subsidy rate lowers participation and crowds out private insurance, worsening the moral hazard distortion (Chetty & Saez, 2010). Optimal subsidy rate would balance the consumption smoothing gain of social transfer with the compounded moral hazard inefficiency arising from reduced labor supply and crowd-out. Corresponding sufficient statistics are those quantifying the rate of crowd-out and the subsidy elasticity of labor supply, which I estimate empirically from post reform Massachusetts. An alternative approach to quantify these mechanism would be a dynamic job search models where workers match with firms offering different bundles of wage and insurance, as in Aizawa & Fang(2015) and Aizawa(2015). The advantage of the approach is greater flexibility in counterfactuals and a more general equilibrium scope, whereas the limitation in this particular application is the lack of empirical support for some of their findings, as ex post data are not yet available. In particular, simulation from Aizawa(2015) suggests older workers tend to sort into lower productivity jobs and obtain insurance from the public source, and to prevent the loss in productivity, optimal subsidy rate should be substantially declining in age. As the two reforms bear major similarity, the reduced form estimates in Massachusetts can be thought of as empirical counterparts to the mechanism suggested in Aizawa(2015). Estimating these statistics can be challenging because observed subsidy is endogenous. To isolate exogenous variation of subsidy schedule, I follow Currie & Gruber(1996) and simulate subsidy from a reference national sample. To increase the variation of the instrumental variable, I follow Mahoney(2015) and simulate subsidy for a total of 1008 demographic cells from the national sample. It turns out that crowd-out in Massachusetts is modest: one percentage point increase in subsidy rate induces the marginal enrollee to drop private insurance by an extra 0.36 percentage point, lower than the range found in previous estimates. Most of the crowd-out occurs among the younger workers, and appears to be result of endogenous job sorting as employer offer rate remains high during this period. This stands in sharp contrast to the proposition in Aizawa(2015), where crowd-out is more likely among the older workers. In terms of labor supply, I find consistent evidence across different measures that older workers are most likely to exit labor market at higher subsidy rates, and the effect is not to be confounded with longer unemployment duration or job search frictions that seem to disproportionately affect entering workers. The combined evidence seems to suggest that in near retirement age, insurance subsidy induces workers to leave the labor market altogether rather than sort into differential jobs and insurance types, and the welfare loss of the reform is probably more substantial than the reduction in productivity due to sub-optimal matching. The paper is organized as follows. Section II introduces the Massachusetts reform and its relation to ACA. Section III describes the data. Section IV contains main results from a variety of empirical strategies and robustness checks. Section V formulates a welfare model and estimates sufficient statistics. Section VI concludes. 6

7 2 Massachusetts Health Care Reform The Massachusetts comprehensive health reform is signed into law by the then-governor Mitt Romney in As evident in Figure 1, Massachusetts has higher pre-reform insurance rate than the nation s average, and quickly achieves near universal coverage within a few years of the reform. Central to the law is the individual mandate requiring all Massachusetts residents over age 17 to acquire affordable health insurance that meets a set of minimum creditable coverage standards. Failure to obtain coverage will result in a tax penalty, unless the individual is able to demonstrate unaffordability (for instance, below 150% of FPL) or religious exemption. Figure 1: Non-Elderly Insurance Rate, MA USA Northeastern states except MA Note: I derive aggregate insurance coverage rate from CPS using the insurance sample weight. Census Bureau defines the Northeastern region as including the states of Connecticut, Maine, Massachusetts, New Hampshire, New Jersey, New York, Pennsylvania, Rhode Island, and Vermont. Following a 1950 proposal, I also include Delaware, Maryland and Washington, D.C. throughout the analysis. The law builds upon a sequence of pre-2006 regulations of the state insurance market. Massachusetts merged its small-group and non-group plans into a single risk pool, mandated community rating and guaranteed issue, and formulated a set of coverage and benefit criteria that became the basis of minimum creditable coverage standards in 2006 and the minimal essential coverage standards under ACA. Plans are categorized into bronze, silver and gold tiers according to actuarial values, and similar classification is adopted in ACA. The readiness of a relatively good infrastructure ex-ante is believed to have fostered the quick penetration of the reform and its immediate impact on insurance take-up. To encourage enrollment among the low income population, the reform expands the Massachusetts Medicaid program (MassHealth) and institutes a publicly-subsidized Exchange 7

8 market known as the Commonwealth Health Insurance Connector. The new MassHealth covers children with family income no greater than 300% of FPL, up from the previous 200% cap. Low income population ineligible for Medicaid (for example, non-elderly, non-disabled, childless adults with income above 133% FPL) can obtain coverage from the Connector, a state clearing house bringing together consumers and state-certified individual plans. The Connector has a subsidized Commonwealth Care program and an unsubsidized Commonwealth Choice program. Commonwealth Care is open to eligible individuals whose family income is no greater than 300% of FPL and who are not offered health insurance from their employers. Those not eligible for subsidy can buy from the Commonwealth Choice program. Affordability and premium subsidy schedules are released in the middle of the previous year. In determining the tax penalty, the Connector sets the maximum monthly premium a person in a given income bracket needs to pay towards her coverage, or the affordability. The amount is zero for individuals with family income below 150% FPL. In 2010, for example, out-of-pocket premium cap for an individual plan is $ 39 per month for the % bracket, $ 77 per month for the % bracket, and $ 119 for the % bracket. Individuals are not held accountable for failing to enroll in plans with premium contribution exceeding their affordability threshold. Subsidy schedule works closely with affordability to ensure most of the low-income population are eligible for a subsidized Commonwealth Care plan. Applying subsidy, enrollee contribution falls to 0 for those below 150% FPL, roughly 10% for the % bracket, 20% for % and 30% for %. Alongside the individual mandate, Massachusetts also implements an employer mandate which requires employers with more than 11 full-time equivalent workers make fair and reasonable contribution towards the premium cost of full-time employees, or pay a fine of up to $ 295 per worker. Employers must also provide its employees a section 125 plan that allows premium payment on a pre-tax basis. Failing to do so will incur a free rider surcharge. Additionally, employers have Health Insurance Responsibility Disclosure (HIRD) obligation, and must collect signed HIRD forms from employees who refuse to enroll in employer-sponsored plans. These measures are meant to maintain the central role of employers in insuring workers and their families, and to minimize the crowd-out from private insurance. Due to concerns over administrative costs to firms, and in anticipation of the federal employer mandate phasing in, Massachusetts repealed its employer provisions effective Jul. 1st, Figure 2 depicts trend of employer-sponsored health insurance (ESHI) in Massachusetts. ESHI measures for are from May 2011 edition of Key Indicators, a quarterly report on the Massachusetts health care industry, and data for 2011 are CHIA 1 calculation from Massachusetts Health Insurance Survey. Disaggregation by firm size is derived from CPS by the author. All numbers exclude Medicare enrollees. Since 2007, the year when Massachusetts reaches near universal coverage, the proportion of ESHI among all insurance types has been declining over subsequent years, with nearly a one-to-one increase in the fraction covered from a public source (not shown). Comparing the trend with state employment 1 CHIA, Center for Health Information and Analysis, is an independent agency in Massachusetts that collects information on the performance of the state healthcare system. It administers and analyzes surveys tailored to answer specific questions of the reform. For example, insurance rate estimated from the Massachusetts Health Insurance Survey is around 97%-98%, 2-3 percentage point higher than census estimates. Data from the Employer Health Insurance Survey suggests employer offer rate is stable since the reform at about 70%. 8

9 Figure 2: ESHI Coverage Among Insured Massachusetts Residents, Excluding Medicare ESHI ESHI, firm size 50+ ESHI, firm size<50 Employment Rate Source: ESHI data for are from May, 2010 Key Indicators; for 2011 it is from CHIA. ESHI by firm size is author calculated from CPS. Employment rate is 100% minus unemployment rate, obtained from BLS. rate over the same period, it appears that ESHI percentage drops further despite improving economic conditions in recent years, especially among small businesses with fewer than 50 employees 2. At the same time, there is no evidence that employers are dropping insurance offers as CHIA estimates a relatively stable employer offer rate during this period. Therefore, at least part of the decrease in aggregate private insurance is potentially attributable to workers sorting into public insurance, possibly through matching with jobs not mandated to offer employee coverage, and the sorting is not completely an expediency in the time of recession. This motivates a closer look at the extent of crowd-out in Massachusetts, an issue I analyze further in Section V. Compared to Commonwealth Care, the ACA Exchange market covers families with income up to 400% FPL, up from 300% in Massachusetts, but average cost sharing among the subsidized is also higher. Qualified plans must meet a set of minimal essential coverage criteria, and are subject to similar regulations such as fair pricing based on single risk pool and guaranteed issue already in place in Massachusetts. ACA raises Medicaid income limit to 133% FPL, and encourages states to expand the program further. Starting 2016, the ACA employer mandate requires businesses with more than 50 full-time equivalent employees to cover at least 95% of full-time workers and their dependents below age 26, or pay a fine. Due to the obvious similarities between the two reforms, understanding the incentives and disincentives of the Massachusetts reform, as well as the behavior and motivations driving its 2 In all other Northeastern states, the decline in ESHI coverage rate among small businesses over this period is less than 8%, from 84.17% in 2006 to 76.80% in

10 outcomes, contributes important insight to the prescience of ACA and the normative design of optimal policy. 3 Data My primary data are the annual releases of American Community Survey (ACS), ACS is the most comprehensive census data currently collected in the US. The newest 2013 release samples over 3.5 million addresses, and all annual releases are representative at the state level, and at sub-state level for geographical areas with a minimum population of 65,000. Response to ACS is mandatory by law, giving ACS the lowest non-response rate (around 3%) among commonly used census data such as CPS and SIPP. Since my identification depends critically on within-state variation between narrowly defined age bands, and in some cases sub-state geographical areas, ACS is most suited for my purpose. However, in the appendix I show the same result holds using either March CPS over the same study period, or individual panels in SIPP despite significantly smaller sample size. ACS interviews are conducted continuously throughout the year. Respondents answer questions regarding labor supply status, income, and demographics. Starting 2008, ACS also asks insurance coverage and type. Age in ACS is rounded down to the nearest integer. Labor supply over the past 12 months and last week is recorded. If a person reports having worked in the past 12 months, I assign participation to this person at the prior age. Nonparticipation at a given age means that the person started sometime in that age a spell of non-employment that lasted at least 12 months. This is roughly in line with the notion that she retired in that age, so long as average unemployment duration is less than 12 months over the study period 3. Full-time work is also retrospectively defined at the prior age for jobs requiring more than 35 hours per week. Alternatively, I define current participation status if the person reports active on the labor market last week. Results are similar using the two measures for near-retirement workers. Following previous literature, I define transition into retirement as having worked in the past 12 months but not in labor force last week. Retirement from full-time work is similarly defined. I focus on civilian labor force over the years , excluding those working in the military. I also exclude group quarter individuals because they do not enter ACS until I proxy premium eligibility using reported family income from last year, which I transform into FPL percentages using information on family size and yearly poverty guidelines published by the Department of Health and Human Services. For subsidy, I rely on information contained in yearly HC Schedule Worksheets that help Massachusetts residents determine affordability and penalty when filing tax returns. The worksheets tabulate affordability thresholds by income brackets for that year, and give the premium of the cheapest individual plan by five year age bands available in a given region of residence. A region is a collection of counties with similar premium rates. Subsidy as a percentage is defined as one minus the ratio of affordability limit over the lowest cost premium for a given age-income-region cell as laid out in the worksheets. I map public use micro area (PUMA), the smallest geographical 3 According to BLS, average unemployment duration in Massachusetts 2009 is 23.9 weeks, and the median is 14.4 weeks 4 Group quarter residents constitute less than 1.5% of the age group in Massachusetts 10

11 area identifiable in ACS, to regions. For PUMAs straddling more than one region, I weight subsidy rate by the relative population size in each region. By definition, subsidy is 0 for individuals with family income over 300% FPL, and 1 for those below 150%. Table 1 compares baseline characteristics of the age group in Massachusetts and other Northeastern states, pooled over pre-reform years. Insurance variables are aggregated from March CPS using health insurance weights over the entire non-elderly population. All other variables are aggregated from ACS for the age group, further stratified into five year age bands if noted. Compared to other Northeastern states, Massachusetts has an old age population that is better educated, with higher income, healthier, and more likely to remain active in the labor force. Baseline insurance rate is higher in Massachusetts, with more insured obtaining coverage from a private source. Retirement rate is lower in Massachusetts, and fewer people are drawing social security retirement compared to other Northeastern states. These pre-existing discrepancies tend to lower the external validity of the results. For internal validity, identification of the difference-in-differences model relies on parallel trends, and difference in baseline characteristics does not in and of itself invalidate the approach. Nevertheless, I correct for baseline imbalance using Abadie weights, and find similar results. 4 Empirical Strategies and Findings This section presents the main estimation methods and results. In section 4.1, I first present graphical evidence from the aggregated data documenting differential transition patterns between the below age group (60-64) and above (65-69), for both the treatment state and control states. I show how comparing neighboring age groups around Medicare better isolates the effect of health insurance and better fends off the potential confound of recession. Section 4.2 presents triple difference estimates, and various robustness checks including a spatial discontinuity design. Section 4.3 proposes a double differenced regression discontinuity design to quantify the local policy impact at Medicare and early retirement age. I complete the characterization of retirement transition in each integer age between 60 and 65, and discuss implications for subgroups stratified by subsidy eligibility. I also note the program complementarity with social security old age. Section 4.4 finds additional support for the motivation and estimates in the main regression using the synthetic cohort method. 4.1 Differences-in-Differences I start with a within-state analysis that compares neighboring age groups differentially affected by the reform. With near universal coverage by Medicare beyond age 65, the joblock matters less for the elderly workers who are arguably less affected by the reform. I hence open a five year band at Medicare age: individuals aged when sampled belong to the below group, and those aged are in the above group. Differential retirement patterns across groups before and after the reform suggest the role of health insurance in retirement transitions at the population level. Note that the comparison does not require the reform to have nil effect on the above age group at all. There are a few reasons to believe that the above group might also be affected. 11

12 Table 1: Baseline Characteristics, Years Old, Massachusetts Other Northeastern States High School *** Some College *** Male Married * Child Present Family Size White *** Black *** Hispanic *** Any Insurance *** Private Insurance *** Difficulty Limiting Work * *** % FPL ** % FPL *** *** Social Security Retirement *** *** In Labor Force *** *** Work Last Year *** *** Full-Timer Last Year *** Part-Timer Last Year *** *** Hours Worked * Retirement from Full Time Work ** Part Time Work * ** Any Work ** Demographic variables and labor market variables are aggregated from ACS over for the age group unless otherwise noted; sampling weights are applied. Insurance variables are aggregated from CPS over the entire non-elderly population, adjusted by insurance sampling weights. Asterisks next to Massachusetts summary statistics indicate significance of difference from corresponding measures from Northeastern states. *** 0.01 ** 0.05 *

13 For instance, for the working head to provide insurance for the entire family, one may have incentive to retain employer sponsored insurance even after Medicare age. Subsidy on the public plan tends to counteract such necessity, and indeed I find evidence that non-working individuals are much more likely to drop private insurance, presumably from spouses, than working individuals. Since part of the control group is also treated, it tends to bias the estimate downward. Alternatively, if insurance coverage leads to more health care utilization which ultimately brings about better health, the reform may induce higher participation rate among the above group. In that case, the estimate can be biased upward. Figure 3 plots the time trend of aggregate labor outcomes of the two age groups, separately for the treatment state and the collection of control states. The vertical line indicates the first observation of the post-treatment period. I look at both the retrospective and the point-in-time measure of participation. There is rising labor force participation among older workers in this period, but the increase for Massachusetts below group in post-reform years is either slower or stays flat relative to the above group. The difference is most striking for retirement from full-time work, with the age group gap nearly vanishing in a post-reform period overlapping with recession. Retirement from part-time work clearly fails the parallel trend condition in the first few years of the survey, and overall retirement seems mostly driven by transition from full-time work. I hence focus primarily on full-time retirement rate for transition outcomes. Importantly, group differentials in the control states are remarkably stable for the main outcomes over the study period: neither the onset of the insurance reform nor the recession seems to break the parallelism of the trends. This is expected as workers in the two age groups tend to have similar human capital but differ in health stock. The latter may explain the difference in average participation rate, but similarity in the former implies common trending in face of any economy-wide productivity shocks. Loosely treating pooled Northeastern states as the counterfactual for Massachusetts, Figure 3 lends graphical support to the identifying assumption of difference-in-differences. I estimate the following difference-in-differences model in the treatment state: y it = β 0 below post + β 1 below + β 2 post + ϵ it, where below is an indicator variable that takes value 1 if age is between 60-64, and post takes value 1 if year is 2007 or after. I take out transition year 2006 from my sample 5. β 1 captures the rising labor force participation for older workers in this period, and β 2 shows age group differential in participation, or the transition effect. β 0 gives the differential transition effect before and after the reform, or the treatment effect the insurance reform. Because I do not utilize cross-state variation in the difference-in-differences model, I cluster standard error by year. In light of the small number of years covered, I block bootstrap as in Duflo et al.(2004). Panel A of Table 2 shows the results. Retrospective participation drops by 2.9 percentage points after the reform among below age group, and full-time retirement rate increases by 3.6 percentage points, a 40% increase from a baseline of 8.8%. Decrease in current participation status and past full-time work is smaller in magnitude and insignificant. Panel B reports 5 Absorbing 2006 into the pre-reform period does not significantly alter my point estimates. 13

14 Figure 3: Age Group Differentials, Massachusetts and Northeastern Controls Participation (Retrospective), Massachusetts Participation (Retrospective), Other NE States Below, Above, Below, Above, Participation (Current), Massachusetts Participation (Current), Other NE States Below, Above, Below, Above, Full Time Work, Massachusetts Full Time Work, Other NE States Below, Above, Below, Above, Ret. from Full Time Work, Massachusetts Ret. from Full Time Work, Other NE States Below, Above, Below, Above, Ret. from Part Time Work, Massachusetts Ret. from Part Time Work, Other NE States Below, Above, Below, Above, Ret. from Any Work, Massachusetts Ret. from Any Work, Other NE States Below, Above, Below, Above, 65 69

15 estimates from a richer specification y it = β 0 below post + α a + α t + γ X it + ϵ it, where α a and α t are age and year fixed effects, respectively. Covariates in X it includes basic demographics such as gender, race, education, marital status and presence of own child under age 21. To account for any cohort specifics that may differentially affect the age groups over time, and most notably, normal retirement age (NRA), I include dummy variable of formal retirement age being 66 versus 65 for individuals in my sample 6 For outcomes conditional on past year participation, such as hours worked and transition, I also control for industry and occupation fixed effects. I additionally include family income as percentage of FPL and log personal income in transition specifications. I run the same regression over different Northeastern states, and present results for each state in Panel B. Including individual covariates produces larger estimates for participation and full-time retirement, both significant at 5%. To the extent that industries have different retirement age as a norm, and occupation sorting may be correlated with the worker s ability of securing insurance outside of job-lock, controlling for industry and occupation fixed effects tend to alleviate the biases from omitted variables and selection. Compared with placebo experiments in control Northeastern states, the effect on both measures of participation and full-time retirement is strongest in Massachusetts. In the pooled regression in Panel B, I essentially test for the parallel trend assumption in the absence of insurance reform, using other Northeastern states as proxies for Massachusetts. I control for state and state-year fixed effects in the pooled sample. For the main outcomes in the first five columns, most deviation from the common trend appears to be small and economically insignificant, except for point-in-time participation showing a 1.3 percentage point increase over the same period. To investigate if such increase is reflecting any differential impact of recession by age group, I open a two-year window around the onset of recession (December 2007, NBER), and compare age groups before ( ) and during ( ) the recession. Due to the extremely small number of years (4), I cluster standard error by household. Results in Panel C show negligible impact of recession on my main outcomes, including point-in-time participation. This suggests the slight deviation from common trend in control states is more likely due to unaccounted cohort differences than recession, and sweeping out such difference in the triple difference model will only strengthen the results. This careful defense against potential confounds in not possible in an alternative difference-in-differences model where only the below group is compared across state and time (Heim & Lin, 2014). Figure 3 shows that the pre-treatment trend for most outcomes of either age group differs perceptibly across states, invalidating the common trend assumption. Estimated effect is then a mixture of true insurance effect and any other factor varying by state and year, including heterogeneous local labor market shocks that tend to dominate the insurance effect in such models. This might explain why the increase in retirement rate is much smaller (0.6%) in Heim & Lin(2014), 6 I define two cohorts for my sample: the first cohort, born in , has NRA at 65, and the later cohort, , has NRA roughly at 66. Controlling for finer cohorts gives similar results, but introduces higher degree of multicollinearity with the full set of year and age fixed effects already in the model. Unaccounted cohort specifics may bias the difference-in-differences estimates, but will be differenced out across states in the triple difference model. 15

16 Table 2: Differences-in-Differences, Massachusetts (1) (2) (3) (4) (5) (6) (7) Participation Participation Ret. From Ret. From Ret. From (Retro.) (Current) Full Time Log Hours Full-Time Part-Time Any Work Panel A: Massachusetts below post ** * (0.0142) (0.0172) (0.0151) (0.0475) (0.0184) (0.0297) (0.0181) below *** *** *** *** *** *** (0.0113) (0.0154) (0.0126) (0.0379) (0.0171) (0.0266) (0.0171) post *** *** *** *** *** (0.0140) (0.0173) (0.0113) (0.0430) (0.0193) (0.0208) (0.0150) R N Panel B: Northeastern States Massachusetts ** ** (0.0162) (0.0185) (0.0173) (0.0504) (0.0210) (0.0328) (0.0222) Connecticut (0.0196) (0.0213) (0.0197) (0.0747) (0.0295) (0.0547) (0.0226) Delaware (0.0253) (0.0240) (0.0248) (0.1017) (0.0477) (0.0590) (0.0369) D.C (0.0369) (0.0423) (0.0351) (0.1291) (0.0463) (0.0999) (0.0489) Maine * (0.0265) (0.0302) (0.0228) (0.1041) (0.0446) (0.0622) (0.0397) Maryland (0.0152) (0.0187) (0.0137) (0.0519) (0.0314) (0.0330) (0.0236) New Hampshire (0.0255) (0.0300) (0.0282) (0.0861) (0.0318) (0.0507) (0.0292) New Jersey (0.0130) (0.0193) (0.0123) (0.0177) (0.0230) (0.0340) (0.0177) New York (0.0097) (0.0136) (0.0086) (0.0343) (0.0178) (0.0351) (0.0168) Pennsylvania (0.0134) (0.0121) (0.0087) (0.0349) (0.0157) (0.0237) (0.0146) Rhode Island (0.0312) (0.0255) (0.0284) (0.0925) (0.0450) (0.0668) (0.0313) Vermont ** (0.0357) (0.0481) (0.0291) (0.1218) (0.0441) (0.0795) (0.0420) Pooled Control States ** ** ** *** (0.0063) (0.0064) (0.0044) (0.0154) (0.0084) (0.0123) (0.0060) Panel C: Recession below post * * ** (0.0053) (0.0053) (0.0047) (0.0168) (0.0062) (0.0101) (0.0053) Specifications for log hours worked and retirement transition are estimated from respective conditional samples of past year participants, full-time workers, part-time workers, etc. Panel A estimates treatment effects on Massachusetts below age group with no individual controls. Panel B shows estimated coefficient before the interactive term in a specification with year and age fixed effects as well as individual controls, for each single Northeastern state and pooled control states. In the latter case I also include state and state-year fixed effects. Individual controls include gender, race, education and family composition for all outcomes. For conditional outcomes, industry and occupation fixed effects are included. For transition outcomes, family income as percentage of FPL and log personal income are included. Panel C compares age group differential before ( ) and after ( ) the onset of recession. The regression pools over Northeastern control states and controls for age, year, state, and state-year fixed effects, in addition to the same set of individual controls as in Panel B. All regressions are weighted by ACS sampling weights. Standard errors in parentheses in Panel A and B are clustered by year, block bootstrapped from 500 repetitions; in Panel C clustered by households. *** 0.01 ** 0.5 *

17 whereas models based on insurance discontinuity at Medicare show an effect as high as 4.5%. 4.2 Triple Difference Further comparing age group differentials across states leads to the triple difference model. Inclusion of state-year fixed effects should address the confound introduced by the recession, as suggested by pooled regression over Northeastern control states. Year-age fixed effects flexibly capture any cohort-year differences that may bias the difference-in-differences estimates. State-age fixed effects in addition control for state-specific retirement age gradients correlated with factors extraneous to insurance availability. The remaining source of variation in the triple interaction term is the differential retirement behavior between age groups that persist even after controlling for all two-way fixed effects, or in this case, due to the Massachusetts health insurance reform in The main triple difference specification takes the form y ist = β 0 below post treat + α a + α s + α t + α st + α at + α as + γ X ist + ϵ ist, where treat is indicator of Massachusetts. I include a fully disaggregated set of state, year, and age fixed effects and their two-way interactions. Covariates in X ist are the same as in the case of double difference. Standard errors are clustered by states to allow for general serial correlation patterns, and block bootstrapped due to small number of cluster units (12). Table 3 show both triple difference estimates and previous difference-in-differences estimates. Correcting for the background increase in point-in-time participation, triple difference finds similar decline in both measures of participation by 3 percentage points, of which 2.2 percentage points is decrease in full-time work, significant at 5%. There is no evidence of reduced hours among workers, and the effect occurs mostly along the extensive margin where full-time workers transit directly into retirement, and the rate of transition increases by 4 percentage points. Lower personal earning is associated with earlier exit from the labor force, and lower education is associated with lower participation rate. Absence of co-residing young children is also a strong predictor of early retirement. Retirement from part-time work does not appear to be affected once compared against control states, and retirement from any work seems mainly driven by retirement from full-time work. However, since the common trend assumption in the last two outcomes is less tenable, triple difference estimates might still be biased, and I hereafter exclude them from the analysis. In Table 4 I show a similar triple difference model using only aggregate retirement rates. In the upper panel, I aggregate state-year-group level participation rate, full-time rate, log hours and full-time retirement rate, and regress the outcomes on triple interaction and all two-way interactions. To tease out the effect of differential labor market condition facing age groups, I control for unemployment rate at the state-year-group level obtained from BLS. I experiment with different methods to cluster standard errors. The square bracket contains 90% confidence interval from a randomization inference procedure by Conley & Taber(2011). They note that difference-in-differences estimates with only a few treated units are asymptotically biased, and the distribution of the bias term can be recovered from the residuals of placebo experiments in control states assuming random program placement. I permute the policy intervention in 11 Northeastern control states, and derive the 90% 17

18 Table 3: Triple Difference Estimates of Insurance Reform on Retirement (1) (2) (3) (4) (5) (6) (7) Participation Participation Ret. From Ret. From Ret. From (Retro.) (Current) Full Time Log Hours Full-Time Part-Time Any Work Difference-in-Differences below post ** ** (0.0162) (0.0185) (0.0173) (0.0504) (0.0210) (0.0328) (0.0222) R N Triple Difference treat below post *** *** ** *** (0.0101) (0.0108) (0.0096) (0.0291) (0.0138) (0.0196) (0.0113) Male *** *** *** *** ** * (0.0043) (0.0040) (0.0049) (0.0087) (0.0025) (0.0061) (0.0027) Race:Black ** *** (0.0143) (0.0157) (0.0174) (0.0335) (0.0054) (0.0087) (0.0066) Race: Other *** ** * *** * ** *** (0.0071) (0.0079) (0.0065) (0.0156) (0.0044) (0.0093) (0.0043) Hispanic Origin ** *** ** *** *** (0.0134) (0.0148) (0.0109) (0.0190) (0.0078) (0.0126) (0.0059) High School *** *** *** ** (0.0042) (0.0044) (0.0037) (0.0138) (0.0039) (0.0080) (0.0038) Some College *** *** *** *** ** *** * (0.0063) (0.0071) (0.0061) (0.0162) (0.0044) (0.0099) (0.0052) Married * *** *** *** *** *** (0.0030) (0.0030) (0.0027) (0.0086) (0.0020) (0.0040) (0.0021) Child Present *** *** *** *** *** * *** (0.0070) (0.0053) (0.0059) (0.0121) (0.0035) (0.0120) (0.0034) Percentage FPL (0.0002) (0.0006) (0.0003) Log Personal Income *** *** *** (0.0021) (0.0047) (0.0026) R N Difference-in-differences estimates are the same as in Panel B, Table 2; triple difference estimates are from a specification with fully disaggregated state, year, age fixed effects and two-way fixed effects. All regressions are weighted by ACS sampling weights. Standard errors are clustered by state, block bootstrapped from 500 repetitions. Transition variables additionally include industry and occupation fixed effects, not shown in the table. *** 0.01 ** 0.05 *

19 confidence interval containing the range of true policy effect that cannot be rejected at size 10%. The curly bracket shows the 95% confidence interval from 500 repetitions of wild bootstrap as in Cameron et al.(2008). Similar to Duflo et al.(2004), wild bootstrap works well for small number of clusters. Both Conley-Taber and the wild bootstrap intervals show significant effect of the reform on aggregate outcomes. Estimated treatment effect is very similar with or without controlling for unemployment rate, and when included, coefficient before unemployment rate is statistically indistinguishable from zero. Table 4: Triple Difference Estimates of Insurance Reform on Retirement, Aggregated Variables (1) (2) (3) (4) Participation Participation Ret. From (Retro.) (Current) Full Time Full-Time Aggregated by State: treat below post [-.0476,-.0153] [-.0415,-.0109] [-.0659,-.0020] [.0199,.0775] {-.0420,-.0229} {-.0390,-.0193} {-.0433,-.0144} {.0319,.0595} unemployment rate {-.0022,.0020} {-.0046,.0026} {-.0063,-.0001} {-.0063,.0075} N R Aggregated by PUMA: treat below post [-.0681,.0049] [-.0556,.0027] [-.0681,.0049] [.0329,.0866] {-.0297,-.0074} {-.0348,-.0181} {-.0295,-.0096} {.0403,.0585} unemployment rate {-.0059,.0009} {-.0028,.0023} {-.0033,.0016} {-.0034,.0029} R N Upper panel shows triple difference estimates using aggregated variables at the state-year-group level. Lower panel shows triple difference estimates where outcomes are aggregated by PUMA-year-group and the regression includes PUMA fixed effects and uses only observations in year Unemployment rate is obtained from BLS at the state-year-group level. Standard errors are clustered by states. The square bracket contains 90% confidence interval from the Conley-Taber randomization procedure. The curly bracket contains 95% confidence interval from 500 repetitions of wild bootstrap. *** 0.01 ** 0.05 * 0.10 One unique advantage of ACS over other census data is its rich geographical information at the sub-state level. This allows me to aggregate labor market outcomes over public use micro area (PUMA), the smallest geographical unit identifiable in ACS. The Census Bureau revises PUMA demarcation following each decennial census. To retain consistent PUMA coding linkable over year, I restrict my sample to year A total of 52 PUMAs are superimposed on 14 counties in Massachusetts over this period, with population in each PUMA ranging from 100,000 to 200,000. PUMAs do not cross state borders, lending natural definition to treated and control units. The lower panel of Table 3 reports estimates from 19

20 the model y pt = β 0 treat below post+β 1 treat below+β 2 below after+β 3 below+γ UE st +α p +α t +α st +ϵ pt, where α p is PUMA fixed effects, and α s and α st are state and state-year fixed effects. I drop the interaction treat post having controlled α st. Accounting for smaller area variations, estimated treatment effect of retrospective outcomes (participation and full-time work) is smaller in magnitude, and Conley-Taber intervals extend to the positive domain for participation outcomes, although not by much. Inference by wild bootstrap still suggests significant policy impact on all outcomes, and insignificance of unemployment rate in each case. Overall, the tests seem to indicate that identification by age group differentials is fairly robust to unobserved labor market heterogeneity, and the magnitude does not appear sensitive to the unit of analysis or the particular study period chosen. Table 5: Triple Difference Estimates of Insurance Reform on Retirement, Spatial Discontinuity (1) (2) (3) (4) Participation Participation Ret. From (Retro.) (Current) Full Time Full-Time Border Segment: treat below post {-.0843,-.0072} {-.0693,-.0164} {-.1060,-.0548} {.0013,.0624} N R Contiguous PUMA Pairs: treat below post {-.1125,-.0306} {-.0773,-.0267} {-.1082,-.0526} {-.0457,.0275} R N Upper panel restricts to PUMA-level triple difference to 31 border PUMAs. Lower panel shows estimates using with PUMA-pair variation from a total of 30 contiguous PUMA pairs that straddle Massachusetts border. Standard errors are clustered by state in the upper panel; in the lower panel they are clustered by state and PUMA. In both cases I wild bootstrap from 500 repetitions and show 95% confidence intervals in the curly bracket. *** 0.01 ** 0.05 * 0.10 Upper panel in Table 5 estimates the same regression but restricted only to the border segment comprised of 31 PUMAs from Massachusetts and 5 neighboring states 7. If border area has more homogeneous labor market conditions, estimated effect is closer to the true effect of insurance reform on retirement transition. On the other hand, if there is significant degree of spatial heterogeneity within state and locational sorting by either firms or households, the effect by the border may lack external validity if interest is on average treatment effect in the population. It turns out there is larger decrease in participation along the border, but smaller increase in retirement transition. Most noticeably, the decline in full-time work is significant at 7.6 percentage point, nearly three times larger than the state-level estimates. The lower panel further groups PUMAs into contiguous pairs straddling Massachusetts borders. If a Massachusetts PUMA is contiguous with multiple PUMAs 7 New Hampshire and Vermont borders Massachusetts from the north, New York to the west, Connecticut and Rhode Island to the south. 20

21 from control states, then it enters multiple pairs. This way I construct 30 pairs, and include pair fixed effects and pair-year fixed effects (Dube et al., 2010). Essentially I compare the age group differential within each pair-year combination, which constitutes the most trusted defense against unobserved local market shocks. Because multiple entry by a single PUMA into pairs generates correlation across pairs, and because the policy varies by state, I cluster by both PUMA and state using a two-way clustering procedure by Cameron et al.(2011). I bootstrap the state dimension considering the small number of states (6). 95% confidence intervals from 500 repetitions of wild bootstrap are in the curly brackets. Strikingly, decline in retrospective participation and full-time work is over 7 percentage point, whereas the transition increment is minimal and insignificant. Although the spatial discontinuity re-affirms the importance of health insurance on labor supply, the discrepancy from average treatment effect suggests substantial heterogeneity within the treatment state. Omission of the Boston metropolitan area from the border sample, despite being the most populous and economically vibrant area in Massachusetts, tends to suggest these differences are meaningful. From a policy perspective, the average effect over state residents is probably more interesting than one specific to border residents 8. For sake of representativeness, I focus on state-level analysis in what follows. Figure 4: Estimated Treatment Effect of Insurance Reform by Year Participation (Retro.) Participation (Current) Full Time Work Retirement from Full Time Work I plot coefficients before triple interaction terms disaggregated by year, sheathed in 95% confidence intervals from 500 repetitions of block bootstrap clustering by state. 8 The border sample includes 14 PUMAs from Massachusetts, which, according to ACS population estimates, comprise only 27% of the total state population ( out of ). 21

22 Turning back to micro data, I disaggregate the triple interaction term by year and present program dynamics in Figure 4. Overall, effect of the insurance reform appears persistent, and the pattern for both measures of participation is comparable. Interestingly, the recession years are not associated with particularly large decrease in the stock of workers, but do witness larger exit among full-time workers. Retirement rate then subsides starting year 2011, when full-time participation is at its lowest point. The combined time series of the stock and flow variables is consistent with an equilibrating process of the labor market. Marginal retirees tend to exit labor force in the first few years of the policy, and as the stock of full-time workers decrease, those who remain employed full-time in later years are less likely to retire, giving rise to the decreasing marginal rate as depicted. Note that participation drops lower in the first year (2007), but rebounds at the onset of the economic downturn and declines further thereafter. This might suggest the unanticipated recession could have trivialized the role of insurance affordability in the retirement planning of workers, dampening the salience of the reform. Absent the recession, participation may have dropped lower during and stabilized sooner. Disaggregating by age, Table 6 shows age-specific effect on retirement transition. At the population level, the age gradient peaks at age 62, the earliest age to begin social security retirement, and for transition from full-time work, there is also a significant surge of retirement one year before Medicare onset at age 64. The non-linearity and the bunching at early retirement age suggest agents may selectively time retirement around social security cut-offs to maintain a relatively constant flow of income to smooth consumption. The intertemporal substitution between consumption and leisure by a forward-looking agent generates complementarity between the programs, and depending on the strength of the complementarity, may have important fiscal implication for the social security trust fund. I hence include benefit claiming in my outcome variables (Column 9, Table 6). ACS provides limited but useful information on benefit claiming behavior. In each interview respondents are asked if she receives any income from social security retirement in the previous 12 months. This includes own retirement benefit, spousal benefit, survival benefit and disability. Except for survivor and disability claiming, the earliest age to initiate own and spousal payment is 62. Once initiated, social security is rarely interrupted 9, and I assume an individual is receiving social security at the current age if she reports positive income from this source last year. With only pooled retirement income I do not observe the specific type of benefit one is receiving, and hence cannot isolate the effect on old age benefit which is the relevant type for most workers in the economy 10. Using staggered onset of different social security programs, however, it does appear that the increase in ages are likely a consequence of increased disability claiming before early retirement age, and the larger increase in age 62 is mostly contributed by new old age beneficiaries. Although data cannot directly test the hypothesis, there is suggestive evidence of an unraveling chain reaction following the dispensing of the need to bridge towards Medicare, making more people only need to bridge towards old age, or even before that through disability. Therefore program interaction may well be dynamic, and complementarity versus substitutability can 9 The major exception is disability insurance, for which eligibility is reviewed annually. 10 I can better identify old age beneficiaries from potential disability claimants in a differenced RD design centered around age 62. I provide more details in Section

23 vary by programs and the particular timing in the life cycle when studied. The message echoes what Inderbitzin, Staubli & Zweimller(2015) finds among Austrian retiring workers, for whom unemployment insurance and disability are complements when younger, but are substitutes when closer to retirement. Table 6: Effect of Insurance Reform on Retirement, by Age (1) (2) (3) (4) (5) (6) (7) (8) (9) Participation Participation Ret. From Ret. From Ret. From Ret. From Social Security (Retro.) (Current) Full Time Log Hours Full-Time Full-Time Full-Time Full-Time Retirement treat below post *** *** ** *** ** ** ** (0.0101) (0.0108) (0.0096) (0.0291) (0.0138) (0.0503) (0.0151) (0.0200) (0.0096) Age-Disaggregated Effects: ** * ** (0.0158) (0.0196) (0.0162) (0.0373) (0.0178) (0.0588) (0.0188) (0.0231) (0.0126) ** * ** (0.0187) (0.0177) (0.0164) (0.0413) (0.0183) (0.0602) (0.0187) (0.0256) (0.0124) ** ** * *** ** *** ** (0.0180) (0.0187) (0.0172) (0.0430) (0.0203) (0.0618) (0.0219) (0.0306) (0.0185) ** * *** (0.0171) (0.0205) (0.0171) (0.0471) (0.0229) (0.0581) (0.0256) (0.0346) (0.0212) * *** *** (0.0204) (0.0192) (0.0158) (0.0487) (0.0199) (0.0627) (0.0228) (0.0276) (0.0233) Income 300% > 300% >600% R N First row shows the (un-disaggregated) average effect, and the following rows show age-specific effect where the triple interaction term is disaggregated by integer age in Same set of individual covariates are included for each outcome variable as in the difference-in-differences case. The new outcome, Social Security Retirement in Column 9 has the same individual covariates as retrospective participation, current participation, and full-time work. All regression are weighted by ACS sampling weights. Standard errors in the parentheses are clustered by state, block bootstrapped from 500 repetitions. *** 0.01 ** 0.05 * 0.10 In Column 6-8 I stratify sample by income bracket and show drastically different transition patterns between those eligible for subsidy and those not. Comparison across income groups of full-time retirement rate is meaningful because full-time workers have relatively homogenous retirement rate in the baseline: 10.58% among full-timers earning less than 300% FPL and 8.58% among those earning above. Stratifying by income for unconditional outcomes, however, is problematic because income is positively correlated with participation 11. With similar baseline retirement rates, the increase in early retirement rate is more than three times as large among the low income group, and the gap keeps gaping as agents age closer to Medicare. Policy impact quickly tends toward zero higher up the income distribution (Column 6 and 7). Noticeably, the age profile among the subsidy eligibles is nearly monotone and clearly rising in age, whereas the overall effect is single-peaked at 62. This naturally piques the question whether effect immediately before Medicare age continues the upward trend or reverts back to a lower level, a question I answer using a differenced RD design in the next section. Because insurance affordability is less of a constraint for higher income households, and the majority of the newly insured enroll in public plans receiving subsidy if family income is below 300% FPL, the significantly different magnitude of effect over the income distribution provides the fourth difference that further defends the validity of my identifying strategy. Linking benefit collection decisions with labor supply, it appears that the two economic activities are planned over separate horizons especially among poor households: while larger 11 The unconditional low-income group is comprised mostly of non-participants, whereas the higher income represents more the working population. Stratifying by sample by income would lead to the erroneous conclusion that the reform in fact has smaller effect on subsidy eligibles 23

24 exit from labor force comes later and closer to Medicare, benefit onset appears immediate once viable. However, it is not very clear at this point whether the found increase in benefit collection is mainly from new social security retirement onset, or from carry-over of disability, which seems to drive the increase in ages The next section circumvents this difficulty with a localized difference-discontinuity analysis at the early retirement cut-off that better distinguishes the two programs. 4.3 Differenced Regression Discontinuity Motivated by larger behavioral impact at policy cutoff ages, policy makers may be particularly interested in local treatment effects at exactly the cutoff. One standard approach is to use a regression discontinuity design comparing subjects just below and above the threshold. This gives sharper identification at the threshold and is less susceptible to unobserved confounds and selection that tend to undo a difference-in-differences model. However, in this particular application, identifying treatment effect at the threshold poses several challenges not commonly encountered in the literature. The standard regression discontinuity design would assume that Medicare is the only discrete change that occurs at the threshold, but several other factors, some unobservable to the researcher, can generate similar discontinuity at 65. Formal retirement age, for example, coincides with Medicare onset for those born before 1941, and kinks in pension accrual rules may introduce additional financial incentive to exit at age 65. To the extent that these confounds are time-invariant, and under some common trend assumption at the threshold, one can derive an unbiased estimate by differencing the discontinuity over time. A still bigger challenge is time-varying factors that persist after first differencing over time. In fact the major source of confound in this setting, the normal retirement age, is timevarying and rises with later cohort. If higher normal retirement age induces greater labor supply effort in the first few years of Medicare coverage, then the RD estimate differenced over time tends to under-estimate the true insurance effect on retirement. One way to eliminate the bias is to second difference across states. By the same argument that motivates the triple difference model, a double differenced RD design removes all factors that may contribute to the discontinuous retirement behavior at Medicare but which do not vary either by time or state, and better isolates insurance availability from local economic shocks and long-run cohort-specific trends. I am not aware of any other paper in the literature that motivates and implements this double differenced RD design, which I propose and formalize below. A final difficulty has to do with the discreteness of the age variable in ACS. As the RD design essentially compares treatment effect to the left and right limit of the threshold, the running variables, in this case age, needs to be continuous. However, ACS only codes respondent s age in reference to her last birthday, giving a discrete, rounded-down version of the continuous age variable. Dong(2015) shows that not accounting for the rounding down of age gives biased estimates, and proposes a simple formula to correct for the bias. The formula can be easily adapted to my differenced RD design, although in this application I do not find evidence that the correction makes any meaningful differences to the estimates. I develop the model starting with the standard (sharp) regression discontinuity design. Let X denote the difference between the running variable and the threshold at t. Under perfect compliance, T = I{X < 0} is the treatment indicator. Conditional mean of potential 24

25 outcome in the case of treatment is given by g 1 (X), and in the case without treatment by g 0 (X). For the moment assume both functions are continuous in X at threshold t, and there is no rounding bias in X. In particular, I focus on local linear specification below, although the argument easily extends to the case where g i (X) is polynomial. The ATE at the threshold t is simply the difference lim X 0 g 1 (X) lim X 0 + g 0 (X), and can be estimated by running the following regression Y i = d 0 + d 1 X i + c 0 T i + c 1 X i T i + ϵ i, where the coefficient c 0 corresponds to the ATE at the discontinuity. Dong(2015) shows that for the rounding down of ages from census data, c 0 1c 2 1 recovers the true ATE. The correction term is related to the changes in the first (and higher order if g is polynomial) derivatives at both sides of the threshold. Larger deviation in the derivatives implies larger biases in the round-down; if, on the other hand, the functional forms only differ by a constant term, then ignoring the round-down in age has no impact on the estimates. The factor 1 is 2 because the round-down bias follows standard uniform distribution absent selective timing of birth within a year. To compare the discontinuity across states and over time, I nest the basic RD design within a double difference structure. Specifically, the complete model involves the regression Y i = (d 0 + e 1 T r i + e 2 P ost i + e 3 T r i P ost i ) + (d 1 + f 1 T r i + f 2 P ost i + f 3 T r i P ost i )X i + (c 0 + g 1 T r i + g 2 P ost i + g 3 T r i P ost i )T i + (c 1 + h 1 T r i + h 2 P ost i + h 3 T r i P ost i )X i T i + ϵ i, where T r is the indicator for the treated state, and P ost post-reform periods. The specification essentially pools together four separate RD designs, and compares the discontinuity over time and treatment status as in the standard difference-in-differences model. The key parameter of interest is the coefficient of the tripe difference term, g 3, which under the assumption of parallel trends at the threshold, identifies the average treatment effect at the threshold among the policy states (ATET). In the case that running variable is age rounded down to the nearest integer, ATET is instead estimated by g 3 1h 2 3. Formally, let Ysy, i s = 0, 1, y = 1, 2, i = 0, 1 denote the potential outcome given policy status s, year y and treatment status i, and gsy(x) i the conditional mean of potential outcome given X. D indicates the policy state where treatment occurs for those below threshold t. ATE at the threshold in state s and year y is given by τ sy = gsy(0) 1 gsy(0). 0 The actual policy effect can be modeled as τ 12 τ 02, or the incremental discontinuity introduced by the policy. In relation to observable outcomes, outcome in period 1 is Y1 i = Y01, i and outcome in period 2 is Y2 i = DY12 i + (1 D)Y02. i Differencing gives Y2 i Y1 i = Y02 i Y01 i + D(Y12 i Y02). i Proposition: Under the assumption that Y 02 Y 01 D X = 0, OLS estimate of g 3 is an unbiased estimate of E[τ 12 τ 02 D = 1], or ATET where treatment effect is defined at the threshold as an incremental discontinuity from the baseline. Proof : Proof follows the standard differences-in-differences case. Note that g 3 = lim E[Y i X 0 2 Y1 i D = 1] lim E[Y i X Y1 i D = 1] lim E[Y i X 0 2 Y1 i D = 0] + lim E[Y i X Y1 i D = 0]. 25

26 Using the relation Y i 2 Y i 1 = Y i 02 Y i 01 + D(Y i 12 Y i 02), g 3 = E[g 1 12(0) g 1 01(0) D = 1] E[g 0 12(0) g 0 01(0) D = 1] E[g 1 02(0) g 1 01(0) D = 0] + E[g 0 02(0) g 0 01(0) D = 0]. The common trend assumption implies that E[g i 02(0) g i 01(0) D = 0] = E[g i 02(0) g i 01(0) D = 1], i = 0, 1. Canceling terms it is easy to show that g 3 = E[τ 12 τ 02 D = 1]. For a graphical illustration of what the differenced RD estimate is capturing, Figure 5 compares the before and after age profile of participation and retirement, with the outcome differenced across the treatment and control states. First notice that profiles for both outcomes are smoother and flatter after the treatment than before, and retirement propensity among the aggregate below group increases appreciably relative to the above group, illustrating findings from triple difference estimates. Zooming in on the Medicare threshold age, the significant dip in participation immediately upon Medicare coverage disappears in postreform years. Similarly, while previously retirement seems to bunch right after Medicare age, it is now more likely to occur right before at age 64. The degree to which post-reform profiles reverses pre-treatment patterns identifies the policy impact at exactly the threshold age. Figure 5: Age Profile of Retirement, Before vs. After Participation (Retrospective) Full Time Retirement Treatment Control Difference Treatment Control Difference Before, After, Before, After, In each graph I plot the Massachusetts-control difference in outcome at each integer age between 60 and 69, averaging over the pre-reform ( ) and post-reform ( ) years separately. In practice, I include two years to the left and right the threshold age (63-66), and impose stronger parallel assumption that slopes of the local linear trend may differ at both sides of the cutoff, but are same across state and time. This allows me to set coefficients f 1...f 3 and h 1...h 3 to zero. Any changes in the discontinuity is then treated as if an intercept shift. The reason to desist from a full specification as in the proof is due to large variability in the measurement of certain labor market outcomes at consecutive ages, and linear extrapolation based on these observations may lead to unrealistic projection at the cutoff. The bottom line is that true ATE to the left of the threshold should not differ considerably from the aggregate 26

27 level at 64, and to the right side, the level at 65. Forcing the slopes to be parallel helps average out and compress the larger variation across integer ages, and generally agrees well with a local triple difference including only age 64 and 65. The imposition of common trend may be particularly problematic for the transition variable, because marginal outflow from work force necessarily flips sign with the reform immediately after Medicare than before, violating common trend. Even in this case, however, estimating the full-model gives similar results upon adjustment of rounding. Hence, I present only results using the lean specification Y i = β 0 below after treat + β 1 below treat + β 2 below after + β 3 below + β 4 rule i + β 5 rule i below + γ X i + α s + α t + α st + ϵ i, age i [63, 66], where rule i = age i 65, and covariates in X i are the same as in triple difference specifications. Note that I replace the intercept portion of the full model with a fully disaggregated set of state, year and two-way fixed effects. I cluster standard error at the state level by block bootstrap. I apply this specification to labor market outcomes and benefit collection behavior at both the Medicare (65) and early retirement (62) cutoff. In the latter case,i restrict my sample to ages 60 to 63, and the below variable is replaced by an above variable that takes value 1 for age 62 and 63. That is, for the early retirement specification, coefficient β 0 gives changes right after age 62, whereas in the Medicare case, it shows changes right before age 65. In addition, to minimize the confound of disability benefit that does not have a policy cutoff at 62 but tends to be classified likewise, I further restrict the early retirement sample to exclude whose who have not worked in the past five years, or the long-term unemployed. The excluded cases include individuals who never extensively participated in the labor force and hence do not have own earning records, such as household caretakers, and those who are retired by the age 58 if not earlier 12. Almost all disability claimants belong to the longterm unemployed group in the early retirement sample, since to qualify one must document inability to engage in substantial gainful activity in the economy. The remaining sample is more homogeneously composed of active workers starting own non-disability benefit. They are more likely to be insurance-constrained prior to the reform, and may not be entitled to retirement benefit before 62. Complementarity between insurance and social security old age, if any, should be stronger and more relevant for this subset of workers. Table 7: Differenced Regression Discontinuity Estimates Participation Participation Ret. From Ret. From Ret. From Social Security Social Security Social Security (Retro.) (Current) Full Time Log Hours Log Hours Log Hours Full-Time Full-Time Full-Time Retirement Retirement Retirement ** * 0.247*** (0.0172) (0.0175) (0.0148) (0.0440) (0.115) (0.0438) (0.0228) (0.0669) (0.0215) (0.0199) (0.0315) (0.0215) R N * ** *** ** 0.117*** ** (0.0145) (0.0165) (0.0177) (0.0301) (0.0816) (0.0331) (0.0139) (0.0412) (0.0142) (0.0126) (0.0331) (0.0139) R N Income 300% > 300% 300% > 300% 300% > 300% Estimates are from a double differenced version of regression discontinuity specification. I restrict the sample to year olds to estimate local ATE at age 65, and year olds to the effect at 62. In the latter case I also exclude the long-term unemployed. Standard errors clustered by state from 500 repetitions of block bootstrap in the parentheses. 12 The reason I do not apply the same exclusion to the triple difference sample is that doing so will eliminate practically all early retirees among the above age group, resulting in potentially biased estimates. 27

28 Table 7 presents the results. Note that I also disaggregate by income log hours worked and full-time retirement rate, both of which are conditional on either past year participation or full-time status, and are less subject to the selection bias that undermines a similar stratification of unconditioned retrospective outcomes. Despite the same issue with social security claiming, I nonetheless compare across income groups for this variable, to highlight the important empirical fact that poor households are not only more reliant on social security in the baseline (34.93% of the low income workers receive benefit in age in pre-treatment Massachusetts, versus 23.52% among high income workers), but are also more inclined to start benefit the first moment it is available with the insurance reform (up by 5.74 percentage points, a 16% increase). The effect on higher income group is minimal at both cutoffs. This result is unlikely a consequence of endogenous income status: with the sample restricted to active workers in the economy, income should correlate well with actual earnings from work. Differenced RD design therefore finds strong evidence of large behavioral externality well beyond the original intent of the insurance reform, and raises interesting questions to the degree of overlap between different social programs at the junction of retirement. Upon early retirement age, hours decrease significantly among low income workers by 23%, although actual reduction may be lower if one accounts for the potential bias that lower hours may itself lead to lower income. Nevertheless, the more robust measure of retirement transition shows the same pattern that lower income full-time workers are much more likely to retire immediately after age 62 than higher income counterparts. There is also an aggregate decline in point-in-time participation, and a smaller albeit insignificant decline in full-time status. At the Medicare threshold, increase in retirement rate among low income workers strikes higher at percentage points, the rightful culmination of the bridge towards Medicare. Impending Medicare is also associated with a decrease in participation and full-time work, as well as reduction in hours especially among the higher income workers, although not all are significant. There does not appear any evidence of an income differential in benefit claiming right before Medicare, although the measure itself can be badly constructed due to selection 13. Overall, the reform has led to a reduction in labor supply well before the Medicare threshold, with some of the effects taking hold starting the early retirement age. Figure 6 conflates the age-disaggregated treatment effects with differenced RD estimates to completely characterize the bridge towards Medicare for my main outcomes. 95% confidence bands are based on block bootstrapped standard errors clustered by state. While most outcomes exhibit the hump-shaped pattern peaking at early retirement age, the lower income group is the only case where transition propensity is higher when closer to Medicare, showing a near monotone and rising relationship with age. To the extent that the labor market is yet to equilibrate within the first few years of the policy, and absent any dynamic adjustments by the first generation of retirees facing the mandate, the effect at specific ages should reflect the particular strength of any labor market constraint insurance availability previously imposes on workers at that age. In addition, since only lower income workers receive exogenous variations in premium rates, the unique pattern of this group lends strong support to the behavioral relevance of insurance affordability in old age labor supply, and 13 I do not restrict my sample to active workers for the differenced RD design at 65 to ensure the comparability of estimates when I combine the ATE at 65 with age-specific effects at 60 to

29 Figure 6: Treatment Effect of Insurance Reform on Retirement, by Age Participation (Retro.) Participation (Current) Full Time Work Retirement from Full Time, below 300% FPL Retirement from Full Time, above 300% FPL Social Security Retirement In each graph I plot the average treatment effect at integer ages between 60 and 65, with the point estimates sheathed in 95% confidence intervals from 500 repetitions of block bootstrap clustering by state. Estimated treatment effects between 60 and 64 are from age-disaggregated triple difference models, and at 65 is from the differenced RD design. substantiates the central theme of the paper. 4.4 Synthetic Control This section shows the found effect on transition outcome is not sensitive to alternative construction of control groups, and similar result holds if comparing Massachusetts with a composite control states averaged over the rest of US using Abadie weights (Abadie & Gardeazabal, 2003). Control states bearing more resemblance to Massachusetts in terms of key pre-treatment covariates in addition to the outcome variable receive higher weights in the synthetic control. In doing so, the method balances over important baseline characteristics across states, a potential improvement over the difference-in-differences strategy where such discrepancy need not be accounted for in the estimation. There are a few reasons to believe results from synthetic cohort should agree or disagree with those from triple difference. Abadie et al.(2010) motivates synthetic control as extending the difference-in-differences model allowing time-varying fixed effects in the form of multiplicative factors. In a standard double difference setup, these fixed effects would not have been possible. In my triple difference setup, however, time-varying factors are proxied by state-year and age-year fixed effects, and results from the two approaches should be comparable. On the other hand, if there is no convex combination of existing states that sufficiently replicate Massachusetts in key dimensions, or if there are unobserved trend breaks among some of the control states after the reform, the weights constructed from pretreatment data will give poor predictions of counterfactuals, resulting in potentially biased estimates. 29

30 In addition to being a robustness check on estimates, synthetic cohort can also be a robustness check on motivations. In constructing the Abadie weights, the criterion to determine overall fit relies on a weighting matrix over covariates and outcome that, conditional on a given iteration of Abadie weights, gives the best fit of the pre-treatment outcome. The final output therefore contains two sets of weights, one across the donor states, and the other across baseline characteristics and outcome. Once an agnostic researcher specifies a large number of covariates, the algorithm then statistically selects the most important factors and assigns higher weights to the relevant variables. These variables then signal the likely pathways of policy impact. I include 28 covariates covering a wide range of social-economic conditions that may affect differential retirement across age group at the state level: demographics, unemployment rate, macroeconomic structure, income, wage, health expenditure and health insurance coverage rate and type, as well as labor supply and transition for the below group and group differentials. Outcome is group differential in full-time retirement rate. To reduce over-fitting that occurs to single year irregularities in retirement rate, which could be due to aggregation error over relatively small sample, I smooth over three year intervals to arrive at the retirement rate of the middle year, and then take difference between age groups. I average outcome and covariates over the pre-treatment period, and use the averages to derive optimal weights. Results are summarized in Table 8. Table 8: Estimates from Synthetic Control Panel A: Control Composition State Weight (W) Minnesota New York District of Columbia Washington Wisconsin Panel B: Covariate Match Unweighted Massachusetts Synthetic Control Sample Mean Covariate Weight (V) Percent uninsured Percent on employer plan Percent covered by government Manufacturing sector in GDP Service sector in GDP High school degree Some college White Black Hispanic Below group Above group Total participation Total unemployment rate Male participation Male unemployment rate Below unemployment rate Below participation Below full-time work Below full-time retirement Group dif. in full-time retirement Group dif. in full-time work Group dif. in participation Log medical expenses Log average wage rate Log average household income Log personal income GDP growth rate Panel A breaks down the composition of the synthetic control. The largest contributor is Minnesota, followed by New York, D.C., Washington and Wisconsin. Panel B illustrates 30

31 the gain from using Abadie weights rather than simple averages: pre-treatment balance in observables improves significantly for most covariates. Importantly, predictors with the highest weights are manufacturing sector, percent on employer plan, and male unemployment rate, followed by the outcome variable group dif. in full-time retirement. These covariates suggest that, in addition to macro and labor market conditions, the degree of job-lock by employer-provided private insurance can be an important mechanism leading to differential retirement around Medicare eligibility, confirming the motivation of my main analysis. This is also reassuring indication that the synthesis control is not derived from a mechanic fit over pre-treatment outcome alone, and may have fair external validity when extrapolation is complicated by recession. Figure 7: Synthetic Control Estimate of Insurance Reform on Full-Time Retirement Below Above Difference in Full Time Retirement MA Synthetic MA Treatment Effect, Permutation, N= Treatment Effect, Permutation, N= Upper panel shows time series of actual outcome in Massachusetts and the counterfactual outcome based on the synthetic control. The counterfactual outcome is derived from weighting observed time series across control states with Abadie weights. Lower panel shows placebo treatment effects when the same policy is conducted across control states. The left panel plots the treatment effect over 32 experiments where the pre-treatment fit is no worse than three times of that in Massachusetts. The right panel shows estimates from 22 experiments where the pre-treatment fit is at least as good as in Massachusetts. 31

32 Figure 7 in the upper panel compares the trending of group differential in full-time retirement across Massachusetts and the synthetic Massachusetts constructed from control states using Abadie weights. The difference between the two series in post-reform years ( ) gives treatment effect in a given year. The same hump-shaped pattern emerges as in the triple difference model. The average effect over years is 3.3%, somewhat lower than the triple difference estimate. To the extent that synthetic Massachusetts tends to overpredict retirement differentials in pre-treatment years, the difference may be attributable to the lack of a perfect replica of Massachusetts using existing states and covariates. Overall, the two estimates are comparable in both scale and dynamics. The lower panel of Figure 7 shows results from a permutation test: supposing the insurance reform instead occurred in each of the donor states, I compare the actual treatment effect in Massachusetts with those estimated from placebo experiments. In the lower left panel, I include experiments where the pre-treatment prediction error of outcome is no larger than three times the level in Massachusetts. In the lower right panel, I only include experiments with pre-treatment fit no worse than that in Massachusetts. In both cases, curve of the actual policy dominates all placebo curves in magnitude. The estimated increase by 3.3% is therefore significant at size 3.125% ( 1 ). 32 To summarize, using a variety of empirical strategies, I find consistent evidence that the 2006 Massachusetts reform has led more workers in ages to exit the labor force earlier, and the effect is especially large among low-income workers eligible for premium subsidy and at policy cut-off ages of 62 and 65. However, it is generally impossible to tease out the effect of individual aspects of the insurance reform on retirement using a difference-in-differences framework, when the reform has multiple policy instruments implemented at the same time. One way to overcome the limitation is by isolating exogenous variations peculiar to a specific element of the reform. Utilizing price variation in insurance premium, I quantify in Section 5 the relationship between increasing early retirement rate and premium subsidy, and discuss the welfare implication of the subsidy program on the economy at large. 5 Welfare In this section, I build up a social insurance model (Baily, 1978) for the mandate economy where eligible agents receive premium subsidy funded by tax on the working. Similar to Chetty & Saez(2010), I model endogenous private provision of insurance through workplace, and outcome in the private sector need not be optimal in the presence of public expansion. I show that the welfare formula critically depends on the magnitude of two labor market consequences of the reform: crowd-out of private insurance and disincentive on labor supply. Overall welfare depends on the compounded effect of both effects, with higher rate of crowdout worsening any given level of moral hazard distortion on labor supply. To empirically quantify crowd-out and moral hazard distortion, I isolate exogenous variation in subsidy rates that differ by year, region and age band from yearly releases of HC Schedule, and simulate corresponding subsidy rate from a pre-reform national sample as instrument. I enrich the variation in the instrument by simulating over finer demographic cells that additionally vary by gender, education, race and family composition. Two-stage least square estimates suggests higher subsidy rate induces larger and earlier exit from labor force 32

33 among workers aged 50 and above, has nil effect on the prime-age workforce in ages 35-49, and generates longer unemployment duration for younger workers below age 34. Crowd-out, on the other hand, is largest among younger workers and declines over age. Welfare calculation implies the current program is likely over-subsidizing public plan enrollment over average, and significantly so among near-retirement workers. This section proceeds as the follows. Section 5.1 sets up the social insurance model tailored for the mandate economy in Massachusetts, and derives welfare formula and the sufficient statistics involved. Section 5.2 shows how I simulate the instrument and estimate the extent of crowd-out and non-participation corresponding to one percentage point exogenous increase in subsidy. I characterize crowd-out and moral hazard distortion for both the average population and age subgroups. Section 5.3 calibrates statistics not directly estimable from ACS. Section 5.4 discusses the welfare implication from the model. 5.1 Model Consider an economy where insurance coverage is mandated by law. An agent can either obtain it from a private source, such as own current employer, previous employer, or spousal insurance coverage, or from a public source if private insurance is unobtainable. Depending on income, public coverage comes at reduced cost. Let λ p [0, 1] denote the fraction of premium paid by subsidy in a public plan. The subsidy is a form of public transfer funded by a lump-sum tax τ pb on the currently working. Private transfer in the economy flows from workers to non-workers: the former provides partial insurance to the latter, paying the premium of those who obtain group coverage as spouses, dependents or early retirees. This generates some degree of pre-existing moral hazard even before the mandate came into effect. The representative agent in this economy chooses the effort of working, e [0, 1], and the level of health investment, g [0, 1], at a convex increasing cost of ϕ(e) and ψ(g), respectively. e is also the probability of employment in a given period, and 1 g is the probability of utilizing medical service due to bad health. In the case of utilization, average total medical cost is M, and consumer copay in a representative health plan is C. Assuming premium is actuarially fair, so that insurance company makes zero profit 14, average premium in the economy is (1 g)(m C). Let A be the subsistence income regardless of employment and healthcare utilization status. In addition, workers are paid their marginal productivity w, subject to a lump-sum tax τ pb levied by the government and private transfer τ pv paid toward a fraction of nonemployees with private insurance. Specifically, let λ e denote the fraction of workers who are covered by employer plan, and λ 1 e the fraction of non-workers covered by employer plan. c ij, i, j = 0, 1 represents the consumption of the agent in employment status i and healthcare utilization status j. The consumption of an average worker in good health is then c 10 = A + w τ pb λ e τ pv (1 λ p )(1 λ e )(M C)(1 g), where (1 λ p )(1 λ e )(M C)(1 g) is the out-of-pocket premium paid by workers enrolled in 14 It is simple to include a cost mark-up in this case. However, in Section 5.3 I show that, depending on the definition of total health care cost M, breakeven of insurance company may not be a bad approximation. 33

34 public plans subsidized at rate λ p 15. Similarly, the consumption of an average non-employee in good health is c 00 = A (1 λ p )(1 λ 1 e )(M C)(1 g), where the λ 1 e fraction has their insurance premium covered through private transfer from the working enrollees, and only the 1 λ 1 e fraction pays the unsubsidized part of the premium. For both workers and non-workers, utilization of healthcare service reduces consumption by the amount of copay C: c i1 = c i0 C, i = 0, 1. Note that I assume employers pass on the cost of insurance to employees, and wage is true labor productivity net of private transfer τ pv. Kolstad & Kowalski(2012) finds empirical evidence of the pass-through. The implicit cost of insurance premium generates wage differentials across firms that differ in employer sponsorship of health insurance. Larger differentials incentivize selection into smaller firms that do not provide insurance and substitution into publicly subsidized plans where coverage is cheaper. If the saving in premium is larger than wage loss net of insurance pass-through, then workers will optimally sort into smaller firms and drop private insurance. Aizawa(2015) suggests such incentive is particularly strong among older workers. Transfers are related to individual choices of e, g, aggregate measures of λ e, λ 1 e, and a policy subsidy rate of λ p in the following way: λ e τ pv = ( 1 e λ 1 e + λ e )(M C)(1 g) (1) [ e ] 1 e τ pb = (1 λ 1 e ) + 1 λ e λ p (M C)(1 g) (2) e Assuming expected utility, consumer welfare is given by W = e g u(c 10 ) + e (1 g) u(c 11 ) + (1 e) g u(c 00 ) + (1 e) (1 g) u(c 01 ) ϕ(e) ψ(g) (3) A social planner would substitute out transfers in consumption using Equation(1)-(2), and optimally choose the first-best e, g, λ e, λ 1 e and λ p of the mandate economy. In decentralized decision making, however, agents are price takers and do not fully internalize the social externality of transfer, and first-best is not feasible. In particular, I assume that individuals optimally choose e, g taking transfers τ pb, τ pv as given, and aggregate measures of λ e, λ 1 e need not be optimized in the economy. The sub-optimality in the private provision of insurance may be due to asymmetric information in the insurance market (Einav et al., 2010, 2013), or from behavioral features that lead to imperfect optimization (Abaluck et al., 2011, Baicker et al., 2015, Handel, 2013, Handel & Kolstad, 2015). Had the level of private insurance been optimal, equilibrium outcome from the private market is constrained Pareto-efficient, 15 I implicitly assume everyone in the mandate economy is insured. Given the insurance rate in Massachusetts after the reform averages over 95% in census data, and higher at 97%-98% in state-administered surveys, the assumption seems innocuous. 34

35 and government taxation leads to strict welfare loss(prescott & Townsend, 1984a, 1984b). On the other hand, in cases where public insurance program is large and effective, private insurance market is almost certainly suboptimal. Proposition: For the general case where private insurance is not optimized, a) a marginal increase in λ p leads to a welfare gain of [ dw = (1 dλ e)ũ (c 1 )(M C)(1 g) 1 λ 1 e + (1 λ p ) dλ 1 e p + (1 λ 1 e + λ 1 e )( ϵ 1 e,λ p + ϵ 1 g,λp ) + (1 λ e + λ ] e e ) λ p e λ p 1 e ϵ 1 g,λ p [ + (1 e)ũ (c 0 )(M C)(1 g) 1 λ 1 e + (1 λ p ) dλ ] 1 e (4) b) optimal subsidy λ p satisfies ũ (c 0 ) ũ (c 1 ) = 1+ 1 λ 1 e + λ 1 e λ p 1 λ 1 e + (1 λ p) dλ 1 e ( ϵ1 e,λp e + ϵ 1 g,λp )+ 1 λ e + λ e λ p 1 λ 1 e + (1 λ p) dλ 1 e e 1 e ϵ 1 g,λ p, where ũ (c i ) is the average marginal utility given employment i across utilization status: ũ (c i ) = g u (c i0 ) + (1 g) u (c i1 ). Proof : First totally differentiate Eqn(1) and Eqn(2) to get [ [ dλ e τ pv 1 e = (M C)(1 g) ( ϵ 1 e,λ p + ϵ 1 g,λp ) λ 1 e + dλ ] 1 e λ e + ϵ 1 g,λp + dλ ] e e e λ p λ p [ dτ pb = (M C)(1 g) (1 λ 1 e ) 1 e (1 + ϵ 1 g,λp + ϵ ] 1 e,λ p + ϵ 1 λ1 e,λ e e p ) + (1 λ e )(1 + ϵ 1 g,λp + ϵ 1 λe,λ p ). Then take derivative of W w.r.t. λ p, applying envelope theorem to e, g, ( dw dλe τ pv = dλ eũ (c 1 ) + dτ pb (1 λ e + (1 λ p ) dλ ) e )(M C)(1 g) p + (1 e)ũ (c 0 )(1 λ 1 e + (1 λ p ) dλ 1 e )(M C)(1 g) Plugging in λ edτ pv, dτ pb will lead to a). b) follows from a). Equation (5) embodies the trade-off optimal level of subsidy must balance. The consumption smoothing benefit of social transfer is pit against the behavioral moral hazard effect that takes place in both labor supply (ϵ 1 e,λp ) and healthcare utilization (ϵ 1 g,λp ). While a large literature is dedicated to the estimation of the latter elasticity (Manning et al., 1987, Aron-Dine et al., 2013), the estimation and the welfare implication of the former have not come under much attention in the literature. Equation (5) also shows that any moral hazard distortion in the economy tends to be exacerbated in the presence of crowdout: larger dλ 1 e magnifies the behavioral effect of both elasticity, which in turn lowers the net benefit of public subsidy. In the extreme case where dλ 1 e > 1 λ 1 e 1 λ p, because ũ (c 0 ) > 1, ũ (c 1 ) (5) 35

36 any increase in subsidy will lead to strict welfare loss regardless of the gain in consumption smoothing, and the government should reduce λ p to a level where smaller crowd-out rate and elasticity balance the two sides of Equation (5). Although motivated in a slightly different setup, the conclusion that crowd-out of private transfer worsens pre-existing moral hazard in a generally suboptimal private market is well in line with the argument in Chetty & Saez(2010). Welfare formula in both cases augments the classical Baily(1978) formula with extra terms capturing the level and marginal substitution rate between public and private transfers. In particular, in my application, only crowd-out between private coverage of non-employees and public insurance ( dλ 1 e ) matters for social welfare, rather than between the total level of private and public insurance. This is because the working population is essentially self-insured: any substitution into public insurance dλ among the currently working reduces the premium payment by λ e, p which is completely offset by an equal increase in the transfer through τ that goes to pay for this amount on the Exchange. The net effect of crowd-out among current employees is therefore zero. For a marginal decrease in non-employee insurance, however, saving in the transfer from the working population is (1 λ p ) dλ 1 e, which is also the increase in out-of-pocket premium cost among the unemployed. Because the marginal utility of consumption is greater among the unemployed, the substitution introduces welfare loss proportional to the degree of crowdout in dλ 1 e. By the same token, the level of both λ e and λ 1 e affects the size of moral hazard in utilization ϵ 1 g,λp, but only λ 1 e is relevant for labor supply distortion ϵ 1 e,λp. When applying the above analysis to study specific age groups, one needs to account for the redistribution of tax revenue among age groups. With a uniform lump-sum tax, revenue from groups with less demand for subsidy are re-directed to the assistance of more needy groups. Instead of fully fleshing out the interdependency, I adjust τ pb, the tax revenue needed to finance subsidy within group, by a heuristic factor κ, to get at the population tax level actually in place in the economy. Empirically κ is pinned down by the distribution of premium subsidy over age. For a particular age group, Equation(5) is modified as he following: ũ (c 0 ) ũ (c 1 ) [ =κ 1 ( 1 κ 1) e + 1 e 1 λ e + λ e λ p 1 λ 1 e + (1 λ p) dλ 1 e 1 λ e + (1 λ p) dλe 1 λ 1 e + (1 λ p) dλ + 1 e ] e 1 e ϵ 1 g,λ p 1 λ 1 e + λ 1 e λ p 1 λ 1 e + (1 λ p) dλ 1 e ( ϵ1 e,λp e + ϵ 1 g,λp ) (6) Note that Equation (6) goes back to (5) if κ = 1. The extra term weights the relative extent of crowd-out for both types of private insurance. dλ e enters subgroup analysis because workers in a given age band need not be self-insured considering fiscal externality. Among beneficiary groups with κ < 1, within-group moral hazard distortion tends to be smaller due to free-ride, and the reduction is equivalent to an increase in consumption benefit of transfer by a factor of 1. In that case, if the crowd-out of both types are small, or dλ β 1 λ κ < β 1 λ p, β = e, 1 e, then the government is marginally more inclined to increase the subsidy of this age group relative to the entire population, holding constant the moral hazard distortion across age groups. On the other hand, if crowd-out in both cases is large, dλ β 1 λ > β 1 λ p, then marginal cost from government intervention strictly increases, and the government should 36

37 scale back subsidy to this group and target redistribution to groups with larger gain from insurance provision but smaller rate of crowd-out. 5.2 Estimation Equation (5) and (6) show how welfare depends on a few sufficient statistics capturing the labor and insurance market distortion in the mandate economy. Some of these statistics have been estimated in the literature, including crowd-out and price elasticity of healthcare utilization, while others, such as premium elasticity of non-participation, is new and first estimated in this paper. There are a few reasons, however, that previous estimates of crowd-out may not directly apply in this setup. Firstly, previous estimates focus on Medicaid expansion to cover parents and children, and impute eligibility from reported family income in the census data. Due to the relative low take-up rate of Medicaid (Card & Shore- Sheppard, 2004), simulated eligibility may contain substantial misclassification error that biases the estimates. This is less likely to be an issue in Massachusetts, where the individual mandate led to near universal insurance coverage within one year of the policy. In addition, failure to obtain insurance incurs a tax penalty which is absent in previous public insurance expansion. The financial incentive increases the willingness to pay for insurance, and may have different implication for insurance substitution on the margin than is suggested in previous estimates. Lastly, while eligibility for Medicaid is often dichotomous, subsidy schedule generates continuous variation in out-of-pocket premium cost, and it is the differential exposure to subsidy on the intensive margin, rather than the extensive margin of eligibility, that is of policy interest in this study. This subsection describes how quantities of crowd-out ( λe λ p, λ 1 e λ p ) and labor supply disincentive (ϵ 1 e,λp ) can be estimated using insurance and participation outcomes in post-reform Massachusetts in ACS. The underlying source of identification is exogenous policy exposure that varies across region, year, age band and demographic cells. As described in Section 3, I obtain affordability limit for different income brackets and the lowest premium rate of an individual plan in a given region and age band from yearly releases of Massachusetts HC Schedule Worksheets. For example, if in year t, region r, an individual i of income bracket j is supposed to pay no more than L ijt per month towards insurance premium, and the lowest monthly premium in her region of residence and age band a is P iatr, then the person would be entitled to a subsidy level of subs iajtr = 1 L ijt P iatr on the Exchange. This definition reflects the fact that in Commonwealth Care, for each corresponding income bracket j below 300% FPL, there always exists a subsidized plan with out-of-pocket premium payment no greater than L ijt. Since L ijt does not vary by age and region, older people who would be paying higher premium rates are subsidized more, and so are residents in regions with higher market premium rates. These differences create exogenous within-year variation in policy intensity that identifies the effect of subsidy schedule on labor supply and crowd-out. Specifically, age bands are 0-26 years old, 27-29, 30-34, 35-39, 40-44, 45-49, 50-54, and Massachusetts limits the age rate adjustment factor to no larger than 2:1, so that pre- 16 According to HC Schedule from 2007 to 2011, there is no premium variation within the age band across all regions. I hence do not further divide the age band into 5-year subgroups in my empirical analysis. 37

38 mium charged to the oldest enrollee of a plan cannot more than double the amount charged to the youngest enrollee. In 2011 and the region of Berkshire, Franklin, and Hampshire, for example, the lowest individual plan premium for a 30 years old is $ 258 per month, and that for a person aged 55 years or older is $ 455. Regions are collections of individual counties. A similar regulation on area rate adjustment limits the geographical variation of premium rates within the range 0.8 to 1.2. In my empirical strategy, the unit of geographical information is at the level of public use micro areas (PUMA) in ACS. PUMAs are geographically contiguous units build on census tracts and counties that do not cross state borders. As explained in the previous section, PUMAs are linkable within each decennial census, and in year , Massachusetts is divided into 52 PUMAs, most of which are exposed to the same policies that vary at the region level. For PUMAs that straddle two policy regions, I generate additional policy variation by weighting subsidy rate across regions, with the weights corresponding to the fraction of population in each region. My estimation sample consists of Massachusetts residents insured from a source other than Medicare who are aged between 27 and 64 when sampled during Young adults below age 26 pay lower premium and often obtain coverage as dependents. The dependent mandate of ACA passed in 2010 further increases the percentage of young adults insured from a parental source (Akosa Antwi et al., 2013). To avoid complication of inter-generational insurance allocation and the early effects of ACA dependent mandate, I restrict my sample to individuals over age 27, who are more likely to be workers, jobseekers and less likely full-time students. Since premium subsidy does not exist before the reform, nor the mandate, I exclusively use post-reform years to estimate sufficient statistics of the model. Because insurance coverage type is first asked in ACS in 2008, I start my sample in 2008 and extend it through 2011, beyond which sub-state geographic area is no longer linkable. Also, since my model assumes universal coverage, I further limit the sample to those reporting insured by a non-medicare source, reducing sample size from to individuals 17. The simulation sample comes from continental US population in releases of ACS. The choice of a national rather than state or regional sample in particular alleviates the bias from endogenous program placement: if the reform in Massachusetts is related to state or region level unobserved factors, then simulated subsidy from Massachusetts or the broader Northeastern sample will be correlated with the error term, and two-stage least square estimate will be biased. The concern of endogenous program placement cannot be warded off by inclusion of state and regional fixed effects in this application, because estimation is restricted to the treatment state where such fixed effects cannot be identified or estimated 18. It hence depends critically on a national sample to strip away any factors that 17 It is straightforward to extend the current setting to study tax penalty and the decision to obtain insurance jointly with premium subsidy. Holding constant the effect of penalty on insurance coverage, however, allows simpler characterization of the trade-off inherent in an optimal design of subsidy schedule. The high coverage rate following the individual mandate suggests such omission need not be problematic. Nevertheless, I show in Table 9 and 10 the effect of premium subsidy on insurance demand, where the sample includes both insured and uninsured residents. 18 There is some reason to believe that simulated subsidy from the Northeastern sample might still be biased, given the fact that the region has higher insurance rate over this period than the national average, and besides Massachusetts, states including New York, Vermont, Maine, Connecticut and District of Columbia have implemented some form of health insurance reform aimed at lowering uninsurance and insurance cost. 38

39 may contribute to the incidence of reform in Massachusetts. Even with a national sample, there are still concerns that simulated IV from the post-reform period may be contaminated by the confounding effect of recession, and instead of being a pure parametrization of subsidy generosity, also embodies any time-varying shocks that hit the economy over this period. Exogeneity will be violated either because of imperfect control of time-varying factors within Massachusetts, or because of common regional or national trends that cannot be controlled for in a within-state regression. I therefore simulate over the relatively stationary economy in , predating both the reform and the concurrent recession. From the simulation sample, I calculate subsidy rate based on reported family income applying schedules from different region-year combination. Within each combination, HC schedule provides variation in premium rate by age groups, and I utilize this information when generating subsidy. I augment the variation by age with extra demographic variables of gender, race (White, Black, other), Hispanic origin, education (high school drop, high school, some college), marital status, and the presence of own children below age 21 in the family. Fully interacting the factors, I derive 1008 demographic cells. For each region-year combination, I take within-cell mean of simulated subsidy rate in the simulation sample, and construct the instrument by assigning the mean to corresponding individuals in the estimation sample. The artificial variation by demographics is crucial for identifying causal estimates within age band, for otherwise there would be no variation left in the instruments. The variation by demographic cell is large and meaningful: for example, in year 2011 and region of Berkshire, Franklin and Hampshire, the average subsidy rate for a year old White, non-hispanic male with some college eduction who is married but childless is 6.22%, whereas for a year old single mother who is Black, Hispanic and a high school drop-out, it is 99.10%. The first-stage equation is subs idtp = α 0 subsiv idtp + α t + α p + α tp + γ X idtp + µ idtp, where outcome is observed for individual i of demographic cell d in year t and PUMA p. The second stage is y idtp = β 0 subs idtp + α t + α p + α tp + θ X idtp + ϵ idtp. As noted above, exogenous subsidy variation in subsiv idtp is at the year-puma-demographiccell level, although most of the variation across PUMA varies at the region level except for borderline PUMAs. I include PUMA, year and PUMA-year fixed effects to fully address any unobserved local heterogeneity that may be permanent or time-varying. This importantly soaks up any endogenous program placement bias arising from spacial differences in insurance market structure and pricing, or from residential sorting driven by population unobservables such as health. It also flexibly picks up any differential impact of recession over time and locality, an extra source of confound in this period. Netting out these fixed effects, the remaining variation in the IV is by demographic cells. To jointly account for the interactive effects of all demographic controls, I include cell fixed effects in X 19 idtp. Considering that None of them, however, has an individual mandate as in Massachusetts. 19 There are a total of 963 such fixed effects in the estimation sample. 39

40 such large number of fixed effects might dilute the explanatory power of the first stage, I alternatively include only marginal demographic fixed effects. I also experiment with replacing the age group fixed effects with integer age fixed effects. Conditional on all the fixed effects and demographic controls, variation in the instrument is by policy rules that differ across region, age, year and income. As a mere parametrization of such variation, simulated subsidy rate is exogenous to any omitted variable that may enter the decision of labor supply and insurance choice, and exclusivity is satisfied by construction. The instrument importantly corrects for biases from reverse causality if individuals sort into public subsidy, attenuation of OLS estimates if income is measured with error, and unobserved heterogeneity in local insurance and labor markets that may affect both treatment status and outcome. Table 9 shows the two-stage least square estimates for the mandate economy. Standard errors are clustered by PUMA. I look at labor supply outcomes using various measures in ACS, total insurance demand, demand for private insurance and crowd-out by insurance type in Table 9. Sample of labor supply outcomes and private insurance demand includes only insured Massachusetts residents not covered by Medicare in the age of Total insurance demand includes both insured and uninsured residents not enrolled in Medicare. Employee (Non-employee) private insurance coverage is conditional on the sample of current employees (non-employees). The left panel shows the first stage as I experiment with different demographic controls. Including a complete set of demographic cell fixed effects greatly reduces the power of the first stage: F-statistic on the instrument is less than 20, and even lower for conditional outcomes due to smaller sample size. Using marginal demographic fixed effects significantly boosts the F-statistic, and brings the coefficient before subsiv closer to unity. Further disaggregating to integer ages barely changes the first stage. The right panel shows the corresponding second stage for each outcome. Using integer age fixed effect halves the moral hazard effect on all labor supply outcomes, and renders most of them insignificant. There is minuscule effect on reported point-in-time non-participation, but larger effect on actual employment outcome either in the past year or last week. Although not significant at the population level, the aggregate estimate masks substantial heterogeneity in the moral hazard effect across age subgroups, which I make clear below in Table 10. Insurance outcomes are less sensitive to alternative models of marginal fixed effects. The increase in demand of any health insurance in response to one percentage point increase in subsidy rate is 0.17 percentage points. Although not one of the sufficient statistics, this estimate is interesting in and of itself as it summarizes the effectiveness of premium subsidy on improving insurance rate, and the same information is difficult to extract from previous estimates of demand elasticity absent the mandate. Overall crowd-out estimate is Considering subsidy rate is around 60% among insured Massachusetts residents not covered by employer group plan, a marginal enrollee in Commonwealth is associated with a % = 38% chance of dropping private insurance, smaller than the 50%-60% range found in previous literature. Stratifying by employment status, about two-thirds of the overall crowd-out is attributed to non-employees dropping private insurance, and the crowd-out from current employees is smaller by comparison. Hence there is evidence that employee mandate in Massachusetts has been largely successful in maintaining the central role of employers in the provision of employee health insurance, although worker selection into low-productivity jobs not sponsoring insurance also cannot be rejected by the data. 40

41 Table 9: 2SLS Estimates of Labor Supply Disincentive, Insurance Demand, and Crowd- Out (1) (2) (3) (4) (5) (6) Non-Participation, Retro. First stage: Second stage: α *** *** *** β ** (0.3975) (0.0313) (0.0319) (0.1630) (0.0326) (0.0340) R R F-statistic on IV N Non-Participation, Current First stage: Second stage: α *** *** *** β (0.3975) (0.0313) (0.0319) (0.1830) (0.0314) (0.0331) R R F-statistic on IV N Non-Employment, Current First stage: Second stage: α *** *** *** β *** * (0.3975) (0.0313) (0.0319) (0.2069) (0.0365) (0.0380) R R F-statistic on IV N Any Health Insurance First stage: Second stage: α *** *** *** β *** *** (0.4120) (0.0304) (0.0308) (0.1943) (0.0294) (0.0290) R R F-statistic on IV N Total Private Insurance First stage: Second stage: α *** *** *** β *** *** *** (0.3975) (0.0313) (0.0319) (0.2398) (0.0350) (0.0356) R R F-statistic on IV N Employee Insurance First stage: Second stage: α *** *** *** β *** *** *** (0.4008) (0.0320) (0.0325) (0.2897) (0.0370) (0.0370) R R F-statistic on IV N Non-employee Insurance First stage: Second stage: α ** *** *** β ** *** *** (0.8649) (0.0576) (0.0588) (0.5721) (0.0711) (0.0701) R R F-statistic on IV N PUMA-year fixed effects X X X X X X Demographic cell fixed effects X X Marginal demographic fixed effects X X X X Integer age fixed effects X X This table summarizes 2SLS estimates of premium subsidy on different measures of labor supply, total insurance demand, and private insurance crowd-out among those insured. Instrument is simulated subsidy rate from the continental US sample, at the level of region-year-demographic cells. Estimation sample for labor supply outcome and total private insurance is from Massachusetts residents between age who are insured from a non-medicare source; for demand for any insurance it includes both insured and uninsured residents but not Medicare enrollees. The sample for employee (non-employee) private insurance includes only the currently working (non-working). All specification includes PUMA, year and PUMA-year fixed effects, as well as demographic controls. Standard errors clustered by PUMA in the parentheses. The left panel shows estimates from the first stage, where demographic controls differ. I experiment with cell fixed effects (Column 1), marginal fixed effects (Column 2), and marginal fixed effects disaggregated to integer ages (Column 3). Corresponding second stage estimates are in Columns 4-6 in the right panel. *** 0.01 ** 0.05 *

42 Table 10: 2SLS Estimates of Labor Supply Disincentive, Insurance Demand, and Crowd-Out, Age Subgroups (1) (2) (3) (4) (5) (6) (7) (8) Panel A: Non-Participation, Retro. β ** ** ** *** (0.0385) (0.0347) (0.0455) (0.0354) (0.0453) (0.0421) (0.0407) (0.0340) F-statistics R Non-Participation, Current β * ** *** (0.0402) (0.0338) (0.0432) (0.0336) (0.0428) (0.0414) (0.0370) (0.0331) F-statistics R Non-Employment, Current β *** *** * * (0.0433) (0.0397) (0.0488) (0.0379) (0.0461) (0.0503) (0.0456) (0.0380) F-statistics R Any Health Insurance β *** *** *** *** *** *** *** *** (0.0411) (0.0341) (0.0306) (0.0315) (0.0330) (0.0344) (0.0374) (0.0290) F-statistics R Total Private Insurance β *** *** *** *** *** *** *** *** (0.0475) (0.0381) (0.0391) (0.0342) (0.0448) (0.0461) (0.0489) (0.0356) F-statistics R Employee Insurance β *** *** *** *** *** *** *** *** (0.0595) (0.0413) (0.0490) (0.0410) (0.0504) (0.0498) (0.0556) (0.0370) F-statistics R Non-Employee Insurance β *** *** *** *** *** *** *** *** (0.1165) (0.0868) (0.0670) (0.0702) (0.0691) (0.0779) (0.0789) (0.0701) F-statistics R Panel B: Group Mean Population Non-Participation, Retro Non-Participation, Current Non-Employment, Current Subsidy Among Non-Privately Insured Any Health Insurance Private Insurance Employee Insurance Non-Employee Insurance ϵ 1 e,λp Retro. Non-Participation Current Non-Participation Current Non-Employment Panel A summarizes age-group-specific 2SLS estimates of premium subsidy on different measures of labor supply, total insurance demand, and private insurance crowd-out among those insured. I construct group-specific (simulated) subsidy rate by interacting (simulated) subsidy rate with age group indicators. I show F-statistic from the first stage of each endogenous regressor in the column corresponding to that age group. R 2 is from the second stage. All specification includes PUMA, year and PUMA-year fixed effects, as well as marginal demographic fixed effects with integer age fixed effects. Standard errors clustered by PUMA in the parentheses. Panel B shows summary statistics for key outcome variables and subsidy rate by age groups, and calculates implied subsidy elasticity of non-participation for different measures of labor supply outcomes. *** 0.01 ** 0.05 *

43 Insurance mandate and premium subsidy may have different implication for workers at different stages of life cycle. To uncover heterogeneous effects of subsidy across age subgroups, I interact subs and subsiv with respective age group indicators and estimate group-specific effects in a pooled regression. Table 10 summarizes 2SLS estimates based on the preferred specification with disaggregated marginal demographic fixed effects in Panel A. I suppress the first stage but show the F-statistic for each endogenous age-specific subsidy rate in the corresponding column. In Panel B I show descriptive statistics of key outcomes and subsidy rate by age groups, and calculate the implied elasticity of non-participation ϵ 1 e,λp. Crossreferencing retrospective and point-in-time non-participation, both show similar age profiles in Panel B, but in Panel A, effect of subsidy on point-in-time non-participation is larger only among near-retirement workers, whereas on retrospective non-participation it is also larger among younger workers. The difference seems to suggest subsidy has led to earlier exit from labor market among pre-retirees, and involuntarily long spell of unemployment among entering workers. Indeed, one percentage point increase in subsidy rate reduces the chance of youth employment by 0.15 percentage point, with no significant impact on the employment of older workers. None of the labor supply measures show any meaningful impact on the prime age workforce aged Demand for any insurance in more responsive to subsidy at older ages. Crowd-out is more concentrated among young workers, and crowd-out from own employer plan declines substantially over age. The combined evidence implies the employer mandate may have worsened the labor market position of entering workers, placing more of them on subsidy to fulfill the individual mandate. There is no evidence, however that selection into public insurance is occurring among older workers, as argued in Aizawa(2015). If older workers indeed switch into lower-productivity jobs to obtain cheaper coverage from the Exchange, empirically one expects to find smaller decline in crowd-out toward retirement age if not a rising age profile of crowd-out. But neither is the case in Massachusetts. The distinction matters crucially for welfare analysis of the reform. In Aizawa(2015), inefficiency of the reform stems from productivity loss when higher skilled workers sort into lower productivity jobs; in the alternative where pre-retirees bridge towards Medicare and relinquish labor supply altogether, expected welfare loss can be much larger. 5.3 Calibration Because ACS does not contain information in consumption and healthcare utilization, I calibrate the remaining statistics using other datasets or infer them from previous estimates. I integrate information on hospitalization usage rate among Massachusetts residents, average premium rate, and total health care cost published by CHIA and CMS, and extrapolate the RAND elasticity of health care utilization (Manning et al., 1987) to derive the increase in usage with respect to premium subsidy. I calibrate consumption ratio across employment and utilization status from HRS-CAMS. Details are explained below. The RAND elasticity of -0.2 states that one percent increase in out-of-pocket healthcare cost reduces usage by 0.2 percent. In this application, note that the variation is not from outof-pocket cost C, but rather from premium subsidy that applies to the portion of population not covered by employer plan. To the extent that premium subsidy constitutes a small proportion of total out-of-pocket medical cost consisting of insurance premium and copay, 43

44 the magnitude of ϵ 1 g,λp tends not to be large. Formally, the population level out-of-pocket medical cost is C = (1 λ p λ ne )(M C)(1 g) + C, where λ ne = e(1 λ e ) + (1 e)(1 λ 1 e ) is the portion not having employer plan and eligible for subsidy λ p. Differentiating w.r.t. λ p gives d C = (1 λ p λ ne )(M C) d(1 g) dλ (λ ne + λ ne p )(M C)(1 g). Note that ϵ 1 g,λp is related to the RAND elasticity ϵ RAND λ d through ϵ 1 g,λp = ϵ RAND p c C, which by definition is also equal to d(1 g) λ p. Equating the 1 g two expressions solves for d(1 g) as a function of observables in the data: dλ d(1 g) λ ne + λ ne p dλ = ϵ RAND (1 g) p (M C)(1 g). Cλ p ϵ RAND (1 g)(1 λ p λ ne )(M C) Calibration proceeds as follows. Based on Acute Care Hospital Utilization Trends in Massachusetts FY released by CHIA, inpatient care usage among the age group is 0.081, and among age group is Using linear interpolation, the median age (45) usage rate is 1 ˆ g = With mean premium rate in the individual market at $ 400 per person per month, the implied out-of-pocket medical cost excluding premium is M ˆ C = $4211. The average total health care expenditure (THCE) in Massachusetts over this period is around $ 400 per person per month. Adjusting for any under-count relative to the CMS measure of State Health Expenditure Account (SHEA) 20, I inflate the figure by Hence M is set to = $5263, and copay C is set at = $1052, corresponding to a coinsurance rate of 20%. Note that such calibration will approximately make insurance company break even. I also have dλ ne = 0.63 from IV estimates. Plugging in the numbers gives a tiny increase in utilization: = , and an d(1 g) elasticity of The negligible impact on moral hazard in health care utilization is due to the small percentage of subsidized premium in the total medical cost of utilization. In subsequent analysis, I therefore shut down this channel of moral hazard, and set d(1 g) and ϵ 1 g,λp to zero. Previous calibration of consumption has either stratified by employment status (Gruber, 1997) or by healthcare utilization status (Cochrane, 1991). In this setup, I stratify by both using data from Consumption and Activity Mail-out Survey (CAMS) of HRS. HRS is the only survey that contains detailed consumption information along with employment and healthcare utilization status 21. The limitation of HRS is it mainly samples individuals over age 50, and is not representative for the entire population. Assuming that younger and older workers smooth consumption similarly in face of negative employment and health shocks, but differ by the incidence of such shocks, I infer average consumption smoothing patterns from those of older workers. 20 THCE released by CHIA includes all insurance related payment made by or on behalf of Massachusetts residents for health care services. It particularly excludes dental insurance and any payments made by third-party programs not surveyed by Commonwealth. Expenditure in over-the-counter drugs not covered by insurance is not included. These items account for a 20% under-count, with the total level of under-count about 30%. 21 Other common sources of consumption data such as CEX and PSID do not have information on utilization, and PSID only contains food consumption. 44

45 CAMS is a biannual survey following respondents in the main HRS survey the previous year. In the main survey, respondents answer questions on employment status, health insurance coverage and health care access. I restrict the sample to years olds reporting insurance coverage from a non-medicare source. To avoid complications of inter-generational allocation, I include only single and couple households with no co-residing children, and divide consumption evenly between husband and wife for couple households. I suppose household members do not participate in labor force if neither spouse is working full-time. All dollars are deflated to reflect 2005 amount. For inpatient use, HRS records the number of nights spent in hospital over the past two year period. The 90th percentile is 4. I hence assign utilization status to households reporting spending over 4 hospital nights per person in the following main survey year. The average inpatient usage rate on the extensive margin is 0.11 from the national sample of HRS, similar to the in post-reform Massachusetts. This again seems to suggest that premium subsidy has not led to significantly different utilization patterns. Table 11: Consumption Calibration Non-Durable Consumption: mean g 1 g median g 1 g e e e e Food Consumption: mean g 1 g median g 1 g e e e e I include in consumption expenditures on non-durable goods inclusive of housekeeping expenses such as laundry. As a robustness check I also restrict consumption to food expenditures only. I present both mean and median statistics in Table 11. Both show similar variation across cells, but median consumption appears more robust to outliers towards the upper tail of the distribution. Consistent across total and food consumption, comparing medians implies c 1,0 c 1,1 = 1, c 1,0 0.8 c 0,0 = 1, and c 1,0 0.8 c 0,1 = 1. Although ratio by utilization status 0.7 cannot be directly compared with previous estimates, by employment my estimate seems to understate agent s ability to smooth consumption over negative employment shock. This might stem from the fact that I calibrate over a relatively old population for whom the retirement consumption puzzle (Battistin, 2009) may have exacerbated any dip associated with job loss. When extrapolated to apply to the younger population, the ratios then place an upper bound on the consumption smoothing gain of social transfer. Following standard practice, I assume utility takes CRRA functional form, with the risk coefficient γ calibrated to 2. There is no general consensus on the appropriate range of the risk coefficient in the retirement context, with the estimated value close to 1 in Rust & Phelan(1997) and around 5 in French & Jones(2011). Chetty(2006a) argues that for the expected utility model to be empirically congruent with observed substitution patterns between wage and leisure, the risk coefficient cannot be very large. He places an upper 45

46 bound of γ = 2. At this value, ũ (c 0 ) ũ (c 1 ) = for the age group where 1 g = 0.101, and for the average population where 1 g = Finally, κ is estimated from the age distribution of subsidies. Let subscript o denote the age group, and y denote the younger population. µ i denotes the fraction of each age group in the population. Average taxation relative to premium is given by i=o,y t = µ iλ ne,i λ p,i θ i i=o,y µ, ie i where θ captures the age adjustment of premium for the younger population. Using listed rates in HC Schedule, θ o = 1, θ y = The calibrated tax level is for an average agent in the economy. Should the subsidy to older workers be funded completely by taxation within group, the implied tax rate is I therefore calibrate κ = = Welfare Formula The calibration of ϵ 1 g,λp being zero simplifies welfare discussion. Define subsidy in absolute term λ p = λ p (M C)(1 g), or the amount of subsidy applied to an average plan. Note that d λ p = (M C)(1 g). Recall that λ ne measures the proportion of agents not covered by employer plan and entitled to coverage from a public source. Given that transfer goes from taxation on workers to subsidy to public insurance enrollees, a monetary representation of welfare normalizes the marginal gain of a dollar increase in λ p accruing to the subsidized by the marginal gain of a dollar increase in the wage of the employed: dw d λ p /λ ne dw dw /e =1 e ũ (c 0 ) λ ne ũ (c 1 ) ( 1 λ 1 e + (1 λ p ) dλ ) 1 e κ 1 e λ ne e 1 e ( 1 κ 1)(1 λ e + (1 λ p ) dλ e ) + [ 1 λ 1 e + (1 λ p ) dλ 1 e ( 1 λ 1 e + λ 1 e λ p ) ϵ1 e,λp Table 12 summarizes values of sufficient statistics and calculates the welfare gain according to Equation (7). I choose different measures of labor supply for the average and the old age population. As I show the effect of subsidy on older workers is mainly on earlier retirement, I plug in ϵ 1 e,λp from retrospective non-participation past year, which agrees well with current non-participation as measures of voluntary exit from labor force. Given the effect on the overall population is a synthesis of both voluntary non-participation among older workers and involuntary unemployment among younger workers, I rely on the retrospective measure of labor supply last year, and set ϵ 1 e,λp = I show separate results for different values of CRRA coefficient from 1 to 3. Result is not sensitive to this range of risk aversion commonly used in the literature. On average the subsidy is slightly above the optimal: one more dollar of subsidy on the margin reduces welfare by dollar. Accounting for the upward bias extrapolating ũ (c 0 ) ũ (c 1 ) from the HRS sample, the overall welfare loss might be larger. Among older workers, there is clear evidence that subsidy is well above the optimal: depending on the degree of risk e ] (7) 46

47 aversion, the marginal welfare loss of an incremental dollar on subsidy ranges from dollars. Should the current subsidy level be optimal, the implied risk coefficient would be close to 8, completely out of bounds of most empirical estimates. Not accounting for fiscal externality across age groups, or the attenuation of moral hazard by free-riding, the welfare loss would be even higher at dollar. The policy implication is that government should scale back subsidy substantially among older workers approaching retirement, and direct most of the saving to prime age workers exempt from moral hazard distortion. Table 12: Sufficient Statistics and Welfare Source e ACS, retrospective participation λ e ACS, group plan coverage among currently working λ 1 e ACS, group plan coverage among non-employees λ ne ACS, fraction not covered by group plan λ p ACS, subsidy based on repored family income ϵ 1 e,λp IV estimate, retrospective dλe dλp IV estimate dλ1 e dλp IV estimate ũ (c0) ũ (c1) γ = HRS consumption and CHIA inpatient use, MA, 2012 γ = γ = κ ACS, subsidy across age group 1 λ 1 e + (1 λ p ) dλ1 e dλp 1 λ e + (1 λ p ) dλe dλp 1 λ 1 e + λ1 e 1 e λne λp dw d λp /λne dw dw /e γ = γ = γ = In relations to other welfare analysis on the insurance reform, the model in this paper takes a more normative stance than before-after comparisons that underlie Hackmann et al.(2015) and Kolstad & Kowalski(2012), and the implication to policy design echoes that of a structural simulation exercise in Aizawa(2015). Aizawa(2015) argues that optimal subsidy rate should decline substantially with age. This is motivated by the observation that actual subsidy rate is much higher for older workers, making sorting into lower productivity jobs profitable. Although policy prescription from both approaches coincides for pre-retirees, mechanism differs: instead of sorting, empirical evidence from Massachusetts suggests early exit from labor force as the major source of inefficiency. Compared to disincentives on the extensive margin of participation, welfare loss due to sub-optimal matching within work 47

48 force is probably second-order. In addition, there is evidence that insurance mandate may have introduced market friction that particularly disadvantages entering workers, who spend more time searching for job and are more likely to be unemployed. To the extent that unemployment is involuntary due to government intervention, premium subsidy for the young tends to be larger to compensate the income loss. To the extent that health insurance, in the similar spirit of unemployment insurance, generates agent level moral hazard reducing search effort, premium subsidy need not be as generous. Overall subsidy as a function of age may well be non-linear, and there seems consensus across different approaches that subsidy towards older workers is very likely above the optimal level. 6 Conclusion This paper finds clear empirical evidence that affordability of health insurance matters for continued labor supply of workers near retirement age, and the institutional fabric of public coverage at older age in the US has led to the salient behavioral pattern of bridging towards Medicare among years old workers with access to private coverage from employer. Causal identification comes from a natural experiment in Massachusetts that implements an individual mandate and subsidizes the insurance purchase of low income households. These measures effectually eliminate the insurance discontinuity at age 65, and result in a large pull-back from labor force and earlier transition into retirement. The effect is especially large at policy threshold ages of Medicare and early onset of social security, where the reduction in labor market effort is greater among low-income, subsidy-eligible workers on both the intensive and extensive margin. The rising age profile of retirement rate of these workers suggest prior to the reform, the employment-lock of insurance availability is stronger the closer to Medicare age. The large behavioral response to the reform is then considered in a social insurance model where public subsidy on insurance raises moral hazard issues. Welfare formula suggests subsidy impinges on welfare potentially by way of labor supply disincentives and crowdout of private insurance, exacerbating any pre-existing inefficiencies in the private market. Using policy variation as well as demographic variation in policy exposure, I quantify disincentive and crowd-out for a succession of age groups. While crowd-out of own-employer plan is largest among younger workers and declining in age, disincentive on participation is larger among both younger and older workers. Effect on self-reported non-participation is stronger only among near-retirement workers. The combined evidence seems to suggest the mandate has resulted in longer unemployment duration for entering workers, whereas for near-retirement workers, participation is probably a more important pathway than selection. Policy prescription from welfare calculation would scale back the average subsidy rate in the economy, especially among older workers. The differential susceptibility to moral hazard by age group implies optimal subsidy rule may well be age-dependent. However, a complete characterization of the policy function cannot do away with a comprehensive set of assumption over all aspects of economic interaction between workers, firms, and the government, and in addition needs to address the adverse labor market effects on younger workers found in the case of Massachusetts, and the large pull-back from labor force among older workers well before the presumed retirement age of 65. In terms of external validity, to 48

49 the extent that an economy out of recession is better able to match workers with vacancies, and the employer mandate under ACA is less harsh on the part of small businesses, the phase-in of ACA may not witness as strong an effect on the labor market. Finding from its precursor in Massachusetts is certainly relevant, but caution needs to be exercised when predicting over a lot more heterogeneous set of states the likely consequences of a somewhat different policy regime. Future research using richer variation in the roll-out of ACA will undoubtedly further our understanding of insurance mandate and its effect on society at large. References [1] Abadie, A., Diamond, A., & Hainmueller, J. (2010). Synthetic control methods for comparative case studies: Estimating the effect of Californias tobacco control program. Journal of the American Statistical Association, 105(490). [2] Abadie, A., & Gardeazabal, J. (2003). The economic costs of conflict: A case study of the Basque Country. American economic review, [3] Abaluck, J., & Gruber, J. (2011). Choice Inconsistencies Among the Elderly: Evidence from Plan Choice in the Medicare Part D Program. The American Economic Review, 101(4), [4] Aizawa, N. (2015). Health Insurance Exchange Design in an Empirical Equilibrium Labor Market Model. manuscript, University of Minnesota. [5] Aizawa, N., & Fang, H. (2015). Equilibrium Labor Market Search and Health Insurance Reform, Second Version. [6] Aron-Dine, A., Einav, L., & Finkelstein, A. (2013). The RAND Health Insurance Experiment, Three Decades Later. The Journal of Economic Perspectives, 27(1), [7] Aron-Dine, A., Einav, L., Finkelstein, A., & Cullen, M. (2014). Moral Hazard in Health Insurance: Do Dynamic Incentives Matter?. Review of Economics and Statistics, (0). [8] Baicker, K., Finkelstein, A., Song, J., & Taubman, S. (2014). The Impact of Medicaid on Labor Market Activity and Program Participation: Evidence from the Oregon Health Insurance Experiment. American Economic Review, 104(5), [9] Baicker, K., Mullainathan, S., & Schwartzstein, J. (2015). Behavioral Hazard in Health Insurance. The Quarterly Journal of Economics (2015) 130 (4): [10] Baily, M. N. (1978). Some Aspects of Optimal Unemployment Insurance. Journal of Public Economics, 10(3), [11] Battistin, E., Brugiavini, A., Rettore, E., & Weber, G. (2009). The Retirement Consumption Puzzle: Evidence from a Regression Discontinuity Approach. The American Economic Review, 99(5), [12] Bertrand, M., Duflo, E., & Mullainathan, S. (2004). How Much Should We Trust Differences-in- Differences Estimates?. The Quarterly Journal of Economics, 119(1), [13] Blau, D. M., & Gilleskie, D. B. (2001). Retiree Health Insurance and the Labor Force Behavior of Older Men in the 1990s. Review of Economics and Statistics, 83(1),

50 [14] Blau, D. M., & Gilleskie, D. B. (2006). Health Insurance and Retirement of Married Couples. Journal of Applied Econometrics, 21(7), [15] Blau, D. M., & Gilleskie, D. B. (2008). The Role of Retiree Health Insurance in the Employment Behavior of Older Men. International Economic Review, 49(2), [16] Cameron, A. C., Gelbach, J. B., & Miller, D. L. (2008). Bootstrap-based improvements for inference with clustered errors. The Review of Economics and Statistics, 90(3), [17] Cameron, A. C., Gelbach, J. B., & Miller, D. L. (2011). Robust inference with multiway clustering. Journal of Business & Economic Statistics, 29(2). [18] Card, D., & Shore-Sheppard, L. D. (2004). Using discontinuous eligibility rules to identify the effects of the federal medicaid expansions on low-income children. Review of Economics and Statistics, 86(3), [19] Chetty, R. (2006a). A New Method of Estimating Risk Aversion. The American Economic Review, [20] Chetty, R. (2006b). A General Formula for the Optimal Level of Social Insurance. Journal of Public Economics, 90(10), [21] Chetty, R. (2009). Sufficient Statistics for Welfare Analysis: A Bridge Between Structural and Reduced-Form Methods. Annu. Rev. Econ., 1(1), [22] Chetty, R., & Saez, E. (2010). Optimal Taxation and Social Insurance with Endogenous Private Insurance. American Economic Journal. Economic Policy, 2(2), 85. [23] Cochrane, J. H. (1991). A Simple Test of Consumption Insurance. Journal of Political Economy, 99(5), [24] Conley, T. G., & Taber, C. R. (2011). Inference with difference in differences with a small number of policy changes. The Review of Economics and Statistics, 93(1), [25] Currie, J., & Gruber, J. (1996). Health Insurance Eligibility and Child Health: Lessons from Recent Expansions of the Medicaid Program. Quarterly Journal of Economics, 111(2), [26] Cutler, D. M., & Gruber, J. (1996). Does Public Insurance Crowd Out Private Insurance?. The Quarterly Journal of Economics, 111(2), [27] Dague, L., DeLeire, T., & Leininger, L. (2014). The Effect of Public Insurance Coverage for Childless Adults on Labor Supply (No. w20111). National Bureau of Economic Research. [28] Dey, M. S., & Flinn, C. J. (2005). An Equilibrium Model of Health Insurance Provision and Wage Determination. Econometrica, 73(2), [29] Dong, Y. (2015). Regression Discontinuity Applications with Rounding Errors in the Running Variable. Journal of Applied Econometrics, 30(3), [30] Dube, A., Lester, T. W., & Reich, M. (2010). Minimum Wage Effects across State Borders: Estimates Using Contiguous Counties. The review of economics and statistics, 92(4), [31] Einav, L., Finkelstein, A., & Cullen, M. R. (2010). Estimating Welfare in Insurance Markets Using Variation in Prices. The Quarterly Journal of Economics, 125(3), 877. [32] Einav, Liran, Finkelstein, A., & Schrimpf, P. (2010). Optimal Mandates and The Welfare Cost of Asymmetric Information: Evidence from The U.K. Annuity Market. Econometrica 78(3),

51 [33] Einav, L., Finkelstein, A., Ryan, S., Schrimpf, P., & Cullen, M. R. (2013). Selection on Moral Hazard in Health Insurance. The American economic review, 103(1), 178. [34] French, E., & Jones, J. B. (2011). The Effects of Health Insurance and SelfInsurance on Retirement Behavior. Econometrica, 79(3), [35] Garthwaite, C., Gross, T., & Notowidigdo, M. J. (2014). Public Health Insurance, Labor Supply, and Employment Lock. The Quarterly Journal of Economics, 129(2), [36] Gruber, J. (1997). The Consumption Smoothing Benefits of Unemployment Insurance. The American Economic Review, [37] Gruber, J. (2013). Evaluating the Massachusetts Health Care Reform. Health Services Research, 48(6pt1), [38] Gruber, J., & Madrian, B. C. (1994). Health Insurance and Job Mobility: The Effects of Public Policy on Job-Lock. Industrial and Labor Relations Review, 48(1), [39] Gruber, J., & Madrian, B. C. (1995). Health-Insurance Availability and the Retirement Decision. American Economic Review, 85(4), [40] Gruber, J., & Madrian, B. C. (1997). Employment Separation and Health Insurance Coverage. Journal of Public Economics, 66(3), [41] Gruber, J., & Madrian, B. C. (2004). Health Insurance, Labor Supply, and Job Mobility: A Critical Review of the Literature. Health Policy and the Uninsured, ed. Catherine G. McLaughlin, [42] Gruber, J., & Simon, K. (2008). Crowd-out 10 years later: Have recent public insurance expansions crowded out private health insurance?. Journal of health economics, 27(2), [43] Hackmann, M. B., Kolstad, J. T., & Kowalski, A. E. (2015). Adverse Selection and an Individual Mandate: When Theory Meets Practice. The American Economic Review, 105(3), [44] Handel, B. R. (2013). Adverse Selection and Inertia in Health Insurance Markets: When Nudging Hurts. American Economic Review, 103(7), [45] Handel, B. R., & Kolstad, J. T. (2013). Health Insurance for Humans : Information Frictions, Plan Choice, and Consumer Welfare. American Economic Review, 105(8), [46] Hartman, M., Martin, A. B., Lassman, D., & Catlin, A. (2015). National health spending in 2013: growth slows, remains in step with the overall economy. Health Affairs, 34(1), [47] Heim, B., & Lin, L. K. (2014). Does Health Reform Lead to an Increase in Early Retirement? Evidence from Massachusetts. Evidence from Massachusetts (August 19, 2014). [48] Inderbitzin, L., Staubli, S., & Zweimller, J. (2013). Extended unemployment benefits and early retirement: Program complementarity and program substitution. University of Zurich, Department of Economics, Working Paper, (119). [49] Kolstad, J. T., & Kowalski, A. E. (2012). Mandate-Based Health Reform and the Labor Market: Evidence from the Massachusetts Reform (No. w17933). National Bureau of Economic Research. [50] Madrian, B. C. (1994). Employment-Based Health Insurance and Job Mobility: Is there Evidence of Job-Lock?. The Quarterly Journal of Economics, 109(1), [51] Mahoney, N. (2015). Bankruptcy as Implicit Health Insurance. The American Economic Review, 105(2),

52 [52] Manning, W. G., Newhouse, J. P., Duan, N., Keeler, E. B., & Leibowitz, A. (1987). Health Insurance and the Demand for Medical Care: Evidence from a Randomized Experiment. The American Economic Review, 77(3), [53] Prescott, E. C., & Townsend, R. M. (1984a). General Competitive Analysis in an Economy with Private Information. International Economic Review, [54] Prescott, E. C., & Townsend, R. M. (1984b). Pareto Optima and Competitive Equilibria with Adverse Selection and Moral Hazard. Econometrica: Journal of the Econometric Society, [55] Rust, J., & Phelan, C. (1997). How Social Security and Medicare Affect Retirement Behavior in a World of Incomplete Markets. Econometrica: Journal of the Econometric Society, 65(4),