Arts, Faculty of
Vancouver School of Economics
DSpace
UBCV
Duan, Yige
Doctor of Philosophy - PhD
University of British Columbia
This dissertation consists of three chapters. The first chapter studies the long-run effect of job displacement on workers' commuting costs to subsequent jobs. Using German employee-employer data, geo-coordinates of workers' residences and workplaces, and a matched event study design, we estimate the response of workers' commuting distances to job displacement in mass layoffs. Displaced workers take up new jobs requiring 21 percent longer commuting, and the effect persists in the subsequent 10 years. To quantify the monetary value of increased commuting, we develop and estimate an on-the-job search model for workers' willingness to pay to avoid commuting. The extra commuting cost amounts to one-fifth of the wage losses facing displaced workers, which exacerbates the total cost of job displacement. In the second chapter, we show that dockless bike sharing solves the "last-mile problem" in public transportation by reducing the commuting cost between home and subway stations. As such, shared bikes increase the attractiveness and prices of apartments distant from subways relative to those nearby. Using resale apartment data and the staggered entry of bike sharing in 10 Chinese cities, we find that bike sharing reduces the housing price premiums near the subway by 29 percent. The reduction is equivalent to 1,893-2,127 CYN (282-317 USD) of the commuting cost per household per year over 30 years of residence. It is driven by a relative increase in the listing prices of and the demand for apartments distant from vis-à-vis proximate to subways. The third chapter assesses the effects of a corporate income tax cut for small businesses on employee earnings. Following a 2014 reform in Quebec, Canada, firms receiving the tax cut significantly raised the earnings of their workers. The earnings growth is connected with firms’ increased profits, as the effects are larger in high-growth industries where firms invest more and enjoy greater productivity. We estimate that workers bear up to three-quarters of the tax burden, and 35 percent of the surplus from the tax cut is passed onto workers.
Essays on Worker Mobility, SpatialLabor Markets, and Urban RealEstate MarketsbyYige DuanB.A, Fudan University, 2015M.A, National University of Singapore, 2016A 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)June 2024© Yige Duan 2024The following individuals certify that they have read, and recommend to the Faculty of Graduateand Postdoctoral Studies for acceptance, the dissertation entitled:Essays on Worker Mobility, Spatial Labor Markets, and Urban Real Estate Marketssubmitted by Yige Duan in partial fulfilment of the requirements forthe degree of Doctor of Philosophyin EconomicsExamining Committee:Thomas Lemieux, Professor, Economics, UBCCo-supervisorNicole Fortin, Professor, Economics, UBCCo-supervisorKyungchul Song, Professor, Economics, UBCSupervisory Committee MemberDavid A. Green, Professor, Economics, UBCUniversity ExaminerThomas Davidoff, Associate Professor, Strategy and Business Economics, UBCUniversity ExaminerFabian Lange, Professor, Economics, McGill UniversityExternal ExaminerAdditional Supervisory Committee Members:Raffaele Saggio, Assistant Professor, Economics, UBCSupervisory Committee MemberiiAbstractThis dissertation consists of three chapters. The first chapter studies the long-run effect of jobdisplacement on workers’ commuting costs to subsequent jobs. Using German employee-employerdata, geo-coordinates of workers’ residences and workplaces, and a matched event study design,we estimate the response of workers’ commuting distances to job displacement in mass layoffs.Displaced workers take up new jobs requiring 21 percent longer commuting, and the effect persistsin the subsequent 10 years. To quantify the monetary value of increased commuting, we develop andestimate an on-the-job search model for workers’ willingness to pay to avoid commuting. The extracommuting cost amounts to one-fifth of the wage losses facing displaced workers, which exacerbatesthe total cost of job displacement.In the second chapter, we show that dockless bike sharing solves the “last-mile problem” inpublic transportation by reducing the commuting cost between home and subway stations. Assuch, shared bikes increase the attractiveness and prices of apartments distant from subways rel-ative to those nearby. Using resale apartment data and the staggered entry of bike sharing in 10Chinese cities, we find that bike sharing reduces the housing price premiums near the subway by29 percent. The reduction is equivalent to 1,893–2,127 CYN (282–317 USD) of the commuting costper household per year over 30 years of residence. It is driven by a relative increase in the listingprices of and the demand for apartments distant from vis-a`-vis proximate to subways.The third chapter assesses the effects of a corporate income tax cut for small businesses onemployee earnings. Following a 2014 reform in Quebec, Canada, firms receiving the tax cut signifi-cantly raised the earnings of their workers. The earnings growth is connected with firms’ increasedprofits, as the effects are larger in high-growth industries where firms invest more and enjoy greaterproductivity. We estimate that workers bear up to three-quarters of the tax burden, and 35 percentof the surplus from the tax cut is passed onto workers.iiiLay SummaryMy dissertation consists of three chapters in labor and urban economics. The first chapter in-vestigates the impacts of involuntary job loss on workers’ commuting behavior. After losing theirprevious jobs, workers commute longer distances to subsequent jobs, and the increased commutingcost exacerbates the welfare cost of job loss beyond earnings and wages. The second chapter studieshow commuting costs shape individuals’ residential location choices. In 10 major cities of China,dockless bike sharing makes subways more accessible to residents distant from subway stations. Assuch, housing prices of distant apartments rise relative to those nearby to capture the reduced com-muting cost. The third chapter evaluates the labor market effects of a corporate tax cut targetingsmall manufacturing businesses in Quebec, Canada. The tax cut increases firms’ labor and capitalinput, profits, and productivity, while workers at these firms enjoy higher earnings.ivPrefaceChapter 2 is joint work with Ramona Jost and Oskar Jost at the Institute for Employment Researchof the German Federal Employment Agency. I was involved throughout each stage of this research,including data analysis, modeling, writing, and subsequent revisions of the research for publication.Chapter 3 is joint work with Junhong Chu at the University of Hong Kong and Xianling Yangand Li Wang at Lianjia Research Institute. Chapter 4 is joint work with Terry S. Moon at theUniversity of British Columbia. In both chapters, I formulated the research idea, performed themajority of data analysis, co-wrote the manuscript, and participated equally in subsequent revisionsof the research for publication.A version of Chapter 3 was published as Chu, Junhong, Yige Duan, Xianling Yang, and Li Wang.“The Last Mile Matters: Impact of Dockless Bike Sharing on Subway Housing Price Premium.”Management Science 67, no. 1 (2021): 297–316.vTable of ContentsAbstract . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . iiiLay Summary . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . ivPreface . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . vTable of Contents . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . viList of Tables . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . ixList of Figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . xiList of Abbreviations . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . xiiiAcknowledgements . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . xiv1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 12 Beyond Lost Earnings: Job Displacement and the Cost of Commuting . . . . . 62.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 62.1.1 Related Literature . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 92.2 Data and Empirical Methods . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 102.2.1 Mass Layoffs and Displaced Workers . . . . . . . . . . . . . . . . . . . . . . 122.2.2 Matching Non-Displaced Workers . . . . . . . . . . . . . . . . . . . . . . . . 122.2.3 Event Study . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 132.3 The Effects of Job Displacement . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 142.3.1 The Value of Granularity . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 162.3.2 Effect Heterogeneity . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 162.3.3 Trade off Wage Losses and Longer Commuting . . . . . . . . . . . . . . . . . 172.3.4 Robustness . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 182.4 A Job Search Model . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 182.4.1 Job Match Surplus and the WTP for Commuting . . . . . . . . . . . . . . . 202.4.2 Recovery from Job Displacement . . . . . . . . . . . . . . . . . . . . . . . . . 212.5 The Monetary Cost of Commuting . . . . . . . . . . . . . . . . . . . . . . . . . . . . 222.5.1 Identification . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 23vi2.5.2 Structural Estimates . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 252.5.3 Welfare Implications . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 272.6 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 283 The Impact of Dockless Bike Sharing on Subway Housing Price Premiums . . 403.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 403.1.1 Related Literature . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 413.2 Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 433.2.1 Housing Prices and Characteristics . . . . . . . . . . . . . . . . . . . . . . . 433.2.2 Entry of Bike Sharing . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 443.2.3 Distance to Subway Stations . . . . . . . . . . . . . . . . . . . . . . . . . . . 443.2.4 Summary Statistics . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 453.3 Empirical Strategy . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 453.3.1 Difference-in-Differences at the Apartment Level . . . . . . . . . . . . . . . . 453.3.2 Two-Step Estimation at the City-Month Level . . . . . . . . . . . . . . . . . 463.4 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 473.4.1 Mechanisms . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 483.4.2 Welfare Implications . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 493.4.3 Effect Heterogeneity . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 503.4.4 Robustness . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 513.5 Validation . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 523.5.1 Parallel Pre-Trends . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 523.5.2 Exogenous and Unanticipated Entry . . . . . . . . . . . . . . . . . . . . . . . 523.5.3 No Compositional Change . . . . . . . . . . . . . . . . . . . . . . . . . . . . 543.5.4 Alternative Explanations . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 543.6 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 574 Corporate Tax Cuts and Worker Earnings: Evidence from Small Businesses . 674.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 674.1.1 Related Literature . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 694.2 Institutional Background and Empirical Strategy . . . . . . . . . . . . . . . . . . . . 704.2.1 Corporate Income Taxes in Canada . . . . . . . . . . . . . . . . . . . . . . . 704.2.2 Identifying the Tax Effects on Firm Outcomes . . . . . . . . . . . . . . . . . 714.2.3 Identifying the Tax Effects on Worker Outcomes . . . . . . . . . . . . . . . . 724.3 Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 734.3.1 Firm Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 734.3.2 Worker Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 744.4 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 754.4.1 Comparing Elasticities with Prior Estimates . . . . . . . . . . . . . . . . . . 784.4.2 Robustness . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 78vii4.5 Mechanisms . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 794.5.1 Alternative Mechanisms . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 804.5.2 Contemporaneous Tax Reforms . . . . . . . . . . . . . . . . . . . . . . . . . 824.6 Welfare Implications . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 834.6.1 Incidence of Corporate Taxes on Workers and Firm Owners . . . . . . . . . 834.6.2 Pass-Through Estimates . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 844.6.3 Cost-per-Job Estimate . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 854.7 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 865 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 98Bibliography . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 99AppendicesA Appendices to Chapter 2 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 109A.1 Additional Data Sets . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 109A.2 Additional Figures and Tables . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 110A.3 Trade off Wage Losses and Commuting Costs . . . . . . . . . . . . . . . . . . . . . . 127A.4 Model Proofs and Extensions . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 128A.4.1 Proof for Proposition 1 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 128A.4.2 Proof for Proposition 2 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 128A.4.3 Endogenous Search Efforts . . . . . . . . . . . . . . . . . . . . . . . . . . . . 129A.4.4 Human Capital Dynamics . . . . . . . . . . . . . . . . . . . . . . . . . . . . 131A.5 Structural Estimation . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 132A.5.1 Implementation . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 132A.5.2 Identifying the Copula Parameter . . . . . . . . . . . . . . . . . . . . . . . . 133A.5.3 Identifying Unemployment Benefits . . . . . . . . . . . . . . . . . . . . . . . 133A.5.4 Sensitivity Analysis . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 134B Appendices to Chapter 3 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 140B.1 Distance to the Nearest Subway Station . . . . . . . . . . . . . . . . . . . . . . . . . 140B.2 Implied Reduction of Commuting Costs . . . . . . . . . . . . . . . . . . . . . . . . . 141B.3 Additional Figures and Tables . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 142C Appendices to Chapter 4 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 146C.1 Additional Figures and Tables . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 146C.2 User Cost of Capital . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 160C.3 Robustness . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 161viiiList of Tables2.1 Pre-Layoff Worker Characteristics . . . . . . . . . . . . . . . . . . . . . . . . . . . . 372.2 Effects of Job Displacement on Employment, Wage, and Commuting . . . . . . . . . 372.3 Margins of Adjustment . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 382.4 The Value of Granular Commuting Data . . . . . . . . . . . . . . . . . . . . . . . . . 382.5 Simulated Method of Moments: Results . . . . . . . . . . . . . . . . . . . . . . . . . 392.6 Willingness to Pay for Less Commuting . . . . . . . . . . . . . . . . . . . . . . . . . 393.1 City Characteristics . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 623.2 Summary Statistics . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 633.3 Bike Sharing and the Subway Housing Price Premiums . . . . . . . . . . . . . . . . . 633.4 Mechanism . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 643.5 Effect Heterogeneity . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 643.6 Robustness . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 653.7 Validation . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 653.8 Alternative Explanations . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 664.1 Summary Statistics . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 934.2 Effective Tax Rates, Tax Payable, and Taxable Income . . . . . . . . . . . . . . . . . 944.3 Employment, Payrolls, and Capital Stock . . . . . . . . . . . . . . . . . . . . . . . . 944.4 Incumbent Worker Earnings and Job Transitions . . . . . . . . . . . . . . . . . . . . 954.5 Sales, After-Tax Profits, and Productivity . . . . . . . . . . . . . . . . . . . . . . . . 954.6 High-Growth versus Low-Growth Industries . . . . . . . . . . . . . . . . . . . . . . . 964.7 Pass-Through Estimates . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 97A.1 Share of Commuters by Modes of Commuting and Distance Segments . . . . . . . . 120A.2 Effects of Job Displacement on Labor Supply and Earnings . . . . . . . . . . . . . . 121A.3 Additional Effects of Job Displacement . . . . . . . . . . . . . . . . . . . . . . . . . . 121A.4 Effect Heterogeneity by Worker Demographics . . . . . . . . . . . . . . . . . . . . . . 122A.5 Effect Heterogeneity by Pre-Layoff Firm Characteristics . . . . . . . . . . . . . . . . 123A.6 Effect Heterogeneity by Labor Market Conditions . . . . . . . . . . . . . . . . . . . . 124A.7 Robustness . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 125A.8 Alternative Measures of Commuting Time . . . . . . . . . . . . . . . . . . . . . . . . 126A.9 Dependence between AKM Firm Effects and Commuting Distances . . . . . . . . . . 138ixA.10 Dependence between AKM Worker Effects and Commuting Distances . . . . . . . . 139B.1 Measuring Distance to the Subway . . . . . . . . . . . . . . . . . . . . . . . . . . . . 140B.2 Reduction in Commuting Costs per Year . . . . . . . . . . . . . . . . . . . . . . . . . 141B.3 Effect Heterogeneity across Cities . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 144B.4 Exogenous Entry of Bike Sharing: The Hazard Rate Test . . . . . . . . . . . . . . . 145B.5 Exogenous Entry of Bike Sharing: Randomized Entry Dates . . . . . . . . . . . . . . 145C.1 Corporate Income Tax Rates . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 148C.2 Entrant Earnings and Worker Composition . . . . . . . . . . . . . . . . . . . . . . . 149C.3 Other Firm Outcomes . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 149C.4 Owner Outcomes . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 150C.5 Tax Effects on Workers with and without Ownership . . . . . . . . . . . . . . . . . . 150C.6 Summary Statistics: High-Growth versus Low-Growth Industries . . . . . . . . . . . 151C.7 Tax Effects by High-Tech versus Low-Tech Industries . . . . . . . . . . . . . . . . . . 152C.8 Tax Effects by Pre-Reform Leverage Ratio . . . . . . . . . . . . . . . . . . . . . . . . 153C.9 Tax Effects by Pre-Reform Capital Intensity . . . . . . . . . . . . . . . . . . . . . . . 154C.10 Tax Effects by Pre-Reform Labor Market Concentration . . . . . . . . . . . . . . . . 155C.11 Tax Effects by Worker Gender . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 156C.12 Tax Effects by Worker Age and Earnings Quartiles . . . . . . . . . . . . . . . . . . . 157C.13 Additional Tax Deductions for Transportation Costs . . . . . . . . . . . . . . . . . . 158C.14 Investment Tax Credits . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 158C.15 Additional Tax Deductions for Transportation Costs . . . . . . . . . . . . . . . . . . 159xList of Figures2.1 Mass Layoff Statistics . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 302.2 Effects of Job Displacement on Employment, Wage, and Commuting . . . . . . . . . 312.3 Margins of Adjustment . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 322.4 The Value of Granular Commuting Data . . . . . . . . . . . . . . . . . . . . . . . . . 332.5 Model Implications and Empirical Evidence . . . . . . . . . . . . . . . . . . . . . . . 342.6 Job Offer Distributions . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 352.7 Actual and Simulated Effects of Job Displacement . . . . . . . . . . . . . . . . . . . 363.1 Baidu Search Index for “Bike Sharing” . . . . . . . . . . . . . . . . . . . . . . . . . . 593.2 Distribution of Apartments by Distance to the Nearest Subway Station . . . . . . . 603.3 Estimates by Distance Segment . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 613.4 Event Study Estimates . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 614.1 Small Business Tax Rates in Quebec, British Columbia, and Ontario . . . . . . . . . 874.2 Effective Tax Rates, Tax Payable, and Taxable Income . . . . . . . . . . . . . . . . . 884.3 Employment, Payrolls, and Capital Stock . . . . . . . . . . . . . . . . . . . . . . . . 894.4 Incumbent Worker Earnings . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 904.5 Sales, After-Tax Profits, and Productivity . . . . . . . . . . . . . . . . . . . . . . . . 914.6 Tax Effects by High-Growth versus Low-Growth Industries . . . . . . . . . . . . . . 92A.1 Distribution of Commuting Distances and Time . . . . . . . . . . . . . . . . . . . . . 110A.2 Effects of Job Displacement on Labor Supply and Earnings . . . . . . . . . . . . . . 111A.3 Additional Effects of Job Displacement . . . . . . . . . . . . . . . . . . . . . . . . . . 112A.4 Effect Heterogeneity by Worker Demographics . . . . . . . . . . . . . . . . . . . . . . 113A.5 Effect Heterogeneity by Pre-Layoff Job Characteristics . . . . . . . . . . . . . . . . . 114A.6 Effect Heterogeneity by Labor Market Condition . . . . . . . . . . . . . . . . . . . . 115A.7 Including Part-Time Jobs . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 116A.8 Displacement due to Establishment Closure . . . . . . . . . . . . . . . . . . . . . . . 116A.9 Selection into Reemployment . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 117A.10 Commuting Zone by Year Fixed Effects . . . . . . . . . . . . . . . . . . . . . . . . . 117A.11 Excluding Large Layoffs . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 118A.12 Excluding Multi-Location Establishments . . . . . . . . . . . . . . . . . . . . . . . . 118A.13 Alternative Measures of Commuting Time . . . . . . . . . . . . . . . . . . . . . . . . 119xiA.14 Heterogeneous and Dynamic Effects . . . . . . . . . . . . . . . . . . . . . . . . . . . 119A.15 Identifying the Commuting Cost . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 135A.16 Identifying Unemployment Benefits . . . . . . . . . . . . . . . . . . . . . . . . . . . . 135A.17 Sensitivity Analysis . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 136A.18 Simulated Effects of Job Displacement with Remote Work . . . . . . . . . . . . . . . 137B.1 Exogenous Entry of Bike Sharing: Predictive Power of City Characteristics . . . . . 142B.2 Monthly Average Prices of Resale and Rental Apartments . . . . . . . . . . . . . . . 143C.1 SBD Phase-out Schedule and Size Distribution of SBD Claimants . . . . . . . . . . . 146C.2 Firm Entry and Exit . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 147C.3 Additional Fixed Effects . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 161C.4 Firms with Taxable Capital below 10 Million CAD . . . . . . . . . . . . . . . . . . . 162C.5 Including Other Provinces . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 163C.6 Including Other Sectors . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 164C.7 Including Part-time and Multiple-job Workers and Dropping Tenure Restrictions . . 165C.8 Distribution of Taxable Income among Treated Firms . . . . . . . . . . . . . . . . . 165C.9 Firms with Taxable Income Close to the Eligibility Threshold . . . . . . . . . . . . . 166C.10 Placebo Tests Using Non-CCPCs . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 167C.11 Difference-in-Differences (DID) Estimates . . . . . . . . . . . . . . . . . . . . . . . . 168C.12 Worker Reallocation . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 169xiiList of AbbreviationsAKM Abowd, Kramarz, and Margolis (1999)BHP Establishment History PanelCAD Canadian DollarCCPC Canadian-Controlled Private CorporationCNY Chinese YuanDID Difference in DifferencesEBITDA Earnings before Interest, Taxes, Depreciation, and Amortizationft2 Square FootGPS Global Positioning SystemIEB Integrated Employment Biographieskm KilometerM&P Manufacturing and Processingm2 Square MeterOLS Ordinary Least SquaresSBD Small Business DeductionSMM Simulated Method of Momentss.d. Standard Deviations.e. Standard ErrorTFP Total Factor ProductivityU.S. United StatesUSD United States DollarWTP Willingness to PayxiiiAcknowledgementsI am deeply indebted to my advisors, Thomas Lemieux, Nicole Fortin, Raffaele Saggio, and KevinSong, for their generous support and guidance; to my pre-doctoral advisors, Ivan Png, JunhongChu, Huailu Li, and Kaiwen Leong, for encouraging me to pursue an academic career; and to myfamily for their unconditional love. This work would not have been possible without the dedicationof my coauthors Oskar Jost, Ramona Jost, and Terry S. Moon.I also want to thank many UBC faculties, Gorkem Bostanci, Victor Couture, Giovanni Gallipoli,David Green, Sam Hwang, Torsten Jaccard, Hiro Kasahara, Vadim Marmer, and Sam Norries, mycolleagues and friends, Pierre-Loup Beauregard, Paul Corcuera, Sam Gyetvay, Sev Hou, KonstantinKo¨rner, Uyseok Lee, Catherine van der List, Leo Ma, Ratzanyel Rinco´n, and Steven Zhang, amongmany others, for their constant support and help.xivChapter 1IntroductionWorkers’ mobility across space plays a significant role in individuals’ job search and labor supplydecisions and households’ location choices. Limited worker mobility, such as the cost of commut-ing and relocation, is also a key determinant of labor market dynamics, leaving room for policyinterventions to enhance market efficiency and welfare. This dissertation aims to contribute toour understanding of worker mobility in the following aspects: How do individuals value the costof commuting? How does the commuting cost affect people’s location choices and real economicoutcomes? Finally, how does limited worker mobility shape the effectiveness of economic policiesthat target a specific set of firms and workers in a labor market?This dissertation consists of three chapters that analyze the role of worker mobility with re-gard to spatial labor markets, urban real estate markets, and labor market policies. Chapter 2focuses on the commuting behavior of displaced workers, studying how job displacement impactstheir commuting distances and monetary commuting cost to subsequent jobs, and evaluates thewelfare implication for the total cost of job loss. Chapter 3 relates commuting costs to individuals’residential choices, showing that accessibility to subways is an important consideration in the urbanreal estate market, and that a technology-driven reduction in short-distance commuting costs (bikesharing) narrows the housing price premiums near subway stations. Finally, Chapter 4 evaluatesthe labor market impacts of a corporate tax policy in a frictional labor market, showing that smallbusinesses and their workers respond positively to a corporate tax cut by increasing capital and la-bor input and labor earnings. In particular, workers benefit from the tax cut via increased earnings,partly by sharing firms’ enhanced profitability and productivity.Chapter 2 examines the role of commuting costs in individuals’ job search behavior and recoveryfrom job displacement. While a large literature has documented the earnings and wage lossesfacing displaced workers, less is known about how job displacement affects non-wage amenities ofsubsequent jobs, especially the commuting cost between home and work. Besides, there is littleevidence on how non-wage job amenities are accounted for in the total cost of job loss. Combininggeo-referenced employee-employer data in Germany with a matched event study design, we estimatethat workers who have lost their jobs in mass layoffs experience not only large and persistent wagelosses but also longer commuting distances to subsequent jobs. Structurally estimating an on-the-job search model, we find that the increased commuting distances imply a large monetary cost equalto one-fifth of the wage losses. Therefore, accounting for the commuting effect would exacerbateworkers’ total cost of job displacement beyond the earnings losses.We take two steps to quantify the commuting effect of job displacement in monetary terms.1First, we estimate the causal effect of job displacement on workers’ commuting distances. Usinggeo-coordinate level data on workers’ residences and workplaces, we measure their commutingdistances between home and work along actual routes. The geo-coordinate level information isimportant to capture workers’ commuting behavior within administrative regions, as a large shareof German workers commute within counties or cities. Then to identify the causal effect of jobdisplacement, we compare workers who involuntarily lose their jobs in mass layoffs with a matchedcontrol group of statistically similar workers who are not displaced in the same year (Jacobson etal., 1993; Krolikowski, 2018; Schmieder et al., 2023). Analogous to the wage losses documented inprior literature, we find a large and persistent increase in workers’ commuting distances after jobdisplacement. In the first year, workers commute 20.9 percent (3.35 kilometers one-way) longerdistances to their new jobs; over the next 10 years, the effect gradually declines as workers switchjobs from distant to nearby firms with respect to their homes.In the second step, we develop and structurally estimate a job search model to quantify workers’willingness to pay (WTP) for less commuting. The model features on-the-job search and firmheterogeneity in productivity, non-wage amenities, and commuting distances. This establishes ajob ladder where workers prefer more productive and less distant jobs to vice versa. Due to jobsearch friction, workers losing their previous jobs take up less preferred jobs in the short run,implying a wage cut and an increase in commuting distance. However, on-the-job allows workersto move to more preferred jobs in the long run, which explains the recovery in both outcomes.Structurally estimating the model yields a sizeable monetary commuting cost: Each kilometer ofcommuting is worth 1.36 percent of workers’ average daily wage, and an average worker’s commutingcost equals 20 euros per day or one-fifth of their average daily wage. As workers receive lower wagesbut commute longer distances after displacement, the increase in monetary commuting cost addssignificantly to the total cost of job loss by one-fifth of the wage losses.Chapter 2 makes three contributions to the literature. First, it extends the literature on jobdisplacement (e.g., Jacobson et al., 1993; Davis and von Wachter, 2011; Burdett et al., 2020;Schmieder et al., 2023; Bertheau et al., 2023; Athey et al., 2023) by examining the commutingeffects and highlighting the non-wage aspects in the total cost of job loss. Relative to existingstudies on the mobility outcomes of displaced workers (Meekes and Hassink, 2019, 2022; Fackler andRippe, 2017; Huttunen et al., 2018), it takes further steps to measure commuting with granular geo-coordinate data, estimate the monetary cost of commuting using a structural model, and comparethe commuting effects with the wage losses. Second, it contributes to the literature that estimatesthe cost of commuting. Our estimates are comparable with existing studies (Small et al., 2005;Van Ommeren and Fosgerau, 2009; Le Barbanchon et al., 2021; Mattia, 2023) but significantlylarger than what is implied by compensating wage differentials (Mulalic et al., 2014; Dauth andHaller, 2020). The discrepancy highlights the role of job search friction, which prevents wagesfrom equalizing the difference in commuting costs across jobs. Finally, our study belongs to theburgeoning literature that quantifies the non-wage job values using structural methods (Sorkin,2018; Taber and Vejlin, 2020; Lagos, 2021; Sockin, 2022; Maestas et al., 2023).2The cost of commuting also affects urban dwellers’ residential location choices. In metropolitansworldwide, while public transportation (e.g., subways and trams) provides an affordable means ofstation-to-station commuting, door-to-station commuting remains costly and gives rise to the “last-mile problem”. To alleviate the last-mile commuting cost, people are willing to pay higher housingprices to live near subway stations, resulting in a price premium for apartments near the subwayrelative to those further away (Dewees, 1976; Coulson and Engle, 1987; Baum-Snow and Kahn, 2000;Gibbons and Machin, 2005; Fesselmeyer and Liu, 2018). In Chapter 3, we argue that dockless bikesharing, an innovative and economical means of short-distance urban commuting, solves the last-mile problem by making the subway more accessible to residents not living near subway stations.This would drive up the demand for and the price of apartments distant from vis-a`-vis proximateto the subway, thereby reducing the subway housing price premiums.Our study exploits the staggered entry of dockless bike sharing in 10 major Chinese cities during2016–2017. Combining detailed information on resale apartments, subway networks, and staggeredentry times of bike sharing, we estimate the housing price gradient (i.e., the rate at which theprice of otherwise identical apartments declines in the distance from the subway) within a three-kilometer radius to each subway station and compare the gradients before and after bike sharing’sentry. To identify the causal effect of bike sharing on the price gradients, we adopt an apartment-level difference-in-differences (DID) estimator controlling for detailed apartment characteristicsand location-specific fixed effects; we also directly estimate the price gradients for each city-monthbefore and after the entry using a two-step estimator. Both approaches yield a consistent finding:Without bike sharing, average housing prices fall by 4.2 percent per kilometer away from subwaystations. The entry of bike sharing attenuates the gradient to 3.0 percentage points so that distantapartments become relatively more expensive than proximate ones. The change in relative pricesis economically large, equivalent to an urban resident’s yearly disposable income. Further analysisreveals that both buyers and sellers respond to the entry of bike sharing, respectively, by raisingthe initial listing prices and making more viewings to distant apartments.In addition, we use a back-of-the-envelop analysis to infer the reduction of commuting costsdue to bike sharing from changes in housing price gradients. The underlying assumption is thatthe housing market is competitive and housing prices capitalize any change in living amenities,including the commuting cost to the subway. We estimate that, on average, bike sharing reducesa household’s annual commuting cost (specifically to subway stations) by 1,893–2,127 CNY over30 years of residence. This is substantially larger than the user cost of bike sharing (480 CNY peryear), implying that home sellers and buyers capture a sizeable portion of bike sharing‘s benefits.This chapter contributes to the literature on the sharing economy. To our knowledge, we areamong the first to study the economic impact of dockless bike sharing (other studies include Cao etal. 2021 and Pelechrinis et al. 2017). Studies have found that docked shared bikes reduce congestionand air pollution (Woodcock et al., 2014; Pelechrinis et al., 2016), whereas we emphasize the effectsof reducing commuting costs and improving subway accessibility. A large literature has focusedon ride-hailing or accommodation platforms that seek to disrupt the traditional business (Cramer3and Krueger, 2016; Zervas et al., 2017; Berger et al., 2018; Barron et al., 2018; Chen et al., 2019;Angrist et al., 2021). In contrast, bike sharing serves more as a complement to public transit, andthe complementary effect could be more salient for dockless bikes as they offer greater flexibility inriding routes than docked bikes. Moreover, we contribute to the literature on how transportationcondition impacts housing prices (Bajic, 1983; Baum-Snow and Kahn, 2000; Bowes and Ihlanfeldt,2001; Coulson and Engle, 1987; Dewees, 1976; Fesselmeyer and Liu, 2018; Gibbons and Machin,2005; Yiu and Wong, 2005). Our findings align with existing ones that housing prices are highernear subway stations as residents enjoy more convenient public transit. However, we take a furtherstep to show that bike sharing offers a complementary means of commuting to subways and reducesthe overall commuting cost for subway riders.Having investigated individuals’ mobility across space and firms, Chapter 4 turns to the analysisof economic policies in a frictional labor market. In this chapter, we assess the effects of corporatetax policies on small business workers’ earnings and welfare. We focus on small businesses partlybecause they account for 60 percent of sales and 70 percent of employment in Canada. In 2014, theQuebec province of Canada announced and implemented a major tax cut targeting domestic smallbusinesses in the manufacturing and proceeding (M&P) sector. The reform lowered the income taxrate for targeted firms from 19 percent to 17 percent in 2014, and from 17 percent to 15 percent in2015 and afterward. Using tax record data covering the universe of Canadian firms and workers in2011–2017, we evaluate the causal effect of the reform, calculate the tax incidence and pass-throughbetween firms and workers, and compute the fiscal cost of job creation after the reform.To identify the causal effect, we first compare treated firms in the M&P sector in Quebec versusthose in non-M&P sectors in Quebec. Since sector-specific shocks may confound our results, wemake the same cross-sector comparison in Ontario and British Columbia, two other major provincesof Canada without any tax rate change over the sample period. This gives rise to a triple-differencesdesign which absorbs any sector- or province-specific shocks that may coincide with the reform.Moreover, we use foreign firms that are ineligible for the tax cut regardless of their locations orsectors as a placebo test to strengthen our findings. We estimate that small M&P firms in Quebecincrease employment, average payrolls, and tangible assets by 1.7 percent, 2.3 percent, and 3.2percent, respectively, after receiving the tax cut. They also increase sales, after-tax profits, andproductivity, partly driven by investment in productive capital such as computers. On the workerside, workers at treated firms before the reform enjoy an annual earnings growth of 1.3 percent,especially for those who stay at the same firm after the reform. Workers with ownership of theirfirms bear roughly 40 percent of the tax benefit, while non-owner workers bear about one-third.Taken together, the tax incidence on workers is about three-quarters, larger than estimates fromthe literature (Sua´rez Serrato and Zidar, 2016; Fuest et al., 2018). Accounting for owner-workersis important given our setting, as it is prevalent for small business owners to work at their firms.Next, we exploit rich firm balance sheet data to understand how corporate taxes impact workeroutcomes. We find that firms respond more strongly to the tax cut in high-growth industries, wherethey likely have higher-value projects to invest. In such industries, we observe larger increases in4capital and labor input, profits, productivity, and worker earnings. Following Kline et al. (2019),we estimate that an average firm passes 35 percent of the extra surplus from the tax cut to workers.Finally, we perform a cost-and-benefit analysis and compare the fiscal cost of the tax cut against thenumber of jobs created. Within our sample of analysis, the average cost per job is roughly 14,000CAD, which is lower but comparable with estimates in the U.S. (Garrett et al., 2020). Overall,the tax cut yields economically meaningful benefits on the earnings and welfare of small businessworkers.Chapter 4 contributes to the growing literature on how corporate taxes affect worker earnings.Combining firm- and worker-level data, we not only distinguish the earnings effect on individualworkers from the effect on within-firm worker composition (Arulampalam et al., 2012; Sua´rez Ser-rato and Zidar, 2016), but also pin down the growth mechanisms by which the tax benefits arepassed on to workers (Fuest et al., 2018). Moreover, we use ownership data to distinguish workerswith and without ownership, an important difference in the setting of small businesses. As smallfirms are typically cash-constrained, they may respond differently to tax incentives than large firms(Smart, 2021; Harju et al., 2022). Thus, our findings provide empirical evidence for designing aneffective corporate tax system.5Chapter 2Beyond Lost Earnings: JobDisplacement and the Cost ofCommuting2.1 IntroductionJob displacement has profound consequences on individual workers. Since Jacobson et al. (1993),extensive literature has documented the large and persistent loss in earnings and wages facingdisplaced workers. However, less is known about how job displacement affects non-wage amenitiesof subsequent jobs, and whether changes in job amenities exacerbate or dampen the total cost of jobloss. These questions are particularly important in light of recent studies on non-wage job amenitiesand inequality. By compensating wage differentials (Rosen, 1974a; Roback, 1982a), workers receivelower wages for better amenities so that the wage losses would overstate the welfare cost of jobloss. By contrast, recent studies show that low-paying jobs tend to provide worse amenities, whichrather amplifies the total cost of job loss (Sockin, 2022; Maestas et al., 2023).To fill this gap in the literature, this paper studies the impact of job displacement on animportant job (dis)amenity—workers’ commuting cost between home and work.1 Using Germangeo-referenced employee-employer data in 2000–2017 and a matched event study design, we firstestimate the effect of job displacement on workers’ commuting distances. After being displacedin mass layoffs, workers commute longer distances to subsequent jobs by up to 21 percent; in thenext 10 years, the effect gradually declines as workers switch to jobs closer to their homes. Werationalize the findings using an on-the-job search model with heterogeneous firm productivityand commuting distances. Next, we quantify the monetary cost of the increased commuting tocompare the commuting effect with workers’ wage loss and total cost of job loss all in monetaryterms. Structural estimation of the model implies that workers’ average willingness to pay (WTP)to avoid commuting equals 20 euros per day, and the rising commuting cost after displacement isequivalent to 15–20 percent of the wage losses. Thus, accounting for the commuting effect wouldsignificantly amplify the total cost of job displacement beyond the earnings and wage losses.Our study makes three major contributions. First, we use geo-coordinate level data on workers’1In the 2010s, the average daily commuting time exceeded 40 minutes in most member states of the EuropeanUnion; the United States and the United Kingdom saw even longer daily commuting times of 50–60 minutes (Burdet al., 2021; Gime´nez-Nadal et al., 2022). The monetary-equivalent value of commuting time is estimated to be 0.9to 2.5 times the opportunity cost of foregone wages (Small et al., 2005; Mattia, 2023).6residences and workplaces to measure their door-to-door commuting distances between home andwork. This allows us to distinguish commuting from migration, avoid measurement errors in county-or city-level data, and consistently estimate the effect of job displacement on commuting distances.In particular, we show that the long-run recovery in commuting distances is driven by workersswitching from distant to nearby jobs rather than relocating their homes; besides, using regional-level data causes a significant bias in the estimated causal effects. Second, we establish the jointeffect of job displacement on workers’ wages and commuting distances. In contrast to the theoryof compensating wage differentials, we find displaced workers suffer from both lower wages andlonger commuting, and the observed correlation between wages and commuting distances wouldunderstate the WTP for less commuting. Therefore, our third contribution is to estimate the WTPusing a structural job search model. By incorporating job search friction, endogenous locationchoice, and unobserved non-wage amenities, our model yields a WTP comparable with the recentliterature using survey methods (Le Barbanchon et al., 2021). Although the displacement effect ondistances seems moderate, the associated monetary cost is large and meaningfully contributes tothe total cost of job loss.The first part of our study estimates the job displacement effect on workers’ commuting distancesto subsequent jobs. To identify the causal effect, we exploit workers who involuntarily lose theirjobs in establishment-level mass layoffs, i.e., working full-time on a stable employment contractbefore displacement (Jacobson et al., 1993). These workers are compared with a matched group ofnon-displaced workers with similar pre-layoff characteristics (Krolikowski, 2018; Schmieder et al.,2023). Analogous to the “scarring effect” on wages, we find a large increase in workers’ commutingdistances after displacement. In the first year, workers’ average commuting distance rises by 20.9percent (3.35 kilometers one-way); in the next 10 years, the effect gradually declines as workersswitch to jobs closer to their homes. By contrast, we find no evidence that workers recover fromjob displacement by relocating homes closer to their employers, which conforms to the fact thatinternal migration is uncommon in Germany.2Further analysis reveals that our estimates are robust to including part-time workers, self-selection into layoffs, heterogeneous unemployment duration, spillover effects of large layoff events,dynamic and heterogeneous effects (Borusyak et al., 2024), and alternative measures of commutingtime. The effects also vary by worker demographics (e.g., gender), firm and job characteristics (e.g.,job tenure), and labor market conditions (e.g., market concentration). In addition, we illustrate thevalue of granular commuting data by comparing our estimates with those from county- and city-leveldata.3 We show that measuring commuting at regional levels causes a sizeable upward bias. Thisis because regional-level data assumes zero commuting distance for two-thirds of all workers whocommute within counties and one-third of workers commuting within cities. If anything, measuring2According to the survey reported in Esipova et al. (2013), the share of individuals who moved across cities duringthe last five years exceeds 21 percent in the U.S. but is less than five percent in Germany.3In 2017, Germany is divided into 141 commuting zones (Glitz, 2012), which are further divided into 401 admin-istrative districts (counties) and 11,014 municipalities (cities). The average size of a county is 890 square kilometersand the average size of a city is 32 square kilometers.7commuting at a more granular level would help reduce the bias.In the second step, we develop an on-the-job search model (Burdett and Mortensen, 1998)with heterogeneous firm productivity, non-wage amenities, and commuting distances to rationalizeour empirical findings. The model establishes a preferential order of jobs ranked by their matchsurplus. Higher-surplus jobs enjoy greater productivity, wages, amenities, and short commutingdistances than lower-surplus jobs. On the one hand, on-the-job search allows workers to move fromlow-surplus to high-surplus jobs, which explains the long-term recovery in wages and commutingdistances of displaced workers. On the other hand, workers fall along the job ladder upon jobdisplacement, consistent with the estimated short-run losses in both dimensions.More importantly, we use the model to estimate the monetary cost of commuting and itscontribution to the total cost of job loss. In the presence of job search friction, wage differentialsacross jobs may not fully compensate for differences in commuting costs. A recent study by Lu et al.(2024) shows that exogenous reduction in commuting time increases workers’ utility and bonus pay,suggesting that the observed wage variation could imply a negative commuting cost. To addressthis challenge, our model characterizes workers’ trade-offs between the three job attributes in africtional labor market. In particular, it allows us to isolate from the estimated WTP the effectsof endogenous commuting distances due to workers’ and firms’ spatial sorting and unobservedamenities in the job offer distribution.Using the Simulated Method of Moments, we estimate that each kilometer of commuting isworth 1.36 percent of workers’ average daily wage. Accordingly, an average worker incurs a com-muting cost of 20 euros per day. This exceeds the opportunity cost of commuting time (15 euros)and amounts to one-fifth of the average daily wage of German workers. While the marginal com-muting cost exhibits little contingency on distance or wage, we find that women have a marginalWTP for commuting whereas they commute shorter distances than men; as such, women’s aver-age commuting cost turns out to be smaller. Our estimate is one magnitude larger than what isimplied by compensating differentials assuming a perfectly competitive labor market, and most ofthe discrepancy is explained by job search friction that results in utility dispersion across jobs.Combining the event study estimates with the estimated WTP, we finally evaluate the increasein commuting costs after job displacement. On average, the greater commuting cost of displacedworkers equals 20 percent of their wage losses in the short run and 15 percent in the long run.Instead of compensating for the wage losses, the extra commuting cost significantly adds to thetotal cost of job loss. Counterfactual analysis further reveals that reducing the commuting costleads to a smaller increase in commuting after job displacement but exacerbates the wage losses.This is because such interventions alter workers’ trade off between the two margins. Therefore,policies such as commuting subsidies and remote work could have countervailing effects to mitigatethe total losses of displaced workers.To summarize, our paper makes both empirical and methodological contributions. We documenta substantial increase in commuting distances after job displacement and a long-run recovery due tojob change. Then we develop a structural job search model to estimate workers’ WTP for shorter8commuting, accounting for job search friction, spatial sorting, and unobserved firm amenities.Combining both reduced-form and structural estimates, we find the increased commuting costexacerbates the overall cost of job displacement by 15–20 percent of the wage losses. Besides,we use geo-coordinate data to precisely measure workers’ commuting distances between home andwork. This allows us to distinguish commuting from migration and overcome a sizeable estimationbias in regional-level data.2.1.1 Related LiteratureOur paper contributes to several strands of literature. First of all, a large literature has examinedthe earnings losses due to job displacement (e.g., Jacobson et al., 1993; Davis and vonWachter, 2011;Burdett et al., 2020; Schmieder et al., 2023; Bertheau et al., 2023; Athey et al., 2023). Other studiesalso consider displacement effects on health, crime, job stability, and skill mismatch (Sullivan andVon Wachter, 2009; Britto et al., 2022; Neffke et al., 2022; Jarosch, 2023; Ahammer et al., 2023).Related to our work, Meekes and Hassink (2019, 2022) investigate how job displacement impactscross-regional commuting, while Fackler and Rippe (2017) and Huttunen et al. (2018) study themigration behavior of displaced workers. Our work differs from the above in two important ways.First, we exploit geo-coordinate level data on workers’ residences and workplaces to examine theircommuting behavior both within and across administrative regions and distinguish commutingfrom migration. In particular, we show that focusing on inter-regional commuters leads to biasedestimates of the displacement effect. Second, we estimate not only the increase in commutingdistances but also the monetary cost. Using structural estimation, we find the commuting effectamplifies the total cost of job displacement by 15–20 percent of the wage loss.Relatedly, we contribute to the literature that estimates the cost of commuting.4 Using reduced-form strategies, Mulalic et al. (2014) and Dauth and Haller (2020) find small wage elasticities withrespect to commuting distances ranging from 0.009 to 0.015. By contrast, Le Barbanchon et al.(2021) and Van Ommeren and Fosgerau (2009) exploit structural and survey methods and estimatean elasticity between 0.12 and 0.15. A large literature in transportation economics also finds varyingvalues of commuting time, ranging from one to 2.5 times the wage rate (e.g., Small et al., 2005;Mattia, 2023). We argue that these discrepancies could be driven by three potential biases: utilitydispersion due to job search friction, spatial sorting of firms and workers, and confounding non-wageamenities. While the effect of utility dispersion has been discussed in the literature, our structuralmethod attempts to address all three factors. Using counterfactual analysis, we show that ignoringjob search friction would significantly understate the WTP; in contrast, the unobserved correlationbetween firm productivity, commuting distances, and other job attributes plays a minimal role inour estimates.4Another strand of literature investigates workers’ mobility costs in terms of migration costs, commuting costs,and information friction. In particular, the information friction constrains workers’ application for distant jobsthrough a different channel from the commuting cost (Manning and Petrongolo, 2017; Marinescu and Rathelot, 2018;Monte et al., 2018; Ransom, 2021). Our findings suggest that migration is not the main driver of workers’ long-termcommuting recovery from job displacement.9Third, we contribute to the literature that quantifies non-wage job values. Recent studies usestructural methods to estimate the total value of non-wage job amenities, which are found to amplifyrather than mitigate the wage inequality across jobs (Sorkin, 2018; Taber and Vejlin, 2020; Lagos,2021; Sockin, 2022; Maestas et al., 2023). Others evaluate the value of specific job amenities usingquasi-experimental or survey methods.5 In comparison, we develop a structural model to estimatethe WTP for less commuting. Instead of exploiting exogenous variation in commuting distances,we use the model to disentangle the commuting cost from job search friction and endogenouscommuting distances.Finally, our study belongs to the burgeoning literature applying geo-referenced data in spatialand labor market research. Granular geo-data enables investigation of novel topics such as migrationand commuting (Dauth and Haller, 2020; Jost, 2024), intra-city structure (Heblich et al., 2020), andurban real estate markets (Chu et al., 2021). Combining the geo-referenced data with route planningalgorithms, we measure workers’ commuting distances precisely and avoid a large estimation biasusing aggregated data.The rest of the chapter proceeds as follows. Section 2.2 discusses the data and reduced-formidentification strategies. Section 2.3 reports the estimated effects of job displacement and illustratesthe value of granular commuting data. Sections 2.4–2.5 develop and estimate a job search modelto quantify the monetary cost of commuting. Section 2.6 concludes.2.2 Data and Empirical MethodsOur study exploits two administrative data sets provided by the Institute for Employment Researchin Germany: the Integrated Employment Biographies (IEB) and the Establishment History Panel(BHP). The IEB data covers a representative sample of German workers subject to social secu-rity contributions. It contains each individual’s age, gender, educational attainment, employmenthistory by job spells, the average daily wage and occupation in each job spell, and the receipt of un-employment benefits. We also identify workers’ residences and workplaces by labor market regions(equivalent to U.S. commuting zones, Glitz, 2012), counties, and cities. However, the data excludescivil servants and the self-employed, which constitute up to 15 percent of the German labor force(Goldschmidt and Schmieder, 2017). Meanwhile, the BHP provides information on all establish-ments with at least one registered employee in Germany, including the industry classification andemployment on June 30 each year. Appendix A.1 describes other data used in the analysis.We merge the employee-employer data with the supplement IEB-GEO data (Ostermann et al.,2022) containing the geo-coordinates of each worker’s residence and workplace. The geo-data isconverted from residential addresses for both employed and unemployed workers and registrationaddresses for all establishments. Over 90 percent of German firms have a single establishment(Gumpert et al., 2022) and their locations are unambiguously identified.6 Hereafter, we refer to5For example, see Mas and Pallais (2017) for the valuation of work schedule flexibility, Png and Tan (2021) forhandling cash among supermarket cashiers, and Cole and Taska (2023) for retirement benefits.6Multi-establishment firms must register at least one of their establishments per city and industry. Hence, the10“firms” and “establishments” interchangeably.Combining the geo-coordinate data with route planning algorithms (OpenStreetMap.org, Huberand Rust, 2016; Dauth and Haller, 2020; Jost, 2024), we calculate the door-to-door driving distancesand drive time for all employed workers. We argue that the driving distance is a plausible measureof the commuting distance, as 68 percent of German workers drive to work.7 Driving distances arealso highly correlated with distances via other means of transportation. Moreover, the door-to-door distances outperform traditional measures such as straight-line distances or distances betweenliving and working regions: the former tend to underestimate the actual commuting distance, andthe latter do not capture commuters within regions. In Section 2.3.1, we illustrate that ignoringwithin-regional commuters may substantially bias the estimated effect of job displacement.By contrast, the driving time might underestimate the true commuting time if workers commuteon foot, by bike, or by public transit. Following the transportation literature, we address thisproblem using two alternative measures of commuting time. First, we take the average walking,cycling, and driving time for each trip weighted by the share of commuters using each mode oftransportation. Following Scheiner (2010), we allow the shares to vary with distance to capturethe fact that workers walk or ride more often for shorter trips. In Appendix A.2, Table A.1 liststhe weights of walking, cycling, and driving by distance segments. Second, we predict commutingtime from commuting distances, assuming a constant elasticity of speed with respect to distancesof 0.4 (Van Ommeren and Dargay, 2006), plus five minutes for departing and parking. Then wescale the results to match the average commuting time in Germany of 23.5 minutes one-way.Figure A.1 plots the distributions of driving distances and the three measures of commutingtime. Most workers commute below 40 kilometers or 60 minutes one-way. Comparing panels (a)–(b), the distribution of driving time is slightly more dispersed than driving distances because theformer already accounts for variations in driving speed. However, panels (c)–(d) show greaterdispersion in the alternative measures, further reflecting changes in the mode of transportation.Particularly, short trips are assigned slower speeds and thus take longer times. In subsequentanalysis, we focus on driving distances as the baseline outcomes and show that our estimates arerobust for different measures of commuting time.Our sample spans from 2000 to 2017, during which the geo-coordinate data is available. Weinclude workers of both genders between 20 and 54 years old but exclude those with a maximumcommuting distance above 100 kilometers as they are unlikely to commute every day (Dauth andHaller, 2020). Following Dauth and Eppelsheimer (2020), we transform IEB’s employment spellsinto a worker-year panel. In each year, we observe workers’ total earnings, the number of days infull-time, part-time, and mini jobs8, and the “main” employer on June 30. If a worker has multipleemployers on June 30, we choose the one with the highest daily wage as the main employer. Forthe main employer, we calculate the commuting distance and commuting time. In addition, weregistered address may not be the actual workplace if a firm has several establishments in a city in the same industry(Ostermann et al., 2022). Section 2.3.4 addresses this issue in detail.7See www.destatis.de/DE/Themen/Arbeit/Arbeitsmarkt/Erwerbstaetigkeit/im-Fokus-Pendler.html.8Mini jobs are a form of marginal employment in Germany with monthly income below 450 euros.11impute missing education variables (Fitzenberger et al., 2005) and top-coded wages due to socialsecurity thresholds (Card et al., 2013).2.2.1 Mass Layoffs and Displaced WorkersTo identify the causal effects, we consider mass layoffs as the source of job displacement (Jacobsonet al., 1993; Davis and von Wachter, 2011; Schmieder et al., 2023; Illing et al., 2024). Following theliterature, we define a mass layoff event in calendar year τ if an establishment (i) has at least 50employees in year τ , (ii) reduces the number of employees by at least 30 percent from year τ to yearτ +1, and (iii) the number of employees in year τ is below 130 percent of that in year τ − 1. Usingworker-flow data between establishments, we distinguish mass layoffs from firm reorganizations andoutsourcing (Hethey-Maier and Schmieder, 2013; Goldschmidt and Schmieder, 2017). In Section2.3.4, we alternatively use establishment closure for identification and obtain similar results.Figure 2.1 shows the number and average size of mass layoffs over time and across space. Exceptfor a hike in 2010, mass layoffs are dispersed over time and hardly correlated with business cycles.The average establishment has 153.6 workers before the layoff and 59 percent are laid off. Masslayoffs are not spatially concentrated either. As shown in panels (c)–(d), most counties have onlya few mass layoffs per year. Across all counties, the number of displaced workers is small relativeto the local population. Section 2.3.4 further shows that our estimates are not confounded byunobserved, time-varying labor market conditions or spillover effects of large layoffs.We define a worker as being displaced if her main employer undergoes a mass layoff in year τand she separates from the employer between year τ and τ + 1. We focus on workers who haveworked full-time at the displacing firms for at least three consecutive years before layoffs. This rulesout marginal or low-productivity workers who might self-select into mass layoffs. Additionally, weexclude workers recalled by the displacing firms. In total, we identify 9,949 workers displacedbetween 2002 and 2012. Focusing on layoffs up to 2012 enables us to track each worker for at leastfive years after displacement.2.2.2 Matching Non-Displaced WorkersNext, we construct a control group of workers who are not displaced but have similar characteristicsto the displaced workers. The control group is obtained using coarsened exact matching (CEM,Iacus et al., 2012). For workers displaced in year τ , we first identify potential matches as those notdisplaced in year τ and having full-time jobs at the same firm in the past three years. FollowingKrolikowski (2018), we allow these workers to be displaced in later years. Then we match displacedand non-displaced workers within each year τ by gender, age, education, firm tenure, firm size,industry, and western versus eastern Germany in year τ . We also match by annual earnings in yearτ −1. If a worker experiences multiple mass layoffs, only the first is included in the matching. Thisprocedure yields a matched control group of 384,071 workers.Table 2.1 provides summary statistics of displaced and matched non-displaced workers in theyear before displacement. For displaced workers (column (a)), Almost one-third of the workers are12female, and the average age before displacement is 40.5 years old. Most displaced workers havevocational training (71.5 percent) and live in western Germany (83.2 percent). The average workerhas 14.1 years of total work experience and 7.6 years of experience with the current employer, andshe earns roughly 100 euros per day. Following Abowd et al. (1999, AKM hereafter) and Card etal. (2013), we measure firm- and worker-specific wage premiums using firm fixed effects and workerfixed effects estimated from a two-way fixed effects model of wage formation (see Appendix A.1 fordetails). Consistent with Gime´nez-Nadal et al. (2022), the average worker travels 16 kilometers or23.5 minutes one-way. Moreover, a sizeable share of commutes occurs within administrative regions.Only 37.3 percent of workers commute across counties and 59 percent across cities. As shown incolumn (b), non-displaced workers exhibit similar characteristics to their displaced counterparts inyear τ − 1, except that non-displacing firms pay higher wages on average. Finally, roughly half ofthe workers are from manufacturing, trade, and construction industries.2.2.3 Event StudyWe exploit an event study design (Jacobson et al., 1993) to identify the causal effects of jobdisplacement. Assume the outcome Yit for worker i in year t is given byYit =∑k ̸=−1(αkI{t=τ(i)+k} + βkI{t=τ(i)+k}MLi)+X ′itγ + ϕi + ψt + ϵit. (2.1)In equation (2.1),MLi indicates that worker i is displaced according to the criteria in Section 2.2.1.For displaced workers, we define τ(i) as the year of displacement. For workers in the matched controlgroup, τ(i) is the year of matching. The indicator I{t = τ(i)+k} equals one if the focal year t is thek-th year after displacement. As such, αk captures the outcome of non-displaced workers k yearsafter displacement relative to the year immediately before (τ(i)− 1). For displaced workers, this iscaptured by (αk + βk). Therefore, βk represents the partial effect of job displacement on Yit afterk years. In addition, Xit controls for time-varying worker characteristics, i.e., a cubic polynomialof age. Other time-invariant characteristics, such as gender and education, are absorbed by theworker fixed effect ϕi. Finally, ψt is the calendar-year fixed effect, and ϵit is the error term clusteredby establishments.A potential concern with the above specification is that displaced workers’ commuting outcomesare unobserved until they find a new job (see also Jarosch, 2023; Meekes and Hassink, 2019, 2022;Bertheau et al., 2023). In our treated group, 13.3 percent of worker-year observations are missingdue to unemployment (especially in the first few years after job displacement) and 5.0 percent aremissing due to attrition from IEB’s coverage (e.g., becoming civil servants, self-employed, earlyretired, or going abroad). In the matched control group, the share of missing observations isbelow 3 percent. If displaced workers are endogenously selected for reemployment, the compositionof reemployed workers could change over time and confound the estimated dynamic effects. Forexample, workers who find a new job in the first year after displacement could be more productivethan those who find a new job in later years. Thus, the average productivity of workers would13deteriorate over time and we would understate the short-run wage losses but overstate the long-runeffects. To correct for this bias, we use an alternative specification of equation (2.1) to estimatethe effect of job displacement by years since reemployment:Yit =∑k<−1(αkI{t=τ(i)+k} + βkI{t=τ(i)+k}MLi)+∑k≥0(αkI{t=τ˜(i)+k} + βkI{t=τ˜(i)+k}MLi)+X ′itγ + ϕi + ψt + ϵit.(2.2)In the second line of equation (2.2), τ˜(i) is the year worker i finds her first job after displacement.Conditional on reemployment, the estimates βk will capture the dynamic effects of mass layoffs netof the changing sample composition. In Section 2.3.4, we show that the two specifications yieldsimilar estimates.Additionally, we estimate the average displacement effect across all post-displacement years.The estimates are obtained from a standard difference-in-differences (DID) regression:Yit = αPostit + β (MLi × Postit) +X ′itγ + ϕi + ψt + ϵit, (2.3)where Postit equals one for all t > τ(i). Other terms remain the same as equation (2.1).To identify the causal effects, we assume that mass layoff events are uncorrelated with workers’characteristics (or the characteristics of firms and local labor markets) relevant to their labor marketoutcomes. This assumption is justified as follows. First, mass layoffs occur at the establishmentlevel, causing involuntarily job displacement at the worker level. It is unlikely that workers withstable full-time job tenure could anticipate or select into mass layoffs, especially as they have beenworking in the same firms for over three years. Second, one might be concerned that displacingfirms are, on average, less productive than non-displaced ones. By including worker fixed effects,we can absorb any difference across workers and their displacing firms. We will also show that theoutcomes of displaced and non-displaced workers evolve in parallel trends before mass layoffs.Third, mass layoffs by small-to-medium establishments constitute the majority of our sample,and they are unlikely to generate spillover effects on the entire local labor market. We have alsoshown that mass layoffs are not concentrated in particular years, industries, or geographic regions.Finally, we use CEM to compare displaced and non-displaced workers with similar pre-layoff char-acteristics, and this control group helps us identify dynamic and heterogeneous displacement effects(Borusyak et al., 2024). Section 2.3.4 reports various robustness checks to support our argument.2.3 The Effects of Job DisplacementThis section presents the estimated effects of job displacement. Figure 2.2, panel (a) plots estimatesof equation (2.1) using a balanced worker-year panel and the indicator of full-time employment asthe dependent variable. We find mass layoffs significantly impact workers’ employment trajectories.In the first year after displacement, displaced workers are 67.6 percent less likely to be full-time14employed than non-displaced workers. Nonetheless, the employment gap diminishes over time.Table 2.2, column (a) shows the DID estimates from equation (2.3). Averaged across 10 yearspost-layoff, job displacement reduces workers’ employment probability by 33.9 percentage points.9Next, Figure 2.2, panel (b) illustrates the effect of job displacement on the daily wages ofsubsequent jobs. Conditional on full-time employment, workers’ average daily wage drops by 21percent in the first year after displacement. This large wage loss persists for three years andmodestly recovers in the long run. Table 2.2, column (b) shows that the average daily wage ofdisplaced workers falls by 18.9 percent over the entire post-displacement period. Additionally, wefind that a significant portion of the wage losses is driven by losses in firm-specific wage premiums(Figure A.2 and Table A.2).Figure 2.2, panel (c) reports estimates on commuting distances. Opposite to the employmentand wage effects, workers’ average commuting distance increases by 20.9 percent in the first yearafter displacement and gradually declines in subsequent years. Evaluated at the pre-layoff means,the short-term increase equals 16.02 × 0.209 = 3.35 kilometers one-way. Table 2.2, column (c)shows that the long-run increase in commuting distance is 14.8 percent or 2.37 kilometers one-way.The above results are quantitatively robust if we directly estimate the displacement effects on dailywages and commuting distances in level (Figure A.3 and Table A.3). Besides, panel (d) shows thatworkers’ commuting time increases significantly after job displacement and recovers in the long run.Margins of adjustment. To reduce commuting, workers can either switch to employers closer totheir homes or relocate their homes closer to employers. Contrary to the U.S. where internal migra-tion is prevalent, home relocation is much less common in Germany (Esipova et al., 2013). Meekesand Hassink (2019) shows that job displacement due to firm bankruptcy reduces the likelihoodof relocation, and Huttunen et al. (2018) argue that non-economic factors drive home relocationby displaced workers. Consistent with their findings, we provide three pieces of evidence that thecommuting dynamics are primarily driven by job change rather than home relocation and thatcommuting is a more effective response to job displacement.First, we estimate (2.1) using indicators of job change and relocation as dependent variables. Asshown in Figure 2.3, panels (a)–(b), job change and relocation both increase in the first few yearsafter displacement, but the increase in relocation is smaller in magnitude and does not persist insubsequent years. Second, Figure 2.3, panel (c) reports estimates on commuting distance only forworkers who do not relocate after displacement. For these workers, we observe a long-term declinein commuting distances similar to the baseline estimates (Table 2.2, column (c)). Third, we showthat workers do not relocate systematically towards where they work. For each displaced workerwho relocates but does not change jobs between years t and t+ 1 after displacement, we computethe distance from her workplace to her residence in both years. As shown in Figure 2.3, panel (d),9Figure A.2 and Table A.2 show a similar decline in employment across all job types. However. the loss in full-time employment is partially offset by increased days working in part-time and mini jobs. In the long run, part-timeand mini-job employment declines as workers return to full-time employment. The results suggest that displacedworkers take part-time and mini jobs as stepping stones back to full-time employment.15the distribution of distances remains unchanged before and after relocation.102.3.1 The Value of GranularityAs mentioned above, a major advantage of our study is the geo-coordinate level commuting data:for each worker, we can calculate the door-to-door commuting distance between her residence andworkplace along actual routes. Compared with distances measured at the county or city level, ourdata overcomes two types of errors. First, regional-level data omits commuters within the sameregion, leading to a censoring problem. Second, an individual’s commuting distance rarely coincideswith the distance between two regional centers. If workers living at regional borders are more likelyto commute across regions, the distance between two regional centers will overstate the averagecommuting distance. In what follows, we quantify the magnitudes of both errors.In Figure 2.4, panel (a), we compare estimates of equation (2.1) using our baseline measure ofcommuting distances versus alternative measures at the county level. In the first step, we “omit”within-county commuters by forcing their distances to zero. This leads to an overestimation of thejob displacement effect by 8.1 log points in the first year after displacement, and the magnitude ofthe bias is almost 40 percent of the baseline effect. As shown in Table 2.4, panel A, the long-runeffect of job displacement is also overestimated by 12.8 percent. Then in the second step, we furtherassume that commuters from one county to another all take the same route, the distance of whichis calculated using OpenStreetMaps between county centers. We find this assumption has a smallerimpact on the causal estimates. Accounting for both errors, the effects of job displacement areoverestimated by 41.9 percent in the short run and by 13.5 percent in the long run.Figure 2.4, panel (b) and Table 2.4, panel B repeat the comparison at the city level, respectively.Since a German city is smaller than a county, both biases become smaller in magnitude. In total, theshort-run effects are biased upwards by 19.4 percent and the long-run effects by 6.1 percent. Hence,we conclude that using regional-level commuting data overestimates the effect of job displacement,primarily due to omitting commutes within regions. Nevertheless, measuring commuting at a finerlevel will mitigate the bias.2.3.2 Effect HeterogeneityThe effect of job displacement could vary across workers, firms, and labor markets in severalways. First, they could differ across workers with different preferences or demographics. FigureA.4, panels (a)–(d) present separate estimates of equation (2.1) by gender and age, respectively.We find that female and older workers suffer from greater wage losses, while their commutingdistances increase less than male and younger workers. This is consistent with Illing et al. (2024)and Meekes and Hassink (2022) who argue that women face higher commuting costs than men.Also, the displacement effects may vary with the difficulty of relocation. For example, homeowners10In Figure A.3 and Table A.3, we further show that workers are more likely to commute across counties and citiesafter displacement. They also work more often in different occupations and industries from their pre-displacementjobs (Neffke et al., 2022).16and married workers are expected to be less flexible than tenants and singles in terms of homelocation. While data on home ownership is not available, Figure A.4, panels (e)–(f) compare theeffects between married versus single workers (see Appendix A.1), showing that the increase incommuting distance is smaller and recovers faster for married workers. However, Table A.4 reportsthat the long-run effects on commuting distances exhibit no statistical difference across subsamples.Second, the effects could differ across displacing firms. According to a job ladder model, jobdisplacement from productive firms is more costly as workers lose more firm-specific wage premiums(Fackler and Rippe, 2017). Figure A.5 and Table A.5 show that workers displaced from high-wagefirms suffer from greater wage losses and larger increases in commuting distances, and the long-termdifferences are large and statistically significant. Similarly, displacement from longer-tenure jobs ismore costly as workers accumulate more job-specific wage premiums on such jobs. However, high-and low-wage workers experience similar effects on both outcomes after job displacement.Third, the displacement effects may depend on job accessibility in the local labor market. Asshown in Figure A.6, panels (a)–(b), urban workers experience a smaller increase in commutingdistances but larger wage losses after displacement. We argue that thicker labor markets in urbanareas explain the smaller commuting effect, while the extra wage penalty is due to higher firmproductivity or better match quality in pre-displacement jobs (Fackler and Rippe, 2017). Alter-natively, less concentrated labor markets offer more outside options so that displaced workers aremore likely to find a job with relatively higher wages and shorter commuting distances. This isconfirmed in Figure A.6, panels (c)–(d), where we use the Herfindahl–Hirschman index to measurelabor market concentration by commuting zones and industrial sectors.Finally, workers may recover faster from job loss if their industry-specific skills better matchthe local labor demand, e.g., they are displaced from industries that make up a higher employmentshare in the local labor market (Macaluso, 2023). Hence, Figure A.6, panels (e)–(f) compare thedisplacement effects by the employment share of the displacing industry in the commuting zone.Within each industry, we compare commuting zones below and above the median employmentshare. As expected, workers with better skill matches see smaller wage losses and lesser commutingincreases, whereas the long-term differences are small and statistically insignificant (Table A.6).2.3.3 Trade off Wage Losses and Longer CommutingIn Appendix A.3, we further estimate the correlation between the wage losses and the commutingeffects at the worker level. The estimated Pearson correlation coefficient is approximately 0.060,suggesting that greater wage losses are associated with less increase in commuting. Assumingcompensating wage differentials, i.e., variations in wage losses fully capture different commutingdistances, the estimates imply a wage elasticity with respect to commuting distances of 0.018. Thisis close to Mulalic et al. (2014) who estimate an elasticity of 0.014–0.017 using firm relocation asexogenous shocks to workers’ commuting distances.In contrast, our estimate is one magnitude smaller than Le Barbanchon et al. (2021) whoexplicitly account for utility dispersion among realized job matches and obtain an elasticity of170.121–0.148. If workers value commuting by the opportunity cost of commuting time (15 eurosper day), the equivalent wage elasticity would be 0.150, which also exceeds our implied estimate.This is inconsistent with Small et al.’s (2005) review that workers’ valuation for commuting timeis 0.9–2.5 times the opportunity cost. Therefore, it is unlikely that wage differentials across jobsfully compensate for variations in commuting costs.2.3.4 RobustnessIn what follows, we perform various robustness checks for the displacement effects on daily wagesand commuting distances. Figure A.7 shows that including part-time jobs slightly exacerbates thewage losses but has minimal impact on the commuting estimates. Second, we use establishment clo-sure as an alternative treatment to address workers’ self selection into displacement. We impose thesame age, maximum distance, and tenure restrictions as before, identify workers displaced duringestablishment closure, match them with non-displaced workers by CEM, and re-estimate equation(2.1). In Figure A.8, we find that the results are similar to those of mass layoffs. Third, we estimatethe alternative specification in equation (2.2) to address workers’ selection into reemployment andthe changing composition of reemployed workers. Conditional on reemployment, workers’ dailywages grow more steadily in post-displacement years. Thus, the previously estimated slow recoverycould partly result from less productive workers’ taking longer time to find new jobs. At the sametime, their commuting distances follow similar dynamics as before (see Figure A.9).Fourth, we rule out spillover effects of large layoffs that negatively impact both displaced andnon-displaced workers in the local labor market (Gathmann et al., 2020). To do so, we run separateanalyses (i) excluding mass layoffs of more than 500 workers, and (ii) adding fixed effects bycommuting zones and years. Fifth, recall that our data does not differentiate multiple workplacesof the same establishment in the same city and industry. To rule out possible measurement errorsin the workplace addresses, we exclude workers in finance, trade, and transportation industries(Ostermann et al., 2022), where firms are more likely to operate at multiple locations within a city.As shown in Figures A.10–A.12, our results are robust to such concerns.Finally, we estimate the effects on other measures of commuting time. We also use the imputa-tion method of Borusyak et al. (2024) to account for dynamic and heterogeneous treatment effects.As shown in Figures A.13–A.14, the results are similar to the baseline estimates. For all robustnesschecks above, the corresponding DID estimates are reported in Tables A.7–A.8.2.4 A Job Search ModelIn the following sections, we develop and estimate a partial-equilibrium, random job search model torationalize our causal estimates and quantify the monetary commuting cost. The model, in the spiritof Burdett and Mortensen (1998), features on-the-job search and three dimensions of heterogeneity:firm productivity, firm’s provision of non-wage job amenities, and commuting distances. Readersare referred to Appendix A.4 for proofs.18Environment. Consider an infinite-horizon, discrete-time setting with a continuum of firms andworkers. Firms are ex-ante heterogeneous in their productivity y and non-wage amenity a. Theidiosyncratic locations of firms and workers give rise to heterogeneous commuting distances r. Ajob match is characterized by a triple θ = (y, a, r). Within the model, we take firms’ and workers’locations as given; alternatively, the locations could be determined by a spatial equilibrium whereagents have no incentive to move.In each period, an unemployed worker receives unemployment benefits z and draws a job offerwith probability λ0. If employed in a job match θ, the worker consumes a flow wage w(θ, θˆ) andamenity a, incurs commuting cost cr, and receives a job offer with probability λ1. The flow wagedepends on both the current job match θ and the worker’s best outside option θˆ. The commutingcost is linear in the distance r with c > 0 being the marginal commuting cost. For a representativeworker, the distribution of potential job matches (job offers) is given by Fθ and the same forunemployed and employed workers. While Fθ is exogenous, we allow for correlation between firmattributes and commuting distances to capture possible spatial sorting by firms and workers.Given the worker’s outside option θˆ, the value of a job match θ is equal toW (θ, θˆ) for the workerand J(θ, θˆ) for the firm. The values for an unemployed worker and an unmatched firm are U andzero, respectively. For unemployed workers, an offer turns into a job match if the joint surplusS(θ) ≡W (θ, θˆ)− U + J(θ, θˆ), (2.4)is positive. Note that S is the net value of employment for both firms and workers and does notdepend on θˆ, which only affects how the surplus is split. With slight abuse of notation, we use u todenote job offers that do not lead to a match, so that S(u) ≤ 0. Finally, all job matches dissolveexogenously with probability δ.Wage bargaining. With on-the-job search, bargaining takes place as sequential auctions (Postel-Vinay and Robin, 2002a,b). If an unemployed worker receives a job offer θ, she will bargain for anexogenous share α ∈ [0, 1] of the joint surplus:W (θ, u)− U = αS(θ). (2.5)If the worker with outside option θˆ is currently in a job match θ1 and receives an offer θ2, oneof the following will happen. If S(θ2) > S(θ1), the worker will move to the new firm and the newwage is determined byW (θ2, θ1)− U = S(θ1) + α(S(θ2)− S(θ1)), (2.6)so that the worker gains α share of the incremental surplus. If S(θˆ) < S(θ2) < S(θ1), firm θ1 retainsthe worker at a higher wage by matching the outside option θ2. The renegotiated wage satisfiesW (θ1, θ2)− U = S(θ2) + α(S(θ1)− S(θ2)). (2.7)19Finally, if S(θ2) ≤ S(θˆ), the worker remains at the current firm at the current wage.For the sake of convenience, we define M1(θ1) = {θ : S(θ) > S(θ1)} as the set of firms thatsuccessfully poach the worker from θ1, and M2(θ1, θ2) = {θ : S(θ2) < S(θ) ≤ S(θ1)} as thosetriggering wage renegotiation at firm θ1 when the worker’s original outside option is θ2. Thecorresponding probability measures are p1(θ1) and p2(θ1, θ2), respectively. In later analysis, we alsodenote p3(θ2) = p1(θ1) + p2(θ1, θ2).Value functions. For unemployed workers, the value function U is given byU = z + β{λ0∫M1(u)W (x, u)dFθ(x) + (1− λ0p1(u))U}. (2.8)Within the braces, the first term is the expected continuation value of being employed at somefirm x. The second term means that the worker receives no job offer or the job offer creates zerosurplus.Similarly, the value function of an employed worker at firm θ with outside option θˆ isW (θ, θˆ) = w(θ, θˆ) + a− cr + β{δU + (1− δ)[λ1∫M1(θ)W (x, θ)dFθ(x)+ λ1∫M2(θ,θˆ)W (θ, x)dFθ(x) + (1− λ1p3(θˆ))W (θ, θˆ)]}.(2.9)The four terms in the braces represent the continuation value of separation into unemployment,moving to a higher-surplus job, renegotiating wages with the incumbent firm, and staying with theincumbent firm at the current wage, respectively.Lastly, the value function of the firm is given byJ(θ, θˆ) = y − w(θ, θˆ) + β(1− δ){λ1∫M2(θ,θˆ)J(θ, x)dFθ(x) + (1− λ1p3(θˆ))J(θ, θˆ)}. (2.10)2.4.1 Job Match Surplus and the WTP for CommutingTo investigate the relationship between firm-specific values (productivity and non-wage amenities)and commuting costs, we associate both outcomes with the match surplus. Plugging the wagebargaining rules (2.5)-(2.7) and value functions (2.8)-(2.10) into (2.4), we obtain an expression ofthe surplus function:S(θ)1− β(1− δ) = y + a− cr − z − αβλ0∫M1(u)S(x)dFθ(x)+ αβ(1− δ)λ1∫M1(θ)(S(x)− S(θ)) dFθ(x).(2.11)Proposition 1. S strictly increases in y and a and strictly decreases in r.20By Proposition 1, workers prefer jobs with higher productivity, better amenities, and lowerdistances. From the view of revealed preference, S serves as a “utility function” that rationalizesworkers’ mobility patterns: workers voluntarily move from unemployment to positive-surplus jobsand from low-surplus to high-surplus jobs. Accordingly, Figure 2.5, panel (a) plots the daily wagesand commuting distances among the first jobs accepted by displaced workers. Our model predictsthat these jobs all have a positive surplus. Indeed, the minimum wage of accepted jobs increasesas commuting distances become longer because otherwise, these jobs will likely have a negativesurplus.Focusing on workers’ valuation for commuting distances relative to other job attributes, wedefine v = y + a as the “total value” of jobs (Sorkin, 2018; Sockin, 2022). All jobs (v, r) satisfyingS(v, r) = 0 define a “reservation value curve” with a slope of c in the v-r space (see Figure 2.5,panel (b)). Holding the surplus constant, the parameter c governs workers’ trade-off between v andcommuting distance r. If v is measured in pecuniary terms and r is measured in kilometers, then crepresents workers’ WTP for one kilometer less of commuting. Note that S depends on commutingdistances r which vary across workers within the same firm. In comparison, v does not vary withinfirms and represents workers’ common or systematic preferences over firms.2.4.2 Recovery from Job DisplacementGiven Proposition 1 and the upward-sloping reservation value curve, we argue that workers areexpected to match with higher-value and more proximate firms over time.Proposition 2. Let E[v|s] and E[r|s] be the expectation of total job value and commuting distancesconditional on surplus level s, respectively. E[v|s] increases in s and E[r|s] decreases in s if (i)Fv and Fr are twice differentiable; (ii) the density functions fv and fr are log-concave; and (iii)Fθ = FvFr.We also discuss cases where v and r are not independent. If v and r are negatively correlated,i.e., more productive firms locate closer to workers, then the results of Proposition 2 still hold,because recovery along the job value dimension directly reduces the expected commuting distancesand vice versa. However, if v and r are positively correlated, higher-surplus jobs may have highervalue but are further away. As opposed to our empirical results, either E[v|s] may decrease orE[r|s] may increase in s.Proposition 2 explains the short-run effects of job displacement. After workers lose their jobs,they are willing to accept any new job with a positive surplus, so that the expected surplus of thenew jobs would weakly decline relative to their previous jobs. This implies a wage loss and anincrease in commuting distance. Moreover, our model rationalizes the larger effect of displacementfrom high-paying firms and longer-tenure jobs. In such cases, workers have accumulated greater jobmatch surplus by standing higher on the job ladder or staying employed for a longer time. Afterlosing their jobs, they experience a greater decline in the surplus, which results in greater losses inboth dimensions.21In what follows, we further illustrate how workers recover from job displacement.Corollary 3. For a worker employed in periods t = 1, 2, · · · , let (vt, rt) denote the matched firmtype in period t. Under the assumptions of Proposition 2, the expectation of vt increases in t andthe expectation of rt decreases in t.With on-the-job search, employed workers either stay at their current jobs or move to higher-surplus jobs. Proposition 2 implies that whenever they move, the new job is expected to delivera higher surplus, thereby having a higher total value and being more proximate. When workers’bargaining power α is large, wages will increase in v so that the expected wage also increases in s(Jarosch, 2023). Taken together, the model characterizes how workers recover from job displace-ment, consistent with our empirical findings.To conclude this section, we discuss two extensions to our model. In Appendix A.4.3, weintroduce endogenous search efforts and directed search, assuming that it is more costly for workersto search in a larger geographical area. As workers accumulate job match surplus, the probabilityof finding an even better job declines, and the marginal payoff from searching decreases. Therefore,workers optimally reduce the search radius during on-the-job search. Although we do not observeworkers’ search efforts, this offers a complementary explanation for the recovery of commutingdistances after displacement.Then in Appendix A.4.4, we introduce productivity-enhancing humancapital h. Workers accumulate human capital while on the job but lose it while unemployed. Thus,we extend W , U , J , and S to be functions of h. Incorporating human capital dynamics helps usbetter capture workers’ wage dynamics and improve model fitting with the data.2.5 The Monetary Cost of CommutingIn this section, we estimate the monetary cost of commuting (workers’ WTP) and quantify theincrease in commuting cost after job loss.Identifying workers’ WTP for a specific job attribute can be challenging for three reasons. First,utility dispersion leads to an omitted variable bias. The wage differentials between two jobs mayreflect not only different commuting costs but also different levels of utility (Le Barbanchon etal., 2021; Lu et al., 2024). Second, wages and commuting distances could be jointly determinedby unobserved economic factors such as spatial sorting or agglomeration. If productive firms sortinto downtown to stay close to workers, then firm wages would be negatively correlated withcommuting distances, and the observed correlation would underestimate workers’ WTP for lesscommuting. Third, workers trade off commuting distances with both wages and non-wage amenities.A burgeoning literature has documented that high-wage firms may also offer better non-wageamenities (Lagos, 2021; Sockin, 2022; Maestas et al., 2023). As such, the wage compensationfor longer commuting distances may represent only part of the WTP.To address these challenges, we structurally estimate the job search model in Section 2.4 usingthe Simulated Method of Moments (SMM). The estimation is implemented as follows. For a given22vector of parameters, we first solve the model and simulate workers’ employment trajectories fromthe model. Next, we calculate a set of moments from the simulated and actual data. The trueparameters are estimated by jointly matching the moments. To obtain the data moments, weconvert the IEB data in Section 2.2 into a monthly panel. Workers’ main employers are definedon the 15th of each month. Notably, the estimation does not rely on job displacement or masslayoffs, so the identified WTP applies to the entire labor force rather than displaced workers. Moreestimation details are given in Appendix A.5.1.2.5.1 IdentificationTo begin with, we set the monthly discount factor β = 0.996 corresponding to an annual factor of0.95. Other model parameters are identified as follows.Job search and separation. First of all, we choose offer arrival rates for the unemployed andemployed (λ0 and λ1) to match the empirical job finding (U-E) rate of the unemployed and theemployer-to-employer transition (E-E) rate of the employed, respectively. Since not all job offersare accepted, the arrival rates could be larger than the empirical transition rates. The separation(E-U) rate δ directly matches its empirical counterpart.Job offer distributions. We parameterize the joint distribution Fθ in several aspects. Assumey = y¯Y where Y follows a univariate beta distribution Beta(ηy1, ηy2) with a support on the unitinterval. Analogously, let r = 100R where R ∼ Beta(ηr1, ηr2). Then we model the dependencebetween y and r by assuming that (Y,R) follow a Gaussian copula with parameter ρcyr. Sincenon-wage amenities are unobservable, we take a parsimonious approach by writing a = κ1y + κ2Awhere A is uniformly distributed in the unit interval. Thus, κ1 governs the correlation between yand a and κ2 determines the dispersion of a. Then we find v = y + a.The distributional parameters are identified as follows. For the marginal distributions of y andr, we identify (ηy1, ηy2, ηr1, ηr2) by matching the actual and simulated 75th-50th and 50th-25thpercentile gaps of AKM firm effects and commuting distances, respectively. In particular, we usethe parameters to simulate the distribution of firm types and the wage bargaining rules to simulatethe distribution of wages. Then, we compute firm-specific wage premiums and compare them withactual AKM firm effects.11 The scale parameter y¯ is identified by the 99th-1st percentile gap ofAKM firm effects.To identify ρcyr, one needs information about the correlation between y and r among potentialjob offers. Since we only observe realized job matches, we exploit the richer information of firms’and workers’ geo-coordinates to recover the job offer distribution. Specifically, we compute the11In general, the AKM firm effects are different from firm productivity y, but the two quantities coincide at α = 1.As workers have full bargaining power, they capture the entire job match surplus and firms’ value equals their outsideoption J ≡ 0. In this case, the flow wage w equals the flow output y and the job search model degenerates into awage-posting model where firms are heterogeneous in posted wages w = y. In the presence of additive human capital(Appendix A.4.4), the AKM firm effects estimated from flow wages also coincide with y. As discussed later, ourcalibrated α is indeed close to one.23pair-wise commuting distance between each worker and firm in the same commuting zone anduse the resulting distribution (together with the distribution of AKM firm effects of all firms) toproximate the job offer distribution. Then, we use the Pearson correlation coefficient ρyr, averagedacross all commuting zones, as the moment to identify ρcyr. This requires additional assumptionsthat workers and firms in a commuting zone constitute a labor market. In Appendix A.5.2, wedemonstrate that the correlation between AKM firm effects and pair-wise commuting distances isinsensitive to different definitions of labor markets.Finally, we calibrate (κ1, κ2) using estimates from Taber and Vejlin (2020). They use Danishdata to estimate a job search model similar to ours—where jobs differ in firm-specific productivityand non-wage utility and a firm-worker-specific match component. While Taber and Vejlin (2020)do not observe the match component, they use worker flow across firms to back out the first twoattributes at the firm level. Two of their findings are relevant to our exercise: that firm productivityis only weakly correlated with the provision of non-wage amenities and that the variance of non-wage amenities is as large as the variance of wages.Commuting cost. Given the job offer distribution Fθ, we identify the WTP for less commutingc by comparing Fθ with the observed distribution of realized job matches. With slight abuse ofnotation, let w¯(r) denote the expected wage w conditional on distance rw = w¯(r) + ϵ, E[ϵ|r] = 0. (2.12)By Proposition 1, a potential job match is realized if it lies above the worker’s reservation wagecurve. i.e., w > cr + ϑ0 for some cutoff value ϑ0. Among realized job matches, let w˜(r) be thetruncated expectation of w conditional on rw˜(r) = w¯(r) +E[ϵ|r, ϵ > −w¯(r) + cr + ϑ0]︸ ︷︷ ︸ξ(r). (2.13)Since we observe realized job matches, w˜(r) can be computed from the data. As shown above,w¯(r) can also be identified from Fθ. This allows us to find the truncated residuals ξ(r). Equivalently,knowing the derivatives w¯′(r) and w˜′(r) allows us to identify ξ′(r). An important observation isthat for r > 0,∂ξ′∂c> 0. (2.14)Hence, there exists a unique c that is consistent with the identified ξ′.Figure A.15 illustrates the intuition behind (2.14). The shaded area indicates the support ofrealized job matches, which yield a positive surplus, in the w-r space. These job matches aretruncated by the reservation wage curves (in dark blue). In panel (a), the commuting cost is highand the realized matches are heavily truncated. Hence, the truncated expectation of wages (in red)increases fast in distances. In panel (b), the commuting cost is low, so the truncated expectationof wages increases slowly.24In practice, we estimate c by indirect inference. Using all first jobs of displaced workers, we runan OLS regression of log daily wages against commuting distancesw = γ0 + γ1r + ϵ. (2.15)Then we re-estimate equation (2.15) using the simulated data, focusing on the first jobs after eachunemployment spell. We choose c to match the empirical and simulated slope coefficients γ1. Noticethat the indirect inference leverages linear approximation, and does not require w¯(r) to be trulylinear in r. In what follows, we also provide an alternative identification strategy for c that exploitsthe event study estimates in Section 2.3.Other parameters. As discussed in Appendix A.4.4, we introduce human capital dynamics to fitour model better to the data. Assume that workers possess productivity-enhancing human capitalh, which lies in the unit interval and takes 20 discrete values h1 < · · · < h20. In each period,hk decreases to min{hk−1, h1} with probability π0 if the worker is unemployed, and increases tomax{hk+1, h20} with probability π1 if employed. Then we generalize the wage bargaining rules asequations (A.19)–(A.21), the value functions as equations (A.22)–(A.24), and the surplus functionas equation (A.25). Following Jarosch (2023), we calibrate π0 = 0.260, π1 = 0.133, and workers’bargaining power α = 0.928. Finally, Appendix A.5.3 describes how we identify the unemploymentbenefits z = −0.017 using the support of first jobs accepted by displaced workers.2.5.2 Structural EstimatesTable 2.5 reports SMM estimates of the model parameters. We find the job arrival rates forthe unemployed and employed are λ0 = 0.057 and λ1 = 0.041, respectively. The observed U-Etransition rate is 89.5 percent of the offer arrival rate λ0. In other words, when an unemployedworker meets a firm, the probability that the firm lies above the worker’s reservation value curveis 0.895. Similarly, when an employed worker meets a new firm, the firm’s probability of deliveringa greater surplus and inducing an E-E transition is 0.012/0.041 = 0.293.Regarding Fθ, Figure 2.6, panels (a)–(c) plot the marginal distributions of firm productivity y,total values v, and commuting distances r, respectively. The first two distributions are bell-shaped,whereas the last is right-skewed. As such, workers draw fewer job offers from distant firms regardlessof their willingness to commute, which captures the notion of spatial friction (Schmutz and Sidibe´,2019). Table 2.5 shows that the copula parameter ρyr = −0.020 is negative but close to zero.As explained in Appendix A.5.2, the weak correlation seems inconsistent with spatial sorting oragglomeration forces that productive firms, on average, locate closer to workers. However, it couldbe explained by dispersed productive and residential amenities. In fact, our results are consistentwith Schoefer and Ziv (2022) who also find weak spatial sorting by firm productivity in Germany.Table 2.6, column (a) also reports the estimated WTP. For one kilometer’s increased commutingdistance, workers require 1.365 percent higher daily wages to compensate for the utility losses. For a25sample-average worker who earns 100.4 euros per day and commutes 14.39 kilometers one-way, theestimate implies a wage elasticity with respect to commuting distances of 14.39× 1.365% = 0.196.This is comparable to but larger than Van Ommeren and Fosgerau (2009) whose estimates are basedon a structural model, and Le Barbanchon et al. (2021) who exploit a similar identification strategythat compares jobs on and above the reservation wage curves. It is also one magnitude larger thanwhat is implied by our reduced-form estimates (see Section 2.3.3) where the match surplus isassumed equal across all jobs. In Appendix A.5.4, we further show that surplus dispersion explainsmost of the discrepancy between our structural and reduced-form estimates.Validation Our structural estimates are validated in several ways. First, one might be concernedthat the WTP is identified from functional-form restrictions, without exogenous variation in theactual commuting distances. Therefore, we exploit an alternative identification strategy where cis identified by matching the event study estimate of the job displacement effects. Specifically,we match changes in log commuting distances and AKM firm effects from the last year beforedisplacement to the first year of the new jobs.12 As shown in Table 2.6, column (b), this alternativestrategy yields a very similar estimate cˆ = 1.398. Second, our structural estimates are able tomatch the dynamic effects of job displacement on both wage and commuting distances. In Figure2.7, we plot event study estimates from equation (2.1) using simulated data from the model andthey are quantitatively similar to the actual estimates.Third, our identification of ρyr relies on additional assumptions regarding the scope of labormarkets and job search, and the identification of ρya relies on the external validity of prior studies.Appendix A.5.4 validates that our estimated commuting cost c is insensitive to measurement errorsin ρyr or ρya. For a plausible range of (ρyr, ρya), the estimated c varies within a narrow interval[1.309, 1.460]. Under the generic assumption that firm productivity is negatively correlated withdistances and positively correlated with amenities, the estimate at (ρyr, ρya) = (0, 0) yields a lowerbound of the marginal WTP cˆ = 1.309, which is close to our baseline results and existing estimates.Finally, while we assume a constant, additive marginal WTP, we could probe non-linear com-muting costs by assuming a polynomial reservation wage curve and matching higher-order coeffi-cients inw = γ0 + γ1r + γ2r2 + ϵ. (2.16)It turns out the estimated γˆ2 = −0.0038 has a negligible magnitude—below four percent of thelinear coefficient γ1 = 0.096. That means by increasing the commuting distance from zero to100 kilometers, the percentage change in the marginal commuting cost is less than eight percent.One might expect that the marginal cost of commuting increases in distance or that the marginalcost diminishes as people switch to faster modes of transportation for longer trips. While eithereffect could take place, our finding of the constant marginal cost may result from the increasingand diminishing marginal costs offsetting each other. Moreover, Section 2.3.2 has shown that the12The data moment is the estimated βˆ1 in equation (2.2). The two event study moments also allow us to identifyz without information on the support of first jobs of displaced workers (Appendix A.5.3).26displacement effects are similar between high-wage and low-wage workers so the marginal WTP isunlikely to be contingent on wages.2.5.3 Welfare ImplicationsPut into context, our structural estimates imply a large monetary cost of commuting. As shownin Table 2.6, for an average worker, the WTP for commuting is 100.4 × 1.365% = 1.37 euros perkilometer and 1.37 × 14.39 = 19.72 euros per day. In comparison, the average commuting time ofa German worker is 0.75 hours per day and the average hourly wage is 20 euros (Gime´nez-Nadalet al., 2022). Thus, the opportunity cost of commuting time is 15 euros per day or three-quartersof the WTP. This gap is in line with existing studies (e.g., Small et al., 2005; Van Ommeren andFosgerau, 2009) and reflects additional disutility of commuting, such as the cost of the vehicle, fuel,or tickets, and the subjective distaste for long commutes.Using the structural estimates, we further compare the increase in commuting costs with thewage losses of displaced workers. Recall that job displacement increases workers’ average commutingdistances by 20.9 percent in the first year after displacement. For an average worker, this equals14.39× 20.9% = 3.01 additional kilometers or 3.01× 1.37 = 4.12 euros per day. In comparison, thecontemporaneous loss in daily wages is 100.4 × 21% = 20.08 euros. Taken together, the increasedcommuting cost is equivalent to 20.5 percent of the wage loss in the short run, and 15.4 percent inthe long run.13 Therefore, the increasing commuting cost significantly adds to the total cost of jobdisplacement, rather than compensating for the wage losses.14Gender gap in the cost of commuting. Additionally, we estimate the structural model sep-arately by gender, targeting gender-specific moments. Table 2.6, columns (c)–(d) report the esti-mated c for men and women, respectively. The elasticity estimates are larger for women than formen, suggesting that women exhibit greater marginal WTP for shorter commuting (Le Barbanchonet al., 2021). However, since an average woman in our sample earns a lower wage and commutes ashorter distance than an average man, the out-of-pocket commuting cost exhibits a reverse gendergap. On average, the commuting cost per day is 21.54 euros for men and 18.19 euros for women.1513Using estimates in Table 2.2, we calculate the long-run wage losses as 100.4× 18.9% = 18.98 euros and long-runincrease in commuting distances as 14.39× 14.8% = 2.13 kilometers, which translates to 2.13× 1.37 = 2.92 euros.14The above comparison focuses on employed workers. Displaced workers who have yet to find a job will sufferfrom earnings losses due to reduced labor supply but save the commuting cost. Using the change in employmentrates after mass layoffs, we can compute the total change in commuting distance accounting for both unemployed andreemployed workers. It turns out that the cost savings from unemployment outweigh the increased cost of reemployedcommuters. In the short run (first year after displacement), the net change in commuting distance is −8.62 kilometersper day. The corresponding monetary cost amounts to 2952.7 euros per year (assuming 250 working days), whichoffsets 15 percent of the contemporaneous earnings losses. In the long run, the net change in commuting distance is−3.47 kilometers per day, and the cost saved offsets 9.9 percent of the long-term earnings losses.15For the urban-rural gap, we find an average urban resident faces more productive and proximate job opportuni-ties, but she does not value commuting more than an average rural worker. As such, the heterogeneous displacementeffects mainly arise from different job offer distributions rather than different WTP.27Implications for remote work. Finally, we address a policy-relevant question: Can policymak-ers mitigate the cost of job loss by encouraging commuting? Exploiting the opening of new subwaystations, Lu et al. (2024) show that reduced commuting time improves workers’ satisfaction andproductivity. Franklin (2018) finds that unemployed youth in Ethiopia benefit from transportationsubsidies by increasing search intensity and landing a job more quickly; however, receiving trans-portation subsidies does not increase the wages of the new jobs. To reconcile this discrepancy, weargue that a lower commuting cost has countervailing effects on displaced workers. On the onehand, it flattens the reservation value curve, encourages workers to accept distant job offers, andshortens their unemployment duration. It also raises wages in the long run as workers accumulatejob tenure. On the other hand, workers become willing to accept lower-wage jobs conditional onthe same commuting distance, which drives down the average wage of reemployed workers.To illustrate the countervailing effects, we use the structural job search model to simulate theeffect of remote work, which reduces workers’ marginal commuting costs to zero.16 The simulatedeffect of job displacement in this counterfactual scenario is plotted in Figure A.18. With remotework, workers no longer value commuting distances in job search and the average commutingdistance remains unchanged before and after job displacement (Paetzold, 2019). As such, displacedworkers benefit from remote work by saving the extra commuting costs. However, remote workalso leads to slightly greater wage losses and more sluggish long-run recovery after displacement.This results from workers’ accepting previously undesired jobs due to the commuting cost, whichlowers the average wages of accepted jobs.2.6 ConclusionIn this paper, we investigate the impact of job displacement on workers’ commuting behavior.Using an event study approach, we estimate the short-run and long-run effects of being displacedin mass layoffs on commuting distances to subsequent jobs. Symmetric to the scarring effect ofwage losses, workers commute up to 21 percent longer distances after displacement and the effectgradually recovers in the next 10 years. Further analysis reveals that the recovery is driven byworkers’ moving from distant to proximate firms with respect to their residences.To quantify the monetary cost of the increased commuting, we build an on-the-job search modelwith heterogeneous firm productivity, non-wage amenities, and commuting distance. With on-the-job search, workers can increase their job match surplus by moving from less to more productivefirms and from distant to proximate firms. This explains the long-run recovery of wages andcommuting after job displacement. Also, workers trade off wages and non-wage amenities againstcommuting costs, giving rise to a reservation value curve increasing in distances. Structurally16We focus on remote work not only for its prevalence in the post-pedantic labor markets but also because itrelaxes workers’ spatial job search friction (i.e., the job offer arrival rates no longer depend on distance). Unlikecommuting subsidies, remote work imposes no fiscal externality on in-person workers. These features greatly simplifyour counterfactual analysis, as we need not account for the impacts of remote work on the distance distribution ofjob offers or the taxation of wages.28estimating the model, we find that workers incur an average commuting cost of 20 euros per day,and increased commuting amplifies the total cost of job displacement by one-fifth of the wage losses.A large literature has documented the profound consequences of job displacement on individualworkers. We contribute to the literature by emphasizing the multi-dimensional cost of job loss.Displaced workers experience not only lower wages and earnings but also increased commutingcosts to subsequent jobs. Future research may examine other outcomes of displaced workers andquantify their contributions to the total cost of job loss.For policymakers, our paper sheds light on the value of transportation infrastructure, working-from-home, and employment assistance programs. Besides cash transfers and skill training, mea-sures to reduce commuting costs and job search friction would also benefit unemployed workers,as they face high commuting costs to find new jobs. Using counterfactual analysis, we explore thecountervailing effects of lower commuting costs on post-displacement jobs. It would also be valuableto study how job search friction impacts the effectiveness of employment assistance programs.Finally, our study highlights the importance of granular commuting data for studying indi-viduals’ responses to job displacement. People’s commuting decisions are also important in otherresearch areas such as urban development, industrial organization, labor market monopsony, andsocial networks. The precise location and commuting data provide new venues for those research.29Figures and TablesFigure 2.1: Mass Layoff Statistics(a) Mass layoff events by year02000400060002002 2004 2006 2008 2010 2012Year(b) Mass layoff sizes by year01002003002002 2004 2006 2008 2010 2012YearPre-layoff establishment sizeWorkers laid off(c) Mass layoff events per year, by county5 - 203 - 51 - 3.5 - 10 - .5(d) Displaced workers per ’000 residents5 - 103 - 51 - 3.5 - 10 - .5Notes: The sample comprises all establishments in the BHP data that went through a mass layoff event in 2002–2012.Panel (a) plots the number of mass layoff events by year. Panel (b) plots the average pre-layoff establishment sizeand the average number of displaced workers per layoff by year. Panel (c) plots the number of mass layoff events peryear by county. Panel (d) plots the number of displaced workers per 1,000 residents by county. In panels (c)–(d),county boundaries are based on 2016 data available at https://ec.europa.eu/eurostat/fr/web/gisco/geodata/reference-data/administrative-units-statistical-units.30Figure 2.2: Effects of Job Displacement on Employment, Wage, and Commuting(a) Full-time employment-1-.8-.6-.4-.20.2-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10Year(b) Daily wage (log)-.3-.2-.10.1-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10Year(c) Commuting distance (log)-.10.1.2.3-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10Year(d) Commuting time (log)-.10.1.2.3-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearNotes: Each plot depicts estimates of βk in equation (2.1) with dependent variables in subtitles. Samples comprisea yearly panel of workers with full-time jobs on June 30 (except panel (a) which comprises a balanced sample). Thevertical dashed line indicates the displacement year. The dots represent the point estimates and the bars representthe 95 percent confidence intervals. All estimates control for a polynomial of age, worker fixed effects, calendar yearfixed effects, and year relative to displacement fixed effects. Robust standard errors are clustered by establishments.31Figure 2.3: Margins of Adjustment(a) Job change-.20.2.4.6.81-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10Year(b) Home relocation-.20.2.4.6.81-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10Year(c) Commuting distance (log)-.10.1.2.3-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10Year(d) Home relocation and distance to work0.05.1.15Share0 20 40 60Distance to workplace (km)Old residenceNew residenceNotes: Panels (a)–(c) depict estimates of βk in equation (2.1) with dependent variables in subtitles. Samples comprisea yearly panel of workers with full-time jobs on June 30 (except column (c) excluding workers who ever relocatedafter displacement). The vertical dashed line indicates the displacement year. The dots represent the point estimatesand the bars represent the 95 percent confidence intervals. All estimates control for a polynomial of age, workerfixed effects, calendar year fixed effects, and year relative to displacement fixed effects. Robust standard errors areclustered by establishments. Panel (d) depicts the distribution of distances between home and work before and afterrelocation. The sample comprises workers who relocated but did not change jobs between two consecutive years afterdisplacement.32Figure 2.4: The Value of Granular Commuting Data(a) Commuting distance by county-.10.1.2.3.4-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearBaseline Omit commutes within regionsSame route across regions(b) Commuting distance by city-.10.1.2.3.4-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearBaseline Omit commutes within regionsSame route across regionsNotes: Each plot depicts estimates of βk in equation (2.1). Samples comprise a yearly panel of workers with full-timejobs on June 30. Dependent variables: The dark blue line uses driving distances between geo-coordinates of anindividual’s residence and workplace; the dashed blue line assigns zero log distance for commutes within regions;the orange line further replaces the commuting distances of all commuters between two regions by the commutingdistance between regional centers (assuming commuters take the same route). Panels (a) and (b) define regions bycounty and city, respectively. The vertical dashed line indicates the displacement year. The dots represent the pointestimates and the bars represent the 95 percent confidence intervals. All estimates control for a polynomial of age,worker fixed effects, calendar year fixed effects, and year relative to displacement fixed effects. Robust standard errorsare clustered by establishments.33Figure 2.5: Model Implications and Empirical Evidence(a) First jobs of displaced workers33.544.55Daily wage (log)0 20 40 60 80 100Commuting distance (km)(b) Ranking jobs by surplus Total job value v Commuting distance rHigh SMed SLow SNotes: Panel (a) depicts the log daily wages and commuting distances of all first jobs accepted by displaced workers.Daily wages are trimmed at the first and the 99th percentiles. Panel (b) depicts three isosurplus curves on the jobspace v-r. Jobs on the same curve have the same surplus level and jobs with greater total value v or lower commutingdistance r have higher surplus levels.34Figure 2.6: Job Offer Distributions(a) Productivity0.511.5Density0 .3 .6 .9 1.2 1.5y(b) Total value0.511.5Density0 .4 .8 1.2 1.6v(c) Commuting distance0.01.02.03Density0 20 40 60 80 100rNotes: Panels (a)–(c) plot the estimated marginal distributions of firm productivity y, total job value v, and com-muting distances r, respectively, derived from the joint job offer distribution Fθ. We estimate that y = 1.489Y whereY ∼ Beta(2.217, 2.550), r = 100R where R ∼ Beta(0.614, 2.130), and v = y + a where a = 0.055100y + 0.337A and A isuniformly distributed in [0, 1].35Figure 2.7: Actual and Simulated Effects of Job Displacement(a) Daily wage (log)-.3-.2-.10-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearData Simulation(b) Commuting distance (log)-.10.1.2.3.4-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearData SimulationNotes: Each plot depicts estimates of equation (2.1) with dependent variable in the subtitle. The dark blue linesreplicate estimates in Figure 2.2, panels (b)–(c). The red lines show estimates from simulated data. All estimatescontrol for worker fixed effects and year relative to displacement fixed effects. Robust standard errors clustered byestablishments.36Table 2.1: Pre-Layoff Worker Characteristics(a) (b)Displaced workers Matched control workersFemale 0.330 (0.470) 0.303 (0.460)Age 40.46 (8.435) 40.81 (8.267)High school or less 0.220 (0.414) 0.224 (0.417)Vocational training 0.715 (0.451) 0.722 (0.448)University or above 0.053 (0.224) 0.045 (0.207)East Germany 0.168 (0.374) 0.159 (0.365)Working experience 14.12 (7.712) 14.94 (7.801)Firm tenure 7.614 (6.126) 8.290 (6.597)Annual earnings (’000) 30.21 (11.20) 31.32 (10.96)Daily wage 99.66 (41.64) 100.7 (37.29)AKM firm effects 0.046 (0.245) 0.017 (0.231)AKM worker effects 4.425 (0.316) 4.487 (0.314)Commuting distance 16.02 (16.69) 14.76 (15.32)Commuting time 23.50 (15.90) 22.20 (14.66)Commute across counties 0.373 (0.484) 0.338 (0.473)Commute across cities 0.590 (0.492) 0.594 (0.491)Workers 9,949 384,071Notes: The table reports the average characteristics of workers displaced in mass layoffs and matched non-displacedworkers in the year before displacement. The sample is obtained using exact matching on gender, education qualifi-cation, industries, and living in eastern Germany, and coarsened matching on age, firm tenure, firm size, and annualearnings in the year before displacement. Standard deviations are reported in parentheses.Table 2.2: Effects of Job Displacement on Employment, Wage, and Commuting(a) (b) (c) (d)Full-time Daily wage Commuting Commutingemployment (log) distance (log) time (log)ML × Post -0.339*** -0.189*** 0.148*** 0.077***(0.005) (0.005) (0.019) (0.010)Observations 4,593,491 4,316,096 4,316,096 4,316,096Workers 394,020 394,020 394,020 394,020R2 0.311 0.898 0.817 0.808Notes: Each column reports estimates of β in equation (2.3) with dependent variables in column titles. Samplescomprise a yearly panel of workers with full-time jobs on June 30 (except column (a) which uses a balanced panel).All estimates control for a polynomial of age, worker fixed effects, and calendar year fixed effects. Robust standarderrors in parentheses are clustered by establishments. (* p < 0.1; ** p < 0.05; *** p < 0.01)37Table 2.3: Margins of Adjustment(a) (b) (c)Job change Home relocation Commuting distance (log)excl. relocated workersML × Post 0.270*** 0.038*** 0.164***(0.004) (0.003) (0.028)Observations 4,316,096 4,316,096 2,591,952Workers 394,020 394,020 245,950R2 0.076 0.067 0.895Notes: Each column reports estimates of β in equation (2.3) with dependent variables in column titles. Samplescomprise a yearly panel of workers with full-time jobs on June 30 (except column (c) which excludes workers whoever relocated after displacement). All estimates control for a polynomial of age, worker fixed effects, and calendaryear fixed effects. Robust standard errors in parentheses are clustered by establishments. (* p < 0.1; ** p < 0.05;*** p < 0.01)Table 2.4: The Value of Granular Commuting Data(a) (b) (c)Baseline commuting Omit commutes Same routedistance (log) within regions across regionsA. Distance by countyML × Post 0.148*** 0.167*** 0.168***(0.019) (0.028) (0.030)Observations 4,316,096 4,316,096 4,316,096Workers 394,020 394,020 394,020R2 0.817 0.817 0.823B. Distance by cityML × Post 0.148*** 0.173*** 0.157***(0.019) (0.024) (0.024)Observations 4,316,096 4,316,096 4,316,096Workers 394,020 394,020 394,020R2 0.817 0.830 0.830Notes: Each column reports estimates of β in equation (2.3). Samples comprise a yearly panel of workers withfull-time jobs on June 30. Dependent variables: Column (a) uses driving distances between geo-coordinates of anindividual’s residence and workplace; Column (b) assigns zero log distance for commutes within regions; Column (c)further replaces the commuting distances of all commuters between two regions by the commuting distance betweenregional centers (assuming commuters take the same route). Panels A and B define regions by county and city,respectively. All estimates control for a polynomial of age, worker fixed effects, and calendar year fixed effects.Robust standard errors in parentheses are clustered by establishments. (* p < 0.1; ** p < 0.05; *** p < 0.01)38Table 2.5: Simulated Method of Moments: ResultsA. External ParametersParameter Value Sourceα 0.928 Jarosch (2023)π0 0.260 Jarosch (2023)π1 0.133 Jarosch (2023)κ1 × 100 0.055 Taber and Vejlin (2020)κ2 0.337 Taber and Vejlin (2020)B. Estimated ParametersParameter Value Moment Model Dataλ0 0.057 U-E rate 0.051 0.051λ1 0.041 E-E rate 0.012 0.012δ 0.014 E-U rate 0.014 0.014y¯ 1.489 w˜99 − w˜1 1.367 1.366ηy1 2.217 w˜50 − w˜25 0.273 0.260ηy2 2.550 w˜75 − w˜50 0.219 0.207ηr1 0.614 r50 − r25 0.075 0.055ηr2 2.130 r75 − r50 0.100 0.098ρcyr -0.020 ρyr -0.018 -0.018c× 100 1.365 γ1 × 100 0.094 0.096z -0.004 S((0, 0), h1) 0.000 0.000Notes: Panel A reports external parameters based on the literature. Panel B reports estimates using the SimulatedMethod of Moments with corresponding model and data moments.Table 2.6: Willingness to Pay for Less Commuting(a) (b) (c) (d)Baseline Alternative Male FemaleidentificationSemi-elasticity (c) ×100 1.365 1.398 1.136 1.838Elasticity 0.196 0.201 0.181 0.231Commuting cost per km (euro) 1.370 1.404 1.350 1.448Commuting cost per day (euro) 19.72 20.20 21.54 18.19Average daily wage (log) 100.4 100.4 118.8 78.8Average commuting distance (km) 14.39 14.39 15.96 12.56Notes: The upper panel reports SMM estimates of the WTP for less commuting c, the implied wage elasticitywith respect to commuting distances, average commuting cost per kilometer, and average commuting cost per day.The last three estimates are evaluated at the sample-average commuting distance and daily wage. Columns (a)–(b)report estimates from the baseline model (Section 2.5.1) and the alternative identification strategy (Section 2.5.2),respectively. Columns (c)–(d) report estimates from the baseline model separately by gender.39Chapter 3The Impact of Dockless Bike Sharingon Subway Housing Price Premiums3.1 IntroductionIn recent years, over 1,500 cities around the world have embraced shared bikes as an innovativeand economical alternative for urban commuting. From 2013 to 2018, the number of shared bikesworldwide increased from 700,000 to 18 million, most of which are dockless bikes that are operatedwithout docking stations and technically can be parked almost anywhere. Studies have found thatdocked shared bikes can reduce commuting costs, traffic congestion, and air pollution (Woodcocket al., 2014; Pelechrinis et al., 2016); dockless bikes are likely to have similar benefits.In particular, dockless bike sharing may provide an effective solution to the “last-mile problem”facing urban dwellers. Despite affordable means of station-to-station commuting via public transit(e.g., subways, buses, and trams), commuting remains costly between home and a public transitstation. To alleviate such costs, people choose to live near subway stations, which drives up thedemand for and the price of proximate apartments. This gives rise to the “subway housing pricepremiums” for apartments close to subway stations relative to distant ones (Dewees, 1976; Coulsonand Engle, 1987; Baum-Snow and Kahn, 2000; Gibbons and Machin, 2005; Fesselmeyer and Liu,2018). By contrast, dockless bike sharing offers a convenient and affordable means of door-to-doorcommuting to complement public transit.17 It allows people to live farther from a subway but stillaccess subway services easily. This is expected to drive up the demand for and the price of distantapartments and reduce the price premiums of proximate apartments.In this chapter, we study how dockless bike sharing moderates the relationship between housingprices and distances to the subway (the “housing price gradient”, Dewees, 1976) and quantify themonetary value of dockless bike sharing in solving the last-mile problem. Our empirical analysisexploits detailed information on nearly 400,000 resale apartments in 10 major Chinese cities, whichhave a combined population of 152 million and over 1,400 subway stations in operation. To identifythe causal effect of dockless bike sharing on subway housing price premiums, we use the staggeredentry of Ofo and Mobike into these Chinese cities at different times as a quasi-natural experiment.17A survey of 1,255 shared bike riders in China reports that 68 percent of the respondents ride from and to publictransit hubs, and over 90 percent of trips cover a distance under three kilometers. LimeBike, a U.S. bike sharingcompany, reports that 40 percent of its rides serve the same purpose, and an average ride in U.S. metropolitan areasis around one mile. Another report from China finds that over half of the rides are within one-half to two kilometersor six to 20 minutes. See https://www.cbinsights.com/research/bike-sharing-boom, http://report.iresearch.cn/wx/report.aspx?id=2961, and http://www.chinadaily.com.cn/a/201801/10/WS5a557e01a3102e5b17371d1b.html.40Ofo and Mobike are the two largest dockless bike sharing companies in China, with a combinedmarket share of over 90 percent. Since 2015, they have jointly introduced 17 million dockless bikesto more than 200 cities globally, and each has acquired over 200 million users.18 Among all docklessbike sharing companies, Ofo and Mobike are also the first entrants into cities in our analysis.We establish the causal relationship via two empirical strategies: (i) a difference-in-differences(DID) analysis at the apartment level and (ii) a two-step estimator at the city-month level. In theDID approach, the effect is identified from the price variation of apartments at different distances tothe same subway station before and after the entry. In the two-step approach, we directly estimatethe housing price gradients in each city at different time points and identify the effect by comparingthe gradients before and after the entry. Both approaches yield a consistent finding: The entry ofbike sharing significantly attenuates the housing price gradient by 29 percent, from 4.2 percentagepoints to 3.0 percentage points per kilometer, the average value of which is equivalent to an urbanresident’s yearly disposable income.Using the hedonic price method (Rosen, 1974b; Roback, 1982b), we further infer the reductionin commuting costs due to bike sharing from changes in the housing price gradient. Assuming aperfectly competitive housing market where housing prices fully capitalize the commuting costs,the implied reduction in annual commuting costs amounts to 1,893–2,127 CNY (282–317 USD)19per household over 30 years of residence. Further analysis reveals that the effect is driven by arelative increase in the attractiveness of distant apartments to potential buyers, as well as a rela-tive rise in their initial listing prices. In addition, the effects are heterogeneous across apartments,communities, and cities, robust to alternative samples, time windows around entry, distance mea-sures, and competing explanations. We also rule out pre-trends, endogenous or anticipated entryof bike sharing, and changing composition of apartments at different distances from the subway asconfounding factors to our estimates.To summarize, our main contributions are as follows. First, we use different approaches toestablish the causal effect of dockless bike sharing on subway housing price premiums. Second, weexplore mechanisms of the reduced price premiums from the supply side and the demand side. Wefind that property owners and buyers both respond to the entry of dockless bike sharing, whichjointly reduces the housing price gradient. We also find that the gradient reduction arises from areduction in commuting costs. Third, we quantify the monetary value of reduced commuting costsand demonstrate the benefits of bike sharing in solving the last-mile problem. As such, our findingshave significant implications for bike sharing firms, property developers, policymakers, and bikeriders.3.1.1 Related LiteratureOur research contributes to the burgeoning literature on the sharing economy. Pioneered by Uber,Airbnb, and other gig companies, the sharing economy has triggered significant changes in the18See https://www.bbc.com/news/business-44066083 and https://mobike.com/cn,http://www.ofo.com.19Hereafter, we fix the exchange rate between CNY and USD at 6.7:1.41traditional economy. Existing studies find that Airbnb reduces the prices of low-end hotels (Zervaset al., 2017) but raises the prices of rental properties (Barron et al., 2018); Uber promotes self-employment among taxi drivers (Berger et al., 2018) and complements public transit and taxis(Mammen and Shim, 2017; Hall et al., 2018), but also reduces taxi drivers’ earnings (Berger et al.,2018). On the other hand, the traditional economy responds to threats from the sharing economy invarious ways. Uber’s entry in New York City and Chicago reduces consumer complaints about taxiservices, which implies that competition from Uber improves the service quality of taxis (Wallsten,2015). In Singapore, taxi companies introduced a flat-fare option to mitigate competition fromride-hailing platforms (Miao and Chu, 2019).The sharing economy boom has important welfare implications. Fraiberger and Sundararajan(2017) find that a peer-to-peer rental market for used goods raises consumer surplus by acceleratingthe replacement of used goods and offering lower prices. Ride-hailing platforms are shown toimprove rider welfare by matching drivers to riders who value the ride the most (Cohen et al.,2016) and serving areas under-served by taxis (Lam and Liu, 2017). They also benefit drivers byoffering more flexible working hours (Chen et al., 2019), proportional commission fees to share therisk of demand uncertainty (Angrist et al., 2021), and higher capacity utilization rates of vehicles(Cramer and Krueger, 2016). In terms of non-pecuniary benefits, Uber is found to relieve trafficcongestion (Li et al., 2016) and reduce traffic accidents related to drunk driving (Greenwood andWattal, 2017). Docked bike sharing is found to reduce traffic congestion (Wang and Zhou, 2017)and carbon emissions (Pelechrinis et al., 2016). For a comprehensive review of the literature, werefer the reader to Proserpio and Tellis (2017).Our study extends the literature in several ways. To the best of our knowledge, we are thefirst to study the economic impact of dockless bike sharing. In contrast to Uber, which seeks todisrupt the traditional business, bike sharing serves more as a complement to public transit, and thecomplementary effect could be more salient for dockless bikes because they offer greater flexibilityin riding routes than docked bikes. Instead of studying closely related industries such as taxis andpublic transit, we investigate how dockless bike sharing affects subway housing price premiums andquantify the monetary value of dockless bike sharing in reducing commuting costs.20Beyond the sharing economy literature, our paper is also related to the urban economics liter-ature on China’s housing market (e.g., Chen and Wen, 2017; Deng et al., 2014; Fang et al., 2016;Wei et al., 2017) and the effects of transportation condition on housing prices (e.g., Bajic, 1983;20Related to our research, Pelechrinis et al. (2017) study the effect of docked bike sharing in Pittsburgh on housingprices around docking stations. However, their study does not provide sufficient evidence to justify the parallel pre-trend assumption and the exogeneity of docking stations, and thus cannot establish a causal relationship. By contrast,we use two approaches and various robustness checks to demonstrate the causal effect of dockless bike sharing on thesubway housing price premium. We further show that the effect depends on an apartment’s distance to a subwaystation, i.e., dockless bike sharing reduces the negative effect of distance on housing price, while Pelechrinis et al.(2017) do not investigate how the distance between docking stations and other public transit options affects housingprice. We also take further steps to explore the mechanism underlying the change from both the demand side andthe supply side and quantify the savings in commuting costs brought forward by bike sharing. Another related studyis Cao et al. (2021), who examine the competition between dockless bike sharing companies in China. We look at thesame market but focus on a different aspect: How dockless bike sharing reduces commuting costs and thus moderatesthe relationship between housing price and distance to the subway.42Baum-Snow and Kahn, 2000; Bowes and Ihlanfeldt, 2001; Coulson and Engle, 1987; Dewees, 1976;Fesselmeyer and Liu, 2018; Gibbons and Machin, 2005; Yiu and Wong, 2005. Our results are consis-tent with existing findings that housing prices are higher nearer subway stations because residentsenjoy more convenient public transport services. Furthermore, we validate that households make atrade-off between lower commuting costs and higher housing prices. As the entry of dockless bikesharing reduces commuting costs, the housing price premiums near subway stations fall, and theprice difference between houses of different distances to the subway shrinks.The remainder of the paper is organized as follows. Section 3.2 presents the data. Section 3.3introduces our empirical strategy, and Section 3.4 reports the main findings. Section 3.5 conductsvalidation and robustness tests, and Section 3.6 concludes.3.2 Data3.2.1 Housing Prices and CharacteristicsWe exploit a novel administrative data set of resale apartments provided by a Chinese real estateagency, which has the largest market share in most Chinese cities. The data comprises 507,975apartments initially listed for resale between July 1, 2015 and December 31, 2017 and tracks allunsold apartments until March 12, 2018, when the data was compiled. Thus, each apartment inour data is observed for at least 2.5 months. The data contain detailed characteristics of eachapartment, including the size, floor, age of the building, number of rooms, decoration status,window directions, geo-coordinates, and whether it is located in a public school district. It alsotracks each apartment’s price history, sales status (sold or not), and number of visits by potentialbuyers. We focus on 10 major Chinese cities with developed subway systems by 2015: Beijing,Chengdu, Chongqing, Dalian, Hangzhou, Nanjing, Shanghai, Shenzhen, Tianjin, and Wuhan.We distinguish an apartment’s initial price, adjusted price, and last/transaction price as follows.When a seller decides to list their apartment on the agency’s website, they set an initial price forthe apartment at will. Before the apartment is sold, the seller can overwrite the previous pricewith an adjusted price, which can be lower or higher. The data set records all price adjustmentsand the time of adjustments. If the apartment is sold via the agency, the data will record thetransaction date and actual transaction price. Thus, an apartment will have multiple observationsif there are price adjustments or updates on the sales status. If an apartment is sold withoutnotifying the agency (usually to avoid paying the agent commissions), the last price is likely theactual transaction price, but the transaction status of the apartment is not updated.When an apartment is available for resale, interested buyers may contact the agency to arrangea visit to the apartment and may bargain with the seller for a lower price. The sale of an apartmenttypically involves many rounds of viewing and bargaining. For all apartments, we observe the totalnumber of visits by interested buyers up to March 12, 2018; for apartments in Beijing, we also havea detailed viewing history with anonymized viewer identifiers.433.2.2 Entry of Bike SharingIn Table 3.1, we report the entry dates of Ofo and Mobike to each city (see also Cao et al., 2021).The earlier of Ofo’s and Mobike’s entry dates are defined as the entry date of dockless bike sharing.It is worth noting that, upon entry to each city, the placement of shared bikes may not be random atthe street level. It is possible that shared bikes are more concentrated in areas near subway stationsthat have higher demand for commuting. However, the high mobility and dockless feature of sharedbikes will randomize the distribution of new bikes soon after they are released, and residents distantfrom the subway will have similar access to shared bikes as proximate ones. In addition, the bikesharing companies regularly relocate bikes across neighborhoods during non-peak hours.Following Hall et al. (2018) who use Google Trend to proxy Uber’s penetration in the U.S.,we also use the daily Baidu search index21 of the keyword “bike sharing” to proxy bike sharing’spenetration in each city. As Figure 3.1 shows, in many cities, the index peaked right after the entryof Ofo and Mobike.3.2.3 Distance to Subway StationsWe manually collect information on each city’s subway network, which includes each station’s geo-coordinates and the starting date of operation. Then we match each apartment to its nearestsubway station by geodesic distance and keep apartments within three kilometers of the neareststations. Twelve percent of apartments beyond three kilometers are excluded because buyers ofthese apartments are less likely to use shared bikes to commute between home and the subway (seefootnote 17). As shown in Appendix B.1, an apartment’s distance to the subway may decrease asnew subway stations are built closer to it.Figure 3.2 compares the distribution of distances from each apartment to the nearest subwaystation before and after the entry of bike sharing. In panel (a), we find a greater share of apartmentswithin one kilometer of the nearest subway after the entry. However, it is likely due to the openingof new stations. In panel (b), we plot the distribution of distances from each apartment in panel(a) to the nearest station open before June 30, 2015. As such, apartments previously matched toa new station could be matched to a different but more distant one. Focusing on existing stations,we find little difference in the distribution of distances before and after the entry.The geodesic distance to the subway is intuitive for illustrating the housing price gradient. Inreality, however, commuters may also consider walking distance to a subway station. Therefore,we use a route-planning algorithm (Baidu Maps) to determine the walking distance from eachapartment to the nearest subway station identified by geodesic distance. The two distance measuresare highly consistent, with a correlation coefficient of 0.89. However, we might occasionally matchan apartment to a non-nearest station because of the potential discrepancy between geodesic andwalking distance, and thus lose 3.8 percent of observations.21The Baidu search index is the Chinese substitute of Google Trend developed by Baidu.com, the largest searchengine in China. It counts how many times a keyword is searched on Baidu.com every day in each city.443.2.4 Summary StatisticsTable 3.2 presents summary statistics of our data. In total, we have 617,271 price records from399,840 apartments matched to 1,422 stations. The average price is 31.54 thousand CNY/m2(437USD/ft2); the average price adjustment over the previous price is 7.4 percent, with a standarddeviation of 5.6 percent. An average apartment is 90.5 m2(974 ft2) in size, has 2.2 bedrooms,and is located on the ninth floor of a 14-year-old building22. Half of the apartments are in schooldistricts. In addition, 13 percent of the apartments come with basic decoration, 20 percent withintensive decoration, and the remaining with no decoration or missing decoration information. Theapartments have windows that face different directions, with the most common direction beingsouth (77 percent) and the least common being west (12 percent). The average geodesic andwalking distances to the subway are 1.08 kilometers and 1.62 kilometers, respectively, and ninepercent of apartments are matched to an interchange station. Finally, 55 percent of apartmentsare listed before and 45 percent after the entry of bike sharing.3.3 Empirical StrategyOur objective is to identify how dockless bike sharing moderates the relationship between housingprices and distances to the subway by reducing commuting costs between home and subway stations.We take two approaches to establish the causal impact of dockless bike sharing on the housing pricegradient: A DID approach at the apartment level and a two-step estimator at the city-month level.Then, we use a back-of-the-envelop analysis to back out the implied reduction of commuting costsin the spirit of hedonic prices (Rosen, 1974b; Roback, 1982b).3.3.1 Difference-in-Differences at the Apartment LevelFirst, we exploit the staggered entry of Ofo and Mobike into the 10 Chinese cities as a quasi-naturalexperiment. Our DID specification is similar to Archibong and Annan (2017) who perform a DIDestimation on cross-sectional data with some observations entering the sample before the treatmentand others after the treatment. In our study, we estimate the price gradients of apartments atdifferent distances to the subway and obtain the change before and after the entry of bike sharing:ln(Pit) = Dististβ1 +Bikectβ2 + (Distist ×Bikect)β3 +X ′itγ + αs + ϕct + ϵit. (3.1)In equation (3.1), i, s, c, and t represent apartments, subway stations, cities, and time, respectively;Pit is apartment i’s price per m2, listed or adjusted at time t; Distist is apartment i’s distance tothe nearest subway station s at time t; Bikect indicates that the price Pit is listed after bike sharingenters city c. In the baseline estimates, we define Distist as the geodesic distance and Bikect as22About 37 percent of observations have missing building age. To avoid losing these observations, we create anindicator for apartments with missing data on age and replace the missing data with the mean of reported ages. InTable 3.6, column (e), we report estimates without controlling for building age as a robustness check.45the indicator of the earlier entry of Ofo and Mobike in each city.The vector Xit represents apartment characteristics, including size, floor number, building age,number of bedrooms, indicators of decoration status, window directions, and school district. Wealso include in Xit a measure of apartment density, i.e., the number of apartments matched to thesame subway station as the focal apartment in the same month. Apartments with adjusted priceshave multiple observations, so we also include indicators of the initial and last prices, respectively.Controlling for apartment characteristics allows us to compare the prices of similar apartments.In addition, we control for subway station fixed effects αs and city-month fixed effects ϕct. Thestation fixed effects account for factors that may affect both housing prices and the suitability ofbike riding (e.g., road conditions), while the city-month fixed effects control for any city-wide policyimpacts, such as regulations on the housing market or the bike sharing companies. Since docklessbike sharing may enter a city in the middle of a month, ϕct does not completely absorb Bikect.Finally, ϵit is the error term.The economic intuition of equation (3.1) is as follows. Before the entry of bike sharing (Bikect =0), the housing price gradient with respect to distance to a subway station is β1, which is expectedto be negative. After the entry (Bikect = 1), the gradient becomes β1 + β3. Ceteris paribus, theaverage housing price drops by 100β1 percent before entry and by 100(β1+β3) percent after entry,for each kilometer away from the subway. As such, β3 identifies the impact of bike sharing on thegradient. A positive β3 implies that dockless bike sharing flattens the gradient and reduces theprice premiums of apartments near subway stations.3.3.2 Two-Step Estimation at the City-Month LevelIn the DID specification, we do not include apartment fixed effects because many apartmentshave only one observation. The presence of unobserved apartment characteristics or other macro-socioeconomic factors may bias the estimates if they affect apartments at different distances fromthe same subway station differently. Therefore, we conduct another analysis at the city-month levelvia a two-step approach. In the first step, we estimate a housing price gradient for each city-monthcell by equation (3.2a); second, we compare the gradients before and after the entry using equation(3.2b):ln(Pit) =βctDistist +X′itβ + αs + ϕt + ϵit, (3.2a)βˆct =γBikect + αc + ξit. (3.2b)Essentially, both strategies rely on the exogenous price variation (before and after the entry ofbike sharing) for similar apartments at different distances to the same subway station. The keyidentifying assumption is that, in the absence of bike sharing, housing prices at different distancesto the subway evolve similarly, or the price gradient remains unchanged. In Section 3.5, we provideempirical evidence that (i) there is no pre-trend for housing prices at different distances to thesubway, (ii) the entry of bike sharing to each city is unanticipated and exogenous to city-level46characteristics, and (iii) there is no compositional change of apartments near vis-a-vis away fromsubway stations. We also rule out confounding factors that affect apartments matched to the samestation differently depending on their distances, especially after the entry of bike sharing.3.4 ResultsWe estimate equation (3.1) with robust standard errors clustered by subway station. Table 3.3,column (a) presents the average effect of the entry of dockless bike sharing on housing prices withinthree kilometers of subway stations. First, the coefficient of distance to the subway, -0.042 (s.e.0.003), indicates that apartments near subway stations enjoy a price premium before the entry ofbike sharing. For each kilometer away from a subway station, average housing prices fall by 4.2percent. Next, the coefficient of distance interacted with bike sharing, 0.012 (s.e. 0.003), impliesthat the entry of bike sharing reduces the premium and flattens the gradient by 1.2 percentagepoints or 29 percent of the pre-entry level. As a result, apartments near subway stations still enjoya price premium after entry, but the magnitude is 71 percent of that before entry.At the average housing price of 31,536 CNY/m2and the average size of 90.5 m2, the estimatedprice gradient for an average apartment is 119,868 CNY (17,890 USD) per kilometer before entry.In other words, an average apartment one kilometer closer to a subway enjoys a price premium of119,868 CNY. After the entry, the reduction in the gradient translates to a lower price of 34,248CNY (5,112 USD) per kilometer. The effect is both statistically and economically significant: In2016, the average disposable income of an urban resident in China was 33,616 CNY, so the reductionis approximately one year of the disposable income.Alternatively, columns (b) and (c) define the entry of bike sharing using the entry of Ofo andMobike, which attenuate the gradient by 1.3 and 1.1 percentage points per kilometer, respectively.Column (d) uses the Baidu search index to measure the penetration of bike sharing in each city(Hall et al., 2018). For every increase of 1,000 in the search index, the gradient will be flattened by1.0 percentage points per kilometer. Moreover, Table 3.3, column (e) reports two-step estimates ofequation (3.2b) at the city-month level. After the entry of bike sharing, the housing price gradientdecreases by 1.4 percentage points, close to estimates from the DID model controlling for stationfixed effects and city-month fixed effects. Given the similarity, we will focus on equation (3.1) insubsequent analyses.Nonlinear effects. The above estimates assume that the housing price gradient is constant acrossall distances to the subway. To detect any non-linear pattern of the price gradient, we re-estimateequation (3.1) but replace the continuous variable Distist with indicators that an apartment fallsinto every 500 meters bin of distance to the nearest subway, with the last bin (beyond two kilome-47ters) as the reference group. This allows the gradients to vary by distance:ln(Pit) =4∑k=11{0.5(k − 1) ≤ Distist < 0.5k}β1,k +Bikectβ2+Bikect4∑k=11{0.5(k − 1) ≤ Distist < 0.5k}β3,k +X ′itγ + αs + ϕct + ϵit.(3.3)In Figure 3.3, the blue dots depict coefficient estimates before entry (β1,k), the red ones depictestimates after entry (β1,k + β3,k), and the bars denote the corresponding 95 percent confidenceintervals. Consistent with the findings in Table 3.3, the estimated housing price gradients arenegative both before and after the entry of bike sharing, but the gradient becomes flatter after theentry. However, neither the slope nor the change is uniform. Both before and after entry, the slopeis the steepest between 500 meters to two kilometers of the subway. The entry of bike sharing“rotates” the gradient curve, which implies that the price premiums of proximate apartments (themore expensive ones) decrease relative to those further away.3.4.1 MechanismsThe above estimates indicate that the entry of dockless bike sharing is associated with a reduction inthe subway housing price gradient around subway stations and a narrower price gap between distantand proximate apartments. As we proposed, dockless bike sharing increases the attractiveness ofapartments distant from vis-a`-vis proximate to subway stations and shifts the former’s demandcurve outwards. Anticipating this, sellers of distant apartments may raise their listing prices andgain more bargaining power in price negotiations. Using detailed data on housing prices and thetransaction process, we empirically test the above mechanisms.We estimate equation (3.1) with five outcomes: the number of visits by potential buyers, theinitial listing price, the last price, the transaction price, and price adjustments. The frequencyof visits indicates buyers’ interest and purchase intention; the initial price indicates the seller’sperceived value of the apartment; the last and transaction prices reflect the prices in market equi-librium; and the direction of price adjustment reveals the bargaining power of sellers and buyers.Hence, the effect of bike sharing on these variables represents its effect on the demand side, thesupply side, and the market equilibrium, respectively.Table 3.4, column (a) reports estimates for the frequency of visits. The coefficient of distanceto the subway, -0.018 (s.e. 0.005), implies that apartments proximate to subway stations attractmore visits before the entry of dockless bike sharing despite their higher prices: For every kilometeraway from a subway, the number of visits declines by 1.8 percent. The coefficient of distance ×bike sharing, 0.016 (s.e. 0.006), means that the entry of bike sharing increases visits to apartmentsfarther from subway stations relative to proximate ones and that potential buyers become moreinterested in the distant apartments.Next, column (b) shows the estimates for initial prices. The coefficient of distance × bike48sharing is positive and significant (0.015, s.e. 0.003), which indicates that the entry of bike sharingreduces the gradient of initial prices by over one-third (0.015/0.043). This suggests that whensetting initial listing prices, property owners already take into account the effect of dockless bikesharing on housing prices. Table 3.4, columns (c) and (d) report, respectively, estimates on lastprices for all apartments and transaction prices for sold apartments. The coefficients of distance ×bike sharing are both positive and have similar magnitudes as that for initial prices. They implythat in equilibrium, dockless bike sharing narrows the price gap between distant and proximateapartments by roughly one-third.Finally, column (e) reports the estimates for price adjustment. The coefficients of distanceto subway and distance × bike sharing are in the same direction as above, but they are notstatistically significant. This implies that there is no significant difference in price negotiationbetween apartments closer to and farther away from subway stations, either before or after theentry of bike sharing. Combining the above estimates, we conclude that both the demand side andthe supply side respond to the entry of dockless bike sharing and jointly determine the housingprice gradient.3.4.2 Welfare ImplicationsOur analysis above indicates that dockless bike sharing generates considerable benefits for urbancommuters by making subway services more accessible to those living farther from subway stations.Potentially, dockless bike sharing reduces commuting costs via several channels. For people whowalk to subway stations, bike sharing offers a faster commuting option and hence saves travel time.For people who first walk to bus stops and then take buses to subway stations, dockless bike sharingcan reduce their waiting time for buses, is less vulnerable to bad traffic, and could be cheaper thanthe bus fare.For people who ride their own bikes, bike sharing saves not only the cost to purchase,maintain, and park their bikes, but also the risk of having their bikes stolen or damaged. Moreover,with shared bikes, people no longer need to return to the same subway station to pick up their ownbikes. Finally, for people who do not travel by subway because they live too far from a station, bikesharing provides them with easier access to the subway and encourages them to substitute cheaperpublic transit for other means of commuting such as driving their own cars or taking a taxi.In this subsection, we conduct a back-of-the-envelope analysis to recover the reduction in com-muting costs from the previously estimated change in housing price gradient. From a hedonic priceperspective, we interpret the subway housing price premiums as the compensating commuting costsfor living in proximate apartments in a competitive housing market. Analogously, the reduction inthe gradient can be interpreted as lower commuting costs due to the entry of dockless bike sharing.If there is friction in the housing market, the change in housing prices will capture part of thereduction in commuting costs.The calculation is performed as follows. For each apartment listed after entry (all with Bikect =1), we use the estimates in Table 3.3, column (a) to predict its total price (predicted price per m2×size) and counterfactual total price as if there were no bike sharing (Bikect = 0). Then, we compute49the difference between these two prices, which we treat as the reduction in commuting costs (or thepart captured by housing prices) during the buyer’s entire stay in the apartment. Next, we amortizethe long-term reduction into 30 years of residence23 to obtain the annual amount. We use China’slatest compound interest rate for 5-year fixed deposits (2.86 percent per year) and 5-year treasurybills (3.86 percent per year), respectively, as the lower- and upper-bounds of discount factors.With these estimates, we find the annual reduction in commuting costs to be 1,893–2,127 CNY(282–317 USD) per apartment, averaged across all apartments. In comparison, the annual cost ofdockless shared bikes is 240 CNY per person or 480 CNY per household. These figures imply thatdockless bike sharing reduces commuting costs for urban dwellers significantly more than its usercost. In other words, bike sharing companies do not fully internalize all of the benefits of providingdockless shared bikes; the benefit of solving the last-mile problem is at least partly captured bybuyers or sellers in the housing market.3.4.3 Effect HeterogeneityThe effect of bike sharing on housing price premiums near the subway may vary across apartments,communities, and cities. In Table 3.5, we examine the within-city heterogeneity by introduc-ing three-way interactions between distance to subway, entry of bike sharing, and apartment- orcommunity-level moderators. The coefficient of distance × bike sharing represents the averageeffect size across all apartments, while the coefficient of distance × bike sharing × moderator repre-sents the change in the effect size as the moderator increases by one standard deviation (continuousmoderators are normalized to zero mean and unit standard deviation).Table 3.5, columns (a) and (b) report, respectively, the effect of bike sharing by apartment sizeand floor number. We find that the average effect of bike sharing is centered around the previousestimate, but is particularly large for larger and higher-level apartments: One standard deviation(42.7 m2) of increase in apartment size is associated with an increase in the treatment effect by two-thirds (0.007/0.011); one standard deviation of rise in floor number (7.8 stories) is associated withan increase in the treatment effect by one-third (0.004/0.013). This is consistent with the fact thatbigger and higher-floor apartments tend to be priced higher and have greater price elasticity. Asbike sharing reduces the commuting cost to the subway, these apartments become more affordablein terms of the combined cost of housing prices and commuting, so they respond to the entry morestrongly than cheaper apartments.Table 3.5, column (c) reports the effects of bike sharing by whether an apartment is in a schooldistrict. The coefficient of distance × bike sharing × moderator is statistically insignificant, whichmeans that the effect of bike sharing is not contingent on whether an apartment is within a schooldistrict. This provides further evidence that bike sharing mainly benefits adults’ commuting towork rather than children’s commuting to school: Children under 12 years old are not allowed toride shared bikes on streets.23In China, residential buildings become eligible for demolition and reconstruction after 30 years of use. Table B.2reports estimates using alternative residential duration.50In addition, we study how local commuting conditions moderate the effect of dockless bike shar-ing. We measure commuting conditions in two ways to capture the accessibility of subways: whetheran apartment is near an interchange station that connects several subway lines and the number ofsubway stations within three kilometers of an apartment. Columns (d)-(e) report estimates usingeach of the two measures. Both coefficients of the three-way interactions are positive, which indi-cates that the effect of bike sharing on subway housing premium is stronger for apartments withadvantageous commuting conditions via subways. This further testifies to the complementarity ofdockless bike sharing to subway commuting.Next, we examine the heterogeneous effect of dockless bike sharing across cities. We estimateequation (3.1) separately for each city and report the results in Table B.3. We find downward-sloping housing price gradients in all cities, which reflects higher housing prices near subway sta-tions, but the magnitude differs substantially across cities. The gradients are attenuated after theentry of dockless bike sharing: by 3.7 percentage points in Shanghai, 2.9 percentage points in Bei-jing, 2.1 percentage points in Shenzhen, 2.0 percentage points in Wuhan, and 1.5 percentage pointsin Chongqing. The attenuation effects in other cities are statistically insignificant.In reference to housing prices and disposable income, the impact of dockless bike sharing onhousing price gradients is huge. In Beijing, the housing price gradient drops by 52.7 percent, whichis equivalent to 2.98 times the city’s per capita disposable income in 2016; the reduction amountsto 2.96 times the per capita disposable income in Shanghai, 2.03 times in Shenzhen, and 0.81 timesin Wuhan. In Chongqing, dockless bike sharing completely flattens the housing price gradient.3.4.4 RobustnessIn the baseline estimates, we limit the sample to apartments within three kilometers of the nearestsubway station. Table 3.6, columns (a)-(c) report, respectively, estimates using apartments withintwo kilometers, four kilometers, and five kilometers of the nearest station. All estimates of thebike sharing effects remain positive and significant and diminish as the radius increases. This isconsistent with survey evidence that people ride shared bikes only for short-distance commutes. Asthe distance gets longer, fewer people will use shared bikes to commute to the subway. This alsoprovides indirect evidence that dockless bike sharing, as a commuting option, is complementary tothe subway.Table 3.6, column (d) reports estimates using walking distances between apartments and subwaystations. For every kilometer of walking distance, housing prices decline by 2.6 percent; the entryof bike sharing flattens the gradient by 0.9 percentage points or one-third (0.009/0.026) of the pre-entry level. Note that one kilometer of geodesic distance is roughly equivalent to 1.5 kilometers ofwalking distance, so the magnitude of the coefficient would be 1.35 percentage points per kilometerin the geodesic distance, almost the same as in Table 3.3, column (a).In addition, we check whether the imputation of missing building age significantly alters ourestimates. Table 3.6, column (e) reports estimates excluding building age and the indicator formissing age from the controls, and the results are similar to before.51In DID regressions, Bertrand et al. (2004) and Donald and Lang (2007) recommend clusteringstandard errors at the level of treatment, which is the cities in our study. With only 10 cities,however, it is difficult to consistently estimate the standard errors by clustering. As such, Table3.6, column (f) reports standard errors clustered by cities obtained from bootstrap, which helpsadjust for the small number of clusters (Cameron et al., 2008). The estimate is statistically thesame as that when standard errors are clustered by subway stations.3.5 ValidationThe above estimates indicate that the subway housing price gradient becomes flatter after theentry of bike sharing. To interpret this effect as causal, we require that (i) the entry time of bikesharing is unanticipated, not correlated with any natural trend of the housing price gradients or anycity characteristics that also affect the housing price gradients, and (ii) there is no compositionalchange in the housing characteristics at different distances to the subway after the entry. Thesecond assumption is necessary as many apartments are only observed once, so we cannot controlfor compositional changes through apartment fixed effects. This section provides empirical evidenceto support our causal interpretation.3.5.1 Parallel Pre-TrendsParallel pre-trends imply that absent the entry of bike sharing, the prices of apartments near andfarther from the subway should move in parallel, or the housing price gradient should remainunchanged. To test this assumption, we estimate the subway housing price gradient for each monthrelative to the entry of bike sharing and examine its time trend. We extend equation (3.1) to allowfor time-varying effects,ln(Pit) =∑k ̸=−1DististBikect,kβk +X′itγ + αs + ϕct + ϵit. (3.4)where Bikect,k indicates that the price Pit of an apartment i in city c is listed in the k-th monthafter bike sharing enters the city; βk captures the housing price gradient in the k-th month relativeto the month before entry.Figure 3.4 plots the coefficient estimates and 95 percent confidence intervals of βk. In the sixmonths before bike sharing’s entry, the estimated housing price gradients remain almost constantat around -0.042. The gradients start shrinking (in absolute value) in the second month after entry,and we reject the joint hypothesis that post-entry estimates of βk all equal to β−1.3.5.2 Exogenous and Unanticipated EntryExogenous entry. We argue that the entry dates of bike sharing into each city are plausiblyexogenous, given how local governments regulate the entry of bike-sharing companies. Beforeentering a city, a bike sharing company must submit a proposal to the municipal authority for52approval. Even if the company endogenously chooses the time to submit the proposal, the time ofapproval largely depends on administrative processing time rather than local housing prices or theprice gap between apartments at different distances to the subway.We conduct three statistical tests to validate the exogeneity of entry dates at the city level.Following Zervas et al. (2017), we construct a balanced panel comprising 240 city-year-monthobservations (10 cities from January 2016 to December 2017). To examine whether pre-entry citycharacteristics impact the entry decision of bike sharing, we estimateBikect =∑t(DtXc)θt + ϵct, (3.5)where Bikect indicates the presence of bike sharing in city c, month t. Dt are monthly dummiesand Xc represents pre-entry city characteristics measured in 2015: log population, log annual GDP,log annual subway ridership, and log annual average housing price. For ease of illustration, citycharacteristics variables are standardized to have zero mean and unit standard deviation. FigureB.1 plots estimates of θt with 95 percent confidence intervals. All but one coefficient is statisticallyinsignificant at the five percent level.Second, we conduct a hazard rate test similar to Seamans and Zhu (2013), using the citycharacteristics from (3.5) to predict the hazard rate of entry. As shown in Table B.4, none of theestimated coefficients is statistically significant at the five percent level. Thus, it is reasonable tobelieve that pre-entry city characteristics do not predict the entry of bike sharing, which is plausiblyexogenous at the city level.Third, we estimate our baseline model using random entry dates following Bertrand et al. (2004).Given the multi-level structure of our empirical context and data set, we randomize the entry datesacross cities, subway stations, apartments, and even observations. In particular, varying the entrydates at lower levels helps alleviate the endogenous spatial distribution of bikes within each city.Table B.5 reports estimates with randomized entry dates at each level. The estimates for distance× bike sharing are all attenuated toward zero.Unanticipated entry. If the entry of bike sharing is anticipated, housing price gradients wouldstart to flatten prior to the entry and our estimates will not fully capture the causal effects. How-ever, Figure 3.4 suggests no pre-trend in the event study estimates, suggesting no early reaction.Moreover, we conduct two additional tests to rule out the anticipation effect.In many cities, Ofo was available on university campuses months before its entry into the entirecity (see Table 3.1). If citywide entry were anticipated due to the presence of campus bikes, housingprices would start to respond sometime between the entry to campuses and the entry to the wholecity. In Table 3.7, column (a), we show that the effect of bike sharing only appears after thecitywide entry. The change in housing price gradient between the campus entry and the citywideentry is merely 0.4 percentage points and statistically insignificant. Given this result, it is unlikelythat Ofo’s entry to campuses creates market expectations of citywide entry.53We also consider the anticipation of new subway stations. It is possible that prospective subwaystations also raise surrounding housing prices. The entry of bike sharing, therefore, may offset theprice premiums by reducing the expected commuting cost to the subway. In Table 3.7, column (b),we conduct a falsification test using apartments near planned subway stations in Beijing that arestill in the planning or construction stage and have no commuting value yet. We find that aroundplanned stations, the housing price gradients are flat and statistically indistinguishable from zeroboth before and after the entry of bike sharing. Therefore, bike sharing reduces the actual ratherthan anticipated commuting cost.3.5.3 No Compositional ChangeSince many apartments have only one observation, we cannot use apartment fixed effects to controlfor unobserved apartment characteristics. This raises the question of whether the characteristics ofapartments change systematically, especially at different distances to the subway, after the entryof bike sharing. Therefore, we estimate equation (3.1) with additional grid fixed effects. We usethe geo-coordinates of the apartments to partition the sample into 173,175 grids with the size of10 × 10 meters, each containing 2.3 apartments on average. The grid size is roughly the size of anaverage apartment, and multiple apartments within the same grid are typically on different floorsof the same building. As shown in Table 3.7, column (c), the effect of bike sharing on the pricegradient, 0.012 (s.e. 0.003), is similar to that using subway station fixed effects. The grid fixedeffects also address the concern that the spatial distribution of shared bikes is not even within cities.Alternatively, the attenuating effect of bike sharing could result from more listings (supply) ofapartments proximate to subway stations relative to distant ones. However, recall in Figure 3.2 thatthe distribution of distances to the nearest subway stations remains unchanged after the entry ofbike sharing, especially with respect to existing stations. In Section 3.5.4, we report robustness testsfocusing on apartments matched to existing subway stations or city months without the openingof new stations.3.5.4 Alternative ExplanationsContemporaneous changes in local socioeconomic conditions. In our baseline specifica-tion, the inclusion of station fixed effects and city-month fixed effects does not rule out time-varyingconfounders within cities. With 1,421 subway stations and 33 months, it is not statistically feasibleto include subway-month fixed effects and obtain significant estimates. We take three approachesto tackle this issue.First, we estimate equation (3.1) with additional fixed effects by administrative districts andmonths. There are 108 districts in the 10 cities. As such, these fixed effects control for time-varyingadministrative and policy-related factors at the district level, as well as the average number of sharedbikes in each district each month. As shown in Table 3.8, column (a), we obtain nearly identicalestimates as the main specification.54Second, we use the apartments’ geo-coordinates to partition the sample into 388 grids of 6 ×6 kilometers (similar to Table 3.7, column (c)), with 3.7 stations in each grid. Then we estimateequation (3.1) with additional grid-month fixed effects. These fixed effects are finer than district-month fixed effects and capture time-varying factors specific to each grid, including the time-varyingnumbers of shared bikes per grid. In Table 3.8, column (b), we obtain a similar estimate of theeffect of bike sharing on the subway housing price premiums. The estimate, 0.008 (s.e. 0.003),is significant but smaller than the baseline estimate. This is because apartments matched to thesame station may be divided into different grids, and thus, the price gradient is partially absorbedby the fixed effects.Third, we limit our sample to a shorter time window before and after the entry of bike sharing,which is less likely to capture contemporaneous changes in unobservables at the community level.In Table 3.8, columns (c) and (d), we limit the sample period to a one-year window (183 daysbefore and after entry) and a half-year window (90 days on each side), respectively, and find thatthe effect of bike sharing remains positive and significant. The estimates have smaller magnitudesbecause they only capture the short-run impacts, whereas our baseline estimates capture the long-run impacts.Expansion of public transit. According to Bajic (1983) and Fesselmeyer and Liu (2018), ex-panding a subway network enhances the benefit of living near an existing subway station and resultsin a steeper housing price gradient. This might countervail the effect of bike sharing and bias ourestimates. To address this concern, we estimate equation (3.1) using cities that did not have anynew subway station opening in the three months before and three months after the entry of bikesharing; we also focus on apartments listed between the last opening of new stations before theentry and the first opening after the entry. For these apartments, changes in housing prices cannotbe due to the expansion of subway networks. Table 3.8, column (e) reports estimates using thissubsample, and the coefficient of interest remains positive and statistically significant.Second, note that our sample comprises apartments within three kilometers of the nearestsubway station at the time of initial listing. Hence, the opening of new subway stations mayexpand the geographic range of our housing sample, and apartments listed before and after theentry of bike sharing may differ in geographic distribution and become less comparable. In Table3.8, column (f), we focus on apartments within three kilometers of a subway station that was inexistence by January 1, 2016, so that the geographic distribution of apartments does not changeover time as the subway network expands. The estimated effect of bike sharing remains unchanged.Third, cities may expand bus services to supplement the subway system, which mainly benefitsresidents who live farther from subway stations. As such, the housing price gradient with respectto the subway will get flatter. In contrast, we find that all cities in our sample experienced a steadydecline in bus service relative to city population and per capita GDP. In Beijing, for example, totalbus ridership dropped by 18 percent from 2015 to 2017, while its population remained unchangedand GDP per capita increased by 13.8 percent. Thus, this alternative explanation is also ruled out.55Worsened amenities near subway stations. People living too close to subway stations couldsuffer from worse amenities due to the high volume of traffic and peddlers. The situation may beexacerbated by the entry of bike sharing since many bikes are parked around the stations and mayclog the street. As such, it is possible that bike sharing flattens the housing price gradient becauseit reduces the value of apartments close to subway stations. In Table 3.8, column (g), we find thatthe effect of bike sharing on the housing price gradient beyond 500 meters of the subway remainsthe same as for the whole sample. For apartments beyond 500 meters of a subway station, changesin the housing price gradient cannot be explained by worsened amenities near the station.Easier access to shopping malls. Since some subway stations are built next to shopping malls,people may ride shared bikes to shop rather than to transit to a subway. To address this competingexplanation, we estimate equation (3.1) excluding apartments whose nearest subway station iswithin 200 meters of a shopping mall. As Table 3.8, column (h) shows, the effect of bike sharingremains unchanged, as visiting or shopping at a mall is less frequent than daily commuting towork. Similarly, we show that the change in housing price gradients is not explained by peopleusing shared bikes to access parks.Reduced viewing cost. Table 3.4, column (b) shows that the entry of bike sharing increasesthe frequency of visits to distant apartments relative to proximate ones. We interpret this asthe greater interest of potential buyers in distant apartments, which enjoy improved access to thesubway. However, it could also be that bike sharing reduces the cost of viewing: Potential buyersmay find it easier to visit apartments distant from subway stations or have time to view moreapartments in a single trip.To test this explanation, we collect more detailed viewing visit data on apartments in Beijingwith the time and visitor identifier of each visit. After bike sharing is introduced, the averagenumber of visits per day per viewer declines from 1.65 to 1.52. For each viewer, the averagedistance from a subway to apartments visited experiences no significant change before and afterentry (difference equals 0.006 kilometers, s.e. 0.006). Therefore, to rationalize our finding in Table3.3, the only possible explanation is that bike sharing attracts more buyers interested in distantapartments.Regulations on the housing market. During the data period, the Chinese government im-plemented three waves of housing market regulations on March 25, 2016, September 30, 2016, andMarch 20, 2017, respectively. The regulations aimed to curb the growth of housing sales prices byraising the costs of purchasing properties. This could increase the demand for and price of cheaperapartments, e.g., those distant from subway stations, and thus narrow the price gap between prox-imate and distant apartments without bike sharing (Ouazad and Rancie`re, 2019).To assess whether apartments close to vis-a-vis distant from subway stations are deferentiallyimpacted by the regulations, we examine the effect of bike sharing on rental prices. As we show inFigure B.2, each wave of regulation corresponds to a price hike in the resale housing prices but does56not affect the trend in rental prices. This not only justifies the purpose of the regulations but alsoindicates that in China, the property resale and rental markets are largely separated. If the changein the resale price gradient is solely due to the regulations, we should find no structural change inrental price upon the entry of bike sharing. Therefore, to rule out this competing explanation, weestimate the effect of bike sharing on rental prices. Using a sample of rental apartments in the 10cities, we estimate equation (3.1) with Pit being the monthly rent per apartment. The resultingeffect follows the same pattern as that on sales prices: The rent gradient flattens significantly by1.0 percentage points (s.e. 0.004).3.6 ConclusionAs a green, convenient, and affordable complement to urban transportation, dockless bike sharinghelps resolve the last-mile problem by increasing the accessibility of subway service to people wholive farther from the subway. Consequently, it increases the attractiveness of distant apartmentsand narrows the price gap between apartments at different distances to the subway. Using theentry of dockless bike sharing in 10 major Chinese cities as a quasi-experiment, we find that bikesharing flattens the housing price gradient around subway stations by 29 percent, which is equivalentto an urban resident’s yearly disposable income. The effect is heterogeneous across apartments,communities, and cities, and is more salient for larger, higher-floor apartments and apartmentswith better access to the subway. Further analysis of the transaction process reveals that sellersand buyers both react to the entry of dockless bike sharing, which shifts the housing market to anew equilibrium with a flatter price gradient. Tests of parallel pre-trends and the exogeneity ofentry, a two-step estimation, and various robustness checks all validate the causal effect of docklessbike sharing on the subway housing price premiums.We contribute to the literature on the sharing economy by demonstrating the causal impactof dockless bike sharing on reducing the subway housing price premiums and narrowing the pricegap between apartments at different distances to subway stations, exploring the mechanisms, andinferring the reduction in a household’s commuting cost. We also contribute to the urban economicliterature by documenting how improved transportation affects livability. It is noteworthy thatdockless bike sharing is a new means of transportation that is powered by modern information andcommunications technology (ICT). We provide an example of how ICT transforms mobility in away that may lead to significant impacts on other important markets.Our findings have significant implications for bike sharing companies, property developers, pol-icymakers, and urban commuters. In most markets, property developers and dockless bike sharingcompanies are two separate entities. Our findings show that dockless bike sharing substantiallyreduces commuting costs and increases the relative attractiveness of distant apartments, but dock-less bike sharing companies do not fully capture such benefits. One implication might be thatproperty developers could subsidize dockless bike sharing, or dockless bike sharing companies couldpartner with developers to provide better services. For example, in Singapore, nearly all private57condominiums provide their residents with free or subsidized commuting services between homeand the nearest subway station, which are often operated by third-party transport companies.Currently, all dockless shared bikes are provided by private companies. Given that docklessbike sharing offers an effective solution to the last-mile problem and reduces commuting costs,governments and city municipalities may consider integrating dockless bike sharing into urbantransport planning, similar to how they provide stationed public bikes. In this way, they maybetter harness the benefits and reduce the negative effects of dockless bike sharing. In manycities, such as Beijing, Wuhan, and Hangzhou, governments and bike sharing companies have beenexperimenting with such joint arrangements.Regarding venues for future research, our study focuses on one specific benefit of bike shar-ing: the impact on the subway housing price premium due to its effective solution to the last-mileproblem. Dockless bike sharing has other benefits, such as its impacts on health, pollution, traf-fic congestion, and traffic safety, and costs such as haphazard parking, clogged streets, and bikevandalism. A comprehensive study is needed to fully assess the benefits and costs of dockless bikesharing; the government can then decide how to regulate dockless bike sharing.58Figures and TablesFigure 3.1: Baidu Search Index for “Bike Sharing”(a) Beijing010002000300040001/1/2016 7/1/2016 1/1/2017 7/1/2017 1/1/2018Date(b) Shanghai010002000300040001/1/2016 7/1/2016 1/1/2017 7/1/2017 1/1/2018Date(c) Chengdu010002000300040001/1/2016 7/1/2016 1/1/2017 7/1/2017 1/1/2018Date(d) Chongqing010002000300040001/1/2016 7/1/2016 1/1/2017 7/1/2017 1/1/2018Date(e) Dalian010002000300040001/1/2016 7/1/2016 1/1/2017 7/1/2017 1/1/2018Date(f) Hangzhou010002000300040001/1/2016 7/1/2016 1/1/2017 7/1/2017 1/1/2018Date(g) Nanjing010002000300040001/1/2016 7/1/2016 1/1/2017 7/1/2017 1/1/2018Date(h) Shenzhen010002000300040001/1/2016 7/1/2016 1/1/2017 7/1/2017 1/1/2018Date(i) Tianjin010002000300040001/1/2016 7/1/2016 1/1/2017 7/1/2017 1/1/2018Date(j) Wuhan010002000300040001/1/2016 7/1/2016 1/1/2017 7/1/2017 1/1/2018DateNotes: In each plot, the dark blue line depicts the Baidu search index for “bike sharing” per day from January 1,2016 to March 12, 2018 by cities. The red solid and red dashed lines represent the entry dates of Ofo and Mobike,respectively.59Figure 3.2: Distribution of Apartments by Distance to the Nearest Subway Station(a) Stations upon listing(b) Stations before July 1, 2015Notes: The sample comprises resale apartments in 10 Chinese cities, initially listed between July 1, 2015 and December31, 2017, and within 7 km of a subway station. Panel (a) plots the distribution of distance from each apartment tothe nearest subway station at the time of listing. Panel (b) plots the distribution of distance to the nearest subwaystation open before July 1, 2015. The blue solid line and the red dashed line represent apartments before and afterthe entry of bike sharing, respectively.60Figure 3.3: Estimates by Distance Segment0.02.04.06.08.1Estimated price premiums0 .5 1 1.5 2 2.5 3Distance to the subway (km)Before entryAfter entryNotes: The figure depicts the estimated subway housing price premiums by distance segments (0-0.5 km, 0.5-1 km,1-1.5 km, and 1.5-2 km) relative to the furthest segment (2-3 km) from equation (3.3). The sample comprises resaleapartments in 10 Chinese cities, initially listed between July 1, 2015 and December 31, 2017, and within 3 km of asubway station. The estimates control for apartment characteristics, apartment density, indicators of initial and lastprices, subway station fixed effects, and city-month fixed effects. The blue and red dots represent estimates beforeand after the entry and bike sharing, respectively, and the bars represent 95 percent confidence intervals.Figure 3.4: Event Study Estimates-.06-.05-.04-.03-.02Estimated price gradient-6 -4 -2 0 2 4 6Month relative to entryNotes: The figure depicts estimated housing price gradients by months relative to the entry month of bike sharingfrom equation (3.1). The sample comprises resale apartments in 10 Chinese cities, initially listed between July 1, 2015and December 31, 2017, and within 3 km of a subway station. The estimates control for apartment characteristics,apartment density, indicators of initial and last prices, subway station fixed effects, and city-month fixed effects. Thedots represent coefficient estimates and the bars represent 95 percent confidence intervals. The vertical line indicatesthe entry time of bike sharing, and the horizontal line indicates the point estimate of the price gradient in the monthbefore entry.61Table 3.1: City Characteristics(a) (b)City Bike sharing entry date Subway stationsOfo campus Ofo Mobike Jul-15/Dec-17Beijing Jun 6, 2015 Oct 10, 2016 Sep 1, 2016 265/288Chengdu Aug 22, 2016 Dec 16, 2016 Nov 16, 2016 48/100Chongqing Jan, 10 2017 Jan 10, 2017 May 1, 2017 108/119Dalian Jun 26, 2017 Jun 26, 2017 Apr 16, 2017 41/65Hangzhou Sep 12, 2016 Feb 20, 2017 Apr 16, 2017 44/56Nanjing Aug 22, 2016 Jan 8, 2017 Jan, 12 2017 113/128Shanghai May 9, 2016 Oct 10, 2016 Apr 22, 2016 279/294Shenzhen Sep 11, 2016 Dec 9, 2016 Oct 16, 2016 118/167Tianjin Aug 27, 2016 Jan 13, 2017 Feb 12, 2017 84/105Wuhan Apr 18, 2016 Jan 6, 2017 Dec 29, 2016 75/123(c) (d) (e) (f)City Apartments Average price Average size Income per capita(CNY/m2) (m2) (CNY)Beijing 62,689 58,668 91.81 52,350Chengdu 53,294 12,233 95.35 35,902Chongqing 35,650 9,242 97.3 29,610Dalian 32,457 11,054 82.41 38,050Hangzhou 19,562 27,251 93.02 52,185Nanjing 34,073 26,247 89.02 49,997Shanghai 59,031 50,880 87.17 55,358Shenzhen 37,816 54,255 86.81 48,695Tianjin 29,969 26,833 77.28 34,074Wuhan 35,299 15,716 102.2 39,737Notes: Column (a): entry dates of Ofo (campus only), Ofo (citywide) and Mobike (citywide); the first and thirdcolumns are from Cao et al. (2021) and the second column is collected from the Internet by authors; In subsequenttables, the entry of bike sharing is defined as the earlier citywide entry of Ofo or Mobike (in bold). Column (b):number of subway stations by July 2015 and December 2017, calculated by authors; Columns (c)-(e): number ofapartments, average price per m2and average apartment size, calculated from the sample; Column (f): income percapita in 2016, collected from China City Statistical Yearbook 2017, Beijing: China Statistics Press, 2018.62Table 3.2: Summary Statistics(a) (b) (c) (d)Variables Mean S.D. Min. Max.Price (’000 CNY/m2) 31.54 24.23 4.440 147.9Price adjustment (%) 7.440 5.570 -15.38 23.75Size (m2) 90.50 42.71 20 300Floor number 8.991 7.827 -8 50Building age (year) 13.82 7.879 0 68Number of bedrooms 2.205 0.851 1 4School district 0.505 0.500 0 1Bike sharing 0.452 0.498 0 1Ofo’s entry 0.411 0.492 0 1Mobike’s entry 0.437 0.496 0 1Baidu search index 350.0 508.0 0 3,471Geodesic distance to subway (km) 1.083 0.695 0.004 3.000Walking distance to subway (km) 1.618 0.985 0.000 5.200Interchange station 0.091 0.287 0 1Observations 617,271Apartments 399,840Notes: Sample comprises resale apartments in 10 Chinese cities (see Table 3.1), initially listed between July 1, 2015and December 31, 2017, and within 3 km of a subway station.Table 3.3: Bike Sharing and the Subway Housing Price Premiums(a) (b) (c) (d) (e)Variables DID Ofo’s Mobike’s Baidu Two-stepentry entry index estimatorDistance to subway -0.042*** -0.042*** -0.042*** -0.040***(0.003) (0.003) (0.003) (0.003)Distance × bike sharing 0.012*** 0.013*** 0.011*** 0.010***(0.003) (0.003) (0.003) (0.003)Bike sharing 0.014**(0.005)Observations 617,271 617,271 617,271 617,271 329Apartments 399,840 399,840 399,840 399,840Subway stations 1,422 1,422 1,422 1,422Adjusted R2 0.91 0.91 0.91 0.91 0.60Notes: Columns (a)–(d) report estimates of equation (3.1) with apartment price per m2(log) as the dependent variable;the sample comprises resale apartments in 10 Chinese cities, initially listed between July 1, 2015 and December 31,2017, and within 3 km of a subway station; all estimates control for apartment characteristics, apartment density,indicators of initial and last prices, subway station fixed effects, and city-month fixed effects; robust standard errorsclustered by subway stations in parentheses. Column (e) reports estimates of equation (3.2b) with estimated pricegradient per city-month as the dependent variable; estimates control for city fixed effects; robust standard errorsclustered by cities. (* p < 0.1, ** p < 0.05, *** p < 0.01)63Table 3.4: Mechanism(a) (b) (c) (d) (e)Variables Number of Initial Last Transaction Pricevisits (log) price (log) price (log) price (log) adjustmentDistance to subway -0.018*** -0.043*** -0.043*** -0.048*** -0.031(0.005) (0.003) (0.003) (0.004) (0.027)Distance × bike sharing 0.016*** 0.015*** 0.015*** 0.013*** 0.003(0.006) (0.003) (0.003) (0.005) (0.039)Observations 399,840 399,840 399,838 42,697 217,431Apartments 399,840 399,840 399,838 42,697 119,589Subway stations 1,420 1,420 1,422 1,185 1,387Adjusted R2 0.36 0.91 0.91 0.93 0.16Notes: Columns (a)–(e) report estimates of equation (3.1) with dependent variables in column titles (except column(a) where the dependent variable is log(number of visits+1)). The sample comprises resale apartments in 10 Chinesecities, initially listed between July 1, 2015 and December 31, 2017, and within 3 km of a subway station (exceptcolumn (d), which limits to sold apartments). All estimates control for apartment characteristics, apartment density,indicators of initial and last prices, subway station fixed effects, and city-month fixed effects. Robust standard errorsclustered by subway stations in parentheses. (* p < 0.1, ** p < 0.05, *** p < 0.01)Table 3.5: Effect Heterogeneity(a) (b) (c) (d) (e)Variables Size Floor School Interchange Stationsdistrict station within 3 kmDistance to subway -0.042*** -0.042*** -0.042*** -0.042*** -0.043***(0.003) (0.003) (0.003) (0.003) (0.003)Distance × bike sharing 0.011*** 0.013*** 0.012*** 0.012*** 0.022***(0.003) (0.003) (0.003) (0.003) (0.003)Distance × bike sharing 0.007*** 0.004*** 0.001 0.018*** 0.009***× moderator (0.001) (0.001) (0.003) (0.005) (0.002)Observations 617,271 617,271 617,271 617,271 617,271Apartments 399,840 399,840 399,840 399,840 399,840Subway stations 1,422 1,422 1,422 1,422 1,422Adjusted R2 0.91 0.91 0.91 0.91 0.91Notes: Columns (a)–(e) report estimates of equation (3.1) with apartment price per m2(log) as the dependent variable.The sample comprises resale apartments in 10 Chinese cities, initially listed between July 1, 2015 and December 31,2017, and within 3 km of a subway station. All estimates control for apartment characteristics, apartment density,indicators of initial and last prices, subway station fixed effects, and city-month fixed effects. Columns (a)–(b)include three-way interaction with apartment size and floor, respectively, both standardized to zero means and unitvariance. Columns (c)–(d) include three-way interaction with indicators of school districts and apartments matchedto interchange stations, respectively. Column (e) includes three-way interaction with the number of subway stationswithin 3 km of the apartment. Robust standard errors clustered by subway stations in parentheses. (* p < 0.1, **p < 0.05, *** p < 0.01)64Table 3.6: Robustness(a) (b) (c) (d) (e) (f)Variables Within Within Within Walking Excl. age Cluster2 km 4 km 5 km distance as control by citiesDistance to subway -0.041*** -0.040*** -0.039*** -0.026*** -0.037*** -0.041***(0.003) (0.003) (0.003) (0.002) (0.003) (0.004)Distance × bike sharing 0.014*** 0.008*** 0.007*** 0.009*** 0.012*** 0.011***(0.003) (0.003) (0.002) (0.002) (0.003) (0.004)Observations 541,482 655,719 676,231 593,429 617,271 617,271Apartments 349,911 424,407 437,418 385,356 399,840 399,840Subway stations 1,417 1,424 1,425 1,422 1,421 1,422Adjusted R2 0.91 0.91 0.91 0.91 0.91 0.91Notes: Columns (a)–(f) report estimates of equation (3.1) with apartment price per m2(log) as the dependent variable.The sample comprises resale apartments in 10 Chinese cities, initially listed between July 1, 2015 and December 31,2017. Columns (a)–(c) limit to apartments within 2 km, 4 km, and 5 km of a subway station, respectively; columns(d)–(f) limit to apartments within 3 km of a subway station. Column (d) measures the distance to the subway bythe walking distance computed from Baidu Maps. All estimates control for apartment characteristics, apartmentdensity, indicators of initial and last prices, subway station fixed effects, and city-month fixed effects (except column(e) without control for building age). Robust standard errors clustered by subway stations (except column (f) withbootstrap standard errors clustered by cities) in parentheses. (* p < 0.1, ** p < 0.05, *** p < 0.01)Table 3.7: Validation(a) (b) (c)Variables Ofo campus Planned stations Grid fixed effectsDistance to subway -0.043*** -0.003 0.006(0.004) (0.014) (0.004)Distance × bike sharing 0.010*** 0.006 0.012***(0.003) (0.006) (0.003)Distance × Ofo campus 0.004(0.004)Observations 617,271 69,930 617,271Apartments 399,840 41,699 385,356Subway stations 1,422 75 1,421Adjusted R2 0.91 0.76 0.98Notes: Columns (a)–(c) report estimates of equation (3.1) with apartment price per m2(log) as the dependent variable.The sample comprises resale apartments in 10 Chinese cities, initially listed between July 1, 2015 and December 31,2017, and within 3 km of a subway station. Column (a) additionally controls Ofo’s entry to campuses and itsinteraction with distance to the subway. Column (b) limits to apartments in Beijing, within 3 km of the nearestplanned subway station. Column (c) additionally controls fixed effects by geo-coordinate grids of 10 m × 10 m. Allestimates control for apartment characteristics, apartment density, indicators of initial and last prices, subway stationfixed effects, and city-month fixed effects. Robust standard errors clustered by subway stations in parentheses. (*p < 0.1, ** p < 0.05, *** p < 0.01)65Table 3.8: Alternative Explanations(a) (b) (c) (d)Variables District-level 6 km × 6 km One year Half-yeartrends grid-level trends time window time windowDistance to subway -0.040*** -0.041*** -0.043*** -0.045***(0.003) (0.004) (0.003) (0.004)Distance × bike sharing 0.013*** 0.008*** 0.008*** 0.006**(0.002) (0.003) (0.003) (0.003)Observations 617,271 617,271 240,904 112,834Apartments 399,840 399,840 162,887 79,269Subway stations 1,421 1,421 1,380 1,341Adjusted R2 0.92 0.92 0.90 0.91(e) (f) (g) (h)Variables Periods w/o Excl. new Excl. nearest Excl. mallsnew stations stations 500 mDistance to subway -0.036*** -0.041*** -0.045*** -0.041***(0.007) (0.003) (0.004) (0.003)Distance × bike sharing 0.022*** 0.015*** 0.012*** 0.011***(0.006) (0.003) (0.003) (0.003)Observations 114,875 409,100 480,268 589,826Apartments 72,887 292,856 311,102 382,641Subway stations 511 1,368 1,419 1,422Adjusted R2 0.85 0.91 0.91 0.91Notes: Columns (a)–(h) report estimates of equation (3.1) with apartment price per m2(log) as the dependent variable.The sample comprises resale apartments in 10 Chinese cities, initially listed between July 1, 2015 and December 31,2017, and within 3 km of a subway station. All estimates control for apartment characteristics, apartment density,indicators of initial and last prices, subway station fixed effects, and city-month fixed effects. Column (a) additionallycontrols for district-month fixed effects. Column (b) divides the sample into 388 grids of size 6 km × 6 km and controlsfor grid-month fixed effects. Columns (c) and (d) limit to apartments listed 183 and 90 days, respectively, beforeand after the entry of bike sharing. Column (e) limits to city-months with no subway station open 3 months beforeand after the entry of bike sharing (Beijing, Dec 26, 2015 to Dec 21, 2016; Hangzhou, Nov 24, 2015 to Jul 3, 2017;Nanjing, Jul 1, 2015 to Jan 8, 2017; Wuhan, Dec 28, 2015 to Dec 28, 2016). Column (f) excludes apartments whosenearest station opened in or after 2016. Column (g) excludes apartments within 500 meters of the nearest station.Column (h) excludes apartments whose nearest subway station is within 200 meters of a shopping mall. Robuststandard errors clustered by subway stations in parentheses. (* p < 0.1, ** p < 0.05, *** p < 0.01)66Chapter 4Corporate Tax Cuts and WorkerEarnings: Evidence from SmallBusinesses4.1 IntroductionThis chapter investigates how corporate tax cuts stimulate economic growth and worker earnings,a central question in fiscal policies. This is a recurring topic in policy debates with theoreticallyopposing views. On the one hand, Harberger (1962) predicts that firm owners bear the entirecorporate tax burden in a closed economy with limited capital mobility. On the other hand, sub-sequent studies emphasize the importance of international capital mobility and argue that workersalso share the tax burden. While extensive literature has examined the tax effects on investmentand employment, surprisingly little evidence exists about how worker-level outcomes respond tochanges in corporate tax rates.Evaluating the tax effects on worker earnings is challenging, partly because it is difficult to findlarge and exogenous variations in tax rates across firms and workers. In most settings, corporateincome tax rates depend on firm sizes or profits, making it difficult to find a control group of firmsand workers unaffected by tax rate changes and to isolate the tax effects from business cycles.24Without employee-level data, it is also difficult to distinguish whether changes in firm-level averagepayrolls are driven by changes in incumbent workers’ earnings or changing worker compositions.To accurately measure corporate tax incidence on workers, it is important to exploit a credibleempirical design and employee-level data to track the same workers over time.To assess the tax effects on both worker-level and firm-level outcomes, we combine a quasi-experimental tax reform with administrative employee-employer data from tax records in Canada.In 2014, the province of Quebec implemented a tax cut for domestic small firms in the manufacturingand processing (M&P) sector, reducing their corporate income tax rate from 19 percent to 15percent. Using a triple differences design, we first compare the treated firms with domestic smallfirms in non-M&P sectors in Quebec before and after the reform; then to isolate any sector-specificshocks that may coincide with the reform, we make the same comparison for domestic small firms24Prior studies have exploited variations cross industries (Zwick and Mahon, 2017; Ohrn, 2018; Curtis et al., 2022),states or municipalities (Sua´rez Serrato and Zidar, 2016; Fuest et al., 2018), and business types (Giroud and Rauh,2019; Harju et al., 2022; Kennedy et al., 2022).67in British Columbia and Ontario, two other major provinces with no change in small business taxrates. This framework allows us to identify the causal effects net of any sector- or province-specificunobservables.For small M&P firms in Quebec, we show that they increase employment, average payrolls, andtangible assets, respectively, by 1.7 percent, 2.3 percent, and 3.2 percent after the reform. Treatedfirms also experience increased sales, after-tax profits, and productivity. At the worker level, theaverage annual earnings increase by 1.3 percent for incumbent workers at treated firms. Usingownership data, we also estimate that workers who own shares at their working firms bear about40 percent of the corporate tax burden. Non-owner workers bear about one-third of the corporatetax burden, which aligns with the estimate of Sua´rez Serrato and Zidar (2016). Combining bothtypes of workers, the tax incidence on workers (with or without ownership) is about three-quarters,larger than the prior estimates. Focusing on medium to large firms in the U.S., Kennedy et al.(2022) find that corporate tax incidence falls mostly on workers in the top ten percent of thewithin-firm income distribution. In contrast, we find a high incidence on workers below the top tenpercent in the within-firm earnings distribution among small businesses.We find that the increased capital investment, especially in productive assets such as computers,partly explains the rise in productivity after the tax cut. As these firms are all small businesses,they typically face cash constraints and high borrowing costs, which prevent them from reachingthe optimal level of investment. We estimate that treated firms finance 38 percent of the increasedoperating expenditures through debt, and the marginal cost of investment roughly equals themarginal return without the tax reduction. Accounting for the tax benefits, however, the marginalreturn on the additional spending almost doubles, making it worthwhile to increase investment.Therefore, we conclude that cash constraints and high borrowing costs explain why treated firmsin our setting did not invest before the tax cut, even if the additional investment would have ledthem to higher profitability and productivity.To further associate the increase in worker earnings with increased productivity and profitability,we test whether firms and workers in high-growth industries respond more strongly to the tax cutthan those in low-growth industries. Since firms in high-growth industries tend to have higher netpresent value projects, these firms have a stronger incentive to invest and expand. We find thatafter the reform, treated firms in high-growth industries invest more in capital, hire more workers,and experience larger increases in after-tax profits and productivity. Furthermore, the responsesin worker earnings are concentrated in high-growth industries, suggesting that the wage increaseis closely tied to increased productivity and profits in our setting. Following Kline et al. (2019),we estimate that an average firm passes 35 percent of the extra surplus generated from the taxcut onto workers. In addition, we examine other possible mechanisms, including relaxing the cashconstraints, lowering the cost of capital, firms’ labor market power, and rent-sharing (Risch, 2024).We conduct several robustness tests to strengthen the validity of our results. Besides the tripledifferences design, we present difference-in-differences (DID) estimates separately for Quebec andother provinces, comparing small M&P firms and workers against small non-M&P firms and workers68before and after the reform. This confirms our results are not driven by upward trends specific tothe M&P sector or Quebec. To account for industry- or location-specific shocks coinciding withthe reform, we additionally control for fixed effects by industry and year and by commuting zoneand year. Moreover, our results are robust to alternative sample restrictions, worker reallocationacross firms, and bunching at the eligibility threshold. Finally, we conduct placebo tests usingnon-domestic firms ineligible for the tax cut.4.1.1 Related LiteratureThis chapter’s contributions to the literature are three-fold. First, our paper contributes to thegrowing literature on how corporate taxes affect worker earnings. While earlier studies exploitcompany- or state-level variation in corporate tax rates to assess the tax effects on firm-levelaverage payrolls (Arulampalam et al., 2012; Sua´rez Serrato and Zidar, 2016), few studies (Fuest etal., 2018) leverage employee-level data to evaluate the corporate tax impacts on wages or controlfor changes in worker compositions.A unique contribution of our paper is that we exploit detailed firm outcomes from tax records tomeasure tax incidence and explore mechanisms behind the tax effect. On one hand, the data allowsus to measure tax incidence on workers and firm owners more accurately without making furtherassumptions on how firms’ after-tax profits change after a tax cut. Using ownership data, we canseparately estimate the tax incidence on workers with or without ownership. This is particularlyimportant for small businesses where workers’ ownership rates are high. Without the ownershipinformation, the incidence on workers could be underestimated as we cannot distinguish workerswith ownership from other firm owners. Once we incorporate owner-workers, our estimate of taxincidence on workers almost doubles.On the other hand, the combined firm- and worker-level data helps us link worker responseswith firm responses to a tax cut and investigate potential mechanisms behind our findings. We findthat firms treated by the tax cut increase investment in both labor and capital, leading to higherproductivity and after-tax profits. In particular, the responses in worker earnings and investmentare concentrated in high-growth industries where we see most of the gains in productivity andprofitability, suggesting that the wage increase is closely tied to enhanced productivity after thetax cut. Moreover, the combined individual and corporate tax records allow us to estimate thepass-through of extra surpluses on workers, confirming significant profit-sharing between workersand firm owners (Fuest et al., 2018).Second, our paper contributes to the literature on how corporate taxes affect small businesses.While governments in developed and developing countries spend a significant portion of their bud-gets on providing tax incentives for small businesses, evidence of how tax reductions affect smallfirms’ growth and worker earnings is scant. Studying the tax effects on small firms is importantnot only because small businesses constitute a large component of the economy (60 percent of salesand 70 percent of employment in Canada), but also because they are often cash-constrained andhave higher ownership rates by workers. This unique feature could result in different responses to69tax cuts from large firms. Thus, understanding how small firms respond to tax incentives is crucialfor designing an effective corporate tax system.To our knowledge, we are the first to identify the effects of tax cuts targeting small businesses onboth firm-level and worker-level outcomes. Contrary to Harju et al. (2022) who find an increase ininvestment and sales among cash-constrained firms, we find that most responses are concentrated inhigh-growth industries in our setting. Given that both studies examine small businesses, differencesin institutional settings, other firm characteristics, or the nature of the reforms may all drive thedifferences. Moreover, we perform a benefit-cost analysis for the tax cut using our quantitativeestimates. Critics of the tax cut emphasize the costs in terms of increased opportunities for taxavoidance by high-income professionals (Smart, 2021) and misallocation of resources from large,productive businesses to small, inefficient ones. However, we argue that the benefits are larger thanpreviously estimated when accounting for the growth of firms, the increased welfare of workers, andhigher personal income taxes resulting from higher salaries.Third, this paper complements an extensive literature showing the effects of fiscal policies onreal outcomes. For example, temporary reforms such as accelerated depreciation are shown tostimulate aggregate spending (House and Shapiro, 2008; Zwick and Mahon, 2017). Furthermore,our results are consistent with the growing empirical literature that documents how investmentrespond to corporate tax incentives (Ohrn, 2018; Chen et al., 2023; Giroud and Rauh, 2019; Liuand Mao, 2019; Maffini et al., 2019; Curtis et al., 2022) and payout taxes (Poterba and Summers,1983; Moon, 2022), and large innovation responses to personal income taxes (Akcigit et al., 2022).The rest of this chapter is organized as follows. Section 4.2 provides background informationon Canadian corporate income taxes and introduces our empirical design. Section 4.3 describesthe data. Sections 4.4–4.5 shows the main results and explores potential mechanisms. Section 4.6discusses the welfare implications of our findings. Section 4.7 concludes.4.2 Institutional Background and Empirical Strategy4.2.1 Corporate Income Taxes in CanadaCorporate income taxes in Canada are levied at both federal and provincial levels. In Appendix C.1,Table C.1 reports the federal and provincial corporate income tax rates from 2009 to 2017. In 2011,the baseline federal tax rate was 16.5 percent after a general tax reduction and was reduced to 15percent in 2012–2017. Meanwhile, domestic small firms are eligible for a small business deduction(SBD), which lowers their corporate income tax rate by 4 percentage points for the first 500,000CAD of their taxable income. To qualify for the SBD, the firms must be Canadian-ControlledPrivate Corporations (CCPC) with taxable capital below 10 million CAD.25 Firms with taxablecapital between 10 million and 15 million CAD also quality for the SBD, but the eligible taxableincome is reduced by ten cents for every dollar increase in taxable capital. As such, the benefits25Taxable capital includes mainly capital stock and retained earnings net of investment allowance. The precisedefinition is given in https://www.canada.ca/content/dam/cra-arc/formspubs/pbg/t2sch33/t2sch33-15e.pdf.70completely phase out when taxable capital reaches 15 million CAD (see Appendix Figure C.1, panel(a)). This phase-out schedule also applies to the provincial tax rates.Each province in Canada also sets its own corporate income tax rates. In Ontario, the largestprovince of Canada, the general tax rate was 11.5 percent from 2011 to 2017, whereas the tax ratefor small businesses was 4.5 percent. During this period, British Columbia set the general tax rateat 10–11 percent and the small business tax rate at 2–2.5 percent. In Quebec, the general rate was11.8–11.9.In 2014, the Quebec government announced and implemented a tax rate reduction for smallbusinesses in the M&P sector. The reform lowered the tax rate from eight percent in 2011–2013 tosix percent in 2014, and to four percent after 2015. Meanwhile, the tax rate for small businessesin non-M&P sectors remained unchanged. Figure 4.1 compares the corporate income tax rates forsmall businesses across provinces and sectors. The tax cut in Quebec reduces the tax rate for M&Psmall businesses by one-half within two years, which is economically significant compared with taxrates in Ontario and British Columbia. In what follows, we describe how to use the Quebec reformto identify its effect on firms and workers.Besides the tax cut, three additional tax benefits specific to small M&P firms were introducedin Quebec in or around 2014: (i) additional tax deductions for transportation costs for firms locatedfar away from major urban centers, (ii) refundable tax credits for investment in buildings, and (iii)refundable tax credits for integrating information technologies in the business process. In Section4.5.2, we confirm that our findings are unlikely driven by these extraneous tax benefits.4.2.2 Identifying the Tax Effects on Firm OutcomesWe exploit a triple differences design to identify the effects of the Quebec tax cut on firm-leveloutcomes. First, we compare responses to the tax cut between M&P and non-M&P firms withinthe province of Quebec; second, we make the same comparison for firms in British Columbia andOntario and contrast the results with that in Quebec. Since firms in non-M&P sectors in Quebecand those in British Columbia or Ontario experienced no change in small business tax rates from2011 to 2017, the last two comparisons partial out any sector- or province-specific shocks that mayhave coincided with the reform. For simplicity, we interpret our triple differences as comparingtreated firms and control firms before and after the reform, where “treated firms” refer to smallbusinesses in the M&P sector in Quebec that were impacted by the tax cut, and “control firms”refer to small businesses in non-M&P sectors, British Columbia, or Ontario that experienced nochange in tax rates.Based on this idea, we estimate the following regression model:Yjt = θ · Postt ·MPj ·QCj + β · Postt ·MPj + γ · Postt ·QCj + αj + αt + ujt, (4.1)where Yjt is the outcome of interest for firm j in year t; Postt indicates years after 2014; MPj is anindicator for firms in the M&P sector; and QCj is an indicator for firms in Quebec. αj and ϕt are71firm fixed effects and year fixed effects, respectively. We cluster standard errors at the firm level.26We also run an event study model:Yjt =2017∑τ=2011θτ ·1{t=τ}·MPj ·QCj+2017∑τ=2011βτ ·1{t=τ}·MPj+2017∑τ=2011γτ ·1{t=τ}·QCj+αj+ϕt+ujt, (4.2)where each coefficient θτ measures the difference in Yjt between treated and control firms in yearτ . Coefficients in 2013, i.e., the year before the reform, are normalized to zero. Other variables aredefined as in equation (4.1). Section 4.4 reports estimates from both equations.The main identifying assumption of our design is that the outcomes of treated and control firmswould have evolved similarly in the absence of the policy change. A key threat to this design is thattime-varying shocks may coincide with the reform and potentially confound our estimates. Thetriple differences would absorb any sector- or province-specific shocks, and we present three piecesof evidence that this threat is minimal. First, key outcomes of treated and control firms exhibitparallel trends for multiple years prior to the reform. Second, we rule out industry-specific orlocation-specific shocks that may coincide with the reform by controlling for industry-by-year fixedeffects and commuting zone-by-year fixed effects. These controls would absorb shocks at finer levelsthan sectors and provinces. Third, we conduct placebo tests using non-CCPCs that are ineligiblefor the SBD and unaffected by the reform in 2014. We fail to reject the null hypothesis that non-CCPCs in the M&P sector in Quebec exhibit no difference in their outcomes as non-CCPCs innon-M&P sectors, British Columbia, or Ontario (see Appendix C.3).4.2.3 Identifying the Tax Effects on Worker OutcomesAnalogously, we estimate the effects of the tax cut on worker-level outcomes using the same tripledifferences design:Yijt = θ · Postt ·MPij ·QCij + β · Postt ·MPij + γ · Postt ·QCij + αi + ϕt + uijt, (4.3)where Yijt is the outcome of worker i at firm j in year t; MPij and QCij indicate worker i at afirm j in the M&P sector and in the province of Quebec, respectively; Postt indicates year t after2014. Again, αi are worker fixed effects and ϕt are year fixed effects. Standard errors are two-wayclustered at both firm and worker levels.The corresponding event study design is given byYijt =2017∑τ=2011θτ · 1{t=τ} ·MPij ·QCij +2017∑τ=2011βτ · 1{t=τ} ·MPij +2017∑τ=2011γτ · 1{t=τ} ·QCij+ αi + ϕt + uijt.(4.4)26In Appendix B.3, we show that our main results are robust to clustering standard errors at the industry bycommuting zone level.72Identifying the effects on worker-level outcomes is more complicated because workers may movefrom treated to control firms and vice versa. To address the endogenous mobility of workers, wefollow the mass layoff literature (Jacobson et al., 1993) and focus on workers at treated or controlfirms with full-time job tenure for at least three years (2011–2013) before the reform. As such, wecan identify treated and control workers by whether they have worked in a treated or control firmprior to the reform. While we do not restrict worker mobility after the reform, we find quantitativelysimilar estimates focusing on workers who stay at the same firm after 2014. We also show thatworker mobility between treated and control firms is limited in scale, and adjusting for workermobility has minimal impacts on our findings. Section 4.3 discusses how we construct the workersample in greater detail.4.3 DataFor empirical analysis, we use the Canadian Employer Employee Dynamics Database, a matchedemployee-employer data set that covers the universe of workers and firms in Canada from 2011 to2017.27 The data draws information from individuals’ T1 and corporations’ T2 tax return records,merged with job-level information using T4 employee tax records and Record of Employment data,and firm-level information from the National Accounts Longitudinal Micro-data File.284.3.1 Firm DataFor the firm-level analysis, we impose the following sample restrictions. First, we focus on CCPCsthat account for roughly 98 percent of all firms in our data. Non-CCPCs are used only as a placebogroup in our robustness check. Second, we focus on firms with total assets below 10 million CADand, therefore, qualify for small business deductions. While firms are legally required to reporttheir taxable capital if the latter is above 10 million CAD, only about one percent of firms reportedtaxable capital above 10 million CAD in our sample. As such, we use total assets as a proxy todefine small firms. It is worth noting that total assets are larger than taxable capital, so we areunlikely to include ineligible firms in our sample. On the contrary, Figure C.1, panel (b) showsthe cumulative share of SBD claimants where 99 percent of claimants have total assets below 10million CAD. If anything, we will omit only a small number of eligible firms above the total assetsthreshold.In addition, we drop firms that have moved across provinces (0.84 percent), switched industries(4.42 percent), or have establishments in multiple provinces (1.6 percent). Fourth, we exclude27We exclude years before 2011 mainly because there were non-trivial changes in the general and small businesstax rates In 2010, Ontario’s general tax rate and the tax rate for M&P dropped from 14 percent to 12 percent and 12percent to 10 percent, respectively, while the small business tax rate dropped from 5.5 percent to 4.5 percent. BritishColumbia’s general tax rate dropped from 12 percent to 11 percent in 2008, and to 10.5 percent in 2010, while thesmall business tax rate dropped from 4.5 percent to 2.5 percent in 2008.28To prevent the disclosure of confidential information, Statistics Canada requires that all estimates and observa-tion counts are rounded. Variables are winsorized at the first and ninety-ninth percent levels, except provincial andfederal income tax rates, provincial income taxes paid, taxable income, and after-tax profits that are winsorized atthe fifth and ninety-fifth percent levels.73firms in agriculture (1.6 percent), finance and real estate (7.1 percent), healthcare (7.8 percent),and professional services (14.7 percent) sectors. These sectors appear least comparable to the man-ufacturing sector and are more vulnerable to tax avoidance by high-income professionals. Finally,we focus on firms in Quebec, British Columbia, and Ontario, which jointly make up 75 percent ofall firms in Canada. Firms in Alberta, New Brunswick, Nova Scotia, Newfoundland and Labrador,Prince Edward Island, and Yukon are dropped because they experienced non-trivial changes in thegeneral or small business tax rates between 2011 and 2017. The remaining provinces (Manitoba,Northwest Territories, Nunavut, and Saskatchewan) account for 5.6 percent of firms in our dataand including them has minimal impacts on our results.Table 4.1, panel I shows the means for key firm-level variables during the pre-reform period(2011–2013) by provinces and sectors. These variables include capital stock, total revenue, employ-ment, average payroll, EBITDA per worker, after-tax profits, taxable income, and provincial andfederal income tax rates. We use the reported book value of tangible assets, net of depreciation,to measure capital stock, and the average number of employees reported in T4 slips to measureemployment. EBITDA is defined as a company’s earnings before interest, taxes, depreciation, andamortization. After-tax profits are defined as net income after taxes and extraordinary items.Provincial and federal income tax rates are the firm’s provincial and federal taxes (reported as PartI tax) payable, scaled by taxable income, respectively. These tax rates are equal to zero in a givenyear if the firm does not have positive taxable income or does not pay any tax. Therefore, theyreflect the effective tax rates facing the firms.On average, firms in the M&P sector are older and larger than firms in non-M&P sectors, interms of tangible assets, revenue, employment, and payrolls. However, firms in non-M&P sectorshave higher profit margins and EBITDA per worker. Within the M&P or non-M&P sector, firmsare similar in size across treated and control provinces. In Quebec, the share of firms in the M&Psector is about 10 percent. The majority of non-M&P firms are in construction (25 percent),retail (19.2 percent), transportation (9.5 percent), and other services (34.1 percent), which includeadministrative support, education, accommodation, and food services. The sectoral compositionis similar for firms located in British Columbia or Ontario. Notice that the effective tax ratesare lower than the statutory tax rates due to tax deductions and credits. As such, any change ineffective tax rates is likely smaller than in statutory tax rates.4.3.2 Worker DataFor the worker-level analysis, we define treated and control workers, respectively, as those workingin a treated or a control firm in 2013, the year before the reform. We drop worker-years withannual earnings below 4,000 CAD and workers with multiple jobs in any given year (“multiple-jobholders”), so that our sample focuses on plausibly full-time workers (Card et al., 2013; Sorkin, 2018).Each worker’s annual earnings are aggregated across all employers in a given year. Nevertheless,we associate each worker with a “dominant” employer from which she receives the highest pay inthe year. As mentioned above, we also focus on workers employed in the same treated or control74firms during 2011–2013 (Jacobson et al., 1993). In Appendix C.3, we perform a robustness checkincluding part-time workers, multiple-job holders, or workers failing the tenure restriction, and wefind qualitatively similar results.Table 4.1, panel II shows the means for key worker-level variables in 2011–2013 by provincesand sectors. On average, workers in the M&P sector are slightly older and earn a bit more thanworkers in non-M&P sectors. Additionally, the share of male workers is larger in the M&P sector.While workers in Quebec are younger and earn less than workers in British Columbia or Ontario,the sectoral differences are similar across provinces. In Quebec, the share of workers in the M&Psector is about 16 percent. The majority of workers in non-M&P sectors are in construction (20.2percent), retail (25.2 percent), transportation (7.1 percent), and other services (35.1 percent). Thiscomposition is similar in British Columbia or Ontario.4.4 ResultsEffective tax rates, taxes payable, and taxable income Figure 4.2 plots estimates of θτin equation (4.2) on provincial income tax rates, federal income tax rates, provincial income taxespayable, and taxable income. For all outcomes, treated and control firms exhibit parallel trendsbefore 2014. As a result of the tax cut, provincial income tax rates decrease significantly for treatedfirms after 2014 (panel (a)), whereas federal income tax rates remain flat. This is consistent withthe fact that the reform only reduced the provincial tax rates of treated firms. Accordingly, panel(c) shows a decline in the provincial corporate income taxes paid by treated firms after 2014.Table 4.2, columns (a)–(c) present the corresponding triple differences estimates. After thereform, the provincial income tax rate of treated firms decreases by 1.4 percentage points. Relativeto their pre-reform effective tax rate (7.7 percent, see Table 4.1), the implied net-of-tax rate increasesby 1.5 percent. We compute the change in net-of-tax rate as(τ0 − τ1)(1− τ0) =0.0139(1− 0.077) = 0.015, (4.5)where τ0 is the initial tax rate. If we use the statutory tax rates, the net-of-tax rate is increasedby 4.94 percent.29 Additionally, the provincial income taxes paid by treated firms decrease by anaverage of 3,033 CAD per year after the reform. These results suggest that the reform significantlyreduces the corporate income tax rates for treated firms.Moreover, the tax cut leads to a steady increase in the taxable income of treated firms (Figure4.2, panel (d)). Table 4.2, column (d) shows that treated firms’ average taxable income increasesby 5,161 CAD per year after 2014, so the tax cut leads these firms to grow. Using the change in29Assuming taxable income below 500,000 CAD and taxable capital below 10 million CAD, firms’ statutorycorporate income tax rate was 19 percent (11 percent for the federal and eight percent for Quebec) before the reform.Since the treated firms’ statutory provincial tax rate decreased from eight percent to four percent after the reform,the net-of-statutory tax rate change was 0.04(1−0.19) = 0.0494. Using just the statutory provincial tax rate would yieldthe net-of-tax rate change of 0.04(1−0.08) = 0.0435, which is similar to the one using the combined statutory tax rate.75statutory tax rates for small M&P firms in Quebec, the implied average tax saving equals 3,170CAD per year, which is computed as the increased taxable income (79,216 CAD) multiplied by thetax rate cut (four percentage points). Notice that the amount of average tax savings is similar tothe estimated reduction in provincial taxes payable in Table 4.2, column (c).Employment, payrolls, and capital investment. Next, we examine the tax effect on firmgrowth. Figure 4.3 plots estimates of θτ from equation (4.2) on employment, average payrolls,tangible assets, and investment. We find significant increases in these outcomes for treated firmsafter 2014, suggesting that the tax cut led these firms to increase demand for both labor and capital.Table 4.3 presents triple differences estimates on these firm-level outcomes. Columns (a)-(b)show that the employment and average payrolls increase by 1.74 percent and 2.34 percent, respec-tively, for treated relative to control firms. This indicates a large and significant response in labordemand. Columns (c)–(d) show that treated firms’ tangible assets increase by 3.17 percent andinvestment in physical assets by 2,036 CAD per year. Using the changes in statutory tax rates, theelasticities of firms’ employment, average payrolls, and tangible assets with respect to the net-of-taxrate are 0.35, 0.47, and 0.64, respectively.Worker earnings and worker composition. To disentangle the tax effect on labor demandand average payrolls, we exploit worker-level data to separately identify the effects on worker-level earnings and worker composition within each firm. In Figure 4.4, panel (a), we plot θˆτ fromequation (4.4) on workers’ annual earnings. By tracking the same workers over time, we focuson changes among incumbent workers. The annual earnings of treated incumbent workers exhibitsimilar trends as control workers’ before 2014 but increase significantly afterward. Accordingly,Table 4.4, column (a) reports the triple differences estimates from equation (4.3). On average,the annual earnings of treated workers increase by 1.34 percent after the reform. The elasticity ofworkers’ earnings with respect to the net-of-statutory corporate income tax rate is 0.27, implyingthat a one-percent increase in the net-of-tax rate raises worker earnings by 0.27 percent.Next, we examine whether the earnings growth is driven by higher pay at the incumbent firms orjob transition to higher-paying firms. In Figure 4.4, panel (b), we estimate equation (4.4) focusingon workers who stay at their pre-reform employers for at least one year after 2014, and trackthem until they leave for other firms. After the reform, stayers at treated firms experience similarearnings increases as all incumbents, by an average of 1.37 percent (Table 4.4, column (b)). Bycontrast, we find no response in workers’ job transition rates after the reform (Table 4.4, column(c)). Hence, the earnings effects are not driven by treated workers moving to higher-paying firms.On the other hand, Table C.2, columns (a)–(d) report estimates of the tax effects on entrants’average annual earnings and worker composition within firms. These outcome variables are con-structed by aggregating worker-level data at the firm level. We find that the tax reform leadsto an increase in new entrants’ average payrolls by 1.8 percent, comparable with the estimate onincumbent workers. By contrast, there is no change in the gender composition or the average ageof workers in treated versus control firms after the reform. Table C.2, column (e) estimates the tax76effect on the probability of working full-time (not part-time workers or multiple-job holders). Theshare of full-time workers at treated firms is 74.3 percent before the reform, and increases by 0.4percentage points after the reform. If anything, there is a small increase in the share of workerstransitioning to full-time jobs.Productivity and profitability. We associate firms’ response in labor and capital input withchanges in their profitability and productivity after the tax cut. Figure 4.5 plots estimates of θτ fromequation (4.1) on total revenue, after-tax profits, EBITDA per worker, and total factor productivity(TFP). Following Ackerberg et al. (2015), we use firms’ total revenue, tangible assets, employment,and intermediate inputs to estimate the production function by 4-digit NAICS industry, accountingfor endogenous input choices of labor and capital, and define TFP as the regression residuals. Alloutcomes follow similar trends between treated and control firms before the reform. After 2014, wefind significant increases in these outcomes for treated firms, suggesting that treated firms becomemore profitable and productive as they increase investment and employment after the tax cut. It isworth noting that firms’ profitability and productivity respond more gradually to the reform thanemployment and investment.Table 4.5 presents the triple differences estimates on these firm-level outcomes. On average,treated firms’ total revenue and after-tax profits increase by 5.17 percent and 7,263 CAD peryear, respectively. Subtracting the mechanical tax savings (3,170 CAD, Table 4.2) from after-taxprofits yields an increase in profits of 4,093 CAD, implying that treated firms indeed become moreprofitable after the reform. Besides, EBITDA and TFP increase by 890 CAD per worker and1.5 percentage points, respectively, so treated firms are also more productive after the reform. Apotential explanation for the productivity effect is that firms increasingly invest in productivity-enhancing technologies. As shown in Table C.3, columns (a)–(b), treated firms increase theirinvestment in intangible assets, and roughly one-third of the rise in total (Table 4.3) investmentwas tied to computers and software.Owner outcomes Finally, we examine whether the tax cut raises the capital income of businessowners. Using ownership data, we link each business with its individual owners and shares owned.Critics of the tax cut may argue that small business owners would use any increase in after-taxprofits to increase payouts to themselves, offsetting the tax benefits on firm and worker outcomes.We focus on owners who have any share in either treated or control firms in 2013. TableC.4, column (a) reports the tax effects on owners’ dividends income averaged at the firm level.Column (b) reports the effects on shares owned by each individual owner at each firm.30 We findno significant change in these outcomes after the reform.30The unit of observation is owner-firm-year and the effects are estimated analogous to equation (4.3). For example,if an owner owns multiple firms, we track her ownership in each firm as separate observations.774.4.1 Comparing Elasticities with Prior EstimatesTo compare our estimates with those from prior studies, we also estimate the change in the cost ofcapital after the reform. In Appendix C.2, we show that the user cost of capital for treated firmsdecreases by 1.5 percent, from 0.372 before the reform to 0.366 afterward.As such, the capital stock elasticity with respect to the change in the cost of capital is −2.11percent, in line with recent estimates from Zwick and Mahon (2017), Moon (2022), and Curtiset al. (2022). The estimated labor elasticity is −1.16 percent, close to the estimated elasticityof production labor in the United States (Curtis et al., 2022). Turning to worker-level earnings,the elasticity of workers’ earnings with respect to the net-of-statutory tax rate is −0.27, whichis comparable to the estimate of −0.39 found in Germany (Fuest et al., 2018). Since we observeneither workers’ wages nor their hours of work, we focus on plausibly full-time workers to isolatechanges in workers’ hours and argue that our earnings estimate is close to a wage estimate. Eitherway, we conclude that workers bear a significant burden of corporate taxes.Overall, our estimated elasticities of capital stock, labor, and worker earnings are comparable tothose in other settings such as the United States and Germany. However, there might be country-specific institutional differences that generate heterogeneous responses to a tax cut.4.4.2 RobustnessAppendix C.3 reports robustness checks for key outcomes in our analysis. First, we estimate equa-tions (4.1)–(4.4) controlling for 4-digit NAICS industry by year fixed effects and commuting zoneby year fixed effects. We also cluster standard errors two-way by industries and commuting zones.The results remain similar as before, suggesting that our estimates are not driven by unobservedshocks at the industry or local labor market level. Second, we define small businesses alternativelyas those with taxable capital missing or below 10 million CAD, as firms with taxable capital below10 million CAD are not legally required to report the information. Third, our estimates are robustto including firms and workers in agriculture, finance and real estate, healthcare, and professionalservices, and in other Canadian provinces without change in corporate income tax rates in 2011–2017. Fourth, the tax effects on worker earnings remain positive and significant after includingpart-time workers (with annual earnings below 4,000 CAD), multiple job holders, and workers notcontinuously employed by the same firm in 2011-2013. As shown in Figures C.3–C.7, all estimatesand quantitatively similar to our baseline results.Besides, one may be concerned about small firms bunching at the taxable income of 500,000CAD, as firms above the threshold face a higher marginal tax rate. Figure C.8 plots the distributionof treated firms’ taxable income between 250,000 and 750,000 CAD. Before and after the reform,the distributions are smooth and exhibit no difference. Figure C.9 further shows that firms withtaxable income between 400,000 and 500,000 CAD and thus close to the eligibility threshold hardlyrespond to the tax cut. This may explain the absence of the bunching effect. Additionally, FigureC.10 reports a placebo test using non-CCPCs that are ineligible for the SBD and unaffected by78the tax cut. The estimated effects are indistinguishable from zero, suggesting that the tax cut forsmall M&P firms in Quebec had minimal spillover effects on other ineligible firms.In Figures C.11, we plot separate DID estimates that (i) compare small firms in M&P versusnon-M&P sectors in Quebec and (ii) make the same comparison in British Columbia and Ontario.Across all main outcomes, the sectoral difference either stays flat or moves in parallel before the taxcut, thereby validating the assumption of our triple differences design. However, worker earningsin the M&P sector start to decline relative to non-M&P sectors before the reform, but the declinefollows a parallel trend between Quebec and the other two provinces. Hence, the triple differencesare essential to net out the sectoral-specific trends.Finally, we examine how much of the employment effect is driven by worker reallocation betweentreated and control firms. If the increased employment in treated firms’ is driven by workers movingfrom control firms, our triple differences estimate would double-count the true effect. Figure C.12,panel (a) shows the inflow, outflow, and net inflow rates for workers from control to treated firmsin 2011-2017. After the reform, the net inflow of workers from control to treated firms increasesby 0.03 percentage points or 780 workers per year. Panels (b)–(c) further show that most of thereallocation takes place within Quebec. Adjusting for this reallocation will reduce the estimatedeffect on employment from 1.74 to 1.71 percent (Table 4.3). Therefore, worker reallocation betweentreated and control firms has minimal impacts on our main estimates. Similarly, only 0.18 percentof firms in non-M&P sectors switched to the M&P sector and 0.01 percent of firms outside of Quebecmoved to Quebec after the reform, suggesting little reallocation of firms across sectors or provinces.This is consistent with that most firms in our analysis are small, have only one establishment, andoperate within one province.4.5 MechanismsAfter establishing the effect of the tax cut on firm growth, productivity, and profitability, a naturalquestion is why treated firms did not increase investment before the tax cut, even if this could haveled to better outcomes. We hypothesize that the tax effect operates through a combination of cashconstraints and borrowing costs. Since all treated firms are small businesses, they tend to financea significant part of the increased investment via debts. Without the tax cut, the marginal returnon investment may not cover the borrowing cost, making it not worthwhile to increase spending.The tax cut increases firms’ marginal after-tax returns, making it profitable to invest and expand.Table C.3, columns (c)–(d) provide empirical evidence to support our hypothesis. After thereform, treated firms increase operating expenses by an average of 72,586 CAD per year. Atthe same time, the average debts increase by 27,483 CAD, implying that roughly 38 percent ofthe increased expenses are financed by borrowing. At a risk-free rate of four percent and theaverage interest rate of eight percent estimated from our firm-level data, the weighted-average costof investment is 8 × 0.38 + 4 × (1 − 0.38) = 5.52 percent. On the other hand, the increase inafter-tax profits (7,263 CAD per year, see Table 4.5) implies a marginal return to spending of797,26372,586 × 100% = 10 percent. Without the tax saving of 3,170 CAD per year, however, the marginalreturn is only 7,263−3,17072,586 × 100% = 5.6 percent and makes it unworthy to invest, especially giventhe presence of risk premiums. Therefore, tax saving raises firms’ marginal returns to spendingabove the marginal cost, making it profitable to invest and expand.High-growth and low-growth industries. We demonstrate that firms and workers in high-growth industries respond more strongly to the tax cut than their counterparts in low-growthindustries. We compute the year-to-year changes in firms’ total assets in 2011–2013, aggregateat the industry level, and define high- versus low-growth industries with growth rates above andbelow the sample median. Then we estimate equations (4.1)–(4.4) for high-growth and low-growthindustries separately.31Figure 4.6, panels (a)–(c) show that the tax effects on worker-level earnings, employment, andcapital stock are stronger in high-growth industries. Furthermore, panels (d)–(f) show that firmsin high-growth industries generate higher after-tax profits and become more productive relative tofirms in low-growth industries. Table 4.6 confirms that the differences between high-growth andlow-growth industries are statistically different from zero for all outcomes. In fact, the increases inearnings and productivity are almost entirely driven by workers and firms in high-growth industries.We argue that high-growth industries face higher net present value for investment opportunities,making it more profitable to invest in productive capital. By doing so, firms experience largerincreases in productivity and profitability, leading to more demand for labor and higher salaries forworkers.324.5.1 Alternative MechanismsIn addition, we explore other mechanisms that may drive the aforementioned effects of the tax cut.Lowering corporate income tax rates for small firms could affect their outcomes by increasing cashflow or reducing the cost of capital. We also examine whether the tax cut affects worker earningsby reducing firms’ wage-setting power or rent-sharing.Cash flow. Due to financial constraints, small businesses may not be able to optimally investin capital or labor. Lowering corporate income tax rates may reduce small firms’ tax burdens, in-crease their immediate cash flow, and relax their financial constraints. Our finding that profitability31In the M&P sector, the top five high-growth industries are screw, nut, and bolt manufacturing (3327), plasticproduct manufacturing (3261), general-purpose machinery manufacturing (3339), metalworking machinery manu-facturing (3335), and fabricated metal product manufacturing (3329). On average, firms in high-growth industrieshave higher profit margins, after-tax profits, and taxable income, and workers in high-growth industries have higherearnings. However, firms in high-growth industries have similar capital stock, employment, and average payrolls astheir low-growth counterparts, despite being more profitable and productive (see Table C.6).32Similarly, Table C.7 shows that the tax effects are stronger in high-tech versus low-tech industries in the M&Psector. Following Heckler (2005), We define high-tech versus low-tech industries with employment in technology-oriented occupations above or below 9.8 percent of the industry’s total employment. We focus on the comparisonwithin the M&P sector because most high-tech industries are in non-M&P sectors (professional services or healthcare)excluded from our sample.80increases for treated firms is also consistent with the idea that small businesses were financiallyconstrained before the reform. Hence, we test whether the tax effects are stronger for more finan-cially constrained firms. Table C.8 reports estimates for firms (and workers) with leverage ratiosbelow and above the sample median in 2013. Overall, the effects are stronger for more leveragedand constrained firms, whereas the differences are statistically indistinguishable from zero. Thiscould result from the fact that small businesses in our sample are mostly constrained, and there isnot much variation in this aspect.Cost of capital. Lowering corporate income tax rates may also stimulate firm growth by reducingtheir cost of capital (see equation (C.1) in Appendix C.2). If capital and labor are complements,a tax-induced increase in capital would also raise employment and wages. Table C.9 tests whethercapital-intensive firms respond more strongly to the tax cut than less capital-intensive ones. Weuse capital stock scaled by total revenue as a proxy for capital intensity and compare industrieswith capital intensity below and above the sample median in 2013. For our key outcomes, the taxeffects are larger for capital-intensive industries than less capital-intensive ones but the differencesare not statistically significant. This is likely because the tax cut only induces a small change inthe cost of capital.Labor market monopsony and wage bargaining. A lower corporate income tax rate couldincrease employment and wages via two channels. In competitive labor markets, it may boost laborproductivity, and the higher marginal product of labor directly translates to increased employmentand wages. In monopsonistic labor markets, firms facing the tax cut may also expand in size andgain greater labor market power, which imposes a downward pressure on wages (the markdowneffect). In contrast, our estimates are unlikely to be driven by labor market concentration sincemost employers in our setting are small firms with no dominant power. Table C.10 confirms thatthe tax effects exhibit no difference between more and less concentrated labor markets.33 Besides,the effects seem not to arise from union wage bargaining because 90 percent of workers in ouranalysis are not covered by unions (as they work for small businesses).Rent sharing. Finally, we compare tax effects on worker-level earnings based on worker char-acteristics. Tables C.11–C.12 report estimates by gender, age quartiles, and within-firm earningsquartiles before the reform, respectively. To identify low-earnings versus high-earnings workerswithin each firm, we exclude firms with fewer than four workers from our sample in the last com-parison. Most of the earnings increases are driven by male workers and older workers (above 45years old). This is consistent with the fact that treated M&P firms are dominated by male andolder workers, and recent findings that male workers extract higher rents from a payroll tax cut(Saez et al., 2019) or patent-induced demand shocks (Kline et al., 2019). Within each firm, however,33We define a labor market by 4-digit NAICS industries and commuting zones and measure concentration by theHerfindahl-Hirschmann Index (HHI). High- versus low-concentration markets are defined using HHI above and belowthe sample median in 2013, respectively.81the effects are concentrated among workers in the second and third quartiles. This contrasts a keyfinding in Kennedy et al. (2022) that workers in the top ten percent of the within-firm earningsdistribution disproportionately benefit from the U.S. Tax Cuts and Jobs Act in 2017.4.5.2 Contemporaneous Tax ReformsTo conclude this section, we discuss additional tax benefits targeting small businesses in the M&Psector in Quebec and show that our estimates are not explained by these extraneous tax benefits.Additional tax deductions of transportation costs for remote firms. Since 2014, smallfirms in the M&P sector in Quebec are eligible for additional tax deductions for transportationcosts if their locations are remote from major urban centers. Especially, the amount of tax benefitsincreases in distance from urban centers. In Table C.13, we test whether treated firms in the remotezone or the special remote zone (eligible for more deductions) show stronger responses to the taxcut than firms in the intermediate zone or urban centers (eligible for less or no deduction).34 Wefind no significant difference in the estimated tax effects, implying that this additional tax benefitalong is unlikely to explain our main findings.Tax credits for buildings and information technologies. Also since 2014, small firms in theM&P sector in Quebec are eligible for refundable tax credits for (i) acquiring or making an additionto a building, and (ii) integrating information technologies (IT) in their business processes, such aspurchasing a qualified management software.35 If the additional tax credits are what drive our mainfindings, we should expect a disproportional increase in investment tax credits relative to taxableincome among treated firms. However, Table C.14, column (a) finds no change in this outcomeafter the reform. Also, column (b) directly shows that treated firms do not increase investment inbuildings relative to control firms after the reform.Health services fund contribution. Finally, there was a reduction in the Health ServicesFund (HSF) contribution rate at the end of 2014 for small firms in the primary sectors (agriculture,forestry, fishing, hunting, mining, quarrying and oil & gas extraction) and the manufacturing sector.Specifically, the contribution rate would decrease from 2.7 percent to 1.6 percent for firms with totalpayrolls below one million CAD, and the gap between old rates and new rates would shrink linearly34The major urban centers include the Montreal, Quebec, and Gatineau census metropolitan areas. The interme-diate zone is defined as the territory, delimited by the RCMs, within 100 km of Gatineau or Quebec or within 150 kmof Montreal. Firms in the intermediate zone can deduct 2 percent of their gross income, with a 100,000 CAD cap.The remote zone is beyond 100 km of Gatineau or Quebec or beyond 150 km of Montreal. Firms in the remote zonecan deduct 4 percent of their gross income, with a 250,000 CAD cap. The special remote zone comprises the rest andmore isolated territories, including the municipality of L’ˆlle-d’Anticosti, the agglomeration of Iˆles-de-la-Madeleine,the Golfe-du-Saint-Laurent MRC (Coˆte-Nord) and the Kativik Regional Government (Nord-du-Quebec). Firms inthe special remote zone are eligible to deduct 6 percent of their gross income with no cap.35The rate of the tax credit for buildings (up to 50 percent) is determined by where the building is located andthe paid-up capital of the eligible firm for the taxation year. The expenditures on a building are capped at 150,000CAD cumulatively. The amount of the tax credit for IT integration is limited to 62,500 CAD. Unfortunately, whilewe observe investment in IT-related physical capital assets, we do not observe IT-related expenditures.82in the firms’ payrolls. This policy could generate larger benefits for smaller firms. As such, wecompare another heterogeneity analysis based on firms’ pre-reform total payrolls (below and aboveone million, Table C.15). For worker-related outcomes, smaller firms do not exhibit larger responsesthan larger firms, suggesting that the reduced HSF contribution rate is unlikely a major driver ofour findings.In summary, while additional tax benefits exist to target small M&P firms in Quebec, we showthat these benefits are not the main driver of our findings. Furthermore, we can interpret our resultsscaled by changes in average effective tax rates, which account for the additional tax benefits besidesthe lower statutory tax rate.4.6 Welfare Implications4.6.1 Incidence of Corporate Taxes on Workers and Firm OwnersTo evaluate the distributional effects of the tax cut, we follow Sua´rez Serrato and Zidar (2016) andFuest et al. (2018) to measure tax incidence on workers and firm owners. The idea is to link thechange in marginal tax rates to welfare changes of workers and firm owners.For small businesses, in particular, we distinguish workers without ownership and workers withownership in their firms (“owner-workers”). For both types of workers, the welfare change due tothe change in wage rates is given by (Fuest et al., 2018)dVi = Li(1− ti)dwi = Liwiϵwi(1− ti)d(1− τ), (4.6)where Vi is the indirect utility of a representative worker of type i (1 for non-owners, 2 for owner-workers), Li is the quantity of labor, ti is the marginal income tax rate, wi is the wage rate, and ϵwiis the elasticity of wage with respect to the net-of-tax rate; τ is the tax rate on corporate income.For owner-workers, there exists additional welfare change due to changes in firm profitsψdπ = ψπϵπd(1− τ), (4.7)where π is the firm’s after-tax profits and ϵπ is the elasticity of after-tax profits with respect to thenet-of-tax rate. We estimate that owner-workers own ψ = 0.58 share of the firms. The remainingshares are owned by passive owners (the “capital”).We use our triple differences estimates to pin down ϵw1 , ϵw2 , and ϵπ, along with the pre-reformaverages of L1w1, L2w2, and π for treated firms and workers (see Tables 4.3, 4.5, and C.5). We set(t1, t2) = (0.285, 0.384) as the top marginal income tax rates at the combined federal and provinciallevels based on workers’ average annual earnings in 2013. Then we calculate the tax incidence onnon-owner workers, owner-workers, and capital as follows:Iw1 =dV1dV1 + dV2 + dπ=L1w1ϵw1(1− t1)L1w1ϵw1(1− t1) + L2w2ϵw2(1− t2) + πϵπ= 0.34, (4.8)83Iw2 =dV2 + ψdπdV1 + dV2 + dπ=L2w2ϵw2(1− t2) + ψπϵπL1w1ϵw1(1− t1) + L2w2ϵw2(1− t2) + πϵπ= 0.39, (4.9)Iπ =(1− ψ)dπdV1 + dV2 + dπ=(1− ψ)πϵπL1w1ϵw1(1− t1) + L2w2ϵw2(1− t2) + πϵπ= 0.27. (4.10)By contrast, without ownership information, the incidence on workers would be:Iw =dVdV + dπ=Lwϵw(1− t)Lwϵw(1− t) + πϵπ = 0.37, (4.11)where the right-hand side uses estimates on total employment and firm-level average payrolls fromTables 4.3–4.5 and t = 0.285.The above analysis indicates that workers with and without ownership each bear over one-third of the corporate tax burden. Combined together, the tax incidence on workers is roughlythree-quarters. Focusing on workers without ownership, our estimated incidence of 0.34 is closeto Sua´rez Serrato and Zidar (2016), but smaller than Fuest et al. (2018). However, the combinedincidence of 0.73 is larger than those from prior studies. In addition, ignoring owner workers wouldreduce the tax incidence on workers by almost half. Therefore, distinguishing workers with andwithout ownership is important to accurately assess the incidence of tax burdens, especially forsmall businesses where a significant share of owners also work at their firms.4.6.2 Pass-Through EstimatesTo further connect firm- and worker-level results, we estimate the pass-through of firms’ additionalsurplus from the tax cut on workers’ earnings. Following from Kline et al. (2019), we estimatelogWjt = µ0 logSjt + µ1Postt ·MPj + µ2Postt ·QCj + αj + ϕt + ujt, (4.12)where Wjt is workers’ annual earnings aggregated at the firm level j and Sjt represents firms’surplus per worker. We measure surplus as the sum of firms’ total payrolls and EBITDA so thatthe surplus is almost always positive despite negative values of EBIDTA (Kline et al., 2019). Forcomparability with the literature, we estimate (4.12) using full-time incumbent workers.We exploit the Quebec tax cut to generate exogenous variation in the surplus. Using thethree-way interaction Postt ·MPj ·QCj as an instrument for surplus per worker, the first stage islogSjt = η0Postt ·MPj ·QCj + η1Postt ·MPj + η2Postt ·QCj + αj + ϕt + ujt. (4.13)Table 4.7, column (a) shows the pass-through estimate µˆ0 = 0.353, i.e., an average firm passes35.3 percent of the additional surplus generated by the tax cut onto workers. This is in line withthe estimate from Kline et al. (2019). Column (b)–(c) distinguish a smaller pass-through of 0.249to owner-workers but a much larger pass-through of 0.465 to non-owner workers. Workers withoutownership likely have less bargaining power than owner-workers, so the large increase in theirearnings is inconsistent with rent-sharing. Instead, it suggests that firms face an upward labor84supply curve and raise wages in response to increased productivity and labor demand.4.6.3 Cost-per-Job EstimateFinally, to compare the fiscal cost of the reform to the number of jobs created, we estimate acost-per-job formula:Cost per job =Losses in corporate tax revenue−Gains in labor income tax revenueNumber of jobs created. (4.14)We focus on the firm sample in Table 4.1 where the number of treated firms is 10,205. Given thefirm-average loss in provincial income taxes (3,033 CAD per year, Table 4.2, column (c)), the totalloss in corporate tax revenue is estimated to be 30.9 million CAD per year in the first four yearsafter the reform. This corresponds to a medium-run loss in tax revenue by the Quebec government.On the other hand, the tax cut increases the provincial labor income of treated workers by 28.2CAD per worker per year. Without changes in labor income tax rates, the effect is driven by theworkers’ higher annual earnings (the tax base) after the reform. Multiplying this estimate by thenumber of treated workers yields gains in personal income tax revenue, which equals 1.8 millionCAD per year.Finally, the number of jobs created is 2,024 per year (Table 4.3, column (a)) among all treatedfirms. Combining these estimates yields an estimated cost per job of 14,402 CAD. It is lower than,but still comparable with, the estimate of 20,000 USD per job (Garrett et al., 2020) for the bonusdepreciation policy in the United States.We interpret the cost per job with caution as several factors may understate or overstate theestimate. For example, the employment growth among treated firms could partly stem from workerreallocation from other firms and overestimate the number of real jobs created. While we see aslight increase in the net inflow of workers from control to treated firms, we also find a decline in thenet inflow from out-of-sample firms and firms ineligible for the SBD (Figure C.12, panels (d)–(e)).This, on the contrary, implies an underestimation of the jobs created. Figure C.12, panel (f) furthershows that treated firms recruit fewer and fewer workers from non-employment in years before thereform, but the downward trend turns flat after the reform. Therefore, the tax cut indeed createsnew jobs at treated firms and increases overall employment.Additionally, our estimate is based on medium-run outcomes within our sample of firms andworkers, whereas the effects could differ in the long run or across different provinces and sectors. Ourpartial equilibrium framework also ignores potential general equilibrium effects. We do not accountfor positive externalities from productivity spillovers through firm expansion and job creation ornegative spillovers from competition in input markets with firms in other sectors. A comprehensivewelfare calculation accounting for these components would be valuable for future research.854.7 ConclusionThis paper exploits variations in tax rates across Canadian provinces and sectors, a provincialpolicy reform, and administrative data from tax records, to estimate the effects of corporate taxcuts on small businesses and worker earnings. From 2014 to 2015, small firms in the M&P sectorin Quebec received a tax reduction of four percentage points down from the statutory rate of 19percent. We compare the outcomes of affected firms and workers with those unaffected in non-M&P sectors and in other major provinces of Canada. We find that worker earnings and firms’investment increased significantly for treated firms after the tax cut, and these responses are largerin high-growth industries where firms experience larger increases in productivity and profitability.Taken together, our findings suggest that workers bear a significant corporate tax burden and thatthe increase in worker earnings is closely connected with increased profits.86Figures and TablesFigure 4.1: Small Business Tax Rates in Quebec, British Columbia, and Ontario0246810Small Business Tax Rate (%)2011 2012 2013 2014 2015 2016 2017YearQuebec M&P Quebec non-M&PB.C. M&P and non-M&P Ontario M&P and non-M&PNotes: The figure shows the provincial corporate income tax rates on small businesses in Quebec, British Columbia(B.C.), and Ontario, from 2011 to 2017. For Canadian-Controlled Private Corporations (CCPCs) with taxable capitalbelow 10 million CAD, only the first 500,000 CAD of taxable income is eligible for these small business tax rates.CCPCs with taxable capital between 10 million CAD and 15 million CAD are also eligible for these tax rates, withless qualified taxable income (see Section 4.2).87Figure 4.2: Effective Tax Rates, Tax Payable, and Taxable Income(a) Provincial income tax rates-.03-.02-.010.01Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017Year(b) Federal income tax rates-.03-.02-.010.01Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017Year(c) Provincial income tax payable (’000)-6-4-202Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017Year(d) Taxable income (’000)-20-100102030Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017YearNotes: Panels (a)–(d) plot estimates of θτ from equation (4.2) with dependent variables in subtitles. Samples compriseCCPCs with total assets below 10 million CAD and located in Quebec, British Columbia, and Ontario in 2011–2017.Provincial and federal income tax rates are the firm’s provincial and federal taxes (reported as Part I tax) payable,respectively, scaled by taxable income. The solid vertical line indicates the reform year. All estimates control for firmfixed effects and year fixed effects. The dashed lines represent 95 percent confidence intervals.88Figure 4.3: Employment, Payrolls, and Capital Stock(a) Employment (log)-.04-.020.02.04.06Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017Year(b) Average payrolls (log)-.06-.030.03.06.09Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017Year(c) Tangible assets (log)-.06-.030.03.06.09Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017Year(d) Investment (’000)-4-20246Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017YearNotes: Panels (a)–(d) plot estimates of θτ from equation (4.2) with dependent variables in subtitles. Samples compriseCCPCs with total assets below 10 million CAD and located in Quebec, British Columbia, and Ontario in 2011–2017.The book value of tangible assets, net of depreciation, represents a firm’s capital stock. Investment is the sum ofexpenditures in different asset classes from a data set on capital cost allowance for depreciated capital. All estimatescontrol for firm fixed effects and year fixed effects. The solid vertical line indicates the reform year. The dashed linesrepresent 95 percent confidence intervals.89Figure 4.4: Incumbent Worker Earnings(a) Annual earnings (log)-.02-.010.01.02.03Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017Year(b) Annual earnings (log) for stayers-.02-.010.01.02.03Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017YearNotes: Panels (a)–(b) plot estimates of θτ from equation (4.4) with dependent variables in subtitles. Samples compriseworkers at CCPCs with total assets below 10 million CAD and located in Quebec, British Columbia, and Ontario in2011–2017, excluding part-time workers with annual earnings below 4,000 CAD, multiple-job holders, and workers notcontinuously employed by the same firm in 2011–2013. Panel (b) focuses on workers who stay with their pre-reformemployers after 2014 and track them until they leave the firms. All estimates control for worker fixed effects andyear fixed effects. The solid vertical line indicates the reform year. The dashed lines represent 95 percent confidenceintervals.90Figure 4.5: Sales, After-Tax Profits, and Productivity(a) Revenue (log)-.06-.030.03.06.09Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017Year(b) After-tax profits-20-100102030Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017Year(c) EBITDA per worker-2-10123Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017Year(d) Total factor productivity-.04-.020.02.04.06Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017YearNotes: Panels (a)–(d) plot estimates of θτ from equation (4.2) with dependent variables in subtitles. Samples compriseCCPCs with total assets below 10 million CAD and located in Quebec, British Columbia, and Ontario in 2011–2017.After-tax profits are defined as firms’ net income after taxes and extraordinary items. EBITDA is earnings beforeinterest, taxes, depreciation, and amortization. Total factor productivity is estimated using the method of Ackerberget al. (2015) at the 4-digit NAICS industry level. All estimates control for firm fixed effects and year fixed effects.The solid vertical line indicates the reform year. The dashed lines represent 95 percent confidence intervals.91Figure 4.6: Tax Effects by High-Growth versus Low-Growth Industries(a) Annual earnings (log)-.020.02.04.06Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017YearHigh-growth Low-growth(b) Employment (log)-.030.03.06.09Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017YearHigh-growth Low-growth(c) Tangible assets (log)-.050.05.1.15Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017YearHigh-growth Low-growth(d) After-tax profits-150153045Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017YearHigh-growth Low-growth(e) EBITDA per worker-20246Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017YearHigh-growth Low-growth(f) Total factor productivity-.020.02.04.06Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017YearHigh-growth Low-growthNotes: Panel (a) plots estimates of θτ from equation (4.4) with log annual earnings as the dependent variable. Theestimates control for worker fixed effects and year fixed effects. Panels (b)–(f) plot estimates of θτ from equation(4.2) with dependent variables in subtitles. All estimates control for firm fixed effects and year fixed effects. Samplescomprise CCPCs (and their workers) with total assets below 10 million CAD and located in Quebec, British Columbia,and Ontario in 2011–2017. Part-time workers with annual earnings below 4,000 CAD, multiple-job holders, andworkers not continuously employed by the same firm in 2011–2013 are excluded. The solid vertical line indicates thereform year. The dashed lines represent 95 percent confidence intervals. The dark blue lines indicate estimates forhigh-growth industries, and the red lines indicate estimates for low-growth industries.92Table 4.1: Summary StatisticsQuebec B.C./Ontario(a) (b) (c) (d)M&P Non-M&P M&P Non-M&PA. FirmsTangible assets (’000) 790.6 363.1 709.8 314.0Revenue (’000) 1649.6 1264.3 1582.8 1176.8Employment 11.4 8.2 10.0 7.6Average payrolls (’000) 35.6 21.6 36.2 21.4EBITDA per worker (’000) 7.4 9.9 6.6 8.6After-tax profits (’000) 51.8 35.4 45.3 29.6Taxable income (’000) 74.1 47.5 63.5 39.4Provincial income tax rates 0.077 0.079 0.041 0.041Federal income tax rates 0.080 0.087 0.082 0.089Firm age 14.2 12.0 14.1 11.2Mining and utility 0.002 0.004Construction 0.250 0.223Wholesale trade 0.002 0.004Retail trade 0.192 0.181Transportation 0.095 0.110Information 0.021 0.025Other services 0.341 0.356Observations 28,740 274,110 56,075 595,425Firms 10,205 100,245 20,165 222,825B. WorkersAnnual earnings (’000) 38.3 35.1 46.3 39.9Age 45.7 43.3 46.6 43.7Male 0.689 0.627 0.704 0.607Mining and utility 0.002 0.003Construction 0.202 0.207Wholesale trade 0.002 0.003Retail trade 0.252 0.218Transportation 0.071 0.072Information 0.016 0.018Other services 0.351 0.373Observations 192,755 1,007,210 320,735 1,883,400Workers 64,250 335,740 106,915 627,800Notes: Panels A and B report summary statistics for firms and workers, respectively, by province and M&P sectorversus non-M&P sectors. The firm sample comprises CCPCs (and their workers) with total assets below 10 millionCAD and located in Quebec, British Columbia (B.C.), and Ontario in 2011–2013. The worker sample comprisesworkers at those CCPCs, excluding part-time workers with annual earnings below 4,000 CAD, multiple-job holders,and workers not continuously employed by the same firm in 2011–2013. The book value of tangible assets, net ofdepreciation, represents a firm’s capital stock. EBITDA is earnings before interest, taxes, depreciation, and amor-tization. After-tax profits are firms’ net income after taxes and extraordinary items. Provincial and federal incometax rates are the firm’s provincial and federal taxes (reported as Part I tax) payable, respectively, scaled by taxableincome. Other services include administrative support, education, arts and entertainment, and accommodation andfood services.93Table 4.2: Effective Tax Rates, Tax Payable, and Taxable Income(a) (b) (c) (d)Provincial income Federal income Provincial income Taxabletax rates tax rates tax payable (’000) income (’000)Post × MP × QC -0.0139*** 0.0001 -3.0330*** 5.1606***(0.0009) (0.0006) (0.2335) (1.3170)Mean dep. var. 0.077 0.080 12.9 74.1Observations 1,165,415 1,274,865 1,165,415 2,106,660Firms (treated) 7,645 7,970 7,645 10,205Firms (control) 244,595 264,835 244,595 343,235Adjusted R2 0.363 0.474 0.674 0.724Notes: Columns (a)–(d) report estimates of θ from equation (4.1) with dependent variables in column titles. Samplescomprise CCPCs with total assets below 10 million CAD and located in Quebec, British Columbia, and Ontario in2011–2017. Provincial and federal income tax rates are the firm’s provincial and federal taxes (reported as Part Itax) payable, respectively, scaled by taxable income. All estimates control for firm fixed effects and year fixed effects.Robust standard errors clustered by firms in parentheses. (* p < 0.1, ** p < 0.05, *** p < 0.01)Table 4.3: Employment, Payrolls, and Capital Stock(a) (b) (c) (d)Employment Average payrolls Tangible assets Investment(log) (log) (log) (’000)Post × MP × QC 0.0174*** 0.0234*** 0.0317*** 2.0361***(0.0052) (0.0063) (0.0084) (0.7206)Mean dep. var. 11.4 35.6 790.6 40.9Observations 2,106,660 2,106,660 2,011,725 2,111,875Firms (treated) 10,205 10,205 10,165 10,160Firms (control) 343,235 343,235 339,825 340,285Adjusted R2 0.917 0.888 0.938 0.449Notes: Columns (a)–(d) report estimates of θ from equation (4.1) with dependent variables in column titles. Samplescomprise CCPCs with total assets below 10 million CAD and located in Quebec, British Columbia, and Ontario in2011–2017. The book value of tangible assets, net of depreciation, represents a firm’s capital stock. Investment is thesum of expenditures in different asset classes from a data set on capital cost allowance for depreciated capital. Allestimates control for firm fixed effects and year fixed effects. Robust standard errors clustered by firms in parentheses.(* p < 0.1, ** p < 0.05, *** p < 0.01)94Table 4.4: Incumbent Worker Earnings and Job Transitions(a) (b) (c)Annual earnings (log) Job transition Annual earnings (log)of stayersPost × MP × QC 0.0134*** -0.0011 0.0137***(0.0026) (0.0013) (0.0026)Mean dep. var. 38.3 0.040 38.6Observations 6,692,730 6,692,730 6,211,970Workers (treated) 64,250 64,250 61,230Workers (control) 1,070,455 1,070,455 1,010,275Adjusted R2 0.812 0.080 0.829Notes: Columns (a)–(c) report estimates of θ from equation (4.3) with dependent variables in column titles. Samplescomprise workers at CCPCs with total assets below 10 million CAD and located in Quebec, British Columbia, andOntario, excluding part-time workers with annual earnings below 4,000 CAD, multiple-job holders, and workers notcontinuously employed by the same firm in 2011–2013. Column (b) focuses on workers who stay with their pre-reformemployers after 2014 and track them until they leave the firms. All estimates control for worker fixed effects andyear fixed effects. Robust standard errors clustered by firms and workers in parentheses. (* p < 0.1, ** p < 0.05, ***p < 0.01)Table 4.5: Sales, After-Tax Profits, and Productivity(a) (b) (c) (d)Revenue (log) After-tax profits EBITDA Total factorper worker productivityPost × MP × QC 0.0517*** 7.2627*** 0.8895*** 0.0150***(0.0062) (1.3717) (0.2707) (0.0039)Mean dep. var. 1649.6 51.8 7.4 0.335Observations 2,106,660 2,106,660 2,106,660 1,864,920Firms (treated) 10,205 10,205 10,205 9,950Firms (control) 343,235 343,235 343,235 318,975Adjusted R2 0.916 0.629 0.581 0.994Notes: Columns (a)–(d) report estimates of θ from equation (4.1) with dependent variables in column titles. Samplescomprise CCPCs with total assets below 10 million CAD and located in Quebec, British Columbia, and Ontarioin 2011–2017. After-tax profits are defined as firms’ net income after taxes and extraordinary items. EBITDAis earnings before interest, taxes, depreciation, and amortization. Total factor productivity is estimated using themethod of Ackerberg et al. (2015) at the 4-digit NAICS industry level. All estimates control for firm fixed effects andyear fixed effects. Robust standard errors clustered by firms in parentheses. (* p < 0.1, ** p < 0.05, *** p < 0.01)95Table 4.6: High-Growth versus Low-Growth Industries(1) (2) (3)Annual Employment Tangibleearnings (log) (log) assets (log)Post × MP × QC (low-growth) -0.0001 0.0104 0.0116(0.0033) (0.0067) (0.0104)Post × MP × QC (high-growth) 0.0216*** 0.0336*** 0.0528***(0.0040) (0.0084) (0.0143)Difference 0.0217*** 0.0232** 0.0412**(0.0048) (0.0107) (0.0177)Mean dep. var. (low-growth) 37.3 11.2 726.8Mean dep. var. (high-growth) 41.4 11.9 910.7Observations 6,692,730 2,106,660 2,011,725Workers/firms (treated) 64,250 10,205 10,165Workers/firms (control) 1,070,455 343,235 339,825Adjusted R2 0.813 0.917 0.938(4) (5) (6)After-tax EBITDA Total factorprofits per worker productivityPost × MP × QC (low-growth) 2.1759 0.0895 0.0057(1.6183) (0.3207) (0.0052)Post × MP × QC (high-growth) 16.0480*** 1.9388*** 0.0261***(2.4845) (0.4820) (0.0058)Difference 13.8721*** 1.8493*** 0.0204***(2.9651) (0.5790) (0.0078)Mean dep. var. (low-growth) 43.2 6.2 0.160Mean dep. var. (high-growth) 68.0 9.4 0.724Observations 2,106,660 2,106,660 1,864,920Firms (treated) 10,205 10,205 9,805Firms (control) 343,235 343,235 310,025Adjusted R2 0.629 0.581 0.994Notes: Column (a) reports estimates of θτ from equation (4.4) with log annual earnings as the dependent variable.The estimates control for worker fixed effects and year fixed effects. Columns (b)–(f) report estimates of θτ fromequation (4.2) with dependent variables in column titles. All estimates control for firm fixed effects and year fixedeffects. Samples comprise CCPCs (and their workers) with total assets below 10 million CAD and located in Quebec,British Columbia, and Ontario in 2011–2017. Part-time workers with annual earnings below 4,000 CAD, multiple-jobholders, and workers not continuously employed by the same firm in 2011–2013 are excluded. Robust standard errorsclustered by firms and workers (column (a)) or by firms (columns (b)–(f)) in parentheses. (* p < 0.1, ** p < 0.05,*** p < 0.01)96Table 4.7: Pass-Through Estimates(a) (b) (c)Annual Annual earnings (log) Annual earnings (log)earnings (log) of owner workers of non-owner workersSurplus per worker (log) 0.3531*** 0.2487* 0.4645***(0.0522) (0.1365) (0.0615)Observations 1,505,810 909,475 1,170,460Firms 255,500 157,395 209,695F -statistic 121.6 27.8 111.6Notes: Columns (a)–(c) report estimates of µ0 from equation (4.12) with dependent variables in subtitles, aggregatedby firms, and surplus per worker (log) instrumented by Post × MP × QC (Kline et al., 2019). Samples compriseCCPCs with total assets below 10 million CAD and located in Quebec, British Columbia, and Ontario in 2011–2017. Part-time workers with annual earnings below 4,000 CAD, multiple-job holders, and workers not continuouslyemployed by the same firm in 2011–2013 are excluded. All estimates control for firm fixed effects and year fixedeffects. Robust standard errors clustered by firms in parentheses. (* p < 0.1, ** p < 0.05, *** p < 0.01)97Chapter 5ConclusionTo conclude, this dissertation examines the economic implications of worker mobility from differentperspectives. Chapter 2 investigates workers’ commuting behavior after job displacement. Usinggeo-referenced employee-employer matched data in Germany and a matched event study design,we estimate that displaced workers commute up to 21 percent longer distances to subsequent jobsand gradually reduce commuting by switching jobs closer to their homes. Structural estimation ofa job search model reveals that workers’ daily commuting cost amounts to one-fifth of their averagedaily wages, and the longer commuting after displacement amplifies the total cost of job loss byone-fifth of the contemporaneous wage losses. Therefore, accounting for the commuting effect, orthe effect on non-wage job amenities in general, is important to comprehensively evaluate workers’total cost of job loss.Continuing the discussion on commuting costs, Chapter 3 studies their impacts on residentiallocation choices. While public transit like subways offers a convenient and affordable means ofcommuting for urban dwellers, door-to-station remains costly, giving rise to higher demand for andprices of housing near subway stations. The introduction of dockless bike sharing in China effectivelysolves this “last-mile problem” by making public transit more accessible to distant residents. As aresult, apartments distant from subway stations become relatively more expensive than apartmentsnearby, reflecting a narrower difference in the commuting cost to the subway. Our analysis usesdetailed real estate market data and the staggered entry of bike sharing in 10 major Chinese citiesto confirm this effect and quantify the reduction of commuting costs in monetary terms.Limited worker mobility also leads to imperfect labor market competition, leaving room foreconomic policies to improve efficiency and welfare. Chapter 4 evaluates the labor market effectsof a corporate tax cut targeting small businesses in the manufacturing sector in Quebec, Canada.Despite concerns that small businesses are generally inefficient and not responsive to tax incentives,we find strong and positive responses to the tax cut in terms of firms’ capital and labor input, pro-ductivity and profitability, and workers’ earnings. Combining firm- and worker-level tax filing data,we further show that the tax effect happens through reducing firms’ cost to invest in productivecapital, which allows firms to expand and pass extra surplus to workers. 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The resulting estimates αˆ and ψˆ representworker-specific wage premiums common to all firms and firm-specific wage premiums common toall workers, respectively. Both variables are made available as part of the IEB data.Couples Goldschmidt et al. (2017) identify couples using a de-anonymized version of the IEBdata and we use the resulting identifier (missing or not) to distinguish single versus married workers.To identify two individuals as couples, Goldschmidt et al. (2017) impose the following criteria: (i)opposite genders, (ii) age difference below 15 years old, (iii) sharing a common last name or one’slast name is a part of the other’s, (iv) living at the same address, (v) no third person living at thesame address but satisfying criteria (i)–(iii).Given these strict restrictions, Goldschmidt et al. (2017) validate that roughly 90 percent ofidentified couples are real couples. However, this method likely misses real couples who do not livetogether, who live with another family member (e.g., their adult child), or who are not coveredby the social security system (e.g., one spouse is a civil servant or self-employed). By contrast,missing identification of homosexual couples, couples with a large age difference, or couples withdifferent last names is rare. Hence, the absence of heterogeneous displacement effects could bepartly explained by misclassification of the real couples.109A.2 Additional Figures and TablesFigure A.1: Distribution of Commuting Distances and Time(a) Commuting distance (b) Driving time(c) Weighted average commuting time (d) Constant speed elasticityNotes: Panels (a)–(b) plot the distributions of driving distances and driving time, respectively, calculated by Open-StreetMaps. Panel (c) plots the distribution of the average walking, cycling, and driving time weighted by the shareof workers using each mode of transportation. Panel (d) plots the distribution of commuting time predicted fromcommuting distances, assuming a constant speed elasticity with respect to distance of 0.4. The sample comprises ayearly panel of workers with full-time jobs on June 30.110Figure A.2: Effects of Job Displacement on Labor Supply and Earnings(a) Regular employment-250-200-150-100-50050-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10Year(b) Days in full-time jobs-250-200-150-100-50050-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10Year(c) Days in part-time jobs-50510152025-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10Year(d) Days in mini jobs-50510152025-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10Year(e) Annual earnings (’000)-25-20-15-10-505-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10Year(f) AKM firm effects-.2-.15-.1-.050.05-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearNotes: Each plot depicts estimates of βk in equation (2.1) with dependent variables in subtitles. The sample comprisesa balanced yearly worker panel (except panel (f) which comprises workers with full-time jobs on June 30). The verticaldashed line indicates the displacement year. The dots represent the point estimates and the bars represent the 95percent confidence intervals. All estimates control for a polynomial of age, worker fixed effects, calendar year fixedeffects, and year relative to displacement fixed effects. Robust standard errors are clustered by establishments.111Figure A.3: Additional Effects of Job Displacement(a) Daily wage-25-20-15-10-505-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10Year(b) Commuting time-1012345-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10Year(c) Commuting across counties-.020.02.04.06.08.1-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10Year(d) Commuting across cities-.020.02.04.06.08.1-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10Year(e) Changing industries-.20.2.4.6.81-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10Year(f) Changing occupations-.20.2.4.6.81-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearNotes: Each plot depicts estimates of βk in equation (2.1) with dependent variables in subtitles. Samples comprise ayearly panel of workers with full-time jobs on June 30. The vertical dashed line indicates the displacement year. Thedots represent the point estimates and the bars represent the 95 percent confidence intervals. All estimates controlfor a polynomial of age, worker fixed effects, calendar year fixed effects, and year relative to displacement fixed effects.Robust standard errors are clustered by establishments.112Figure A.4: Effect Heterogeneity by Worker Demographics(a) Daily wage (log)-.3-.2-.10.1-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearMale Female(b) Commuting distances (log)-.10.1.2.3-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearMale Female(c) Daily wage (log)-.3-.2-.10.1-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearYoung Old(d) Commuting distance (log)-.10.1.2.3-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearYoung Old(e) Daily wage (log)-.3-.2-.10.1-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearSingle Married(f) Commuting distance (log)-.10.1.2.3.4-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearSingle MarriedNotes: Each plot depicts subsample estimates of βk in equation (2.1) with dependent variables in subtitles. Thesample comprises a yearly panel of workers with full-time jobs on June 30, split by gender (panels (a)–(b)), age(panels (c)–(d)), and married versus single workers (panels (e)–(f), Goldschmidt et al., 2017). Young and olderworkers are defined, respectively, by ages below and above the sample median in the year before displacement. Thevertical dashed line indicates the displacement year. The dots represent the point estimates and the bars representthe 95 percent confidence intervals. All estimates control for a polynomial of age, worker fixed effects, calendar yearfixed effects, and year relative to displacement fixed effects. Robust standard errors are clustered by establishments.113Figure A.5: Effect Heterogeneity by Pre-Layoff Job Characteristics(a) Daily wage (log)-.3-.2-.10.1-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearHigh AKM firm Low AKM firm(b) Commuting distance (log)-.10.1.2.3-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearHigh AKM firm Low AKM firm(c) Daily wage (log)-.3-.2-.10.1-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearHigh AKM worker Low AKM worker(d) Commuting distance (log)-.10.1.2.3-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearHigh AKM worker Low AKM worker(e) Daily wage (log)-.3-.2-.10.1-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearShort tenure Long tenure(f) Commuting distance (log)-.20.2.4.6-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearShort tenure Long tenureNotes: Each plot depicts subsample estimates of βk in equation (2.1) with dependent variables in subtitles. Thesample comprises a yearly panel of workers with full-time jobs on June 30, split by AKM firm effects (panels (a)–(b)),AKM worker effects (panels (c)–(d)), and job tenure (panels (e)–(f)) in the pre-layoff job. Firm and worker fixedeffects are estimated from a two-way fixed effects regression of log daily wages (Abowd et al., 1999) and split by thesample median in the year before displacement. Short and long job tenure is defined as below and above the samplemedian job tenure in the year before displacement. The vertical dashed line indicates the displacement year. Thedots represent the point estimates and the bars represent the 95 percent confidence intervals. All estimates controlfor a polynomial of age, worker fixed effects, calendar year fixed effects, and year relative to displacement fixed effects.Robust standard errors are clustered by establishments.114Figure A.6: Effect Heterogeneity by Labor Market Condition(a) Daily wage (log)-.3-.2-.10.1-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearUrban Rural(b) Commuting distance (log)-.10.1.2.3-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearUrban Rural(c) Daily wage (log)-.3-.2-.10.1-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearLow HHI High HHI(d) Commuting distance (log)-.20.2.4.6-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearLow HHI High HHI(e) Daily wage (log)-.3-.2-.10.1-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearHigh industry share Low industry share(f) Commuting distance (log)-.10.1.2.3-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearHigh industry share Low industry shareNotes: Each plot depicts subsample estimates of βk in equation (2.1) with dependent variables in subtitles. Thesample comprises a yearly panel of workers with full-time jobs on June 30, split by urban versus rural residence(panel (a)–(b)), labor market concentration (panel (c)–(d)), and local industry share (panels (e)–(f)) of the pre-layoffjob.. Labor market concentration is measured by the Herfindahl–Hirschman index (HHI) within commuting zonesand industrial sectors, and split by the sample median. Local industry share is measured by the employment share ofthe displacing industry within the focal commuting zone, and split by industry-specific sample medians. The verticaldashed line indicates the displacement year. The dots represent the point estimates and the bars represent the 95percent confidence intervals. All estimates control for a polynomial of age, worker fixed effects, calendar year fixedeffects, and year relative to displacement fixed effects. Robust standard errors are clustered by establishments.115Figure A.7: Including Part-Time Jobs(a) Daily wage (log)-.3-.2-.10.1-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10Year(b) Commuting distance (log)-.10.1.2.3-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearNotes: Each plot depicts estimates of βk in equation (2.1) with dependent variables in subtitles. The sample com-prises a yearly panel of workers with full-time or part-time jobs on June 30. The vertical dashed line indicates thedisplacement year. The dots represent the point estimates and the bars represent the 95 percent confidence intervals.All estimates control for a polynomial of age, worker fixed effects, calendar year fixed effects, and year relative todisplacement fixed effects. Robust standard errors are clustered by establishments.Figure A.8: Displacement due to Establishment Closure(a) Daily wage (log)-.3-.2-.10.1-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10Year(b) Commuting distance (log)-.10.1.2.3-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearNotes: Each plot depicts estimates of βk in equation (2.1) with dependent variables in subtitles. The sample comprisesa yearly panel of workers with full-time jobs on June 30. We focus on job displacement due to establishment closure.The vertical dashed line indicates the displacement year. The dots represent the point estimates and the bars representthe 95 percent confidence intervals. All estimates control for a polynomial of age, worker fixed effects, calendar yearfixed effects, and year relative to displacement fixed effects. Robust standard errors are clustered by establishments.116Figure A.9: Selection into Reemployment(a) Daily wage (log)-.3-.2-.10.1-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10Year(b) Commuting distance (log)-.10.1.2.3-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearNotes: Each plot depicts estimates of βk in equation (2.2) with dependent variables in subtitles. The sample comprisesa yearly panel of workers with full-time jobs on June 30. We estimate the effects of job displacement by years sincethe worker is reemployed in a full-time job. The vertical dashed line indicates the displacement year. The dotsrepresent the point estimates and the bars represent the 95 percent confidence intervals. All estimates control for apolynomial of age, worker fixed effects, calendar year fixed effects, and year relative to displacement (for k ≤ 0) andyear relative to reemployment (for k > 0) fixed effects. Robust standard errors are clustered by establishments.Figure A.10: Commuting Zone by Year Fixed Effects(a) Daily wage (log)-.3-.2-.10.1-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10Year(b) Commuting distance (log)-.10.1.2.3-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearNotes: Each plot depicts estimates of βk in equation (2.1) with dependent variables in subtitles. The sample comprisesa yearly panel of workers with full-time jobs on June 30. The vertical dashed line indicates the displacement year.The dots represent the point estimates and the bars represent the 95 percent confidence intervals. All estimatescontrol for a polynomial of age, worker fixed effects, calendar year fixed effects, and year relative to displacementfixed effects. We additionally control for commuting zone by year fixed effects. Robust standard errors are clusteredby establishments.117Figure A.11: Excluding Large Layoffs(a) Daily wage (log)-.3-.2-.10.1-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10Year(b) Commuting distance (log)-.10.1.2.3-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearNotes: Each plot depicts estimates of βk in equation (2.1) with dependent variables in subtitles. The sample comprisesa yearly panel of workers with full-time jobs on June 30. We exclude mass layoffs of more than 500 workers. Thevertical dashed line indicates the displacement year. The dots represent the point estimates and the bars representthe 95 percent confidence intervals. All estimates control for a polynomial of age, worker fixed effects, calendar yearfixed effects, and year relative to displacement fixed effects. Robust standard errors are clustered by establishments.Figure A.12: Excluding Multi-Location Establishments(a) Daily wage (log)-.3-.2-.10.1-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10Year(b) Commuting distance (log)-.10.1.2.3-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearNotes: Each plot depicts estimates of βk in equation (2.1) with dependent variables in subtitles. The sample comprisesa yearly panel of workers with full-time jobs on June 30. We exclude firms in finance, trade, and transportationindustries. The vertical dashed line indicates the displacement year. The dots represent the point estimates and thebars represent the 95 percent confidence intervals. All estimates control for a polynomial of age, worker fixed effects,calendar year fixed effects, and year relative to displacement fixed effects. Robust standard errors are clustered byestablishments.118Figure A.13: Alternative Measures of Commuting Time(a) Driving time (log)-.10.1.2.3-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10Year(b) Constant speed elasticity-.10.1.2.3-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearNotes: Panels (a)–(b) depict estimates of equation (2.1). The sample comprises a yearly panel of workers withfull-time jobs on June 30. Dependent variables: Panel (a) uses log driving time; Panel (b) uses commuting timepredicted from commuting distances, assuming a constant speed elasticity with respect to the distance of 0.4. Thevertical dashed line indicates the displacement year. The dots represent the point estimates and the bars representthe 95 percent confidence intervals. All estimates control for a polynomial of age, worker fixed effects, calendar yearfixed effects, and year relative to displacement fixed effects. Robust standard errors clustered by establishments.Figure A.14: Heterogeneous and Dynamic Effects(a) Daily wage (log)-.3-.2-.10.1-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10Year(b) Commuting distance (log)-.10.1.2.3-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearNotes: Each plot depicts estimates of βk in equation (2.1) with dependent variables in subtitles. The sample comprisesa yearly panel of workers with full-time jobs on June 30. We use the imputation method of Borusyak et al. (2024)to estimate the treatment effects. The vertical dashed line indicates the displacement year. The dots represent thepoint estimates and the bars represent the 95 percent confidence intervals. All estimates control for a polynomial ofage, worker fixed effects, calendar year fixed effects, and year relative to displacement fixed effects. Robust standarderrors are clustered by establishments.119Table A.1: Share of Commuters by Modes of Commuting and Distance SegmentsDistance (km) Walking (%) Cycling (%) Driving (%)≤0.2 94 5 10.2–0.4 81 11 80.4–0.6 64 19 170.6–0.8 56 21 230.8–1.0 38 19 431.0–1.5 25 19 561.5–2.0 18 17 652.0–3.0 10 14 763.0–5.0 4 9 875.0–7.0 1 6 937.0–10.0 1 4 9510.0–20.0 0 2 98>20.0 1 1 98Notes: The table lists the share of commuters by modes of commuting in 2002. Driving includes public transit,motorcycles, and private cars. Source: Table 2, Scheiner (2010).120Table A.2: Effects of Job Displacement on Labor Supply and Earnings(a) (b) (c)Regular employment Days in full-time jobs Days in part-time jobsML × Post -0.303*** -103.9*** 14.20***(0.005) (1.847) (0.904)Observations 4,593,491 4,593,491 4,593,491Workers 394,020 394,020 394,020R2 0.239 0.356 0.336(d) (e) (f)Days in mini-jobs Annual earnings (’000) AKM firm effectsML × Post 14.52*** -12.06*** -0.113***(0.606) (0.193) (0.004)Observations 4,593,491 4,593,491 4,314,221Workers 394,020 394,020 394,020R2 0.245 0.760 0.945Notes: Each column reports estimates of β in equation (2.3) with dependent variables in column titles. The samplecomprises a balanced yearly worker panel (except column (f) which comprises workers with full-time jobs on June 30).All estimates control for a polynomial of age, worker fixed effects, and calendar year fixed effects. Robust standarderrors in parentheses are clustered by establishments. (* p < 0.1; ** p < 0.05; *** p < 0.01)Table A.3: Additional Effects of Job Displacement(a) (b) (c)Daily wage Commuting distance Commuting across countiesML × Post -16.53*** 1.904*** 0.042***(0.474) (0.296) (0.008)Observations 4,316,096 4,316,096 4,316,096Workers 394,020 394,020 394,020R2 0.905 0.787 0.826(d) (e) (f)Commuting across cities Switching industries Switching occupationsML × Post 0.038*** 0.214*** 0.157***(0.007) (0.003) (0.003)Observations 4,316,096 4,316,096 4,316,096Workers 394,020 394,020 394,020R2 0.837 0.068 0.278Notes: Each column reports estimates of β in equation (2.3) with dependent variables in column titles. Samplescomprise a yearly panel of workers with full-time jobs on June 30. All estimates control for a polynomial of age, workerfixed effects, and calendar year fixed effects. Robust standard errors in parentheses are clustered by establishments.(* p < 0.1; ** p < 0.05; *** p < 0.01)121Table A.4: Effect Heterogeneity by Worker Demographics(a) (b)Daily wage (log) Commuting distance (log)A. GenderML × Post × Male -0.176*** 0.155***(0.006) (0.022)ML × Post × Female -0.228*** 0.129***(0.010) (0.034)Difference -0.053*** -0.026(0.010) (0.040)Observations 4,316,096 4,316,096Workers 394,020 394,020R2 0.898 0.817B. AgeML × Post × Young -0.164*** 0.160***(0.006) (0.023)ML × Post × Old -0.237*** 0.127***(0.008) (0.029)Difference -0.072*** -0.033(0.009) (0.035)Observations 4,316,096 4,316,096Workers 394,020 394,020R2 0.898 0.817C. Marital statusML × Post × Single -0.190*** 0.155***(0.006) (0.020)ML × Post × Married -0.189*** 0.120***(0.010) (0.042)Difference 0.001 -0.035(0.010) (0.044)Observations 4,315,987 4,316,096Workers 392813 394,020R2 0.898 0.817Notes: Each column reports subsample estimates of βk in equation (2.1) with dependent variables in column titles.The sample comprises a yearly panel of workers with full-time jobs on June 30, split by gender (panel A), age (panelB), and married versus single workers (panel C, Goldschmidt et al., 2017). Young and older workers are defined,respectively, by ages below and above the sample median in the year before displacement. All estimates control fora polynomial of age, worker fixed effects, and calendar year fixed effects. Robust standard errors in parentheses areclustered by establishments. (* p < 0.1; ** p < 0.05; *** p < 0.01)122Table A.5: Effect Heterogeneity by Pre-Layoff Firm Characteristics(a) (b)Daily wage (log) Commuting distance (log)A. AKM firm effectsML × Post × Low firm effect -0.150*** 0.107***(0.006) (0.027)ML × Post × High firm effect -0.233*** 0.196***(0.008) (0.026)Difference -0.083*** 0.089**(0.010) (0.038)Observations 4,316,096 4,316,096Workers 394,020 394,020R2 0.898 0.817B. AKM worker effectsML × Post × Low worker effect -0.191*** 0.161***(0.006) (0.023)ML × Post × High worker effect -0.181*** 0.126***(0.008) (0.030)Difference 0.010 -0.035(0.010) (0.037)Observations 4,316,096 4,316,096Workers 394,020 394,020R2 0.898 0.855C. Job tenureML × Post × Short tenure -0.171*** 0.095***(0.006) (0.020)ML × Post × Long tenure -0.258*** 0.338***(0.009) (0.038)Difference -0.087*** 0.243***(0.010) (0.041)Observations 4,316,096 4,316,096Workers 394,020 394,020R2 0.819 0.817Notes: Each column reports subsample estimates of βk in equation (2.1) with dependent variables in column titles.The sample comprises a yearly panel of workers with full-time jobs on June 30, split by AKM firm effects (panel A),AKM worker effects (panel B), and job tenure (panel C) in the pre-layoff job. Firm and worker effects are estimatedfrom a two-way fixed effects regression of log daily wages (Abowd et al., 1999) and split by the sample median in theyear before displacement. All estimates control for a polynomial of age, worker fixed effects, and calendar year fixedeffects. Robust standard errors in parentheses are clustered by establishments. (* p < 0.1; ** p < 0.05; *** p < 0.01)123Table A.6: Effect Heterogeneity by Labor Market Conditions(a) (b)Daily wage (log) Commuting distance (log)A. Urban/ruralML × Post × Rural -0.174*** 0.158***(0.007) (0.032)ML × Post × Urban -0.201*** 0.139***(0.006) (0.024)Difference -0.027*** -0.018(0.009) (0.040)Observations 4,316,096 4,316,096Workers 394,020 394,020R2 0.898 0.817B. Labor market concentrationML × Post × Low HHI -0.185*** 0.159***(0.006) (0.027)ML × Post × High HHI -0.210*** 0.266***(0.011) (0.036)Difference -0.025* 0.107**(0.013) (0.045)Observations 4,126,564 4,126,564Workers 373,740 373,740R2 0.891 0.823C. Local industry shareML × Post × Low share -0.201*** 0.161***(0.007) (0.025)ML × Post × High share -0.174*** 0.131***(0.007) (0.028)Difference 0.026*** -0.030(0.010) (0.038)Observations 4,316,096 4,316,096Workers 394,020 394,020R2 0.898 0.817Notes: Each column reports subsample estimates of βk in equation (2.1) with dependent variables in column titles.The sample comprises a yearly panel of workers with full-time jobs on June 30, split by urban versus rural residence(panel A), labor market concentration (panel B), and local industry share (panel C) of the pre-layoff job. Urbanversus rural residence is determined in the year before displacement. Labor market concentration is measured by theHerfindahl–Hirschman index (HHI) within commuting zones and industrial sectors, and split by the sample median.Local industry share is measured by the employment share of the displacing industry within the focal commutingzone, and split by industry-specific sample medians. All estimates control for a polynomial of age, worker fixed effects,and calendar year fixed effects. Robust standard errors in parentheses are clustered by establishments. (* p < 0.1;** p < 0.05; *** p < 0.01)124Table A.7: Robustness(a) (b)Daily wage (log) Commuting distance (log)A. Including part-time jobsML × Post -0.228*** 0.134***(0.006) (0.018)Observations 4,366,931 4,366,931Workers 394,020 394,020R2 0.881 0.807B. Displacement due to establishment closureML × Post -0.190*** 0.149***(0.005) (0.019)Observations 4,304,403 4,304,403Workers 391,722 391,722R2 0.898 0.817C. Selection into reemploymentML × Post -0.189*** 0.148***(0.005) (0.019)Observations 4,316,096 4,316,096Workers 394,020 394,020R2 0.898 0.817D. Commuting zone by year fixed effectsML × Post -0.189*** 0.152***(0.005) (0.018)Observations 4,316,096 4,316,096Workers 394,020 394,020R2 0.900 0.821E. Excluding large layoffsML × Post -0.182*** 0.161***(0.005) (0.020)Observations 3,822,703 3,822,703Workers 346,950 346,950R2 0.896 0.816F. Excluding multi-location establishmentsML × Post -0.176*** 0.211***(0.007) (0.026)Observations 3,699,967 3,699,967Workers 336,615 336,615R2 0.906 0.836Notes: Each column reports estimates of β in equation (2.3) with dependent variables in column titles. The samplecomprises a yearly panel of workers with full-time jobs on June 30 (except panel A, which includes part-time jobs).All estimates control for a polynomial of age, worker fixed effects, and calendar year fixed effects. Panel B usesestablishment closure as the reason for job displacement; Panel D additionally controls for commuting zone by yearfixed effects; Panel E excludes mass layoffs of more than 500 workers; Panel F excludes workers displaced fromfinance, trade, and transportation industries. Robust standard errors in parentheses are clustered by establishment(* p < 0.1; ** p < 0.05; *** p < 0.01).125Table A.8: Alternative Measures of Commuting Time(a) (b)Driving time (log) Commuting time (log)w/ const. speed elasticityML × Post 0.125*** 0.089***(0.016) (0.011)Observations 4,316,096 4,316,096Workers 394,020 394,020R2 0.817 0.817Notes: Each column reports estimates of β in equation (2.3) with dependent variables in column titles. The samplecomprises a yearly panel of workers with full-time jobs on June 30. All estimates control for a polynomial of age, workerfixed effects, and calendar year fixed effects. Robust standard errors in parentheses are clustered by establishment (*p < 0.1; ** p < 0.05; *** p < 0.01).126A.3 Trade off Wage Losses and Commuting CostsTo investigate the correlation between wage losses and commuting increases after job displacement,we extend equation (2.3) by including worker-specific random coefficientsY1,it = α1,iPostit + β1,i(MLi × Postit) +X ′itγ + ϕi + ψt + ϵ1,it, (A.2)Y2,it = α2,iPostit + β2,i(MLi × Postit) +X ′itγ + ϕi + ψt + ϵ2,it, (A.3)where Y1 and Y2 represent log daily wages and log commuting distances, respectively. The coeffi-cients (α1,i, β1,i, α2,i, β2,i) vary across workers. The outcome of interest is the correlation between(β1,i, β2,i).As Lachowska et al. (2023) suggest, OLS estimates of equations (A.2)–(A.3) do not yield con-sistent estimates of the random coefficients: If estimation errors in βˆ1,i and βˆ2,i are correlated,the estimated correlation between (βˆ1,i, βˆ2,i) will be contaminated and inconsistent for the truecorrelation. To remove the bias, we take a split-sample approach. First, we regress both outcomesagainst X ′it, ϕi, and ψt in the original equation (2.3) to partial out these terms. Second, we dividethe sample into G cells g = 1, 2, · · · , G by workers’ labor market regions, gender, age, and dailywages (below and above the median) before displacement. Imposing a minimum cell size of 20displaced workers, we obtain 287 cells in total. Then, we randomly split each cell into two sub-samples, estimating the wage effect β1,g on the first subsample and the commuting effect β2,g onthe second. For both outcomes, we regress the residualized dependent variables from the first stepagainst Postit and (MLi × Postit). Finally, we calculate the correlation coefficient across cells.Since estimation errors are independent across subsamples within each cell, this procedure removescorrelated estimation errors and gives a consistent estimator of the correlation of interest. Thebias-corrected Pearson correlation coefficient estimate is 0.060. In comparison, the uncorrectedOLS estimate without dividing the cells is 0.084. If we regress βˆ1,g against βˆ2,g across cells, theslope coefficient equals 0.018.Our approach is similar to Athey et al. (2023) who use machine learning to estimate the het-erogeneous effects of job displacement, but differs in two major ways. First, we are interested inthe correlation between the wage and commuting effects whereas Athey et al. (2023) estimate thedistribution of treatment effects on a single outcome. Second, Athey et al. (2023) find substantialheterogeneity in the earnings effects that is largely driven by differences in employment. In contrast,we find limited variation in the wage effects conditional on employment.127A.4 Model Proofs and ExtensionsA.4.1 Proof for Proposition 1Define ϑ ≡ y + a − cr. Then there exists S˜ : R → R such that S(θ) = S˜(ϑ) for all θ = (y, a, r).Following Appendix A.1, Part I of Jarosch (2023), S˜(ϑ) strictly increases in ϑ. Hence, S(θ) strictlyincreases in both y and a and strictly decreases in r.A.4.2 Proof for Proposition 2By Proposition 1, we can write ϑ = S˜−1(S(ϑ)). Define the set of job matches that generate surpluss as the following:Ls = {(v, r)|v − cr = S˜−1(s)}. (A.4)The expectation of v conditional on s is given byE[v|s] =∫LsydF (v, r|s), (A.5)where F (v, r|s) is the conditional distribution of (v, r) given Ls. By independence of v and r, thedensity function isf(v, r|s) = fv(v)fr(r)∫LsdF (v, r|s)=fv(v)fr(v − S˜−1(s)c)∫ ∞S˜−1(s)fv(v)fr(v − S˜−1(s)c) √2cdv. (A.6)Plug (A.6) into (A.5),v¯(s) =∫ ∞S˜−1(s)vfv(v)fr(v − S˜−1(s)c)dv∫ ∞S˜−1(s)fv(v)fr(v − S˜−1(s)c)dv≡ V1V2. (A.7)The derivatives of V1 and V2 with respect to s are, respectively,V ′1 = −g′(s)[∫ ∞S˜−1(s)vfv(v)cf ′r(v − S˜−1(s)c)dv + S˜−1(s)fv(S˜−1(s))fr(0)], (A.8)V ′2 = −g′(s)[∫ ∞S˜−1(s)fv(v)cf ′r(v − S˜−1(s)c)dv + fv(S˜−1(s))fr(0)]. (A.9)128Notice thatV ′1V2 − V ′2V1 = g′(s)fv(S˜−1(s))fr(0)∫ ∞S˜−1(s)(v − S˜−1(s))fv(v)fr(v − S˜−1(s)c)dv+g′(s)c[∫ ∞S˜−1(s)vfv(v)fr(v − S˜−1(s)c)dv∫ ∞S˜−1(s)fv(v)f′r(v − S˜−1(s)c)dv−∫ ∞S˜−1(s)fv(v)fr(v − S˜−1(s)c)dv∫ ∞S˜−1(s)vfv(v)f′r(v − S˜−1(s)c)dv].(A.10)The first line on the right-hand-side is non-negative because g is increasing and v = S˜−1(s) + cr ≥S˜−1(s). Meanwhile, dividing the second and third lines byA =g′(s)c(∫ ∞S˜−1(s)fv(v)fr(v − S˜−1(s)c)dv)2> 0, (A.11)yields, for some B > 0,V ′1V2 − V ′2V1A=BA+∫∞S˜−1(s) vfv(v)fr(v−S˜−1(s)c)dv∫∞S˜−1(s) fv(v)fr(v−S˜−1(s)c)dv︸ ︷︷ ︸E[v|s]×∫∞S˜−1(s) fv(v)f′r(v−S˜−1(s)c)dv∫∞S˜−1(s) fv(v)fr(v−S˜−1(s)c)dv︸ ︷︷ ︸E[f ′r(r)fr(r)∣∣∣s]−∫∞S˜−1(s) vfv(v)f′r(v−S˜−1(s)c)dv∫∞S˜−1(s) fv(v)fr(v−S˜−1(s)c)dv.︸ ︷︷ ︸E[vf ′r(r)fr(r)∣∣∣s](A.12)Along the curve Ls, v is increasing in r and decreasing in f′r(r)/fr(r). Thus,E[vf ′r(r)fr(r)∣∣∣∣ s]−E [ f ′r(r)fr(r)∣∣∣∣ s]E [v| s] = Cov(v, f ′r(r)fr(r)∣∣∣∣ s) < 0. (A.13)Putting everything together, we find∂E[v|s]∂s=V ′1V2 − V ′2V1V 22> 0. (A.14)The case of E[r|s] can be proved analogously.A.4.3 Endogenous Search EffortsSuppose that searching for jobs in a larger geographic area is more costly. While job offers aredrawn from the distribution Fθ, workers only receive those with r < r¯ if they exert an increasingand convex search cost q(r¯). Following Proposition 2, we assume that Fθ = FvFr.129With the search cost, the value function of unemployed workers becomesU = maxr¯{z − q(r¯) + β[λ0∫ r¯0∫ ∞cr′−S˜−1(0)W (v′, r′, u, u)dfv(v′)dFr(r′)+(1− λ0∫ r¯0∫ ∞cr′−S˜−1(0)dfv(v′)dFr(r′))U]},(A.15)The value function of employed workers isW (v, r, vˆ, rˆ) = maxr¯{w(v, r, vˆ, rˆ) + a− cr − q(r¯) + βδU + β(1− δ)×[λ1∫ r¯0∫ ∞cr′−S˜−1(S(v,r))W (v′, r′, v, r)dfv(v′)dFr(r′)+ λ1∫ r¯0∫ cr′−S˜−1(S(v,r))cr′−S˜−1(S(vˆ,rˆ))W (v, r, v′, r′)dfv(v′)dFr(r′)+(1− λ1∫ ∞cr′−S˜−1(S(vˆ,rˆ))dfv(v′)dFr(r′))W (v, r, vˆ, rˆ)]}.(A.16)Solving for the first-order conditions, we find the optimal search radius r¯∗ satisfiesq′(r¯∗) = αβλ0∫ ∞cr¯∗−S˜−1(0)S(v′, r¯∗)dfv(v′), (A.17)q′(r¯∗) = β(1− δ)λ1{α∫ ∞cr¯∗−S˜−1(S(v,r))(S(v′, r¯∗)− S(v, r)) dfv(v′)+ (1− α)∫ ∞cr¯∗−S˜−1(S(v,r))(S(v, r)− S(yˆ, rˆ)) dfv(v′)+(1− α)∫ cr¯∗−S˜−1(S(v,r))cr¯∗−S˜−1(S(vˆ,rˆ))(S(v′, r¯∗)− S(yˆ, rˆ)) dfv(v′)} ,(A.18)when the worker is unemployed and employed, respectively.The left-hand-sides of equations (A.17) and (A.18) represent the marginal cost of search, andthe right-hand-sides represent the present-value marginal payoff from search. In particular, the firsttwo lines on the right-hand-side of equation (A.18) indicate the increase in current job surplus andoutside options, respectively, when the worker moves to a new firm. The third line represents theincrease in outside options when she renegotiates wages with the incumbent firm. For α > 1/2, theright-hand-side of equation (A.18) decreases in both S(vˆ, rˆ) and S(v, r). Thus, the optimal searchradius decreases along the recovery from displacement.130A.4.4 Human Capital DynamicsSuppose that workers have ex-post heterogeneous human capital h ∈ H. Let h and h′ denote thehuman capital in the current and next periods, respectively. For employed workers, h′ follows aconditional distribution H1(h′|h). For unemployed workers, h′ follows H0(h′|h).With human capital dynamics, the wage bargaining rules in equations (2.5)–(2.7) become(for unemployed workers) W (θ, u, h)− U(h) = αS(θ, h). (A.19)(for job movers) W (θ2, θ1, h)− U(h) = S(θ1, h) + α(S(θ2, h)− S(θ1, h)). (A.20)(for wage renegotiation) W (θ1, θ2, h)− U(h) = S(θ2, h) + α(S(θ1, h)− S(θ2, h)). (A.21)The value functions becomeU(h) = z + β∫H{λ0∫M1(u,h′)W (x, u, h′)dFθ(x) + (1− λ0p1(u, h′))U(h′)}dH0(h′|h). (A.22)W (θ, θˆ, h) = w(θ, θˆ, h) + a− cr + β∫H{δU(h′) + (1− δ)[λ1∫M1(θ,h′)W (x, θ, h′)dFθ(x)+ λ1∫M2(θ,θˆ,h′)W (θ, x, h′)dFθ(x) + (1− λ1p3(θˆ, h′))W (θ, θˆ, h′)]}dH1(h′|h),(A.23)J(θ, θˆ, h) = y + h− w(θ, θˆ, h) + β(1− δ)∫H{λ1∫M2(θ,θˆ,h′)J(θ, x, h′)dFθ(x)+(1− λ1p3(θˆ, h′))J(θ, θˆ, h′)}dH1(h′|h).(A.24)Accordingly, the surplus function becomesS(θ, h) =W (θ, θˆ, h)− U(h) + J(θ, θˆ, h)= y + a+ h− cr − z + β(∫HU(h′)dH1(h′|h)−∫HU(h′)dH0(h′|h))+ β(1− δ)∫HS(θ, h′)dH1(h′|h)− αβλ0∫H∫M1(u,h′)S(x, h′)dFθ(x)dH0(h′|h)+αβ(1− δ)λ1∫H∫M1(θ,h′)(S(x, h′)− S(θ, h′)) dFθ(x)dH1(h′|h)}.(A.25)131A.5 Structural EstimationA.5.1 ImplementationTo estimate the job search model, we convert the IEB data described in Section 2.2 into a monthlypanel. As in the yearly panel data, we focus on the years 2000–2017, impose the age restriction of20–54 years old, and a maximum commuting distance of 100 kilometers.From the monthly data, we identify U-E transition if a worker has been unemployed for atleast three months and becomes full-time employed in the subsequent month. Analogously, E-Utransition is defined as a worker who has been employed consecutively for three months becomingunemployed in the next month. We identify E-E transition if a worker moves from one employerto another directly or with an unemployment gap of less than three months. In addition, we dropworker-month observations related to establishment closure, reorganization, and outsourcing.To solve the job search model, we approximate the distributions of Y and R by 40 grid pointseach on the unit interval. For each value of (ηy1, ηy2, ηr1, ηr2, ρyr), we first draw a random vector(U1, U2) from the unit square [0, 1]2. Both U1 and U2 follow a uniform distribution and their jointdistribution is given by a Gaussian copula with dependence parameter ρyr. Then we apply theinverse transformation on (U1, U2) to find (Y,R) with marginal beta distributions. After obtaining(y, r), we construct a and v for each value of y.Workers’ human capital is evaluated at 20 grids on the unit interval, and the initial distributionis set as uniform. In total, we solve for S and U at 1601 × 20 states, and W , w, and J at1601× 1601× 20 states.We use the model to simulate a monthly panel of 50,000 workers and 276 months (23 years)to obtain workers’ employment and wage trajectories. We drop the first 60 months (5 years) toisolate the impact of initial conditions. The remaining panel spans 18 years, corresponding to thelength of our actual data. Then we calculate data moments from the actual monthly panel andmodel moments from the simulated panel. Let ϕ ∈ Rk, M(ϕ) ∈ Rk, and Mˆ ∈ Rk denote thevectors of structural parameters, model moments, and data moments, respectively. We estimate ϕˆby minimizing the L2-distance between the model and data moments:ϕˆ = argminϕ(M(ϕ)− Mˆ)′Σ(M(ϕ)− Mˆ). (A.26)We use the identity matrix Σ = Ik×k as the weighting matrix.To simulate the effect of job displacement, we collapse the simulated monthly panel into a yearlypanel. Treated workers are those experiencing E-U transitions. Then we construct a control groupof workers without E-U transitions in the same year but with similar job tenure (matched by CEM)in the year before separation.132A.5.2 Identifying the Copula ParameterThe copula parameter ρcyr is identified by matching the correlation between y and r among potentialjob matches. Given (ηy1, ηy2, ηr1, ηr2, ρyr), we simulate one million pairs of (y, r) and calculatethe Pearson correlation coefficient ρyr as the model moment. To construct the data moment,we approximate the joint distribution of (y, r) using all firms’ AKM effects and the commutingdistances between all worker-firm pairs in the same labor market. We take the average across alllabor markets in our data.In our preferred specification, we define labor markets by commuting zones constructed usingworker-flow data (Glitz, 2012). This is because workers may switch occupations and industries.Table A.9, Panel A shows the correlation coefficient ρyr = −0.0181, which is close to zero. Thecorrelation between higher-order polynomials of y and r is also negligible, suggesting that y and rare not dependent in non-linear ways. Table A.9, Panel B shows similar results for labor marketsdefined by both geographical regions and industries.At first glance, the lack of correlation between firm productivity and commuting distances seemscounter-intuitive if workers and firms locate endogenously. For example, if productive firms andworkers sort into downtown whereas unproductive ones sort into peripheral areas, then both firms’and workers’ productivity will negatively correlate with commuting distances. This agglomerationeffect implies that the correlation is stronger in urban areas. However, Table A.9, Panels C–Dfind that the correlation between y and r are similarly negligible for urban and rural firms. TableA.10 further shows that the correlation coefficients between AKM worker effects and commutingdistances are close to zero as well. Hence, the results suggest limited spatial sorting by either firmsor workers.Nevertheless, the above findings are consistent with Schoefer and Ziv (2022) who find weakagglomeration in German local labor markets. The absence of dependence can be rationalized bya quantitative spatial model with location-specific production and residential amenities (Heblichet al., 2020). If the spatial distribution of production amenities is uncorrelated with residentialamenities, this may countervail the agglomeration forces and cause workers and firms to spreadover space. As such, the distribution of commuting distances may depend little on the specificlocation of firms or workers.A.5.3 Identifying Unemployment BenefitsThis section discusses an alternative approach to identifying the unemployment benefits z. Recallin equation (2.11) that the surplus function decreases in z. In the simpler case with homogeneousworkers, we can identify z from the position of the reservation wage curve in the w-r space. Asshown in Figure A.16, a higher reservation wage curve (the dark blue line) truncates the support of(w, r) more heavily than a lower reservation wage curve. In panel (a), the curve passes the origin,so that the truncated job match distribution has a triangular support. In contrast, the reservationwage curve in panel (b) crosses the v-axis below the origin, and the truncated distribution has atrapezoidal support.133We empirically distinguish the two scenarios by running a threshold regression of w against r(Hansen, 2000). The dashed red lines in Figure A.16 depict the hypothetical fitting lines. In panel(b), the threshold is strictly positive corresponding to the shape of the trapezoidal support. Theestimated slope to the left of the threshold represents the untruncated correlation between w andr, and the slope to the right becomes more positive due to truncation. In panel (a), however, thedistribution is truncated for all r > 0 and there is no positive threshold.Using all first jobs of displaced workers, we estimate this threshold model and cannot reject athreshold at r = 0. Thus, we choose z such that S((v, 0), h1) = 0, so that S((v, 0), h) < 0 for allr > 0 and h ≥ h1.A.5.4 Sensitivity AnalysisIn Figure A.17, we plot the estimated c given different values of (ρcyr, κ1) ∈ [−0.05, 0] × [0, 10−3].The ranges are chosen to cover the baseline values ρcyr = −0.02, κ1 = 0.55 × 10−3 in Table 2.5.At each pair of (ρcyr, κ1), we take both parameters as given and estimate the remaining modelparameters by matching their respective moments.Within this range of (ρcyr, κ1), our estimated cˆ is bounded between 1.309 and 1.460, a narrowinterval around the baseline estimates (see Table 2.6, columns (a)–(b)). The estimate decreasesin the value of ρcyr and increases in κ1. On the one hand, if more productive firms are closerto workers, the difference in wages and commuting distances between two arbitrary jobs is morelikely explained by different surplus levels. Hence, the greater downward bias in the OLS estimateneeds to be countervailed by a larger WTP. On the other hand, if productivity and wages are morecorrelated with non-wage amenities, workers would compensate for longer commuting distanceswith greater wages and non-wage amenities at the same time, so the correlation between wages anddistances would capture a smaller portion of the WTP. Again, a greater WTP is required to matchthe OLS estimate.Moreover, the above results allow us to partially identify cˆ without knowing the specific valuesof (ρcyr, κ1). Generally assume that firm productivity is negatively correlated with commutingdistances due to agglomeration or spatial sorting, and positively correlated with non-wage amenities(Sockin, 2022; Maestas et al., 2023). Then the estimate cˆ = 1.309 at ρcyr = κ1 = 0 (ρyr = ρya = 0)yields a lower bound of the true WTP. In this case, we would ignore any correlation between jobattributes, but the estimate does not differ from our baseline result cˆ = 1.365 by more than fivepercent. Therefore, without making any quantitative assumption on the dependence structure ofthe job offer distribution Fθ, we still find a large WTP for less commuting that is close to ourbaseline estimate. The large lower bound estimate also suggests that most discrepancy between thestructural and OLS estimates of the WTP is caused by job search friction and utility dispersionacross jobs.134Figure A.15: Identifying the Commuting Cost(a) High commuting cost wrReservation wage OLS fitting line(b) Low commuting cost wrReservation wage OLS fitting lineNotes: Panels (a)–(b) illustrate the effects of high and low commuting costs (slopes of the reservation value curve) onthe distribution of realized job matches, respectively. In each panel, the shaded area represents the support of realizedjob matches in the w-r space. The dark blue line represents the reservation wage curve. The red line represents theOLS fitting line from a regression of w against r using realized job matches.Figure A.16: Identifying Unemployment Benefits(a) Zero threshold wrReservation wage OLS fitting line(b) Positive threshold wrReservation wage OLS fitting lineNotes: Panels (a)–(b) plot two scenarios with different values of z which yield different positions of the reservationwage curves. The dark blue lines represent the reservation wage curves. The shaded areas represent the support ofrealized job matches. The dashed red lines represent the fitting lines from threshold regressions.135Figure A.17: Sensitivity AnalysisNotes: The figure plots the SMM estimate of c at different values of (ρcyr, κ1) ∈ [−0.05, 0] × [0, 10−3]. The rangesare set to cover the baseline values of (ρcyr, κ1) = (−0.02, 0.55 × 10−3) (see Table 2.5). At each pair of (ρyr, κ1), weestimate c and the remaining model parameters by SMM while ignoring the moment related to ρyr. The estimatedc reaches the minimum of 1.309 at (ρcyr, κ1) = (0, 0) and the maximum of 1.460 at (ρcyr, κ1) = (−0.05, 10−3).136Figure A.18: Simulated Effects of Job Displacement with Remote Work(a) Daily wage (log)-.3-.2-.10-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearBaseline Remote work(b) Commuting distance (log)-.10.1.2.3.4-4 -3 -2 -1 0 1 2 3 4 5 6 7 8 9 10YearBaseline Remote workNotes: Each plot depicts estimates of equation (2.1) with dependent variable in the subtitle. The red lines replicateestimates from simulated data in Figure 2.7. The light blue lines show estimates from simulated data assuming c = 0(resulting from remote work). All estimates for worker fixed effects and year relative to displacement fixed effects.Robust standard errors clustered by establishments.137Table A.9: Dependence between AKM Firm Effects and Commuting Distancesy y2 y3 y4A. Commuting zonesr -0.0181 0.0021 -0.0005 -0.0037r2 -0.0182 0.0034 -0.0016 -0.0024r3 -0.0167 0.0038 -0.0020 -0.0016r4 -0.0151 0.0039 -0.0022 -0.0011B. Commuting zones × industriesr -0.0237 0.0037 -0.0078 0.0045r2 -0.0237 0.0053 -0.0092 0.0058r3 -0.0216 0.0060 -0.0094 0.0064r4 -0.0193 0.0061 -0.0090 0.0063C. Commuting zones: urbanr -0.0022 -0.0043 0.0051 -0.0069r2 -0.0026 -0.0031 0.0043 -0.0060r3 -0.0021 -0.0023 0.0035 -0.0050r4 -0.0018 -0.0017 0.0028 -0.0040D. Commuting zones: ruralr -0.0315 0.0156 -0.0148 0.0103r2 -0.0306 0.0154 -0.0144 0.0099r3 -0.0280 0.0142 -0.0131 0.0089r4 -0.0254 0.0130 -0.0118 0.0079Notes: This table reports Pearson correlation coefficients between polynomials of AKM firm effects y and polynomialsof commuting distance r between displaced workers and firms. Panel A: all potential job matches in the samecommuting zone; Panel B: potential job matches in the same commuting zone and industry; Panel C: potential jobmatches in the same commuting zone with urban firms; Panel D: potential job matches in the same commuting zonewith rural firms.138Table A.10: Dependence between AKM Worker Effects and Commuting Distancesyp y2p y3p y4pA. Commuting zonesr 0.0027 0.0030 0.0033 0.0037r2 0.0028 0.0031 0.0035 0.0040r3 0.0027 0.0031 0.0036 0.0041r4 0.0026 0.0030 0.0034 0.0039B. Commuting zones × industriesr -0.0038 -0.0038 -0.0038 -0.0036r2 -0.0034 -0.0032 -0.0028 -0.0024r3 -0.0031 -0.0027 -0.0022 -0.0016r4 -0.0029 -0.0024 -0.0018 -0.0011C. Commuting zones: urbanr 0.0261 0.0269 0.0276 0.0282r2 0.0280 0.0289 0.0296 0.0302r3 0.0283 0.0291 0.0297 0.0302r4 0.0273 0.0280 0.0286 0.0290D. Commuting zones: ruralr 0.0002 0.0003 0.0004 0.0007r2 -0.0045 -0.0043 -0.0004 -0.0036r3 -0.0074 -0.0071 -0.0067 -0.0062r4 -0.0090 -0.0086 -0.0082 -0.0076Notes: This table reports Pearson correlation coefficients between polynomials of AKM worker effects y˜ and polyno-mials of commuting distance r between displaced workers and firms. Panel A: all potential job matches in the samecommuting zone; Panel B: potential job matches in the same commuting zone and industry; Panel C: potential jobmatches in the same commuting zone with urban workers; Panel D: potential job matches in the same commutingzone with rural workers.139Appendix BAppendices to Chapter 3B.1 Distance to the Nearest Subway StationAn apartment can have more than one record due to upward or downward price adjustments orchanging sales status, for both of which we observe a timestamp for the change. For each record,we define distance as that between the apartment and the nearest subway station that is openwhen the price record is created. Seventy percent of the apartments only have one price record.Their distances to subway stations are calculated only once and do not vary with time. But forapartments with multiple records, it is possible their distances to the subway will vary with time:The distances typically decrease when a new and closer subway station is built. However, thedistances do not change if the new station is further away from the apartment or its opening fallsoutside the listing period of the apartment. In the following paragraph, we give several examplesto illustrate this idea.As shown in Table B.1, suppose an apartment has three price records [1]-[3], created on May15, June 15, and July 15, 2017, respectively. Before May 31, 2017, the nearest subway station (S0)to this apartment is 2.5 kilometers away. On June 1, 2017, a new subway line is built, and a newstation (S1) 1.5 kilometers away from the apartment comes into use. Opening at the same timeis another new station (S2) 3.5 kilometers away. On September 1, 2017, a third new station (S3)one kilometer away comes into use. In this case, the apartment’s three observations [1]-[3] willhave different distances to the subway. Observation [1]’s distance to the subway is 2.5 kilometers.Observation [2]’s distance is 1.5 kilometers (the opening of S2 did not play a role because it wasfurther from the apartment than S0). Finally, observation [3]’s distance to the subway remains at1.5 kilometers because S3 opened after [3] is created.Table B.1: Measuring Distance to the SubwayPrice records (date and matched distance)Station Open date Distance from [1] [2] [3]apartment May 15, 2017 Jun 15, 2017 Jul 15, 2017S0 May 1, 2017 2.5 km 2.5 kmS1 Jun 1, 2017 1.5 km 1.5kmS2 Jun 1, 2017 3.5 kmS3 Sep 1, 2017 1 km 1.5 km140B.2 Implied Reduction of Commuting CostsThe calculation method is as follows. For each apartment listed after the entry, we use the estimatesin Table 3.3, Column (a) to obtain the predicted total price (predicted price per m2× apartment size)and the counterfactual total price assuming no entry of bike sharing. Then we treat the differencebetween the predicted and counterfactual total prices as the total reduction in commuting costsand amortize it into 30, 40, 50, 60, and 70 years of annual values. Table B.2, columns (a) and(b) report the resulting cost per year using the compound interest rate for 5-year fixed deposits(2.86 percent per annum) and 5-year treasury bills (3.86 percent per annum) as discounter factors,respectively. The exchange rate between CNY and USD is 6.7:1.Table B.2: Reduction in Commuting Costs per Year(a) (b)Duration Discount factor 2.86% Discount factor 3.86%30 years 1,893 CNY, or 282 USD 2127 CNY, or 317 USD40 years 1,597 CNY, or 238 USD 1,851 CNY, or 276 USD50 years 1,429 CNY, or 213 USD 1,700 CNY, or 254 USD60 years 1,324 CNY, or 198 USD 1,610 CNY, or 240 USD70 years 1,255 CNY, or 187 USD 1,554 CNY, or 232 USD141B.3 Additional Figures and TablesFigure B.1: Exogenous Entry of Bike Sharing: Predictive Power of City Characteristics(a) Population (b) GDP(c) Subway Ridership (d) Housing PriceNotes: The figure plots the coefficient estimates of θt by month and pre-entry city characteristics in equation (3.5)with 95 percent confidence intervals. City characteristic variables are standardized to have zero mean and unitstandard deviation. The test specification follows Zervas et al. (2017).142Figure B.2: Monthly Average Prices of Resale and Rental Apartments3456Rental price per month ('000 CNY)10203040Sales price per m2 ('000 CNY)2015m7 2016m1 2016m7 2017m1 2017m7 2018m1Resale price Rental priceNotes: The sample comprises resale and rental apartments in 10 Chinese cities, initially listed between July 1, 2015and December 31, 2017, and within 3 km of a subway station. The blue dots depict the average price per m2of resaleapartments. The red dots depict the average monthly rents of rental apartments. The grey vertical lines representthe housing market regulations on March 25, 2016, September 30, 2016, and March 20, 2017, respectively.143Table B.3: Effect Heterogeneity across Cities(a) (b) (c) (d) (e)Variables Beijing Chengdu Chongqing Dalian HangzhouDistance to subway -0.053*** -0.041*** -0.009 -0.054*** -0.039*(0.007) (0.008) (0.006) (0.010) (0.020)Distance × bike sharing 0.030*** 0.002 0.015** 0.004 0.012(0.005) (0.011) (0.006) (0.006) (0.015)Observations 105,543 84,579 53,224 55,790 33,313Apartments 62,689 53,294 35,650 32,457 19,562Subway stations 285 100 117 62 56Adjusted R2 0.75 0.54 0.51 0.57 0.64(f) (g) (h) (i) (j)Variables Nanjing Shanghai Shenzhen Tianjin WuhanDistance to subway -0.024* -0.065*** -0.028*** -0.068*** -0.046***(0.014) (0.006) (0.008) (0.009) (0.008)Distance × bike sharing -0.009 0.036*** 0.021*** 0.001 0.017***(0.011) (0.005) (0.005) (0.005) (0.006)Observations 56,564 60,681 62,419 55,045 50,113Apartments 34,073 59,031 37,816 29,969 35,299Subway stations 121 294 163 102 122Adjusted R2 0.60 0.65 0.60 0.67 0.60Notes: Columns (a)–(j) report city-specific estimates of equation (3.1) with apartment price per m2(log) as thedependent variable. Samples comprise resale apartments in each city, initially listed between July 1, 2015 andDecember 31, 2017, and within 3 km of a subway station. All estimates control for apartment characteristics,apartment density, indicators of initial and last prices, subway station fixed effects, and month fixed effects. Robuststandard errors clustered by subway stations in parentheses. (* p < 0.1, ** p < 0.05, *** p < 0.01)144Table B.4: Exogenous Entry of Bike Sharing: The Hazard Rate Test(a) (b)Variables Coefficient Hazard ratioEnd-of-year population -0.380 0.684(1.247) (0.853)Annual GDP 1.741 5.701(1.779) (10.14)Annual subway ridership 4.045* 57.12(2.416) (138.0)Annual average housing price 0.613 1.846(0.712) (1.314)Observations 125 125Cities 10 10Log pseudo-likelihood -13.30 -13.30Notes: Estimated by a hazard rate model using Stata routine, stcox. The sample comprises city-year months fromJanuary 2016 to the entry month of bike sharing. The dependent variable is an indicator of the entry of bike sharing.Explanatory variables are standardized to zero mean and unit standard deviation. Column (a) reports the coefficients;column (b) reports the respective hazard ratios. Robust standard errors clustered by city in parentheses. (* p < 0.1,** p < 0.05, *** p < 0.01)Table B.5: Exogenous Entry of Bike Sharing: Randomized Entry Dates(a) (b) (c) (d)Randomized Randomized Randomized RandomizedVariables by cities by stations by apartments by observationsDistance -0.040*** -0.041*** -0.040*** -0.040***(0.004) (0.003) (0.003) (0.003)Distance × bike sharing 0.005 0.008** 0.006*** 0.005(0.004) (0.003) (0.002) (0.003)Observations 617,271 617,271 617,271 617,271Apartments 399,840 399,840 399,840 399,840Stations 1,422 1,422 1,422 1,422R-squared 0.91 0.91 0.91 0.98Notes: Columns (a)–(d) report estimates of equation (3.1) with apartment price per m2(log) as the dependent variable.The sample comprises resale apartments in 10 Chinese cities, initially listed between July 1, 2015 and December 31,2017, and within 3 km of a subway station. In each column, respectively, the entry date of bike sharing to each city,subway station, apartment, and price record is randomized by a uniform distribution from July 1, 2015 to March12, 2018. All estimates control for apartment characteristics, apartment density, indicators of initial and last prices,subway station fixed effects, and city-month fixed effects. Robust standard errors clustered by subway stations inparentheses. (* p < 0.1, ** p < 0.05, *** p < 0.01)145Appendix CAppendices to Chapter 4C.1 Additional Figures and TablesFigure C.1: SBD Phase-out Schedule and Size Distribution of SBD Claimants(a) Phase-out schedule14710131619Federal Tax Rate (%)0100300500700900Taxable Income ('000)0 5 10 15 20Taxable Capital (Million)Taxable Income ('000) Federal Tax Rate (%)(b) Distribution of total assets among SBD claimants020406080100Percent0 5 10 15 20Total Assets (Million)PDFCDFNotes: Panel (a) shows the phase-out schedule for the SBD. At each level of taxable capital (x-axis), the navy lineindicates how much of a firm’s taxable income is qualified for the lower federal tax rate of 11 percent (y-axis on theleft), and the red line indicates the average federal corporate income tax rate after SBD (y-axis on the right). Weassume that the firm’s taxable income is 500,000 CAD. Panel (b) shows the probability distribution function (PDF)and cumulative distribution function (CDF) of total assets among SBD claimants in 2013. About 99 percent of firmsthat claimed small business deductions had total assets below 10 million CAD.146Figure C.2: Firm Entry and Exit05101520Entry and Exit Rate (%)2011 2012 2013 2014 2015 2016 2017YearTreated: Entry Rate Control: Entry RateTreated: Exit Rate Control: Exit RateNotes: This figure shows the share of firms entering or exiting our sample each year in 2011–2017. The dark navylines indicate treated firms in the M&P sector in Quebec, and the red lines indicate control firms in non-M&P sectorsor in British Columbia (B.C.) or Ontario. The solid lines indicate entry rates and the dashed lines indicate exit rates.147Table C.1: Corporate Income Tax RatesProvince Firm type 2009 2010 2011 2012 2013 2014 2015 2016 2017FederalGeneral (M&P) 19 18 16.5 15 15 15 15 15 15General (non-M&P) 19 18 16.5 15 15 15 15 15 15Small (M&P) 11 11 11 11 11 11 11 10.5 10.5Small (non-M&P) 11 11 11 11 11 11 11 10.5 10.5QuebecGeneral (M&P) 11.9 11.9 11.9 11.9 11.9 11.9 11.9 11.9 11.8General (non-M&P) 11.9 11.9 11.9 11.9 11.9 11.9 11.9 11.9 11.8Small (M&P) 8 8 8 8 8 6 4 4 4Small (non-M&P) 8 8 8 8 8 8 8 8 8BritishColumbiaGeneral (M&P) 11 10.5 10 10 11 11 11 11 11General (non-M&P) 11 10.5 10 10 11 11 11 11 11Small (M&P) 2.5 2.5 2.5 2.5 2.5 2.5 2.5 2.5 2Small (non-M&P) 2.5 2.5 2.5 2.5 2.5 2.5 2.5 2.5 2OntarioGeneral (M&P) 12 10 10 10 10 10 10 10 10General (non-M&P) 14 12 11.5 11.5 11.5 11.5 11.5 11.5 11.5Small (M&P) 5.5 4.5 4.5 4.5 4.5 4.5 4.5 4.5 4.5Small (non-M&P) 5.5 4.5 4.5 4.5 4.5 4.5 4.5 4.5 4.5AlbertaGeneral (M&P) 10 10 10 10 10 10 12 12 12General (non-M&P) 10 10 10 10 10 10 12 12 12Small (M&P) 3 3 3 3 3 3 3 3 2Small (non-M&P) 3 3 3 3 3 3 3 3 2ManitobaGeneral (M&P) 12 12 12 12 12 12 12 12 12General (non-M&P) 12 12 12 12 12 12 12 12 12Small (M&P) 1 0 0 0 0 0 0 0 0Small (non-M&P) 1 0 0 0 0 0 0 0 0New BrunswickGeneral (M&P) 12 11 10 10 12 12 12 14 14General (non-M&P) 12 11 10 10 12 12 12 14 14Small (M&P) 5 5 5 4.5 4.5 4.5 4 3.5 3Small (non-M&P) 5 5 5 4.5 4.5 4.5 4 3.5 3Nova ScotiaGeneral (M&P) 16 16 16 16 16 16 16 16 16General (non-M&P) 16 16 16 16 16 16 16 16 16Small (M&P) 5 5 4.5 4 3.5 3 3 3 3Small (non-M&P) 5 5 4.5 4 3.5 3 3 3 3Newfoundlandand LabradorGeneral (M&P) 5 5 5 5 5 5 5 15 15General (non-M&P) 14 14 14 14 14 14 14 15 15Small (M&P) 5 4 4 4 4 3 3 3 3Small (non-M&P) 5 4 4 4 4 3 3 3 3NorthwestTerritoriesGeneral (M&P) 11.5 11.5 11.5 11.5 11.5 11.5 11.5 11.5 11.5General (non-M&P) 11.5 11.5 11.5 11.5 11.5 11.5 11.5 11.5 11.5Small (M&P) 4 4 4 4 4 4 4 4 4Small (non-M&P) 4 4 4 4 4 4 4 4 4NunavutGeneral (M&P) 12 12 12 12 12 12 12 12 12General (non-M&P) 12 12 12 12 12 12 12 12 12Small (M&P) 4 4 4 4 4 4 4 4 4Small (non-M&P) 4 4 4 4 4 4 4 4 4Prince EdwardIslandGeneral (M&P) 16 16 16 16 16 16 16 16 16General (non-M&P) 16 16 16 16 16 16 16 16 16Small (M&P) 2.1 1 1 1 4.5 4.5 4.5 4.5 4.5Small (non-M&P) 2.1 1 1 1 4.5 4.5 4.5 4.5 4.5SaskatchewanGeneral (M&P) 10 10 10 10 10 10 10 10 9.5General (non-M&P) 12 12 12 12 12 12 12 12 11.5Small (M&P) 4.5 4.5 2 2 2 2 2 2 2Small (non-M&P) 4.5 4.5 2 2 2 2 2 2 2YukonGeneral (M&P) 2.5 2.5 2.5 2.5 2.5 2.5 2.5 2.5 2.5General (non-M&P) 15 15 15 15 15 15 15 15 12Small (M&P) 4 4 4 2.5 2.5 1.5 1.5 1.5 1.5Small (non-M&P) 4 4 4 4 4 3 3 3 2148Table C.2: Entrant Earnings and Worker Composition(1) (2) (3) (4)Annual earnings (log) Male share Average age Full-timeof entrantsPost × MP × QC 0.0184*** -0.0005 -0.0261 0.0044**(0.0067) (0.0012) (0.0527) (0.0019)Mean dep. var. 25.7 0.697 44.3 0.743Observations 1,155,455 1,935,580 1,931,270 12,740,900Firms/workers (treated) 9,975 9,965 9,965 115,330Firms/workers (control) 329,345 328,640 328,535 2,623,440Adjusted R2 0.698 0.917 0.881 0.472Notes: Columns (a)–(c) report estimates of θτ from equation (4.2) with dependent variables in column titles. De-pendent variables are aggregated from worker-level data to the firm-year level. All estimates control for firm fixedeffects and year fixed effects. Column (d) reports estimates of θτ from equation (4.4) with the indicator of full-timejob as the dependent variable. The estimates control for worker fixed effects and year fixed effects. Samples compriseCCPCs (and their workers) with total assets below 10 million CAD and located in Quebec, British Columbia, andOntario in 2011–2017. Robust standard errors clustered by firms (columns (a)–(c)) or by firms and workers (column(d)) in parentheses. (* p < 0.1, ** p < 0.05, *** p < 0.01)Table C.3: Other Firm Outcomes(a) (b) (c) (d)Intangible Investment in Operating Total debtsassets (log) computers (’000) expenses (’000) (’000)Post × MP × QC 0.0468*** 0.7740*** 72.5861*** 27.4833***(0.0128) (0.1515) (6.2289) (1.8470)Mean dep. var. 16.2 7.1 1532.6 552.6Observations 2,010,400 2,111,875 1,341,780 2,106,660Firms (treated) 10,160 10,160 8,640 10,205Firms (control) 339,810 340,285 261,455 343,235Adjusted R2 0.903 0.414 0.935 0.897Notes: Columns (a)–(d) report estimates of θ from equation (4.1) with dependent variables in column titles. Samplescomprise CCPCs with total assets below 10 million CAD and located in Quebec, British Columbia, and Ontario in2011–2017. Intangible assets are measured in book value, net of amortization. Investment in computers is calculatedusing separate data on firms’ capital cost allowance of related asset classes. All estimates control for firm fixed effectsand year fixed effects. Robust standard errors clustered by firms in parentheses. (* p < 0.1, ** p < 0.05, *** p < 0.01)149Table C.4: Owner Outcomes(a) (b)Dividends income Share ownedPost × MP × QC -0.3297 0.0004(0.2636) (0.0018)Mean dep. var. 13.0 0.562Observations 1,654,425 2,420,885Firms (treated) 8,300 8,110Firms (control) 286,675 270,235Adjusted R2 0.638 0.892Notes: Columns (a) report estimates of θ from equation (4.1) with individual owners’ dividends income averagedby firms as the dependent variables. Columns (b) report estimates of θ from equation (4.3) with individual owners’shares owned as the dependent variables. Samples comprise CCPCs (and their owners) with total assets below 10million CAD and located in Quebec, British Columbia, and Ontario in 2011–2017. All estimates control for firm fixedeffects and year fixed effects. Robust standard errors clustered by firms in parentheses. (* p < 0.1, ** p < 0.05, ***p < 0.01)Table C.5: Tax Effects on Workers with and without Ownership(a) (b)Annual earnings (log) Annual earnings (log)of owner workers of non-owner workersPost × MP × QC 0.0066 0.0153***(0.0071) (0.0029)Mean dep. var. 58.6 35.6Observations 1,183,225 5,509,505Workers (treated) 7,425 56,825Workers (control) 181,500 888,950Adjusted R2 0.751 0.454Notes: Columns (a)–(b) report estimates of θτ from equation (4.4) with dependent variables in column titles. Samplescomprise CCPCs with total assets below 10 million CAD and located in Quebec, British Columbia, and Ontarioin 2011–2017. Part-time workers with annual earnings below 4,000 CAD, multiple-job holders, and workers notcontinuously employed by the same firm in 2011–2013 are excluded. All estimates control for firm fixed effects andyear fixed effects. Robust standard errors clustered by firms (columns (a)–(c)) or by firms and workers (column (d))in parentheses. (* p < 0.1, ** p < 0.05, *** p < 0.01)150Table C.6: Summary Statistics: High-Growth versus Low-Growth IndustriesQuebec B.C./Ontario(1) (2) (3) (4)High-growth Low-growth High-growth Low-growthA. FirmsTangible assets (’000) 399.6 409.8 329.5 369.1Total revenue (’000) 1,353.4 1,250.0 1,274.2 1,149.0Employment 7.0 10.0 6.4 9.1Average payroll (’000) 23.6 22.3 23.8 21.6EBITDA per worker (’000) 13.1 6.3 11.0 5.9After-tax profits (’000) 44.0 30.2 37.1 24.8Taxable income (’000) 57.0 43.3 47.6 35.4Provincial income tax rates 0.082 0.076 0.043 0.042Federal income tax rates 0.085 0.086 0.088 0.086Firm age 12.0 12.5 11.4 11.6Observations 148,855 153,995 326,155 325,345Firms 54,500 55,930 122,355 120,615B. WorkersAnnual earnings (’000) 41.6 30.9 47.7 34.9Age 44.5 43.1 44.9 43.4Male 0.737 0.557 0.707 0.547Observations 530,510 669,455 1,016,630 1,187,505Workers 176,835 223,155 338,880 395,835Notes: Panels A and B report summary statistics for firms and workers, respectively, by province and high-growthversus low-growth industries. The firm sample comprises CCPCs (and their workers) with total assets below 10million CAD and located in Quebec, British Columbia (B.C.), and Ontario in 2011–2013. The worker samplecomprises workers at those CCPCs, excluding part-time workers with annual earnings below 4,000 CAD, multiple-jobholders, and workers not continuously employed by the same firm in 2011–2013. The book value of tangible assets,net of depreciation, represents a firm’s capital stock. EBITDA is earnings before interest, taxes, depreciation, andamortization. After-tax profits are firms’ net income after taxes and extraordinary items. Provincial and federalincome tax rates are the firm’s provincial and federal taxes (reported as Part I tax) payable, respectively, scaled bytaxable income.151Table C.7: Tax Effects by High-Tech versus Low-Tech Industries(a) (b) (c) (d)Employment Average Tangible Annual(log) payrolls (log) assets (log) earnings (log)Post × MP × QC (low-tech) 0.0122** 0.0160** 0.0266*** 0.0122***(0.0055) (0.0066) (0.0088) (0.0027)Post × MP × QC (high-tech) 0.0579*** 0.0813*** 0.0724*** 0.0238***(0.0151) (0.0182) (0.0236) (0.0069)Difference 0.0456*** 0.0654*** 0.0458* 0.0116(0.0159) (0.0191) (0.0249) (0.0072)Mean Dep. Var. (low-tech) 11.5 34.8 807.3 37.3Mean Dep. Var. (high-tech) 11.1 42.4 660.8 46.4Observations 2,106,660 2,106,660 2,011,725 6,692,730Firms/Workers (treated) 10,205 10,205 10,165 64,250Firms/Workers (control) 343,235 343,235 339,825 1,070,455Adjusted R2 0.917 0.888 0.938 0.813Notes: Columns (a)–(c) report estimates of θτ from equation (4.2) with dependent variables in column titles. Allestimates control for firm fixed effects and year fixed effects. Column (d) reports estimates of θτ from equation (4.4)with log annual earnings as the dependent variable. The estimates control for worker fixed effects and year fixedeffects. Samples comprise CCPCs (and their workers) with total assets below 10 million CAD and located in Quebec,British Columbia, and Ontario in 2011–2017. Part-time workers with annual earnings below 4,000 CAD, multiple-jobholders, and workers not continuously employed by the same firm in 2011–2013 are excluded. We estimate equations(4.2) and (4.4) for treated firms (and workers) in high-tech and low-tech industries both relative to the control groupand compare the difference between the two estimates. Robust standard errors clustered by firms (columns (a)–(c))or by firms and workers (column (d)) in parentheses. (* p < 0.1, ** p < 0.05, *** p < 0.01)152Table C.8: Tax Effects by Pre-Reform Leverage Ratio(a) (b) (c) (d)Employment Average Tangible Annual(log) payrolls (log) assets (log) earnings (log)Post × MP × QC (low-leverage) 0.0207*** 0.0250*** 0.0323*** 0.0084**(0.0067) (0.0080) (0.0115) (0.0033)Post × MP × QC (high-leverage) 0.0233*** 0.0329*** 0.0447*** 0.0187***(0.0084) (0.0103) (0.0126) (0.0038)Difference 0.0025 0.0079 0.0124 0.0103**(0.0107) (0.0130) (0.0169) (0.0051)Mean dep. var. (low-leverage) 12.4 39.1 876.4 39.1Mean dep. var. (high-leverage) 10.1 31.2 672.5 37.2Observations 2,106,660 2,106,660 2,011,725 6,692,730Firms/workers (treated) 10,205 10,205 10,165 64,250Firms/workers (control) 343,235 343,235 339,825 1,070,455Adjusted R2 0.917 0.889 0.938 0.814Notes: Columns (a)–(c) report estimates of θτ from equation (4.2) with dependent variables in column titles. Allestimates control for firm fixed effects and year fixed effects. Column (d) reports estimates of θτ from equation (4.4)with log annual earnings as the dependent variable. The estimates control for worker fixed effects and year fixedeffects. Samples comprise CCPCs (and their workers) with total assets below 10 million CAD and located in Quebec,British Columbia, and Ontario in 2011–2017. Part-time workers with annual earnings below 4,000 CAD, multiple-jobholders, and workers not continuously employed by the same firm in 2011–2013 are excluded. We estimate the taxeffects separately on firms (and workers) with leverage ratios below and above the sample median in 2013 and comparethe difference between the two estimates. Robust standard errors clustered by firms (columns (a)–(c)) or by firmsand workers (column (d)) in parentheses. (* p < 0.1, ** p < 0.05, *** p < 0.01)153Table C.9: Tax Effects by Pre-Reform Capital Intensity(a) (b) (c) (d)Employment Average Tangible Annual(log) payrolls (log) assets (log) earnings (log)Post × MP × QC (low-capital) 0.0158 0.0101 0.0508 0.0153*(0.0215) (0.0255) (0.0343) (0.0088)Post × MP × QC (high-capital) 0.0200*** 0.0292*** 0.0264*** 0.0098***(0.0056) (0.0067) (0.0088) (0.0029)Difference 0.0042 0.0191 -0.0244 -0.0055(0.0222) (0.0263) (0.0354) (0.0093)Mean dep. var. (low-capital) 10.4 30.2 331.2 41.9Mean dep. var. (high-capital) 11.5 36.1 832.8 38.0Observations 2,106,660 2,106,660 2,011,725 6,692,730Firms/workers (treated) 10,205 10,205 10,165 64,250Firms/workers (control) 343,235 343,235 339,825 1,070,455Adjusted R2 0.917 0.888 0.938 0.813Notes: Columns (a)–(c) report estimates of θτ from equation (4.2) with dependent variables in column titles. Allestimates control for firm fixed effects and year fixed effects. Column (d) reports estimates of θτ from equation (4.4)with log annual earnings as the dependent variable. The estimates control for worker fixed effects and year fixedeffects. Samples comprise CCPCs (and their workers) with total assets below 10 million CAD and located in Quebec,British Columbia, and Ontario in 2011–2017. Part-time workers with annual earnings below 4,000 CAD, multiple-jobholders, and workers not continuously employed by the same firm in 2011–2013 are excluded. We estimate the taxeffects separately on firms (and workers) with industry-specific capital intensity below and above the sample medianin 2013 and compare the difference between the two estimates. Robust standard errors clustered by firms (columns(a)–(c)) or by firms and workers (column (d)) in parentheses. (* p < 0.1, ** p < 0.05, *** p < 0.01)154Table C.10: Tax Effects by Pre-Reform Labor Market Concentration(a) (b) (c) (d)Employment Average Tangible Annual(log) payrolls (log) assets (log) earnings (log)Post × MP × QC (low-HHI) 0.0222** 0.0298*** 0.0379*** 0.0153*(0.0087) (0.0106) (0.0139) (0.0088)Post × MP × QC (low-HHI) 0.0194*** 0.0274*** 0.0266** 0.0098***(0.0070) (0.0084) (0.0113) (0.0029)Difference -0.0028 -0.0024 -0.0114 -0.0055(0.0116) (0.0140) (0.0184) (0.0093)Mean dep. var. (low-HHI) 11.9 36.2 874.6 41.9Mean dep. var. (high-HHI) 11.2 35.3 738.2 38.0Observations 2,106,660 2,106,660 2,011,725 6,692,730Firms/workers (treated) 10,205 10,205 10,165 64,250Firms/workers (control) 343,235 343,235 339,825 1,070,455Adjusted R2 0.917 0.889 0.938 0.813Notes: Columns (a)–(c) report estimates of θτ from equation (4.2) with dependent variables in column titles. Allestimates control for firm fixed effects and year fixed effects. Column (d) reports estimates of θτ from equation (4.4)with log annual earnings as the dependent variable. The estimates control for worker fixed effects and year fixedeffects. Samples comprise CCPCs (and their workers) with total assets below 10 million CAD and located in Quebec,British Columbia, and Ontario in 2011–2017. Part-time workers with annual earnings below 4,000 CAD, multiple-jobholders, and workers not continuously employed by the same firm in 2011–2013 are excluded. We estimate the taxeffects separately on firms (and workers) in labor markets (by commuting zone by 4-digit NAICS industry) withindustry-specific Herfindahl-Hirschman Index (HHI) below and above the sample median in 2013 and compare thedifference between the two estimates. Robust standard errors clustered by firms (columns (a)–(c)) or by firms andworkers (column (d)) in parentheses. (* p < 0.1, ** p < 0.05, *** p < 0.01)155Table C.11: Tax Effects by Worker Gender(a)Annual earnings (log)Post × MP × QC (female) -0.0012(0.0042)Post × MP × QC (male) 0.0221***(0.0028)Difference 0.0233***(0.0045)Mean dep. var. (female) 30.2Mean dep. var. (male) 41.9Observations 6,601,005Workers (treated) 63,945Workers (control) 1,053,550Adjusted R2 0.815Notes: Column (a) reports estimates of θτ from equation (4.4) by worker gender and compare the difference betweenthe two estimates. Samples comprise workers at CCPCs with total assets below 10 million CAD and located in Quebec,British Columbia, and Ontario in 2011–2017. Part-time workers with annual earnings below 4,000 CAD, multiple-jobholders, and workers not continuously employed by the same firm in 2011–2013 are excluded. All estimates controlfor worker fixed effects and year fixed effects. Robust standard errors clustered by firms and workers in parentheses.(* p < 0.1, ** p < 0.05, *** p < 0.01)156Table C.12: Tax Effects by Worker Age and Earnings Quartiles(a) (b)Annual earnings (log) Annual earnings (log)Post × MP × QC (1st quartile) 0.0037 0.0124***(0.0050) (0.0040)Post × MP × QC (2nd quartile) 0.0088** 0.0166***(0.0036) (0.0038)Post × MP × QC (3rd quartile) 0.0139*** 0.0152***(0.0035) (0.0036)Post × MP × QC (4th quartile) 0.0132*** 0.0051(0.0043) (0.0046)Mean dep. var. (1st quartile) 32.0 26.4Mean dep. var. (2nd quartile) 40.8 32.4Mean dep. var. (3rd quartile) 41.3 41.4Mean dep. var. (4th quartile) 37.5 65.1Observations 6,437,905 6,484,840Workers (treated) 63,615 63,255Workers (control) 1,024,465 1,042,980Adjusted R2 0.821 0.818Notes: Columns (a)–(b) report estimates of θτ from equation (4.4), for subsamples split by worker’s age quartiles andwithin-firm earnings quartiles in 2013, respectively. Samples comprise workers at CCPCs with total assets below 10million CAD and located in Quebec, British Columbia, and Ontario in 2011–2017. In column (b), firms with fewerthan four employees in 2013 are excluded. Part-time workers with annual earnings below 4,000 CAD, multiple-jobholders, and workers not continuously employed by the same firm in 2011–2013 are excluded. All estimates controlfor worker fixed effects and year fixed effects. Robust standard errors clustered by firms and workers in parentheses.(* p < 0.1, ** p < 0.05, *** p < 0.01)157Table C.13: Additional Tax Deductions for Transportation Costs(a) (b) (c) (d)Employment Average Tangible Annual(log) payrolls (log) assets (log) earnings (log)Post × MP × QC (non-remote) 0.0168*** 0.0250*** 0.0369*** 0.0116***(0.0061) (0.0073) (0.0102) (0.0029)Post × MP × QC (remote) 0.0233*** 0.0276*** 0.0335*** 0.0173***(0.0079) (0.0096) (0.0111) (0.0039)Difference 0.0065 0.0027 -0.0034 0.0057(0.0090) (0.0109) (0.0132) (0.0043)Mean dep. var. (non-remote) 11.6 36.6 766.9 39.0Mean dep. var. (remote) 11.1 33.6 840.6 36.5Observations 2,106,660 2,106,660 2,011,725 6,692,730Firms/workers (treated) 10,205 10,205 10,165 64,250Firms/workers (control) 343,235 343,235 339,825 1,070,455Adjusted R2 0.917 0.889 0.938 0.813Notes: Columns (a)–(c) report estimates of θτ from equation (4.2) with dependent variables in column titles. Allestimates control for firm fixed effects and year fixed effects. Column (d) reports estimates of θτ from equation (4.4)with log annual earnings as the dependent variable. The estimates control for worker fixed effects and year fixedeffects. Samples comprise CCPCs (and their workers) with total assets below 10 million CAD and located in Quebec,British Columbia, and Ontario in 2011–2017. Part-time workers with annual earnings below 4,000 CAD, multiple-jobholders, and workers not continuously employed by the same firm in 2011–2013 are excluded. We estimate equations(4.2) and (4.4) for treated firms (and workers) in remote and special remote zones versus other regions of Quebecboth relative to the control group and compare the difference between the two estimates. Robust standard errorsclustered by firms (columns (a)–(c)) or by firms and workers (column (d)) in parentheses. (* p < 0.1, ** p < 0.05,*** p < 0.01)Table C.14: Investment Tax Credits(a) (b)Investment in buildings investment tax credits/ taxable incomePost × MP × QC -0.0670 -0.0007**(0.2831) (0.0003)Mean dep. var. 5.7 0.012Observations 2,106,660 2,106,660Firms (treated) 10,205 10,205Firms (control) 343,235 343,235Adjusted R2 0.274 0.560Notes: Columns (a)–(b) report estimates of θτ from equation (4.2) with dependent variables in column titles. Samplescomprise CCPCs with total assets below 10 million CAD and located in Quebec, British Columbia, and Ontario in2011–2017. All estimates control for firm fixed effects and year fixed effects. Robust standard errors clustered byfirms (columns (a)–(c)) or by firms and workers (column (d)) in parentheses. (* p < 0.1, ** p < 0.05, *** p < 0.01)158Table C.15: Additional Tax Deductions for Transportation Costs(a) (b) (c) (d)Employment Average Tangible Annual(log) payrolls (log) assets (log) earnings (log)Post × MP × QC (below 1M) 0.0196*** 0.0230*** 0.0424*** 0.0117***(0.0058) (0.0071) (0.0091) (0.0032)Post × MP × QC (above 1M) 0.0224* 0.0360*** -0.0189 0.0167***(0.0125) (0.0125) (0.0237) (0.0041)Difference 0.0027 0.0130 -0.0613** 0.0050(0.0137) (0.0143) (0.0253) (0.0052)Mean Dep. Var. (below 1M) 7.4 21.2 535.6 35.7Mean Dep. Var. (above 1M) 40.2 138.2 2514.4 41.1Observations 2,106,660 2,106,660 2,011,725 6,692,730Firms (treated) 10,205 10,205 10,205 67,490Firms (control) 338,160 338,160 338,160 1,130,655Adjusted R2 0.917 0.889 0.938 0.814Notes: Columns (a)–(c) report estimates of θτ from equation (4.2) with dependent variables in column titles. Allestimates control for firm fixed effects and year fixed effects. Column (d) reports estimates of θτ from equation (4.4)with log annual earnings as the dependent variable. The estimates control for worker fixed effects and year fixedeffects. Samples comprise CCPCs (and their workers) with total assets below 10 million CAD and located in Quebec,British Columbia, and Ontario in 2011–2017. Part-time workers with annual earnings below 4,000 CAD, multiple-jobholders, and workers not continuously employed by the same firm in 2011–2013 are excluded. We estimate equations(4.2) and (4.4) for treated firms (and workers) with total payrolls below and above 1 million CAD in 2013 andcompare the difference between the two estimates. Robust standard errors clustered by firms (columns (a)–(c)) orby firms and workers (column (d)) in parentheses. (* p < 0.1, ** p < 0.05, *** p < 0.01)159C.2 User Cost of CapitalFollowing the literature (Zwick and Mahon, 2017; Maffini et al., 2019; Curtis et al., 2022), we usea standard definition of the user cost of capitalc =1− τz1− τ (r + δ), (C.1)where τz represents the net present value of tax deductions due to capital cost allowances for onedollar increase in investment, τ is the marginal corporate tax rate, r is the interest rate (assumedto be 15 percent), and δ is the economic rate of depreciation (assumed to be 20 percent).To compute d, we use data on claims of CCA derived from corporate tax returns (T2 Schedule8). The data contains firms’ undepreciated capital costs (UCC), costs of acquiring new assets,and statutory CCA rates by different asset classes. For each firm, we find d as the average CCArate across different asset classes, weighted by their undepreciated capital costs. Prior to thereform, the estimated rate of depreciation for tax purposes (capital cost allowance rate, or CCArate hereinafter) is d = 0.265 for treated firms in our sample.Then the net present value of tax deductions is computed as:τz =12d+d(1− 12d)1 + r(1 +1− d1 + r+(1− d1 + r)2+(1− d1 + r)3+ ...)=d(1 + 12r)r + d= 0.686τ. (C.2)Since there was no change in CCA schedule in 2011–2017, we can compute the user cost for treatedfirms before (c0 = 0.372) and after (c1 = 0.366) the reform, using the change in the marginalstatutory tax rate (from 19 percent to 15 percent). Then the percent change in the user cost ofcapital for the treated firms after the reform is (c1 − c0)/c0 = −0.015.160C.3 RobustnessFigure C.3: Additional Fixed Effects(a) Employment (log)-.04-.020.02.04.06Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017Year(b) Average payrolls (log)-.06-.030.03.06.09Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017Year(c) Tangible assets (log)-.06-.030.03.06.09Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017Year(d) Annual earnings (log)-.02-.010.01.02.03Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017YearNotes: Panels (a)–(c) plot estimates of θτ from equation (4.2) with dependent variables in subtitles. All estimatescontrol for firm fixed effects and year fixed effects. Panel (d) plots estimates of θτ from equation (4.4) with logannual earnings as the dependent variable. The estimates control for worker fixed effects and year fixed effects.Samples comprise CCPCs (and their workers) with total assets below 10 million CAD and located in Quebec, BritishColumbia, and Ontario in 2011–2017. Part-time workers with annual earnings below 4,000 CAD, multiple-job holders,and workers not continuously employed by the same firm in 2011–2013 are excluded. The solid vertical line indicatesthe reform year. The dashed lines represent 95 percent confidence intervals. We additionally control for 4-digitNAICS industry by year and commuting zone by year fixed effects.161Figure C.4: Firms with Taxable Capital below 10 Million CAD(a) Employment (log)-.04-.020.02.04.06Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017Year(b) Average payrolls (log)-.06-.030.03.06.09Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017Year(c) Tangible assets (log)-.06-.030.03.06.09Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017Year(d) Annual earnings (log)-.02-.010.01.02.03Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017YearNotes: Panels (a)–(c) plot estimates of θτ from equation (4.2) with dependent variables in subtitles. All estimatescontrol for firm fixed effects and year fixed effects. Panel (d) plots estimates of θτ from equation (4.4) with log annualearnings as the dependent variable. The estimates control for worker fixed effects and year fixed effects. Samplescomprise CCPCs (and their workers) with taxable capital below 10 million CAD or missing during 2011–2013, andlocated in Quebec, British Columbia, and Ontario in 2011–2017. Part-time workers with annual earnings below 4,000CAD, multiple-job holders, and workers not continuously employed by the same firm in 2011–2013 are excluded.The solid vertical line indicates the reform year. The dashed lines represent 95 percent confidence intervals. Weadditionally control for 4-digit NAICS industry by year and commuting zone by year fixed effects.162Figure C.5: Including Other Provinces(a) Employment (log)-.04-.020.02.04.06Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017Year(b) Average payrolls (log)-.06-.030.03.06.09Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017Year(c) Tangible assets (log)-.06-.030.03.06.09Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017Year(d) Annual earnings (log)-.02-.010.01.02.03Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017YearNotes: Panels (a)–(c) plot estimates of θτ from equation (4.2) with dependent variables in subtitles. All estimatescontrol for firm fixed effects and year fixed effects. Panel (d) plots estimates of θτ from equation (4.4) with log annualearnings as the dependent variable. The estimates control for worker fixed effects and year fixed effects. Samplescomprise CCPCs (and their workers) with total assets below 10 million CAD and located in Quebec, British Columbia,Ontario, and other provinces without tax rate changes in 2011–2017. Part-time workers with annual earnings below4,000 CAD, multiple-job holders, and workers not continuously employed by the same firm in 2011–2013 are excluded.The solid vertical line indicates the reform year. The dashed lines represent 95 percent confidence intervals.163Figure C.6: Including Other Sectors(a) Employment (log)-.04-.020.02.04.06Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017Year(b) Average payrolls (log)-.06-.030.03.06.09Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017Year(c) Tangible assets (log)-.06-.030.03.06.09Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017Year(d) Annual earnings (log)-.02-.010.01.02.03Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017YearNotes: Panels (a)–(c) plot estimates of θτ from equation (4.2) with dependent variables in subtitles. All estimatescontrol for firm fixed effects and year fixed effects. Panel (d) plots estimates of θτ from equation (4.4) with logannual earnings as the dependent variable. The estimates control for worker fixed effects and year fixed effects.Samples comprise CCPCs (and their workers) with total assets below 10 million CAD and located in Quebec, BritishColumbia, and Ontario in 2011–2017. Firms (and their workers) in agriculture, finance and real estate, healthcare, andprofessional services sectors are also included. Part-time workers with annual earnings below 4,000 CAD, multiple-jobholders, and workers not continuously employed by the same firm in 2011–2013 are excluded. The solid vertical lineindicates the reform year. The dashed lines represent 95 percent confidence intervals.164Figure C.7: Including Part-time and Multiple-job Workers and Dropping Tenure Restrictions-.020.02.04Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017YearNotes: This figure plots estimates of θτ from equation (4.4) with log annual earnings as the dependent variable.The sample comprises workers at CCPCs with total assets below 10 million CAD and located in Quebec, BritishColumbia, and Ontario in 2011–2017. Part-time workers with annual earnings below 4,000 CAD, multiple-job holders,and workers not continuously employed by the same firm in 2011–2013 are also included. The solid vertical lineindicates the reform year. The dashed lines represent 95 percent confidence intervals.Figure C.8: Distribution of Taxable Income among Treated Firms0.02.04.06.08Firm Share250 300 350 400 450 500 550 600 650 700 750Taxable Income ('000')Before AfterNotes: This figure shows the distribution of taxable income between 250,000 and 750,000 CAD for domestic smallfirms in the M&P sector in Quebec. The light and dark blue lines represent the distributions before and after thereform, respectively.165Figure C.9: Firms with Taxable Income Close to the Eligibility Threshold(a) Employment (log)-.2-.10.1.2.3Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017Year(b) Average payrolls (log)-.2-.10.1.2.3Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017Year(c) Tangible assets (log)-.2-.10.1.2.3Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017Year(d) Annual earnings (log)-.2-.10.1.2.3Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017YearNotes: Panels (a)–(c) plot estimates of θτ from equation (4.2) with dependent variables in subtitles. All estimatescontrol for firm fixed effects and year fixed effects. Panel (d) plots estimates of θτ from equation (4.4) with log annualearnings as the dependent variable. The estimates control for worker fixed effects and year fixed effects. Samplescomprise CCPCs (and their workers) with total assets below 10 million CAD and located in Quebec, British Columbia,Ontario, and other provinces without tax rate changes in 2011–2017. Part-time workers with annual earnings below4,000 CAD, multiple-job holders, and workers not continuously employed by the same firm in 2011–2013 are excluded.In addition, we focus on firms (and their workers) with taxable income between 400,000 CAD and 500,000 CAD in2013. The solid vertical line indicates the reform year. The dashed lines represent 95 percent confidence intervals.166Figure C.10: Placebo Tests Using Non-CCPCs(a) Employment (log)-.2-.10.1.2Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017Year(b) Average payrolls (log)-.2-.10.1.2Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017Year(c) Tangible assets (log)-.6-.30.3.6Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017Year(d) Annual earnings (log)-.2-.10.1.2Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017YearNotes: Panels (a)–(c) plot estimates of θτ from equation (4.2) with dependent variables in subtitles. All estimatescontrol for firm fixed effects and year fixed effects. Panel (d) plots estimates of θτ from equation (4.4) with log annualearnings as the dependent variable. The estimates control for worker fixed effects and year fixed effects. Samplescomprise non-CCPCs (and their workers) in Quebec, British Columbia, and Ontario in 2011–2017. Part-time workerswith annual earnings below 4,000 CAD, multiple-job holders, and workers not continuously employed by the samefirm in 2011–2013 are excluded. The solid vertical line indicates the reform year. The dashed lines represent 95percent confidence intervals.167Figure C.11: Difference-in-Differences (DID) Estimates(a) Employment (log)-.04-.020.02.04.06Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017YearQuebec BC/Ontario(b) Average payrolls (log)-.06-.030.03.06.09Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017YearQuebec BC/Ontario(c) Tangible assets (log)-.06-.030.03.06.09Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017YearQuebec BC/Ontario(d) Annual earnings (log)-.02-.010.01.02.03Coefficient Estimates [2013 = 0]2011 2012 2013 2014 2015 2016 2017YearQuebec BC/OntarioNotes: Panels (a)–(c) plot DID estimates with dependent variables in subtitles. All estimates control for firm fixedeffects and year fixed effects. Panel (d) plots DID estimates of with log annual earnings as the dependent variable.The estimates control for worker fixed effects and year fixed effects. Samples comprise CCPCs (and their workers)with total assets below 10 million CAD and located in Quebec, British Columbia, and Ontario in 2011–2017. Part-time workers with annual earnings below 4,000 CAD, multiple-job holders, and workers not continuously employedby the same firm in 2011–2013 are excluded. The solid vertical line indicates the reform year. The dashed linesrepresent 95 percent confidence intervals. The dark blue lines indicate estimates comparing M&P versus non-M&Pfirms and workers in Quebec, and the red lines indicate estimates for the same comparison in British Columbia andOntario.168Figure C.12: Worker Reallocation(a) Treated and control firms-.20.2.4.6.81Share of Workers (%)2011 2012 2013 2014 2015 2016 2017YearInflow to Treated Outflow from TreatedNet Inflow to Treated [2013 = 0](b) Treated and control firms (Quebec)-.20.2.4.6.81Share of Workers (%)2011 2012 2013 2014 2015 2016 2017YearInflow to Treated Outflow from TreatedNet Inflow to Treated [2013 = 0](c) Treated and control firms (non-Quebec)-.20.2.4.6.81Share of Workers (%)2011 2012 2013 2014 2015 2016 2017YearInflow to Treated Outflow from TreatedNet Inflow to Treated [2013 = 0](d) Treated and out-of-sample firms-.20.2.4.6.81Share of Workers (%)2011 2012 2013 2014 2015 2016 2017YearInflow to Treated Outflow from TreatedNet Inflow to Treated [2013 = 0](e) Treated and ineligible firms-.20.2.4.6.81Share of Workers (%)2011 2012 2013 2014 2015 2016 2017YearInflow to Treated Outflow from TreatedNet Inflow to Treated [2013 = 0](f) Treated firms and non-employment-20246810Number of Workers ('000)2011 2012 2013 2014 2015 2016 2017YearInflow to Treated Outflow from TreatedNet Inflow to Treated [2013 = 0]Notes: Panels (a)–(f) show worker reallocation between treated firms and each of the following: (a) control firms,(b) control firms in Quebec, (c) control firms out of Quebec, (d) out-of-sample firms, (e) ineligible firms, and (f)non-employment. Out-of-sample firms refer to CCPCs with total assets below 10 million, not in Quebec, B.C., orOntario, or in excluded sectors. Ineligible firms refer to non-CCPCs or CCPCs with total assets above 10 millionregardless of their provinces or sectors. Non-employment refers to workers without T4 earnings for at least twoconsecutive years. The dashed dark blue lines represent gross inflow into treated firms. The dashed light blue linesrepresent gross outflow from treated firms. The solid dark blue lines represent the net inflow into treated firms scaledby the net inflow in 2013. In panels (a)–(e), the number of reallocated workers is scaled by the number of workers inthe corresponding group in the previous year.169
Thesis/Dissertation
eng
Economics
Vancouver : University of British Columbia Library
Attribution-NonCommercial-NoDerivatives 4.0 International
Graduate
Lemieux, Thomas
Fortin, Nicole M.
Essays on worker mobility, spatial labor markets, and urban real estate markets
Text