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Essays on public economics Yang, Tzu-Ting 2015

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Essays on Public EconomicsbyTzu-Ting YangB.A., National Taiwan University, 2005M.A., National Taiwan University, 2008A THESIS SUBMITTED IN PARTIAL FULFILLMENT OFTHE REQUIREMENTS FOR THE DEGREE OFDOCTOR OF PHILOSOPHYinThe Faculty of Graduate and Postdoctoral Studies(Economics)THE UNIVERSITY OF BRITISH COLUMBIA(Vancouver)April 2015© Tzu-Ting Yang 2015AbstractThis dissertation applies various program evaluation techniques to examineboth the intended and unintended consequences of government spending andregulation that affect family labor supply, children’s healthcare utilization,and household saving behavior. Chapter 2 of this dissertation exploits thelarge and anticipated cash influx in the first quarter of the calendar yearinduced by the Earned Income Tax Credit (EITC) to estimate the causaleffect of the receipt of a cash transfer on the timing of family labor supply.I find that income seasonality caused by EITC receipt induces changes inthe intra-year labor supply patterns of married women. In contrast, thereceipt of the EITC does not affect the timing of the labor supply of marriedmen and single women. The subgroup analysis implies that my results aremainly driven by those from liquidity-constrained families and those who aresecondary earners within their families. Chapter 3 exploits a sharp increasein patient cost-sharing at age 3 in Taiwan that results from young children“aging out” of the cost-sharing subsidy to examine the causal effect of costsharing on the demand for young children’s healthcare. It shows that theincrease in the level of patient cost sharing at the 3rd birthday significantlyreduces utilization of outpatient care. However, the utilization of inpatientcare for young children does not respond to a change in cost sharing at the3rd birthday. Chapter 4 exploits workplace pension reform in Taiwan toestimate the casual effect of workplace pension provision on the householdsaving rate. It shows that pension reform significantly reduces the prime-age(20–50) household saving rate by between 2.06 percentage points and implythat the degree of substitutability between workplace pensions and savingis about −0.50 to −0.60.iiPrefaceChapter 3 uses data from Taiwan’s National Health Insurance ResearchDatabase (NHIRD). Ethics approval under the project title Patient Cost-Sharing and Health Care Utilization in Early Childhood: Evidence froma Regression Discontinuity Design was obtained through the BehaviouralResearch Ethics Board of the University of British Columbia (H14-00869).Chapter 3 Patient Cost-Sharing and Health Care Utilization in EarlyChildhood: Evidence from a Regression Discontinuity Design of this dis-sertation is a joint work with Hsing-Wen Han and Hsien-Ming Lien. Dr.Hsing-Wen Han is an Associate Professor from the Department of Account-ing at the Tamkang University. Dr. Hsien-Ming Lien is a Professsor fromthe Department of Public Finance at the National Chengchi University. Iwas highly involved throughout every stage of the research: collecting andpreparing data, designing empirical models, carrying out estimation, orga-nizing and presenting results, writing and editing the manuscript.iiiTable of ContentsAbstract . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . iiPreface . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . iiiTable of Contents . . . . . . . . . . . . . . . . . . . . . . . . . . . . ivList of Tables . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . viiList of Figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . ixAcknowledgements . . . . . . . . . . . . . . . . . . . . . . . . . . . xiDedication . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . xiii1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 12 Family Labor Supply and the Timing of Cash Transfers:Evidence from the Earned Income Tax Credit . . . . . . . 42.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . 42.2 Background on The Earned Income Tax Credit . . . . . . . . 112.3 Data and Sample . . . . . . . . . . . . . . . . . . . . . . . . 142.3.1 Data . . . . . . . . . . . . . . . . . . . . . . . . . . . 142.3.2 Imputed EITC Payment . . . . . . . . . . . . . . . . 152.3.3 Sample . . . . . . . . . . . . . . . . . . . . . . . . . . 162.4 Identification Strategy . . . . . . . . . . . . . . . . . . . . . . 182.4.1 Triple Differences Estimation . . . . . . . . . . . . . . 192.4.2 Event Study Analysis . . . . . . . . . . . . . . . . . . 232.4.3 Individual Variation in Predicted EITC Payments . . 24ivTable of Contents2.5 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 262.5.1 Triple Differences Estimates . . . . . . . . . . . . . . 262.5.2 Event Study Analysis . . . . . . . . . . . . . . . . . . 272.5.3 Results from Individual Variation in EITC Payments 272.5.4 Robustness Checks . . . . . . . . . . . . . . . . . . . 282.5.5 Discussion: Magnitude of the Estimates . . . . . . . . 302.5.6 Mechanisms behind the Findings . . . . . . . . . . . . 312.6 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . 392.7 Figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 412.8 Tables . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 503 Patient Cost-Sharing and Healthcare Utilization in EarlyChildhood: Evidence from a Regression Discontinuity De-sign . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 593.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . 593.2 Policy Background . . . . . . . . . . . . . . . . . . . . . . . . 663.2.1 National Health Insurance in Taiwan . . . . . . . . . 663.2.2 Patient Cost-Sharing . . . . . . . . . . . . . . . . . . 673.2.3 Change in Patient Cost Sharing at the 3rd Birthday . 703.3 Data and Sample . . . . . . . . . . . . . . . . . . . . . . . . 723.3.1 Data . . . . . . . . . . . . . . . . . . . . . . . . . . . 723.3.2 Sample . . . . . . . . . . . . . . . . . . . . . . . . . . 733.4 Empirical Specification . . . . . . . . . . . . . . . . . . . . . 743.5 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 773.5.1 Outpatient Visits and Expenditure . . . . . . . . . . 773.5.2 Inpatient Admissions and Expenditures . . . . . . . . 863.6 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . 883.7 Figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 903.8 Tables . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 964 The Effect of Workplace Pensions on Household Saving: Ev-idence from a Natural Experiment in Taiwan . . . . . . . . 1044.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . 104vTable of Contents4.2 Policy Background . . . . . . . . . . . . . . . . . . . . . . . . 1084.3 Data and Sample . . . . . . . . . . . . . . . . . . . . . . . . 1114.3.1 Data . . . . . . . . . . . . . . . . . . . . . . . . . . . 1114.3.2 Sample . . . . . . . . . . . . . . . . . . . . . . . . . . 1114.4 Empirical Specification . . . . . . . . . . . . . . . . . . . . . 1134.5 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1174.5.1 Summary Statistics . . . . . . . . . . . . . . . . . . . 1174.5.2 Main Results . . . . . . . . . . . . . . . . . . . . . . . 1184.5.3 Falsification Tests . . . . . . . . . . . . . . . . . . . . 1204.5.4 Magnitude of Estimates . . . . . . . . . . . . . . . . . 1214.6 Specification Checks . . . . . . . . . . . . . . . . . . . . . . . 1224.6.1 Different Methods of Statistical Inference . . . . . . . 1224.6.2 Different Definition of Saving Rate . . . . . . . . . . 1234.6.3 Different Definitions of Treatment and ControlGroups . . . . . . . . . . . . . . . . . . . . . . . . . . 1244.6.4 Different Sample Periods . . . . . . . . . . . . . . . . 1244.6.5 Controlling Household Earned Income . . . . . . . . . 1244.7 Impact Across the Saving Rate Distribution . . . . . . . . . 1254.7.1 Quantile Differences-in-Differences Estimation . . . . 1254.8 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1274.9 Figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1294.10 Tables . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 130Bibliography . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 136AppendicesA Appendix to Chapter 2 . . . . . . . . . . . . . . . . . . . . . . 150A.1 Appendix Figures . . . . . . . . . . . . . . . . . . . . . . . . 150B Appendix to Chapter 3 . . . . . . . . . . . . . . . . . . . . . . 154B.1 Appendix Tables . . . . . . . . . . . . . . . . . . . . . . . . . 154viList of Tables2.1 Share of Annual EITC Disbursements by Month . . . . . . . 502.2 Sample Selection: Summary Statistics . . . . . . . . . . . . . 512.3 Treatment and Comparison Groups: Summary Statistics . . . 522.4 Triple Differences Estimates . . . . . . . . . . . . . . . . . . . 532.5 Estimates from Individual Variation in EITC Payments . . . 542.6 Robustness Checks . . . . . . . . . . . . . . . . . . . . . . . . 552.7 Subgroup Analysis Based on Tendency toward Being Liquid-ity Constrained (Married Women) . . . . . . . . . . . . . . . 562.8 Secondary Earner Channel v.s. Gender Difference Channel . 572.9 Month-to-Month Labor Force Transitions (Married Women) . 583.1 Patient Cost-Sharing in Taiwan NHI . . . . . . . . . . . . . . 963.2 Weighted Average Out-of-Pocket Cost per Visit/Admission . 973.3 Selected Characteristics at Age Three before and after SampleSelection . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 973.4 Descriptive Statistics . . . . . . . . . . . . . . . . . . . . . . . 983.5 Descriptive Statistics: By Healthcare Provider . . . . . . . . . 993.6 RD Estimates on Outpatient Care at Age 3 . . . . . . . . . . 1003.7 RD Estimates on Outpatient Care at Age 3: By Choice ofProviders . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1013.8 RD Estimates on Outpatient Care at Age 3: By Diagnoses,Birth Order, Gender, and Household Income . . . . . . . . . 1023.9 RD Estimates on Inpatient Care at Age 3 . . . . . . . . . . . 1034.1 Comparison Between New and Old Pension Systems . . . . . 1304.2 Descriptive Statistics . . . . . . . . . . . . . . . . . . . . . . . 131viiList of Tables4.2 Descriptive Statistics . . . . . . . . . . . . . . . . . . . . . . . 1324.3 The Effect of Mandatory Private Pension on Household Vol-untory Saving . . . . . . . . . . . . . . . . . . . . . . . . . . . 1334.4 Empirical Specification Checks . . . . . . . . . . . . . . . . . 1344.5 Quantile DD Results . . . . . . . . . . . . . . . . . . . . . . . 135B.1 Placebo Test for Other Age Cutoff . . . . . . . . . . . . . . . 155B.2 Sensitivity to Bandwidth and Polynomial Selection in Para-metric RD Regressions . . . . . . . . . . . . . . . . . . . . . . 156B.3 Sensitivity to Bandwidth Selector and Kernel Function Selec-tion in Nonparametric RD Regressions . . . . . . . . . . . . . 157B.4 Donut RD for Outpatient Expenditure and Visits . . . . . . . 158viiiList of Figures2.1 Real Federal Spending on EITC and TANF: 1975–2011 . . . 412.2 EITC schedule (Tax Year 2007) . . . . . . . . . . . . . . . . . 422.3 Share of Annual EITC Disbursements by Month . . . . . . . 432.4 EITC Amount by Treatment Status and Family Type . . . . 442.5 The Impact of EITC on Intra-Year Labor Supply Patterns:Married Women . . . . . . . . . . . . . . . . . . . . . . . . . . 452.6 The Impact of EITC on Intra-Year Labor Supply Patterns:Married Men . . . . . . . . . . . . . . . . . . . . . . . . . . . 462.7 The Impact of EITC on Intra-Year Labor Supply Patterns:Single Women . . . . . . . . . . . . . . . . . . . . . . . . . . . 472.8 Weekly Disbursement Patterns of Income Tax Refunds . . . . 482.9 Month-to-Month Labor Force Transitions . . . . . . . . . . . 493.1 Age Profile of Out-of-Pocket Costs . . . . . . . . . . . . . . . 903.2 Age Profile of Outpatient Expenditure and Visits . . . . . . . 913.3 Age Profile of Outpatient Visits per 10,000 Person-Years byType of Provider . . . . . . . . . . . . . . . . . . . . . . . . . 923.4 Age Profile of Outpatient Expenditure per 10,000 Person-Years (NTD) by Type of Provider . . . . . . . . . . . . . . . 933.5 Age Profile of Outpatient Visits per 10,000 Person-Years byDiagnosis . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 943.6 Age Profile of Inpatient Expenditure and Visits . . . . . . . . 954.1 Workplace Pension Coverage in Private Sector: 2002–2007 . . 129ixList of FiguresA.1 The Impact of EITC on Intra-Year Labor Supply Pattern(including Pre-Trend): Married Women . . . . . . . . . . . . 151A.2 The Impact of EITC on Intra-Year Labor Supply Pattern(including Pre-Trend): Married Men . . . . . . . . . . . . . . 152A.3 The Impact of EITC on Intra-Year Labor Supply Pattern(including Pre-Trend): Single Women . . . . . . . . . . . . . 153xAcknowledgementsI am extremely grateful to my supervisors Joshua Gottlieb and Kevin Mil-ligan for their countless hours of advice and supervision. Their sharp sensein economics and strict academic standard greatly improved my work. Inaddition, both of them were generous in their time and gave me timely helpthroughout the job market “year”. Without them, I would not have beenable to get my dream job. I would also like to thank my dissertation commit-tee members Thomas Lemieux and Marit Rehavi for their insightful sugges-tions and much encouragement. I thank my university (external) examiners:Mukesh Eswaran, Thomas Davidoff, and Ted McDonald for carefully read-ing my thesis and making useful comment. I also benefited greatly fromtalking to many VSE faculty members Patrick Francois, Matilde Bombar-dini, Nicole Fortin, David Green, Florian Hoffmann, Amartya Lahiri, CraigRiddell, and Giovanni Gallipoli. I also thank my coauthors: Hsien-MingLien and Hsing-Wen Han for their help and support. I am also indebtedto Maureen Chin for her invaluable help in dealing with the administrativework throughout the program, especially during the job market.I want to thank my outstanding colleagues and friends at UBC, Alexan-dre Corhay, Francis Michaud, Zhengfei Yu, Zhe Chen, Yawen Liang, BipashaMaity, Guidon Fenig, Hugo Jales, Nathan Canen, and Sharon Hu for theirsupport. I thank my colleagues in the public finance reading group, AlixDuhaime-Ross, Oscar Becerra, Timea Laura Molnar, Daniel Shack, and LoriTimmins, for their generous feedback and insightful discussion in the lasttwo years of the program.I benefited greatly from sharing the daily life with residents of St John’sCollege (SJC) at dining time. Many of them have become my lifetimefriends. I also want to thank my friends at Taiwanese Graduate StudentxiAcknowledgementsAssociation in Vancouver (TGSA). Joining TGSA activities greatly curesmy homesick.I also wish to acknowledge classmates and faculty members at the Na-tional Taiwan University, particularly Ming-Ching Luoh, who encouragedme to study abroad.Finally, I would like to express my deepest gratitude to my parents, to mybrother and to Yi-Ling Lin for their unconditional support, encouragementand love.xiiDedication獻給親愛的父母, 弟弟與妻子For my parents, brother, and wifexiiiChapter 1IntroductionThis dissertation applies various program evaluation techniques to examineboth the intended and unintended consequences of government spending andregulation that affect family labor supply, children’s healthcare utilization,and household saving behavior.Dissertation OutlineThe second chapter, “Family Labor Supply and the Timing of Cash Trans-fers: Evidence from the Earned Income Tax Credit” provides new evidenceon how families adjust their labor supply in response to the receipt of ananticipated cash transfer. In particular, I exploit the unique disbursementtiming and benefit rules of the Earned Income Tax Credit (EITC) to assessthe effect of the receipt of a cash transfer on the timing of family labor sup-ply. My results show that income seasonality caused by EITC receipt leadsto changes in the intra-year labor supply patterns of married women. Onaverage, receiving a $1,000 EITC payment significantly reduces the propor-tion of married women who work, by 1.6 percentage points, in the monthin which the EITC is received. The income elasticity of labor supply formarried women based on this estimate is around −0.06. In contrast, thereceipt of the EITC does not affect the timing of the labor supply of mar-ried men and single women. The subgroup analysis suggests families mightreduce the labor supply of secondary earners in response to receiving ananticipated EITC payment. In addition, My results suggest that the pres-ence of liquidity constraints and myopia could be important reasons for myfindings.Healthcare for young children is highly subsidized in many public health1Dissertation Outlineinsurance programs around the world. However, the existing literaturelacks evidence on how the demand for young children’s healthcare reactsto these medical subsidy policies. The third chapter “Patient Cost-Sharingand Healthcare Utilization in Early Childhood: Evidence from a RegressionDiscontinuity Design” (joint with Hsing-Wen Han and Hsien-Ming Lien)exploits a sharp increase in patient cost sharing — the share of healthcarecosts the patient must pay out of their own pocket — at age 3 in Taiwan,resulting from young children “aging out” of the cost-sharing subsidy. Thisprice shock on the 3rd birthday allows us to use a regression discontinuitydesign to examine the causal effect of cost sharing on the demand for youngchildren’s healthcare by comparing the utilization of healthcare for youngchildren right before and right after their 3rd birthday. Our results showthat the increase in the level of patient cost sharing at the 3rd birthday sig-nificantly reduces total outpatient expenditure. The implied price elasticityof outpatient expenditure is around −0.10. However, the demand for inpa-tient care for young children does not respond to a change in cost sharing atthe 3rd birthday even though the price variation is much larger. This resultimplies that providing full insurance coverage for children’s inpatient carecan substantially reduce the financial risk for the households but does notinduce excessive utilization of inpatient care.Population aging causes financial imbalance in pay-as-you-go public pen-sion programs. To remedy this problem but also ensure the adequacy ofretirement savings for employees, many countries complement or substitutefor public pensions by regulating workplace pensions. The fourth chapter“The Effect of Workplace Pensions on Household Saving: Evidence froma Natural Experiment in Taiwan” is the first to utilize a national pensionpolicy change as a natural experiment to identify the impact of employer-sponsored pensions on voluntary household saving. Specifically, I evaluatethe response in household saving to a workplace pension reform in Taiwanthat has mandated, since 2005, that all private-sector employers contributeat least 6% of wages to employees’ individual pension accounts monthly.I use the workers in the unaffected sector as a comparison group and em-ploy a difference-in-differences method to estimate the impact of the reform2Dissertation Outlineon the household saving rate. My estimates suggest that making privatepensions mandatory significantly reduces the prime-age (20–50) householdsaving rate by between 2.06 and 2.45 percentage points and imply that thedegree of substitutability between workplace pensions and saving is about−0.50 to −0.60. Since workplace pensions only partially offset householdsaving, a mandatory workplace pension policy could effectively raise em-ployees’ retirement wealth.3Chapter 2Family Labor Supply and theTiming of Cash Transfers:Evidence from the EarnedIncome Tax Credit2.1 IntroductionDo households adjust their behavior in response to receiving expected in-come payments? This question is crucial to understanding households’ be-havior and analyzing aspects of government policies. For example, the an-swer to this question has important implications for the design of welfareprograms, especially for determining the payment frequency of welfare ben-efits. If the benefit recipient’s behavior is sensitive to the receipt of income,then more frequent payments could improve policy by helping recipientsto smooth out their consumption. On the other hand, the effectiveness ofshort-run fiscal policies, such as temporary rebates during a recession, largelydepends on how people adjust their behavior after receiving payments. Thecentral implication of the life cycle model with a perfect credit market isthat consumption behavior should not respond to predictable changes in in-come. A growing empirical literature tests this claim by examining whetherthe timing of the receipt of income is associated with the timing of house-hold spending. Most prior studies find that families increase their spendingright after they receive expected income payments, such as a public pension(Stephens, 2003; Stephens and Unayama, 2011), temporary rebate42.1. Introduction(Johnson et al., 2006, 2013; Parker, 2014) or income tax refund (Souleles,1999). These findings generally offer evidence against the theory.1This paper deviates from the previous studies by considering an econom-ically important but seldom addressed question — Do families change theirlabor supply in response to the receipt of an anticipated cash transfer?2Empirically investigating the labor supply response has important implica-tions for both economic theory and public policy. On the theoretical side,such investigation examines one central prediction of the life cycle model oflabor supply: Any anticipated income changes should not affect labor sup-ply behavior. When families are informed of a future income change, theycan adjust their labor supply (i.e. leisure consumption) in advance throughborrowing and saving. Thus, there should be no change in labor supplyat the time when the income change is experienced. Several recent studies(e.g. Saez, 2003; Looney and Singhal, 2006) use this prediction to assumeaway income effects associated with anticipated changes in tax rates whenestimating the intertemporal substitution elasticity of labor supply. How-ever, its validity is questionable given the vast evidence on the householdspending response to predictable changes in income. Regarding policy, suchinvestigation helps us better understand how the timing of welfare bene-1Johnson et al. (2013) exploit the random timing of the receipt of tax rebates (i.e. USeconomic stimulus payments) to examine the spending response to the receipt of income.They find that households spend 60% of the tax rebate within three months of receivingit. Stephens and Unayama (2011) use the Japanese public pension which is distributedevery three months; they find that household spending closely follows the disbursementpatterns of the public pension benefit. Stephens (2003) finds that households spend moreon weekly nondurable consumption upon receiving the monthly US Social Security check.Souleles (1999) provides evidence that households in the US spend around 30% to 60%of an income tax refund within one quarter of receiving it. However, not all tests ofthe life cycle model that examine the spending response to the receipt of income findevidence contradicting consumption-smoothing behavior. Hsieh (2003) utilizes Alaska’sannual oil revenue dividend payment, which is equal to two-thirds of the monthly pre-taxhousehold income. He finds that Alaskan households do not change their spending whenthey receive this payment. Paxson (1993) finds that Thai households can smooth out theirspending over a striking degree of variation in seasonal income. Jappelli and Pistaferri(2010) provide an excellent review of this strand of the literature.2Previous studies examining the validity of the life cycle model usually abstract fromthe labor supply decision and implicitly assume that saving and borrowing are the onlyways to smooth out household spending.52.1. Introductionfit payments affects household behavior. Past policy debates have mainlyfocused on the impact of the timing on household spending. My resultswill show that the timing of cash transfers also matters for the family laborsupply decision.I investigate the above issue by assessing the immediate labor supply re-sponse to the receipt of the Earned Income Tax Credit (EITC), a refundabletax credit that subsidizes the earnings of the working poor.3 The EITC isthe largest cash transfer program for low-income families in the US.4 Thereare two features of the EITC that make it an interesting case to study theissue I want to address. First, it is widely known and highly anticipatedby the recipients. Previous studies suggest that most EITC recipients knowwhat their EITC refund will be before filing their taxes (Chetty and Saez,2013; Romich and Weisner, 2000).Second, the EITC could be the single largest cash transfer that many ofthe working poor will receive during the year. The payment is fairly largerelative to the recipients’ family income.5 The average amount of EITC foreligible families is around $2,000 and can account for one month of familyincome.6 For some families, it can comprise as much as 45% of their annualincome. In addition, most EITC recipients receive their credit in the formof a one-time lump-sum payment within a narrow time frame.7 Figure 2.33The EITC is fully refundable. That is, any excess credit beyond a family’s incometax liability will be paid in the form of a tax refund. Over 90% of the value of the EITCis delivered in the form of tax refunds, as opposed to serving to reduce tax liabilities(McGranahan and Schanzenbach, 2014).4The structure of the US welfare system has undergone a substantial change in thepast three decades. The federal income tax system has become a major policy tool forproviding cash assistance to low-income families with children (Eissa and Hoynes, 2011).The expansion of the EITC accounts for most of this dramatic transformation. In 2011,the federal government spent $61 billion on the EITC, substantially more than the $27.1billion spent on Temporary Assistance for Needy Families (TANF), the flagship cashtransfer program in the US, while the two programs were of a similar size in 1994 (seeFigure 2.1).5The amount of the EITC largely depends on the family’s income, the number ofchildren, and the marital status of the taxpayer in the previous year. I will discuss theEITC benefit rules in detail in Section 2.2.6This number is based on the EITC payment schedule during my sample period (1997–2012).7Recipients formerly had the option of receiving installments of their expected credit62.1. Introductionshows that over half of EITCs are paid in the month of February.8 Thisconcentrated delivery of cash transfers induces a large variation in families’disposable income across 12 months.9 I use it to examine how family laborsupply reacts to the receipt of anticipated cash transfers by providing thefirst evidence on how the EITC payment timing affects the timing of thefamily labor supply.10Since most EITC recipients are low-income families with children, theprimary concern over relying on variation in payment timing is that myestimates may simply reveal the intra-year labor supply patterns of specificdemographic groups, such as those with low incomes or those who havechildren, rather than reflecting the impact of receiving the EITC payment.I deal with this concern in two ways.First, I conduct triple differences estimations by using a comparisongroup of individuals, such as those with children but with incomes justabove the EITC range or those without children but incomes within theEITC range, who are similar to those in the treatment group in many waysbut receive much smaller EITC payments to control any confounding effectsunrelated to the receipt of the EITC. Note that membership in the treat-on a monthly basis in the calendar year prior to tax filing (Advance EITC). This advancepayment option has been unavailable since 2011 due to a very low take-up rate. I willdiscuss this issue in Section 2.2.8This is because recipients need to file their taxes first and will then obtain their refunda few weeks later. The US government usually opens the tax window in the middle ofJanuary and low-income taxpayers tend to file their taxes early, meaning that most taxrefunds for low-income families are issued in February.9Previous studies find strong evidence that the timing of the household spending ofEITC recipients is closely related to the timing of the EITC arrival. EITC recipientstend to increase their household spending, especially on durable goods (Barrow and Mc-Granahan, 2001; Adams et al., 2009), consume more healthy food (McGranahan andSchanzenbach, 2014) and use more healthcare services (Hoynes et al., 2014; Niedzwiecki,2013) in the February when they receive the credit.10One recent paper finds that the tax refund provides liquidity for EITC-eligible joblosers at the beginning of their unemployment spell (LaLumia, 2013). The author exploitsthe timing of the EITC refund to examine whether the unemployment duration (i.e. jobsearch intensity) of EITC recipients is sensitive to the provision of a lump-sum transferat the beginning of their unemployment spell and then estimates the liquidity effect ofunemployment insurance. She finds that EITC recipients who become unemployed inFebruary have longer unemployment duration than those entering unemployment in othermonths of the year.72.1. Introductionment group is based on family characteristics in the previous year. It ispredetermined and cannot change during the year. My results show thatthe receipt of EITC causes the labor supply of married women to show asharp drop in February and a substantial decline in January, March andApril. This pattern is largely coincident with the payment timing of theEITC. In contrast, the receipt of the EITC has little impact on the timingof labor supply for married men and single women.Second, I restrict my sample to those receiving EITC payments and uti-lize the variation in the amount they receive in a given month, which ispredetermined by the time the labor supply decision is made, so as to quan-tify the impact of the EITC receipt on recipients’ monthly labor supply.My estimates indicate that receiving a $1,000 EITC payment significantlyreduces a married woman’s likelihood of working, by 1.6 percentage points,in the month of the EITC arrival, from a base of 47%.11 The income elas-ticity of labor supply for married women based on this estimate is around−0.06, which lies between the estimates in the previous studies (Blau andKahn, 2007; Heim, 2007). In line with the results from the triple differencesestimation, I do not find any statistically detectable effect of receiving a$1,000 EITC payment on the probability of working for either married menor single women.I conduct several subgroup analyses to explore possible causes of myresults. First, I investigate why there are very different labor supply re-sponses to the receipt of EITC across married women, married men andsingle women. The subgroup analysis reveals such patterns to be due tothe fact that the majority of married women are secondary earners in theirfamilies and not to gender differences in labor supply patterns among EITCrecipients.12 I find that married women who are secondary earners signif-icantly reduce their labor supply in response to the receipt of EITC butthose who are primary earners do not. Interestingly, a similar pattern also11I use the likelihood of working in October, a month in which little of the EITC isdisbursed, to represent the baseline mean for the treatment group.12The definition of a secondary earner is an individual who earned less income than herspouse in the previous year. Single women are primary earners.82.1. Introductionemerges in the sample of married men. These results suggest that familiesmight adjust the labor supply of secondary earners in response to receivingan anticipated EITC payment. This result is consistent with findings inprevious studies (Cullen and Gruber, 2000; Kohara, 2010) suggesting thatthe labor force participation of secondary earners is sensitive to changes infamily resources.13Next, I analyze why the family labor supply changes at the time ofreceipt of the anticipated EITC payment. My results suggest that it couldbe due to the presence of liquidity constraints and myopia among EITC-eligible families. The presence of liquidity constraints forces families tokeep their labor supply high so as to maintain liquidity until receiving theEITC payment. Following previous studies, I conduct subgroup analysis bysplitting the sample into those who are liquidity constrained and those whoare less constrained. I find that married women from constrained families,such as families with low liquid assets or high mortgage-to-income ratios,exhibit a significantly negative labor supply response to the receipt of theEITC but those from less constrained families do not. However, liquidityconstraints cannot fully explain why the receipt of the EITC causes marriedwomen to reduce their labor supply temporarily in February rather thansmoothing out their labor supply in the months following the receipt ofthe cash. The observed pattern reveals that recipients could be somewhatmyopic in planning for their future consumption.Finally, I exploit month-to-month labor force transitions so as to under-stand the main cause of married women’s decreased likelihood of workingin February (relative to other months). Although the estimates are notprecise, my results provide suggestive evidence that married women couldtemporarily leave their jobs without pay upon receiving the EITC refund inFebruary.This paper contributes to the existing literature in two ways. First,13These phenomena have been addressed in field work. A respondent in Smeeding et al.(2000) vividly described her working status before receiving the EITC refund. As theauthors explain: “She can pay off all her [back] bills, be caught up with all her bills andnot feel stressed..... All she has to do is keep working until December. Then in Januaryshe can turn in her tax form so she can get that money.”92.1. Introductionit examines the labor supply response to the receipt of an anticipated cashtransfer, which is largely unexplored in prior studies. Only two recent studieshave studied the response of labor supply to an anticipated income changeinduced by cash transfers, both in developing countries where people havedifficulty accessing credit. Edmonds (2006) finds that the timing of theanticipated public pension in South Africa is associated with the timingof child employment. Receipt of the pension reduces child labor supplyand increases children’s enrolment in school. Fernandez and Saldarriaga(2014) utilize exogenous variation in the time between the payment date ofthe conditional transfer program and the interview date of the householdsurvey to find evidence of women’s working hours in Peru declining uponreceipt of a cash transfer. Due to data limitations, neither paper is able toconduct rigorous empirical investigations into the possible causes of theirresults. I use detailed asset and debt information in my data to investigatethe mechanisms behind my findings. In addition, the present paper providesthe first evidence on the causal effect of the receipt of a cash transfer on thetiming of family labor supply in the context of a developed country.Second, this paper represents the first attempt to analyze the short-run(i.e. intra-year) effects of the EITC on the labor supply. Since the EITCis a tax credit that subsidizes the earnings of low-income families, previousstudies mainly focus on how a change in the level of the EITC paymentaffects the level of family labor supply.14 They exploit various expansions ofthe EITC, which boosted the level of the EITC payment for eligible familiesbetween the mid-1980s and the mid-1990s, to evaluate the labor supplyeffect of the EITC. They find that EITC expansion resulted in an increasein the employment rate of single women(Eissa and Liebman, 1996; Meyer,2010; Meyer and Rosenbaum, 2001) and a decline in the employment rateof married women (Eissa and Hoynes, 2004).15 The present paper does not14Theoretically, it should have both a substitution effect and an income effect on laborsupply. The substitution effect comes about as a result of the EITC altering the family’slabor supply decision by changing the marginal tax rate on earnings. The income effectresults from the tax credit increasing the family’s resources and leading individuals todecrease their labor supply (consume more leisure).15Hotz and Scholz (2003) offer a literature review on behavioral responses to the EITC.102.2. Background on The Earned Income Tax Creditexamine a change in the level of the annual EITC payment or labor supply.Rather, it focuses on whether the timing of EITC receipt affects the timing offamily labor supply within any given year, keeping the annual EITC amountconstant. My results clearly show that the timing of the disbursement ofthe EITC matters for the labor supply decision of married women.The paper proceeds as follows. Section 2.2 briefly describes relevant fea-tures of the EITC. Section 2.3 discusses the data and sample selection pro-cess. Section 2.4 proposes the identification strategies. Section 2.5 presentsmy main results and robustness checks, and discusses possible mechanismsbehind my findings. Section 2.6 concludes.2.2 Background on The Earned Income TaxCreditThe EITC is a refundable tax credit for low-income working people, partic-ularly those with children, in the US. In 1975, the EITC began as a smallprogram but it has since grown into one of the largest anti-poverty pro-grams in the US. In 2012, the US federal government spent $61 billion onthe EITC, supporting more than 28 million families.A taxpayer’s eligibility for the EITC relies largely on her family’s earnedincome (or adjusted gross income), number of qualifying children, and fil-ing status during the tax year (i.e. previous year).16 First, as the EITCis a policy tool aimed at encouraging the poor to work, a taxpayer musthave positive earned income, defined as the sum of wage income and self-employment income. The final EITC payment depends on the minimumamount of credits based on either earned income or adjusted gross income(AGI).17 Second, as with other means-tested transfer programs, a taxpayer’sEissa and Hoynes (2006) provide a review focused particularly on the EITC’s impact onlabor supply.16According to the Internal Revenue Service, “A tax year is an annual accounting periodfor keeping records and reporting income and expenses.” Thus, a tax year usually refersto the previous year. From here on, I will use tax year and previous year interchangeably.There are three filing statuses: joint filing, single, and head of household. The first is fora married couple and the last two are for unmarried people.17AGI is a taxpayer’s total income from all sources, excluding non-taxable income such112.2. Background on The Earned Income Tax CreditAGI and earned income have to be below a particular income cutoff, whichdepends on the number of qualifying children and filing status. Third, a tax-payer with one or more qualifying child is eligible for a much larger amountof credit. Qualifying children must be under the age of 19 years, or 24 yearsif studying full-time, and must live with the taxpayer for at least half of theyear. A small amount of credit is provided to childless taxpayers.Figure 2.2 displays the EITC schedule for taxpayers with and withoutchildren.18 The payment level is quite stable during my sample period of1997 to 2012.19 The EITC schedule consists of three regions: the phase-inregion, where the tax credit increases at a given rate as earned income (orAGI) rises, the plateau region, where the tax credit stays constant at themaximum amount, and the phase-out region, where the tax credit declinesat a specific rate for each extra dollar of income. The phase-in and phase-outrates depend on the number of qualifying children. For example, the phase-in rate for a taxpayer with one child is 0.34, so that one extra dollar of incomewould raise the EITC refund by 34 cents. The credit stops rising when itreaches the maximum amount and then stays unchanged until income hitsthe phase-out threshold. The credit will then start to phase out at the rate of16 cents per dollar until it disappears entirely. Since 2002, married couples(i.e. married and filing jointly) have had a larger income threshold underwhich the maximum amount of credit can be given, which means that moretax credit is offered to married couples than to singles. In sum, there is alot of heterogeneity in the amounts of credit paid to EITC recipients. Fora taxpayer with two or more children, the maximum credit can account for40% of family annual income. However, the maximum credit for a childlessas welfare benefits, minus any adjustments to income. The adjustments could be movingexpenses, alimony paid, health savings account deductions, and so on.18This is the EITC payment schedule for year 2007.19In each year, the EITC payment is adjusted for inflation. The program was still beingexpanded somewhat during this period. For example, during from 2010 to 2013, as part ofthe American Recovery and Reinvestment Act, the EITC was temporarily expanded forfamilies with three or more children. Therefore, the phase-in rate for families with threeor more children became 45% of income (up from 40%). This change effectively raisedthe maximum credit for these families by around $600. The act also increased the incomethreshold at which credit begins to phase out for married couples to $5,000.122.2. Background on The Earned Income Tax Credittaxpayer only accounts for 5% of family annual income.EITC payments usually arrive in the first quarter of the calendar year,mostly in February. This is because the EITC is part of the annual taxrefund; EITC recipients receive their refunds in the first few weeks after filingtheir taxes, and the Internal Revenue Service (IRS) usually opens the filingwindow in mid-January.20 This disbursement pattern is very different fromthose of other transfer programs and overpayment refunds, which tend to bedistributed evenly over the calendar year.21 Table 2.1 documents the shareof total EITC disbursements that occur in each month, averaged across theyears 1997 to 2012, based on various issues of Monthly Treasury Statements(MTS).22 In each year, over 80% of EITC payments are disbursed betweenJanuary and March. On average, the share of payments made in Februaryis 56% and that in March is 22%.Recipients could, during my sample period, obtain their payments evenearlier than the MTS data show by using Refund Anticipation Loan (RALs),for which users were charged a very high fee (i.e. implicit interest rate) forthe expedition of the receipt of their benefits. The service allowed a taxpayerto receive their refund immediately upon filing their tax return. Wu (2012)shows that around 18% of EITC recipients receive their tax refunds earlyvia RALs. Moreover, according to McGranahan and Schanzenbach (2014),around 10% of EITC benefits were used to reduce the recipient’s tax liability,and presumably such credits are received when the tax was paid. Takentogether, these aspects imply that a substantial number of EITC recipientsmay have obtained their credits in January.It was not necessary for a recipient to receive the EITC in the form ofa one-time lump-sum payment during most of my sample period. Prior to20In 2011, the window opened on January 14th.21Other transfer programmes, such as Supplemental Security Income, Food Stamps,and Temporary Assistance to Needy Families, send the benefits out monthly. Individualincome tax refunds are distributed evenly over March to May (Barrow and McGranahan,2001).22These are published by the Treasury Department’s Financial Management Service.The information is available at http://www.fms.treas.gov/mts/backissues.html. Asthe IRS did not provide disbursement information in 1997, I used the 1998 distribution ofdisbursements to impute it.132.3. Data and Sample2011, a recipient had the option of using “Advance EITC” to get back aportion of their expected credit each month over the calendar year prior tofiling their taxes. However, this option was not the default and involvedsubmitting paperwork to one’s employer.23 According to previous estimates(GAO, 1992), the take-up rate of Advance EITC was between just 0.5% and3%. Given the evidence on liquidity constraints among EITC recipients, theextremely low participation in Advance EITC seems to have been a puzzle.Jones (2010) finds that the low take-up of Advance EITC did not resultfrom a lack of information, administrative costs or stigma, and suggests thatmaking Advance EITC the default option could have substantially increasedits participation rate.24 However, due to the very low usage rate, it has notbeen available since 2011.2.3 Data and Sample2.3.1 DataThe data I use come from the 1996, 2001, 2004, and 2008 panels of the Sur-vey of Income and Program Participation (SIPP). The SIPP is a nationalrepresentative survey of welfare program participation, employment and in-come dynamics, health insurance coverage, assets, liabilities, and relatedtopics. The initial sample size for each panel is about 35,000 householdsand 100,000 individuals. Each panel is a longitudinal survey that followsthe initially selected household members for at least three years and inter-views them every four months.25 In each interview, the respondent reportsher or his labor participation and income sources for each of the precedingfour months. Most of the information is reported at a monthly or quar-23The maximum amount of advance credit that could be received was 60% of the max-imum credit for a taxpayer with one child. The remaining credit was received after taxeswere filed at the beginning of the next year. In 2009, a potential EITC recipient couldobtain at most $1,826 through the Advance EITC.24Based on my SIPP sample, I find that over 70% of EITC-eligible families hold at leastone full-time jobs through out a year and 80% of them stay in the same jobs.25Some panels, such as the 1996 panel, follow their sample for up to four years. Inearlier years, the SIPP also had a short panel that followed selected household membersfor less than two years (e.g. the 1989 panel).142.3. Data and Sampleterly frequency. One exception is the variable indicating labor force status,which the SIPP provides weekly for each respondent. I use this informationto construct my outcome variables.26The SIPP data have two features making them especially suitable forthis paper. First, the SIPP data have a longitudinal structure. This featurenot only allows me to determine the treatment status for each person andprecisely calculate the EITC payments by utilizing information on each fam-ily’s income and number of qualifying children during the previous year, butalso enables me to control for the unobservable time-invariant heterogeneityby including individual fixed effects in the regression.Second, the SIPP also surveys household wealth and asset informationonce per year in its Assets, Liabilities, and Eligibility topical module.27 Themodule provides the latest measurements of household assets, wealth, anddebts as at the interview date, such as the value of deposits in bank accounts,stock and mutual fund holdings, home equity, vehicle equity, business equity,secured and unsecured debt, and mortgages. This information is particularlyuseful when I conduct subgroup analysis to explore possible explanations formy empirical findings by splitting the sample based on a family’s tendencyto be trapped by liquidity constraints. I use asset and wealth data fromthe topical module of the previous year to construct my measures of thefamily’s liquid assets and mortgage-to-income ratio. This predeterminedwealth information is used to form proxies indicating a family’s liquiditysituation in the current year.2.3.2 Imputed EITC PaymentThe SIPP does not provide valid information about the amount of EITC thateach eligible family would have received.28 I predict the amount of the EITC26I will discuss my outcome variable in detail in Section 2.4.27The waves of topical modules used in this paper are wave 3, wave 6, and wave 9 inthe 1996, wave 3 and wave 6 in the 2001 and 2004 panels, and wave 4, wave 7 and wave10 in the 2008 panel.28SIPP indeed asks a question about the amount of EITC that a respondent receives inits tax topical module. However, the response rate of this question is fairly low, only 24%.In addition, some of answers to income questions in the tax module are inconsistent with152.3. Data and Sampleusing information on family (earned) income, number of qualifying children,and filing (marital) status in the previous year. As mentioned before, thefinal amount of the EITC depends on the minimum amount of credits, basedon either earned income or AGI. Since the SIPP has information aboutfamily earned income, I use this variable directly. However, the SIPP doesnot provide valid information about AGI. I use family income, the sum ofearned income and unearned income, excluding non-taxable income, such asmeans-tested cash transfers,29 to approximate AGI.30Qualifying children must be under the age of 19 years, or 24 years ifstudying full-time, and must live with the taxpayer for at least half of theyear. I use detailed information about the age of each family member, parent(father and mother) identifiers, school enrollment status, and number ofmonths living with parents to calculate each family’s number of qualifyingchildren. According to EITC rules, married couples have to file their taxesjointly. Single individuals can choose either single or head of household filingstatus. Both filing statuses lead to the same EITC amount.31 Thus, I usemarital status to infer taxpayer’s filing status when computing the EITCpayment.2.3.3 SampleTo improve the measurement of my outcome variable and the EITC pay-ments for my estimation, I select my sample as follows. Table 2.2 displaysthe summary statistics of selected variables after each sample selection cri-terion has been applied. First, I require a respondent to have been followedin SIPP for at least two years. This criterion allows me to use the previousthose in the core SIPP files (Sisson and Short, 2001).29The SIPP classifies family income sources into four categories: (1) earned income, (2)property income, (3) means-tested cash transfers, and (4) other income. The last threeare unearned income but means-tested cash transfers are generally non-taxable income.Therefore, I define family income as the sum of earned income and unearned income,excluding means-tested cash transfers and use that to approximate AGI.30Again, the SIPP has a question about the amount of AGI but the data quality is notgood (i.e. low response rate and inaccurate numbers).31However, filing as a head of household can provide more generous tax brackets andlarger standard deductions than filing as a single.162.3. Data and Sampleyear’s information on family income and number of qualifying children toassign treatment status to an individual and infer the EITC amount thather family is likely to receive in the current year. For example, I use arespondent’s 1996 information on family income and number of qualifyingchildren to calculate the size of payment her family would have been likelyto receive in 1997, and examine the impact of receiving the EITC paymenton her intra-year labor supply pattern in 1997. Since I focus on low-incomefamilies, the estimated sample is restricted to those with positive earnedincome and family incomes below $40,000 in the previous year, which servesas the income cutoff for the comparison group (Column 1).32 Followingthe previous EITC literature (Eissa and Hoynes, 2004; Eissa and Liebman,1996), I conduct estimations separately for three subgroups that have beenthe populations of interest in previous studies: married women, marriedmen, and single women (Column 2). Therefore, I only include those whoare the reference person of their household or the spouse of the referenceperson. Note that a married couple filing their taxes together are from thesame family and thus have the same predicted EITC amounts.The basic unit interviewed in the SIPP is the household, and each house-hold might have several families residing in it. In order to avoid the impactof the EITCs of other subfamilies within the same household, any individualliving in a household with more than one family is dropped from the sample(Column 3). Furthermore, I restrict the sample to those aged from 20 to55 so as to reduce the impact of retirement on my estimated labor supplyresponses (Column 4).33Since my main focus is the intra-year change in labor supply, I requirethe sample to be observed for all 12 months in the years that I use forlabor supply estimation (i.e. except in the first year of each panel) so as tomitigate concern about the impact of a change in sample composition onmy estimates. This selection criterion ensures that my estimates identify32I discuss the treatment and comparison groups in detail in Section 2.4.33For married couples, this criterion is based on the wife’s age. About 93% of thehusbands are also within this age range. In Section 2.5, I report a robustness check usinga sample in which both husband and wife are in the required age range (20 to 55).172.4. Identification Strategychanges in individuals’ behavior instead of shifts in the composition of thesample (Column 5). Finally, for the first year of each panel, which is usedonly for determining the EITC amount and the treatment status in thefollowing year, the sample can be observed for less than 12 months becausea new SIPP panel might start after January. To obtain precise estimatesof the EITC payments, I restrict the sample in these years to those with atleast six months of observations (Column 6).34The years I use for my estimations are 1997–1999, 2002–2003, 2005–2006, and 2009–2012. Note that I also use the first year of each panel (i.e.1996, 2001, 2004, and 2008) to infer the treatment status and predictedEITC amount in the following years.35 The final sample size comprises25,564 individuals and 484,104 individual-month observations. From Table2.2, one can see that the sample characteristics are fairly similar after eachsample selection criterion is applied. The age restriction (Column 4) causesthe biggest changes in the sample characteristics, causing the sample to havehigher average earned income, a higher average number of children, a higherpredicted EITC amount, a higher portion of EITC recipients, lower averagewealth, and lower average liquid assets. According to statistics from theIRS, during my sample period, the average amount of the EITC paymentwas about $1,974, which is quite close to the average value of the imputedcredit amount, at $2,130.362.4 Identification StrategyIn this section, I describe the empirical specifications used to examine theimpact of the EITC receipt on the labor supply of low-income families.My identification strategy relies on the intra-year variation in the timingof EITC disbursement. EITC recipients receive their payments during thetax filing season, mostly in the month of February. I utilize this plausibly34For those without twelve months of observations, I scale their incomes up to create anannual income. For example, for those with seven months of income information. I usethe seven-month income multiplied by 12/7 to obtain an estimate of the annual income.35These years are 1997, 2002, 2005, and 2009.36All dollar amounts are in 2007 dollars.182.4. Identification Strategyexogenous timing of payments and the benefit rules of the EITC based onthe previous year’s information to estimate the causal effect of EITC receipton low-income families’ intra-year labor supply.2.4.1 Triple Differences EstimationI begin with triple differences analysis. This method compares the differ-ence in labor supply for a treatment group, between February and the othermonths, to that for a comparison group, which is presumed to remove anyshocks in February, other than the receipt of EITC payments, that mightaffect the labor supply decision of a treatment group. Following the priorliterature (McGranahan and Schanzenbach, 2014; Niedzwiecki, 2013; La-Lumia, 2013; Barrow and McGranahan, 2001), I define my treatment andcomparison groups using predetermined information based on EITC benefitrules: (1) the family income in the previous year, and; (2) the number ofqualifying children in the previous year. I estimate the following regression:Limt = α+ βlLowIncit−1 + βcChildit−1 + βeEITCit + βDDDEITCit × Feb+M + (LowIncit−1 ×M)βlm + (Childit−1 ×M)βcm + δt + νi +Ximtψ + εimt(2.1)where Limt is my outcome of interest, the share of weeks worked byindividual i in month m of year t. Since SIPP provides weekly labor forcestatus,37 I use the number of working weeks divided by number of weeks ina month to construct this variable: Limt = 1 if individual i works for thefull month; Limt = 0 if individual i does not work at all during the month;0 < Limt < 1 denotes cases in between.38 The advantage of the above37The SIPP questionnaire gives a respondent five choices for weekly labor force status:(1) with job or business, working; (2) with job or business, absent without pay; (3) withjob or business, on layoff; (4) no job or business, looking for job or on layoff; (5) no jobor business, neither looking for job nor on layoff. I use the first option to indicate that arespondent is working in a given week and the other four to indicate that she or he is notworking.38That is, an individual works for part of the month. For example, February has fourweeks. If an individual only works for two weeks, I would assign Limt = 0.5 to this192.4. Identification Strategydefinition is that it can also capture changes in labor force status within amonth. Later I report a robustness check of my estimates in which I used adifferent definition of the outcome variable.39 The variable LowIncit−1 refersto whether individual i’s family income in year t − 1 is greater than zeroand less than the EITC income limit (LowIncit−1 = 1) or is greater thanthan EITC income limit and less than $40,000 (LowIncit−1 = 0).40 Theincome limit roughly corresponds to the maximum EITC-eligible income forthe families with one child during my sample period. For a married couple,the income limit is $36,000 and for single women it is $33,000. The variableChildit−1 refers to whether individual i has one or more qualifying childrenin year t − 1 (Childit−1 = 1) or has no qualifying children in year t − 1(Childit−1 = 0).The treatment group dummy EITCit can be expressed as an interactionterm between LowIncit−1 and Childit−1. Therefore, EITCit = 1 indicatesthat individual i belongs to the treatment group that is expected to receivehigh EITC payments in the year t, namely, those whose family income isbelow the EITC income limit and who have one or more children in yeart− 1. EITCit = 0 denotes that individual i is in the comparison group thatis expected to receive low EITC in year t due to either having too great anincome or being childless in year t − 1.41 Note that the group assignmentis based on the previous year’s information, which is predetermined by thetime an individual makes her labor supply decision. In other words, anindividual’s current labor supply cannot affect her treatment status.observation.39Limt = 1 if individual i is working in any week during a month and Limt = 0 otherwise.40The income cut-off for the comparison group is chosen to narrow down the incomedifference between the two groups of families while retaining a sufficiently high samplesize in the comparison group.41I consider three comparison groups of individuals who are similar to those in the treat-ment group in many ways but receive very low EITC payments. The first consists of thoseindividuals with a similar income level to those in the treatment group (i.e. individualswhose family income is below the EITC income limit) but no qualifying children. Thesecond comprises those individuals with one or more qualifying child but whose familyincome in the previous year is just above the income limit and below $40,000. The thirdcomparison group includes childless individuals whose family income during the previousyear is above the income limit but below $40,000.202.4. Identification StrategyFigure 2.4 compares the distribution of EITC payments between thetreatment and comparison groups for married couples and single women.One may notice that most individuals in the comparison group have pre-dicted EITC payments of zero. On average, the predicted amount of EITCfor married couples in the treatment group is about $2,450. However, thosefrom the comparison groups only receive $140 on average. For single women,individuals from the treatment group are predicted to receive about $2,370and those from the comparison groups just $70. Table 2.3 displays sum-mary statistics of selected variables for the treatment group and compari-son groups. As expected, the treatment group has larger family (earned)incomes, more children, and greater predicted EITC amounts than the com-parison groups. In addition, the treatment group consists of more young, lesswealthy, and less educated individuals than the comparison groups. How-ever, except for the EITC-related variables, the differences in the covariatesbetween the treatment and comparison groups are not statistically signif-icant after controlling for individual fixed effects. Furthermore, I controlfor these covariates and individual fixed effects in all specifications, whichsubstantially reduces the impact of these group differences on my estimates.The variable Feb is a dummy for the month of February, when mostEITC recipients receive their tax refunds. The key variable used for identi-fication is EITCit × Feb, which indicates the February observation of indi-vidual i who is expected to receive a high EITC payment. Since the timingof the EITC payments is highly concentrated in February, the treatmentgroup will experience a large cash influx in February due to the receipt ofthe EITC, which is assumed to be the only difference between the treatmentand comparison groups during the year. Hence, I can attribute any Februaryeffect found in the treatment group to the impact of receiving the EITC.The coefficient of interest βDDD represents the causal effect of the EITCreceipt on the labor supply of individuals receiving high EITC payments inFebruary.Two assumptions are essential to ensure that βDDD has a causal inter-pretation. First, in absence of EITC payments, the difference in labor supplybetween the treatment and comparison groups should be similar across all212.4. Identification Strategytwelve months. In a later section, I conduct an event study analysis toinvestigate whether the differences in labor supply between treatment andcomparison groups are similar across the months when very few EITC pay-ments are disbursed. Second, the composition of the two groups cannotchange across months. Since the membership of the groups is based onthe previous year’s information, there is no change in group compositionwithin the current year. Moreover, the estimated sample is a fixed panelthat follows the same individuals over twelve months.I include a set of month dummies M so as to control for the monthlypatterns in labor supply that is common to both treatment and comparisongroups in all years, such as holiday-season jobs. The advantage of the tripledifferences regression is that it allows me to include more fixed effects thatare related to the group-level seasonality in the labor supply. Since my treat-ment group consists of low-income individuals with children, the primaryconcern with my estimates is that the results could simply reveal monthlypatterns in labor supply for specific groups, namely low-income individualsor individuals with children, regardless of the impact of receiving the EITCpayment. Hence, I interact month dummies M with the low-income dummyLowIncit−1 to further control for any monthly seasonality in labor supplythat is specific to low-income individuals. Note that I use October as thebaseline month since less than 1% of the total EITC disbursement is paid inthis month. Similarly, to control for any monthly employment patterns forindividuals with children, I also include group-specific month fixed effectsfor those who have qualifying children: Childit−1 × M .42 To control forcommon macroeconomic effects during my sample period, I include a seriesof year dummies δt. In addition, the panel structure of the data allows meto include individual fixed effects νi to control for any unobservable time-invariant differences in labor supply preferences between various individuals.Finally, to improve the precision of the estimates, I include a number of co-variates Ximt that could affect an individual’s labor supply: educationalattainment, age, number of children below 18, family wealth, monthly state42Again, I use October as the omitted month.222.4. Identification Strategyunemployment rate, state fixed effect, state-specific time trend, industryfixed effect, industry-specific time trend, a dummy denoting the interviewmonth, a dummy indicating that the individual worked part-time in theprevious year, and month fixed effect specific to part-time workers.43The variable εimt represents an error term. Since I follow the same indi-viduals over time, to account for possible serial correlation that might affectthe estimation of the standard error, the standard errors in all regressions areclustered at the person level. All regressions are weighted using person-levelweights provided by SIPP.442.4.2 Event Study AnalysisOne possible concern in the above specifications is that I treat all monthsother than February as part of the comparison groups, i.e. as unaffected bythe receipt of the EITC refund. However, nontrivial EITC payments aredisbursed in other months, particularly January, March and April. Hence,the results from equation (2.1) might bias the estimates downward (in ab-solute value). To address this issue, I conduct an event study by replacingEITCit × Feb with a full set of month effects M interacted with the treat-ment group dummy EITCit in regression (2.1).45 The estimation is basedon the following regression.43The categories of an individual’s educational attainment are high school drop-out,high school degree, and post-secondary education. Information about family wealth (2007dollars) is taken from the Assets, Liabilities, and Eligibility topical module for the previousyear. I use the information on a respondent’s industry in the previous year and a quadratictime trend to construct an industry-specific time trend variable. I categorize individualsinto five groups: agriculture, manufacturing, service, self-employed, and not working. Thedefinition of a part-time worker is that the average weekly hours worked by the individualin the previous year were greater than zero but less than 20.44In Section 2.5, I conduct robustness checks of my estimates by computing the standarderror at different cluster levels and using unweighted regressions.45Again, October is the omitted month.232.4. Identification StrategyLimt = α+ βlLowIncit−1 + βcChildit−1 + βeEITCit + (EITCit ×M)βem+M + (LowIncit−1 ×M)βlm + (Childit−1 ×M)βcm + δt + νi +Ximtψ + εimt(2.2)In practice, I plot the coefficients on the interactions between M andEITCit (October is the omitted month) to examine whether the monthlypatterns of group differences in the labor supply are coincident with thetiming of the EITC refund.2.4.3 Individual Variation in Predicted EITC PaymentsThe triple differences approach has the virtue of having a source of identi-fication that is quite transparent as it compares group-level outcomes. Thedrawback of this approach is that it compares differential treatment of rel-atively broad groups (i.e. high EITC versus low EITC) and assumes thattreatment intensity (i.e. EITC payment amount) is the same within a group.However, there is substantial within-group variation in the amount of theexpected EITC payment across individuals.In this section, I utilize the EITC refund that the recipients are expectedto receive in a given month to quantify the impact of the receipt of a $1,000EITC refund on the recipient’s labor supply during the month in which therefund is disbursed. To alleviate the concern over the comparability of laborsupply behavior between EITC-eligible and EITC-ineligible individuals, Ilimit the sample to EITC recipients. The estimation is based on the followingregression:Limt = α+ βINDRefundit × Sharemt + κ1Refundit + κ2Sharemt +M+Ximtψ + δt + νi + εimt(2.3)In the spirit of Souleles (1999) and McGranahan and Schanzenbach242.4. Identification Strategy(2014), I construct a variable indicating the EITC payment that each recip-ient is predicted to receive in a given month in the following ways. First,the variable Refundit represents the EITC payment (in thousands of dol-lars) that individual i is predicted to receive in year t. Note that Refunditis predetermined as regards the dependent variable Limt since the amountof the EITC payment is based on information from the previous year (i.e.year t − 1). In other words, the current labor supply decision has no im-pact on the amount of EITC received. Second, since SIPP does not haveinformation about when respondents receive their EITC payments, I use theaggregate-level measure of the share of annual EITC disbursement paid outin a given month m of year t, Sharemt, to approximate the date on which therecipient receives their EITC refund.46 For example, Share is set to 0.6 inFebruary 2010 since 60% of the 2010 EITC refunds were disbursed in Febru-ary. Using group-level refund timing instead of the exact dates on whichindividuals receive their EITC refunds could substantially reduce the endo-geneity problem since the exact timing of the refund will largely depend onwhen an individual files her tax statement, which might be correlated withunobservable determinants of the individual’s labor supply.The key variable in this regression is the interaction term betweenRefunditand Sharemt, which represents the expected EITC payment in a given monthfor individual i. The coefficient of interest, βIND, directly measures the ef-fect of receiving a $1,000 EITC payment on individual i’s labor supply inthe month in which the EITC payment arrives. This estimate is useful later,when I compute the income elasticity of labor supply based on this short-runchange in labor supply induced by the EITC refund. Consistent with thetriple differences analysis, I also control for month fixed effect M , year fixedeffect δt, the individual fixed effect νi and the same set of covariates Ximtas before.It has to be pointed out that most but not all of the tax refunds receivedby low-income families come from the EITC. Several previous studies (La-Lumia, 2013; Romich and Weisner, 2000) show that the EITC could account46The share data come from various issues of MTS.252.5. Resultsfor 70% to 80% of the tax refund for EITC-eligible families. Furthermore,the amount of the non-EITC refund, which comes from elements such asthe child tax credit, may be positively correlated with the amount of theEITC. Therefore, it may be reasonable to assume that a larger EITC pay-ment will be associated with a larger tax refund. The predicted amount ofthe EITC payment should provide a good approximation of the tax refundthat low-income families will receive.2.5 Results2.5.1 Triple Differences EstimatesI start by presenting the estimates from the triple differences estimations.Table 2.4 reports the estimated coefficient on the key variable EITC ×Febin the triple differences estimation (equation (2.1)). Panels A to C presentthe results for married women, married men and single women, respectively.I begin by presenting the estimate from the basic triple differences regressioncontrolling for the low-income group, the group with children, and monthfixed effects as well as all possible two-way interactions between those threedimensions. Then, I gradually include the individual fixed effect, year fixedeffect, state effect, and other individual characteristics that could determinethe monthly labor supply,47 so as to gain an understanding of the impactof adding other covariates to my estimates. The fact that the estimatesdo not change much across specifications with different sets of covariates iscomforting, given the causal interpretation of the estimates.In general, I find that the income seasonality induced by the receipt ofthe EITC refund leads to changes in the intra-year labor supply patterns ofmarried women. My preferred specification (Column 5 in Panel A) indicatesthat, compared to married women who receive low amounts of credit, thosewho receive high EITC payments are, significantly, 2.9 percentage points lesslikely to work in the month of February than in other months. In sharp con-47For a detailed list of the covariates in each specification, please see the note underTable 2.4.262.5. Resultstrast, married men and single women who receive high EITC payments donot exhibit distinct likelihoods of working in February compared to the othermonths. The point estimates in Column 5, Panels B and C, suggest thatthe likelihood of working declines, in February (relative to other months),for married men and single women, by only 0.3 percentage points and 0.2percentage points, respectively. Both estimates lack statistical significance.2.5.2 Event Study AnalysisNext, I extend the triple difference estimation by replacing EITCit × Febwith a full set of month effects M interacted with the treatment groupdummy EITCit so as to examine whether the monthly pattern of group dif-ference in labor supply largely follow the disbursement timing of the EITC.Figure 2.5 displays the coefficients on EITCit ×M and the corresponding95% confidence intervals based on the sample of married women. One cansee that the event study coefficients largely mirror the timing of the EITCdisbursement. Compared to marred women who receive low EITC payment,the labor supply of those receiving high EITC payments drops much morein February and also shows a substantial decline in January, March andApril (relative to October). Outside of these months, the difference in la-bor supply between the treatment and comparison groups is quite close tothe baseline level in October. Figures 2.6 and 2.7 present the estimates formarried men and single women, respectively. Consistent with the resultsfrom the triple differences estimation, no such pattern emerges for the mar-ried men and single women. Instead, the group differences in the outcomevariable are quite similar over the twelve months.2.5.3 Results from Individual Variation in EITC PaymentsFinally, I report the results based on variation in the predicted size of theEITC payment for each recipient in a given month. This approach has theadvantage of allowing variation in treatment intensity among EITC recipi-ents. If the intra-year labor supply pattern of married women found in theprevious section is driven by the receipt of the EITC, I should also find a272.5. Resultsmore negative effect on the labor supply among those receiving larger EITCpayments.Table 2.5 reports the estimated coefficients on Refund × Share fromequation (2.3). Again, I gradually include different sets of covariates so asto determine the impact of these covariates on my estimates. The estimatesacross the specifications are fairly independent of the introduction of differ-ent covariates. My preferred estimates (Column 5) suggest that the receiptof a $1,000 EITC payment reduces the proportion of married women workingby 1.6 percentage points in the month in which the EITC is received. Sincethe baseline mean of the outcome variable is 47%, the estimated decreaserepresents a 3.4% decline in the mean.48 In line with my triple differencesresults, receiving a $1,000 EITC payment does not have a statistically de-tectable impact on the share of weeks worked by either married men or singlewomen in the month when the EITC is paid out.2.5.4 Robustness ChecksIn this section, I examine the sensitivity of my result to a variety of alterna-tive sample selection criteria and empirical specifications. Table 2.6 displaysseveral of the resulting estimates. The first row presents the estimates basedon triple differences regression and the second row the estimates that utilizeindividual variation in predicted EITC payments. Column 1 presents theresults for a sample with a lower age cut-off of 50. This sample selectionfurther alleviates concerns over the impact of retirement on labor supply.In both specifications, the results suggest that this change has little impacton the estimates.Next, I address the fact that the baseline sample is restricted to marriedwomen aged 20 to 55 while their spouses might not be between the ages of 20and 55. In fact, 7% of the married women in the baseline sample had spouses48Using hours of work and rates of pay, I can provide some insights into the extent oflabor income offset by the EITC payments. The average hours of work for married womenis $105 hours per month and the average rate of pay is $12. Therefore, my estimates inColumn 5 of Table 2.5 implies $1000 EITC payment can offset monthly earned income by$20. The income replacement rate based on this calculation is around 2%.282.5. Resultsaged above 55. Column 2 presents results based on a sample excludingmarried women whose spouses are outside of the specified age range. Theestimates are quite similar to my baseline cases. Column 3 shows that theestimated coefficients from an unweighted regression are smaller than mymain estimates (in terms of absolute value), although the point estimatesare statistically indistinguishable from my main estimates. In Column 4, Iredefine my outcome variable as follows: Limt = 1 for an individual whoworks in any week during the given month and Limt = 0 otherwise. Thisdefinition is more comparable to the outcome variable of labor supply inprevious studies that use annual data but it ignores within-month variationin labor supply. Again, this change has little impact on my estimates.Column 5 of Table 2.6 presents statistical inferences based on a differentclustering level of standard errors. Since the policy variation I use is at thegroup-month level,49 I present the standard errors clustered on the group-month cells to account for any dependence of the unobservable error withinthe group-month level.There is a potential concern that my estimates could be confounded withfluctuations in labor demand due to holiday season jobs. Workers in thesejobs are usually hired in the fourth quarter of the calender year and mightquit their jobs in the first quarter of the following year. To alleviate thisconcern, Column 6 of Table 2.6 presents estimates based on a sample thatexcludes those who worked in the retail industry at the end of the previousyear. This restriction reduces my sample by around 8% but has little impacton my estimates.Some states have supplemental state EITCs. The size of state EITCsvary across states and time, which generates an additional source of variationin EITC payments. The last column of Table 2.6 presents the estimate basedon regression 2.3 incorporating this state-level variation. I find that thisestimate is quite similar to my baseline estimate.49I have four groups. One is the treatment group and the other three are comparisongroups. Therefore, the total number of group-month cells is 48 (4 groups x 12 months).292.5. Results2.5.5 Discussion: Magnitude of the EstimatesIn this section, I begin by discussing the estimates obtained from the twoempirical approaches and then compare their magnitudes to estimates fromthe prior literature. Specification (2.3) suggests that, on average, the receiptof a $1,000 EITC payment leads to a reduction in the likelihood of marriedwomen working by 1.6 percentage points during the month in which theEITC is received. The magnitude based on this specification indeed providesa similar qualitative conclusion to my triple-differences estimation. I presenta simple calculation to confirm their similarity. First, the triple-differencesestimation (specification (2.1)) suggests that the receipt of the EITC refundleads married women from the treatment group to be 2.9 percentage pointsless likely to work in February than in other months. Additionally, the av-erage gap in EITC payments between the treatment and comparison groupsin the triple differences estimation is around $2,310. Note that around 56%of the EITC is paid out in February. Therefore, the estimate based on tripledifferences regression implies that receiving a $1,000 EITC refund could re-duce the proportion of married women working by 2.2 percentage points.50The estimates based on these two approaches are fairly close.One way to think about the magnitude of my estimates is to calculatethe income elasticity of labor supply and then compare it to the estimatesreported in previous studies. The unearned income of married women iscomputed using the secondary earner assumption. That is, it is equal tothe husband’s monthly earned income plus the family’s monthly unearnedincome. Since the receipt of the EITC has little impact on married men’slabor supply, it could be reasonable to assume that the average size ofmonthly unearned income is unrelated to the EITC refund. The mean valueof monthly unearned income for married women is around $1,847. My esti-mate suggests that receiving a $1,000 EITC refund could significantly reducethe proportion of married women working in the month in which the refundis received, by 1.6 percentage points from the base of 47%. In other words,a 54% increase in unearned income could lead to a 3.4% decline in the like-50This is derived from a simple calculation: 0.0292.31× 0.56 = 0.022.302.5. Resultslihood of working in the month of payment arrival. This implies that theincome elasticity of labor supply for married women is around −0.06.My estimated income elasticity is largely consistent with the findings inprevious studies. McClelland and Mok (2012) provide an up-to-date reviewof labor supply elasticities. They point out that the previously estimatedincome elasticities of employment among married men and single womentend to be quite small, namely, close to zero. However, the responsiveness ofthe employment of married women to income changes is substantially largerthan that for married men and single women. Heim (2007) finds the incomeelasticity of employment for married women to be between −0.13 and −0.05.Blau and Kahn (2007) estimate the income elasticity for married women tobe about −0.1. Both studies rely on cross-sectional variation in unearnedincome. A few recent studies use more exogenous variation in income fromrandomized experiments, such as lotteries, to get more credible estimates ofthe income elasticity. Jacob and Ludwig (2012) use a randomized lotteryfor housing vouchers and estimate the income elasticity among lower-incomeindividuals who apply for housing assistance to be −0.09.One caveat should be noted when comparing my results to those in theprevious literature. My estimated elasticity relies on a higher-frequencychange in income and labor supply than previous studies have done. I ex-ploit the monthly change in income induced by the tax refund and study theimpact of this short-run income change on an individual’s monthly workingdecision. However, most prior studies have utilized annual changes in incomeand labor supply to estimate income elasticity, meaning that their estimatescould represent the relatively long-run relationship between income and la-bor supply. With this caveat in mind, my estimates are generally similar inmagnitude to the previously estimated income elasticities of labor supply.2.5.6 Mechanisms behind the FindingsSecondary EarnerI examine why married women’s labor supply responds to the receipt of anEITC refund but married men’s and single women’s do not. One possible312.5. Resultsexplanation is most married women are the secondary worker in a family.Prior studies find that labor supply of a secondary earner is quite sensi-tive to changes in family resources (Cullen and Gruber, 2000). The “addedworker effect” hypothesis holds that, under an imperfect credit market, thesecondary earners, typically married women, in families could provide tran-sitory earning sources to smooth out household spending whenever familiesface temporary shortages of liquidity (e.g. if the family has a mortgagecommitment). Secondary earners may then exit the labor market once thefamily’s need for liquidity is met (Goux and Petrongolo, 2014; Heckman andMaCurdy, 1980; Kohara, 2010; Lundberg, 1980; Mincer, 1962).51 Hence, oneshould expect a secondary earner to exhibit a more negative labor supplyresponse to the receipt of the EITC than a primary earner. Another poten-tial explanation for my findings is that female EITC recipients have specificintra-year patterns in labor supply that are coincident with the timing ofthe EITC disbursement.I use information on individual earnings in the previous year to definethe primary and secondary earners within each family. An individual whohad lower annual earnings than her or his spouse during the previous yearis classified as the secondary earner. I begin by focusing on married couplesand estimate specification (2.3) for the following four subgroups: marriedwomen who are primary earners, married women who are secondary earners,married men who are primary earners, and married men who are secondaryearners.The first four columns in Table 2.8 display the coefficients on Refund×Share for the above four subgroups. The estimates in Columns 1 and 2suggest that the negative labor supply response to EITC receipt for marriedwomen found in the previous section is exclusively driven by those who aresecondary earners in their families. On average, upon receiving a $1,000EITC payment, married women who are secondary earners are significantlyless likely to work, by 1.7 percentage points in the month in which the EITC51For example, Cullen and Gruber (2000) find that more generous unemployment in-surance would “crowd out” the labor supply of married women who face a temporaryreduction in household resources due to the unemployment of their husbands.322.5. Resultsrefund is received. In contrast, those who are primary earners only showan insignificant decreased likelihood of working, of 0.7 percentage points.Interestingly, a similar pattern arises in the sample of married men. Amarried man who is his family’s secondary earner exhibits a reduction of 1.6percentage points in his working likelihood in the month in which he receivesa $1,000 EITC refund. The magnitude of this estimate is fairly close to theestimate for married women but is not statistically significant due to thesmall sample size for this group. The above results imply that the negativelabor supply response to the receipt of the EITC for married women couldresult from the different gender roles due to the division of labor withinfamilies, rather than gender differences in intra-year labor supply patternsamong EITC recipients.To further compare the two possible channels that could underlie my re-sults, I pool the whole sample together (including single women)52and “horserace” the “secondary earner” channel against the “gender difference” chan-nel by interacting the intercept, a set of month dummies, and the predictedmonthly EITC amount with an indicator for being female (Female) anda dummy indicating that a person is a secondary earner (Second), respec-tively, in specification (2.3). The first row in the last column of Table 2.8suggests that receiving a $1,000 EITC payment leads the baseline group’slikelihood of working in the month when the EITC is received to decline by0.3 percentage points, insignificantly.53 The “secondary earner” channel co-efficient (in the second row) reveals that those who are secondary earners intheir families will be an additional 1.4 percentage points less likely to workin a month in which they receive a $1,000 EITC refund. The point esti-mate is significant, with a p-value of 0.03. However, the “gender difference”channel coefficient (in the third row) suggests that there is no statisticallydetectable additional impact of being female on the probability of workingin the month in which the refund arrives, after controlling for the effect ofbeing a “secondary earner.”52By definition, all single women are the primary earners in their families.53The baseline group consists of married men who are primary earners.332.5. ResultsLiquidity ConstraintsNext, I analyze why families reduce labor supply upon receipt of an antici-pated EITC payment. The leading explanation for the observed behavior isthe presence of liquidity constraints preventing families from borrowing fu-ture income to finance current spending. In this situation, families may keeptheir level of labor supply high to improve their liquidity until their tightbudget is loosened by the receipt of the EITC refund. If liquidity constraintsdo play an important role in determining the family labor supply, one wouldexpect the negative labor supply response of married women to the receiptof the EITC to be driven by those women from “more constrained” families.I use two proxy variables to indicate the family’s tendency to be liquid-ity constrained: liquid assets (i.e. the value of bank deposits in the previousyear) and the mortgage-to-income ratio (i.e. the amount of the mortgagedivided by total family income in the previous year). Both variables arecomputed at the family level for the calendar year before EITC receipt.Following the standard methodology in the prior literature (Parker, 2014;Johnson et al., 2013; Johnson et al., 2006; Souleles, 1999; Zeldes, 1989), foreach variable, I divide the sample into two sets of individuals: those likelyto be liquidity-constrained and those likely not to be. I use Constrained todenote membership of the liquidity-constrained group and interact it withthe intercept and the expected EITC amount in a given month in specifica-tion (2.3). Hence, the additional labor supply response to the receipt of a$1,000 EITC payment for liquidity-constrained individuals would be identi-fied by the interaction between the indicator for the constrained group andthe predicted monthly EITC payment.Individuals with low liquid assets could be unable to draw down theirwealth to smooth out their spending. In order to improve their family’sliquidity, they are likely to adjust their labor supply, which could resultin a greater negative response of labor supply to the receipt of the EITCpayment. In the spirit of Parker (2014), I label those with liquid assets belowthe one-month average family income (i.e.$2,000) as constrained families and342.5. Resultsthe rest as unconstrained.54 Column (1) of Table 2.7 shows how the laborsupply response to an EITC payment varies according to the liquid assetsheld. The first row indicates that the receipt of a $1,000 EITC paymentreduces the likelihood of working for married women with high liquid assetsby 0.3 percentage points in the month in which the EITC received and thisestimate is not statistically significant. In sharp contrast, receiving a $1,000EITC refund significantly lowers the proportion of married women with lowliquid assets working by 1.7 percentage points (Row 3). This labor supplyresponse is almost five times as large as that of married women from familieswhose liquid assets are above the average monthly family income (in absolutevalue). The point estimate of the group difference is statistically significant,with a p-value of 0.07 (Row 2).Prior studies (Del Boca and Lusardi, 2003; Fortin, 1995) show that mort-gage commitment is an important factor determining the labor force par-ticipation of married women. Furthermore, those who have large mortgagesmight also have limited borrowing ability since housing collateral is oftenused for borrowing (Mian et al., 2014; Mian and Sufi, 2011). I use themortgage-to-income ratio to approximate the likelihood of families beingbound by liquidity constraints. Families with high mortgage-to-income ra-tios may be under greater pressure to meet their mortgage commitmentand have limited credit lines for borrowing additional money. Under thesecircumstances, married women with high mortgage-to-income ratios mightenter the labor market temporarily to increase family liquidity, and theirworking decision may be sensitive to the change in family liquidity inducedby the EITC refund. To investigate this hypothesis, the estimated sampleis restricted to those who are house owners.55 I classify families with amortgage-to-income ratio of 1.5 or above as constrained and the remainderas less constrained. A mortgage-to-income ratio of 1.5 is around the medianof the distribution of mortgage-to-income ratios. Column 2 of Table 2.7shows how the labor supply response to an EITC payment varies accordingto the mortgage-to-income ratio. For married women with low mortgage-54This value also divides the top 20% in the distribution of liquid assets from the rest.55Around 56% of the EITC recipients in my sample are house owners.352.5. Resultsto-income ratios, the receipt of a $1,000 EITC refund results in a decreaseof 1 percentage point in the likelihood of working in the month in which theEITC is received (Row 1). However, the point estimate is not statisticallysignificant. In contrast, the receipt of a $1,000 EITC refund significantlylowers the proportion of married women with a high mortgage-to-incomeratio who work, by 2.7 percentage points (Row 3). The point estimate ofthe group difference is sizeable and statistically significant, with a p-valueof 0.014 (Row 2).MyopiaThe above subgroup analysis suggests that the presence of liquidity con-straints may be an important reason why married women reduce their laborsupply when receiving anticipated EITC payments. However, the presenceof liquidity constraints cannot fully explain why the receipt of the EITCcauses labor supply of married women to have a temporary drop in Febru-ary, and then revert back quickly to the normal level of labor supply. As-sumed a household’s utility function is concave so marginal utility of leisureis diminishing. Therefore, to maximize intertemproal utility, a householdwants to keep marginal utility equal across time periods. In other words, iffamilies are forward-looking but liquidity constrained, they should smoothout their labor supply (or leisure consumption) after receiving the cash (i.e.when they are no longer liquidity constrained). Thus, we should observea small and persistent decrease rather than a large and temporary drop inlabor supply following receipt of the EITC. This patterns reveals that therecipients could be somewhat present-biased and prefer consuming leisure atthe time when receiving cash transfer rather than use this money for theirfuture consumption.5656There are several theories explaining such present-biased behavior. One possibilityis that poor people could have hyperbolic discount rate (Angeletos et al., 2001), whichresults in time-inconsistent preferences. That is, current selves of EITC recipients wantto enjoy leisure right after receiving payments but future selves of EITC recipients wouldlike to keep their labor supply to finance future spending. Another explanation is that thepresence of temptation goods causes people prefer to consume more today rather than savefor tomorrow (Banerjee and Mullainathan, 2010). In contrast to normal goods, temptation362.5. ResultsMonth-to-Month Labor Force TransitionsFinally, I use detailed information about labor force status from the SIPPto investigate how the receipt of an EITC refund affects the recipient’smonth-to-month labor force transitions. This analysis will help us under-stand the main cause of the decreased likelihood of working for marriedwomen in February (relative to other months). In general, my results couldbe driven by the fact that the receipt of the EITC increases the likeli-hood of working-to-nonworking transitions or decreases the likelihood ofnonworking-to-working transitions (e.g. those who work in January and thenstop working in February or those who do not work in January and thenkeep not working in February due to the receipt of the EITC).As mentioned before, SIPP classifies labor force status into five cate-gories: (1) working, (2) temporary leave without pay, (3) temporary layoffwithout pay, (4) unemployment, and (5) out of the labor force. The lastfour categories are defined as nonworking. In addition, Figure 2.8 displaysthe total amount of income tax refunds paid out in each week from Januaryto April, based on the Daily Treasury Statement, and clearly shows thata large amount of the income tax refund is disbursed in the 6th week andthe 7th week, which corresponds to the second and third weeks of February.Since most EITC recipients obtain their refund in February, this weekly re-fund disbursement pattern is likely to reflect the timing of the receipt of theEITC refund. Therefore, it is quite possible that EITC recipients receivetheir credit in the third week of February.Given the above information, I define the two outcome variables as fol-lows and estimate specification (2.1): The first dependent variable, P (Wim =0|Wim−1 = 1), is an indicator of whether individual i works in the third weekof month m − 1 (i.e. Wim−1 = 1) and stops working in the third week ingoods, such as alcohol or cigarettes, generate utility only at the point of consumption andpeople do not value spending on tomorrow’s temptation goods. For example, you may getpleasure from drinking alcohol today but you may think that it will be bad for your futureselves to drink alcohol. Under the assumption that the proportion of temptation goods isdecreasing as income increases, low-income people would prefer to consume today ratherthan tomorrow since a higher share of their future spending on temptation goods makesthem unwilling to save for tomorrow consumption.372.5. Resultsmonth m (i.e. Wim = 0), which measures the working-to-nonworking tran-sition. Similarly, I measure the nonworking-to-working transition using thedependent variable, P (Wim = 1|Wim−1 = 0), an indicator of whether indi-vidual i does not work in the third week of month m − 1 (i.e. Wim−1 = 0)but does work in the third week of month m (i.e. Wim = 1).The first two columns in Table 2.9 report the estimated coefficients onEITC×Feb for the above two outcome variables. The estimated coefficientimplies that the receipt of an EITC refund would increase the likelihood ofa working-to-nonworking transition for married women by 1.24 percentagepoints in February compared to other months. On the other hand, the re-ceipt of an EITC refund decreases the likelihood of a nonworking-to-workingtransition by 0.2 in February compared to other months. Most changes in la-bor force status are concentrated in the working-to-nonworking transitions,which is around six times as large as the nonworking-to-working transitions,although neither estimate is statistically significant. I further decompose theworking-to-nonworking transition into more detailed changes in labor forcestatus by estimating specification (2.1) with the following outcome variables,respectively: working to unpaid leave, working to temporary layoff, workingto unemployment, and working to out of the labor force. When I do this,I find that most increases in working-to-nonworking transitions in Februaryindeed come from working to unpaid leave transitions. The receipt of theEITC significantly increases the likelihood of working to unpaid leave tran-sition for married women by 1.08 percentage points in February (relative toother months). In contrast, the likelihoods of other labor force transitionsdo not show significant differences between February and other months.Figures 2.9a to 2.9f, which plot the estimated coefficients on EITCit ×Mfrom specification (2.2) (i.e. event study analysis) for each outcome variable,confirm my regression results. Although the estimates are not precise, myresults provide suggestive evidence that married women could temporarilyleave their jobs without pay upon receiving the EITC refund in February.382.6. Conclusion2.6 ConclusionThis paper utilizes the unique disbursement pattern and benefit rules of theEITC to examine the casual effect of the receipt of a cash transfer on the tim-ing of family labor supply. My results show that income seasonality causedby EITC receipt leads to changes in the intra-year labor supply patternsof married women. On average, receiving a $1,000 EITC payment reducesthe proportion of married women who work in the month of credit receiptby 1.6 percentage points from a baseline mean of 47%. The income elastic-ity of labor supply for married women based on these short-run changes inlabor supply and income is around −0.06, which falls within the range ofestimates in the previous literature that were obtained using longer horizonsfor employment and income changes. The analysis of month-to-month la-bor force transitions provides suggestive evidence that married women couldtemporarily leave their jobs without pay upon receiving the EITC refundin February. No such tax refund-induced intra-year labor supply emergesfor married men or single women. The subgroup analysis suggests familiesmight reduce the labor supply of secondary earners in response to receiv-ing an anticipated EITC payment. In addition, my results suggest that thepresence of both liquidity constraints and myopia among EITC recipientsprovide possible explanations for my findings.Several interesting implications arise from my results. First, both thispaper and previous studies consistently provide evidence of a liquidity con-straint among those claiming the EITC. These results imply that providingmore frequent payments prior to the tax filing year, such as through AdvanceEITC, should be an attractive option for low-income taxpayers and couldsubstantially help liquidity-constrained recipients to smooth their spendingand leisure throughout the year. However, the low participation rate in Ad-vance EITC is still a puzzle in the literature, and it has not been an optionsince 2011. Recent studies (Jones, 2010) have made some progress towardsolving this puzzle. In general, they find that the universally low take-upmight not have resulted from recipients’ lack of information about it, fromthe application process being too complicated, or from recipients’ fear of392.6. Conclusionstigma. Jones (2012) finds strong evidence on the presence of inertia amongEITC recipients, suggesting making periodic EITC payments the default op-tion could substantially encourage people to obtain their EITC throughoutthe year before tax filing. Future research on this issue is needed to aid theredesign of a feasible option for periodic EITC payments.On the other hand, my results clearly show that married couples havemore flexibility in terms of adjusting their labor supply so as to smooth outtheir spending than singles. One possibility for future research is to examinewhether the response of household spending to EITC receipt (or the receiptof other anticipated income) varies by family structure, which would providea more complete picture of how families smooth their consumption.402.7. Figures2.7 FiguresFigure 2.1: Real Federal Spending on EITC and TANF: 1975–2011Notes: Data are from Tax Policy Center (2012)412.7. FiguresFigure 2.2: EITC schedule (Tax Year 2007)Notes: Data are from Tax Policy Center (2012). All dollar values are measured in 2007 dollars.422.7. FiguresFigure 2.3: Share of Annual EITC Disbursements by MonthNotes: Data are from various issues of Monthly Treasury Statements. For each monthand year, the fraction of the year’s disbursements was first calculated. These fractionswere then averaged by month across the years: 1997–1998, 2002–2003, 2005–2006, and2009–2012. Because the IRS did not provide disbursement information in 1997, I usedthe 1998 distribution of disbursements to impute it.432.7. FiguresFigure 2.4: EITC Amount by Treatment Status and Family Type(a) Treatment Group: Married Couples(b) Comparison Group: Married Cou-ples(c) Treatment Group: Single Women (d) Comparison Group: Single WomenNotes: This table displays the distribution of predicted EITC amount by treatmentstatus and family type. The horizontal axis indicates the predicted amount of the EITC.The vertical axis indicates the fraction of people within a specific income range. Thebin width is $100.442.7. FiguresFigure 2.5: The Impact of EITC on Intra-Year Labor Supply Patterns:Married WomenNotes: This figure shows coefficients on EITCit × M and associated 95% confidenceinterval from specification 2.2 where the dependent variable L is the share of weeksworked in a month defined as number of working weeks divided by total number ofweeks in a month. Therefore, L = 1 if working for the full month, L = 0 if not workingfor the full month, and 0 < L < 1 if working for partial month. The estimated sampleis restricted to married women. The dependent variable is regressed on the interactionterms between indicator for treatment group EITC and 11 month dummies (Octoberis the omitted month) M . The treatment group consists of those individuals that haveone or more qualifying children and family income during tax year greater than zeroand less than $36,000. The comparison groups comprise (1) those individuals that havefamily income during tax year greater than zero and less than $36,000 but have noqualifying child. (2) those individuals with one or more qualifying children but whoseannual income is just above $36,000 and below $40,000. (3) childless individuals thathave incomes greater than $36,000 and below $40,000. All dollar values are measuredin 2007 dollars. The regression controls for treatment group dummy, an indicator forindividuals with one or more qualifying children, an indicator for individuals with familyincome greater zero and below $36,000, month fixed effect for those who have qualifyingchildren, month fixed effect for those who have family income during tax year less than$36,000, month fixed effect, individual fixed effect, year fixed effect, state fixed effect,monthly state unemployment rate, state specific time trend (quadratic), an indicator forinterviewing month, educational attainment, number of children under 18, age, industryfixed effect, industry specific time trend (quadratic), family wealth, a dummy indicatingthat the individual worked part-time in the previous year, and month fixed effect specificto part-time workers.452.7. FiguresFigure 2.6: The Impact of EITC on Intra-Year Labor Supply Patterns:Married MenNotes: This figure shows coefficients on EITCit × M and associated 95% confidenceinterval from specification 2.2 where the dependent variable L is the share of weeksworked in a month defined as number of working weeks divided by total number ofweeks in a month. Therefore, L = 1 if working for the full month, L = 0 if not workingfor the full month, and 0 < L < 1 if working for partial month. The estimated sampleis restricted to married men. The dependent variable is regressed on the interactionterms between indicator for treatment group EITC and 11 month dummies (Octoberis the omitted month) M . The treatment group consists of those individuals that haveone or more qualifying children and family income during tax year greater than zeroand less than $36,000. The comparison groups comprise (1) those individuals that havefamily income during tax year greater than zero and less than $36,000 but have noqualifying child. (2) those individuals with one or more qualifying children but whoseannual income is just above $36,000 and below $40,000. (3) childless individuals thathave incomes greater than $36,000 and below $40,000. All dollar values are measuredin 2007 dollars. The regression controls for treatment group dummy, an indicator forindividuals with one or more qualifying children, an indicator for individuals with familyincome greater zero and below $36,000, month fixed effect for those who have qualifyingchildren, month fixed effect for those who have family income during tax year less than$36,000, month fixed effect, individual fixed effect, year fixed effect, state fixed effect,monthly state unemployment rate, state specific time trend (quadratic), an indicator forinterviewing month, educational attainment, number of children under 18, age, industryfixed effect, industry specific time trend (quadratic), family wealth, a dummy indicatingthat the individual worked part-time in the previous year, and month fixed effect specificto part-time workers.462.7. FiguresFigure 2.7: The Impact of EITC on Intra-Year Labor Supply Patterns:Single WomenNotes: This figure shows coefficients on EITCit × M and associated 95% confidenceinterval from specification 2.2 where the dependent variable L is the share of weeksworked in a month defined as number of working weeks divided by total number ofweeks in a month. Therefore, L = 1 if working for the full month, L = 0 if not workingfor the full month, and 0 < L < 1 if working for partial month. The estimated sampleis restricted to single women. The dependent variable is regressed on the interactionterms between indicator for treatment group EITC and 11 month dummies (Octoberis the omitted month) M . The treatment group consists of those individuals that haveone or more qualifying children and family income during tax year greater than zeroand less than $33,000. The comparison groups comprise (1) those individuals that havefamily income during tax year greater than zero and less than $33,000 but have noqualifying child. (2) those individuals with one or more qualifying children but whoseannual income is just above $33,000 and below $40,000. (3) childless individuals thathave incomes greater than $33,000 and below $40,000. All dollar values are measuredin 2007 dollars. The regression controls for treatment group dummy, an indicator forindividuals with one or more qualifying children, an indicator for individuals with familyincome greater zero and below $33,000, month fixed effect for those who have qualifyingchildren, month fixed effect for those who have family income during tax year less than$33,000, month fixed effect, individual fixed effect, year fixed effect, state fixed effect,monthly state unemployment rate, state specific time trend (quadratic), an indicator forinterviewing month, educational attainment, number of children under 18, age, industryfixed effect, industry specific time trend (quadratic), family wealth, a dummy indicatingthat the individual worked part-time in the previous year, and month fixed effect specificto part-time workers.472.7. FiguresFigure 2.8: Weekly Disbursement Patterns of Income Tax RefundsNotes: Data are from various issues of Daily Treasury Statements. The graph displaysthe average disbursement of income tax refunds during the first 16 weeks in a year.These amounts were averaged by week across the years: 1997–1998, 2002–2003, 2005–2006, and 2009–2012. Because the IRS did not provide disbursement information in1997, I used the 1998 distribution of disbursements to impute it.482.7. FiguresFigure 2.9: Month-to-Month Labor Force Transitions(a) Working to Nonworking (b) Nonworking to Working(c) Working to Unpaid Leave (d) Working to Temporary Layoff(e) Working to Unemployment (f) Working to Out of Labor ForceNotes: This figure shows coefficients on EITCit ×M and associated 95% confidence intervalfrom specification 2.2 where the dependent variables are working to nonworking, nonworkingto working, working to unpaid leave, working to temporary layoff, working to unemployment,and working to out of the labor force. The estimated sample is restricted to married women.The dependent variable is regressed on the interaction terms between indicator for treatmentgroup EITC and 11 month dummies (October is the omitted month) M . The treatmentgroup consists of those individuals that have one or more qualifying children and family incomeduring tax year greater than zero and less than $36,000. The comparison groups comprise(1) those individuals that have family income during tax year greater than zero and less than$36,000 but have no qualifying child. (2) those individuals with one or more qualifying childrenbut whose annual income is just above $36,000 and below $40,000. (3) childless individualsthat have incomes greater than $36,000 and below $40,000. All dollar values are measured in2007 dollars. The regression controls for treatment group dummy, an indicator for individualswith one or more qualifying children, an indicator for individuals with family income greaterzero and below $33,000, month fixed effect for those who have qualifying children, monthfixed effect for those who have family income during tax year less than $33,000, month fixedeffect, individual fixed effect, year fixed effect, state fixed effect, monthly state unemploymentrate, state specific time trend (quadratic), an indicator for interviewing month, educationalattainment, number of children under 18, age, industry fixed effect, industry specific timetrend (quadratic), family wealth, a dummy indicating that the individual worked part-time inthe previous year, and month fixed effect specific to part-time workers.492.8. Tables2.8 TablesTable 2.1: Share of Annual EITC Dis-bursements by MonthPercent of annual disbursementsJanuary 7.0February 55.5March 22.3April 8.5May 4.1June 1.1July 0.5August 0.3September 0.3October 0.2November 0.1December 0.0Note: Data are from various issues of MonthlyTreasury Statements. For each month and year,the fraction of the year’s disbursements in thatyear was first calculated. These fractions werethen averaged by month across the years: 1997–1999, 2002–2003, 2005–2006, and 2009–2012.Because the IRS did not provide disbursementinformation in 1997, I used the 1998 distributionof disbursements to impute it.502.8. TablesTable 2.2: Sample Selection: Summary Statistics(1) (2) (3) (4) (5) (6)Below Reference person Only one Age Observed First year$40,000 or spouse family 20-55 12 months informationFamily income ($1,000) 24.17 24.53 24.82 24.45 24.90 24.92[10.13] [10.04] [9.98] [10.14] [10.02] [10.03]Earned income ($1,000) 19.78 20.07 20.14 22.14 22.50 22.51[11.02] [11.10] [11.17] [10.67] [10.58] [10.59]# of qualifying children 0.71 0.82 0.85 1.22 1.35 1.41[1.15] [1.21] [1.23] [1.31] [10.58] [1.34]EITC payment (> 0, $1,000) 1.74 1.83 1.86 1.97 2.10 2.12[1.49] [1.49] [1.50] [1.48] [1.48] [1.48]Working 0.67 0.68 0.67 0.72 0.71 0.71[0.46] [0.46] [0.45] [0.44] [0.44] [0.44]Wealth ($1,000) 93.50 93.81 97.52 66.34 71.31 70.79[876.92] [927.03] [930.28] [627.81] [802.97] [816.96]Liquid asset ($1,000) 4.80 4.77 4.97 2.85 2.84 2.81[21.54] [21.16] [21.93] [15.36] [15.19] [14.89]Amount of mortgage ($1,000) 25.53 25.10 25.24 27.19 29.91 29.61[56.48] [55.31] [55.31] [57.59] [60.02] [59.45]Age 43.16 44.18 45.78 39.00 39.52 39.50[15.38] [14.52] [14.92] [9.98] [9.76] [9.75]State Unemployment rate(%) 6.62 6.58 6.58 6.57 6.76 6.58[2.39] [1.24] [1.38] [1.38] [1.39] [1.39]EITC recipients 0.43 0.45 0.46 0.57 0.64 0.66Female 0.56 0.57 0.58 0.56 0.66 0.66Married 0.39 0.48 0.53 0.53 0.67 0.67White 0.77 0.77 0.78 0.76 0.77 0.77High school and below 0.72 0.72 0.72 0.70 0.71 0.71Part time job 0.14 0.14 0.12 0.12 0.12 0.12Secondary earner 0.20 0.24 0.25 0.34 0.34 0.34Agriculture 0.06 0.06 0.07 0.07 0.06 0.06Manufacturing 0.09 0.10 0.10 0.10 0.09 0.09Service 0.57 0.56 0.58 0.58 0.57 0.57Self-emplpoyed 0.10 0.10 0.10 0.10 0.10 0.10Not working 0.18 0.18 0.15 0.15 0.18 0.18# of EITC recipients 41,997 35,383 31,609 29,163 17,027 16,908# of individual 91,607 72,438 64,240 49,580 26,185 25,564# of individual-months 1,672,584 1,339,029 1,154,992 859,007 502,440 484,104Note: SIPP data for years 1996–1999, 2001–2003, 2004–2006, and 2008–2012. Family income is the sumof earned income and unearned income, excluding the non-taxable mean-tested cash transfer. Familyincome, earned income, wealth, liquid asset, amount of mortgage, and EITC payment are in thousands ofdollars. Family income, earned income, wealth, liquid asset, amount of mortgage, # of qualifying children,and EITC payment are based on the family level information in the previous year. All dollar amountsare in 2007 USD. Column (1) includes observations that have positive earned income and family incomeduring the previous year below $40,000. In addition, they are followed for at least two years. Column(2) additionally requires sample to be married women, married men and single women. They are eitherreference person of the household or spouse of reference person. Column (3) additionally requires eachsample to live in a household with only one family. Column (4) additionally imposes age restrictions:individuals with age 20 to 55. For a married couple, the age restriction is based on wife’s age. Column(5) additionally requires individuals to be observed for all 12 months in the year that I use for estimatinglabor supply (i.e. except the first year of each panel). Column (6) additionally restricts the sample to thoseobserved at least six months in the first year of each panel. Standard errors are reported in parentheses.512.8. TablesTable 2.3: Treatment and Comparison Groups: Summary StatisticsMarried Women Married Men Single WomenHigh-EITC Low-EITC High-EITC Low-EITC High-EITC Low-EITCFamily income ($1,000) 23.97 30.49** 23.97 30.49** 17.55 25.11**[8.45] [9.30] [8.45] [9.30] [8.72] [5.68]Earned income ($1,000) 22.14 27.35** 22.14 27.35** 14.61 22.80**[8.94] [10.89] [8.94] [10.89] [8.62] [10.59]# of qualifying children 2.20 0.69** 2.20 0.69** 1.88 0.26**[1.13] [1.20] [1.13] [1.20] [1.02] [10.59]EITC payment ($1,000) 2.45 0.14** 2.45 0.14** 2.33 0.07**[1.44] [0.37] [1.44] [0.37] [1.32] [1.59]Working 0.44 0.58 0.82 0.77 0.77 0.87[0.49] [0.48] [0.49] [0.48] [0.40] [9.93]Wealth ($1,000) 70.97 112.92 70.97 112.92 24.17 46.60[207.1] [1551.83] [207.1] [1551.83] [90.68] [816.96]Age 36.19 41.02 39.13 44.10 37.11 41.09[7.96] [10.06] [8.94] [10.06] [8.24] [9.75]Unemployment rate(%) 6.68 6.61 6.68 6.61 6.39 6.46[2.39] [1.24] [2.39] [1.24] [1.39] [1.39]White 0.83 0.84 0.83 0.84 0.56 0.72High school and below 0.77 0.71 0.77 0.72 0.72 0.55Part time job 0.19 0.16 0.07 0.08 0.14 0.12Agriculture 0.02 0.02 0.06 0.06 0.02 0.02Manufacturing 0.06 0.06 0.26 0.21 0.08 0.08Service 0.42 0.55 0.43 0.44 0.78 0.81Self-employed 0.07 0.08 0.16 0.16 0.06 0.06Not working 0.43 0.29 0.09 0.13 0.06 0.03# of individual 5,202 4,063 5,202 4,063 3,984 4,770# of individual-months 97,524 64,944 97,524 64,944 73,836 85,332Note: SIPP data for years 1996–1999, 2001–2003, 2004–2006, and 2008–2012. Family income is thesum of earned income and unearned income, excluding the non-taxable mean-tested cash transfer.Family income, earned income, wealth, and EITC payment are in thousands of dollars. Familyincome, earned income, wealth, # of qualifying children, and EITC payment are based on thefamily level information in the previous year. All dollar amounts are in 2007 USD. The high-EITCgroup (treatment group) consists of those individuals that have one or more qualifying childrenand family income greater than zero and less than EITC income limit during the previous year.The low-EITC group (comparison group) comprise (1) those individuals that have family incomegreater than zero and less than EITC income limit during the previous year but have no qualifyingchild. (2) those individuals with one or more qualifying children but whose family income duringthe previous year is above EITC income limit and below $40,000. (3) childless individuals that havefamily income during the previous year is above EITC income limit and below $40,000. The incomelimit roughly corresponds to the maximum EITC-eligible income for the families with one childduring my sample period. For a married couple, the income limit is $36,000 and for single womenit is $33,000. Standard errors are reported in parentheses. Star indicates a significant differenceacross the preceding two columns after controlling individual fixed effects. *** significant at the 1percent level, ** significant at the 5 percent level, and * significant at the 10 percent level.522.8. TablesTable 2.4: Triple Differences EstimatesDependent Variable: Working(1) (2) (3) (4) (5)Panel A: Married WomenEITC ×Feb -0.0243** -0.0292** -0.0293** -0.0295** -0.0294**[0.0117] [0.0116] [0.0116] [0.0116] [0.0116]R2 0.025 0.786 0.787 0.790 0.793Baseline mean 0.47# of individual 8,625# of individual-months 162,468Panel B: Married MenEITC ×Feb -0.0046 -0.0035 -0.0035 -0.0037 -0.0031[0.0116] [0.0117] [0.0117] [0.0117] [0.0116]R2 0.018 0.705 0.705 0.708 0.711Baseline mean 0.83# of individual 8,625# of individual-months 162,468Panel C : Single WomenEITC ×Feb -0.0022 -0.0042 -0.0042 -0.0038 -0.0021[0.0092] [0.0092] [0.0092] [0.0091] [0.0091]R2 0.022 0.654 0.654 0.657 0.658Baseline mean 0.78# of individual 8,366# of individual-months 159,168Basic controls √ √ √ √ √Individual fixed effect √ √ √ √Year fixed effect √ √ √State effect √ √Other controls √Note: This table reports coefficients from triple differences regressions (equation (2.1)). Theoutcome variable L is share of weeks worked in a month defined as number of working weeksin a month divided by total number of weeks in a month. Therefore, L = 1 if working forthe full month, L = 0 if not working for the full month, and 0 < L < 1 if working for partialmonth. The outcome variables regressed on the indicator for treatment group, as interactedwith dummy for February. The treatment group consists of those individuals that have oneor more qualifying children and family income greater than zero and less than EITC incomelimit during the previous year. The comparison group comprise (1) those individuals that havefamily income greater than zero and less than EITC income limit during the previous year buthave no qualifying child. (2) those individuals with one or more qualifying children but whosefamily income during the previous year is above EITC income limit and below $40,000. (3)childless individuals that have family income during the previous year is above EITC incomelimit and below $40,000. The income limit roughly corresponds to the maximum EITC-eligibleincome for the families with one child during my sample period. For a married couple, theincome limit is $36,000 and for single women it is $33,000. All dollar values are measured in2007 USD. Column 1 control for treament group dummy, an indicator for individuals with oneor more qualifying children, an indicator for individuals with family income greater zero andbelow $36,000, month fixed effect for those who have qualifying children, month fixed effectfor those who have family income during tax year greater than zero and less than $36,000,and month fixed effect. Column 2 additionally includes individual fixed effects. Column 3additionally includes year fixed effects. Column 4 additionally includes state effects: statefixed effect, monthly state unemployment rate, state specific time trend (quadratic). Column5 additionally includes other controls: educational attainment, age, number of children below18, family wealth, industry fixed effects, industry-specific time trend, a dummy denoting theinterview month, a dummy indicating that the individual worked part-time in the previousyear, and month fixed effects specific to part-time workers. Standard errors are clusteredat the person level and reported in parentheses. *** significant at the 1 percent level, **significant at the 5 percent level, and * significant at the 10 percent level. 532.8. TablesTable 2.5: Estimates from Individual Variation in EITC PaymentsDependent Variable: Working(1) (2) (3) (4) (5)Panel A: Married WomenRefund ×Share -0.0110** -0.0144*** -0.0144*** -0.0161*** -0.0159***[0.0043] [0.0043] [0.0043] [0.0043] [0.0042]R2 0.021 0.777 0.778 0.782 0.785Baseline mean 0.47# of individual 5,933# of individual-months 112,152Panel B: Married MenRefund ×Share -0.0052 -0.0052 -0.0053 -0.0056 -0.0065[0.0043] [0.0043] [0.0043] [0.0043] [0.0042]R2 0.002 0.683 0.683 0.687 0.691Baseline mean 0.83# of individual 5,933# of individual-months 112,152Panel C : Single WomenRefund ×Share 0.0042 0.0053 0.0053 0.0056 0.00001[0.0054] [0.0053] [0.0053] [0.0053] [0.0053]R2 0.013 0.660 0.661 0.666 0.668Baseline mean 0.78# of individual 5,079# of individual-months 92,688Basic controls √ √ √ √ √Individual fixed effect √ √ √ √Year fixed effect √ √ √State effect √ √Other controls √Note: This table reports coefficients from ordinary least squares regressions (equation (2.3)). Theoutcome variable L is monthly employment status defined as number of working weeks in a monthdivided by total number of weeks in a month. Therefore, L = 1 if working for the full month, L = 0if not working for the full month, and 0 < L < 1 if working for partial month. The outcome variableis regressed on the imputed EITC amounts that an individual will receive Refund, as interactedwith share of annual EITC disbursement paid out in a given month and year Share. The sample isrestricted to EITC recipients. All dollar values are measured in 2007 USD. Column 1 controls forRefund, Share, and month fixed effects. Column 2 additionally includes individual fixed effects.Column 3 additionally includes year fixed effects. Column 4 additionally includes state effects:state fixed effects, monthly state unemployment rate, state specific time trend (quadratic). Column5 additionally includes other controls: educational attainment, age, number of children below 18,family wealth, industry fixed effects, industry-specific time trend, a dummy denoting the interviewmonth, a dummy indicating that the individual worked part-time in the previous year, and monthfixed effects specific to part-time workers. Standard errors are clustered at the person level andreported in parentheses. *** significant at the 1 percent level, ** significant at the 5 percent level,and * significant at the 10 percent level.542.8. TablesTable 2.6: Robustness ChecksDependent Variable: Working(1) (2) (3) (4) (5) (6) (7)Age Husbands’ ageUnweighted Different Stardard error No Add20–50 20–55 regression dependent group-month retail Statevariable cluster industry EITCPanel A: Specification(2.1)EITC ×Feb -0.0279** -0.0279** -0.0246** -0.0317*** -0.0294*** -0.0256**[0.0140] [0.0129] [0.0106] [0.0117] [0.0021] [0.0122]R2 0.786 0.789 0.791 0.790 0.792 0.799# of individual 7,488 7,753 8,625 8,625 8,625 8,016# of individual-months 140,904 145,968 162,468 162,468 162,468 150,048Panel B: Specification(2.3)Refund ×Share -0.0155*** -0.0163*** -0.0128*** -0.0160*** -0.0159*** -0.0149***-0.0141***[0.0045] [0.0044] [0.0039] [0.0043] [0.0045] [0.0043] [0.0042]R2 0.782 0.783 0.783 0.781 0.785 0.783 0.792# of individual 5,526 5,581 5,933 5,933 5,933 5,566 5,933# of individual-months 104,340 105,612 112,152 112,152 112,152 104,484 112,152Note: This table reports coefficients from ordinary least squares regressions (equation (2.1) and (2.3)). The outcomevariable L is share of weeks worked in a month defined as number of working weeks in a month divided by totalnumber of weeks in a month. Therefore, L = 1 if working for a full month, L = 0 if not working for a full month,and 0 < L < 1 if working for a partial month. The outcome variable is regressed on the imputed EITC amounts thatan individual will receive Refund, as interacted with share of annual EITC disbursement paid out in a given monthand year Share. The sample is restricted to EITC recipients. Column 1 presents the results for a sample with a lowerage cutoff of 50. Column 2 presents results based on a sample excluding married women whose spouses are outside ofthe age range (20 to 55). Column 3 shows the estimated coefficients from an unweighted regression. Column 4 showsthat the estimated coefficients from an regression that uses different definition of outcome variable: L = 1 if workingin any week during a month, and L = 0 otherwise. Column 5 shows the estimates using standard errors clusteredon the group-month level (4 groups x 12 months). Column 6 presents results based on a sample excluding marriedwomen who worked in the retail industry in the end of previous year. Column 7 presents results that add variation instate EITC. In Panel A, all regressions control for treatment group dummy, an indicator for individuals with one ormore qualifying children, an indicator for individuals with family income greater zero and below $36,000, month fixedeffects for those who have qualifying children, month fixed effects for those who have family income during the previousyear greater than $36,000 and less than $40,000, month fixed effects, individual fixed effects, year fixed effects, statefixed effects, monthly state unemployment rate, state specific time trend (quadratic), an indicator for interviewingmonth, educational attainment, number of children under 18, age, industry fixed effects, industry specific time trend(quadratic), family wealth, a dummy indicating part time job workers in previous year, and month fixed effects specificto part time job workers. In Panel B, all regressions controls for Refund, Share, month fixed effects, individual fixedeffects, year fixed effects, state fixed effects, monthly state unemployment rate, state specific time trend (quadratic),an indicator for interviewing month, educational attainment, number of children under 18, age, industry fixed effects,industry specific time trend (quadratic), family wealth, a dummy indicating part time job workers in previous year,and month fixed effects specific to part time job workers. Standard errors are clustered at the person level and reportedin parentheses. *** significant at the 1 percent level, ** significant at the 5 percent level, and * significant at the 10percent level.552.8. TablesTable 2.7: Subgroup Analysis Based on Tendency toward Be-ing Liquidity Constrained (Married Women)Dependent Variable: Working(1) (2)Liquid Asset Mortgage to IncomeRefund ×Share -0.0034 -0.0109[0.0043] [0.0067]Refund ×Share× Constrained -0.0135* -0.0162**[0.0077] [0.0066]Row 1 + Row 2 -0.0169*** -0.0271***[0.0042] [0.0066]R2 0.785 0.810Mean of EITC (constrained) $2,284 $2,140Mean of EITC (less constrained) $1,860 $1,981# of individual 5,933 3,579# of individual-months 112,152 62,579Note: This table reports coefficients from ordinary least squares regressions(equation (2.3)). In addition, I use Constrained to denote membership in theliquidity-constrained group and interact it with the intercept and predictedEITC amount Refund × Share. The sample is restricted to EITC recipi-ents (Married Women). The outcome variable L is share of weeks workedin a month defined as number of working weeks in a month divided by to-tal number of weeks in a month. Therefore, L = 1 if working for the fullmonth, L = 0 if not working for the full month, and 0 < L < 1 if workingfor partial month. The outcome variable is regressed on the imputed EITCamounts that an individual will receive Refund, as interacted with shareof annual EITC disbursement paid out in a given month and year Share.All dollar values are measured in 2007 dollars. All regressions control forConstrained, Refund, Share, month fixed effects, individual fixed effects,year fixed effects, state fixed effects, monthly state unemployment rate, statespecific time trend (quadratic), an indicator for interviewing month, educa-tional attainment, number of children under 18, age, industry fixed effects,industry specific time trend (quadratic), family wealth, a dummy indicatingpart time job workers in previous year, and month fixed effects specific topart time job workers. Standard errors are clustered at the person level andreported in parentheses. *** significant at the 1 percent level, ** significantat the 5 percent level, and * significant at the 10 percent level.562.8.TablesTable 2.8: Secondary Earner Channel v.s. Gender Difference ChannelDependent Variable: WorkingMarried Women Married Men Full SamplePrimary Earner Secondary Earner Primary Earner Secondary EarnerRefund ×Share -0.0067 -0.0171*** -0.0046 -0.0158 -0.0028[0.0094] [0.0048] [0.0046] [0.0113] [0.0042]Refund ×Share× Second -0.0138**[0.0058]Refund ×Share× Female 0.0028[0.0056]R2 0.648 0.767 0.576 0.776 0.762Baseline mean 0.85 0.36 0.90 0.54 0.67# of individual 1,453 4,766 4,766 1,453 11,012# of individual-months 23,520 88,632 88,632 23,508 316,980Note: This table reports coefficients from ordinary least squares regressions (equation (2.3)). The outcome variable L is share ofweeks worked in a month defined as number of working weeks in a month divided by total number of weeks in a month. Therefore,L = 1 if working for the full month, L = 0 if not working for the full month, and 0 < L < 1 if working for partial month. Theoutcome variable is regressed on the imputed EITC amounts that an individual will receive Refund, as interacted with shareof annual EITC disbursement paid out in a given month and year Share. In the last column, based on equation (2.3), I alsointeract the intercept, predicted monthly EITC amount, and a set of month dummies with a indicator for female (Female) and adummy indicating secondary earner (Second), respectively. The sample is restricted to EITC recipients. All regressions control forFemale, Second, Refund, Share, month fixed effect, month fixed effect specific to female, month fixed effect specific to secondaryearner, individual fixed effect, year fixed effect, state fixed effect, monthly state unemployment rate, state specific time trend(quadratic), an indicator for interviewing month, educational attainment, number of children under 18, age, industry fixed effect,industry specific time trend (quadratic), family wealth, a dummy indicating part time job workers in previous year, and monthfixed effect specific to part time job workers. Standard errors are clustered at the person level and reported in parentheses. ***significant at the 1 percent level, ** significant at the 5 percent level, and * significant at the 10 percent level.572.8. TablesTable 2.9: Month-to-Month Labor Force Transitions (Married Women)Month-to-Month Labor Force Transitions(1) (2) (3) (4) (5) (6)Dependent Working to Nonworking toWorking toWorking to Working to Working toVariable Nonworking Working Unpaid Temporary Unemployed out ofLeave Layoff Labor ForceEITC ×Feb 0.0124 -0.0021 0.0108* -0.0003 0.002 0.00003[0.0086] [0.0073] [0.0056] [0.0038] [0.0036] [0.0052]R2 0.071 0.069 0.074 0.056 0.065 0.062Baseline mean 0.016 0.018 0.004 0.002 0.003 0.007# of individual 8,625 8,625 8,625 8,625 8,625 8,625# of individual-months 162,468 162,468 162,468 162,468 162,468 162,468Note: This table reports coefficients from triple differences regressions (equation (2.1)). The sample isrestricted to married women. The outcome variables across the columns are presented as follows: 1) anindicator for whether an individual work in the third week in the last month and stopped working in thethird week in the current month; 2) an indicator for whether an individual did not work in the third weekin the last month and started working in the third week in the current month; 3) an indicator for whetheran individual worked in the third week in the last month and then took leave without pay in the thirdweek in the current month; 4) an indicator for whether an individual worked in the third week in the lastmonth and then had temporary layoff without pay in the third week in the current month; 5) an indicatorfor whether an individual worked in the third week in the last month and become unemployed in the thirdweek in the current month; 6) an indicator for whether an individual work in the third week in the lastmonth and moved out of the labor force in the third week in the current month; All regressions controlfor treament group dummy, an indicator for individuals with one or more qualifying children, an indicatorfor individuals with family income greater zero and below $36,000, month fixed effects for those whohave qualifying children, month fixed effects for those who have family income during the previous yeargreater than $36,000 and less than $40,000, month fixed effects, individual fixed effects, year fixed effects,state fixed effects, monthly state unemployment rate, state specific time trend (quadratic), an indicatorfor interviewing month, educational attainment, number of children under 18, age, industry fixed effect,industry specific time trend (quadratic), family wealth, a dummy indicating part time job workers inprevious year, and month fixed effects specific to part time job workers. Standard errors are clustered atthe person level and reported in parentheses. *** significant at the 1 percent level, ** significant at the 5percent level, and * significant at the 10 percent level.58Chapter 3Patient Cost-Sharing andHealthcare Utilization inEarly Childhood: Evidencefrom a RegressionDiscontinuity Design3.1 IntroductionHealth conditions and medical treatments in early childhood are widely be-lieved to have a substantial impact on health and labor outcomes in adult-hood (Bharadwaj et al., 2013; Almond et al., 2011; Currie, 2009; Almond,2006; Case et al., 2005; Currie and Madrian, 1999).57 On the other hand,young children also bring about sizeable medical costs for their parents sincethey are vulnerable to diseases.58 In line with this evidence, many publichealth insurance programs around the world subsidize healthcare service foryoung children by requiring relatively low patient cost sharing from this agegroup.59 For example, the United States regulates the level of patient cost57Several recent studies (Bharadwaj et al., 2013; Almond et al., 2011) present convincingevidence showing that early-life medical treatments can reduce mortality and even resultin better long-run academic achievements in school. That is, health intervention in earlychildhood could be an investment with high returns.58For example, in Taiwan, the number of outpatient visits for children under 3 years ofage is around 20 per year. Compared with adults (12 visits per year), this age group hasan especially high demand for healthcare service.59That is, the share of healthcare costs paid out-of-pocket by the patient is lower.593.1. Introductionsharing in Medicaid and the Children’s Health Insurance Program (CHIP)to ensure that children from middle and low-income families can afford es-sential medical treatment.60 Recently, due to tight budgets, many stategovernments have considered raising the level of patient cost sharing forMedicaid and CHIP, which has led to many debates on the possible im-pact.61 Similarly, national health insurance in Japan and Korea offer chil-dren under 6 years of age a lower level of patient cost sharing than thoseabove age 6, to promote health investments in early childhood.62Low patient cost sharing has clear trade-offs. On one hand, low costsharing can protect patients from financial risk induced by huge medicalexpenses. Better financial protection can help households smooth out theirconsumption and then increase the welfare of households. In addition, lowcost sharing can make healthcare service affordable (i.e. income effect). Es-pecially, low-income families might need healthcare service but cannot affordit because they may be liquidity constrained. On the other hand, low costsharing could induce patients to overuse healthcare service. Since insuredpeople do not pay the full cost of healthcare services, the optimal utilizationof healthcare for an individual would be larger than the social optimum,leading to a loss of social welfare (i.e. moral hazard). To determine theappropriate level of cost sharing for children, we need to understand howcost sharing affects children’s demand for healthcare service, namely, priceelasticities of healthcare utilization.60The federal requirement for Medicaid eligibility varies according to the children’s age.For children under age 6 (young children), Medicaid eligibility requires family incomesto be lower than 133% of the federal poverty level (FPL). For children ages aged 6–19(older children), family incomes is required to be below 100% of FPL. Thus, the coverageof Medicaid for children under 6 is much higher than for those above 6.61Since the passing of the Deficit Reduction Act (DRA) of 2005, states have had theright to increase the level of cost sharing in public health insurance programs, such asMedicaid and CHIP, for specific populations and medical services (Selden et al., 2009).62National health insurance in Japan covers almost all medical services, such as out-patient and inpatient care, for all citizens. The patient cost sharing for children underage 6 (pre-school age) is 20% of the original healthcare cost. For children above age six(school-age), patient cost sharing rises to 30% of medical costs. More details of Japanesenational health insurance can be found at this web page:http://www.shigakokuho.or.jp/kokuho_sys/kokuho_en.pdf. In Korea, their national health insurance exempts costsharing for inpatient services for children under age 6.603.1. IntroductionTo date, very little is known about how young children’s demand forhealthcare services reacts to changes in the level of patient cost sharing.Previous studies mainly focus on price elasticities of adults’ demand forhealthcare (Cherkin et al., 1989; Selby et al., 1996; Rice and Matsuoka,2004; Chandra et al., 2010a; Chandra et al., 2010b; Chandra et al., 2014;Shigeoka, 2014).63 However, these estimates might not be valid for thedemand for healthcare services of young children for two reasons.First, the types of healthcare services used by adults and children arequite different. Children’s outpatient visits are rarely for chronic diseasesand mostly for acute diseases, which need timely treatment and should notbe sensitive to a price change. In addition, the majority of children’s inpa-tient admissions are for respiratory diseases, which can be treated with bedrest or medication. Previous studies have found the demand for this type ofinpatient care is not price sensitive.64Second, healthcare interventions in early childhood could substantiallybenefit an individual’s later life, as addressed by recent studies (Bharadwajet al., 2013; Almond et al., 2011). Given such high returns, parents might notbe willing to adjust their children’s medical care in response to price changes.Based on the above two reasons, we expect healthcare utilization for youngchildren to be less price sensitive than that for an older demographic group.Credible estimates of price elasticity for children still rely on evidencefrom the RAND Health Insurance Experiment (RAND HIE), which wasan influential randomized social experiment conducted in the mid 1970s.6563Shigeoka (2014) exploited the sharp reduction in patient cost sharing at age 70 inJapan and applied a regression discontinuity (RD) design to estimate the price elasticityof outpatient and inpatient visits by the elderly. He found the use of both health servicesto respond strongly to the price change with obvious drops at age 70. The estimatedprice elasticities were around −0.17 (outpatient) and −0.15 (inpatient). Chandra et al.(2014) used a cost sharing reform in Massachusetts as an exogenous variation in priceand obtained a price elasticity of healthcare expenditure of around −0.15 for low-incomeadults.64Shigeoka (2014) found that inpatient admissions for non-surgery were less price sen-sitive than those for surgery, especially elective surgery (e.g. cataract surgery). Also, hefound that admissions for the respiratory diseases typically treated with bed rest or med-ication did not respond to a change in cost sharing at age 70 in Japan. Card et al. (2008)obtained similar findings for Medicare eligibility at age 65 in the United States.65Before the passing of the DRA of 2005, state governments had little right to adjust the613.1. IntroductionIts sample comprised people of 62 years of age or under and randomly as-signed participating households to different levels of patient cost-sharing(ranging from free care to 95% cost-sharing). The RAND HIE providedestimates of the price elasticity of healthcare utilization for children under14 years of age (Leibowitz et al., 1985; Manning et al., 1981). It found thathigher patient payments significantly reduced children’s outpatient expendi-ture and utilization, but found mixed evidence of the cost sharing effect onchildren’s demand for inpatient care.66 The estimated price elasticity of thetotal healthcare expenditures was around −0.12.67 However, the sample sizefor children in the RAND HIE was not big. Some estimates or subgroupanalyses were not precise enough to confirm the presence or absence of acost-sharing response (Leibowitz et al., 1985).68 Additionally, the RANDHIE evidence is now over 30 years old. Both medical technology and themarket structure have changed considerably during the past three decades.The varying healthcare environment could affect the way in which demandlevel of patient cost sharing in their public insurance programs (i.e. Medicaid and CHIP)for children. Thus, there is little evidence on the effect of cost sharing on children’sdemand for healthcare service. To the best of our knowledge, only one recent study (Senet al., 2012) has used the copayment change in the CHIP in Alabama, to analyze thisissue. However, their study mainly relied on pre-/post-policy analysis, which suffers fromthe an estimation bias due to uncontrolled trends in children’s medical utilization.66For children under age 4, the RAND HIE found that inpatient care was price sensitive.Children assigned to a free plan had a significantly higher rate of inpatient admission thanchildren assigned to 95% cost-sharing. For children aged between 5 and 13, no consistentpattern of a cost sharing effect on inpatient use was found (Leibowitz et al., 1985).67The health insurance contracts in RAND HIE adopted non-linear pricing, which makesestimating price elasticity challenging. Specifically, the insurance plans required initialcost-sharing (free care, 25%, 50% and 95%) but had an annual stop-loss (Maximum DollarExpenditure), in that the total out-of-pocket medical costs per year could not exceed 4,000USD. Thus, the patient cost-sharing would fall to zero when annual out-of-pocket medicalcosts reached 4,000 USD. Such non-linear pricing imposes on patients different prices forthe same health care at different times in the year. To summarize the estimated priceelasticity, RAND researchers defined four kinds of price that patients respond to whenmaking their healthcare decision: (1) the current “spot” price, (2) the expected end-of-year price, (3) the realized end-of-year price, and (4) the weighted-average of the pricepaid over a year (Aron-Dine et al., 2013). The price elasticity of children’s healthcarementioned here is calculated by defining price as definition (1).68As Leibowitz et al. (1985) comment: “Because hospitalizations for children are in-frequent, our estimates of hospital use have wide confidence intervals and we can be lesscertain than for outpatient care about the presence or absence of a cost sharing response.”623.1. Introductionfor healthcare service changes in response to differences in price. There-fore, our paper fills this gap by providing the latest estimates of the priceelasticity of children’s healthcare utilization.In this paper, we exploit a sharp increase in patient cost-sharing in Tai-wan at the 3rd birthday that results from young children “aging out” of thecost-sharing subsidy. On average, turning age 3 causes a small increase inprice per outpatient visit by about 60 NTD (or roughly 2 USD).69 In addi-tion, the increase in outpatient price at 3rd birthday is not uniform acrossdifferent healthcare providers. Turning age 3 causes larger increase in out-patient price for teaching hospitals than clinic and community hospitals.This is because patients do not pay a copayment before the 3rd birthday.After the 3rd birthday, patients start to pay a copayment for each outpa-tient visit. Copayments for teaching hospitals are much larger than clinicsand community hospitals. Finally, turning age 3 results in a much largerincrease in price per inpatient admission from zero to 1,300 NTD (i.e. 40USD). We use a regression discontinuity (RD) design to examine the causaleffect of patient cost sharing on children’s demand for healthcare serviceby comparing the expenditure and utilization of healthcare for children justbefore and after the 3rd birthday.We obtain three key findings. First, a small increase in outpatient priceat the 3rd birthday results in a sizeable reduction in outpatient utilization.The number of outpatient visits drops sharply at the 3rd birthday. Theimplied price elasticity of outpatient utilization is around −0.10. Second, theprice increase at age 3 not only results in fewer outpatient visits (extensivemargin) but also reduces the expenditure of each visit (intensive margin),namely, it induces patients to switch from high to low-quality providers (e.g.substitution of teaching hospitals with clinics or community hospitals). Wefind turning age 3 (i.e. paying copayment) reduces visits to teaching hospitalsby 50% and most of the foregone visits are for less severe conditions.70Further investigating possible heterogeneous effects in detail, we also find691 USD is equal to 32.5 NTD in 2006 prices.70This result is due to copayments varying between health providers in Taiwan. We willdiscuss this issue in more detail in Sections 3.2 and 3.5.633.1. Introductionpreventive care and mental health services to have larger price responsesthan healthcare for acute respiratory diseases. Third, in sharp contrast tooutpatient services, the demand for inpatient services does not respond tothe price change at the 3rd birthday even if change in the inpatient price atage 3 is much larger than that in the outpatient price in terms of its level andpercentage change. The estimated price elasticity of inpatient utilizationis close to zero (about −0.004). This finding implies children’s inpatientcare could be quite necessary. Parents are unwilling to reduce a children’sinpatient care even through they pay higher price after the children’s 3rdbirthday. The above findings suggest that the level of patient cost sharingfor young children should differ depending on the healthcare service. Forexample, providing free inpatient care for young children does not stimulateexcessive hospital use (i.e. moral hazard) but it might substantially reducethe financial risk for households. On the other hand, having a certain levelof copayment for children’s outpatient care is essential to avoid overuse ofoutpatient care, especially, at teaching hospitals.This paper contributes to the research on patient cost sharing in threeways. First, the unique setting in Taiwan makes our estimates free of thebias from a change in the composition of enrollees induced by the changein cost sharing. Several recent US studies (Chandra et al., 2010a; Chandraet al., 2010b; Chandra et al., 2014) have used a quasi-experimental designby exploiting a change in the copayments of one health insurance plan andusing unchanged insurance plans as a control group. However, the change incost sharing could also affect people’s decision to enroll in insurance plans.Such self-selection behavior could bias the elasticity estimates. For exam-ple, a larger proportion of people with less price sensitivity may continuetheir enrollment after the a cost-sharing increase, which may bias the priceelasticity estimates toward zero. The Taiwanese National Health Insurance(NHI) is a single-payer scheme and every citizen is required to join the pro-gram.71 Thus, our elasticity estimates are free of bias from change in thecomposition of the enrollees after the cost-sharing change.71The only exceptions are citizens who lose their citizenship, die or are missing for morethan six months.643.1. IntroductionSecond, our paper provides credible and transparent estimates of priceelasticities of healthcare utilization for young children, which is largely unex-plored in the previous literature. Our RD design offers a unique opportunityto obtain estimates in a local randomized experiment. The comparison atthe 3rd birthday convincingly isolates the impact of patient cost sharing onhealthcare utilization from other factors because there are no confoundingfactors at the 3rd birthday.72In addition, the data we use in this paper is administrative insuranceclaim data that contains all NHI records of healthcare payments and use forchildren under 4 years of age in Taiwan during our sample period.73 Com-pared with survey data, administrative data have a number of advantages,such as much less measurement error and larger sample sizes. These featuresalso allow us to get an accurate measure of the key variable in this paper —patient’s age at visit. Prior studies using survey data find that there is sub-stantial heaping in the reported birth dates of patients, which might reflectmeasurement error of patients’ ages.74 Also, our large sample size allowsus to get precise estimates of the heterogeneity in the cost-sharing effectacross different subgroups or types of healthcare that could not be analyzedprecisely in the RAND HIE because of its limited sample of children.Finally, this paper presents the first evidence on the effect of differen-tial copayments for outpatient care on the choice of healthcare providers inTaiwan. NHI sets higher copayments for the visits to hospitals than thoseto clinics. This is because there is no gatekeeper system in Taiwan. Pa-tients can choose healthcare providers freely without referral from primarycare physicians. This freedom of choice might make some patients whoseillness can be treated in clinics overuse outpatient resource in hospital (i.e.moral hazard) and crowd out those who have to get treatments in hospitals.72In Taiwan, turning age 3 does not coincide with any confounding factors, such as ageof starting school or a recommended immunization schedule. We will discuss this issue inSection 3.4.7399% of the Taiwanese population is covered by NHI. Furthermore, NHI covers almostall medical services. We will discuss this issue in more detail later.74Shigeoka (2014) finds that respondents in Japanese Patient Survey tend to report thefirst day of the month as their birthday when they forget the exact date of birth.653.2. Policy BackgroundNHI uses differential copayment to lead patients to choose their healthcareproviders based on severity of illness and allocate outpatient resource inhospitals to the patients who need them most. We examine the effective-ness of differential copayments by comparing patient’s choice of providersbefore the 3rd birthday (i.e. no copayment) and after the 3rd birthday (i.e.differential copayment).The rest of the paper is organized as follows. Section 3.2 gives a briefoverview of the institutional background. In Section 3.3, we discuss ourdata and sample selection. Section 3.4 describes our empirical strategy. InSection 3.5, we analyze the main results. Section 3.6 provides concludingremarks.3.2 Policy Background3.2.1 National Health Insurance in TaiwanIn March 1995, Taiwan established the NHI, which is a government-run,single-payer scheme administered by the Bureau of National Health Insur-ance. Prior to this, health insurance was provided through three main oc-cupational forms — labor insurance for private-sector workers, governmentemployee insurance, and farmers’ insurance. These systems accounted foronly 57% of the Taiwanese population (Lien et al., 2008). The remainder ofthe population were not employed: people over 65, children under 14, andunemployed workers. The implementation of the NHI raised the coveragerate of health insurance sharply to 92% by the end of 1995, and since 2000,it has stayed above 99%.The NHI provides universal insurance coverage, with almost all medicalservices covered, such as outpatient, inpatient, dental, and mental healthservices, prescription drugs, and even traditional Chinese medicine. TheNHI classifies healthcare providers into four categories based on accredita-tion: major teaching hospitals, minor teaching hospitals, community hospi-tals, and clinics.75 As in most Asian countries, enrollees are free to choose75The clinic is similar to the physician’s office in Canada and the US.663.2. Policy Backgroundtheir care providers and do not need to go through a general practitioner(i.e. family physician) to obtain a referral. For example, patients can di-rectly access specialists in a major teaching hospital without a referral. Inother words, the NHI does not adopt a gatekeeper system.763.2.2 Patient Cost-SharingPatient cost sharing in Taiwan comprises two parts: (1) the copayment(coinsurance);77 (2) other non-NHI-covered medical costs (e.g. a registrationfee for an outpatient visit).78Cost-Sharing for Outpatient CareWith respect to outpatient care, a patient pays a copayment plus a regis-tration fee for each visit.79 If a physician prescribes a drug at a visit andthe drug cost is above 100 NTD, the patient also needs to pay a share ofthe cost of the prescription drug, which is 20% of total drug cost. However,most visits for children under age 3 have drug costs below 100 NTD so pa-tients usually do not pay for their prescription drug.80 Compared with thecopayment, the average out-of-pocket cost for outpatient prescription drugs(under age 3) is quite small, at only 2.5 NTD per visit.81The copayments are based on a national fee schedule. In general, a highercopayment is set for the health providers that have higher accreditation.8276For example, the National Health Service (NHS) in the United Kingdom adopts agatekeeper system. Patients cannot directly obtain outpatient services at hospitals. In-stead, they need to get a referral from a general practitioner. Provincial Health Insurancein Canada adopts a similar system.77A copayment is a fixed fee paid by the insurance enrollee each time a medical service isaccessed. Coinsurance is a percentage of the medical payment that the insured person hasto pay. The NHI adopts copayments for outpatient care and coinsurance for outpatientprescription drugs and inpatient care.78More discretionary healthcare, such as plastic surgery, sex reassignment surgery andassisted reproductive technology, etc., are not covered by the NHI. Patients have to paythe full cost for these services.79Both are fixed amounts.80If drug cost is under 100 NTD, a patient has no out-of-pocket cost.81The average drug cost per visit is only 61 NTD, which is under 100 NTD and thus,patients do not pay any out-of-pocket cost at most visits.82The NHI in Korea has a similar cost-sharing policy. Patients have to pay 40–50% of673.2. Policy BackgroundThe first rows of Panel A in Table 3.1 summarize the copayments for fourtypes of providers during our sample period (2005 to 2008). To treat thesame illness, a major teaching hospital charge a patient a copayment of 360NTD (i.e. 11 USD) per outpatient visit but the copayment for one clinicvisit is only 50 NTD (1.5 USD).83The spirit of this design is to use the differential copayments to guidepatients to properly choose their health providers based on the severity ofan illness so as to better allocate medical resources to the patients who needthem most. This design is needed because patients in Taiwan (and otherAsian countries) have no restrictions on their choice of healthcare providers.For identical diagnosis, patients might get better and more treatments fromthe outpatient care in hospital. For example, patients could choose a teach-ing hospital or a clinic to treat a cold. But a teaching hospital could providemore tests and prescribe better drugs than a clinic. Table 3.5 comparesmajor teaching hospitals, minor teaching hospitals, community hospitals,and clinics in terms of composition of medical expenses and composition ofpatients. In general, a patient pays higher share of medical expense for onevisit to a teaching hospital than a clinic. A teaching hospital also providesmore medical service than a clinic. The average medical expenses per teach-ing hospital visit is 987 NTD, which is three times as much as that per clinicvisit. This is because a physician in a teaching hospital can conduct morehealth examinations (e.g. X-ray inspection) and medical treatments (e.g.therapeutic radiology) than one in a clinic. If there was no difference in thelevel of patient cost sharing between teaching hospitals and clinics, patientsmight overuse the limited medical resources of the hospitals and crowd outother patients whose illnesses could only be treated at hospitals.In addition to the copayment, the patient must also pay a registration feefor each outpatient visit, which is not covered by the NHI. The registrationfee reflects the health provider’s administrative costs and is determined bytotal medical costs when visiting hospitals but only 15–30% when visiting clinics.83For more detailed information about the copayment schedule, please see the note inTable 3.1. A reimbursement is also paid according to the provider’s accreditation. That is,major teaching hospitals can obtain the highest reimbursement for their medical services.683.2. Policy Backgroundthe provider.84Cost-Sharing for Inpatient CareFor inpatient admissions, the patient cost sharing takes place through coin-surance. Depending on the length of the stay and the type of admission(acute or chronic admission), the coinsurance rate is 10% to 30% of the to-tal medical costs per admission. For example, a patient must pay 10% ofthe hospitalization costs for the first 30 days they stay in an acute admis-sion unit and 20% for the next 30 days. Almost all inpatient admissionsfor young children (99.5%) are acute admissions and the length of a stayin our sample is always within 30 days.85 Thus, coinsurance rates for mostadmissions are around 10%. Panel B in Table 3.1 lists the coinsurance ratesfor inpatient services.86Because inpatient care usually results in larger financial risks than outpa-tient care, the NHI has a stop-loss policy (i.e. maximum out-of-pocket cost)for inpatient admissions. The out-of-pocket cost must be no greater thanthe stop-loss, which is calculated annually as 10% of the gross domesticproduct per capita in Taiwan. The NHI covers all costs above the stop-loss.87 According to NHI statistics, very few patients (less than 1%) reachthis stop-loss, so the non-linearity imposed by it should not seriously biasour estimates of price elasticity.88 Moreover, in contrast to health insuranceplans in the US and other countries, the NHI does not require patients to84Our main dataset lacks this information. However, the NHI has another databasethat provides information about the registration fees of all health providers during oursample period (2005–2008). Major teaching hospitals usually charge 150 NTD, minor andcommunity hospitals 100 NTD, and clinics 50 NTD. We use this information to imputethe registration fees for the four types of providers.85In our empirical analysis, we limit our estimated sample for inpatient services to thecases with acute admissions with length of stay within 30 days.86Some parents might buy private health insurance for their children. Such insurancecan cover the out-of-pocket costs of inpatient care. Nevertheless, private health insurancefor young children is not popular in Taiwan.87In 2008, the annual maximum out-of-pocket cost is about 50,000 NTD.88This is because the NHI waives the cost-sharing for patients with catastrophic illnesses(e.g. cancer), who would have a greater probability of reaching the stop-loss if their costsharing were not waived.693.2. Policy Backgroundpay deductibles before insurance coverage begins. The above two featuressubstantially simplify our computation of the price elasticities.893.2.3 Change in Patient Cost Sharing at the 3rd BirthdayTo reduce the financial burden on parents and ensure that every child ob-tains essential medical treatment in her early childhood, in March 2002, theTaiwan government enacted the Taiwan Children’s Medical Subsidy Pro-gram (TCMSP). This program, through subsidies, exempts all copaymentsand coinsurance for outpatient visits, outpatient prescription drugs, inpa-tient admissions, and emergency room visits for children under the age of3. A patient loses eligibility for subsidies at her 3rd birthday. Since theimplementation of TCMSP, a patient under 3 years of age has only had topay the medical costs not covered by the NHI (e.g. the registration fee foroutpatient care and other non-covered medical services).90Figure 3.1 plots the observed age profile of average out-of-pocket costper outpatient visit and that of average out-of-pocket cost per inpatient ad-mission (180 days before and after the 3rd birthday).91 Figures A.3 and 3.1breveal that patients experience a sharp increase in price for both outpatientand inpatient services at their 3rd birthday. Especially for inpatient services,the out-of-pocket cost per admission suddenly rises from zero to almost 1,300NTD, which could bring about sizeable financial risk to a household withyoung children turning 3 years old.92Note that the observed price changes per visit at the 3rd birthday are89In health insurance, the deductible is the amount that an insured person has to paybefore an insurer (e.g. the insurance company) starts to pay.90If they use medical services not covered by the NHI, they will have to pay all expenses.However, the NHI does cover most health services. Those that are not covered are mostlyquite discretionary, such as plastic surgery, sex reassignment surgery and assisted repro-ductive technology, etc.91Each dot represents the ten days average price of each outpatient visit (inpatientadmission) at a given age. The line is obtained by fitting a linear regression to the agevariables fully interacted with a dummy indicating whether the child is age 3 or older.92The average wage rate is around 225 NTD (i.e. 7 USD) per hour in 2006. The averagemonthly household earned income is around 45,000 NTD (or roughly 1,400 USD) in 2006.Therefore, out-of-pocket costs for an inpatient admission can account for 3 percent of ahousehold’s average monthly income.703.2. Policy Backgroundendogenous. Especially for outpatient services, the price change at the 3rdbirthday is larger for visits to a teaching hospital than to a clinic or commu-nity hospital. For example, the price per visit for a major teaching hospitalincreases by 240% (from 150 to 510 NTD) at the 3rd birthday and the pricefor a minor teaching hospital rises by 240% (from 100 to 340 NTD). How-ever, the visit price for a clinic only increases by 100% (from 50 to 100NTD). In other words, the TCMSP indeed subsidizes outpatient services inteaching hospitals much more than those in clinics or community hospitals.Therefore, patients might also change their choices of providers at their 3rdbirthday, which could make the observed out-of-pocket cost per visit afterthe 3rd birthday endogenous (i.e. already reflected in the change in choiceof provider). To obtain the exogenous price change at the 3rd birthday, weneed to fix the utilization of each type of provider.Table 3.2 presents the weighted average out-of-pocket cost per visit be-fore and after the 3rd birthday.93 The weights are the average daily uti-lization of each type of provider 90 days before the 3rd birthday. Thus,the numbers in the first row are the actual weighted average out-of-pocketcosts per visit before the 3rd birthday and the numbers in the second roware counterfactual weighted average out-of-pocket costs per visit after the3rd birthday, which uses the share of utilization of providers at age 2 (i.e.90 days before the 3rd birthday) as weights. In this way, we can computethe difference between rows (1) and (2) to obtain the exogenous change inout-of-pocket costs per visit/admission at the 3rd birthday. Table 3.2 showsthat the average price of outpatient visits rises by more than 100% (from58.9 to 132.7 NTD) at the 3rd birthday, and the average price of inpatientadmissions jumps sharply from zero to 1296 NTD. To sum up, in terms ofboth the level and the percentage change, the out-of-pocket cost for each in-patient admission sees a much larger increase than that for each outpatientvisit.93The bandwidth is 90 days. Thus, we use out-of-pocket cost per visit/admission withinthe 90 days before and after the 3rd birthday to obtain the estimates in Table 3.2.713.3. Data and Sample3.3 Data and Sample3.3.1 DataTo implement our empirical analysis, we need the following information: (1)the enrollee’s exact age to the day at the time of a visit;94 (2) the utilizationof the outpatient or inpatient services; (3) the expenditures of the outpatientor inpatient services. We use unique claims data from Taiwan’s NationalHealth Insurance Research Database (NHIRD), which contains detailed in-formation about patient’s out-of-pocket costs, total healthcare expendituresand healthcare utilization for each outpatient visit (inpatient admission) ofall NHI enrollees in Taiwan.95 In addition, the NHIRD includes the exactdates of outpatient visits (inpatient admissions) and the exact birth date ofevery enrollee, which allows us to precisely measure the children’s ages indays for our RD design.For our purposes, we linked information from four types of files in theNHIRD: outpatient claims files, inpatient claims files, enrollment files, andprovider files. First, outpatient (inpatient) claims files record informationabout payments and medical treatments for each visit. These files con-tain the enrollee’s ID and birth date, the hospital or clinic ID, the date ofthe visit, the total healthcare expenditures, total out-of-pocket costs, di-agnosis96, and medical treatment.97 Second, we use the enrollee’s ID tomerge the enrollment files and obtain each enrollee’s demographic informa-tion, such as gender, household’s monthly income, number of siblings, andtown of residence. Finally, we use the hospital or clinic ID to link with theinformation (e.g. provider’s accreditation) in the provider files.94That is, we measure age in days.95Due to privacy concern, NHIRD only allows at most 10% sampling for each researchapplication. Thus, we only use claims data of sample with age 2 and 3 during 2005–2008and 1997–2001.96Diagnoses are recorded in five digits according to the ICD9 (International Classifica-tion of Diseases, Ninth Revision, Clinical Modification).97Inpatient claims files have further information about length of stay.723.3. Data and Sample3.3.2 SampleTo avoid the effect of variation in the cohort size on our estimation, wefocus on the healthcare use from the same cohort (fixed panel). Our origi-nal sample is all NHI enrollees born between 2003 and 2004. The originalsample size is 435,206 (see Table 3.3).98 We further restrict our sample tothose enrollees who were continuously registered in the NHI while aged 2and 3, which reduces the sample size by 8,619. In addition, we eliminatethose enrollees in the sample with cost-sharing waivers, such as children withcatastrophic illnesses and children from very low-income families, since thesechildren would not experience any price change when turning 3. The aboveprocedure reduces our original sample by 5.7%, making the final sample sizefor estimation 410,517. Table 3.3 provides summary statistics of the charac-teristics of the enrollees at age 3, in the original sample and the final sampleused in our empirical analysis. We find that the selected characteristics arequite similar between the two samples.We use 2005–2008 NHIRD data to obtain all records of outpatient visitsand inpatient admissions of these children when aged 2 or 3.99 FollowingLien et al. (2008), we also exclude visits relating to dental services, Chinesemedicine, and health check-ups with a copayment waiver.100Table 3.4 provides the descriptive statistics for the outpatient visits andinpatient admissions and compares their characteristics within 90 days be-fore and after the 3rd birthday.101 We find that children use more outpatientand inpatient care before their 3rd birthday. Most young children visit clin-ics for outpatient services. However, they tend to visit teaching hospitalsmore frequently before their 3rd birthday than after it.98Since 99% of Taiwanese are covered by the NHI, this sample represents nearly theentire population of children born between 2003 and 2004 in Taiwan.99The sample period was chosen because children born in 2003 are aged 2 in 2005–2006and children born in 2004 are aged 3 in 2007–2008.100The NHI provides nine health check-ups with copayment waiver for children under theage of 7. Since patient cost sharing for these visits does not change at the 3rd birthday,we eliminate them to avoid biased estimations.101We make this choice because our main results use 90 days as the bandwidth.733.4. Empirical Specification3.4 Empirical SpecificationOur identification strategy is similar to that in recent studies utilizing an“age discontinuity” to identify the insurance coverage effect (Card et al.,2008; Card et al., 2009; Anderson et al., 2012 ) or patient cost-sharing effect(Shigeoka, 2014) on medical utilization by adults or the elderly. We are thefirst to apply the RD design to study the impact of patient cost sharing onhealthcare utilization and expenditure for young children. The general formof our RD regression is as follows:Yi = β0 + β1Age3i + f(ai; γ) + εi (3.1)where Yi is the outcome of interest for the child i, namely (1) the num-ber of outpatient visits or inpatient admissions; (2) the total expenditureof outpatient or inpatient care; (3) the expenditure per outpatient visit (in-patient admission) at a given age. The variable ai is child i’s age and ismeasured in days. The variable Age3i is a treatment dummy that capturesthe higher level of patient cost sharing (i.e. loss of cost-sharing subsidy) atthe 3rd birthday and is equal to one if child i is age 3 or older. The 3rdbirthday is the 1096th or 1095th day after birth.102 The key assumption ofthe RD design is that the age profile of the healthcare utilization is smooth(continuous). Thus, we assume f(ai; γ) to be a smooth function of age withparameter vector γ that accommodates the age profile of the outcome vari-ables. The εi is an error term that reflects all the other factors that affectthe outcome variables. Our primary interest is β1, that measures any de-viation from the continuous relation between age and the outcomes Yi atchild i’s 3rd birthday (i.e. when the treatment variable switches from 0 to 1).If no other factors change discontinuously around the child’s 3rd birthday,that is, E[εi|ai] is continuous at age 3, β1 represents the causal effect of thehigher level of patient cost sharing on the expenditure and on utilization of102Since 2004 is leap year, its February has 29 days. For the children born before 2004February 29th, their 3rd birthday would be 1096th day after birth (365 x 3 + 1 = 1096).For those born after 2004 March 1st, their 3rd birthday would be 1095th day after birth.743.4. Empirical Specificationyoung children’s healthcare. In general, there are two ways to estimate β1,typically referred to as the global polynomial approach and the local linearapproach (Lee and Lemieux, 2010).In the global polynomial approach, we can use all available data to cap-ture the age profile of healthcare utilization f(ai; γ) by using a flexible para-metric function (e.g. in our analysis we use a third-order polynomial ofage).103 One caveat of this approach is that an incorrect functional form forthe regression could create a biased estimate of β1. To avoid a misspecifi-cation bias, we adopt a local linear regression as our main specification andpresent the global polynomial estimates for comparison.In the local linear approach, we capture the age trend of the healthcareuse f(ai; γ) by estimating a linear function over a specific narrow range ofdata on either side of the threshold (i.e. 3rd birthday). The local linearestimates of the treatment effect are the differences between the estimatedlimits of the outcome variables on each side of the discontinuity. Our baselinespecification is the following local linear regression:Yi = β0 + β1Age3i + γ1(ai − 1096) + γ2Age3i(ai − 1096) + εi (3.2)In practice, we obtain the estimated treatment effect β1 by allowing theslope of the age profile to be different on either side of the 3rd birthday,by interacting the age variable fully with the intercept and Age3i. Also, werecenter the age variable to the 3rd birthday to make β1 directly representthe treatment effect at the 3rd birthday.104 The equation (3.2) is estimatedvia weighted least squares using a triangular kernel (i.e. giving more weightto the data points close to the 3rd birthday). We restrict our sample tothe 90 days before and after the 3rd birthday. The choice of bandwidthand the computation of the standard errors of the discontinuity estimatesare important issues for local linear estimation. In Table B.3, we show that103We have all NHI records of medical utilization within 365 days before and after eachindividual’s 3rd birthday (i.e. from 2nd birthday to their 4th birthday).104For the children born before 2004 February 29th, age variable is ai − 1096. For thoseborn after 2004 March 1st, age variable is ai − 1095.753.4. Empirical Specificationour main estimates are robust to various choices of bandwidth and differentmethods of calculating the standard errors.105Following Card et al. (2009), Anderson et al. (2012) and Lemieux andMilligan (2008), we collapse the individual-level data into age cells (measuredin days), which gives us the same estimates as the results from the individual-level data but substantially reduces the computational burden. Therefore,our regressions are estimated on day-level means for each day of age:Ya = β0 + β1Age3 + γ1(a− 1096) + γ2Age3(a− 1096) + εa (3.3)We also take logs of our dependent variables to allow β1 to be interpretedas the percentage change in the dependent variables. That is, the dependentvariables for the RD estimation are the log of total outpatient (inpatient)expenditure, the log of the total number of outpatient visits (inpatient ad-missions), and the log of outpatient (inpatient) expenditure per visit, at eachday of age. The most important assumption for our RD estimation is that,except for the higher level of patient cost sharing, there is no change in anyother confounding factors that affect the demand for healthcare services at105Deciding how “narrow” a range of data to use, namely, choice of bandwidth, is criticalto local linear estimation. If the bandwidth were too wide, the local linear estimate β1could be biased due to misspecification. That is, the linear function would be unable tocapture the age profile over such a “wide” range of data. If the bandwidth were too narrow,there would not be enough data for the estimation to get a precise local linear estimate.Thus, the optimal bandwidth needs to balance bias and precision (variance) to estimate β1.This is quite an active field in the nonparametric literature and there are many competingmethods of selecting the optimal bandwidth, such as the plug-in approach (Imbens andKalyanaraman, 2012; Cattaneo et al., 2013) and the cross-validation approach (Ludwigand Miller, 2007). In Table B.3, we show that our main estimates are robust acrossvarious optimal bandwidth selectors. In addition, the standard error of the discontinuityestimate is an important issue in local linear estimation since the available bandwidthselectors tend to give a “large” bandwidth and lead to biased local linear estimates. Onesolution is to use bias-correction estimates. However, the conventional standard error ofthe bias-correction estimates fails to consider the variability of additional second-orderbias estimates, which results in standard errors that are too small and false statisticalinferences. Cattaneo et al. (2013) proposes a method of accounting for this variability toobtain the robust standard error and confidence interval. In Table B.3, we show that thestatistical inferences of our main estimates are still valid even if we use more conservativeway to compute our standard error.763.5. Resultsthe 3rd birthday. For this age group, potential confounding factors couldinclude vaccination and pre-school attendance. The recommended immu-nization schedule could mechanically increase the healthcare spending anduse of young children at age 3. However, this concern is alleviated sincechildren in Taiwan do not need to have vaccines at age 3 and indeed takemost vaccines before they are 2 years of age (Center of Disease and Control,2013).106 On the other hand, entering pre-school could increase the chanceof a child picking up illnesses (e.g. the flu), which would affect children’shealthcare use. This factor might not interfere with the cost-sharing changeat age 3 because the age of entry for “public” pre-schools is 4 years of ageand the government does not specify a statutory attendance age for “pri-vate” kindergartens. Most importantly, we measure the children’s age at adaily level, so our RD design will be invalid only if these factors also changeabruptly within one or two days of the 3rd birthday. This fact substantiallyalleviates the concern that our estimates could be biased by other factors.We conduct several placebo tests to further confirm the validity of our RDdesign (e.g. using data before 2002 when TCMSP was implemented).3.5 ResultsIn this section, we examine the impact of the higher cost sharing at a child’s3rd birthday on healthcare expenditure and utilization. As mentioned above,our sample consists of the children born between 2003 and 2004 who werecontinuously enrolled in the NHI over the ages of 2 and 3. We follow theseindividuals across their 3rd birthdays to estimate the change in healthcareutilization and expenditure at age 3. We will examine outpatient care firstand then impatient care.3.5.1 Outpatient Visits and ExpenditureFrom Section 3.2, we know that the average out-of-pocket cost for eachoutpatient visit increases by more than 100% when a child passes their106http://www.cdc.gov.tw/professional/page.aspx?treeid=5B0231BEB94EDFFC&nowtreeid=1B4BACA0D1FDDB84773.5. Results3rd birthday. Our main question is how children’s healthcare utilizationand expenditure respond to this exogenous price change. We begin with agraphical analysis.Graphical AnalysisFigure 3.2a shows the actual and fitted age profiles of total outpatient ex-penditure for children born between 2003 and 2004. The dots in the figurerepresent total outpatient expenditure per 10,000 person-years by patient’sage at each visit (measured in days).107 The solid line shows the fittedvalues from a local linear regression that interacts intercept and the agevariables fully with a dummy indicating that the child has passed her 3rdbirthday.108 Corresponding to a sharp increase in patient cost sharing at the3rd birthday, there is an obvious discrete reduction in outpatient expendi-ture when the children turn 3. The change in total outpatient expenditurecan be decomposed into the change in the number of visits and the out-patient expenditure per visit. Figures 3.2c and 3.2e represent the actualand fitted age profiles of outpatient visits per 10,000 person-years109 andoutpatient expenditure per visit, respectively. We find that both variablesalso suddenly jump down, right after the children’s 3rd birthday. On theother hand, we use pre-reform data (1997–2001) to plot the related outcomevariables in Figures 3.2b, 3.2d and 3.2f. In sharp contrast to the graphspresented above, We find no visible discontinuity at the 3rd birthday.Main ResultsTable 3.6 presents the estimated impact of the 3rd birthday on outpatient ex-penditure and visits before (1997–2001) and after (2005–2008) the TCMSP107We compute the total outpatient expenditure per 10,000 person-years by dividing thetotal outpatient expenditure at a particular age by the number of enrollees born between2003 and 2004 and then multiplying this by 10,000. This is a common way to presentdata in the health economics and public health literatures and helps us to compare theestimated results across different sample periods and subgroups. Each dot represents10-days average of the dependent variable.108We use 90 days as our bandwidth.109Again, each dot represents outpatient visits per 10,000 person-years at a given age,averaged over 10 days.783.5. Resultswas introduced. Each panel displays results for different dependent vari-ables of interest. Odd-numbered columns present RD estimates from a non-parametric local linear regression and even-numbered columns present RDestimates from a parametric OLS regression (cubic spline). Column (1) ofTable 3.6 presents our main results for outpatient services and displays theestimates from a local linear regression with a triangular kernel function anda bandwidth of 90 days of age.110 Corresponding to the sharp drop in out-patient expenditure at the 3rd birthday in Figure 3.2a, Panel A shows thatthe rise in the level of patient cost-sharing at the 3rd birthday causes overalloutpatient expenditure to decrease significantly by 6.9%. The implied priceelasticity of outpatient expenditure is around −0.10.111The change in total outpatient expenditure comes from two margins: (1)the number of visits (extensive margin); (2) the outpatient expenditure pervisit (intensive margin). Panel B reveals that the number of outpatient vis-its decreases by 4.7% at the 3rd birthday, which is smaller than the changein total expenditure. The remaining change comes from the change in theoutpatient expenditures per visit. Panel C reveals that the outpatient ex-penditure per visit decreases significantly, by 2.2%, at the 3rd birthday. Infact, this result is likely to be a combination of two forces. First, higher costsharing at the 3rd birthday could change the composition of patients andresult in higher outpatient expenditure per visit at age 3. Assuming thatthe marginal patients are not as sick as those who use healthcare service re-gardless of cost-sharing subsidy eligibility, the average health of the patientsmay drop discretely at the 3rd birthday, leading to higher expenditures per110We only use observation whose age at each visit is within 90 days before and after the3rd birthday.111This elasticity is calculated in the form of price elasticity. The standard formula forthe price elasticity of demand is ((Q2−Q1)/Q1)/((P2−P1)/P1), where Q1 and P1 denotethe baseline healthcare demand and patient cost sharing, respectively, and Q2 and P2 arethe healthcare demand and patient cost sharing after the change in cost sharing. However,in the health economics literature, many studies (Leibowitz et al., 1985; Manning et al.,1981; Chandra et al., 2010a) also use the price elasticity, which denotes the percentagechange relative to the average, since P1 could be zero in some cases (e.g. the free planin Rand HIE or zero out-of-pocket cost for inpatient care in this paper) and then thedenominator of the price elasticity would be undefined. That is, the price elasticity iscalculated as ((Q2 −Q1)/((Q1 + Q2)/2))/((P2 − P1)/((P1 + P2)/2).793.5. Resultsvisit.112 Second, losing the cost-sharing subsidy at the 3rd birthday couldalso affect a patient’s choice of provider (quality of each visit) and lead tolower outpatient expenditure per visit at age 3. As mentioned in Section3.2, TCMSP indeed subsidizes more out-of-pocket costs for teaching hospitalpatients than clinic and community hospital patients, which would encour-age patients to use outpatient services at teaching hospitals before the 3rdbirthday, as patients could thereby extract greater subsidies but also receivea better quality of medical service.113 Therefore, when patients lose theireligibility for the cost-sharing subsidy at the 3rd birthday, they may reducetheir visits to teaching hospitals, resulting in lower expenditures per visit.114Our estimates in Panel C imply that the latter force dominates the former,causing outpatient expenditure per visit to exhibit a discrete drop at the3rd birthday. In a later section, we will discuss this issue in more detail.Validity and Robustness ChecksColumns (3) and (4) in Table 3.6 display the results of a placebo test usingpre-reform data (1997–2001). The results reveal that there is no discontinu-ity in our outcome variables at the 3rd birthday before 2002 (when TCMSPwas introduced). The point estimates are insignificant and close to zero,which substantially reduces concerns about the impact of other confound-ing factors on our estimates. In Table B.1, we conduct another placebo testby examining any discontinuities at other age cut-offs. We find our outcomevariables (log of outpatient expenditure and number of visits) to be smoothacross all selected age cut-offs, except for the 3rd birthday (i.e. 1096 daysold).115For a robustness check of our main specification, we use an alternative112This assumes that healthcare providers spend more on treating less healthy patients.113Every three to four years, the Ministry of Health and Welfare evaluates every NHI-contracted hospital/clinic to determine their accreditation. The category of “major teach-ing hospital” is seen as indicating the best-quality providers.114Because the teaching hospitals may provide more medical services at each visit, suchas health checks or medical treatments, it will cost more for each visit.115There are several “significant” discontinuities at other age cut-offs. However, theirmagnitudes are quite small.803.5. Resultsmethod (global polynomial approach) to estimate the discontinuity in theoutcome variables at the 3rd birthday using all available data (365 daysbefore and after the 3rd birthday) and a third-order polynomial age func-tion with different slopes on either side of the 3rd birthday. Column (2) inTable 3.6 presents very similar estimates to our main results. In Table B.2, we systematically examine the sensitivity of our RD estimates to differ-ent bandwidths and orders of polynomial. The estimates are fairly stableacross different specifications. In Table B.3, we present various local linearestimates from three different bandwidth selectors and kernel functions toshow that our main results are robust to these choices.One caveat could threaten the validity of our RD design. Because everychild eventually “ages out” of her cost-sharing subsidy, parents may antici-pate the sharp increase in the price of medical services after the child’s 3rdbirthday and “stock up” on outpatient care.116 This behavioral responsewould represent an inter-temporal substitution of healthcare (i.e. substi-tuting future healthcare with current healthcare) and not a “real” change(increase) in the demand for healthcare induced by the cost-sharing subsidy,which is our main interest. Such a behavioral response would tend to biasupward our estimates of the change in healthcare utilization at the 3rd birth-day (i.e. the price elasticity of healthcare utilization). From Figures 3.2a and3.2c, we indeed find that outpatient expenditure and visits suddenly rise 20days before the 3rd birthday. In order to account for the possible anticipa-tion effect, we conduct a “donut” RD (Barreca et al., 2011; Shigeoka, 2014)by systematically excluding outpatient expenditure and visits within 3–21days before and after the 3rd birthday (Table B.4). Although there is noconsensus on the optimal size of a donut hole, and while eliminating thesample around the threshold seems to contrast with the spirit of RD design,this type of estimation can still give us some sense of the “stocking up” effecton our estimates. Table B.4 indicates that the estimates from different sizes116Since most outpatient visits of young children are for acute diseases (e.g. 74% of visitsare for respiratory diseases), it is hard to believe that parents would be able to substitutechildren’s outpatient care today for care in one month. However, it would be possible tosubstitute outpatient care within a few days.813.5. Resultsof donut hole give us very similar results to our main RD estimates.Change in Choice of Providers at 3rd birthdayThe NHI in Taiwan (and other Asian countries) does not adopt a gatekeepersystem to restrict patients’ choices of providers. Instead, the NHI sets dif-ferent levels of copayments for four different types of providers to encouragepatients to choose the most suitable provider based on their understandingof the seriousness of the illness and to rectify possible moral hazard behav-iors in choosing providers. As mentioned before, the TCMSP exempts allcopayments for children under the age of 3, which gives us a unique op-portunity to examine the impact of differential copayments on the patient’schoice of provider by comparing the choices right before the 3rd birthday(i.e. no copayments) with those right after the 3rd birthday (i.e. differentialcopayments).117Figures 3.3a to 3.3d present the age profiles of the outpatient visits bytype of provider. We find that outpatient visits to major and minor teach-ing hospitals see strikingly discrete reductions just after the 3rd birthday.However, the number of visits to community hospitals exhibit the oppositepattern, namely jumping at the 3rd birthday, and there is a less obviousdrop in visits to clinics after the 3rd birthday. Most of the decline in theoverall number of outpatient visits indeed comes from the teaching hospitals.The visual evidence suggests that the change in relative prices at the 3rdbirthday results in a significant redistribution of caseloads across differenttypes of providers.Coinciding with the graphical evidence, the RD estimates in Panel Bof Table 3.7 show that turning age 3 substantially reduces the number ofoutpatient visits to major and minor teaching hospitals, by 59% and 44%,respectively. However, outpatient visits to community hospitals increaseby 18% and the caseloads of clinics decrease only slightly, by 2%. Thisresult indicates that patients are quite sensitive to the relative prices ofdifferent types of providers, and can switch providers easily. The question117Before the 3rd birthday, patients still need to a pay registration fee. However, theregistration fee does not vary substantially across different providers.823.5. Resultsthat follows is what kind of healthcare can easily be substituted betweenteaching hospitals and community hospitals/clinics ?In Panel C of Table 3.7, we use outpatient expenditure per visit as aproxy for severity of illness.118 The estimates in Panel C reveal that turningage 3 substantially increases the expenditure per visit to the major andminor teaching hospitals by 20% and 6%, respectively. This result impliesthat most of the reduction in visits to teaching hospitals at the 3rd birthdayis actually related to less severe diseases.Since patients switch their utilization from teaching hospitals to com-munity hospitals/clinics right after the 3rd birthday, we suspect that thereduced visits to teaching hospitals could be for the illnesses for which it isnot necessary to attend a teaching hospital. That is, they can be treatedat clinics or community hospitals instead, which implies a substantial moralhazard whereby outpatient care in teaching hospitals are overused beforethe 3rd birthday when patients do not pay copayments. The above resultssuggest that the differing levels of copayments are an important factor inpatients’ choice of providers. Maintaining differential copayments betweendifferent types of providers could be an effective tool for allocating medicalresources efficiently.119Heterogeneous EffectIn this section, we investigate the heterogeneity of price responses acrossdifferent types of diagnoses and various subgroups of young children. Eachrow displays a different type of diagnosis and subgroup. Column (1) in Ta-ble 3.8 presents the rate of outpatient visits per 10,000 person years 90 daysbefore the 3rd birthday to give us some insights about the relative size ofoutpatient visits across different types of diagnoses and subgroups beforea child’s 3rd birthday. Column (2) and (3) in Table 3.8 display the RD118Here we assume that more severe diseases would incur higher expenditures per visit.119There are 24 major teaching hospitals and 65 minor teaching hospitals in Taiwan. Mostof them are located in urban area. However, Taiwan is highly urbanized (e.g. around 78%people live in cities). In addition, Taiwan has a small geography so it would not take muchtime for a patient living in a rural area to reach the closest teaching hospital.833.5. Resultsestimates of outpatient expenditure (taking logs) and implied price elastic-ity of expenditure, respectively. Panel A in Table 3.8 presents the resultsfor selected diagnoses. The first three rows in Panel A list the top threecommon visit diagnoses for young children and all of them are acute res-piratory diseases: upper respiratory infection (URI), acute bronchitis, andacute sinusitis, which accounts for 40% of total outpatient visits.120 Forsome diseases, such as acute bronchitis and sinusitis, receiving proper out-patient care could be beneficial to children’s health. Column (2) in PanelA shows that the outpatient expenditure for these common diagnoses sig-nificantly decline after the 3rd birthday. However, the estimated sizes ofthe reduction at the 3rd birthday for these diseases are smaller than esti-mates from overall outpatient expenditure. The implied price elasticities ofexpenditure are only −0.04 to −0.08, which reveals patients (parents) arenot price sensitive to outpatient care for acute respiratory diseases.121The remaining rows in Panel A present RD estimates for other selectivediagnoses that may be less serious but need timely treatment to improveliving quality, such as skin diseases. Losing the cost sharing subsidy causesa 14.9% reduction in outpatient expenditure for skin diseases, which is muchlarger than the overall decline in outpatient expenditure. Much larger de-creases can also be found for outpatient care that are more discretionarybut could reduce future healthcare costs, such as mental health service andpreventive care. Turning three substantially reduces outpatient expenditurefor mental illnesses by 23.2% and for preventive care by 24.5%. The impliedprice elasticities for this type of healthcare are quite large (−0.33 for mentalhealth service and −0.69 for preventive care).122 Our results suggest preven-tive and mental care are quite price sensitive, which is especially interestingsince preventive care and early treatment for children’s mental disorders(e.g. autism) could result in better treatment outcomes and might substan-tially reduce future medical costs. This result offers an evidence in support120(119 + 51 + 48)/542 = 0.40121We use the same method mentioned in section 3.2 to obtain an exogenous price changeat the 3rd birthday for each disease and then calculate the price elasticity (price elasticity).122We use the same method mentioned in section 3.2 to obtain an exogenous price changeat 3rd birthday for each disease and then calculate the price elasticity.843.5. Resultsof “behavioral hazard” suggesting patients reduce utilization of healthcareservices that are potentially high-valued (Baicker et al., 2013).Panels B to D in Table 3.8 examine the distinct price response acrossvarious subgroups of young children. Panel B displays the results by birthorder. I find that the baseline visit rate for the two groups are quite similarand the price elasticity of healthcare expenditure for 1st born children issignificantly smaller than that for non-1st born children (in absolute terms).This results implies patients may be more cautious when raising the first-born children. They might think healthcare services for 1st born childrenare more necessary. So they may be less willing to reduce 1st born children’shealthcare utilization when facing higher outpatient price. Panel C presentsthe results by gender. We observe two facts. First, outpatient utilizationsfor male are more price sensitive than those for female. Second, before the3rd birthday, males have more outpatient visits than females.These results might reveal a son preference of parents. Parents take theirboys to see a doctor more often than girls when these is a cost sharing sub-sidy. These visits could be discretionary and price sensitive. Therefore, weobserve outpatient care utilization for sons has a larger response to a changein cost sharing at the 3rd birthday than that for daughters. Panel D presentsthe results based on household income.123 This subgroup analysis can helpus get some sense of the income effect on children’s outpatient utilization. Ifan income effect plays an important role in patient’s utilization decision, weshould expect those unable to afford a healthcare services after the price in-crease, such as low-income children, to reduce their utilization of healthcaremore at the 3rd birthday than high-income children. We find that there isno difference in price sensitivity between high and low-income children. Thisimplies higher cost sharing does not result in larger reduction in outpatientutilization for low-income children, suggesting the income effect might playa limited role in explaining the decreased outpatient utilization at the 3rd123A low-income household is defined as follows: A household with monthly householdincome below 40,000 NTD. A high-income refers a household with monthly householdincome above 40,001 NTD. I also use more elaborate income categories(i.e. five incomecategories) to allow effects to vary. The results are quite similar to Panel D in Table 3.8.853.5. Resultsbirthday.3.5.2 Inpatient Admissions and ExpendituresFor young children, inpatient admissions are much less common than out-patient visits. Among our sample at age 2, the average annual number ofoutpatient visits is 19.8 but the average annual number of inpatient ad-missions is only 0.14. Nevertheless, the cost to the patient of one inpatientadmission is 29 times more than that per outpatient visit and 17% of health-care spending for young children is attributed to inpatient care. More im-portantly, patient cost sharing for inpatient admissions experiences a muchlarger increase at the 3rd birthday than does that for outpatient visits, interms of both the level and the percentage change.124 That is, inpatient carecould have substantial impacts on overall healthcare spending and individu-als’ out-of-pocket cost. Hence, understanding how young children’s demandfor inpatient care responds to cost sharing has important policy and welfareimplications.However, the effect of turning age 3 (losing the cost-sharing subsidy)on the utilization of inpatient care is theoretically ambiguous. On the onehand, children may have fewer inpatient admissions and lower expenditureafter they turn 3 because the patient cost sharing for inpatient care increasessharply at the 3rd birthday. On the other hand, the type of inpatient carethat young children usually use might not respond to the price change.Most admission diagnoses in early childhood, such as pneumonia and acutegastroenteritis, can be treated with medication or bed rest. Previous studies(Card et al., 2008; Shigeoka, 2014) have found that patient cost sharing (orinsurance coverage) has less impact on this type of diagnosis for the elderly.In addition, for young children, admissions requiring surgery are seldomselective (e.g. osteoarthritis, hip and knee replacement) but more likely lifethreatening and essential (e.g. congenital heart disease). Thus, we shouldexpect inpatient care for young children to be less sensitive to price changes124Average patient cost sharing for one inpatient admission increases by 1296 NTD atthe 3rd birthday. However, the average price for one outpatient visit rises by just 74 NTD.863.5. Resultsat the 3rd birthday.Graphical AnalysisFigure 3.6a shows the actual and fitted age profiles of inpatient admissionsfor children born between 2003 and 2004. Similar to the graphs for out-patient care (Figure 3.2), the markers represent total inpatient expenditureper 10,000 person-years at the given age, which is measured in days from the3rd birthday. The solid line shows the predicted values from a local linearregression that interacts the age variables fully with intercept and a dummyindicating that the child has passed her or his 3rd birthday. Surprisingly,in contrast to the sharp drop in outpatient expenditure, Figure 3.6a showsthat inpatient expenditure exhibits no change at the 3rd birthday. Similarly,Figures 3.6c and 3.6e represent the actual and predicted age profiles of inpa-tient admissions and inpatient expenditure per admission. We also find thatthere is little visual evidence of any discontinuity in either inpatient admis-sions or inpatient expenditure per admission at the 3rd birthday. When wecompare these with the graphs plotted using pre-reform data (1997–2001),we find the outcome variables in the pre and post-reform periods to havevery similar age profiles.Main ResultsTable 3.9 presents the estimated effect of the 3rd birthday on inpatientexpenditure and admissions before (1997–2001) and after (2005–2008) theintroduction of the TCMSP. As in Table 3.6 for outpatient services, eachpanel displays results for a different dependent variable of interest. Odd-numbered columns present the RD estimates from nonparametric local lin-ear regressions and even-numbered columns present the RD estimates fromparametric OLS regressions (cubic spline). Consistent with the graphicalevidence in Figure 3.6, all RD specifications in Table 3.9 suggest there isno statistically significant impact of turning age 3 on inpatient expendi-ture and utilization. The point estimates in column (1) of Table 3.9 (ourbaseline estimation) are close to zero and insignificant. They reveal that873.6. Conclusionlosing the cost-sharing subsidy reduces the total inpatient expenditure byonly 0.89% and the number of inpatient admissions by 0.18%. The impliedprice elasticity of inpatient expenditure is about −0.004.125There is little evidence on the impact of patient cost sharing on the de-mand for inpatient services. Our results are consistent with the findingsin the prior literature. Shigeoka (2014) finds that the demand for inpa-tient admissions treated with bed rest and medication do not respond tothe price change at age 70 in Japan. Card et al. (2008) obtained similarfindings for Medicare recipients in the US. Since most admissions for youngchildren involve these types of inpatient care, our results suggest that theutilization of inpatient care for young children could have a very limited re-sponse to patient cost sharing, which implies that young children’s demandfor inpatient care may not be discretionary but necessary. In other words,full insurance coverage of children’s inpatient care does not cause moral haz-ard but substantially reduces the financial risk brought about by inpatientadmissions.3.6 ConclusionIn this paper, we provide convincing evidence on the price response of health-care for young children. We exploit a sharp increase in the required levelof patient cost sharing at age 3 in Taiwan that occurs when young chil-dren “age out” of the cost-sharing subsidy, which results in a higher levelof patient cost sharing for children just after their 3rd birthdays than justbefore. We apply an RD design to estimate the impact of cost sharing onhealthcare utilization in early childhood. We reach three conclusions. First,the demand for outpatient services responds significantly to the change incopayments, but the estimated price elasticity of outpatient expenditureis modest (at around −0.10). Second, differential copayments for outpa-tient care between hospitals and clinics represent an effective policy tool forencouraging patients to visit suitable providers based on the seriousness of125Again, it uses the price change in Table 3.2 and is calculated in the form of priceelasticity.883.6. Conclusiontheir illness. According to our estimates, due to the differential copayments,the number of visits to teaching hospitals is reduced by 50% and most of theforegone visits are for less severe conditions, which can be also treated inclinics. Finally, the demand for inpatient services does not respond to theprice change. The implied price elasticity of inpatient expenditure is closeto zero. The Rand HIE found mixed evidence on this issue and could notdraw strong conclusions. Our results largely support the view that inpatientcare for young children is not price sensitive. Taken together, these resultssuggest that the level of patient cost sharing for young children should dif-fer between healthcare services and healthcare providers. For example, ourresults imply providing full insurance coverage for children’s inpatient carecan substantially reduce the financial risk for the households but does notinduce excessive utilization of inpatient care. On the other hand, our es-timates suggest having a higher level of copayment for outpatient care atteaching hospitals can reduce patient’s moral hazard behavior of choosinghealthcare providers, namely, attending teaching hospitals when they do notneed to do so.Several important questions have not been analyzed in this paper, suchas the long-run health impact of this cost-sharing subsidy program. Futureresearch could focus on this issue and this would give us a more completepicture of the effect of similar programs around the world.893.7. Figures3.7 FiguresFigure 3.1: Age Profile of Out-of-Pocket Costs(a) Average price per outpatient visit (NTD) (b) Average price per inpatient admission (NTD)Notes: The line is from fitting a linear regression on age variables fully interacted withAge3i, a dummy indicating after the 3rd birthday. The dependent variable is averageprice per outpatient visit (inpatient admission) by patient’s age at visit (measured indays, 180 days before and after the 3rd birthday). Each dot represents the 10-dayaverage of the dependent variable.903.7. FiguresFigure 3.2: Age Profile of Outpatient Expenditure and Visits(a) Outpatient expenditures per 10,000person-years: 2005–2008(b) Outpatient expenditures per 10,000person-years: 1997–2001(c) Outpatient visits per 10,000person-years: 2005–2008(d) Outpatient visits per 10,000person-years: 1997–2001(e) Outpatient expenditures per visit :2005–2008(f) Outpatient expenditures per visit:1997–2001Notes: The line is from fitting a linear regression on age variables fully interacted with Age3i, a dummyindicating after the 3rd birthday (90 days bandwidth). The dependent variables are outpatient expenditureper 10,000 person years, outpatient visits per 10,000 person years, and outpatient expenditure per visit bypatient’s age at visit (measured in days, 180 days before and after the 3rd birthday). Each dot representsthe 10-day average of the dependent variable.913.7. FiguresFigure 3.3: Age Profile of Outpatient Visits per 10,000 Person-Years byType of Provider(a) Major Teaching Hospital (b) Minor Teaching Hospital(c) Community Hospital (d) ClinicNotes: The line is from fitting a linear regression on age variables fully interacted withAge3i, a dummy indicating after the 3rd birthday (90 days bandwidth). The dependentvariables are outpatient visits per 10,000 person years (measured in days, 180 days beforeand after the 3rd birthday). Each dot represents the 10-day average of the dependentvariable.923.7. FiguresFigure 3.4: Age Profile of Outpatient Expenditure per 10,000 Person-Years(NTD) by Type of Provider(a) Major Teaching Hospital (b) Minor Teaching Hospital(c) Community Hospital (d) ClinicNotes: The line is from fitting a linear regression on age variables fully interacted withAge3i, a dummy indicating after the 3rd birthday (90 days bandwidth). The dependentvariables are outpatient visits per 10,000 person years (measured in days, 180 days beforeand after the 3rd birthday). Each dot represents the 10-day average of the dependentvariable.933.7. FiguresFigure 3.5: Age Profile of Outpatient Visits per 10,000 Person-Years byDiagnosis(a) Acute upper respiratory infection (b) Bronchitus(c) Sinusitis (d) Diseases of the skin(e) Mental illnesses (f) Preventive careNotes: The line is from fitting a linear regression on age variables fully interacted withAge3i, a dummy indicating after the 3rd birthday (90 days bandwidth). The dependentvariables are outpatient visits per 10,000 person years (measured in days, 180 days beforeand after the 3rd birthday). Each dot represents the 10-day average of the dependentvariable.943.7. FiguresFigure 3.6: Age Profile of Inpatient Expenditure and Visits(a) Inpatient expenditures per 10,000person-years: 2005–2008(b) Inpatient expenditures per10,000 person-years: 1997–2001(c) Inpatient admissions per 10,000person-years: 2005–2008(d) Inpatient admissions per 10,000person-years: 1997–2001(e) Inpatient expenditures peradmission: 2005–2008(f) Inpatient expenditures peradmission: 1997–2001Notes: The line is from fitting a linear regression on age variables fully interacted withAge3i, a dummy indicating after the 3rd birthday (90 days bandwidth). The depen-dent variables are inpatient expenditure per 10,000 person years, inpatient admissionsper 10,000 person years, and inpatient expenditure per visit by patient’s age at visit(measured in days, 180 days before and after the 3rd birthday). Each dot represents the10-day average of the dependent variable.953.8. Tables3.8 TablesTable 3.1: Patient Cost-Sharing in Taiwan NHIPatient Cost-SharingMajor Teaching Minor Teaching Community ClinicHospital Hospital HospitalPanel A: Outpatient serviceCopayment 360 240 80 50Registration Fee 150 100 100 50Panel B: Inpatient service1-30 days 10%31-60 days 20%after 61 days 30%1 USD is 32.5 NTD in 2006. For outpatient service, patient cost-sharing is through copyment.A patient pays copayment plus registration fee for each visit. If a physician prescribes a drugat a visit and the drug cost is above 100 NTD, the patient also needs to pay a share of the costof the prescription drug, which is 20% of total drug cost. However, most visits for the childrenunder age 3 have drug costs below 100 NTD so patients usually do not pay for their prescriptiondrugs. On average, The out-of-pocket cost of prescription drugs per visit is very small (i.e. only2.5 NTD). Information about copayment is from National Health Insurance Research Databasecodebook (2012). NHI implemented this fee schedule since July 2005. Since our sample periodis from January 1st 2005 to December 31st 2008, most of outpatient visits in our sample, exceptvisits on January 1st 2005 to June 30th 2005, are based on the above fee schedule. Before July1st 2005, copayment for outpatient service is according to the following fee scheme: 210 NTDfor major teaching hospital, 140 NTD for minor teaching hospital, 50 NTD for communityhospital, and 50 NTD for clinic. Information about registration fee is from an online databaseof NHI registration fee survey: http://www.nhi.gov.tw/amountinfoweb/Search.aspx?Q5C1_ID=2&Q5C2_ID=900002&Hosp_ID=1131100010&rtype=2 For inpatient care, patient cost-sharing takesplace through coinsurance. Depending on the days of stay and the type of admission (acute orchronic admission), a patient is required to pay 10% to 30% of the total medical expense peradmission. The above fee schedule is only for acute admission since we eliminate all chronicadmissions, which only accounts for 0.3% of inpatient admissions.963.8. TablesTable 3.2: Weighted Average Out-of-Pocket Cost perVisit/AdmissionOut-of-pocket cost per visit/admissionBefore After3rd birthday 3rd birthdayType of ServiceOutpatient service 58.9 132.7Inpatient service 0 1296Note: Data are pooled NHI claims records 2005–2008. Weightedaverage out-of-pocket costs per visit/admission are reported inNew Taiwan Dollar (NTD). 1 USD is 32.5 NTD in 2006.Table 3.3: Selected Characteristics at Age Three before and after SampleSelection(1) (2) (3)Original Sample Continuous enrollment Eliminatingat age two and three cost-sharing waiverMale 0.525 0.525 0.524Birith year: 2003 0.510 0.509 0.509Birith year: 2004 0.490 0.491 0.4911st birth 0.519 0.520 0.5202nd birth 0.368 0.370 0.3703rd birth (above) 0.113 0.112 0.110Number of siblings 1.761 1.760 1.759(0.671) (0.671) (0.669)Number of children 435,206 426,587 410,517Note: Column (1) presents the selected characteristics for original sample: all NHI enrolleesborn in 2003 and 2004. Column (2) restricts the sample to enrollees who continuously registerin NHI at age 2 and 3. Column (3) eliminates observations with cosh-sharing waiver, suchas children with catastrophic illness (e.g. cancer) and children from very low income familiessince these children do not experience any price change when turning three.973.8. TablesTable 3.4: Descriptive StatisticsOutpatient Service Inpatient ServiceBefore After Before After3rd birthday 3rd birthday 3rd birthday 3rd birthdayUtilizationAverage annual visits 19.8 19.0 0.14 0.13Average out-of-pocket cost per visit (NTD) 58.9 123.1 0 1289.7Average medical expenditure per visit (NTD) 443.5 438.7 12980.6 13013.9Choice of providersMajor Teaching Hospital 4.1% 2.3% 28.4% 29.8%Minor Teaching Hospital 5.6% 3.7% 58.6% 58.2%Community Hosptial 3.8% 4.6% 12.8% 11.9%Clinic 86.5% 89.4% 0% 0%Number of children (visits > 0) 375,493 364,075 13,252 12,666Number of children-visit 2,003,097 1,954,591 19,356 18,163Note: Data are pooled NHI claims records 2005–2008. The above descriptive statistics are based on records aboutoutpatient(inpatient) service happened within 90 days before the 3rd birthday and 90 days after the 3rd birthday.Average annual visits is calculated by average visits at each age (measured in day) times 365. Average out-of-pocketcosts and medical expenditures are reported in New Taiwan Dollar (NTD). 1 USD is 32.5 NTD in 2006.983.8. TablesTable 3.5: Descriptive Statistics: By Healthcare ProviderProvider Major TeachingMinor Teaching Community ClinicHospital Hospital HospitalPanel A:Composition of Medical ExpensesAverage medical expenses per visit (NT$) 986.9 697.8 528.2 338.4Average out-of-pocket expenses per visit (NT$) 280.4 196.3 148.0 75.3Portion of out-of-pocket expenses 0.61 0.47 0.40 0.26Average drug fee per visit (NT$) 194.5 134.7 86.4 51.2Average examination/treatment fee per visit (NT$) 543.6 309.9 185.4 16.7Average diagnosis fee per visit (NT$) 204.2 206.3 213.8 255.4Average dispensing fee per visit (NT$) 44.4 46.8 42.4 14.9Average drug day per visit (NT$) 6.9 5.2 3.9 3.1Panel B:Composition of PatientsMale 0.54 0.56 0.56 0.54Household income 53,485.7 47,267.9 45,750.2 47,126.2Number of children-visit 125,847 181,767 165,695 3,483,876Note: 1 US$ is 32.5 NT$ in 2006. The sample are all NHI enrollee born in 2003 and 2004 and continuously registered inNHI at age 2 and 3. The above descriptive statistics are based on NHI claims records within 90 days before and afterenrollee’s 3rd birthday. Thus, data are pooled NHI claims records 2005-2008.993.8. TablesTable 3.6: RD Estimates on Outpatient Care at Age 32005-2008 1997-2001(1) (2) (3) (4)Specification Nonparametric Parametric Nonparametric ParametricLocal linear Cubic spline Local linear Cubic splineVisits rate at age 2 542 568(per 10,000 person-years)Bandwidth (days) 90 365 90 365Panel A: Log(outpatient expenditures)Age3 (X100) -6.90*** -6.99*** 0.09 0.29[0.49] [0.46] [0.24] [0.22]Panel B: Log(number of visits)Age3 (X100) -4.73*** -4.77*** 0.22 0.20[0.31] [0.32] [0.17] [0.16]Panel C: Log(outpatient expenditures per visit)Age3 (X100) -2.17*** -2.22*** -0.12 0.09[0.29] [0.27] [0.13] [0.13]Note: We collapse the individual-level data into age cells. Age is measured in days. The first two columnspresent our main results. Each observation (age cell) represents outpatient expenditures and visits from410,517 children who were born in 2003 and 2004 (when they are age 2 and 3). Therefore, we use 2005–2008NHI data to obtain the above estimated results. The dependent variables for the RD estimation are the logof total outpatient expenditure, the log of the total number of outpatient visits, and the log of outpatientexpenditure per visit, at each day of age. Odd columns use data within 90 days before and after the 3rdbirthday (bandwidth is 90 days) and report the difference in local linear regression estimates just before andafter the 3rd birthday by using a triangular kernel, which gives higher weight on the data close to the 3rdbirthday (equation (3.3)). even columns present estimated regression discontinuities by using all availabledata (365 days before and after the 3rd birthday) and flexible polynominal regression (cubic spline), allowinga different slope on either side of the 3rd birthday. In the last two columns, we use the same selection criteriato create a pre-reform sample: enrollees born between 1995 and 1997 (when they are age 2 and 3). Therefore,we use 1997–2001 NHI data to obtain the above estimated results. All coefficients on Age3 and their standarderrors have been multiplied by 100. Robust standard errors are in parentheses. *** significant at the 1 percentlevel, ** significant at the 5 percent level, and * significant at the 10 percent level.1003.8. TablesTable 3.7: RD Estimates on Outpatient Care at Age 3: By Choice of Providers(1) (2) (3) (4)Providers Major teaching Minor teaching Community Clinichospital hospital hospitalVisits rate at age 2 22 30 20 469(per 10,000 person-years)Panel A: Log(outpatient expenditures)Age3 (X100) -39.29*** -38.89*** 17.76*** -1.92***[2.63] [2.40] [1.64] [0.33]Panel B: Log(number of visits)Age3 (X100) -59.29*** -43.89*** 17.71*** -1.73***[1.96] [1.65] [1.64] [0.32]Panel C: Log(outpatient expenditures per visit)Age3 (X100) 19.85*** 5.76*** 0.05 -0.19*[2.24] [1.77] [1.67] [0.10]Note: We collapse the individual-level data into age cells. Age is measured in days. Each observation(age cell) represents outpatient expenditures and visits from 410,517 children who were born in 2003 and2004 (when they are age 2 and 3). Therefore, we use 2005–2008 NHI data to obtain the above estimatedresults. The dependent variables for the RD estimation are the log of total outpatient expenditure, thelog of the total number of outpatient visits, and the log of outpatient expenditure per visit, at each dayof age. Column (1)–(4) present RD estimates of each outcome for four types of health provides by usingdata within 90 days before and after the 3rd birthday (bandwidth is 90 days) and report the differencein local linear regression estimates just before and after the 3rd birthday by using a triangular kernel,which gives higher weight on the data close to the 3rd birthday (equation (3.3)). All coefficients on Age3and their standard errors have been multiplied by 100. Robust standard errors are in parentheses. ***significant at the 1 percent level, ** significant at the 5 percent level, and * significant at the 10 percentlevel.1013.8. TablesTable 3.8: RD Estimates on Outpatient Care at Age 3: By Diagnoses, Birth Order, Gender,and Household Income(1) (2) (3)Visits rate at age 2 Log(outpatient expenditure) Expenditure Elasticity(per 10,000 person-years)Panel A: By visit diagnosesURI 119 -2.38*** -0.037***[0.65] [0.010]Acute bronchitis 51 -5.56*** -0.084***[0.73] [0.014]Acute sinusitis 48 -4.10*** -0.064***[1.10] [0.019]Skin diseases 20 -14.88*** -0.259***[1.55] [0.041]Mental disorder 4 -23.18*** -0.328***[3.62] [0.061]Preventive care 2 -24.54*** -0.689***[6.07] [0.29]Panel B: By birth order1st birth 535 -5.97*** -0.084***[0.57] [0.009]2nd birth (above) 549 -7.90*** -0.115***[0.40] [0.012]Panel C: By genderMale 570 -7.65*** -0.109***[0.59] [0.010]Female 511 -5.93*** -0.085***[0.67] [0.011]Panel D: By household incomeLow 525 -6.98*** -0.101***[0.63] [0.010]High 562 -6.81*** -0.097***[0.54] [0.011]Note: We collapse the individual-level data into age cells. Age is measured in days. Each observation (age cell)represents outpatient expenditures and visits from 410,517 children who were born in 2003 and 2004 (when theyare age 2 and 3). Therefore, we use 2005–2008 NHI data to obtain the above estimated results. The dependentvariables for the RD estimation are the log of total outpatient expenditure. Panel A to D report RD estimates ofeach outcome for various subgroups. Low income household in Panel D is defined as monthly household income isbelow 40,000 NTD. High income refers households with monthly household above 40,001 NTD. We use data within90 days before and after the 3rd birthday (bandwidth is 90 days) and report the difference in local linear regressionestimates just before and after the 3rd birthday by using a triangular kernel, which gives higher weight on the dataclose to the 3rd birthday. All coefficients on Age3 and their standard errors have been multiplied by 100. Robuststandard errors are in parentheses. *** significant at the 1 percent level, ** significant at the 5 percent level, and* significant at the 10 percent level.1023.8. TablesTable 3.9: RD Estimates on Inpatient Care at Age 32005–2008 1997–2001(1) (2) (3) (4)Specification Nonparametric Parametric Nonparametric ParametricLocal linear Cubic spline Local linear Cubic splineVisits rate at age 2 3.9 2.5(per 10,000 person-years)Bandwidth (days) 90 365 90 365Panel A: Log(inpatient expenditure)Age3 (X100) -0.89 0.46 1.36 2.72[4.85] [4.31] [2.38] [2.20]Panel B: Log(number of admission)Age3 (X100) -0.18 -1.26 1.14 3.12[2.82] [2.56] [2.89] [3.13]Panel C: Log(inpatient expenditure per admission)Age3 (X100) -0.71 1.72 0.20 -0.40[3.49] [3.21] [2.36] [2.48]Note: We collapse the individual-level data into age cells. Age is measured in days. The first two columns presentour main results. Each observation (age cell) represents inpatient expenditures and admissions from 410,517children who were born in 2003 and 2004 (when they are age 2 and 3). Therefore, we use 2005–2008 NHI data toobtain the above estimated results. The dependent variables for the RD estimation are the log of total inpatientexpenditure, the log of the total number of inpatient admission, and the log of inpatient expenditure per visit, ateach day of age. odd columns use data within 90 days before and after the 3rd birthday (bandwidth is 90 days)and report the difference in local linear regression estimates just before and after the 3rd birthday by using atriangular kernel, which gives higher weight on the data close to the 3rd birthday (equation (3.3)). even columnspresent estimated regression discontinuities by using all available data (365 days before and after the 3rd birthday)and flexible polynomial regression (cubic spline), allowing a different slope on either side of the 3rd birthday. Inthe last two columns, we use the same selection criteria to create pre-reform sample: enrolees born between 1995and 1997 (when they are age 2 and 3). Therefore, we use 1997–2001 NHI data to obtain the above estimatedresults. All coefficients on Age3 and their standard errors have been multiplied by 100. Robust standard errorsare in parentheses. *** significant at the 1 percent level, ** significant at the 5 percent level, and * significant atthe 10 percent level.103Chapter 4The Effect of WorkplacePensions on HouseholdSaving: Evidence from aNatural Experiment inTaiwan4.1 IntroductionThere are several reasons why individuals may not have enough retirementsaving. For example, self-control problems make people consume too muchtoday and have too little savings for their future consumption. A recentsurvey shows that most Americans believe they should save more for re-tirement(Adams, 2014). Many countries provide public pensions to assistpeople to have enough retirement saving. However, population aging re-sults in a fiscal strain on pay-as-you-go public pension systems. The use ofmandatory workplace pensions is becoming a popular way for governmentsto increase the provision of pensions without incurring much new publicspending. Several developed countries have begun to complement or sub-stitute for public pensions by mandating workplace pensions. For example,Australia and the Netherlands have long traditions of legislation on compul-sory workplace pensions.126 This ensures that each worker is covered by a126Australia introduced a new compulsory occupational pension system, SuperannuationGuarantee, in 1992 that requires employers to contribute a percentage of an employee’s1044.1. Introductionpension plan and therefore safeguards retirees’ standard of living (OECD,2012). In order to raise the replacement rate of pension income and miti-gate the fiscal burden on the public pension system, the UK government hasrequired all employers to provide workers with a workplace pension plan,so-called automatic enrolment, since 2012. The employers are also obligedto make employer pension contributions.However, the ability of mandatory workplace pension schemes to raiseemployees’ retirement wealth depends on the elasticity of substitution be-tween workplace pensions and individual voluntary savings. If workplacepensions offset personal saving partially, such interventions could increaseworkers’ retirement savings. If, on the other hand, workplace pensions sub-stitute perfectly for private saving, then legislation requiring employers tooffer pensions for their workers may just generate a deadweight loss and failto help employees accumulate more wealth for their retirement.127In this paper, I estimate the causal effect of workplace pensions on house-hold saving by analyzing a pension reform in Taiwan which mandated, from2005 onwards, that all private-sector employers should pay a minimum con-tribution of 6% of each employee’s wage, to the latter’s individual pensionaccount, monthly. Before the reform, most private-sector employees in Tai-wan did not obtain employer-sponsored pensions when they retired. Thus,this reform has substantially increased the pension coverage of private-sectorworkers and raised employers’ pension contributions. I exploit this policychange to obtain exogenous variation in employer’s pension contribution forthe affected workers and employ a difference-in-differences approach to over-come the potential endogeneity problems when estimating the effect of work-place pensions on household saving (Gale, 1998). I find the pension reformsignificantly reduces the household saving rate (as a percentage of disposableincome) of private sector employees by 2.06 percentage points to 2.45 per-salary into the latter’s individual pension account (Tapia, 2008). The Netherlands alsohas mandatory occupational pensions covering more than 95% of employees (Tapia, 2008).127For example, this deadweight loss may come from the administrative cost of imple-menting pension law or distortions of the labor market. If employers can fully shift pensioncosts to workers by reducing employees’ wages, then there would be no distortion in thelabor market.1054.1. Introductioncentage points, suggesting the elasticity of substitution between workplacepensions and household saving is about −0.50 to −0.60.128 Since workplacepensions do not crowd out household saving completely, my results suggestthat making workplace pensions compulsory might be an effective policy toraise workers’ retirement wealth.This paper contributes to the current literature in two important dimen-sions. Firstly, to the best of my knowledge, this paper is the first study touse a national policy change as a natural experiment to identify the causal ef-fect of workplace pensions on voluntary household saving of affected workers.Many early studies used ordinary least squares (OLS) regression to estimatethe offsetting effect of workplace pensions on saving and their results weremixed. Many of them suggest that workplace pensions have a very small andinsignificant effect on household saving (Cagan, 1965; Katona, 1965; Hem-ming and Harvey, 1983; Hubbard, 1986; Gustman and Steinmeier, 1999;Alessie et al., 1997). In contrast, a few studies find that workplace pen-sions may substantially crowd out 49% to 92% of other household savings(Munnell, 1976; Gale, 1998; Euwals, 2000). As Gale (1998) points out, themagnitude of OLS estimates may be upwardly biased towards zero since theestimated offsetting effects are confounded with unobserved heterogeneityin saving preferences. For example, employees with a strong propensity tosave for retirement may choose jobs offering generous pension plans. Thisunobserved preference heterogeneity would introduce a positive correlationbetween workplace pension wealth and household savings. Hence, the OLS-estimated savings-offsetting effects of workplace pensions will tend to beunderestimated.129 To obtain unbiased estimates of offset effect, it is nec-essary to find exogenous variation in workplace pension wealth that maybe driven by an exogenous policy change or instrumental variables (IV). Tomy knowledge, only a recent study by Engelhardt and Kumar (2011) triesto solve this endogeneity problem.130 They use US employer-provided pen-128Namely, my results imply that a 10% increase in employer pension contributions rateis offset by a 5–6% reduction in household saving rate.129In terms of absolute value.130Chetty et al. (2014) use Danish administrative data to investigate the effect of work-place pensions on employees’ saving behavior. They utilize the variation in employer1064.1. Introductionsions Summary Plan Descriptions, legal descriptions of pensions, matchedto Health and Retirement Survey (HRS) respondents, and then employ thisdetailed information on pension rules to construct their instruments. TheirOLS results reveal that workplace pension wealth has no effect on non-pension wealth, but their IV estimates show that workplace pensions offset53–67% of household savings, which is quite similar to my results. Mymethodology is different from theirs. I exploit a reform-induced increasein workplace pension contribution for private-sector employees in Taiwanand use an unaffected sector, namely civil servants and national enterpriseworkers, as a comparison group to control for other, unobserved confound-ing effects. By using this difference-in-differences framework, I am able toacquire causal estimates of the effect of workplace pensions on employees’saving.Secondly, this paper exploits a policy change that is more transparentand easier to interpret theoretically compared to prior literature. Severalrecent studies (Attanasio and Brugiavini, 2003 ; Attanasio and Rohwedder,2003; Feng et al., 2011; Banerjee, 2011) form their instruments for publicpension wealth by exploiting changes in the rules on public pension bene-fits, for example, various increases in the public pension benefit eligibilityage for different cohorts or changes to the indexation of the benefit, togenerate convincingly exogenous variation in public pension wealth acrossdifferent cohorts and occupational groups and then estimate the offsettingeffect of public pensions on non-pension saving. However, the policy changesused in these prior studies are usually not uniform across households, canbe hard to characterize, and might depend on unknown parameters suchas the discount rate. By contrast, the reform used in this paper uniformlypension contributions when employees switch jobs and find that workplace pensions onlyoffset 10%–15% of other household savings. Although they performed many robustnesschecks on their results, their crowding-out estimates may still be downwardly biased (inabsolute value) since job switches are endogenous and the variation in employers’ pen-sions contributions induced by firm switches may be correlated with employees’ savingspreferences. In addition, the reform used in this paper affects most private sector workersin Taiwan. If there exists adjustment cost in saving decision, such big changes in pensioncoverage is more likely to make workers re-optimize their saving decisions, which could alsoexplain why I find larger crowding-out effect than the estimates in Chetty et al. (2014).1074.2. Policy Backgroundimposes that 6% of wage income be invested in illiquid instruments. Thisfeature allows the paper to contribute a clean estimate of substitutabilitybetween illiquid pension savings and household savings, obtained with atransparent methodology. In addition, private-sector workers comprise 85%of employees and more than 60% of the labor force in Taiwan and the pen-sion reform raised the coverage rate of workplace pensions for private-sectorworkers from 44% to 100% in a very short amount of time (Taiwanese LaborStatistics, 2007). Figure 4.1 reveals a salient change-up to a 56% increase-in pension coverage for private-sector employees after the reform.131 Thissudden expansion in workplace pension coverage in Taiwan gives us a rarechance to estimate closely the average treatment effect (ATE) of workplacepensions on employees’ saving behavior.The rest of the paper is organized as follows. Section 4.2 gives a briefoverview of the employer pension system in Taiwan and introduces the con-text of the mandatory workplace pension reform implemented in 2005. Sec-tion 4.3 introduces the data and defines the treatment and control groups.Section 4.4 describes my empirical strategy. Section 4.5 analyzes the mainresults. Section 4.6 performs various specification checks. Section 4.7.1 dis-cusses the distinct impact of the reform across the saving rate distribution.Section 4.8 provides concluding remarks.4.2 Policy BackgroundPrior to the 2005 pension reform, the private-sector pension system in Tai-wan was legislated by the Labor Standard Law that was established in 1984.The law required employers to make flexible pension contributions, of 2–15%131This measure could be the “lower bound” of policy variation, since the pension cover-age rate only indicates the percentage of employees covered by workplace pension plans.It does not mean that these covered workers will be eligible for workplace pensions whenthey retire. In particular, prior to the reform, the vesting period for pension benefits wasvery long (25 years in the same firm) so that many private-sector workers could not obtaina pension even if their company offered a pension plan. The 2005 pension reform intro-duced immediate vesting and made all private-sector workers eligible for pension benefitsafter retirement. Therefore, the “true” increase in pension coverage induced by the reformcould be even larger than 56%. I will discuss this issue in Section 4.4 and Section 4.5.1084.2. Policy Backgroundof an employee’s wage, to retirement funds “owned by firms.” However, thevesting period was very long. The employees had to stay at the same firmfor 25 years, or for 15 years until they were at least 55 years of age. Sincethe average lifespan of companies in Taiwan is 13 years and the average jobtenure is only 6 years (Yang and Luoh, 2009), most private-sector employ-ees, other than senior workers in big firms, did not expect to obtain theirpensions. Only 10% of firms obeyed the law in setting up their companypension funds.To increase the coverage of workplace pensions, the Legislative Yuan(Taiwanese Congress) approved the New Labor Pension Law in July 2004and implemented it one year later (July 2005). The main features of thenew workplace pension regulation were as follows. Firstly, the new pensionscheme introduced compulsory workplace pensions. The employers weremandated to make monthly pension contributions of at least 6% of an em-ployee’s wage to the latter’s individual pension account.132 According to the2005 Taiwanese Labor Statistics,133 in 2004 (i.e. one year before the reform),only 20% of private-sector retirees were eligible for workplace pensions. Inother words, the reform caused 80% of private sector workers to be newlyeligible for workplace pensions. Secondly, the new system provided imme-diate vesting, that is, eligibility for pension benefits would be unrelated to aworker’s current job tenure. In fact, employees’ pension benefits would nowaccumulate in their personal accounts rather than in their firms’ pensionfunds. Consequently, under the new pension system, employees would beassured that they would receive their pensions as long as their employers’paid the monthly contribution.134 Table 4.1 briefly compares the new andold workplace pension systems in Taiwan.135The new pension scheme applies automatically to all private-sector work-132Self-employed workers were not affected by reform. Therefore, my sample does notinclude self-employed workers.133These are published by the Taiwanese Council of Labor Affairs.134However, workers can only use the money in this account after they retire and theretirement age is 60. Before retirement, the government helps employees to invest theirpensions and guarantees a minimum rate of return.135The pension contribution is not taxable until retirement. When people start to receivetheir workplace pensions, this income would be taxed.1094.2. Policy Backgrounders joining the labor market for the first time and to those who switch jobsafter the reform. Employees who stayed in their current job after the reformwere given the option of either staying on their old pension scheme or chang-ing to the new pension plan, within a transition period of five years. At theend of the transition period, all employees had to select their workplacepension plan. The old pension scheme had a higher income replacementrate than the new scheme when workers became eligible for pension bene-fits. In addition, employees who switched to the new system had to giveup all benefits amassed in the old pension system.136 I expect that only se-nior workers who were close to retirement and had accumulated substantialpension wealth in their company’s pension fund would have been likely tohave continued with the old pension plan and thus been unaffected by thepension reform. As reported in the 2006 Taiwanese Labor Statistics, thecoverage rate of the new pension scheme decreases with workers’ age. Thecoverage rate for employees under 50 years of age is 84%, but for workersover 50 it drops to 48%.137In contrast to private-sector workers, public-sector employees, includingcivil servants and workers in national enterprises, have their own pensionsystems that were not affected by the 2005 pension reform.138 Taking ad-vantage of this institutional difference between the two sectors, I use public-sector workers as the control group to identify the causal effect of workplacepension provisions on household savings. In Section 4.5, I will examine thevalidity of the control group.136Since workers changing their jobs in the future would not have been able to obtainthese pension benefits under the old pension system, many employees are likely to haveswitched to the new system even if they had accumulated some pension wealth in the oldsystem.137In the old pension system, there was a maximum tenure of pension contribution (30years). After that, employees have to switch to the new pension system.138In fact, the public-sector pension system was not changed at all during my sampleperiod (2002–2008).1104.3. Data and Sample4.3 Data and Sample4.3.1 DataIn order to calculate the household saving rate and identify the targetedsample, data recording detailed information on household income, consump-tion, and household members’ occupations are required. I use the TaiwaneseSurvey of Family Income and Expenditure (TSFIE), conducted annuallysince 1976 by the Taiwanese Directorate-General of Budget, Accounting andStatistics (DGBAS). The TSFIE is an ongoing repeated cross-section incomeand consumption data set and provides a nationwide representative sampleof Taiwanese households. Its sample size is around 14,000 households and55,000 individuals each year. I use detailed information on household in-come source and expenditure in TSFIE to calculate household saving rate.Also, TSFIE includes information on household members’ occupations andworking status. I use this information to define the treatment and controlgroups.4.3.2 SampleI employ six years of TSFIE data from 2002 through 2008 (excluding the re-form year of 2005). Since the new workplace pension system was introducedin 2005, I use the 2002–2004 and 2006–2008 samples to represent the periodsbefore and after the pension reform, respectively. I confine the sample tofamilies headed by prime-age workers (20–50 years old) for two reasons.139First, the main purpose of this paper is to investigate whether mandatoryworkplace pension provision can raise employees’ retirement “wealth.” Sinceretirement wealth is comprised of prime-age saving, and the average retire-ment age of private-sector workers in Taiwan is around 55 (Taiwanese LaborStatistics, 2005), it is better to focus on pre-retirement (prime-age) savingbehavior rather than that exhibited in old age. Secondly, the coverage rate139Since I focus on employees’ saving behaviors, I exclude households whose wage incomeis zero. I also exclude households whose family members are self-employed or work in theagricultural sector, since workers from these sectors often misreport their income andconsumption (Gale, 1998; Attanasio and Rohwedder, 2003).1114.3. Data and Sampleof the new pension system decreases with workers’ age; most employees un-der 50 years of age are covered by the new pension scheme. In contrast, morethan half of all workers above 50 stayed in the old pension system. Hence,this sample selection also ensures that most of those in our treatment groupreally have been affected by the pension reform. Thus, the original samplesize for the prime-age-employee households is 35,775. To avoid the effectof outliers, I exclude households whose saving rate is above 100% or below−100%. This reduces the sample size to 35,715.In contrast to previous studies (Aguila, 2011; Chou et al., 2003), whichdefine the treatment group by the sector of the head of the household, Iidentify the treatment group using detailed sectoral information on house-hold members drawn from the TSFIE. Hence, the treatment group consistsof those households with at least one member working in the private sectorand no one working in the public sector. In the same way, the control groupcontains those with at least one member working in the public sector andno one working in the private sector. This arrangement is more suitable forAsian families, since the family size tends to be larger, with many familymembers participating in the labor market.140 If I did not take each familymember’s employment sector into account, the estimates of the policy im-pact would be biased toward zero when the head of the family and otherfamily members were working in different sectors.141 After applying thisrequirement, the final sample includes 32,869 households, of which about28,729 (87.31%) belong to the treatment group (private-sector families) and4,140 (12.69%) to the control group (public-sector families).140In my sample period (2002–2008), the average number of family members is 3.88 andmore than one family member (1.69 people) has a job.141For example, suppose the head of the household is a public-sector worker and otherfamily members are private-sector workers. Using the head of the household’s sector asthe criterion, this family would be defined as part of the control group. However, thishousehold’s savings should be affected by the pension reform since other family membersare in the treatment group. These contaminated households are excluded from my sample.I allow only purely private (purely public) sector families in my sample. I will conduct arobustness check on this issue in Section 4.6.1124.4. Empirical Specification4.4 Empirical SpecificationIn this section, I estimate a difference-in-differences model comparing theevolution of the saving rates in private-sector and public-sector householdsaround the time of the pension reform. This strategy will identify the impactof the mandatory pension reform as long as there were no other reasonsfor a change in the relative saving behaviors of private- and public-sectoremployees at that time. The following difference-in-differences regression isused for my main analysis:SRi = βDDPENSIONi + αPRIV ATEi + γY EARi +Xiψ + εi (4.1)Where the outcome variable of interest, the household saving rate SRiis measured as the difference between household disposable income and con-sumption expenditure divided by household disposable income. The house-hold total income includes wage income and non-wage income (e.g. non-wagebenefit, asset returns, and transfer income). I subtract any income tax, capi-tal tax, and employee mandates for health insurance from household incometo get household disposable income. The consumption expenditures includesspending on both durable and non-durable goods. Using the saving rate asthe main outcome variable can help me directly calculate the elasticity ofsubstitution between workplace pension and household saving. In particu-lar, I do this by comparing the employer’s pension contribution rate and thedecreased size of the household saving rate induced by reform. I also uselevel of household savings (take log) as the outcome variable for robustnesscheck.I include PRIV ATEi, a private sector dummy, where PRIV ATEi = 1represents the treatment group (private sector households) and PRIV ATEi =0 denotes the control group (public sector households). Y EARi are yeardummies for each year in the sample period: 2002 to 2008 (except for thereform year 2005). The parameter α measures unobservable time-invariantdifferences in saving rates between private- and public-sector households.1134.4. Empirical SpecificationThe parameter γ captures year-fixed effects (common macroeconomic im-pacts).Since differences in observed covariates may lead to distinct time trendsin the household saving rate between the treatment and control groups, it isnecessary to control the related covariates to eliminate the impact of theseother confounding effects. Controlling covariates can also reduce the resid-ual variance of the regression and produce more efficient estimates(Andrietti and Hildebrand, 2006; Meyer, 1995). I include a number of co-variates Xi that could affect household saving suggested by previous studies(Aguila, 2011; Chou et al., 2003): (1) Family characteristics: head of fam-ily’s age, age squared, their education and their gender; spouse’s education;number of children under 18, number of household members over 65, num-ber of members aged 18–64, number of working members, and dummiesfor area of residence. (2) Industry and occupation: head of family’s indus-try and occupation. (3) Household wealth: household non-wage income;housing assets.142 εi is the error term.The key variable PENSIONi is a dummy indicating that household i isaffected by pension reform, meaning that household i has someone workingin the private sector in the post-reform years 2006–2008.143 Its coefficientβDD is the standard difference-in-differences estimator. Since I control forgroup and year-fixed effects, βDD measures the differential trend in averagehousehold saving rates among private sector workers relative to public-sectorworkers in the post-reform years.I can attribute the difference in the evolution of the household savingrate between the two groups to the effect of the mandatory pension re-form on the saving rate among private-sector households if I impose thefollowing identification assumptions: Firstly, the public- and private-sectorhouseholds’ saving rates would follow a common trend in the absence of thepension policy change. Given this assumption, I can use the observable post-reform trend in the saving rates among public-sector households to derive142Dummy variables for owning one’s house and house size.143PENSIONi = 0 means either that a member of household i works in the publicsector or that the observation is from the years 2002–2004.1144.4. Empirical Specificationthe counterfactual evolution of private-sector household saving rates afterthe reform. This assumption will ensure that my results do not come fromdifferent pre-reform trends in household saving rates between the treatmentand control groups.Secondly, except for the pension reform, no other shock during my sam-ple period has a differential effect on the two groups’ household saving rates.That is, the difference in the evolution of the saving rates for private- andpublic-sector households after 2005 should be driven by the pension reform.I cannot completely rule out that some other shock during this period mighthave had distinct effects on private- and public-sector households’ saving.However, given the magnitude of the pension coverage change,144 it seemshighly unlikely that other shocks could be the driving force for the rela-tive shift in saving rates between the two sectors of workers over this timeperiod.145Thirdly, I assume there is no selection into the treatment based on unob-servables εi once I control for the observable covariates Xi. In other words,I assume that employees with a high savings preference (unobserved) do notswitch to the private sector to obtain workplace pensions after the reform.This assumption ensures that my results are not driven simply by workers’self-selection into the treatment group after reform. Such a self-selectionproblem is unlikely to occur, since public-sector employers offer more gen-erous pensions to their employees than private-sector employers even afterthe pension reform and the substantial increase it brought about in mostprivate-sector workers’ workplace pension wealth.146 In Section 4.5, I willuse three placebo tests to examine the credibility of these identification as-144As mentioned in Section 4.1, this reform made around 80% of private-sector employeesnewly eligible for a workplace pension when they retire.145In fact, during the entire sample period (2002–2008), no other policy change wasmade affecting the labor market or workers’ savings behavior. Thus, it is arguably soundto make this assumption.146Since people need to pass exam to become public sector workers, I find the pass rateof exams did not change a lot during my sample period. The pass rate was 4.9% in 2004and then became 5.5% in 2007. In general, public positions are highly selective. There isconsiderable excess demand for these positions even after the pension reform. In addition,such self-selection may lead to my estimates being underestimated.1154.4. Empirical Specificationsumptions.Two caveats to my estimating procedure have to be mentioned beforeI analyze the results. First, my identification strategy indeed analyzesthe intention-to-treat effect instead of the average treatment effect on thetreated. Since I do not have individual-level data concerning workers’ work-place pension coverage, I estimate the reduced-form effects on all private-sector workers (i.e. the eligible population) rather than on workers who arenewly covered by workplace pensions (i.e. the affected population). To re-cover the average treatment effect on the treated, I need to divide βDD bythe proportion of truly affected private-sector employees (Baker et al., 2008;Bloom, 1984).147 If the fraction of truly affected workers is close to one, theintention-to-treat effect will approach the average treatment effect on thosewho are treated. In my sample (prime-age workers), over 84% of employeesare covered by the new pension scheme. Furthermore, this reform has likelymade 80% of private-sector retirees newly eligible for workplace pensions. Itmay be argued that the fraction of affected employees is high. Hence, βDD(the intention-to-treat effect estimate) may not be far from our quantity ofinterest, namely, the average treatment effect on the treated. I will returnto the specifics of this issue in Section 4.5.Second, the correct computation of standard errors is a crucial issuein the difference-in-differences approach. Since the policy variation I useis at the sector-year level, I present the standard errors clustered on thesector-year cells to account for any dependence of the unobservable errorwithin sector-year cells.148 Furthermore, in recognition of the small numberof clusters, following Cameron et al. (2008)’s suggestion, I adopt relativelyconservative inference by using the T (G − 2) distribution rather than thestandard normal distribution to form critical value and p-values.149 For mysmall number of clusters, this correction may make a substantial differenceto the inference results (Angrist and Pischke, 2009). In Section 4.6, I will147It also needs to be assumed that there are no externalities of the pension reform fortreated households.148There are two sectors (private and public) and six years (2002–2004 and 2006–2008).Therefore, I have 2× 6 = 12 clusters.149G is the number of clusters, namely, 12.1164.5. Resultsalso use different levels of clustering (e.g. clustering by sector and by pre- andpost-reform periods) and various inference methods, such as block bootstrap(Bertrand et al., 2004) and wild bootstrap (Cameron et al., 2008), to addressthis issue.4.5 Results4.5.1 Summary StatisticsTable 4.2 compares the trends in the outcome variables and covariates be-tween the treatment and control groups before and after the reform. It alsopresents the results of simple difference-in-differences estimates for each vari-able.150 Two things can be learnt from Table 4.2. First, for private-sectorworkers, the household saving rate, household savings and wage incomedecrease significantly after the reform.151 However, the corresponding vari-ables for public-sector households remain the same after the reform. Infact, the average growth rate of per capita GDP in Taiwan during 2006 to2008 is around 4%. Therefore, one might expect wage income as well ashousehold savings not to decrease in the absence of pension reform. Thesimple difference-in-differences estimates indicate that the pension reformreduced the household saving rate, household savings and wage income ofprivate-sector workers significantly by 1.62%, 34,022 NT$, and 36,520 NT$,respectively (all annual numbers).152 The finding of decrease in wage incomeindicates that pension reform leads to wage income being reduced by 5.31%and employers may fully shift the mandatory pension cost to the employ-150The simple DD estimates I employ here areV ariablei = δDDPENSIONi + δ1PRIV ATEi + δ2POSTi + ςiwhere PENSIONi and PRIV ATEi are as defined in Section 4.4. POSTi is the dummyfor the post-reform period: 2006–2008. I focus on the DD estimates δDD.151All of these variables are measured in 2007 New Taiwan Dollars.1521 US$ = 32.4 NT$ in 2007.1174.5. Resultsees,153 which is consistent with the findings in Yang and Luoh (2009).154Thus, the pension reform may have little impact on the lifetime income ofprivate-sector households (i.e. no income effect on saving).Second, except for the above three variables and dummies for area of res-idence, the simple difference-in-differences estimates reveal that other vari-ables exhibit different trends between private- and public-sector employeehouseholds after the pension reform. In other words, there is little evidenceof a composition change in the covariates after the reform. I will controlthese covariates further in the following regression analysis.4.5.2 Main ResultsColumns (1)–(4) of Table 4.3 report the estimated coefficients on the keyvariable PENSION in difference-in-differences estimation (equation (4.1)).I begin by presenting the estimate from the basic difference-in-differencesregression controlling for a dummy for private-sector households and yearfixed effects (Column (1)). Then, I gradually include the covariates of familycharacteristics, working industry, occupation and household wealth (Column(2)–(4)). The fact that the estimates are quite stable across different speci-fications is comforting. All of the estimates are significantly different fromzero at the 5% level. My preferred specification (column (4)) implies thatpension reform causes the household saving rates of private sector employeesto fall by 2.06 percentage points. This is a sizeable decrease that amountsto around 10% of the pre-reform household saving rate.155Note that this estimate is an intention-to-treat effect. To arrive at theaverage treatment effect on those treated, it must be divided by the pro-portion of truly treated workers. I propose two measures of this proportion.Firstly, as reported by the 2006 Taiwanese Labor Statistics, around 84% ofworkers below age 50 are known to be covered by the new scheme. Using153This is a simple calculation: 36, 520/673, 430 = 5.31%, 673, 430 is pre-reform wageincome.154Yang and Luoh (2009) use 2003–2007 Manpower Utilization Survey (i.e. labor forcesurvey data, like Current Population Survey in the United States) and find pension reformreduces the hourly wage rate by 5.92%.155The pre-reform household saving rate of private sector workers is 22%.1184.5. Resultsthis number to represent the probability of treatment for my sample, theresulting estimated average treatment effect on the treated indicates thatthe pension reform leads to a 2.45 percentage points decline in the house-hold saving rate of private-sector workers.156 Secondly, I use the change inthe coverage rate of workplace pensions to get an estimate of the percent-age of employees treated. As mentioned in Section 4.1, Figure 4.1 indicatesthat the reform induces a 56% increase in the coverage rate of workplacepensions. The estimate of the average treatment effect on the treated calcu-lated by this method suggests that making workplace pensions compulsoryreduces the household saving rate of private-sector workers by 3.68 percent-age points.157 I prefer the first estimate to the second since, with the longvesting period, many covered employees still failed to qualify for a pensionwhen they retired under the old scheme. In fact, before the reform, only 20%of retired private-sector workers were eligible for workplace pensions. Theestimate of the proportion of truly treated workers derived using the secondmethod could substantially underestimate the probability of treatment.These estimates of the impact of the reform on the household saving ratecan be used to estimate the elasticity of substitution between workplace pen-sions and household savings, which is a major issue in previous studies. Thestatutory contribution rate of employers is at least 6% of a worker’s wage158and the average labor income share for private sector households in my sam-ple is around 68%.159 The simple calculation implies that the contributionrate of workplace pension is around 4.08% of household disposable income.Comparing the estimates of the reform impact on household saving ratewith pension contribution rate, I obtain an implied degree of substitutionbetween a workplace pension and households’ voluntary saving of around−0.50 to −0.60.160 That is, a one dollar increase in the workplace pension156This is just a simple calculation: 2.06/0.84 = 2.45.157This is again just a simple calculation: 2.06/0.56 = 3.68.158According to the 2006 Taiwanese Labor Statistics, most employers pay only the min-imum pension contribution, that is 6% of workers’ wages.159First, I calculate each household’s wage income share (i.e. wage income divided byhousehold disposable income). Then, I compute the mean of wage income share by usingthe sample of private-sector households during the pre-reform period.160This is a simple calculation using the estimate of the intention-to-treat effect:1194.5. Resultsis likely to displace 50 to 60 cents of household savings.4.5.3 Falsification TestsIn this section, I utilize three falsification tests to check the validity of public-sector households as a comparison group. The first placebo test uses previousperiods (2000–2004) of TSFIE data to check whether there exists a paralleltrend in saving rates between private- and public-sector households beforethe reform. I assign a fake policy change to 2002 and choose 2000–2001and 2003–2004 as the pre- and post-reform periods, respectively. Duringthis period, there was no policy change affecting workers’ saving behavior ineither sector. If the two groups’ household savings show a common trend be-fore the pension reform, then insignificance in the “treatment effect” (̂βDD)estimates should be expected in the 2000–2004 sample. The result in Table4.3 column (5) indicates that the point estimate of ̂βDD is only −0.0053 andis not significantly different from zero. This result implies that private- andpublic-sector household saving rates might have shared similar trends beforethe 2005 pension reform.Secondly, I use “less affected” private sector households whose heads ofthe family work in the banking industry as a new treatment group161 toexamine whether there are other confounding factors affecting the savingrate of private and public sector households differently. Before the pensionreform, the workplace pension coverage rate in the banking industry wasparticularly high, with around 90% of employees having a workplace pensionplan (Taiwanese Labor Statistics, 2001). The pension reform should havehad a much smaller impact on these workers. Hence, if there is no shockother than the pension reform having a distinct impact on the saving ratesof private- and public-sector employees, the workers in private banks shouldhave less of a savings response to the reform. Column (6) in Table 4.3indicates that the pension reform led to a small and insignificant reductionin the saving rate of households with heads working in private-sector banking−2.06/4.08 = −0.50 and the estimate of the average treatment effect on the treated:−2.45/4.08 = −0.60.161The comparison group is the same (public sector employees).1204.5. Results(the point estimate is only −0.0050).The last placebo test uses that part of the sample with household headson the verge of retirement (i.e. age of the head of household is above 51years). Since the average age of retirement in Taiwan is around 55, and overhalf of 51–65-year-old private-sector workers are still accumulating their pen-sion wealth under the old system, their savings behavior should be expectedto show less of a response to the mandatory workplace pension reform ifthere was no other shock affecting private- and public-sector workers’ sav-ing behavior differently at the time. The result, shown in Table 4.3, Column(7) confirms my conjecture that the point estimate of ̂βDD would not be sig-nificantly different from zero and indicates that the evolution of the savingrate for private sector employees close to retirement did not change afterthe reform.In Table 4.3, I also test for equality between my main estimate (Column(4)) and the estimates in the three placebo tests. All of the placebo test es-timates are significantly different from the main estimate, lending credenceto my expectations regarding the impact of the reform on households’vol-untary saving. In sum, these placebo tests imply that the pension reformmight be the main reason for the difference between the trends in the aver-age household saving rate for private relative to public-sector workers after2005.4.5.4 Magnitude of EstimatesMy results reveal a substantial offsetting effect of workplace pensions onhousehold savings, with the elasticity of workplace pensions to householdsaving estimated at around −0.50 to −0.60. This finding is in accordancewith recent studies that have employed an IV identification strategy to es-timate the crowding-out effect of public pension or workplace pensions onhousehold savings/wealth.Attanasio and Brugiavini (2003) explore the effect of social security re-form in Italy and obtain an average elasticity of substitution between publicpension and household saving of −0.35 to −0.71 (across all age cohorts: 20–1214.6. Specification Checks65) and find the substitutability particularly high (close to −1) for employ-ees aged 35–45. Using UK household data, Attanasio and Rohwedder (2003)find that the estimated crowding-out effect of public pension on householdsavings is not significant for the young cohort (20–31 year-olds) but thatthe elasticity of substitution is significant and around −0.65 to −0.75 formiddle-aged households (43–64 year-olds).Engelhardt and Kumar (2011) use HRS data and construct IVs for work-place pensions by exploiting the detailed employer-provided pension plansupplement that comes with the HRS. In contrast to this paper, their HRSsample contains households whose heads are aged above 50 years old. How-ever, it is still appropriate to compare their results with my difference-in-differences estimates since they estimate the effect of pension “wealth” onhousehold “assets” (stock variable) rather than savings (inflow variable),and retirement wealth mainly consists of prime-age savings. Actually, theyfind a similar magnitude of substitution between workplace pension wealthand other household assets. That is, workplace pension wealth offsets half(53–67%) of non-pension wealth in the United States.4.6 Specification ChecksMy estimations presented thus far clearly show that the pension reform hasreduced the private-sector family saving rate by between 2.06 and 2.45 per-centage points. The results indicate a considerable elasticity of substitutionof workplace pension for household savings, at around −0.50 to −0.60. I alsoconducted three falsification tests to check the effectiveness of the controlgroup and confirmed that public-sector families probably make a suitablecontrol group. I now experiment with various specifications to examine therobustness of my results.4.6.1 Different Methods of Statistical InferenceIn this section, I explore the robustness of my main results to alternativemethods of statistical inference. Firstly, to account for temporal dependence1224.6. Specification Checksin the error, I start by assuming that the dependence is restricted to the pre-and post-reform periods. However, I find that the standard error becomeseven smaller than in my main results, where the standard error is clusteredon sector-year cells. The point estimate is significantly different from zeroat the 1% level when I use the T (G − 2) distribution to obtain the p-value(see Column (1) in Table 4.4 ).162Next, following Bertrand et al. (2004), I conduct a block bootstrap proce-dure (clustered on sector-year cells). This method maintains the correlationstructure within clusters by keeping samples that belong to the same clustertogether in a block. Furthermore, instead of bootstrapping the standarderror, this method directly bootstraps t-statistics so that I can only reportthe p-value and not the standard error. The result shows that the p-valuecomputed by a block bootstrap, achieves the 1% statistical significance level(see Column (2) in Table 4.4).Finally, I also show results from the wild cluster bootstrap approach163suggested in Cameron et al. (2008). This method is aimed at improvinginference in cases with a small number of clusters and avoids the problem ofinestimable coefficients by resampling the residuals rather than pairs of in-dependent and dependent variables (e.g. block bootstrap). The inestimableproblem is more serious in this paper since I have small clusters and theparameters of interest are indicator variables (difference-in-differences es-timator ̂βDD), producing the problem of the resampling regressors are allbeing 0 or 1. The p-value computed by this approach is, as expected, a bitlarger (0.007) but still indicates the 1% significance level (see Column (3)in Table 4.4).4.6.2 Different Definition of Saving RateDeaton and Paxson (2000) suggest that the household saving rate can beapproximated by the difference between the logarithm of a family’s after-tax income ln(Y ) and the logarithm of the family’s consumption expenditure162G is the number of clusters, making it 4 in this case.163Again, I cluster on sector-year cells.1234.6. Specification Checksln(C). Hence, I redefine my dependent variable, household saving rate, asln(Y )−ln(C). Column (4) of Table 4.4 indicates that pension reform inducesa 2.50 percentage points decline in the household saving rates of privatesector employees. The point estimate is less precise164 and significantlydiffers from zero at the 5% level (p-value is 0.029).4.6.3 Different Definitions of Treatment and ControlGroupsIn the third column (5) of Table 4.4 we follow previous studies (Aguila,2011; Chou et al., 2003) and redefine the treatment and control groups usingthe head of the household’s work sector. As mentioned in Section 4.3, thisspecification should lead to estimates of the pension crowding-out effect ̂βDDthat are upwardly biased toward zero when other family members have jobsin different sector. As expected, I find the estimated reform impact to besmaller, suggesting only a 1.37 percentage points decrease in the householdsaving rate, but is not statistically different from my main estimate.4.6.4 Different Sample PeriodsTo eliminate any influence of the anticipation of the reform on my results,I also exclude 2004 TSFIE data. This is the year in which the new pensionlaw was passed. However, the result based on this sample period is quitesimilar to my main result (see Column (6) in Table 4.4).4.6.5 Controlling Household Earned IncomeTo get some sense of how my main results depend on any change in householdearned income induced by reform, I include household earned income in myregression. After controlling household earned income, the estimated reformimpact is smaller, namely, 1.38 percentage points decrease in the householdsaving rate. However, this estimate is not statistically different from my164Standard error is 0.010.1244.7. Impact Across the Saving Rate Distributionmain estimate (see Column (7) in Table 4.4).1654.7 Impact Across the Saving Rate DistributionThe estimates in the previous sections show the “average” reform impacton workers’ voluntary saving. I find that mandating workplace pensionsfor employees, on average, reduces prime-age workers’ saving rate in thetreatment group by between 2.06 and 2.45 percentage points. However,these estimates summarize the reform’s impact in a single number and donot give us the “overall” reform impact on a worker’s saving behavior ifthe pension reform did not have a uniform effect on each worker. Thisconjecture is highly possible since around 20% of private sector workers hadbeen eligible for workplace pension before 2005 pension reform and theyshould be less affected by the reform. In addition, these workers could havestronger preference toward saving so they might choose the jobs that providegenerous workplace pension and have higher household savings.In this section, I explore the possible heterogeneity of the savings re-sponse to mandatory workplace pensions across the saving rate distribution.This analysis will give us a more complete picture of how mandatory work-place pensions affect workers’ saving behavior. It will also provide usefullessons for other countries (e.g. the UK) implementing similar mandatoryemployer pension policies.4.7.1 Quantile Differences-in-Differences EstimationTo examine how the effect of mandatory workplace pensions differs acrosshouseholds with different saving rates, I use a quantile difference-in-differencesregression to estimate the policy effect on the “entire” distribution of private-sector household saving rates. Since the impact of the pension reform over165I also run a regression of the savings rate on log household earned income to knowsavings rate-wage relationship. I find that 1% increase in household earned income isassociated with 0.15% increase in household saving rate. If employers can fully shift costof pension contribution by reducing 6% of worker’s wage, the saving rate could be reducedby 0.9%.1254.7. Impact Across the Saving Rate Distributionthe unconditional distribution of household saving rates is my outcome ofinterest, I adopt a recently developed estimation technique of unconditionalquantile regression (Firpo et al., 2009) to obtain the quantile difference-in-differences estimator for each quantile. The traditional quantile regressionmethod (Koenker and Bassett, 1978) cannot estimate the treatment effect onunconditional quantiles. Firpo et al. (2009) address this issue by replacingthe outcome variable (i.e. household saving rate) with recentered influencefunction (RIF) and then conducting a standard OLS regression. The RIFin this paper is defined by:RIF (SRi, QS(θ)) = QS(θ) +θ − 1{SRi ≤ QS(θ)}fSR(QS(θ))where QS(θ) is the θth quantile of the household saving rate. 1{.} is anindicator function and fSR(QS(θ)) is the density of the household savingrate at the θth quantile. θ − 1{SRi ≤ QS(θ)}fSR(QS(θ))is the influence function forevaluating the effect on the estimates of the quantile producing by chang-ing one data point in the sample. The key feature of the RIF is that theexpected value of the RIF (conditional on the covariates Xi) is equal to theunconditional quantile of the saving rate QS(θ). Applying this property,Firpo et al. (2009) show that we can obtain the estimates of the covariates’unconditional quantile effect by simply using an OLS regression of the RIFon the covariates. I estimate the following quantile difference-in-differencesregression:RIF (SRi, QS(θ)) = βDD(θ)PENSIONi + α(θ)PRIV ATEi + γ(θ)Y EARi+Xiψ(θ) + εi(θ)The parameter βDD(θ) evaluates the treatment effect of the pensionreform on the household saving rate at the θth quantile. Compared withlinear difference-in-differences estimation, identifying the quantile treatmenteffect by using quantile difference-in-differences requires a more stringent1264.8. Conclusioncommon trend assumption. It requires a common trend to exist in eachquantile of the household saving rate distribution.The results in Table 4.5 imply that the mandatory workplace pensionshave had a significantly negative impact on the households at the bottomand the median of the saving rate distribution (10th percentile to 60th per-centile) but little impact on the top saving rate quantile (above the 70thpercentile). That is, the estimated reform impact shown in my main resultis concentrated on those households with low to median saving rates.This result may reveal that job sorting for workplace pensions may haveexisted among employees before the reform. That is, employees with astronger preference for saving (e.g. people who would like to consume more inretirement) might choose jobs offering more generous pension plans. Beforethe reform, such workers may already have had workplace pensions butalso high voluntary savings. In other words, these employees with employerpension contributions may have stayed in a relatively high quantile of thesavings distribution. Hence, the expansion of workplace pensions broughtabout by the reform should have had less impact on these workers. Thisgives a possible explanation for the differential results seen in the top andbottom quantiles in Table 4.5. In addition, those with low household savingrate are likely to be liquidity constrained. Therefore, when employers helpthem contribute 6% of the wage to pension accounts, they are more likelyto reduce their saving to smooth out their consumption, which providesanother explanation for my findings.4.8 ConclusionThis paper exploits the recent workplace pension reform in Taiwan as anatural experiment through which to investigate the impact of workplacepension provision on households’voluntary savings. My results suggestthat this reform significantly reduces household saving rates by 2.06–2.45percentage points on average. This implies that the average elasticity ofsubstitution between workplace pension and households’ voluntary savingsis between −0.50 and −0.60. Moreover, to examine the reform’s impact1274.8. Conclusionon the entire household saving rate distribution, I conducted unconditionalquantile difference-in-differences estimation and found that most of the aver-age policy effect is indeed concentrated in the bottom and median quantiles.This finding can be explained by employees’ job-sorting behavior, with thesavings-oriented attracted to workplace pensions before the reform. In gen-eral, I find that workplace pensions crowd out only half of household saving,which is similar to previous studies on workplace pensions (Engelhardt andKumar, 2011) or public pension (Attanasio and Brugiavini, 2003; Attanasioand Rohwedder, 2003). Therefore, my results suggest that mandatory work-place pensions could be an effective policy instrument for raising employees’retirement wealth.However, one important caveat should be noted in the interpretation ofmy results. The TSFIE data lack information about the pension coveragerate before the reform and the choice of pension scheme after the reform.Hence I know only the eligible group of employees and not the truly af-fected population. For this reason, my difference-in-differences estimatesidentify the intention-to-treat effect but not the average treatment effecton the treated. From the aggregate data, I find that the reform may havemade 80% of private-sector employees newly eligible for workplace pensionswhen retiring, and that 84% of employees are covered by the new pensionscheme after the reform. Hence, this pension reform actually affected themajority of private-sector employees, which may substantially mitigate thebias this data problem could have had on my estimates of the reform’s im-pact. Nevertheless, it would still be worth linking administrative data fromthe government pension authority with TSFIE data to obtain more preciseestimates of the pension-saving offset..1284.9. Figures4.9 FiguresFigure 4.1: Workplace Pension Coverage in Private Sector: 2002–20071294.10. Tables4.10 TablesTable 4.1: Comparison Between New and Old Pension SystemsNew pension system Old pension systemSystem Defined contribution system Defined benefit systemLaw Labor pension law Labor standard lawVesting period Immediate vesting The employees are required to stay in thesame firm for 25 years or stay in the samefirm for 15 years and become 55 years oldEmployer’s contributionMandatory rate: at least 6% of anemployee’s wageFlexible rate: 2% to 15% of anemployee’s wageSource: Taiwanese Council of Labor Affairs1304.10. TablesTable 4.2: Descriptive StatisticsPrivate sector Public sectorPre-reform Post-reform Diff Pre-reform Post-reform Diff Diff-in-Diff(2002–2004) (2006–2008) (2002–2004) (2006–2008) estimatesSaving rate 0.22 0.206 -0.014*** 0.309 0.312 0.002 -0.016**(0.22) (0.211) [0.003] (0.232) (0.215) [0.007] [0.007]Saving 27.431 25.557 -1.8741*** 47.258 48.786 1.528 -3.402**(43.211) (39.235) [0.487] (50.207) (48.47) [1.546] [1.417]Wage income 67.343 64.897 -2.446*** 82.993 84.2 1.206 -3.652***(40.641) (40.572) [0.479] (42.22) (45.737) [1.370] [1.371]Non-wage income 34.828 35.204 0.376 49.54 50.497 0.957 -0.581(after-tax) (44.236) (38.609) [0.490] (43.425) (40.351) [1.316] [1.391]Consumption 74.739 74.544 -0.195 85.276 85.912 0.635 -0.831(37.31) (35.534) [0.430] (36.852) (35.125) [1.129] [1.217]Head’s age 37.998 38.477 0.478*** 40.393 40.929 0.536** -0.057(7.257) (7.33) [0.086] (6.672) (6.743) [0.210] [0.241]Head’s education 12.045 12.556 0.510*** 14.267 14.646 0.379*** 0.130(3.041) (2.878) [0.035] (2.404) (2.402) [0.075] [0.097]Spouse’s education 7.25 7.048 -0.202*** 9.494 9.302 -0.191 -0.010(6.001) (6.318) [0.073] (6.335) (6.761) [0.204] [0.208]male head 0.775 0.749 -0.025*** 0.763 0.724 -0.039*** 0.013(0.418) (0.433) [0.005] (0.425) (0.447) [0.014] [0.014]# of above 18 2.586 2.572 -0.0140 2.304 2.286 -0.017 0.003(1.1) (1.07) [0.013] (0.876) (0.824) [0.027] [0.035]# of below 18 1.224 1.101 -0.122*** 1.364 1.247 -0.117*** -0.006(1.099) (1.058) [0.013] (1.046) (1.027) [0.032] [0.036]# of above 65 0.27 0.311 0.041*** 0.229 0.241 0.012 0.029(0.558) (0.597) [0.007] (0.529) (0.546) [0.017] [0.019]# of working 1.592 1.587 -0.005 1.352 1.347 -0.006 0.001(0.723) (0.706) [0.008] (0.497) (0.487) [0.015] [0.023]Southern Taiwan 0.178 0.211 0.033*** 0.184 0.20 0.016 0.016(0.383) [0.408] [0.005] [0.388] [0.40] [0.012] [0.013]Middle Taiwan 0.183 0.207 0.024*** 0.213 0.205 -0.008 0.032**(0.387) (0.405) [0.005] (0.409) (0.404) [0.013] [0.013]Northern Taiwan 0.308 0.244 -0.063*** 0.219 0.20 -0.019 -0.044***(0.205) (0.430) [0.005] (0.414) (0.40) [0.013] [0.015]Observations 14,304 14,425 28,729 2,299 1,841 4,140 32,869Note: Saving, wage income, non-wage income, and consumption are scaled in thousands of 2007 New TaiwanDollars. Household disposable income is the sum of wage income and non-wage income(after-tax). The 2007exchange rate is 1 US Dollars = 32.4 New Taiwan Dollars. Southern Taiwan, Middle Taiwan, and NorthernTaiwan are the living area dummies. Standard errors in brackets, *** significant at the 1 percent level, **significant at the 5 percent level, and * significant at the 10 percent level.1314.10. TablesTable 4.2: Descriptive StatisticsPrivate sector Public sectorPre-reform Post-reform Diff Pre-reform Post-reform Diff Diff-in-Diff(2002–2004) (2006–2008) (2002–2004) (2006–2008) estimatesAgriculture 0.015 0.014 -0.001 0.006 0.005 -0.0012 0.001(0.12) (0.116) [0.001] (0.078) (0.07) [0.002] [0.004]Manufacturing 0.515 0.506 -0.008 0.089 0.084 -0.0051 -0.003(0.5) (0.5) [0.006] (0.284) (0.277) [0.009] [0.016]Service 0.471 0.48 0.009 0.905 0.911 0.0063 0.003(0.499) (0.5) [0.006] (0.293) (0.284) [0.009] [0.016]Profession 0.383 0.396 0.013** 0.52 0.526 0.0056 0.007(0.486) (0.489) [0.006] (0.5) (0.499) [0.016] [0.016]White collar 0.357 0.35 -0.007 0.305 0.311 0.0059 -0.013(0.479) (0.477) [0.006] (0.461) (0.463) [0.014] [0.016]Blue collar 0.26 0.254 -0.006 0.174 0.163 -0.0115 0 .005(0.439) (0.435) [0.005] (0.38) (0.369) [0.012] [0.014]Own house 0.84 0.857 0.018*** 0.89 0.902 0.0123 0.006(0.367) (0.35) [0.004] (0.313) (0.297) [0.010] [0.012]Housing size 40.484 42.314 1.830*** 44.776 45.705 0.9290 0.901(20.253) (21.743) [0.248] (21.577) (22.229) [0.684] [0.706]Observations 14,304 14,425 28,729 2,299 1,841 4,140 32,869Note: household size is meausred in square footage. 10 square feet is equal to 3.3057 square meters.Standard errors in brackets, *** significant at the 1 percent level, ** significant at the 5 percentlevel, and * significant at the 10 percent level.1324.10.TablesTable 4.3: The Effect of Mandatory Private Pension on Household Voluntory SavingSaving rate(1) (2) (3) (4) (5) (6) (7)Period 2002–2008 2002–2008 2002–2008 2002–2008 2000–2004 2002–2008 2002–2008Cohort 20–50 20–50 20–50 20–50 20–50 20–50 51–65Treament group private private private private private banking privatePension effect ̂βDD -0.0162** -0.0202*** -0.0201*** -0.0206*** -0.0053 -0.0050 0.0066[0.006] [0.005] [0.006] [0.006] [0.003] [0.008] [0.008]Baseline mean 0.22 0.22 0.22 0.22 0.26 0.20 0.29Equal to (4) accept accept accept reject reject rejectFamily chacteristic √ √ √ √ √ √Industry & occupation √ √ √ √ √Household wealth √ √ √ √observation 32,869 32,869 32,869 32,869 22,422 5,924 8,593R2 0.023 0.225 0.230 0.250 0.235 0.277 0.298Note: Family characteristic: head’s age, age square, education, gender; spouse’s education; # of childrenunder 18, # of members over 65, # of members above 18, # of working members, and living countydummies Industry & occupation : head’s industry and occupation Household wealth: household totalnon-wage income; dummy for indicating having their own house; housing size. Baseline mean is the savingrate for private sector households during pre-reform period (2002–2004). Standard errors clustered onsector/year in brackets, *** significant at the 1 percent level, ** significant at the 5 percent level, and *significant at the 10 percent level.1334.10. TablesTable 4.4: Empirical Specification ChecksSaving rate(1) (2) (3) (4) (5) (6) (7)Standard error Statistical Statistical Dependent Treatment Different Controlsector/period Inference block Inference wild var. group head’s sample earnedcluster bootstrap bootstrap ln(Y)-ln(C)sectoral choice period incomêβDD -0.0206*** -0.0206*** -0.0206*** -0.0250** -0.0137** -0.0214***-0.0138**[0.001] [0.010] [0.005] [0.006] [0.006]p-value (0.000) (0.001) (0.007) (0.029) (0.015) (0.009) (0.041)observation 32,869 32,869 32,869 32,869 34,707 27,302 32,869R2 0.250 0.260 0.255 0.254 0.255Note: Family chacteristic: head’s age, age square, education, gender; spouse’s education; # of children under 18,# of members over 65, # of members above 18, # of working members, and living county dummies Industry& occupation: head’s industry and occupation Household wealth: household total non-wage income; dummy forindicating having their own house; housing size. Standard errors in block bootstrap and wild bootstrap are calculatedby using 999 random repetitions. Standard errors in brackets, *** significant at the 1 percent level, ** significantat the 5 percent level, and * significant at the 10 percent level.1344.10.TablesTable 4.5: Quantile DD ResultsQuantile of saving rate(1) (2) (3) (4) (5) (6) (7) (8) (9)Quantile 10th 20th 30th 40th 50th 60th 70th 80th 90thPension effect ̂βQDD -0.0394*** -0.0289*** -0.0254*** -0.0242*** -0.0212*** -0.0165** -0.0106 -0.0018 -0.0040[0.011] [0.007] [0.007] [0.007] [0.008] [0.008] [0.009] [0.010] [0.013]observation 32,869 32,869 32,869 32,869 32,869 32,869 32,869 32,869 32,869R2 0.080 0.128 0.162 0.181 0.192 0.191 0.176 0.154 0.106Note: Family characteristic: head’s age, age square, education, gender; spouse’s education; # of children under 18, # of members over 65, #of members above 18, # of working members, and living county dummies Industry & occupation : head’s industry and occupation Householdwealth: household total non-wage income; dummy for indicating having their own house; housing size. 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Appendix FiguresFigure A.1: The Impact of EITC on Intra-Year Labor Supply Pattern (in-cluding Pre-Trend): Married WomenNotes: This figure shows coefficients on EITCit ×M (M includes twelve months pluslast seven months in the previous year) and associated 95% confidence interval fromspecification 2.2 where the dependent variable L is the share of weeks worked in amonth defined as number of working weeks divided by total number of weeks in a month.Therefore, L = 1 if working for the full month, L = 0 if not working for the full month,and 0 < L < 1 if working for partial month. The estimated sample is restricted tomarried women. The dependent variable is regressed on the interaction terms betweenindicator for treatment group EITC and 11 month dummies (October is the omittedmonth) M . The treatment group consists of those individuals that have one or morequalifying children and family income during tax year greater than zero and less than$36,000. The comparison groups comprise (1) those individuals that have family incomeduring tax year greater than zero and less than $36,000 but have no qualifying child. (2)those individuals with one or more qualifying children but whose annual income is justabove $36,000 and below $40,000. (3) childless individuals that have incomes greaterthan $36,000 and below $40,000. All dollar values are measured in 2007 dollars. Theregression controls for treatment group dummy, an indicator for individuals with one ormore qualifying children, an indicator for individuals with family income greater zeroand below $36,000, month fixed effect for those who have qualifying children, monthfixed effect for those who have family income during tax year less than $36,000, monthfixed effect, individual fixed effect, year fixed effect, state fixed effect, monthly stateunemployment rate, state specific time trend (quadratic), an indicator for interviewingmonth, educational attainment, number of children under 18, age, industry fixed effect,industry specific time trend (quadratic), family wealth, a dummy indicating that theindividual worked part-time in the previous year, and month fixed effect specific topart-time workers.151A.1. Appendix FiguresFigure A.2: The Impact of EITC on Intra-Year Labor Supply Pattern (in-cluding Pre-Trend): Married MenNotes: This figure shows coefficients on EITCit ×M (M includes twelve months pluslast seven months in the previous year) and associated 95% confidence interval fromspecification 2.2 where the dependent variable L is the share of weeks worked in amonth defined as number of working weeks divided by total number of weeks in a month.Therefore, L = 1 if working for the full month, L = 0 if not working for the full month,and 0 < L < 1 if working for partial month. The estimated sample is restricted tomarried men. The dependent variable is regressed on the interaction terms betweenindicator for treatment group EITC and 11 month dummies (October is the omittedmonth) M . The treatment group consists of those individuals that have one or morequalifying children and family income during tax year greater than zero and less than$36,000. The comparison groups comprise (1) those individuals that have family incomeduring tax year greater than zero and less than $36,000 but have no qualifying child. (2)those individuals with one or more qualifying children but whose annual income is justabove $36,000 and below $40,000. (3) childless individuals that have incomes greaterthan $36,000 and below $40,000. All dollar values are measured in 2007 dollars. Theregression controls for treatment group dummy, an indicator for individuals with one ormore qualifying children, an indicator for individuals with family income greater zeroand below $36,000, month fixed effect for those who have qualifying children, monthfixed effect for those who have family income during tax year less than $36,000, monthfixed effect, individual fixed effect, year fixed effect, state fixed effect, monthly stateunemployment rate, state specific time trend (quadratic), an indicator for interviewingmonth, educational attainment, number of children under 18, age, industry fixed effect,industry specific time trend (quadratic), family wealth, a dummy indicating that theindividual worked part-time in the previous year, and month fixed effect specific topart-time workers.152A.1. Appendix FiguresFigure A.3: The Impact of EITC on Intra-Year Labor Supply Pattern (in-cluding Pre-Trend): Single WomenNotes: This figure shows coefficients on EITCit ×M (M includes twelve months pluslast seven months in the previous year) and associated 95% confidence interval fromspecification 2.2 where the dependent variable L is the share of weeks worked in amonth defined as number of working weeks divided by total number of weeks in a month.Therefore, L = 1 if working for the full month, L = 0 if not working for the full month,and 0 < L < 1 if working for partial month. The estimated sample is restricted tosingle women. The dependent variable is regressed on the interaction terms betweenindicator for treatment group EITC and 11 month dummies (October is the omittedmonth) M . The treatment group consists of those individuals that have one or morequalifying children and family income during tax year greater than zero and less than$33,000. The comparison groups comprise (1) those individuals that have family incomeduring tax year greater than zero and less than $33,000 but have no qualifying child. (2)those individuals with one or more qualifying children but whose annual income is justabove $33,000 and below $40,000. (3) childless individuals that have incomes greaterthan $33,000 and below $40,000. All dollar values are measured in 2007 dollars. Theregression controls for treatment group dummy, an indicator for individuals with one ormore qualifying children, an indicator for individuals with family income greater zeroand below $33,000, month fixed effect for those who have qualifying children, monthfixed effect for those who have family income during tax year less than $33,000, monthfixed effect, individual fixed effect, year fixed effect, state fixed effect, monthly stateunemployment rate, state specific time trend (quadratic), an indicator for interviewingmonth, educational attainment, number of children under 18, age, industry fixed effect,industry specific time trend (quadratic), family wealth, a dummy indicating that theindividual worked part-time in the previous year, and month fixed effect specific topart-time workers.153Appendix BAppendix to Chapter 3B.1 Appendix Tables154B.1. Appendix TablesTable B.1: Placebo Test for Other Age CutoffPanel A: Log(outpatient expenditure)Cutoff Age Coefficient on Cutoff Age Coefficient on(days) cutoff (days) cutoff886 0.66 1186 -0.63[0.42] [0.39]916 0.09 1216 -0.31[0.37] [0.42]946 -0.55 1246 0.85*[0.39] [0.50]976 -0.46 1276 -0.59[0.38] [0.42]1006 0.01 1306 -0.22[0.38] [0.42]1096 -6.90*** 1336 0.51(or 1095) [0.49] [0.44]Panel B: Log(outpatient visits)Cutoff Age Coefficient on Cutoff Age Coefficient on(days) cutoff (days) cutoff886 0.24 1186 -0.80***[0.25] [0.30]916 -0.21 1216 -0.23[0.29] [0.27]946 -0.21 1246 0.59*[0.27] [0.30]976 -0.26 1276 -0.60**[0.25] [0.26]1006 -0.26 1306 -0.12[0.22] [0.31]1096 -4.73*** 1336 0.19(or 1095) [0.31] [0.31]Note: We collapse the individual-level data into age cells. Age is measured in days. Thefirst two columns present our main results. Each observation (age cell) represents outpatientexpenditures and visits from 410,517 children who were born in 2003 and 2004 (when they areage 2 and 3). Therefore, we use 2005–2008 NHI data to obtain the above estimated results.The dependent variables for the RD estimation are the log of total outpatient expenditureand the log of the total number of outpatient visits at each day of age. Column (1) and (3)indicates different cutoff age (measured in days) used in RD estimation. Note that 1096th (or1095th) age day is the 3rd birthday and its estimate is corresponding to our main result inTable 3.6. Column (2) and (4) present estimated regression discontinuities of each interestedoutcome using data within 90 days before and after the 3rd birthday and report the differencein local linear regression estimates just before and after the 3rd birthday by using a triangularkernel, which gives higher weight on the data close to the 3rd birthday (equation (3.3)). Allcoefficients on Age3 and their standard errors have been multiplied by 100. Robust standarderrors are in parentheses. *** significant at the 1 percent level, ** significant at the 5 percentlevel, and * significant at the 10 percent level. 155B.1. Appendix TablesTable B.2: Sensitivity to Bandwidth and Polynomial Selection in Paramet-ric RD RegressionsLog(outpatient expenditure)Bandwidth (days) 60 120 180 240 300 360Polynominal1 -6.69*** -6.19*** -5.54*** -5.10*** -4.54*** -4.65***[0.48] [0.33] [0.28] [0.24] [0.23] [0.20]2 -6.58*** -6.90*** -6.61*** -6.24*** -6.06*** -5.29***[0.74] [0.51] [0.40] [0.37] [0.32] [0.30]3 -7.07*** -6.68*** -7.04*** -6.98*** -6.85*** -6.94***[1.11] [0.70] [0.56] [0.47] [0.42] [0.40]Log(outpatient visits)Bandwidth (days) 60 120 180 240 300 360Polynominal1 -4.55*** -3.92*** -3.39*** -2.88*** -2.35*** -2.52***[0.34] [0.24] [0.20] [0.18] [0.17] [0.15]2 -4.33*** -4.97*** -4.36*** -4.12*** -3.89*** -3.04***[0.53] [0.37] [0.29] [0.26] [0.23] [0.23]3 -4.86*** -4.41*** -5.07*** -4.72*** -4.68*** -4.84***[0.83] [0.49] [0.41] [0.33] [0.30] [0.29]Note: We collapse the individual-level data into age cells. Age is measured in days. Thefirst two columns present our main results. Each observation (age cell) represents outpatientexpenditures and visits from 410,517 children who were born in 2003 and 2004 (when they areage 2 and 3). Therefore, we use 2005–2008 NHI data to obtain the above estimated results.The dependent variables for the RD estimation are the log of total outpatient expenditure andthe log of the total number of outpatient visits at each day of age. Each row indicates differentorder of polynomials used in RD estimation and each column denotes various bandwidthchoice. We obtain RD estimates using OLS regression with uniform kernel function (similar tothe parametric estimation in Table 3.6). Robust standard error in parentheses. All coefficientson Age3 and their standard errors have been multiplied by 100. Robust standard errors arein parentheses. *** significant at the 1 percent level, ** significant at the 5 percent level, and* significant at the 10 percent level.156B.1. Appendix TablesTable B.3: Sensitivity to Bandwidth Selector and Kernel Function Se-lection in Nonparametric RD RegressionsLog(outpatient expenditure) Log(outpatient visits)Bandwidth CCT IK CV CCT IK CVselectorKernel functionTriangular -6.64*** -6.63*** -6.56*** -4.48*** -4.51*** -4.45***[0.48] [0.44] [0.40] [0.39] [0.35] [0.45]Bandwidth 81 89 105 67 79 54Uniform -6.68*** -6.69*** -6.58*** -4.46*** -4.46*** -4.40***[0.47] [0.46] [0.52] [0.36] [0.36] [0.37]Bandwidth 65 66 54 56 56 54Epanechnikov -6.64*** -6.64*** -6.64*** -4.45*** -4.49*** -4.43***[0.47] [0.44] [0.42] [0.39] [0.35] [0.42]Bandwidth 75 82 88 61 70 54Note: We collapse the individual-level data into age cells. Age is measured in days.The first two columns present our main results. Each observation (age cell) representsoutpatient expenditures and visits from 410,517 children who were born in 2003 and2004 (when they are age 2 and 3). Therefore, we use 2005–2008 NHI data to obtainthe above estimated results. The dependent variables for the RD estimation are the logof total outpatient expenditure and the log of the total number of outpatient visits ateach day of age. Each row indicates the specific kernel function used in nonparametricRD estimation and each column denotes the optimal bandwidth selector for choosingbandwidth. CCT is an optimal bandwidth selection method proposed by Matias D.Cattaneo, Sebastian Calonico and Rocio Titiunik (2013). IK is an optimal bandwidthselection procedure proposed by imbens and kalyanaraman (2012). CV is an optimalbandwidth selection procedure proposed by Ludwig and Miller (2007). The above tablepresent estimated regression discontinuities of each interested outcome using data withinspecific bandwidth before and after the 3rd birthday and report the difference in locallinear regression estimates just before and after the 3rd birthday by using a triangularkernel, which gives higher weight on the data close to the 3rd birthday (equation (3.3)).All coefficients on Age3 and their standard errors have been multiplied by 100. Robuststandard errors are in parentheses. *** significant at the 1 percent level, ** significant atthe 5 percent level, and * significant at the 10 percent level.157B.1. Appendix TablesTable B.4: Donut RD for Outpatient Expenditure and VisitsLog(outpatient expenditure)Size of Donut around 0 3 6 9 12 15 18 213rd birthdayAge3 (X100) -6.90*** -6.67*** -6.84*** -6.56*** -6.20*** -6.30*** -6.61*** -6.42***[0.54] [0.48] [0.52] [0.54] [0.55] [0.61] [0.65] [0.76]Log(outpatient visits)Size of Donut around 0 3 6 9 12 15 18 213rd birthdayAge3 (X100) -4.73*** -4.43*** -4.42*** -4.46*** -4.37*** -4.54*** -4.70*** -4.88***[0.38] [0.27] [0.27] [0.29] [0.29] [0.36] [0.42] [0.45]Note: We collapse the individual-level data into age cells. Age is measured in days. The first twocolumns present our main results. Each observation (age cell) represents outpatient expendituresand visits from 410,517 children who were born in 2003 and 2004 (when they are age 2 and 3).Therefore, we use 2005–2008 NHI data to obtain the above estimated results. The dependentvariables for the RD estimation are the log of total outpatient expenditure and the log of thetotal number of outpatient visits at each day of age. Each column presents estimated regressiondiscontinuities of each interested outcome using data within 90 days before and after the 3rdbirthday and report the difference in local linear regression estimates just before and after the3rd birthday by using a triangular kernel, which gives higher weight on the data close to the3rd birthday (equation (3.3)). we conduct a “donut” RD (Barreca et al., 2011; Shigeoka, 2014)by systematically excluding outpatient expenditure and visits within 3–21 days before and afterthe 3rd birthday All coefficients on Age3 and their standard errors have been multiplied by 100.Robust standard errors are in parentheses. *** significant at the 1 percent level, ** significantat the 5 percent level, and * significant at the 10 percent level.158

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