ESSAYS in PUBLIC ECONOMICS Divya Singh Submitted in Partial

ESSAYS IN PUBLIC ECONOMICS

Divya Singh

Submitted in partial fulﬁllment of the requirements for the degree of Doctor of Philosophy under the Executive Committee of the Graduate School of Arts and Sciences

COLUMBIA UNIVERSITY

Divya Singh

Governments play a key role in modern economies. However, modern-day governments face several challenges that limit their functioning. Some examples include inadequate conduct of elections, tax evasion, and market failures. Each chapter in this thesis explores a key challenge faced by government and policy intervention that helps address it. Chapter 1 explores the poor turnout of women in India and tests whether increasing security at the polling booths increases women’s representation. Chapter 2 explores the role of tax evasion by ﬁrms in low revenue collection under a Value Added Tax (VAT) in India. Chapter 3 examines the current housing crisis in major cities across the United States and evaluates the effects of tax incentives designed to encourage new residential investment.

To provide robust causal evidence, I use natural experiments combined with novel microdata. Chapter 1 uses a regression discontinuity design arising from the rule used to assign security measures to polling booths during a major state election in India. In particular, polling booths which received more than 75% of votes in favor of one candidate in the previous election received security measures with a higher probability. I use the regression discontinuity design to estimate effects on women’s share in total turnout and political outcomes. Chapter 2 uses the staggered roll-out of VAT across states in India to estimate the effect of VAT adoption on vertical integration in ﬁrms. Chapter 3 uses a natural experiment in New York City where a delayed implementation of the property tax increase on new construction led to a short-term boom in residential investment as developers rushed to claim expiring tax beneﬁts. I estimate effects on nearby rents, demographics, and businesses.

The end result is a set of robust policy conclusions. Chapter 1 finds that strengthening security at the polling booths increased the women’s turnout, which in turn had consequences for political outcomes. For instance, suggestive evidence indicates that non-incumbent and educated candidates received more votes whereas corrupt candidates received fewer votes. Chapter 2 finds that firms integrated vertically to evade taxes under a Value Added Tax. This suggests that low revenue collection in developing countries is possibly a combination of both evasion and real production response of firms. Chapter 3 finds that new tax-exempt residential investment increased rents in existing buildings within 150 meters. This happened because new building attracted high-income residents who increased demand for local businesses, reflected in the entry of businesses that cater to high-income residents. The result highlights potential negative spillover effects of new construction on incumbent low-income residents and suggests that optimal tax policy must incorporate such spillovers when designing incentives that encourage investment.

2 Table of Contents

List of Tables ...... v

List of Figures ...... viii

Acknowledgments ...... xii

Dedication ...... xiii

Chapter 1: Safer Elections, Women Turnout, and Political Outcomes: Evidence from India . 1

1.1 Background ...... 4

1.2 Data ...... 6

1.3 Empirical strategy ...... 8

1.3.1 The cutoff and the First stage ...... 11

1.4 Results and Discussion ...... 12

1.4.1 Summary Statistics ...... 12

1.4.2 Voting outcomes ...... 13

1.4.3 Political Outcomes ...... 14

1.4.4 Permutation Test ...... 16

1.4.5 Discussion ...... 17

1.5 Conclusion ...... 18

i 1.6 Figures and Tables ...... 19

1.7 Supportive tables and Figures ...... 24

Chapter 2: Merging to Dodge Taxes? Unexpected Consequences of VAT Adoption in India 35

2.1 The VAT tax Reform, 2004-09 ...... 41

2.2 Data and measurement of vertical integration ...... 44

2.2.1 Data ...... 44

2.2.2 Measurement of vertical integration ...... 47

2.3 Empirical strategy and results ...... 51

2.3.1 Main speciﬁcation: VAT and Non-VAT-good Producers ...... 51

2.3.2 Alternative speciﬁcations ...... 55

2.3.3 Effect on mergers and acquisitions ...... 57

2.3.4 Robustness checks ...... 58

2.4 Exploring mechanisms ...... 59

2.4.1 Tax evasion at the retail stage ...... 59

2.4.2 Liquidity constraints under VAT ...... 60

2.4.3 Higher Compliance Costs under VAT ...... 61

2.4.4 Lower tax rates in the VAT regime ...... 62

2.4.5 Higher tax rate on upstream ﬁrms ...... 63

2.5 Discussion ...... 63

2.5.1 Welfare effects of the tax reform ...... 68

2.6 Conclusions ...... 69

2.7 Tables and Figures ...... 70

ii Chapter 3: Do Property Tax Incentives for New Construction Spur Gentriﬁcation? Evi- dence from New York City ...... 103

3.1 Background and data ...... 109

3.1.1 Property tax reform in New York City ...... 109

3.1.2 Data ...... 113

3.2 The time notch and residential investment ...... 115

3.2.1 Anticipated tax increase and short term outcomes ...... 118

3.2.2 Estimating excess housing starts in the time notch ...... 119

3.2.3 Bunching results ...... 120

3.3 Effect of new residential investment on rents ...... 124

3.3.1 Summary statistics ...... 127

3.3.2 Results: Effect of tax-exempt investment on rents ...... 129

3.3.3 Robustness checks ...... 134

3.3.4 Heterogeneity in rent effects ...... 136

3.3.5 Differences-in-differences estimate of the rent Effect ...... 137

3.3.6 Differences in regression discontinuity ...... 139

3.4 A mechanism: Gentriﬁcation ...... 140

3.4.1 Evidence 1: Demographic changes ...... 142

3.4.2 Evidence 2: Changes in amenities ...... 143

3.5 Discussion ...... 144

3.5.1 Incidence of tax-exempt investment in the time-notch ...... 145

3.5.2 Efﬁciency effect of the time-notch ...... 148

3.6 Conclusion ...... 149

iii 3.7 Figures and tables ...... 150

3.8 Marginal response as a function of distance calculation ...... 185

3.9 Data construction: Demographic outcomes ...... 185

3.10 Supportive tables and ﬁgures ...... 187

References ...... 213

Appendix A: Safer Elections, Women Turnout, and Political Outcomes: Evidence from India218

A.1 Data Construction ...... 218

A.1.1 Booth-level turnout by gender ...... 218

Appendix B: Do Property Tax Incentives for New Construction Spur Gentriﬁcation? Evi- dence from New York City ...... 221

B.1 Data ...... 222

B.2 Property taxes in New York City ...... 226

B.3 Effect of the tax reform on property tax across regions ...... 228

B.4 Short Term Outcomes in the Time Notch ...... 232

iv List of Tables

1.1 Voting Outcomes ...... 22

1.2 Political Outcomes ...... 23

1.3 Summary Statistics: Voting outcomes ...... 24

1.4 Summary statistics: Political Outcomes ...... 32

1.5 Voting Outcomes: Unconstrained Regression Discontinuity ...... 33

1.6 Regression Discontinuity using previous turnout share as running variable . . . . . 34

2.1 Summary Statistics ...... 92

2.2 Results for Speciﬁcation 2.1, Firm Inputs ...... 93

2.3 Results for Speciﬁcation 2.1, Firm Outputs ...... 94

2.4 Results for Speciﬁcation 2.3 ...... 94

2.5 Differential effects by tax rate change ...... 95

2.6 Effect on other outcomes ...... 95

2.7 IV estimates ...... 96

2.8 Correlation between state-level delay in VAT adoption and outcomes ...... 97

2.9 Product upstreamness ...... 98

2.10 Results for Speciﬁcation 1 ...... 98

2.11 Results for Speciﬁcation 2, Output Second moments ...... 99

v 2.12 Winsorized Regressions ...... 99

2.13 DD estimates for the average input upstreamness: 2004-2010 (Winsorized) . . . . 99

2.14 Estimation with upstream measure calculated using Pseudo-inverse...... 100

2.15 Robustness check: dropping non-positive upstream values ...... 100

2.16 Lowest and highest upstream products ...... 101

2.17 Correlation among measures ...... 101

2.18 Kolmogorov-Smirnov test ...... 102

2.19 Tax rates pre and post VAT ...... 102

3.1 Changes brough by 2006-08 property tax reform ...... 179

3.2 Summary statistics for non-tax-exempt and tax-exempt parcels in 2015 ...... 180

3.3 Descriptives: Rental parcels in New York City in 2007 ...... 181

3.4 Descriptives: Rental parcels in Brooklyn in 2007 ...... 182

3.5 Excess housing starts in the time-notch ...... 182

3.6 Effect of new tax-exempt residential investment on rents: IV estimates ...... 183

3.7 Effect of new tax-exempt residential investment on rents: Exclusion vs non-exclusion regions ...... 183

3.8 Effect of new tax-exempt residential investment on demographics: IV estimates . . 184

3.9 Effect of new tax-exempt residential investment on rents: Short-term vs long term . 184

3.10 Summary statistics for non-notch and notch properties in 2015 ...... 200

3.11 Effect of new tax-exempt residential projects on rents: IV Estimates ...... 201

3.12 Alternative instrument 0 and ≥ 1 vacant parcels: IV Estimates ...... 201

3.13 Adjusting for spatial correlation: IV Estimates ...... 202

3.14 Effect of new residential investment on rents: Elasticity estimates ...... 202

vi 3.15 Leave a borough out: IV Estimate ...... 203

3.16 Demographics statistics: Exclusion and non-exclusion regions ...... 203

3.17 Selected high and low income elasticity industries ...... 204

vii List of Figures

1.1 Two Dimensional RD ...... 19

1.2 Effect of Poll-booth security ...... 20

1.3 Political Outcomes ...... 21

1.4 Spatial location of polling booths ...... 25

1.5 Events timeline ...... 26

1.6 Distribution of female turnout share in 2009 ...... 27

1.7 Distribution of total turnout as a share of running variable ...... 27

1.8 McCrary density test ...... 28

1.9 Estimate as a function of speciﬁed bandwidth ...... 29

1.10 Hypothetical simulated treatment effects ...... 30

1.11 Hypothetical treatment effect: Political outcomes ...... 31

2.1 Country VAT Adoption ...... 70

2.2 State VAT adoption in India: ...... 71

2.3 State VAT adoption in India ...... 72

2.4 Effect of the VAT adoption on state revenues ...... 73

2.5 Vertical integration in retail sales tax versus VAT ...... 74

2.6 Vertical integration and product upstream measure ...... 75

viii 2.7 Vertical distance of ﬁrms ...... 75

2.8 Distribution of U2 ...... 76

2.9 Tax rate change in VAT reform ...... 77

2.10 Effect of VAT adoption on vertical integration (Inputs) ...... 78

2.11 Effect of VAT adoption on vertical integration (Outputs) ...... 79

2.12 State-level effects ...... 80

2.13 Mechanism 1: Tax evasion ...... 81

2.14 Mechanism 2: Liquidity constraint ...... 82

2.15 Mechanism 3: Compliance costs ...... 83

2.16 Mechanism 5: Higher tax rate on upstream ﬁrms ...... 84

2.17 Mergers and acquisitions ...... 85

2.18 Test of Monotonicity assumption for 2SLS Estimation ...... 86

2.19 Leave-one-out test ...... 87

2.20 Placebo test ...... 88

2.21 Firms number by distance to ﬁnal demand ...... 89

2.22 Effect by industry ...... 90

2.23 Vertical integration under VAT ...... 91

2.24 Firm distribution by industry ...... 97

3.1 421a property tax reform 2006-08 ...... 150

3.2 Distribution of housing stock type in New York City in 2007 ...... 151

3.3 Correlation between age and rent of a housing unit ...... 152

3.4 Effect of time notch on short term and long term outcomes ...... 153

ix 3.5 Aggregate quarterly tax-exempt housing starts in New York City, blue and yellow regions ...... 154

3.6 Spatial distribution of tax-exempt projects in the time notch ...... 155

3.7 Bunching estimation of tax-exempt housing unit starts ...... 156

3.8 Bunching of tax-exempt housing starts in exclusion regions, by boroughs ...... 157

3.9 Effect on aggregate housing starts in exclusion vs non-exclusion regions ...... 158

3.10 Empirical design to estimate the effect of the 2006-08 Tax reform on the Rents . . . 159

3.11 Spatial distribution of vacant parcels in 2005 ...... 160

3.12 Spatial distribution of existing rental buildings in 2005 ...... 161

3.13 Classiﬁcation of parcels developed in the time notch ...... 162

3.14 First stage ...... 163

3.15 Probability that a building receives a tax-exempt unit within 150 meters in the time notch ...... 164

3.16 Rents in buildings with vacant parcel vs buildings with no vacant parcel within 150 meters ...... 165

3.17 IV estimate as a function of the ring radius ...... 166

3.18 IV Estimate as a function of census-tract income ...... 167

3.19 IV Estimate as a function of baseline building rent ...... 168

3.20 IV Estimate as a function of baseline building age ...... 169

3.21 IV estimate as a function of census-tract housing quality heterogeneity ...... 170

3.22 New residential investment and prices: Prices in exclusion and non-exclusion regions171

3.23 Parcels used in differences-in-geographic regression discontinuity ...... 172

3.24 Differences in regression discontinuity at varying bandwidths ...... 173

3.25 Mechanism ...... 174

x 3.26 New tax-exempt residential investment and consumption amenities in Brooklyn . . 175

3.27 First stage: Tax exempt projects in the time notch against baseline land intensity in the zipcode ...... 176

3.28 Log establishments by high land and low land availability ...... 177

3.29 Business activity: Estimates by industry income elasticity ...... 178

3.30 Political process for selection of the exclusion regions ...... 187

3.31 421a property tax exemption use over time ...... 188

3.32 Steps required for a work permit in New York City ...... 188

3.33 Quarterly tax-exempt housing starts by exemption type ...... 189

3.34 Bunching estimates including CONDOS ...... 190

3.35 Distribution of tax-exempt projects across building types ...... 191

3.36 Completion year of notch projects ...... 192

3.37 Effect of new residential investment on rents: OLS estimates ...... 193

3.38 Total investment in within 150 meters from the building ...... 194

3.39 Alterations and renovations ...... 195

3.40 Heterogeneity test ...... 196

3.41 Foreclosures in 2008 in New York ...... 196

3.42 Alternative counterfactual: Commercial and family homes starts ...... 197

3.43 Alternative counterfactual: Non-tax-exempt starts in the non-exclusion regions . . . 197

3.44 Relationship between market valuation and rental income of the building ...... 198

3.45 Marginal rent effect as a function of distance ...... 199

B.1 Geographies in New York City datasets ...... 225

xi Acknowledgements

I am deeply indebted to Columbia University for providing me the opportunity to obtain high-class education and engage in research on exciting topics. I want to extend my sincere thanks to my sponsor, Wojciech Kopczuk, who provided advice in all dissertation stages. I am also grateful to my committee members, Brendan O’Flaherty, Bernard Salanie, Michael Best, and Cailin Slattery for their comments and support.

Many thanks to the supportive faculty at Columbia, Donald Davis, Reka Juhasz, and Jack Willis, who went out of their way to help me at different stages. Finally, I can not begin to express thanks to my mother, Sita Singh, and my husband, Oliver Shetler, who stood by me through the difﬁcult stages of this dissertation.

xii Dedication

I dedicate this dissertation to my father, Baikunth Nath Singh, who taught me to read and write, who showed me the value of scholarship, who encouraged me to pursue my dreams and overcome the challenges I faced, and who cared for me till his last breath. I will always miss him.

xiii Chapter 1: Safer Elections, Women Turnout, and Political Outcomes:

Evidence from India

In recent years, parts of India and Africa have struggled with electoral malpractices such as violence, voter intimidation, and ballot fraud (Witsoe 2013; Collier and Vicente 2012, 2014). These malpractices affect some demographic groups more than others. For instance, if women are more vulnerable to violence than men, the prevalence of polling day violence limits their turnout. Under- standing which interventions work is crucial because the electoral representation has consequences on who gains office and which public goods are provided (Chattopadhyay and Duflo 2004; Bea- man et al. 2009; Pande 2003). This paper estimates the effects of one such policy on turnout and political outcomes in India: strengthening security at the polling booths. To tackle electoral malpractices, the Election Commission of India (ECI) increased security at the polling booths in all elections after 2007. Some measures included deployment of out-of-state security forces, flying squads, micro-observers, and vigilance through cameras. Interestingly, the limited supply of security resources necessitated the commission to identify "critical" booths and target them specifically. A criterion used included the identification of booths wherein the previous election, a single candidate received more than 75% of the votes, and the turnout was higher than 75 %. The empirical strategy uses the single running variable —maximum candidate vote share in the previous election—to assign a polling booth to treatment. Furthermore, the main specification restricts the sample to include booths which also cross the second threshold so that a booth to the right of the first threshold has a higher probability of treatment. I refer to this specification as the "constrained" specification. I select the maximum vote share as the running variable because the other available option—turnout share— is correlated with the baseline voting outcomes. I

1 supplement with a detailed dataset of voting and political outcomes at the polling booth level for the 2012 state elections of Uttar Pradesh (UP), which is the most populous state, encompasses more than 100,000 polling booths, and has historically suffered from electoral malpractices. My main finding is that higher security measures altered turnout composition by increasing the share of women who turn out to vote. In particular, the change in women share in total turnout is higher by 1.8% in the booths just to the right of the threshold than just to the left. The estimate is stable as I vary the bandwidth. In contrast, the growth in total turnout is insignificant at IK bandwidth (Imbens and Kalyanaraman 2012) and significant at 1.2 times the IK bandwidth. McCrary test (2008) rejects significant differences in density around the threshold. Additionally, I find that polling booths with higher security measures are associated with outcomes that favor non-incumbent party, educated candidates, and disfavor candidates with indica- tion of corruption. These results are suggestive in nature because in contrast to the voting outcomes, the unavailability of the baseline data on political outcomes allows me to identify only cross-sectional differences around the threshold. Furthermore, small sample size renders effects underpowered in the constrained specification. Using unconstrained specification, I find that a candidate to the right of the threshold receives 1.3% fewer votes compared with a candidate just to the left of the threshold. Similarly, candidates with significant asset growth in previous office receive 1.6% fewer votes. Candidates with at least a graduate degree receive 1.1% more votes to the right of the threshold. To alleviate the concern that the estimated effect could reflect a threshold-specific noise, I perform a permutation test, which simulates treatment effects at hypothetical thresholds.1 I find that the estimated treatment effect on the female turnout change at the actual threshold is an outlier in the distribution of the simulated effects. Less than 1% of the simulated effects are larger than the observed effect. Furthermore, the main outcome variable is expressed in changes to account for any fixed differences in booths on either side of the threshold. This is useful given that variables such as total turnout are insignificant at the baseline, the female turnout share is not balanced at

1Fisher 1935 proposed this test.

2 10% significance level. While the women turnout result is quite robust, the permutation test for political outcomes is weaker suggesting caution in interpreting the political outcomes results. Because a winning party on average receives 40% of the total constituency votes, an increase in the women turnout of 1.8 percentage points has the potential to affect the election outcome. A limitation of the main result is that it captures the intent to treat estimate. This is because the poll-booth data does not identify which booths actually received greater security. Using rough first-stage statistics from a government report, I find the LATE estimate is 2.5, which suggests that increasing security at booths increases women turnout share by nearly 2.5%. The result suggests that the conduct of free and fair elections can help in bridging the gender gap in the political representation. Previous literature has demonstrated that changes in the turnout composition affects actual outcomes (Miller 2008; Chattopadhyay and Duflo 2004; Beaman et al. 2009; Fujiwara 2015; Iyer et al. 2012). This deems electoral safety crucial for adequate representaion of minorities including women. A future line of work includes exploring who the additional vulnerable groups are and what are the consequences of their increased representation on public goods provision, for instance.2 My paper contributes to three main strands of literature. First, it adds to the literature in incentives to voting. This literature has identified several measures that affect total vote turnout. Some measures include penalties for not voting (Leon 2012); information and social pressure (DellaV- igna et al. 2014; Gerber and Green 2000a, b; Gerber, Green, and Larimer 2008); early voting (Kaplan and Yuan 2019); distance to polling booth (Cantoni 2019); institutional changes such as de-jure enfranchisement of women (Miller 2008); and the introduction of voting machines (Fuji- wara 2015). Second, this paper contributes to the literature on electoral malpractices. While there is a substantial theoretical work that examines the effect of electoral violence on outcomes (Ellman and Wantchekon 2000; Chaturvedi 2005; Collier and Vicente 2012 ), most of the empirical work has focused on clientelism in rural agricultural settings (Baland and Robinson 2008; Anderson

2An additional group could include voters belonging to the low caste and the low-income households.

3 2015), with the exception of Collier and Vincente 2014, who show, using a ﬁeld experiment, that anti-violence campaign decreased violence perception and increased turnout. Relatedly, Gine and Mansuri 2018 show that voter awareness campaign increased women turnout in Pakistan. In contrast, my paper provides quasi-experimental evidence on an alternative intervention—poll booth safety—and suggests that such intervention can have real political effects. Finally, my paper contributes to the literature on the determinants of women electoral participation (Chattopadhyay and Duﬂo 2004, Beaman et al. 2012; and Iyer et al. 2012). Another contribution of this paper is that it explores turnout and political outcomes at the level of a polling booth, in contrast to the previous studies that primarily focus on interventions at the constituency level, a vast geographic region (Jenenius 2016; Fisman et al. 2013; and Asher and Novosad 2017). 3 Studying outcomes at such granular level has the advantage that it controls for any state or constituency level shocks correlated with the voting outcomes. The paper is organized as follows: Section 1.1 discusses the institutional background. Section 1.2 describes the data. Section 1.3 discusses empirical strategy. Section 1.4 reports results. Section 1.5 conludes.

1.1 Background

This section describes the characteristics of elections at the time of the intervention and the details of the intervention. I choose the state of Uttar Pradesh for relevance and data availability reasons. First, Uttar Pradesh (UP) is the most populous state in India, with more than a million villages. In terms of GDP, UP ranks 26th out of 32 states in India. Historically, the state has witnessed violent elections and ﬁelding of candidates who often use force and intimidation to win elections. The political atmosphere in UP is intense. In the 2007 elections (two years before our study period), 20% of the candidates had self-disclosed criminal charges against them, and 10% had severe criminal charges. These ﬁgures remained largely the same in the outcome year. Moreover, 46% of the winners in

3An average constituency contains up to 300 polling booths, depending on the distribution of the population. Each polling booth serves 2000 voters on average.

4 the outcome year had criminal charges against them compared with 35% in 2007.4 Second, Uttar Pradesh is the only state that reports gender decomposition in the voter turnout at the polling booth level. The crucial part of the election process is a polling booth, which is a designated location where the voters exercise their right to vote. Figure 1.4 illustrates the distribution of the polling booths within a constituency (Varanasi). A constituency has around 300 polling booths, with each booth serving about 2000 registered voters. An average village contains one or two booths. A constituency elects a representative to the state legislature through first-past-the-post voting rule. Con- testants not affliated to any party run independently. The party with a majority of the elected representatives in the assembly wins. Historically, polling booths are sensitive and easy targets for intimidating voters, ballot fraud, and booth capturing. Witsoe (2013) documents the interaction between local leaders and the caste- based territorial dominance, which makes it easier for parties to identify "friendly" and "enemy" booths in a village. Booth capturing occurs when the politicians use goons and powerful men to restrict or intimidate voters to enter the "enemy" booths. Booth capturing takes many forms such as: (i) local leaders stand near the voting machine and direct voters to vote for specific candidates; (ii) armed gunmen take control of the polling booth; (iii) or steal the voting machine; (iv) or artificially stamp the ballots; (v) and in the worst case, use bombs and gunfire to cause panic. Booth capturing is even more prominent in the rural areas that are often cut off from media coverage and the police (Witsoe 2013). A consequence of booth capturing is the concentration of violence around the polling booths.5 To deal with this problem, the Election Commission of India (ECI) decided to increase security at the polling booths in all elections held after 2007. Since the required amount of security forces was far greater than the supply (there are millions of polling booths throughout India), the ECI decided to identify vulnerable booths and deploy extra forces in such "critical" booths only. Some extra security measures deployed at the critical booths included police forces, flying squads, micro-

4Figure provided by Association of Democratic Reform. 5http://foreignpolicy.com/2013/03/21/policing-electoral-violence-in-india/

5 observers and CCTV monitoring on the election day. A few of the parameters which governed whether a particular booth was "critical" included:

1. If a single candidate received more than 75% of the votes in the previous election and,

2. If the turnout as the ratio of registered voters was more than 75% in the previous election.

The other criteria included the share of registered voters with no photo registration; share of missing voters under two categories; missing voters with family links and missing voters with no family links; booths which went to repoll in the previous election. Quraishi (2014) points out that an extraordinarily high turnout in the past ﬂags the possibility of booth capturing. Hence, the election ofﬁcials used an Excel sheet with the relevant variables to determine criticality of booths.6

1.2 Data

Data on booth turnout: I obtain booth-level election outcomes for the state of Uttar Pradesh for the years 2007, 2009 and 2012. This information was downloaded from the ECI website in the summer of 2015.7 For each booth, the data lists the total number of registered voters; men and women turnout; the total votes polled for each candidate, the party affiliation of each candidate for elections of 2009 and 2012. The state has 403 assembly constituencies and around 120,000 polling booths. The first election after the announced intervention was held in 2009. Though the ideal setup is to estimate effects in the 2009 elections, the delimitation in 2008 renders this exercise implausible. Delimitation changed booth identifiers which makes it implausible to match booths in 2009 data with 2007 data, necessary to identify the treated booths in 2009.8 Therefore, I focus on the 2012 elections and identify the critical booths, based on the booth outcomes in 2009. Figure 1.5 summarizes the timeline of the events. 6The original order dated October 24, 2008 can be found here: https://eci.gov.in/files/file/ 108-identification-of-critical-polling-stations-and-measures-to-be-taken-to-ensure-free-and-fair-elections/ 7Link here: https://eci.gov.in/statistical-report/link-to-form-20/ 8Delimitation is the process by which boundaries of the Assembly constituency are redrawn to equalize the population sizes in each constituency. The most recent delimitation occurred in 2002.

6 I merge the 2009 dataset with the 2012 dataset through the booth-id. The merge is not straightforward because of the issues related to data loading and cleaning. I describe the data constuction process and issues in Appendix A.1. The final dataset has 110,000 polling booths, which corresponds to 91% of the total number of polling booths in the state. While the booth data provides information on the voting outcomes, it does not identify which booths actually received booth security. In fact, conversations with some ECI officials at the Delhi office revealed that a centralized database of such booth-level information is not available. The ECI issued guidelines that each booth was required to implement individually. If a booth satisfied the criteria to be critical, it requested the resources. Because of this data limitation, this paper calculates the intent-to-treat estimate. In particular, crossing any threshold does not guarantee treatment. Data on candidate characteristics: In addition to the voting outcomes, I am also interested in estimating the effects on the political outcomes. Because the booth voting data provides the vote share of each candidate, I merge candidates’ vote shares with the information on their characteristics . This data comes from the Association of Democratic Reform (ADR) who digitized affidavits filed by candidates at the time of their nomination.9 The key listed information includes the candidates’ assets, liabilities, educational attainment, gender, and party affliation at the nomination time. Both ADR and ECI data are merged using a fuzzy merge on the party name. I choose to merge on the listed party name instead of the candidate name because multiple candidates in the same constituency often have similar names. Further, a candidate’s name is spelled differently in the ADR and ECI data and merging on the party names reduces the chances of incorrect match. I am able to merge 85 % of the observations. The next section discusses the empirical strategy and the underlying assumptions.

9Beginning 2002, the Supreme court made it mandatory for all candidates to disclose criminal, financial and educational background prior to the polls by filing an affidavit with the Election Commission. See http://myneta. info Fisman et al (2014) used this dataset to show that the annual asset growth of winners is 3–5 percent higher than that of runners-up. Additionally, a follow up paper Fisman et al. (2015) provides evidence that asset disclosure led to exit of low ability candidates post disclosure and also possibily reduced rent extraction by office-holders.

7 1.3 Empirical strategy

The intervention design provides the opportunity to implement a regression discontinuity in two dimensions. The probability that a booth receives extra security measures in 2012 is higher when: (i) the maximum votes polled for any candidate exceeded 75%; and (ii) the total turnout exceeded 75% in the 2009 election. Figure 1.1 graphs the distribution of the two running variables. Each cell in the figure has a dimension of 0.02×0.02. The left panel shows the percentage of observations in each cell. I see that a large number of observations have values close to the center of the two running variables. The right panel illustrates why using booth turnout share in 2009 as a running variable is problematic. Each cell in the right panel shows the average women turnout share in 2009. I find that the colors get lighter as we move from left to right. This points to a correlation between outcomes and the running variable at the baseline. In contast, I do not observe any noticeable change in colors when moving vertically. This suggests a weaker correlation between outcomes and the maximum vote share running variable at the baseline. Table 1.6 further illustrates the issue with the use of the turnout share as a running variable. Each estimate in the first row corresponds to the treatment effect on the relevant baseline outcome when turnout share is used as the running variable. The estimation essentially uses specification 1.1, which I explain later. The table reveals that the baseline outcomes are significant in 2009 even in the absence of treatment. Because of these underlying issues, the main empirical exercise in this paper essentially focuses on the single dimensional regression discontinuity. In particular, I assume that the probability of a booth declared critical increases whenever the maximum votes polled for any candidate in the 2009 election exceeded 75%. Because there are multiple criteria to determine treatment, the increase in the treatment probability at the threshold could be small to detect any effect. For this reason, I perform a "constrained RD", which restricts the sample to booths where the baseline total turnout share in 2009 was higher than 75%. Treatment in 2012 election can be defined as:

8 1 vb ≥ 0.75 Tb = { 0 vb < 0.75 where vb is the maximum vote share for any candidate in booth b in the 2009 election. In short, the treatment is positive when the candidate with maximum votes in past election received more than 75% of the votes. The main empirical strategy in this case follows Imbens and Lemieux (2008) who argue that local linear regression around the cutoff has better properties in terms of bias and precision.10 In particular, the speciﬁcation is as follows:

yb = α0 + α1v˜b + βTb × v˜b + b (1.1) where v˜b = vb − 0.75 is the running variable centered at 0. The constrained speciﬁcation restricts the observations to booths that cross the second threshold.11 I weigh regression 1.1 by a triangular or edge kernel following Meng-Yen-Ching, Fan, James S Marron (1997) who show that a triangular kernel is boundary optimal. Intuitively, this bandwidth gives larger weight to observations close to the cutoff and the weights decrease with the distance to cutoff. 12 Unless speciﬁed, I use the optimal bandwidth proposed by Imbens and Kalyanaraman (2012), which is a data-dependent bandwidth and obtained by minimizing mean squared error loss function with a regularization adjustment. I perform regression discontinuity analyses for two outcome variables: (i) female turnout as a share of total turnout in 2012; and (ii) the change in the female turnout share between 2012 and 2019. (i) compares level differences in the outcome around the threshold while (ii) compares differences in trend in female turnout share between 2009 and 2012. An advantage of the latter

10Cheng et al. (1997) show that for a boundary point the local linear method is 100% efﬁcient among linear estimators in a minimax sense. 11Since both the running variables have the same cutoff: 0.75. 12Speciﬁcally, the edge kernel is expressed as: r r K (r ) = 1 | ik | ≤ 1 . 1 − | ik | (1.2) h ik h h where h denotes the bandwidth.

9 approach is that it allows me to control for unobserved ﬁxed booth-level differences and reduces bias. When measuring political outcomes, I use level outcome because of the lack of baseline data. Just like any single-dimensional regression discontinuity design, the two basic assumptions necessary for an unbiased estimation are: (i) the conditional expectation of the counterfactual outcomes is continuous in the running variable around the threshold; and (ii) there is no manipulation of the running variable around the threshold. For the contrained sample, the treatment effect βˆ is essentially:

ˆ β = Etb ≥0.75τ(tb) = Etb ≥0.75{E↑0(yb|vb = 0.75 + ,tb = t˜) − E↓0(yb|vb = 0.75 + ,tb = t˜)} (1.3)

where tb ∈ [0.75,1] represents the second running variable—past turnout share, τ(t˜) denotes the treatment effect at the threshold for all booths where the past turnout share is t˜

τ(t˜) = E↑0(yb|vb = 0.75 + ,tb = t˜) − E↓0(yb|vb = 0.75 + ,tb = t˜) (1.4)

and the continuity assumption requires that all other booth covariates xb are balanced around the threshold.

τ(t˜) = E↑0(xb|vb = 0.75 + ,tb = t˜) = E↓0(xb|vb = 0.75 + ,tb = t˜) (1.5)

In short, restricting the sample to all booths with turnout greater than 0.75 essentially calculates the average of estimand 1.4 weighted over all t˜ ≥ 0.75. The no manipulation assumption can be partially tested using McCrary Density test (2008) which tests for any signiﬁcant differences in the running variable density around the threshold. Figure 1.8 presents the density of the running variable—maximum candidate vote share in 2009. There does not appear to be any discernible difference in the running variable density at the threshold. The continuity assumption implies that the pre-determined outcomes are continuous around

10 the threshold. The second panel of Table 1.1 performs local linear regression for the baseline 2009 outcomes for the constrained sample using specification 1.1 and the IK bandwidth. There is no significant change at the threshold for any variables such as aggregate female and male turnout and registered voters. However, the female turnout share has a p-value of 0.066, which is con- cerning. Because not all baseline outcomes are balanced at the threshold, I instead use the booth level change in the turnout share as the outcome variable. This controls for any unobservable fixed differences in booth characteristics on either side of the threshold.

1.3.1 The cutoff and the First stage

Equation 1.1 calculates the intention-to-treat estimate, which is the difference in the outcomes of booths more likely to be treated and booths less likely to be treated. A relevant parameter of interest is the Local Average Treatment Effect (LATE), which captures the effect of tightened security on the outcomes of the complier booths. Compliers include booths for whom crossing the threshold leads to a change in status from no-treatment to treatment. LATE is essentially the term 1.1 divided by the ﬁrst stage.

Et˜≥ . {E↑0(yb|vb = 0.75 + ,tb = t˜) − E↓0(D|vb = 0.75 + ,tb = t˜)} βˆL = 0 75 (1.6) Et˜≥0.75{E↑0(D|vb = 0.75 + ,tb = t˜)}

Converting ITT estimates into LATE requires the knowldge of the first stage. Unfortunately, ECI did not maintain centralized records of treated and non-treated booths. Booth officers requested security forces if criteria suggested by ECI were met. Despite thorough research, I could not obtain information on the booth-wise treatment status. However, an official report by a District Election Officer in Nalanda, Bihar provides some suggestive insight into the first stage. For Je- hanabad Parliamentry Constituency in 2012, 246 polling booths satisfied the maximum vote share

246 criterion and 347 polling booths were treated, indicating probability of treatment of ( 347 = 0.7). Given ITT estimate, I obtain LATE estimates by dividing the ITT estimate by 0.7. 13

13A copy of the report can be found here.

11 1.4 Results and Discussion

1.4.1 Summary Statistics

Table 1.3 summarizes the voting outcomes in 2009 and 2012. There are nearly 115,000 booths in the sample. A booth had nearly 900 registered voters on average in 2009. Less than half of the registered voters voted. There was a significant gender gap in the voter turnout, with the female turnout almost half of the male turnout, which partly reflects the underlying gender disparity in the voter registration. Unfortunately, the data does not report the gender decomposition in voter registration. Figure 1.7 plots the distribution of female and male turnout in 2009. Female voting distribution lies far left of the male distribution in 2009. A larger number of voters voted in 2012 and a larger share was female. The average registered voters increased to 954 in 2012, a consequence of the growing population. Interestingly, the second panel reveals that the gender gap in turnout improved in 2012. The female share as a share of total turnout increased from 41% in 2009 to 45% in 2012, an increase of 4 percentage points. There was also a significant increase in turnout. Finally, the share of maximum votes polled in favor of any candidate at a booth fell from over 52% in 2009 to 48% in 2009. The 2012 elections consisted of candidates with "criminal" charges against them, very few females and significant variation in declared assets. Table 1.4 summarizes the average candidate characteristics, by the party affliation. The fraction of women candidates in 2012 stood at around 7%. A non-significant fraction of candidates were recontestants. This fraction was understandably highest for the incumbent party (BSP). The recontesting ministers reported a positive asset growth that ranged from a million rupees for a BJP candidate (around $1666) to approximately nine million rupees ($150,000) for a recontesting minister from BSP. These figures are significant and consistent with Fisman et al. (2014) finding of significant private returns to holding public office.

12 1.4.2 Voting outcomes

This subsection presents results for voting outcomes. In particular, I restrict the sample to booths that cross the turnout share threshold. I then perform a local linear estimation around the threshold in the maximum vote share running variable. The top panel of Table 1.1 presents the results of the constrained regression discontinuity. Each column reports the regression estimate using specification 1.1 and the IK bandwidth. The square brackets indicate the p-value. I find that the effect on the total turnout is insignificant. In contrast, the effect on the female turnout share is negative. This is partly reflected by the unbalancedness in this variable at the baseline, as seen by the 2009 estimate in the bottom panel of Table 1.1. For this reason, I present results for the change in female turnout share between 2012 and 2009 (Column 6). I find that the women share in the total turnout is higher by 1.4% in booths just to the right of the threshold compared with the booths just to the left. Figure 1.2 plots the effect of increasing poll booth security on the change in the female turnout share. The left panel presents the raw data in a 0.25 window around the threshold. The points represent the average of the outcome variable in bins of length 0.03 . I find a clear jump in the female share change at the threshold, which is confirmed in the right panel that plots the confidence interval around the local linear estimate. Column 6 in Table 1.1 suggests that the female turnout increased by 1.8% in the booths to the right of of the threshold compared to the booths just to the left of the threshold. This translates into

1.8 a LATE estimate of 0.7 = 2.5 using the first-stage as discussed in 1.3.1. I perform several robustness tests. Table 1.5 reports the results for the same specification but in the unconstrained sample. None of the estimates are significant. A plausible reason could be that the probability of treatment on the right hand side of the threshold in the unconstrained specification is not high enough to detect an effect. Another possibility could be that the observed effect on the change in female turnout share is pure noise. In Section 1.4.4, I discuss and perform a permulation test. The test rejects the hyothesis that the estimated point effect is an attribute of the data. The point estimate is also robust to varying the bandwidth around the threshold. The

13 top panel of Figure 1.9 shows the the point estimate largely remains unchanged as we vary the bandwidth from 0.4IK to 1.4IK. The discussion so far ignored the plausible mechanisms by which tightened security measures increased the women turnout. As highlighted in Section 1.1, the observed effect can be due to two channels. First, violence due to booth capturing restricted women turnout in the past. Conse- quently, tightened security measures removed violence and allowed women to vote. The second possibility is that bogus votes led to lower reported women turnout in previous elections. Tightened security measures removed bogus voting which resulted in higher reported women turnout. Disen- tangling the two channels in the absence of more data is difficult. However, if the second channel is the only operative channel, I expect total (reported) turnout to decrease as a result of fewer bogus votes. In contrast, Column 7 in Table 1.1 shows that the change in the total turnout share, defined as turnout divided by registered voters, is positive and insignificant at the IK bandwidth. In fact, Figure 1.9 illustrates that the point estimate is significant at 1.4 times the IK bandwidth which provides suggestive evidence that the higher reported women turnout reflects an actual increase.

1.4.3 Political Outcomes

I use the booth-level voting outcomes merged with the candidate characteristics to estimate the effects on the political outcomes. I focus on four outcomes: (i) the vote share of the incumbent party candidate; (ii) the vote share of the female candidates; (iii) the vote share of the corrupt candidates and; (iv) the vote share of educated candidates. Corrupt candidates are defined as recontestants with a positive asset growth in the office. I draw this measure of corruption from the previous literature (Fisman et al. 2015). The candidates who held a graduate degree or higher are tagged as educated. The final dataset has 1,350 candidates contesting elections at 352 constituencies encompassing 115,812 polling stations. Approximately 245 candidates are recontestants, of which only 3 had non-positive asset growth. 850 candidates ( 60% ) have at least a graduate degree. Only 7% of the contestants are females, which is consistent with a low female political participation in India.

14 I chose the outcome variables for the following reasons. Incumbent candidates’s vote share is relevant because there is some evidence that females tend to vote against the incumbent party (Gine and Mansuri 2018; Ravi and Kapoor 2014). I estimate the effect on female, educated and corrupt candidates because there is suggestive evidence that elections dominated by violence tend to favor corrupt candidates (Vaishnav 2012; Witsoe 2013) and disfavor minorities such as females. I use the empirical approach similar to the voting outcomes. Because I do not have the baseline political outcomes, I use specification 1.1 and the IK bandwidth to estimate the effect on levels around the threshold. Table 1.2 reports the estimates. The top panel presents the results using the constrained sample, which restricts to booths with more than 75% turnout in the 2009 election. I find that none of the estimates are significant in the constrained specification. The standard errors are large compared with the point estimates, perhaps due to noise. Therefore, in the bottom panel, I present the results from the unconstrained sample. We interpret the following results as more suggestive than causal. I find that for the unconstrained sample (Table 1.2), the point estimate for female is still insignificant whereas the point estimate for the incumbent party candidates is statistically significant and negative. In contrast, the point estimate for the educated candidates is significant and positive. The vote share of the corrupt candidates is lower by 1.6 percentage points in booths just to the right of the threshold, compared with the booths just to the left. Figures 1.3a, 1.3b, 1.3c and 1.3d plot the four outcomes as a function of the running variable in the unconstrained sample. The dots represent the binned outcome mean whereas the line represents the local linear fit using the IK bandwidth. The grey region denotes the 95% confidence interval. The discontinuity in the raw data is clearly visible for the incumbent vote share outcome. For other outcome variables, the discontinuity is less obvious. The next subsection performs a permutation test.

15 1.4.4 Permutation Test

Is it possible that the point estimate reﬂects some unusual characteristic of the threshold rather than a real effect? To check for this possibility, I perform a permutation test ala Fisher 1935.14

In particular, I take a random draw of hypothetical maximum vote share threshold from (0,0.6). I then calculate the hypothetical treatment effect using specification 1.1 and the IK Bandwidth. Intuitively, if the treatment had a real effect on the outcome, I expect the estimated coefficient at the real threshold to be an outlier on the distribution of the simulated treatment effects. I perform this test for every outcome considered in this paper. Figure 1.10 plots the empirical cumulative distribution of the treatment coefficients female turnout change for 600 draws. The vertical line represents the actual treatment coefficient estimated using the main specification at the true threshold of 0.75. I find that the p-value of the estimated coefficient at the true threshold in the simulated distribution is 0.007. This provides evidence in favor of the hypothesis that the estimated treatment coefficient at the true threshold is an outlier and likely represents the actual treatment effect. Figure 1.11 repeats the same process for the political outcomes using 300 draws of each outcome. The p-values are indicated on the graph. Around 11% of the simulated draws in the incumbent vote share and highly-educated vote share have point estimates lower than the estimated effect at the actual threshold. (The corresponding p-values are 0.11 and 0.113 ) For female candidate outcome, 16% of the draws have simulated treatment effect higher than the effect obtained at the actual threshold. (The p-value is 0.16). The corrupt candidates vote share outcome is more robust with p-value of 0.03. Overall, while I detect some effect for the poltical outcomes, the permutation tests do not provide strong evidence against the hypothesis that these estimates are mere noise. It is also possible that some of the booths in the simulation region were also treated, perhaps because they satisfied other criteria. 15 This suggests that political outcomes effects should be

14First proposed by Fisher 1935, this test has been used in multiple economics papers including Chetty et all. 2009. The advantage of this test is that it is distribution-free and inference does not require a large sample size. 15For instance, if they witnessed violence or reported malfesence in the previous election. Unfortunately, the data limitation prevents us from exploring this in further detail.

16 interpreted with caution.

1.4.5 Discussion

There are a few reasons why women turnout responds to tighter polling booth safety. First, the deployment of a massive police force reduces the likelihood of violence and makes the election a safer event. This is important in this context because the prevalence of electoral violence around the polling booths on the election day in India is well-documented (Witsoe 2013). A consequence is that when women are more vulnerable to violence than men (Quraishi 2014), women vote in higher numbers. Second, the dominance of electoral malpractices favors candidates such as corrupt politicians with access to strongmen who have access to illicit means, which undermines the fairness of the elections. Consequently, removing such barriers makes the elections a level-playing field. Further, because the aim of enhancing security at polling booths was to reduce electoral violence, the results suggest that minorities, specifically females, are a target of the electoral violence. 16 This has parallel to the United States where the authors have shown that specific barriers such as distance to the polling booth (Cantoni 2019); poll tax (Naidu 2012); and awareness campaigns (Gine and Mansuri 2018) affect some minority sections more than the others. My paper suggests that providing a safer election environment increases female representation in the turnout. Some descriptive studies have highlighted the phenomenon of rising female turnout in India in recent years. For instance, women for the first time outnumbered men in turnout in the Bihar state elections (another state known for electoral violence) just three years after the period in this study. Media reported such women as the "agents of change" and likely responsible for the election with a full majority of the Chief Minister.17 In his book, S.Y. Quraishi, chief of the election commission who spearheaded this election reform, explains that while studying the gender

16Another group of minorities includes voters belonging to the scheduled castes and scheduled tribe, who are likely affected by this intervention as well. Unfortunately, the decomposition of the voter turnout by caste is not available at the booth-level and renders that exercise implausible. 17See this press article describing the phenomenon and probable measures that contribute to this: https://zeenews.india.com/exclusive/increase-in-women-voter-turnout-in-india_ 3488.html

17 behavior among voters in Bihar, he found that women felt the need for a more safe and secure voting environment. It is not far-fetched to imagine that tightened security measures contributed to an electoral shift in India.

1.5 Conclusion

This paper uses a policy experiment in a major state election in India to study the effect of the increased poll-booth safety on voting and political outcomes. The deployment of the security forces to polling booths was determined such that the booths with the past maximum candidate vote share higher than 75% were more likely to receive extra security measures. Using a regression discontinuity design, I estimate that the increase in the probability of treatment increased women share in total turnout. Furthermore, polling booths with a higher probability of receiving security treatment were associated with lower vote share of candidates belonging to the incumbent party and corrupt candidates, and a higher vote share of candidates with at least a graduate degree. It is worth noting that the effect on political outcomes is less robust and should be interpreted with caution. Nevertheless, results in this paper point to the role of safer elections in adequate gender representation in the election outcomes.

18 1.6 Figures and Tables

Figure 1.1: Two Dimensional RD

These ﬁgures illustrate the distribution along the two running variables. Y-axis denotes the ﬁrst running variable: maximum candidate vote share in 2009. X-axis denotes the second running variable: turnout share in 2009. The policy cutoff was at (0.75, 0.75). Passing this threshold formed one of the criteria for treatment— increased security at the polling booth in the 2012. Panel (a) graphs the percentage observations in each cell. Panel (b) graphs the female turnout as a share of registered voters in 2009. Dataset: Booth voting outcomes, Election Commission of India, 2009-12.

19 Figure 1.2: Effect of Poll-booth security

These figures illustrate the effects of increasing security at the polling booths on the female turnout share. Outcome variable in either figure is the change in the female turnout share between 2009 and 2012. Running variable is the maximum vote share polled for a candidate in 2009. A polling booth was more likely to be treated with extra security measures in 2012 if it satisfied the following two criteria: (i) turnout in the past election (2009 in this case) was greater than 75%; and (ii) the maximum votes polled for any candidate at the booth in 2009 was greater than 75%. The sample is restricted to those polling booths which had more than 75% turnout in 2009 election, which allows to convert the 2-dimensional problem into 1-dimension and increases the probability that a booth on the right of the threshold was treated. The figure on the left hand side denotes the raw data. The figure on the right hand side shows the local linear fit estimated using the IK bandwidth, where the dots represent the mean outcome in bins of width 0.04. Dataset: Booth voting outcomes, Election Commission of India, 2009-12.

20 (a) Vote Share of Incumbent (b) Vote Share of Female Candidates

Figure 1.3: Political Outcomes Each ﬁgure provides graphical evidence of the effect of increased poll-booth security on the booth- level political outcomes in the unrestricted sample. The outcomes variables are explained as follows: (i) "Female" denotes the vote share of the female candidates; (ii) "Incumbent" denotes the vote share of incumbent party candidates; iii) "Educated" denotes the vote share of candidates with at least graduate degree; (iv)"Corrupt" denotes the vote share of recontestants with a positive asset growth in the ofﬁce. Dataset: Booth voting outcomes, Election Commission of India, 2009-12 and Association of Democratic Reform 2012

21 Female12 Male12 Turnout12 Voters12 Female_Share Delta_Share Delta_Turnout Voting outcomes in 2012: Treat 1.462 3.726 6.242 -1.627 -0.008 0.018 0.014 (12.329) (13.399) (25.038) (33.986) (0.004) (0.005) (0.015) [0.906] [0.781] [0.803] [0.962] [0.047] [0.000] [0.342] v˜b -39.519 -110.213 -158.805 -311.389 0.120 -0.069 0.159 (80.967) (83.874) (155.927) (218.728) (0.040) (0.013) (0.127) [0.626] [0.189] [0.309] [0.155] [0.003] [0.000] [0.213] Tb × v˜b -200.431 -196.907 -402.024 -393.562 -0.043 0.160 0.140 (139.510) (137.590) (260.531) (354.703) (0.060) (0.025) (0.180) [0.151] [0.153] [0.123] [0.267] [0.477] [0.000] [0.437] Dep. Var Mean 254.067 303.049 556.689 728.254 0.459 -0.010 -0.069 (7.068) (7.990) (14.639) (20.390) (0.003) (0.003) (0.011) [0.000] [0.000] [0.000] [0.000] [0.000] [0.000] [0.000] Obs 1,574.000 1,746.000 1,714.000 1,708.000 1,211.000 3,339.000 1,482.000 Bandwidth 0.172 0.189 0.186 0.186 0.133 0.429 0.164

Female09 Male09 Turnout09 Voters09 Female_Share Voting outcomes in 2009: Treat -9.425 2.289 -5.322 -2.901 -0.010 (11.765) (13.288) (24.664) (28.287) (0.005) [0.423] [0.863] [0.829] [0.918] [0.066] v˜b -273.176 -294.940 -593.172 -485.878 0.021 (94.466) (106.278) (203.931) (204.180) (0.034) [0.004] [0.006] [0.004] [0.017] [0.545] Tb × v˜b -69.750 71.953 11.122 -37.985 -0.156 (131.962) (171.967) (307.171) (319.996) (0.056) [0.597] [0.676] [0.971] [0.906] [0.005] Dep. Var Mean 233.099 266.671 498.645 597.343 0.460 (7.964) (8.174) (15.880) (17.916) (0.003) [0.000] [0.000] [0.000] [0.000] [0.000] Obs 1,659.000 1,415.000 1,478.000 1,611.000 1,740.000 Bandwidth 0.180 0.156 0.162 0.176 0.188

Table 1.1: Voting Outcomes This table reports the effect of increasing security at the polling booths on the voting outcomes. Each estimate is obtained from the the regression of the outcome variable using 1.1. This regression performs a local linear estimation around the cutoff. The regression is weighed by a triangular kernel that uses an IK bandwidth. All estimates are cross-section averages except "delta_share" which is the change in the booth female turnout share between 2012 and 2009. Robust standard errors are shown in parantheses. p-values are reported in the square brackets. The sample is restricted to booths that had at least 75% turnout in 2009 election. Dataset: Booth voting outcomes, Election Commission of India, 2009-12.

22 Female Incumbent Educated Corupt Treat -0.011 -0.022 0.011 0.016 (0.035) (0.023) (0.016) (0.032) [0.752] [0.337] [0.472] [0.613] v˜b -0.349 -0.134 -0.053 -0.394 (0.328) (0.134) (0.096) (0.280) [0.288] [0.316] [0.579] [0.160] Tb × v˜b 1.138 0.347 -0.163 0.374 (0.771) (0.223) (0.168) (0.490) [0.141] [0.119] [0.334] [0.445] Dep. Var Mean 0.181 0.321 0.198 0.315 (0.032) (0.022) (0.013) (0.030) [0.000] [0.000] [0.000] [0.000] Obs 632.000 2,029.000 4,434.000 925.000 Bandwidth 0.113 0.213 0.191 0.138

Female Incumbent Educated Corrupt Treat 0.009 -0.013 0.007 -0.018 (0.011) (0.006) (0.004) (0.006) [0.392] [0.017] [0.049] [0.002] v˜b -0.014 -0.204 -0.066 0.013 (0.062) (0.035) (0.021) (0.010) [0.824] [0.000] [0.002] [0.169] Tb × v˜b -0.043 0.305 -0.070 0.164 (0.142) (0.073) (0.045) (0.057) [0.762] [0.000] [0.118] [0.004] Dep. Var Mean 0.206 0.276 0.218 0.316 (0.009) (0.006) (0.003) (0.004) [0.000] [0.000] [0.000] [0.000] Obs 9,640.000 34,426.000 88,356.000 73,265.000 Bandwidth 0.178 0.171 0.185 0.419

Table 1.2: Political Outcomes

This table reports the effect of increasing security at the polling booths on the booth-level political outcomes. The top panel reports the estimates for the constrained sample, which includes the booths with at least 75% turnout in previous election. The bottom panel reports the corresponding estimates in the full sample. Each column reports the estimate according to the speciﬁcation 1.1. This regression performs a local linear estimation around the cutoff. The regression is weighed by a triangular kernel that uses an IK bandwidth. Robust standard errors are shown in parantheses. p-values are reported in square brackets. The outcomes variables are explained as follows: (i) "Female" denotes the vote share of the female candidates; (ii) "Incum- bent" denotes the vote share of the candidate belonging to the incumbent party; (iii) "Educated" denotes the vote share of candidates with at least a graduate degree; (iv)"Corrupt" denotes the vote share of recontestants with a positive asset growth in the ofﬁce. Dataset: Booth voting outcomes, Election Commission of India, 2009-12 and Association of Democratic Reform 2012.

23 1.7 Supportive tables and Figures

Mean SD Min p25 p50 p75 max Voting outcomes in 2009 Registered voters 914.56 311.01 73.00 693.00 906.00 1150.00 2639.00 Female turnout 183.58 77.95 0.00 127.00 175.00 230.00 3345.00 Male turnout 255.88 96.17 0.00 186.00 248.00 316.00 913.00 Total turnout 439.47 164.81 1.00 320.00 426.00 543.00 3703.00 Max vote share 0.52 0.16 0.00 0.41 0.49 0.62 14.40 Max Votes 228.56 111.91 0.00 149.00 208.00 284.00 1030.00 Voting outcomes in 2012 Registered voters 954.64 302.31 0.00 742.00 946.00 1176.00 2620.00 Female turnout 263.20 94.62 0.00 195.00 255.00 322.00 792.00 Male turnout 316.77 116.11 0.00 234.00 307.00 389.00 990.00 Total turnout 579.97 203.22 0.00 436.00 565.00 707.00 1741.00 Max vote share 0.49 0.72 0.00 0.37 0.46 0.57 237.95 N 115812

Table 1.3: Summary Statistics: Voting outcomes This table provides summary of voting outcomes. Dataset: Booth voting outcomes, Election Commission of India, 2009-12.

24 Figure 1.4: Spatial location of polling booths

This ﬁgure shows the location of the polling booths in the‘Varanasi South’ Assembly Constituency in Varanasi District of Uttar Pradesh as an example. The red lines depict the boundary of the constituency. A constituency elects a representative to the state assembly. This is achieved through ballot casting at mutiple booths within the constituency. An average constituency has around 200- 300 booths and each booth serves two-thousand voters on average.

25 Figure 1.5: Events timeline

This figure illustrates the timeline of events. The first election in Uttar Pradesh after the announced policy change was in 2009. The probability that a booth is treated in 2009 was determined by the booth outcomes in 2007. However, redrawing of the constituency boundaries in 2008 changed the booth identifiers. Because booths in 2009 can not be matched with the corresponding booth information in 2007, this paper studies the outcomes in 2012 and the treatment probabilities are determined by 2009 outcomes.

26 Figure 1.6: Distribution of female turnout share in 2009

This ﬁgure plots the distribution of the turnout as a share of the total turnout, by gender in 2009. Historically, females turnout iis lower than the male turnout.

Figure 1.7: Distribution of total turnout as a share of running variable

This ﬁgure illustrates the distribution of the total turnout as a function of the running variable. The running variable is the maximum candidate vote share in the 2009 election. All polling booths with the maximum vote share greater than 75% had a higher probability of receiving extra security measures in 2012 elections

27 Figure 1.8: McCrary density test

This ﬁgure performs the McCrary test for the running variable: maximum candidate vote share in 2009. This tests for any signiﬁcant differences in the density around the cutoff. Presence of such differences could indicate manipulation around the cutoff.

28 Figure 1.9: Estimate as a function of speciﬁed bandwidth

These ﬁgures show how the effect of increased poll-booth safety on i) the female vote share, and ii) total turnout change varies with the bandwidth. b represents the fraction of IK bandwidth— for example b = 0.5 represents the treatment effect estimate at half the IK bandwidth. The IK bandwidth for the outcome variable is 0.40. The dashed lines denote 95% conﬁdence interval. 29 Figure 1.10: Hypothetical simulated treatment effects

This ﬁgure plots the distribution of the simulated treatment effects where a hypothetical cutoff is drawn from [0,0.6]. The running variable is the maximum candidate vote share in 2009. The sample is restricted to booths with turnoff greater than 75% to convert the two dimensional regression discontinuity into a single dimension.

30 (a) Vote Share of Incumbent (b) Vote Share of Female Candidates

Figure 1.11: Hypothetical treatment effect: Political outcomes Each ﬁgure plots the simulated treatment effects at hypothetical thresholds drawn from the distribution [0,0.6]. The outcomes variables are explained as follows i) Female denotes the vote share of the female candidates. ii) Incumbent denotes the vote share of incumbent party candidates. iii) "Educated" denotes the vote share of candidates with at least graduate degree. iv) Rerun, a proxy for the corrupt candidates, denotes the vote share of re-contestants with a positive asset growth in the ofﬁce. Dataset: Booth voting outcomes, Election Commission of India, 2009-12 and Associa- tion of Democratic Reform 2012

31 Mean SD Min p25 p50 p75 Max BJP No. of Criminal cases .7827781 1.753594 0 0 0 1 20 Female .0953439 .2936907 0 0 0 0 1 Assets 1.98e+07 3.33e+07 31395 4309400 9708000 2.24e+07 3.75e+08 Liabilities 1812002 6107091 0 0 300000 1227484 6.70e+07 Votes 86.14944 103.3398 0 12 45 126 996 Asset growth 1380931 6229025 -1.24e+07 0 0 0 7.92e+07 If rerunning .1058796 .3076849 0 0 0 0 1 N 112949 INC No. of Criminal cases .7052316 1.427708 0 0 0 1 12 Female .0810269 .2728778 0 0 0 0 1 Assets 3.16e+07 1.00e+08 96586 4774985 1.03e+07 2.14e+07 1.41e+09 Liabilities 1792579 5975859 0 0 247448 1161090 5.82e+07 Votes 76.91737 92.66359 0 14 41 107 1058 Asset growth 2631430 2.58e+07 0 0 0 0 4.77e+08 If rerunning .0739859 .2617493 0 0 0 0 1 N 98708 BSP No. of Criminal cases .6851747 1.806414 0 0 0 1 23 Female .0693322 .2540193 0 0 0 0 1 Assets 3.28e+07 7.38e+07 581000 8030000 1.38e+07 3.00e+07 9.53e+08 Liabilities 4869028 4.19e+07 0 0 554000 2613508 8.12e+08 Votes 148.5319 118.3505 0 60 122 207 1163 Asset growth 9056343 4.31e+07 0 0 0 9080304 7.99e+08 If rerunning .326172 .4688131 0 0 0 1 1 N 116598 SP No. of Criminal cases 1.571623 3.276041 0 0 0 2 27 Female .0705496 .2560721 0 0 0 0 1 Assets 2.57e+07 4.08e+07 42000 6650000 1.32e+07 2.84e+07 4.05e+08 Liabilities 1205257 2779879 0 0 212000 1127000 1.97e+07 Votes 166.4724 133.0281 0 64 138 237 1192 Asset growth 3098325 9809103 -2.94e+07 0 0 0 8.78e+07 If rerunning .205185 .4038385 0 0 0 0 1 N 114175

Table 1.4: Summary statistics: Political Outcomes This table summarizes booth-level political outcomes, by party afﬂiation. I report the four major parties. Note that in the outcome year 2012, incumbent party was BSP and the challenger party was SP. Dataset: Booth voting outcomes, Election Commission of India, 2009-12 and Association of Democratic Reform 2012.

32 Female12 Male12 Turnout12 Voters12 Female_Share Delta_Share Voting outcomes in 2012: Treat 2.953 0.237 2.220 12.863 0.000 -0.001 (2.094) (3.175) (5.136) (6.985) (0.001) (0.002) [0.159] [0.941] [0.666] [0.066] [0.840] [0.639] v˜b -29.768 -23.142 -53.606 -235.879 0.008 -0.014 (10.425) (26.851) (36.146) (35.334) (0.009) (0.013) [0.004] [0.389] [0.138] [0.000] [0.423] [0.286] Tb × v˜b -96.395 -1.871 -76.956 -298.489 -0.058 0.012 (20.994) (47.244) (66.028) (73.051) (0.018) (0.022) [0.000] [0.968] [0.244] [0.000] [0.001] [0.592] Dep. Var Mean 254.338 309.336 563.735 908.757 0.453 0.036 (1.276) (2.040) (3.257) (4.201) (0.001) (0.001) [0.000] [0.000] [0.000] [0.000] [0.000] [0.000]

Female09 Male09 Turnout09 Voters09 Female_Share coef/s.e./p coef/s.e./p coef/s.e./p coef/s.e./p coef/s.e./p Voting outcomes in 2009: Treat 2.171 1.383 3.489 15.964 0.001 (2.117) (2.803) (4.733) (8.590) (0.002) [0.305] [0.622] [0.461] [0.063] [0.593] v˜b 1.399 -7.479 -4.714 -282.322 0.020 (17.769) (26.761) (44.261) (70.494) (0.018) [0.937] [0.780] [0.915] [0.000] [0.272] Tb × v˜b -53.317 11.366 -42.894 -128.880 -0.068 (30.729) (45.528) (75.418) (125.466) (0.030) [0.083] [0.803] [0.570] [0.304] [0.026] Dep. Var Mean 182.554 252.895 435.499 862.249 0.417 (1.366) (1.834) (3.083) (5.446) (0.001) [0.000] [0.000] [0.000] [0.000] [0.000]

Table 1.5: Voting Outcomes: Unconstrained Regression Discontinuity This table reports the effect of increasing security at the polling booths on the voting outcomes. Each estimate is obtained from the regression 1.1. This regression performs a local linear estimation around the cutoff. The regression is weighed by a triangular kernel that uses an IK bandwidth. All estimates are cross-section averages except ‘delta_share’ which is the change in the booth female turnout share between 2012 and 2009. Robust standard errors are shown in parantheses. p- values are reported in the square brackets. Dataset: Booth voting outcomes, Election Commission of India, 2009-12.

33 Female09 Male09 Turnout09 Voters09 Voting outcomes in 2009: Treat -31.495 -57.842 -89.992 -33.564 (4.085) (6.448) (10.942) (12.094) [0.000] [0.000] [0.000] [0.006] v˜b 238.278 222.342 461.200 -765.923 (4.872) (8.562) (13.535) (20.754) [0.000] [0.000] [0.000] [0.000] Tb × v˜b -328.646 -180.950 -604.491 -696.418 (63.219) (173.456) (263.482) (167.830) [0.000] [0.297] [0.022] [0.000] Dep. Var Mean 239.205 307.389 547.040 694.659 (1.489) (2.603) (4.170) (5.590) [0.000] [0.000] [0.000] [0.000]

Table 1.6: Regression Discontinuity using previous turnout share as running variable This table reports results of the tests for continuity of the baseline outcomes using the alternative running variable—booth turnout percentage in 2009. Each estimate is obtained from the regression 1.1. This regression performs a local linear estimation around the cutoff of 0.75. The regression is weighed by a triangular kernel that uses an IK bandwidth. Robust standard errors are shown in parantheses. p-values are reported in the square brackets. Dataset: Booth voting outcomes, Election Commission of India, 2009.

34 Chapter 2: Merging to Dodge Taxes? Unexpected Consequences of VAT

Adoption in India

Recent empirical work in public economics has investigated tax instruments’ ability to raise substantial tax revenues in developing countries in which tax enforcement is inadequate (Pomeranz (2015); Best et al. (2015)). Less studied is the effect of tax instruments on the real decisions of firms that are crucial players in the collection and remittance of taxes. An important question is: Do firms respond to the tax evasion incentives created by tax instruments? Or in the context of this paper, do firms reorganize their production to dodge taxes? An optimal tax does not maintain production efficiency when firms reorganize to evade taxes (Kopczuk and Slemrod (2006)). Under value-added Tax (VAT)—the world’s most popular consumption tax—tax evasion opportunities vary significantly along the production chain. A VAT-remitting firm pays tax on the net value added and is required to provide invoices for its purchases to claim input tax credit. This generates a paper trail for firm-to-firm transactions and allows stricter enforcement of the tax. Consequently, VAT has been successful in reducing evasion and increasing tax revenues. Several countries have switched to VAT in the recent past as illustrated in Figure 2.1 except for the United States, where there is debate regarding whether the country should move to VAT. However, the research has shown that the self-enforcement mechanism under VAT unravels at the last (retail) stage at which there is no cross-reporting by consumers. Slemrod (2007) refers to this enforcement problem at the last stage as the “Achilles heel” of administering VAT.1 In this paper, I show that the ability to evade at the last stage also has consequences for the organization of firms along the production chain.

1Many governments around the world aim to strengthen this part of VAT by offering incentives to consumers to ask for receipts. Naritomi (2013) shows, in the context of Brazil, that an anti-tax evasion program that provided monetary rewards for consumers to ensure that firms report final sales transactions increased reported firms’ revenues by at least 22% over 4 years.

35 The absence of cross-reporting by consumers under VAT implies that in contrast to an unintegrated second-to-last firm that sells to a downstream firm, an integrated retail firm that sells to consumers can evade taxes on its sales. This ability to evade tax at the last stage creates an incentive for the second-to-last firm in the production chain to integrate with the last firm (Kopczuk and Slemrod (2006)), which allows the integrated firm to make larger sales to consumers that are not subject to cross-reporting. A testable prediction is that we expect greater vertical integration in firms closer to the last stage than firms further up the chain when tax enforcement is imperfect under VAT. 2 In this paper, I use a unique quasi-experiment in India, where the state-level retail sales tax (RST) was replaced by VAT in a staggered manner across states. Replacement of RST with VAT provides an exogeneous shock to tax evasion opportunities along the chain. This is because in RST, only the last firm faces any tax liability, and therefore, other firms have no tax-evasion incentive. In contrast, under VAT, all firms remit tax. Furthermore, the ability to evade tax confers an advantage on being the last firm in the chain. I use a staggered differences-in-differences research design to show that a state’s VAT adoption significantly increases vertical integration in firms. Moreover, evidence suggests that the effect is largest for firms closer to the retail stage, which suggests that tax evasion is a plausible mechanism. To measure vertical integration, I construct a measure of product upstreamness using plant- level input-output data (Annual Survey of Industries). Specifically, I use a measure of product upstreamness from the trade literature (Acemoglu et al. (2010); Antras et al. (2012); Antrás and Chor (2013); Fally (2011); Alfaro et al. (2016)). A product that is used more as an input to other products and/or in the production of more upstream products is assigned a higher value of upstreamness. I use the input-output data to construct an upstream index for each product in the sample. To test the effect on vertical integration, I use the fact that a more vertically integrated firm

2Another channel through which ﬁrms might dodge taxes is by selling directly to consumers instead of integrating with the downstream ﬁrm. Unfortunately, testing this is beyond the scope of this paper. We can think of results in this paper as a lower bound to the actual treatment effect.

36 sources inputs that are more upstream, and the vertical distance between its inputs and outputs is higher. Therefore, an increase in vertical integration leads to an increase in the upstreamness of firm inputs (and consequently, an increase in the vertical distance between its inputs and outputs). I also provide more direct evidence of vertical integration by estimating the effect of VAT adoption on vertical and horizontal mergers of firms in this period. The identifying assumption is that the time trends in vertical integration in states that adopted VAT earlier do not differ significantly from states that adopted later, in the absence of VAT adoption. Additionally, the two-way fixed effect specification estimates the average treatment effect when the following hold: homogeneous treatment effects (de Chaisemartin and D’Haultfoeuille (2019)) and time-invariant treatment effects (Goodman-Bacon (2018)).3 Though it was agreed in 2002 that all states would introduce VAT with effect from April 2003, they adopted VAT with varied lags. Political and administrative reasons contributed to the state-specific delay in implementation. Reasons included forthcoming state elections and disagreement between ruling federal and state governments on VAT implementation. Despite observed parallel trends in the pre-treatment period, I cannot rule out heterogeneity or time-varying treatment effects.4 To alleviate such concerns, I complement the staggered differences-in-differences strategy with within-state variation in treatment intensity. Firm-specific variation in treatment intensity arises from the fact that firms that produced VAT-exempt goods prior to VAT adoption are less intensely treated than firms that produced goods subject to VAT. This specification relies on the assumption of common trends between firms producing VAT goods and firms producing VAT-exempt goods. The results indicate that VAT adoption increased vertical integration in firms, as reflected by the average upstreamness of firm inputs. The average upstreamness of inputs increased by 0.35 production steps after state VAT adoption in firms that produced VAT goods, compared with firms that

3Several authors, including Goodman-Bacon (2018); Athey and Imbens (2018); and de Chaisemartin and D’Haultfoeuille (2019), have recently pointed out that in the presence of heterogeneous and time-varying treatment effects, a staggered differences-in-differences design yields a weighted average of treatment effects across all groups and periods, where some weights could be negative. 4In fact, the event study of the state VAT adoption on vertical integration shows strong dynamic effects. More- over, unregistered manufacturing share is a predictor of adoption delay, though it is not obvious whether unregistered manufacturing share is a determinant of vertical integration trends.

37 produced VAT-exempt goods prior to the reform. Evidence on mergers and acquisitions supports the hypothesis. While the log number of horizontal mergers remains unchanged during this period, the state-level log number of vertical mergers increased by 2% after VAT adoption. Because firms have incentives to integrate under sales tax due to double taxation on inputs, the estimates in this paper can be interpreted as a lower bound of the actual treatment effect of the VAT adoption. Next, I explore the channels that explain the finding. In particular, I test whether tax evasion causes firms to vertically integrate under VAT. A testable empirical implication for the presence of this channel is that a substantial part of the effect is driven by firms closer to the final demand. Figure 2.13 illustrates this. The figure plots the treatment effect as a function of distance to the final demand at the baseline. Firms that are at 0 distance to the final demand in the sample exhibit the largest increase in input upstreamness, consistent with the tax-evasion hypothesis. However, other potential channels could explain the increase in vertical integration in the middle of the chain. As we see in Figure 2.13, firms that belong to the 2nd to 10th ventile also experience a small and significant increase in input upstreamness after VAT adoption. An alternative mechanism is that VAT imposes a tax burden and creates incentives to integrate in the middle of the chain. This arises from the fact that firms are required to make monthly/quarterly tax payments on purchased inputs. When inputs are purchased before the realization of sales and tax refunds are slow or nonexistent, VAT can impose a significant tax burden on credit-constrained firms. The second alternative mechanism relates to compliance costs. Filing costs increase or decrease under VAT, depending on the size of the firm and its position in the value chain. If filing costs increase, larger firms benefit from economies of scale under VAT. The third alternative mechanism relates to the possibility that a lower tax rate under VAT increases the net-of-tax price received by firms. Research has shown that a higher output price increases vertical integration in firms (Alfaro et al. (2016)). However, the empirical results do not lend support to the liquidity constraints, compliance costs, or the tax-rate decrease hypotheses. In particular, the effect size of VAT adoption does not depend on the magnitude of financial constraints faced by the firm, as measured by its industry-

38 level cash flow sensitivity estimate (Almeida et al. (2004)). This is at odds with the prediction of the liquidity constraint hypothesis which states that effects are larger for firms with higher liquidity constraints. Additionally, in contrast to the compliance costs hypothesis prediction, which states that the effect is larger for smaller firms, I find that the estimated treatment effect is not correlated with firm size in any meaningful way, where firm size is measured by the number of employees. Finally, though VAT adoption lowered the consumption tax rate by 0.06 percentage points, I find that the vertical integration effect does not differ by whether the tax rate on a firm’s major output increased or decreased as a consequence of the tax reform. A concern with my estimates is that they only capture the reporting responses of firms and exclude the real responses. This has been pointed out in recent work in public economics that uses tax returns data, where it is hard to separate actual responses from misreporting. However, because I use firms’ survey data, it is less likely that they misreport input and output mix. This dataset is collected by the Ministry of Statistics to measure industrial statistics and is separate from tax returns. The identity of firms is confidential and not accessible to tax authorities. Therefore, we can expect that the measured reponses in this paper are real responses and not purely reporting responses. Taken together, the results point to tax evasion as one of the channels that leads to greater vertical integration in firms after VAT adoption. Being at the retail end provides an advantage, because it allows firms to underreport sales and reduce tax liability. In contrast, an integrated firm in the middle of the production chain is subject to cross-reporting on both its inputs and outputs, and therefore has no incentive to integrate to evade. The findings in my paper have important implications for tax policy design in developing countries. First, the results show that firms adjust their production processes in response to evasion, which is a new result in the literature. This implies that lower revenue collection in low-compliance settings is possibly a combination of both actual tax evasion and firm production responses. Sec- ond, integration for evasion imposes a revenue-production efficiency trade-off for the tax authority. Using VAT adoption as an instrument for vertical integration, I show that on average, an integrated

39 firm has higher profits per worker but remits lower taxes, compared with a less integrated firm.5 This introduces a trade-off between tax enforcement and firm profits. Revenue-production efficiency has implications for the optimal tax literature. A canonical result in the optimal tax theory is that an optimal tax must maintain production efficiency (Diamond and Mirrlees (1971)). With perfect enforcement, VAT maintains production efficiency. However, in the presence of integration responses to evasion, a privately optimal firm is larger than a so- cially optimal firm. A revenue-maximizing tax rate under VAT that disregards firms’ incentives to integrate raises lower revenues than one that takes them into account. Therefore, the optimal tax deviates from production efficiency, as has been argued by some authors (Emran and Stiglitz (2005); Kopczuk and Slemrod (2006); Gordon and Li (2009)). Characterization of the optimal tax in the presence of integration for evasion is a potentially interesting avenue for future research. The first contribution of my paper lies in organizational economics. Beginning with Coase (1937), economists have proposed several factors that determine the boundary of a firm.6 Empirical evidence suggests that market competition (Aghion et al. (2006)); tariffs/output price (Alfaro et al. (2016)); and corporate tax avoidance (Auerbach and Reishus (1987)) affect firm boundaries. More recently, Oberfield and Boehm (2019) use the same manufacturing data and a vertical distance measure to show that weak enforcement of contracts incentivizes firms to integrate vertically. I show that tax considerations and tax evasion, in particular, have consequences for a firm boundary as well. This also provides a simple methodological approach to estimate vertical integration by using an upstream measure, which can be useful for studying the effect of value-added taxes along the supply chain when confidential tax returns are not available. Finally, the paper is also aligned with papers that estimate the effect of investor-level taxes on acquisitions and headquarters (Ohrn and Seegert (2019); Huizinga et al. (2012)). The paper’s second contribution lies in the field of public finance. A burgeoning literature

5Integration significantly increases a firm’s value added, defined as the difference between gross sale value and material costs. 6For instance, Coase (1937), p7 notes that, “if we consider the operation of a sales tax, it is clear that it is a tax on market transactions and not on the same transactions organized within the firm...To the extent that firms already exist, such a measure as a sales tax would merely tend to make them larger than they would otherwise be."

40 in public finance argues that in addition to the tax rates, the tax system—such as an institutional setting—plays a key role in determining the tax capacity (Slemrod and Yitzhaki (2002); Gordon and Li (2009)). Recent empirical evidence has demonstrated the revenue implications of tax evasion. The ability to evade taxes implies that cross-reporting of transactions (Pomeranz (2015)); withholding (Brockmeyer and Hernandez (2018)); and the choice of tax instrument (Best et al. (2015) play a key role in determining revenues. This paper shows that tax evasion not only affects revenues but also the real operations of firms. In addition, a growing literature has demonstrated the real effects of a tax structure specific to VAT. For instance, Gadenne et al. (2019) show that size-based exemptions under VAT distort supply chains, whereby exempt firms are more likely to transact with similarly exempt firms. Likewise, Carloni et al. (2019) use VAT changes in the European Union to show that consumer prices respond more to increases than to decreases under VAT. Recent work has also shown variation in tax enforcement along the supply chain has consequences for informality (De Paula and Scheinkman (2010)) and tax incidence (Kopczuk et al. (2016)). The paper is organized as follows. Section 2.1 discusses the tax reform in India. Section 2.2 describes the data and construction of the upstream index. Section 2.3 performs the empirical estimation. Section 2.4 explores the mechanisms that could explain vertical integration effects. Section 2.5 discusses the implications of the results for firms, consumers, the government, and Section 2.6 concludes.

2.1 The VAT tax Reform, 2004-09

Prior to 2017, each state in India imposed and collected its own sales tax. Sales tax accounted for almost two-thirds of a state’s own revenues and one-third of domestic trade taxes in the country. This system of sales tax was reformed between 2003 and 2009 through the adoption of state-level VAT. Pre-reform period: Prior to the implementation of VAT, all states used a single point sales tax system that was highly complex, with many rates, a plethora of explanations, multiple rates for

41 some group of items, extensive use of statutory forms, high and unrealistic quotas for assessment, loss of revenue on value additions, and “tax rate wars” between states (Finance (2005)). The single point of taxation, while fixed, varied by states. Though the subsequent dealer could deduct the sales tax if it had been paid by a previous dealer earlier in the chain, these rules varied by states, leading to substantial cascading and double taxation. The tax reform process: At the conference of State Finance Ministers on January 23, 2002, it was agreed that all 28 states would implement VAT with effect from April 1, 2003. It was also decided that all states would be fully compensated for any revenue loss in the first year, 75% of the loss in the second year, and 50% in the third year to dispel any concerns regarding revenue loss. Nevertheless, only one state, Haryana, implemented VAT on that date. Figure 2.2 illustrates the timeline of state VAT adoption. Sixty percent of the states had adopted VAT by 2006 and the adoption was complete by 2009. Figure 2.3 shows that the majority of smaller states adopted earlier and larger states adopted in different years later on. This delay in implementation was mainly for political and administrative reasons. Nationwide adoption of VAT was a federal government initiative and required cooperation of all states. The opposition party in the center ruled some states, and in those states cooperation was particularly difficult to achieve. This period also coincided with elections in some states. For instance, as the Chairman of the Empowered Committee of State Finance Ministers on VAT noted, “The Delhi Government is apparently citing elections to its State Assembly in November for not implementing VAT immediately. And since Delhi is not implementing VAT now, the neighbouring States are also hesitating." The federal government negotiated with each state individually and the media reported substantial apprehension among traders during this time with respect to the adoption of VAT. 7 Features of the new tax reform: Under the new system8, the tax units (firms registered to pay VAT) remitted taxes according to a tax credit or invoice method in which firms could deduct the

7For instance, one of the dailies reported on February 2, 2005: "So will VAT come into effect on schedule or will it be another ’April Fool’s’ joke? This is the apprehension among many businessmen across the country." 8See Finance (2005) for complete details of the tax reform. Also note that in July 2017, the state-wide VAT system was replaced by the nationwide Goods and Services Tax (GST).

42 tax paid on inputs from the tax paid on outputs to determine the final tax liability. The input tax credit was given to manufacturers and traders for the purchase of inputs/supplies from within the state, and applied to the sale of final output either within or outside the state, irrespective of when the output would be used/sold. However, the tax paid on inputs purchased from other states was not eligible for the tax credit.9 If the tax credit exceeded the monthly tax liability, the excess credit was carried over to the end of the next financial year. Any excess unadjusted input tax credit at the end of the second year was eligible for a refund. Unlike the pre-VAT period, capital goods used as inputs (with the exemption of goods on the "negative" list) were eligible for an input tax credit that could be adjusted over a maximum of 36 equal monthly installments. Exports and sales made to special economic zones were zero-rated, and tax paid on them was subject to a full refund in 3 months. Dealers were required to file returns either monthly or quarterly, depending on their turnover. In addition, small dealers with gross annual turnover below a certain threshold were exempt from VAT registration. Once annual turnover crossed the threshold, dealers were required to register and pay VAT going forward. This threshold varied by state and changed over time. All registered dealers were required by law to issue serially numbered tax invoices, cash memos or bill of sales. The tax reform reduced the multiplicity of tax rates. though the state-specific variation in tax- rates remained, all states broadly had two VAT rates of 4% and 12.5% that covered about 550 goods and served as the floor tax rates. The 4% VAT rate applied to the largest number of goods (about 270), was common to all states, and consisted of basic necessities such as medicine and drugs, agricultural and industrial inputs, and capital goods. The remaining commodities fell under the general VAT rate of 12.5%. There was also a special VAT rate of 1% for gold and silver ornaments. In addition, each state exempted about 46 commodities from taxation. This included natural and unprocessed products in unorganized sectors, items legally barred from taxation, and items with social implications. States could choose 10 of such commodities of local social importance (from

9All interstate sales were subject to a central sales tax (CST). CST revenue accrued to the state in which the sale originated. CST, as an origin-based tax was inconsistent with VAT, which was a destination-based tax; hence it was slowly phased out. At the time of implementation of VAT, CST stood at 4%, which was reduced to 3% in 2007 and then to 2% in 2008. See http://dor.gov.in/centralintro for further details.

43 a list of goods common to all states) without any interstate implications. The rest of the tax-exempt commodities remained common to all states. Replacement of retail sales tax with value-added tax: As long as the tax reform did not vary other aspects, such as tax rates, systematically along the production chain, the replacement of VAT by RST provides exogeneous variation in incentives for firms to integrate at the final stage. To see this clearly, consider Figure 2.5 which illustrates how the production chain is affected when firms integrate to evade tax after the replacement of RST by VAT. Panel (a) shows revenue collected under RST, where the entire tax is remitted by the last firm in the production chain, F3. In contrast to RST, under VAT in panel (b), all firms remit tax equal to the tax rate times their net value added. Total revenues collected in both tax systems are equal when the tax rates are equal and there is no evasion. Panel (d) illustrates how second-to-last firm F3 gains by integrating with the last firm, F4, to evade tax in the VAT system. Integrated firm F3 underreports sales to consumers which lowers the effective tax remitted by F3 to the tax authorities.

2.2 Data and measurement of vertical integration

This section discusses my approach to measuring vertical integration in ﬁrms and the dataset used to estimate the effects of VAT adoption.

2.2.1 Data

The main dataset comes from the Annual Survey of Industries (ASI), which is conducted by the Ministry of Planning and Statistics (MOSPI) every year. The ASI is a repeated cross-section survey representative of formal establishments (stratiﬁed at the state level by 4 digit industry) The cross-section is designed as follows: Large establishments with 200 or more workers are surveyed yearly until 2003-2004, and ﬁrms with 100 or more workers are surveyed each year after 2004 (with about 10% nonreporting each year). Smaller establishments are surveyed with a probability that depends on the state and industry block, with a minimum sampling probability of 15%. The MOSPI has recently allowed researchers to track establishments that were sampled multiple times.

44 I have access to ASI “panels" for years 1999 to 2010. I use the cleaning code and methodolgy of Allcott et al. (2016). I remove establishments with invalid identification codes and that are reported closed/nonresponsive in a given year. This leaves around 37,000 establishments in a year. The survey covers the period from April of one year to March of the next year, which coincides with the fiscal calendar in India. This works to my advantage, because tax reforms in India are largely implemented at the start of the fiscal year, that is, April of a year. The unit of analysis in the sample is an establishment. There is no information on parent firm for multi-unit firms. However, approximately 95% of firms are single unit and file a single return. This implies that the terms “establishment” and “firm” can be used interchangeably. I interpret the findings in this paper as the responses of a firm. The survey requires firm owners to provide information on the status and number of units, labor cost and employment, fixed assets, quantity and type of inputs employed, type, and quantity of 10 major outputs produced. Inputs and outputs are classified at the 5-digit industry level according to the Annual Survey of Industries Commodity Classification (ASICC) code. For outputs, the information provided includes quantity, gross sale value, ex-factory value, sales tax, and excise tax paid. There are several advantages of using the ASI dataset. First, it contains extensive information on firms’ inputs and output decisions, which allows me to identify a firm’s position in the value chain based on its inputs and outputs. Second, because the survey maintains the confidentiality of firms, information reported by firm owners is not accessible to tax authorities; thus there is no incentive for firm owners to misreport information in the survey for tax purposes. Third, the survey is nationally representative, which allows me to assume that the input-output linkages observed in the survey are representative of nationwide linkages. Table 2.1 describes the key firm variables in the ASI data. An average firm employs approximately 139 workers, produces 3 outputs, and uses 11 inputs. There are a few oddities in the data. For instance, some firms report up to 98 inputs, and many firms report 0 outputs and 0 workers. These could reflect reporting errors.

45 Summary statistics reveal that an average firm in the sample uses inputs with an upstream index of 4. This implies that the average inputs used by a firm are approximately 4 production steps away from final consumption in the input-output network generated in the sample. Because the data do not provide information on firm position characteristics, it is not possible to determine whether an observed firm is a manufacturer, wholesaler, or retailer. Nevertheless, rows 2 and 3 of Table 2.1 report the probability that a randomly selected firm in the sample uses inputs with upstreamness less than the median. The median upstream value in the complete product space is 2 (see Figure 2.8). Approximately 10% of the firms in the sample use downstream inputs, which is consistent with the fact that the survey covers mostly manufacturing firms that are more likely to be upstream. Figure 2.24 plots the distribution of the number of firms by 1-digit industry classification (NIC). A large share of the firms belong to mining, quarrying, and basic manufacturing industries. The latter includes the manufacture of metals, paper products, electronics, and fabricated metals. Un- fortunately, wholesale trade and retail industries are poorly represented in the data. Nevertheless, the manufacturing firms’ data are informative, because many firms in the sample produce goods such as TV, radio, and motor vehicles, which are important from a final consumption point of view. In addition, I supplement the above data with information on state-wise VAT adoption date, state-product tax rates, and a list of state-specific tax-exempt goods from state tax laws and reports. The dataset on tax rates is useful for alleviating the concern that the vertical integration effect partially reflects a response to higher net-of-tax prices in the VAT regime. This is because the tax reform effectively lowered the average commodity tax rate (Figure 2.9). Tax rates were collected for each product in the sample for 17 states for both the sales tax and VAT regimes. A research assistant read the state tax laws and assigned relevant tax rates to each product in each state in the two tax regimes. The final sample excludes the northeastern states and the state of Jammu and Kashmir, because of their underrepresention in the ASI data. Finally, I supplement with the PROWESS dataset (2001-2010), which contains information on publicly listed and some private firms. It is compiled using information sourced through the annual and/or quarterly financial statements of approximately 27,000 active business entities. Though not

46 nationally representative, PROWESS data also includes non-manufacturing, financial, and retail firms. More importantly, it contains information on mergers and acquisitions carried out by firms in the sample during this period. This dataset is useful for providing more direct evidence of the effect of VAT on vertical integration.

2.2.2 Measurement of vertical integration

It is generally difficult to directly identify vertically integrated firms in terms of ownership and commodity flows. Previous authors (Acemoglu et al. (2010); Fan and Lang (2000); and Alfaro et al. (2016)) have used indirect measures that use national input-output tables. These measures, however, are fairly broad and identify only a subset of integrated firms. I improve on these method- ologies by proceeding in two steps: (i) I classify goods according to their position in the production chain using a measure of upstreamness and (ii) I determine the implications of greater vertical integration on upstream measures of inputs and outputs and test them in the data. The idea is that a more vertically integrated firm uses inputs that are relatively more upstream, or higher up in the production chain. Recent work in trade has classified goods by their position or “upstreameness" in the production chain (Fally (2011); Antras et al. (2012)). A product that is mainly used as an input for the production of other goods is given a higher score for upstreamness than a product that is sold directly to consumers. In addition, a product used by firms that are more upstream themselves is more likely to be upstream. To illustrate, consider the production chain that consists of three firms in Figure 2.6. F1 supplies to F2, which supplies inputs to retail firm F3, which in turn sells the final output to the consumer. Given the network of firms, products P2 and P3 are more upstream than P1 because they are used in the production of P1. Now suppose that the last two firms integrate by merging, and firm F2 disappears as a result.10 The integrated firm uses P2 as inputs. If we fix the upstreamness of the products at pre-integration levels (as in the top figure), then the average inputs’ upstreamness is higher in the integrated network than the unintegrated network. In addition, if there are no other

10Or they enter into a contract instead of going through an actual merger.

47 accompanying changes in production processes in the integated firm, outputs on average are more downstream in the network with integrated firms. Another intuitive measure of vertical integration is the vertical distance between firms’ inputs and outputs. Vertical distance refers to the number of steps in the production process that are performed within the firm. A more integrated firm performs more steps within the firm, which implies that greater vertical integration is associated with larger vertical distance. An interpretation is that when outputs become more downstream and inputs become more upstream, the vertical distance of a firm increases. Figure 2.7 plots the average vertical distance of firms in the sample in the pre-reform period 2000. A firm had a vertical distance of approximately 1 in 2001. This implies that an average firm in the pre-reform period performed one prodution step in-house.11 The testable hypothesis is: Hypothesis: The replacement of sales tax with VAT increases incentives for a firm closer to the final demand to produce in-house instead of buying it from outside. This is reflected in an increase in its input upstreamness and a decrease in its output upstreamness. Consequently, the vertical distance between its inputs and outputs increases.

The next task is to accurately measure products’ upstreamnes. For this purpose, I draw on a measure from the trade literature.

Measurement of upstreamness

This section provides details on the construction of Fally (2011)’s upstreamness index using an input-output table. Fally (2011) proposes a measure based on the notion that ﬁrms that sell a disproportionate share of their output to relatively upstream ﬁrms should be relatively upstream themselves. Similarly, a product that is largely used in the production of more upstream products is more upstream.

11Recently, Oberﬁeld and Boehm (2019) use a somewhat similar measure of vertical distance and the same data to show that weak contract enforcement distorts production organization in India.

48 N Õ aijYj U = 1 + U 2i Y 2j j=1 i

where ai j refers to the quantity of good i used in the production of good j and Yj denotes the total quantity of good j produced in the economy. Formally, the above can be written as:

−1 U2 = [I − ∆] 1,

where ∆ is the matrix with ai jYj/Yi in entry (i, j) and 1 is a column-vector of ones. ∆ matrix is the productXindustry "Use matrix" provided as part of the Input-Output (IO) tables for a country. The (i, j)th element of this matrix denotes the amount of product i used in the production of product j. India has IO tables at the 3-digit industry level for the year 2003-04. Product classiﬁcation in the ASI data is ﬁner, at the 5-digit level. In addition, there is no clear concordance between IO tables and industry codes in the ASI data. Therefore, I construct the Use matrix from the ASI data for the year 1999-2000, which allows me to use the trading networks of

ﬁrms 4 years before the reform. I next discuss the construction of U2 from the ASI data.

Constructing the Use Matrix from 1999-2000 survey data

For each firm, define the industry to which the firm belongs according to the major product. The major product is one that has a maximum ex-factory value (MOPSI 2013) where12

E xFactoryValue = PerUnitSaleValue × QuantityManu f actured.

For each industry in the data, I calculate the amount of each input used and the total output produced. This is obtained by collapsing ﬁrm-level input-output data to productXindustry level using ASI sampling weights. The use of weights allows me to obtain a nationally representative

Use Matrix. Each element of this matrix is aijYj, that is, the amount of good i used in the production

12I remove ‘unclassiﬁed’ inputs/outputs of the ﬁrm.

49 of good j. From the Use Matrix, I calculate the total absorption of a product across all industries

(Yi). Absorption Yi refers to the total use of product i within the network economy. This includes

all manufacturing ﬁrms in the sample. Yi provides the denominator for each row in ∆. Once ∆ is obtained, U2 can be calculated using the formula

−1 U2 = [I − ∆] 1.

An issue that arises is that the [I − ∆]−1 matrix is not invertible. This happens because of the presence of some goods that are not used across industries, but instead are used within the industry to which they belong. To solve this problem, I use a pseudo inverse. As a robustness check, I also perform Tikhonov regularization to the matrix.13 This procedure assigns upstream measure to each product observed in year 2000, which leads to 3,210 such products.

Making sense of the Upstream measure

Figure 2.8 shows the distribution of products’ upstream indices. The mean product upstreamness is 3.23 and the median is 2.06. Most of the products have upstream values between -5 and 10. Some products have negative upstream values, with the lowest value corresponding to -13. These negative values arise because some rows in the [I − ∆] matrix are zero-valued for cells, except for the diagonal. For instance, knitted garments are largely absorbed within the knitted-garments industry. This is a limitation of the data that do not contain the complete input-output network. In particular, ﬁnal consumption and other wholesale and retail activities are missing from this data. In the absence of full network data and a detailed industry/product classiﬁcation, the upstreamness of such products will be less precisely estimated. To partly alleviate this concern, I perform a ro-

13 −1 I also use Tikhonov regularization as a robustness check: For a given h, this method approximates A with Ch such that lim Ch A = I. h→0

The appropriate Ch is determined such that the norm of (Axˆ − y) is the smallest. When A is rank deﬁcient or ill- conditioned, this gives: 0 2 −1 0 Ch = (A A + h I) A . I implement this for h = 10−3. Section 2.3.4 reports robustness to alternative methods of matrix inversion.

50 bustness check in which I drop products that take negative values from the analysis and the results go through.14 Table 2.16 lists products with the lowest (negative) and highest upstream values. Eyeballing suggests that negative upstream indices correspond to consumer-oriented products, and the highest indices correspond to basic products such as coir ﬁbre, energy products such as LPG, and water for industrial use. Table 2.9 shows how product indices are distributed for four main industries in India. For instance, raw cotton has a higher upstream index than bleached and processed cotton, knitted cloth is much further downstream. Similarly, iron ore is quite upstream, with a value of

4.85. Iron sheets and plates are downstream, with a value of 2.74. Overall, U2 seems to capture the position in the production chain fairly well.

2.3 Empirical strategy and results

Having proposed a measure of vertical integration, this section uses the staggered adoption of VAT to estimate the effect of state VAT adoption on vertical integration in ﬁrms. Firms that produced VAT-exempt goods are less intensely treated by the reform, and serve as a control group in the main speciﬁcation.

2.3.1 Main speciﬁcation: VAT and Non-VAT-good Producers

Identification of the treatment effect requires that vertical integration evolve similarly for early adopters of VAT and later adopters of VAT. The parallel-trends assumption would not hold if, for instance, the delay in implementation were correlated with the state-specific, time-varying characteristics. Table 2.8 tests for the presence of correlation between state-specifc delay in implementation and state growth variables in the pre-reform period. The data come from NITI Ayog’s GDP reports. We see that while the state’s delay is not correlated with its GDP growth rate, manufacturing growth rate, or agricultural growth rate, there is a significant correlation with its unregistered manufacturing growth rate. This is a concern if we assume that trends in unregistered manufac-

14Results using Speciﬁcation 2.1 are reported in Table 2.15.

51 turing could affect vertical integration in the registered manufacturing sector. Also, a specification that uses only the timing variation in state VAT adoption must also satisfy homegeneity and a time-invariant treatment effect for the estimate to offer a causal intepretation (de Chaisemartin and D’Haultfoeuille (2019); Goodman-Bacon (2018)). Therefore, this section reports results for Specification 2.3, which employs variation in treatment intensity within a state: producers of both non-tax-exempt goods and tax-exempt goods, as well as the variation in VAT adoption. As discussed in Section 2.1, a feature of the VAT reform was that each state proposed a list of goods that were to be exempt from VAT within that state. Typical products include agricultural implements; common items such as salt, vegetables, books, and periodicals; and feed for animals and poultry. Relative politcial importance often explained why a product was exempt from VAT in one state and not in another. Some of these products were also tax exempt in the sales tax regime. Frms that produced tax-exempt goods in the pre-reform period act as a control group, because for the manufacturers of these goods, both input and output tax liability are unchanged with the tax reform. Producers of VAT-exempt goods were not eligibile for input-tax credit because their output was not subject to VAT. Moreover, these firms were not required to collect tax or file VAT tax returns. Therefore, we expect the tax burden and compliance costs to be unaffected by the VAT reform for these firms.15 There is another interesting source of variation that I do not exploit due to data limitations. This variation comes from the fact that some firms purchased inputs from within the state while others purchased from outside the state. Recall that under VAT, the tax paid on inputs purchased from firms located outside the state is not subject to tax credit, whereas tax paid on inputs purchased from within the state is subject to VAT. While this is an interesting source of variation, I am not able to use this variation because the source of inputs is not reported in the ASI data. Consequently, my empirical strategy essentially uses within-state variation in treatment intensity based on pre-VAT

15Note that this does not account for any general equilibrium changes that might result from the reform. For instance, these firms might see their profits decline if the average demand for their product decreases due to high price levels in general, resulting from other firms integrating along the chain. This could in turn lead to more integration within control firms. Therefore, we expect the estimated effect in this specification to be a lower bound of the actual treatment effect.

52 output produced by firms. I identify the list of products that were tax-exempt under the VAT law and hand-code their names to products in the ASI data. I identified 172 such VAT-exempt products, which were produced by roughly 1,010 out of 29,920 firms in the 2002 sample. I assign such VAT-exempt firms to the control group and estimate the following specification:

2002 2002 yist = β0 + γt + γs + β1adoptst + β2NonTaxExempti + β3NonTaxExempti × adoptst + ist (2.1) A firm is non-tax-exempt if it did not produce a VAT-exempt product in 2002 (the year before the first state adopted VAT.) The identifying assumption here is that in the absence of the VAT, vertical integration for VAT good producers would evolve over time in ways similar to the vertical integration in firms that produced a VAT-exempt good. All regressions are weighted by the inverse of sampling weights provided in the dataset to account for heterogeneity because of endogenous sampling (Solon, Haider, and Wooldridge (2013)). For greater precision, I focus on the period 2003-2010, when VAT had begun to be implemented. In other variants of the specification, I add industry, firm fixed effects, and state-specific linear time trends. I cluster standard errors at the state level to account for possible serial correlation (Bertrand et al. (2004)). Table 2.2 reports the estimated coefficient of interaction of a non-tax-exempt firm in 2002 and the adoption dummy, β3. I find that the coefficient is significant in all specifications. The effect is largest in the specification that includes only state and year fixed effects (0.584), compared with the regression with firm fixed effects (0.35). The treatment effect in (1) consists of both within-firm effect and a compositional change in the sample due to firm exits, whereas (6) includes only the within-firm effect. In addition, the magnitude and significance of coefficient are unaffected by the inclusion of industry-fixed effects. To explore the dynamic effects of VAT adoption, I also plot the coefficients from the event study version of Specification 2.1, which includes firm fixed effects.

53 The full speciﬁcation is as follows:

3 2002 Õ 2002 yist = β0 +γt +γi +NonTaxExempti + βtYears since Adoptiont ×NonTaxExempti +ist −3 (2.2) The dummy for a year before a state’s VAT adoption is omitted.16 Figure 2.10 presents the results. The bars indicate confidence intervals at 10% significance. We can see that while there are no significant pre-trends, firm input upstreamness increases significantly the first year VAT is adopted. The effect largely remains similar over the next 3 years. Table 2.3 presents tresults with the average upstreamness of firm outputs as the outcome variable. The coefficient of NonTaxExempt XAdopt is insignificant in all specifications. Moreover, the coefficient is of the opposite sign (positive) in the first four columns, which do not include firm fixed effects. Columns (5) and (6) present results with firm fixed effects. Here we see that the coefficient is of the expected negative sign, though largely insignificant. Figure 2.11 presents an event study version of this specification. We see that there is a slight insignificant drop in output upstreamness in the first 2 years after VAT adoption. One reason the output effect is insignificant is that vertical integration changes the composition of outputs. For example, efficiency gains due to integration might allow integrated firms to produce more upstream outputs. To see whether there is any compositional change, Table 2.11 presents results for second moments of output upstreamness. Column (1) presents the effect on the upstreamness rank of firm outputs; that is, the difference between the most upstream and the least upstream output. The coefficient is positive but insignificant. Columns (2) and (3) test for changes in the mean and median absolute deviation. Both coefficients are insignificant. Columns (4) and (5) show some evidence that a firm’s most downstream output is more downstream after the reform, however, it is insignificant even at the 10% significance level. The results here do not provide strong evidence in favor of observable changes in firm output composition, as measured by the second moments of output upstreamness.

16 2002 Note that the variable NonTaxExempti is not perfectly collinear with firm fixed effects. This is because several firms are not observed in 2002, and therefore cannot be categorized in either the treated or the control group.

54 2.3.2 Alternative speciﬁcations

Using staggered state VAT adoption

We can also use the staggered nature of state VAT adoption directly in a differences-in-differences framework to estimate the effects of VAT. This serves as a useful robustness check despite the obvious concerns. Speciﬁcally, I estimate the following speciﬁcation:

yist = β0 + β1 Adoptst + γs + γt + ist . (2.3)

Adoptst takes value 1 if VAT was adopted in state s in year t, and 0 otherwise. γs and γt

denote state and year ﬁxed effects, respectively. yist is the average upstreamness index for ﬁrm i’s inputs (or outputs) in state s and time t. The main identifying assumptions are that the actual date of implementation of VAT in a state is orthogonal to any endogenous trends in the outcome variable; treatment effects are homogeneous; and treatment effects do not vary over time. When

these assumptions hold true, β1 identifies the average treatment effect of the replacement of sales tax with VAT on firms’ inputs upstreamness. Table 2.4 reports the estimated Adopt coefficient when the outcome variable is the average inputs upstreamness for several specifications. The sample is restricted to 2003-2010. (1) is the least restrictive specification and controls for only time and state fixed effects. The coefficient is 0.2 and significant at 1%. This suggests that firms procurred inputs that are 0.2 production steps more upstream after VAT adoption. The significance remains strong when I add state-specific linear trends but the coefficient reduces to 0.176 (2). The coefficient remains unchanged when I add industry fixed effects, implying that most of the effect comes from within the industry. However, the addition of firm fixed effects reduces the coefficient’s size and renders it insignificant at the 10% confidence level. This is a concern as it suggests that after controlling for compositional changes due to firm entry and exit, the state’s VAT adoption did not have a significant effect on vertical integration for firms that remained in the sample. A possibilty is that the effect using state- VAT adoption is underpowered. Staggered VAT adoption relies only on the variation in the timing

55 of VAT adoption. In the case in which the treatment effects vary over time, this leads to smaller estimates when initial adopters—for whom the treatment effect is increasing with time—serve as a control for late adopters.17 State level evidence

We can aggregate firm-wise input-output data to state-level and perform an event analysis of VAT adoption on the aggregate upstreamness of inputs and outputs. This allows us to estimate state-wise aggregate changes. Panel a of Figure 2.12 presents the event analysis of the effect on average state upstream measures of inputs and outputs. We see that while the inputs became more upstream after the state’s VAT adoption, there is no change in the upstream measure of outputs, similar to the findings using the main specification. Panel b shows that the vertical distance between firms’ outputs and inputs increased. Figure 2.4 illustrates the event study with the state’s own revenues as the outcome variable. This allows us to test whether the states’ own tax collec- tions increased following the state’s VAT adoption. I obtain state-level yearly figures from NITI Ayog 2003-2010. The figure shows no significant effect on state log revenues following the VAT reform.18

Heterogeneous effects of the reform

A key dimension of heterogeneity is the industry to which a firm belongs. Figure 2.22 plots estimated treatment effects by 1-digit industry classification (NIC 2004). We see that point estimates are largest for firms in the "Business activity" industry (NIC 7). This includes firms engaged in real estate, research and development, and other business activities. The effect is also large for firms belonging to the manufacture of consumer-related products (NIC 1), such as textiles, food products and beverages, tobacco products, footwear, leather products, and firms related to mining. The effect on firms engaged in wholesale trade and transport is barely significant at 5%, which can partially be explained by their small sample size (see Figure 2.24). The results in this subsection

17This leads to “negative weights" (Goodman-Bacon (2018)), and interpretation of the estimate is not necessarily causal. 18Though it is not clear whether states’ reported revenue also include any compensation from the federal government in this period. The exact components of the states revenue are also not clearly stated.

56 add to the evidence that the effect is dominated by firms engaging in consumer-related products and services. Finally, Figure 2.21 presents the yearly distribution of the number of firms in the ASI data as a function of the distance to final demand, which is measured by the average upstreamness of a firm’s outputs in 2003. We see that from 2004 to 2009, there is a general decline in the number of firms sampled in the data. Moreover, this decline is much larger for firms closer to consumers, suggesting consolidation in production toward the end of the production chain.

2.3.3 Effect on mergers and acquisitions

An obvious concern in the above analysis is that input upstreamness may not accurately measure a firm’s position in the chain. That is, buying more upstream inputs does not directly imply greater vertical integration, especially when integration requires the transfer of ownership. There- fore, in this section I use the mergers and acquisitions data from PROWESS provided by Center for Monitoring Indian Economy (CMIE) to estimate the effect on state merger activity after VAT adoption. When integration occurs through the acquisition of suppliers, we should expect larger vertical mergers and acquisitions after the VAT reform. I obtain the M&A module from CMIE. A firm in the sample is represented by a unique CMIE company code. This does not change, even when a firm is acquired. An observation in this module is a merger/acquisition event. The information includes the date of the announcement, firm code of the “target" and “acquirer" firm, and their respective main products at the time of the merger/acquisition. For example, the data description states, “In 1997, Grasim Industries sold its 53.3 per cent stake in Shree Digvijay Cement Co. to Cimpor, a Portuguese cement company. Since Cimpor acquired the stake in Shree Digvijay, it will be termed as the acquirer for this deal. Shree Digvijay will be the target company.”19 To determine whether a given merger or acquisition is vertical or horizontal, I assign the target and the acquirer firm to a respective sector in India’s national Input-Output table 2003. CMIE defines the main product as that product or service from which the firm derives more than half of

19Fortunately for this paper, M&A information is available only for the years 2000-10, which spans the tax-reform period.

57 its revenue.20 I use the IO matrix to construct upstream indices for each sector using the same methodology as outlined in Section 2.2.2. I then assign an upstreamness measure to both the target and the acquirer. Finally, I code a merger or an acquisition between two firms as vertical if the difference between the upstream index of the acquirer and target firms is not equal to 0; otherwise it is coded as a horizontal merger. There are 7,687 vertical and 3,313 horizontal mergers and acquisitions during this time. I aggregate mergers to the state-year level. Figure 2.17 indicates that vertical mergers and acquisitions increased significantly after the reform. The figure plots the estimated coefficients from a regression of the logarithm of the number of mergers/acquisitions in a state on state and year fixed effects and a dummy indicating years since VAT adoption. All regressions are weighted by the number of companies in the state. In contrast, horizontal merger activity is unchanged during this time.21 Yearly mergers/acquisitions are higher by around 5% after VAT adoption.

2.3.4 Robustness checks

In this section, I perform several robustness checks. First, a concern is that a firm’s classification to an industry on the basis of its major product may not be an adequate description of the firm’s economic activity. This assumption was used in construction of the input-output table from the firm input-output data. Incorrect classification of a downstream product as upstream can potentially lead to underestimation, especially when the effect is heterogeneous with respect to the firm’s position in the production chain. Similarly, incorrect classification in the reverse direction could lead to overestimation. To alleviate these concerns, I estimate the specification similarly to 2.3, but restrict it to a sample of single-output firms. Table 2.10 shows that although total sample size reduces by half, the effect is halved and is still significant. Second, I perform a falsification check in which I move the treatment back to several periods before the reform. Figure 2.20 presents the estimated treatment effects for various perturbations. Reassuringly, I find that the estimated treat-

20The sectors in the IO table are at 3-digit level and are therefore broader than the 5-digit level of product classiﬁ- cation in ASI data. 21Because many state-year observations have zero number of mergers/acquisitions, I add one to the outcome variable.

58 ment effects are insignificant for several periods before the reform. Third, I test whether the results are largely driven by a single state. In particular, I perform "leave-one-out" regressions in which I estimate Specification 2.1 by iteratively dropping a state. Figure 2.19 illustrates the distribution of the estimated treatment effects. The treatment effect is close to the estimated effect in the full sample and is significant in all specifications. Finally, as Figure 2.8 shows, the upstream index has long tails which is a potential concern because the mean is susceptible to outliers. For this reason, I estimate the same specification but winsorize the distribution by 5% in either direction. Table 2.13 reports the results for the winsorized sample. The coefficient size is remarkably close to the estimated effect in the non-winsorized sample.

2.4 Exploring mechanisms

Having established that VAT adoption led to greater vertical integration among ﬁrms in India, in this section I explore ﬁve channels that could explain the effect. I show that the empirical evidence suggests that integration for evasion is the most plausible explanation.

2.4.1 Tax evasion at the retail stage

As illustrated in Figure 2.5, the cross-reporting of transactions made by firms makes evasion an unlikely prospect for upstream firms. The last firm, however, is not subject to the same level of cross-reporting, which allows it to underreport sales and reduce tax liability. Consequently, the second-to-last firm has an incentive to integrate with the last firm, F4. Integrated F3 reports sales of 40 against 50 and pays an effective tax rate lower than the statutory tax rate. A testable implication is that if tax evasion is a channel, a large share of the effect is concentrated in firms located closest to the retail stage. To identify retail firms, I use the fact that firms that produce more downstream products are closer to consumers. A firm’s position in the production chain is described by the average upstream measure of its outputs at the beginning of the reform

59 period. In particular, I estimate the following speciﬁcation:

n 2003 Õ k 2003 vist = β0 + β1adoptst + β2NonTaxExempti + β3 1(distance == k) × NonTaxExempti × adoptst 0 n Õ k + β4 1(distance == k) + γs + γt + ist 0 (2.4)

I create n quantiles and assign a firm to one of these quantiles on the basis of average output upstreamness in 2003. Firms with more upstream outputs in 2003 are less likely to be closer to final demand. Additionally, I include a dummy variable that takes value 1 for firms that have the lowest upstream measure, which includes the most retail firms in the sample. A large share of these firms produce knitted cotton garments, shirts, and dresses.

k In Figure 2.13, I plot the estimated coefficients β3 against quantiles k where n = 20 with a 95% confidence interval. It is interesting to note that the effect is largest for firms closest to consumers where the coefficient is around 2.5. Coefficients are smaller in magnitude but stable at 0.5 for firms in quantiles 1 to 15 and estimated coefficients are insignificant for firms in quantiles above 15. This is consistent with the hypothesis that firms closest to consumers are the most likely to gain from a tax-evasion point of view. This is reflected in the larger estimated coefficients for such firms.

2.4.2 Liquidity constraints under VAT

Another channel by which firms integrate under VAT is that VAT adoption worsens their credit position. This is because the VAT on the firms’ input purchases generates sudden tax liability for them. When the refunds are slow, VAT exacerbates the firm’s credit position. This is more relevant for small-sized firms and firms that make seasonal sales. A liquidity-constrained firm can then avoid immediate payment on its inputs by integrating with the supplier, because use of inputs produced in-house do not trigger tax liability. Consequently, if the liquidity constraints imposed by VAT are a mediating channel, VAT increases vertical integration among firms. To test the liquidity constraints hypothesis, I perform the same steps as above. I measure how

60 liquidity constrained a firm is by its industry’s cash flow sensitivity (Almeida et al. (2004)). The idea is that a firm’s propensity to save cash captures its financial (or liquidity) constraints. I construct the industry-level cash flow sensitivity estimate from firm input-output data in the following ways: I first restrict firm data (ASI) to the pre-reform period 2004. I aggregate firm-level opening and closing stocks of cash to its 3-digit NIC industry level. I then determine the industry-level correlation between the yearly cash growth and opening cash stock, by regressing industry-year cash growth on the full interaction of industry-opening cash stock and industry fixed effects. The coefficients of the interaction in this specification are the cash flow sensitivity estimate (CFSE) for an industry. Finally, I classify a firm as more liquidity constrained if it belonged to an industry with a higher CFSE in 2004. I plot the estimated effect of VAT on vertical integration interacted with the measure of liquidity in Figure 2.14. If liquidity constraints hypothesis is correct, we expect larger effects for firms that are more liquidity-constrained. In contrast, I find that the effect of VAT on vertical integration is relatively stable across firms with varying degrees of liquidity constraints. This suggests a lack of evidence in favor of liquidity constraints as a key channel leading to greater vertical integration among firms.

2.4.3 Higher Compliance Costs under VAT

In contrast to the sales tax remitted by only retail firms, all firms in the production chain are required to file and remit taxes under VAT. This can impose a significant compliance burden on firms, in the form of significant accounting and bookkeeping costs. These compliance costs have generally been studied as fixed costs in the public finance literature (Slemrod and Gillitzer 2014). If higher compliance costs is a channel, the compliance burden imposed by VAT is greater for smaller firms. One way small firms reduce their burden is by integrating and increasing their size. To test the compliance costs hypothesis, I plot the estimated effect of VAT on vertical integration interacted with the firm size quantile in Figure 2.15. I measure firm size by the number of its employees in 2003 (i.e., pre-reform period). If the compliance costs hypothesis is correct, we ex-

61 pect larger effects for smaller firms. In contrast, I find that the effect of VAT on vertical integration is relatively stable across the distribution of firm size. This points to a lack of evidence in favor of compliance costs as a key channel leading to greater vertical integration among firms. Finally, Table 2.17 tests for correlation in the three measures used to test the mechanisms. The table highlights weak correlation among the measures, which suggests that they act independently on the outcome.

2.4.4 Lower tax rates in the VAT regime

An unignorable feature of the tax reform is the reduction in product tax rates. This is a concern, because previous literature has shown that firms are more likely to integrate when output prices are higher (Alfaro et al. (2016)). A consequence of a lower tax rate is a higher net-of-tax output price for firms. The left panel of Figure 2.9 plots the distribution of tax-rate changes at the 5- digit industry level across 17 states. A point in the sample is a product-year. We see that the net effect of the reform was a decline in the tax rate by about 0.06 percentage points. The right panel illustrates the average state tax rate change for late adopters versus early adopters. There is a weak correlation between late adopters and the decline in the average tax rate. This is worrisome, because it suggests that part of the vertical integration response could be driven by firm responses to changes in net-of-tax output prices. To alleviate this concern, I estimate the heterogeneity of the VAT effect by the sign of the product tax-rate change. In principle, if firms are responding to lower tax rates under VAT by vertically integrating, we expect larger effects for firms that face a tax-rate decrease, compared with firms that face a tax-rate increase. A firm is identified as facing an output tax-rate decrease if the tax rate on its major output in 2003 declined as part of the reform. Table 2.5 presents the results. The first column reports the main results using Specification 2.1—total effect of VAT adoption on vertical integration, as measured by average input upstreamness. Notice that the sample size is much smaller: 88,886, as opposed to 243,566 in the main Table 2.2. This is because this sample is restricted to firms that (i) are observed in 2003, and (ii) belong to

62 states with available tax-rate information. The latter restricts the data to 17 states. The regression includes firm and year fixed effects. This means that the results in this column are comparable to Column (5) of Table 2.2. Reassuringly, we find that the point estimate is unchanged despite a smaller sample size. Interestingly, column (2) shows that we cannot reject significant difference in the treatment effect based on whether the firm witnessed an increase or decrease in output tax rate. This increases confidence in the result whereby tax evasion is the main channel that leads to greater vertical integration under VAT.

2.4.5 Higher tax rate on upstream ﬁrms

Even if higher output tax rates did not lead to vertical integration among firms, it is still possible that changes in the statutory tax rates were not neutral along product position in the value chain. This can lead to greater vertical integration, independent of tax evasion. For instance, it is possible that the reform increased the tax rate on more upstream goods even if it decreased the tax rate overall. This is important because, a tax system that leads to a higher tax rate on products that are more upstream can lead to greater vertical integration even when firms are not evading. Such a tax system penalizes production that is performed out-house on the market. By bringing production in-house, firms save on the higher tax rate subject to transactions on the market and pay the lower tax downstream tax rate. I plot changes in statutory tax rates against product position in the value chain. I continue to measure a product’s position by the upstream measure. Figure 2.16 shows the relationship. We see that the tax rates’ decrease was much larger for upstream products than downstream products. This suggests that if anything, the reform lowered the tax rates on upstream products, which suggests that it is less likely that firms integrated to avoid higher taxes on upstream products.

2.5 Discussion

The previous subsection showed that tax evasion is a plausible channel by which the replacement of sales tax with VAT leads to greater vertical integration. However, it leaves the following

63 question unanswered: How does vertical integration largely affect firms and revenues? This is pertinent from an optimal tax policy point of view. Therefore, this section uses the changes in vertical integration brought by the tax reform to estimate the effect on firm outcomes. The state-VAT adoption dummy and a dummy that indicates whether the firm produced VAT-exempt good serve as instruments. I estimate the following specification on a host of firm outcomes:

yist = α0 + α1VIist + α2StatRateˆ ist + α3FirmPositionist + γi + γt + eist, (2.5)

where VIist represents the extent of vertical integration of firm i in year t. I proxy this variable with the average upstreamness of inputs of firm i in year t. This implies that for two firms at a similar distance from the final demand, the firm using more upstream inputs is considered to be more vertically integrated. Firm position, as measured by its distance from the final demand, and the statutory tax rate on outputs faced by the firm serve as included instruments. Because the actual statutory tax rate faced by a firm depends on its output mix, which is endogenous to the tax change, I instead calculate the "predicted" tax rate defined as follows:

Í 2003 k∈(1,K) Y Ratet StatRateˆ = ik , ist Í 2003 k∈(1,K) Yik

where k ∈ (1, K) represents the K outputs of the firm and Yik represents the tax-exclusive value of output k produced by firm i. StatRateˆ ist calculates the effective tax rate faced by the firm. This is an average of tax liability across multiple outputs of a firm, weighed by the pre-reform value of corresponding output (Gruber and Saez (2002)). Weighting is useful, because the effective tax burden faced by a multi-product firm depends on both the statutory tax rate and its share in the total output. A relatively low-tax output that forms a greater share of a firm’s total output imposes a much larger tax burden on the firm than a very high tax output that forms a neglibible share. Clearly, vertical integration is determined by a host of factors, such as firm productivity, expec- tations, and credit position, not all of which can be accounted for. Therefore, I instrument the VIist variable with the VAT tax reform: In particular, the regression in Specification 2.1 forms the first

64 stage, with the addition of the variables StatRateˆ ist and FirmPositionist.

2003 2003 VIist = β0 + β1adoptst + β2NonTaxExempti + β3NonTaxExempti × adoptst (2.6) +β4StatRateˆ ist + β5FirmPositionist + γi + γt + ist

Addition of the statutory tax rate variable controls for any direct effects of changes in the tax rates on firm outcomes, independent of changes in vertical integration. Because the statutory tax rate variable is available for only 19 states, we encounter few cluster problems (Cameron and Miller (2015)). The estimates reported here are not clustered. The key assumptions required to estimate the effect of greater vertical integration on firm outcomes are as follows. First, the instrument is exogenous to firm outcomes. This cannot be completely tested. However, the observed parallel trends before VAT adoption do not suggest any observable correlation between trends in vertical integration and state VAT adoption. Second, the instrument satisfies the exclusion restriction. This suggests that the only effect of the reform on firm outcomes is through vertical integration. Given the nature of the tax reform—which changed effective product tax rates and reduced double taxation by allowing input tax credit—this is a rather strong assumption. I address these two concerns as follows. I control for changes in statutory tax rates brought about by the reform. Firm distance controls for any direct effects of VAT adoption that are correlated with a firm’s position in the production chain. This includes the effects of input tax credits which vary along the production chain.22 The previous sections showed that the VAT reform significantly increased vertical integration among firms. Fourth, because the treatment variable—change in input upstreamness—is of variable intensity, we require the monotonicity assumption. This assumption requires that the instrument increase the treatment at all values of treatment. When monotonocity is satisfied, an IV estimator calculates the weighted average of unit causal response at each value of the treatment variable. For nonnegative values of the treatment variable, a possible test is to compare the CDF of

22A simple way to think about it is that there are two additional mediating channels through which the reform affects ﬁrm outcomes. Controlling for these channels blocks the direct path from the instrument to ﬁrm outcomes.

65 the treatment variable when the instrument is turned on (the firm produces a VAT product) versus when it is turned off (the firm produces a VAT exempt product). If the monotonicity assumption is satisfied, the CDF with the instrument turned on first-order stochastically dominates the CDF when the instrument is turned off (Angrist and Pischke (2009), p. 182). Figure 2.18 illustrates the monotonicity test. The x-axis plots the CDF of the changes in firm- level input upstreamness before and after VAT adoption. The dashed line represents the CDF if the firm produced a tax-exempt output before the reform (instrument off), and the solid line represents the CDF if the firm produced a VAT good before the reform (instrument on). Figure 2.18 shows that more than half of the changes are positive; this can be interpreted as a consequence of the VAT reform which increased average firm upstreamness. Moreover, along the nonnegative values at which the CDF test is valid, the CDF of the changes for firms that produced a VAT-product lies below the CDF of changes for firms that produced a VAT-exempt product in 2003. Finally, Table 2.18 reports the results of Kolmorgorov-Smirnov test of the equality of distribution. The hypothesis of distribution equality is strongly rejected. Table 2.7 reports 2SLS estimates of effect of increased integration on a host of firm outcomes. The Kleibergen-Paap F-stat varies across specifications because of missing outcome values.23 The relative value of the F-stat at about 7.8 is a concern. With weak instruments, IV estimates are biased toward the OLS estimates, which are generally inconsistent. The Stock-Yogo critical values for 25% and 20% bias in the IV estimate are 7.25 and 8.75, respectively. While we reject a 25% bias, we cannot reject 20% maximal bias in the IV. Because in the case of weak instruments, the IV estimate is biased towards the OLS estimate, I report OLS estimates and corresponding standard errors in the third-to-last row of Table 2.7. Two-stage least square estimates indicate that a unit increase in vertical integration, as measured by firm average input upstreamness, significantly increases the firm’s value added, where value added is measured as the difference between gross sales and material costs (Column 1).

23Restricting to ﬁrms that report all outcome variables reduces the sample size by 6,000 observations. Estimates are underpowered, and the F-Stat drops further to 6.5. These issues suggest that the estimates in this section should be interpreted with caution and are more suggestive in nature.

66 Note that if any fixed costs were incurred in the process of integration, they are not reflected in the value-added measure. The effect on ouput per worker is barely significant (Column 2). An integrated firm is larger, as measured by log sales or the log number of workers (Columns 6 and 7). There is no significant effect on either workers’ wages (Column 4) or the net-of-tax output price (Column 8). However, integration hurts government revenues. Column 10 reports the “unpaid tax," which calculates the difference in the tax rate a firm should remit based on the statutory tax rate on its outputs and the tax rate it actually remits, as reported in the ASI “sales tax” paid column.24 The difference between these two quantities does not necessarily indicate evasion. Actual reported tax paid could be lower than the statutory tax when the firm is subject to exemptions, or when it did not report in the survey data. It could also be lower if the firm adjusted its production to produce low-tax outputs or shifted production toward the untaxed good (tax avoidance). Either way, we see that a one-unit increase in vertical integration increases the unpaid tax rate by about 1.14 percentage points (Column 8). Finally, vertical integration significantly increases profit per worker, where profit is defined as the difference in before-tax value added and wages paid. It does not include any fixed or capital costs incurred in the process of vertical integration. To conclude, this section illustrates that tax-policy-induced changes in vertical integration have policy implications. Integration leads to larger firms, as measured by value added, firm gross sales or the number of workers. However, this comes at a cost to the government. The average tax rate remitted by an integrated firm is lower. This implies that the cost of enforcing a VAT increases when firms integrate for evasion. Consequently, an optimal tax under VAT in settings with weak enforcement must incorporate the trade-off between production efficiency (high before-tax profits per worker) and revenues (more evasion leads to lower revenues).

24A firm reports absolute sales tax remitted in addition to the net sales value for each product. I calculate the “actual tax rate" paid as the total tax remitted divided by the net of tax output value. For a significant fraction of firms, this quantity is 0.

67 2.5.1 Welfare effects of the tax reform

This section discusses the aggregate welfare effects of the tax reform. There are three agents in the economy: consumers, producers, and the government. There are several components that determine the welfare impact on these agents. The welfare effect on producers (firms) depends on how VAT adoption changed market competition, output, and prices for firms. Table 2.7 shows that vertical integration induced by VAT adoption led to higher firm output and lower tax remitted. While higher output and lower tax liability likely increase producer welfare, a plausible increase in operation costs mitigates this effect. In addition, integration reduces competition in the market. This is evident in the fact that VAT adoption led to more mergers and acquisitions. Lower competition can lead to an increase in prices benefiting firms. Also, the removal of double taxation as a result of an improperly administered sales tax can increase net-of-tax prices recieved by firms. Table 2.7, however, shows that there was no significant impact on firms’ per-unit output price.25 Overall, the net impact on producer welfare depends on how much firms’ net-of-tax revenues increased in relation to their operation costs. Although lower tax rates and higher output in the VAT regime are welfare improving for consumers, higher prices due to reduced competition is welfare-reducing. It is hard to determine the net welfare impact on consumers, because the ASI data do not report unit prices paid by consumers. Also, reduction in prices as a result of the removal of double taxation can improve consumer welfare. Finally, for a fixed output, the government lost revenue on two counts: lower tax rates and tax evasion in VAT regime. However, higher output could raise total revenues. Unfortunately, the unavailability of state revenue data renders this exercise implausible. While estimating the impact on aggregate welfare is interesting, a complete welfare analysis of VAT adoption is beyond the scope of this paper.

25Note that this is a coarse measure of “per-unit price," obtained by dividing sales net of distributive expenses (including taxes) by units sold, and may not adequately capture the true per-unit net-of-tax price received by the ﬁrm.

68 2.6 Conclusions

Value-added tax is the most popular consumption tax in the world. It is hailed for its ability to generate larger revenues through minimal tax evasion and production efficiency. This paper presents evidence that VAT may not be production-efficient, since it leads to reorganization of production chains. The ability of firms to evade tax at the retail stage creates incentives for the last two firms in the production chain to integrate vertically. To test this hypothesis, I use a quasi-experiment featuring staggered adoption of VAT by states in India between 2003 and 2008 and plant-level input-output data. To measure vertical integration, I create an index of product upstreamness in which the products located higher in the production chain are assigned higher values. Greater vertical integration implies larger upstreamness of inputs. Using a differences-in- differences strategy, I find that the tax reform increased the average upstreamness of firm inputs. Effects are larger for firms situated closer to the final demand suggesting that tax evasion is a plausible channel. Empirical evidence does not lend support to alternative hypotheses, such as higher liquidity constraints, compliance costs, or lower tax rates in the VAT regime. The findings in this paper suggest that firm responses to evasion reduce government revenues. Consequently, an optimal tax under VAT in settings with weak enforcement must incorporate the trade-off between production efficiency (high before-tax profits per worker) and revenues (more evasion leads to lower revenues).

69 2.7 Tables and Figures

Figure 2.1: Country VAT Adoption

This ﬁgure shows the aggregate number of countries that adopted VAT since 1980.

70 Figure 2.2: State VAT adoption in India:

This ﬁgure illustrates the time distribution of state VAT adoption in India. The ﬁrst state Haryana adopted VAT in 2003. The last state Uttar Pradesh adopted VAT in 2008. Data: State VAT laws.

71 Figure 2.3: State VAT adoption in India

This ﬁgure illustrates the spatial distribution of state VAT adoption in India. The only state/territory that never adopted VAT is Andaman and Nicobar Islands. Data: State VAT Laws.

72 Figure 2.4: Effect of the VAT adoption on state revenues This graph presents an event study of log yearly state own revenues and years since since VAT adoption. The specification includes state and year fixed effects. Data: NITI Ayog. Sample restricted to 2003-2010. The bars indicate 10% robust confidence interval.

73 (a)

(b)

(c)

(d)

Figure 2.5: Vertical integration in retail sales tax versus VAT

This figure illustrates change in tax instrument and the resulting change in firm organization. Panel (a) shows tax collection under RST. Only the last firm which sells directly to the consumer is responsible for remitting tax. In Panel (b), all firms remit tax as a fixed proportion of their value added. If the tax rate is same under RST and VAT, the total tax collected across the value chain either (a) or (b) is same. Panel (c) illustrates when second last firm, F3 integrates with the last firm, F4. The integrated firm, F3 gains by under-reporting sales to consumer which are not subject to cross-reporting, in contrast to transactions with other non-consumer firms. This lowers tax paid by F3.

74 Figure 2.6: Vertical integration and product upstream measure

This figure illustrates the implications of vertical integration to the average product upstreamness in the production chain. The top panel illustrates when the last two firms in the chain F2 and F3 are disintegrated. An average firm in this chain uses less upstream inputs and produces more upstream outputs. In contrast, the bottom panel illustrates when the last two firms F2 and F3 integrate. An average firm in the production chain now uses more upstream inputs and produces more downstream outputs.

Figure 2.7: Vertical distance of firms This figure plots the distribution of firms in the sample according to the vertical distance. Vertical distance is the difference between the average upstreamness of the output and input of a firm. A firm that sources inputs which are more upstream has higher vertical distance, compared to a firm with similar output but less upstream inputs. Data: Annual Survey of Industries, 2003-10.

75 Figure 2.8: Distribution of U2

This ﬁgure plots the distribution of products according to their upstream measure. The sample includes products observed in the Annual survey of Industries dataset in year 1999-00.

76 Figure 2.9: Tax rate change in VAT reform The ﬁrst panel presents the distribution of state-product tax rate changes, which were part of the reform. The right panel shows average product tax rate change across states. The tax rate change data is obtained by hand-coding of product tax rate for each state-product, before and after the VAT reform. The tax rate data exists for 17 out of 32 states in the Annual survey of Industries data.

77 Figure 2.10: Effect of VAT adoption on vertical integration (Inputs) This figure presents event study coefficients of firm’s average input upstreamness on the dummies for years since VAT adoption interacted with a dummy indicating whether the firm’s main product in 2002 was non-VAT-exempt. Dummy for a year before the adoption is omitted. The regression also includes firm and year fixed effects. The bars indicate robust 10% confidence interval. Data: Annual Survey of Industries, 2003-10.

78 Figure 2.11: Effect of VAT adoption on vertical integration (Outputs) This figure presents event study coefficients of firm’s average ouput upstreamness on the dummies for years since VAT adoption interacted with a dummy indicating whether the firm’s main product in 2002 was non-VAT-exempt. Dummy for a year before the adoption is omitted. The regression also includes firm and year fixed effects. The bars indicate robust 10% confidence interval. Data: Annual Survey of Industries, 2003-10.

79 (a)

(b)

Figure 2.12: State-level effects

This figure plots the effect of the state VAT adoption on three outcomes: average upstreamness of firm outputs, inputs and vertical distance between firm output and input. Vertical difference is the difference between upstreamness of firm output80 and input. Observation is a state-year average. The bars indicate coefficients from regression of the outcome variable on dummies indicating years since treatment. Dummy for a year before VAT adoption is omitted. Regressions include state and year fixed effects. Robust confidence intervals are plotted at 5% significant level. Data: Annual Survey of Industries, 2003-10. Figure 2.13: Mechanism 1: Tax evasion

81 Figure 2.14: Mechanism 2: Liquidity constraint This figure presents treatment effects as a function of distance from the final demand. Firm-year observations are ordered into 20 quantitles and a quantile for the lowest distance. Distance to final demand is determined by the average upstream measure of firm outputs in 2004. Data: Annual Survey of Industries, 2003-10.

82 Figure 2.15: Mechanism 3: Compliance costs This figure presents treatment effect as a fucntion of the firm size. Firm-year observations are ordered into 20 quantiles according to their size. Firm size serves as a measure of compliance costs faced by a firm under VAT. It is measured as the number of employees in the firm. Data: Annual Survey of Industries, 2003-10.

83 Figure 2.16: Mechanism 5: Higher tax rate on upstream firms This figure tests if the higher tax rates on goods produced by the upstream firms created incentives for firms to integrate under the VAT reform. Higher tax rates on goods produced out-house rather than in-house create penalty for producing out-house. This would be the case if the VAT reform increased tax rates on upstream goods compared to downstream goods. Data: VAT and Sales Tax Laws 2001-2010.

84 Figure 2.17: Mergers and acquisitions This graph plots event-study coefficients of state-year number of log(mergers+1) on dummies indicating years since VAT adoption. The regression includes state, year fixed effects and is weighted by the number of companies in the state. Dummy for a year before adoption is omitted from regression. Confidence intervals are plotted at 5% significance level. Data: PROWESS 2001-2010.

85 Figure 2.18: Test of Monotonicity assumption for 2SLS Estimation

86 Figure 2.19: Leave-one-out test This figure presents results for robustness of the effect of VAT adoption on firm input upstreamness with respect to state. Each bar denotes the estimated effect using specification 2.1, with corresponding state dropped. Data: Annual Survey of Industries, 2003-10.

87 Figure 2.20: Placebo test This ﬁgure presents results of a placebo test where I keep the order of the state VAT adoption but move the year of adoption back. In particular, I estimate regression 2.3 move the adoption one to ﬁve years back. Data: Annual Survey of Industries, 2004-10.

88 Figure 2.21: Firms number by distance to final demand This figure plots the total number of firms observed each in the ASI dataset as a function of distance to the final demand. The distance is calculated as the average upstreamness of firms’ output. Data: Annual Survey of Industries, 2003-10.

89 Figure 2.22: Effect by industry This figure reports the estimates of effect of VAT adoption on average upstreamness of the inputs, as a function of industry. Specifically, each estimate refers to the coefficient Non Tax ExemptX Adopt in regression 2.1. Each bar restricts the confidence interval obtained by restricting the sample to firms in 1 digit ASICC industry as indicated on the x-axis. Data: Annual Survey of Industries, 2003-10.

90 Figure 2.23: Vertical integration under VAT

This figure illustrates the effect of vertical integration on the nature of transactions. Without integration (the left panel) greater number of transactions are ‘arms length’. These include transactions between two firms such as S-M and M-R. In contrast, the transaction between R and C is non arms- length because it is not subject to cross reporting. With vertical integration (the right panel), fewer transactions are arms-length (such as between S and the integrated firm M-R). This leads to higher costs of enforcement under VAT and lower revenues collected.

91 Mean Standard Deviation Min Max N Uptreamness (Inputs) 4.6039351 5.0402157 -13.386 449.45999 316269 P(U < 2) .89354632 .30841789 0 1 316269 P(U ≥ 2) .10645368 .30841789 0 1 316269 Employee Days 55364.136 231786.26 0 16437410 313840 Mean Factory Value 2.120e+08 2.246e+09 0 4.645e+11 301388 Mean Gross Output 2.360e+08 2.437e+09 0 4.860e+11 301388 Per-unit Price 85014.268 4804127.8 -16.76 1.701e+09 301388 Capital 44890312 1.252e+09 -1.708e+11 2.827e+11 313514 Total Liabilities 1.351e+08 1.431e+09 -31129102 3.346e+11 307137 Total Assets 1.772e+08 1.921e+09 -28498084 4.075e+11 313526 Stock of Materials 37643652 4.683e+08 0 1.622e+11 302447 Stock of Finished Goods 31344468 2.370e+08 0 4.724e+10 246631 Materials 32079251 4.329e+08 0 1.465e+11 290249 Loans 1.091e+08 1.303e+09 0 2.086e+11 250926 Cash 8048781.9 2.260e+08 -1246668 6.404e+10 311366 Number of workers 139.19135 611.99213 0 45481 312961 Number of Inputs 11.588845 3.6616965 1 98 313947 Number of Outputs 3.1084546 1.9392734 0 12 313947

Table 2.1: Summary Statistics This table presents summary statistics for key variables in the Annual Survery of Industries dataset 2001-10. This dataset is to estimate effect of the VAT adoption on ﬁrm input upstreamness. An observation in the sample is a ﬁrm-year. Firms larger than 100 employees are surveyed each year. Firms smaller than 100 employees are surveyed with a probability. Please refer to Section B.1 for more details about the dataset.

92 (1) (2) (3) (4) (5) (6) Non Tax ExemptX Adopt 0.584 0.572 0.489 0.482 0.376 0.356 (0.170)*** (0.174)*** (0.206)** (0.207)** (0.162)** (0.169)** Non tax exempt -0.189 -0.162 2.213 2.226 -0.192 -0.182 (0.432) (0.436) (0.560)*** (0.558)*** (0.0827)** (0.0862)** Adopt -0.370 -0.391 0.0477 0.0290 -0.295 -0.490 (0.176)** (0.188)** (0.268) (0.270) (0.278) (0.222)** State speciﬁc linear trends No Yes No Yes No Yes Ind FE No No Yes Yes No No Firm FE No No No No Yes Yes State FE Yes Yes Yes Yes Yes Yes Year FE Yes Yes Yes Yes Yes Yes N 243566 243566 243566 243566 243566 243566 adj. R2 0.073 0.074 0.172 0.172 0.848 0.849

Table 2.2: Results for Specification 2.1, Firm Inputs This table reports the coefficients of regression 2.1 where the outcome variable is the average upstreamness of firm inputs. More specifically, I regress the average upstreamness of firm input mix on a dummy indicating if the main output produced by the firm in 2002 is subject to VAT interacted with the adoption year dummy.. All regressions include state, year fixed effects and a dummy for the year of state VAT adoption. Standard errors clustered at the state level are reported in the parantheses. There are 32 states in the sample. Data: Annual Survey of Industries, 2003-10. *p < 0.10, ** p < 0.05, *** p < 0.01

93 (1) (2) (3) (4) (5) (6) Non Tax ExemptX Adopt 0.212 0.227 0.0684 0.0816 -0.169 -0.164 (0.148) (0.150) (0.154) (0.153) (0.166) (0.164) Non tax exempt -0.773 -0.786 -0.101 -0.113 0.0866 0.0840 (0.219)*** (0.221)*** (0.164) (0.164) (0.0848) (0.0837) Adopt -0.0933 -0.0746 0.0189 0.0367 0.222 0.164 (0.134) (0.137) (0.140) (0.148) (0.210) (0.206) State speciﬁc linear trends No Yes No Yes No Yes Ind FE No No Yes Yes No No Firm FE No No No No Yes Yes State FE Yes Yes Yes Yes Yes Yes Year FE Yes Yes Yes Yes Yes Yes N 212065 212065 212065 212065 212065 212065 adj. R2 0.024 0.024 0.128 0.129 0.776 0.776

Table 2.3: Results for Specification 2.1, Firm Outputs This table reports the coefficients of regression 2.1 where the outcome variable is average upstreamness of firm outputs. More specifically, I regress the average upstreamness of firm output mix on a dummy indicating if the main output produced by the firm in 2002 is subject to VAT interacted with the adoption year dummy. All regressions include state, year fixed effects and a dummy for the year of state VAT adoption. Standard errors clustered at the state level are reported in the parantheses. There are 32 states in the sample. Data: Annual Survey of Industries, 2003-10. *p < 0.10, ** p < 0.05, *** p < 0.01

(1) (2) (3) (4) (5) Adopt 0.209 0.176 0.228 0.179 0.0760 (0.0660)*** (0.0616)*** (0.0728)*** (0.0603)*** (0.209) State speciﬁc linear trends No Yes No Yes No Ind FE No No Yes Yes No Firm FE No No No No Yes State FE Yes Yes Yes Yes Yes Year FE Yes Yes Yes Yes Yes N 243542 243542 243542 243542 243542 adj. R2 0.073 0.074 0.171 0.172 0.848

Table 2.4: Results for Specification 2.3 This table reports the estimates from regression 2.3. Specifically, I estimate the effect of state level VAT adoption on the average upstreamness of inputs. Between 2003 and 2010, states adopted VAT in a staggered manner. All regressions include state and year fixed effects. Robust standard errors clustered at state level are reported in parentheses. Total Number of Clusters=32. Data: Annual Survey of Industries, 2003-10. * p < 0.10, ** p < 0.05, *** p < 0.01

94 (1) (2) Non Tax ExemptX Adopt 0.345** 0.375** (0.106) (0.120)

Non tax exempt -0.0617 -0.0626 (0.0380) (0.0378)

Adopt -0.218 -0.219 (0.161) (0.161)

Non Tax ExemptX AdoptX(Tax change < 0) -0.0827 (0.130)

Constant 4.877*** 4.877*** (0.0612) (0.0613) N 88886 88886

Table 2.5: Differential effects by tax rate change This table presents results for the main speciﬁcation where the treatment is interacted with whether or not the ﬁrm also experiences a decline in tax on its outputs, as part of the tax reform. Standard errors clustered at the state level are reported in the parantheses. Data: Annual Survey of Industries, 2003-10. * p < 0.10, ** p < 0.05, *** p < 0.01

Ln(Assets) Ln(Employment) Ln(Sales) 0.446 0.149 0.270 (0.114)*** (0.0775)* (0.0773)*** Prices Ln(Output Price) Ln(Excise Tax) -0.112 0.000135 (0.262) (0.00213) Standard errors in parentheses * p < 0.10, ** p < 0.05, *** p < 0.01

Table 2.6: Effect on other outcomes This table reports the coefficients of regression 2.1 for several outcomes specified in the column. More specifically, I regress the average upstreamness of firm output mix on a dummy indicating if the main output produced by the firm in 2002 is subject to VAT interacted with the adoption year dummy. All regressions include state, year fixed effects and a dummy for the year of state VAT adoption. Standard errors clustered at the state level are reported in the parantheses. There are 32 states in the sample. Data: Annual Survey of Industries, 2003-10. *p < 0.10, ** p < 0.05, *** p < 0.01

95 (1) (2) (3) (4) (5) (6) (7) (8) (9) (10) Y Y Value added Log( w ) Log( K ) Log wage Log Price Log sales Log workers Tax unpaid Excise paid Proﬁt per worker VI 73627955.4 0.206 0.0922 0.0417 0.164 0.450 0.244 0.0143 -0.0102 1467862.9 (2.07)** (1.63) (0.47) (0.64) (0.59) (2.61)*** (2.20)** (2.82)*** (-0.63) (2.02)**

statrate -15940223.3 0.245 0.0725 0.0693 0.352 0.367 0.131 1.016 -0.249 542884.5 (-0.33) (1.91)* (0.41) (1.12) (1.09) (1.96)** (1.13) (100.88)*** (-0.70) (0.47)

Firm Position -12234757.1 -0.0310 -0.0166 -0.00818 -0.00180 -0.0696 -0.0382 -0.00232 0.00148 -260402.7 (-1.98)** (-1.47) (-0.54) (-0.79) (-0.04) (-2.19)** (-1.94)* (-2.48)** (0.60) (-2.04)** KP F-stat 7.822 7.834 6.891 7.827 5.966 7.840 7.815 7.840 7.840 7.815 Reduced Form 18742017.0 0.120 0.0783 0.0449 0.0762 0.269 0.160 0.0176 -0.00138 242737.4 t-stat 1.619 2.418 0.920 1.398 0.704 4.869 3.742 8.211 -0.352 1.285 OLS -796863.2 -0.0106 -0.00566 -0.00937 0.0253 -0.0176 -0.00682 0.00000171 -0.000536 -23865.5 SE 406090.8 0.00266 0.00314 0.00141 0.00502 0.00315 0.00195 0.0000369 0.000570 11293.5 Observations 84529 84218 82617 84252 78117 84492 84255 84492 84492 84255

Table 2.7: IV estimates

96 This table presents instrumental variables estimate of the effect of vertical integration (VI) on firm outcomes. The instruments include year of state VAT adoption and the interaction with whether the firm produced VAT exempt product in 2004. VI is measured by the average upstreamness of firm inputs. Value-added and profits per worker are winsorized at 1%. Value added is defined as the difference between firm gross sales and material costs. Log wage denotes logarithm of average worker compensation in the firm. Profit per worker is defined as the difference between before-tax value added and wage costs divided by the number of workers. Tax unpaid is defined as the difference between statutory tax rate and actual tax rate remitted as reported in the ASI data. Data: Annual Survey of Industries, 2003-10. t-statistics are reported in parantheses. * p < 0.10, ** p < 0.05, *** p < 0.01 (1) (2) (3) (4) (5) State GDP Manufacturing Unregistered MN Agr. GDP Tax revenues DelayAdoption 0.0177 0.0171 0.0141 -0.0135 -0.0180 (0.0219) (0.0622) (0.00551)** (0.0328) (0.0189) Observations 160 160 160 160 156 Adjusted R2 0.132 0.074 0.604 -0.024 0.054

Table 2.8: Correlation between state-level delay in VAT adoption and outcomes This table reports the coefficients of the first-difference regression of key state outcomes against a variable that takes value equal to the state-specific delay in VAT adoption. Sample restricted to pre-VAT adoption years. All regressions include state-specific fixes effects. Robust standard errors in parentheses. Data: Niti Ayog GDP reports *p < 0.10, ** p < 0.05, *** p < 0.01

Figure 2.24: Firm distribution by industry This ﬁgure plots the distribution of ﬁrm-year observations in the Annual Survey of Industries data against the 1-digit ASICC code.

97 Product Name Upstream Measure Iron Ore 4.85 Pig Iron 3.97 Iron & Steel Nuts, bolts, screw, washers 3.57 Pipe & ﬁlings, cast iron 3.36 Sheets & plates, iron/steel 2.74 Skin, sheep 3.75 Leather Skin, sheep & goat-chrome tanned 2.81 leather, semi-tanned 2 Belt, waist, leather 1 Kapas (raw cotton) 3.36 Cotton Yarn, bleached cotton 2.89 Yarn, ﬁnished/processed 2.72 Knitted fabrics, cloth cotton 2 Meat (all types) 68.98 Meat and meat products Meat fresh 64.50 Meat cooked (not canned) 6.78

Table 2.9: Product upstreamness This table illustrates the distribution of product upstreamness within a value chain. Higher value of upstreamness indicates the product is located higher up in the chain. For more detail about how this measure is created, please refer to Section 2.2.2. Data: Annual Survey of Industries, 1999-00

(1) (2) (3) (4) (5) (6) Adopt 0.128 0.151 0.0972 0.114 0.0194 0.00699 (0.0619)** (0.0740)*** (0.0513)** (0.0551)** (0.0724) (0.0928) State speciﬁc linear trends No Yes No Yes No Yes Ind FE No No Yes Yes No No Firm FE No No No No Yes Yes State FE Yes Yes Yes Yes Yes Yes Year FE Yes Yes Yes Yes Yes Yes adj. R2 0.014 0.015 0.048 0.049 0.849 0.849 N 126269 126269 126269 126269 126269 126269

Table 2.10: Results for Specification 1 This table reports the estimated coefficients in regression 2.3. More specifically, I regress the average upstreamness of firm input mix on a dummy indicating years since state VAT adoption. All regressions include state, year fixed effects. Standard errors clustered at the state level are reported in the parantheses. There are 32 states in the sample. Data: Annual Survey of Industries, 2003-10. *p < 0.10, ** p < 0.05, *** p < 0.01

98 (1) (2) (3) (4) (5) (6) Rank Mean Abs Dev Median Abs Dev Min Max Median Non Tax ExemptX Adopt 0.0588 -0.0305 0.0491 -0.203 -0.349 -0.0729 (0.0624) (0.140) (0.158) (0.152) (0.356) (0.161) Non tax exempt -0.0301 0.0156 -0.0251 0.104 0.178 0.0372 (0.0319) (0.0715) (0.0810) (0.0775) (0.182) (0.0823) Adopt -0.0405 0.177 0.0217 0.126 0.590 0.0797 (0.0694) (0.225) (0.199) (0.143) (0.524) (0.186) Observations 212065 212065 212065 212065 212065 212065 Adjusted R2 0.765 0.640 0.451 0.761 0.729 0.762

Table 2.11: Results for Specification 2, Output Second moments This table presents results of effect of VAT adoption on second moments of firms output upstreamness. All regression use specification2 which controls for firm and year fixed effects. * p < 0.10, ** p < 0.05, *** p < 0.01

Table 2.12: Winsorized Regressions

(1) (2) (3) (4) (5) (6) Adopt × V AT 0.581 0.568 0.486 0.480 0.404 0.386 (0.171)*** (0.174)*** (0.209)** (0.210)** (0.163)** (0.169)** V AT -0.158 -0.133 0.572 0.592 -0.206 -0.197 (0.421) (0.425) (0.539) (0.543) (0.0833)** (0.0865)** Adopt -0.375 -0.396 -0.261 -0.303 -0.309 -0.495 (0.175)** (0.186)** (0.222) (0.214) (0.273) (0.216)** State speciﬁc linear trends No Yes No Yes No Yes Ind FE No No Yes Yes No No Firm FE No No No No Yes Yes State FE Yes Yes Yes Yes Yes Yes Year FE Yes Yes Yes Yes Yes Yes N 243566 243566 243566 243566 243566 243566 adj. R2 0.080 0.081 0.189 0.189 0.863 0.864 Standard errors in parentheses * p < 0.10, ** p < 0.05, *** p < 0.01 Table 2.13: DD estimates for the average input upstreamness: 2004-2010 (Winsorized) Data: Annual Survey of Industries, 2003-10.

99 (1) (2) (3) (4) (5) (6) Adopt 0.214 0.182 0.234 0.186 0.0706 -0.142 (0.0648)*** (0.0607)*** (0.0713)*** (0.0592)*** (0.209) (0.120) State speciﬁc linear trends No Yes No Yes No Yes Ind FE No No Yes Yes No No Firm FE No No No No Yes Yes State FE Yes Yes Yes Yes Yes Yes Year FE Yes Yes Yes Yes Yes Yes N 244295 244295 244295 244295 244295 244295 adj. R2 0.074 0.074 0.173 0.174 0.844 0.845 Standard errors in parentheses * p < 0.10, ** p < 0.05, *** p < 0.01

Table 2.14: Estimation with upstream measure calculated using Pseudo-inverse. Data: Annual Survey of Industries, 2003-10.

(1) (2) (3) (4) (5) (6) Non Tax ExemptX Adopt 0.506 0.492 0.355 0.344 0.386 0.366 (0.170)*** (0.171)*** (0.212) (0.211) (0.161)** (0.167)** Non tax exempt -0.0119 0.0192 0.921 0.952 -0.197 -0.187 (0.436) (0.437) (0.558) (0.562) (0.0821)** (0.0855)** Adopt -0.348 -0.367 -0.207 -0.249 -0.286 -0.484 (0.169)** (0.182)* (0.220) (0.214) (0.271) (0.217)** State speciﬁc linear trends No Yes No Yes No Yes Ind FE No No Yes Yes No No Firm FE No No No No Yes Yes State FE Yes Yes Yes Yes Yes Yes Year FE Yes Yes Yes Yes Yes Yes N 236020 236020 236020 236020 236020 236020 adj. R2 0.074 0.075 0.208 0.208 0.848 0.849 Standard errors in parentheses * p < 0.10, ** p < 0.05, *** p < 0.01

Table 2.15: Robustness check: dropping non-positive upstream values Data: Annual Survey of Industries, 2003-10.

100 Upstreamness ASICC08 Code Description -13.386 63437 GARMENTS, KNITTED- COTTON -12.386 63332 SUITINGS, COTTON -11.21 74066 CUFFS AND LINKS BUTTONS -10.887 91525 CASSETTE, PRE-RECORDED -9.8874 78204 TAPE RECORDERS, AUDIO -9.8874 78205 AUDIO TAPES -9.8874 42127 CASSETTE COVER, PLASTIC -9.6737 55312 PAPER, SAND -9.3363 42425 MAGNETIC TAPE OF PLASTIC / PVC -8.702 78214 CASSETTE COMPONENTS Upstreamness ASICC08 Code Description 52.623 31607 CALCIUM NITRATE 53.184 11101 BUFFALO, LIVE 64.266 11611 MEAT, MEAL 64.507 11209 MEAT FRESH, N.E.C 68.988 11231 MEAT ( ALL TYPES ), CANNED 74.09 85244 PARTS OF SHIPS, BOATS ETC., N.E.C 80.343 11203 BUFFALO MEAT, FRESH/FROZEN 81.343 12141 PEAS, GREEN 85.052 12315 BASMATI RICE 449.46 36121 OIL, GINGERLY

Table 2.16: Lowest and highest upstream products This table presents the ten highest and lowest upstream products. Larger upstream values indicate products that are higher up in the value chain. For details about how this upstream measure is created using the ﬁrm data, please refer to Section 2.2.2. Data: Annual Survey of Industries, 1999-00.

Dist Final Demand Liquidity Firm size Dist Final Demand 1.0000 Liquidity 0.0866 1.0000 Firm size -0.0338 0.0050 1.0000

Table 2.17: Correlation among measures This table presents correlation among three key measures used to test the mechanisms in this paper. These include distance to the final demand, used to test the evasion mechanism; industry- level cash flow sensitivity measure used to test the liquidity constraint mechanism; and firm size measure used to test the compliance costs hypothesis.

101 Smaller group D P-value TaxExempt = 0: 0.0873 0.000 TaxExempt = 1: -0.0368 0.209 Combined K-S: 0.0873 0.000

Table 2.18: Kolmogorov-Smirnov test This table provides test of the hypothesis that the distribution of change in input upstreamness of firms that produced VAT goods before the reform first order stochastically dominates the corresponding distribution of firms that produced VAT exempt goods. Column 2 calculates the difference between the two groups and Column 3 reports the p-value for the hypothesis that group mentioned in row 1 is the smaller group.

Sales Tax (Pre-reform) VAT (Post-reform) Mean 8.29 7.31 Median 8 5 SD 4.57 4.87 Min 0 0 Max 115 65 N 88,935 93,709

Table 2.19: Tax rates pre and post VAT This table presents summary statistics for state tax rates pre-reform (sales tax) and tax rates post reform (VAT). Source: state tax laws 2001-2010 digitized by the author.

102 Chapter 3: Do Property Tax Incentives for New Construction Spur

Gentriﬁcation? Evidence from New York City

Major cities across the United States are grappling with steep increases in housing costs. For instance, more than half of tenants spend more than 30% of their income on rents in New York City. Consequently, economists and policymakers have suggested that a solution to tackle rising rent is to build more units (CEA (2019); Glaeser et al. (2005)).1 However, at the ground level, such proposals often face resistance from local residents and politicians who dislike the changes new development brings to a neighborhood (Quigley and Rosenthal (2005)). Understanding these changes is crucial for adequate policy design. My paper asks: What are the effects of new residential construction on rental prices in a neighborhood? Finding credible causal evidence is particularly challenging, because changes in investment and rent growth are strongly correlated. For instance, developers choose where to invest and when to invest. In this paper, I make progress on this front by using a rare natural experiment in New York City. The government abolished long-standing property tax beneﬁts on new residential units, but it announced the policy change before implementation. Consequently, developers responded by rushing to apply for the expiring beneﬁts and building more units. I estimate the effect of this short-term increase in new units on existing buildings’ rents in the neighborhoods in which these units were constructed. The decline in the expected future return due to the tax reform provides variation in timing that is not correlated with rents. The availability of microdata at the level of a parcel on investment, rent, and property tax data allows me to estimate local effects and control for time-varying factors that determine project location. 2

1Other measures employed to increase affordability include rent control (Olsen (1972); Diamond et al. (2018)); zoning; income tax credits (Diamond and McQuade (2016); Baum-Snow and Marion (2009)); and public housing (Olsen and Barton (1983); Chyn (2018)). See Olsen (2003) for a survey of studies on housing programs in the US. 2A parcel is a piece of land that contains one or more structures. An average parcel in New York City includes a

103 I find that an increase in the future property tax as part of the reform significantly increased new rental residential construction in the anticipatory period. However, the units brought to the market by the reform increased the rents in the neighborhoods in which they were built. I propose that one explanation for why new units increase nearby rent prices is that new units increase the average income of the residents in the neighborhood. Higher neighborhood income, in turn, increases local amenities, such as sidewalk cafés, and allows incumbent landlords to charge higher rents. Evidence of changes in demographics and business composition in regions that received investment during this period provides support for this channel. As a high-rent city with high property taxes, New York City provides an ideal setting. Rental buildings in New York face the highest property tax in the country (Lincoln (2018)). 3 The tax policy—421a property tax exemption—exempts beneficiaries from any increment in property tax due to new construction. Projects that convert vacant land into residential units qualify for the exemption. The standard model suggests that underlying demand and supply elasticities determine how much of the tax decrease is passed on to tenants. However, the model does not incorporate whether new investment leads to neighborhood change. By increasing the conditions attached to the property tax exemption, the tax reform effectively raised property tax on new investment in select "exclusion" regions in the city (blue regions in Fig- ure 3.1) beginning in July 2008. However, the delay between announcement and implementation created incentives for developers to move investment forward in time.4 The excess tax-exempt housing starts in exclusion regions in the period between announcement and implementation allows me to estimate the elasticity of current residential (rental) investment to anticipated changes in the future property tax rate.5 Policymakers selected the exclusion regions based on political and economic reasons. I find that the excess bunching in the housing starts in the time notch suggests that residential building. 3The average property tax rate as a share of assessed valuation is around 3.3% on rental buildings, compared with 0.6-1% on owner-occupied units. 4This is referred to as "grandfathering." 5In other words, the number of projects weighed by the number of units built in each project.

104 investment is responsive to the property tax. A 1% anticipated increase in the future property tax rate increased current residential investment by 0.4%. Lutz (2015) estimates a related elasticity of 0 within Boston and 1 in the suburban ring of Boston; however, this estimate combines inframarginal responses with new construction. Overall, the bunching increased the stock of rental housing in the exclusion regions by around 1%. Next, I estimate the local rent effects of new construction in this period using an instrumental variables approach. In particular, the availability of vacant parcel within a small radius (150 meters in the baseline specification) of an existing rental building acts an an instrument for the magnitude of investment around it in the time notch. A building with a vacant parcel available within 150 meters at the start of the reform received 0.9 more tax-exempt units in the time notch, compared with buildings with no vacant parcels within that distance. The identification relies on the assumption that within a small census tract, which building had a vacant parcel available is uncorrelated with its rent growth in the reform period after controlling for building, year, and census tract-year fixed effects. Several factors not entirely in developers’ control determine whether a building had a vacant parcel nearby. For instance, historic development patterns and whether the vacant parcel was up for sale at the time. The absence of pre-trends in the pre-reform period provides a useful test of these assumptions. Finally, the announced policy reform reduced the return to waiting by an amount exogenous to the rent growth, which provides variation in timing of the investment. A simple model of investment under uncertainty confirms that the investment decision at the deadline depends on the distribution of expected future return, current rents, and the cost distribution, all of which are accounted for in the proposed empirical strategy. The instrumental variable estimate suggests than an additional tax-exempt unit within a 150 meter radius of an existing rental building in the time notch increased its rent by 2.3 log points. Expressed in elasticity terms, a 1% increase in the rental stock within 150 meters from existing buildings increased their rents by 1.8%. Moreover, in the pre-reform period, trends in rents of buildings with no vacant parcel within 150 meters do not differ significantly from trends in rents of buildings with an available vacant parcel within the same distance. This lends support to the

105 exogeneity assumption. Additionally, price changes in exclusion regions corroborate this finding: Compared with non-exclusion regions, the sales price of owner-occupied homes, land, and commercial rents in exclusion regions increased after the reform. Similarly, differences in spatial regression discontinuity at the boundary of the exclusion region support the finding that rents increased in regions that received new tax-exempt residential investment in this period. Having established that new tax-exempt construction increased nearby rents, I then show that the increase in business amenities such as restaurants and cafes explain this finding. While a larger rental stock in a neighborhood puts downward pressure on existing buildings’ rents, it also makes neighborhood more desirable. This is because new units attract high-income tenants, since at any point of time, new units have depreciated less than older units.6 These high-income tenants increase demand for local goods and services, which facilitates the entry of businesses. The arrival of these business amenities renders neighborhoods more desirable and increases rents in existing buildings. Note that this business activity channel is in addition to the direct aesthetic effects of new construction. For instance, research has shown that foreclosures have negative spillovers to the sales prices of existing homes (Anenberg and Kung (2014); Campbell et al. (2011)), and subsidized homeownership programs (Ellen et al. (2001)), eliminating rent control (Autor et al. (2014)), widespread simultaneous reconstruction due to fires (Hornbeck and Keniston (2017)) have been shown to have positive spillover on the prices of nearby properties. I find several pieces of evidence consistent with the business amenity hypothesis. First, using the number of vacant parcels at the baseline as an instrument and census data, I find significant demographic changes in census tracts that received new residential investment in the period following the tax reform. An additional tax-exempt residential project in a census tract increased the number of tenants who have a bachelor’s degree, are white, and have higher income. With respect to businesses, I find that there is an increase in the number of sidewalk cafes (associated with high-income customers) and a decrease in laundromats (associated with low-income customers)

6Sweeney (1974) develops a commodity hierarchy model in which a consumer faces a choice between quality and quantity, and the population growth leads to the construction of high-quality units for high-income residents. In the long run, new units filter down to low-income users as they depreciate.Rosenthal (2014) provides empirical support for filtering in rental units. However, he does not find evidence of filtering in owner-occupied homes.

106 in the exclusion regions in Brooklyn after the reform. This change coincides with a large new residential investment in the exclusion regions in Brooklyn during the reform period. Similarly, using city-wide Zip code-level establishment counts data, I find that larger residential investment in a Zip code increased the number of establishments in industries with high income elasticity. The industry-level income elasticities indicate the propensity of an industry to locate in a high-income zipcode. In conclusion, my results suggest that while residential investment responds to the property tax exemption, local price effects of the new investment do not necessarily mirror aggregate effects. However, there are a few considerations regarding the external validity of these results. First, it is plausible that the effects would be different if the new investment arrived slowly or in regions with low density. Second, I do not estimate general equilibrium effects, if any. For instance, it is plausible that rents fell in the neighborhoods the tenants of new units came from. Third, the estimated effect is a lower bound to the actual effect, given that a substantial number of apartments in the city are subject to rent stabilization. Fourth, while the results in this paper estimate short run elasticities, they do not shed light on how the mechanisms would differ in the long run for instance, in response to unanticipated permanent property tax increases. Nevertheless, my paper’s findings that new construction has differential local welfare effects help explain the puzzle why incumbent residents often oppose new development. My paper makes three main contributions. First, it provides first empirical evidence that new residential investment leads to gentrification. Causal evidence on the determinants of gentrification is limited. Authors have suggested that endogenous amenities (Diamond (2016)); rising top income inequality (Couture et al. (2019)); aggregate demand (Gyourko et al. (2013)); longer work hours (Edlund et al. (2016)); and pioneer businesses (Behrens et al. (2018)) could potentially be contributors to the rising gentrification in cities. Regarding the consequences of gentrification, Dragan et al. (2019) find no effect of gentrification on low-income mobility, though slight health improvements in children who grow up in gentrifying neighborhoods. Moreover, my paper shows that though new residential investment invigorates neighborhoods and increases the revenue base,

107 it comes at the welfare cost of existing tenants if they do not value such amenities. Back-of-the- envelope calculations reveal that annual welfare loss to local low-income households is $524 per unit, welfare gains to local building owners is $1,050, and the city government gains $157 additional property tax revenue, as a result of spillovers from new housing construction. Low-income housing construction (Nathanson (2019)) and the concentration of richer households in downtown neighborhoods (Couture et al. (2019)) have been shown to have welfare costs for low-income households in the presence of endogenous amenities.7 Second, my paper finds that a property tax break for new residential investment stimulates housing supply, which suggests that tax policy is a determinant of housing supply. Authors have identified regulation (Gyourko and Molloy (2014); Quigley and Raphael (2005)) and buildable land (Saiz (2010)) as key constraints that deter housing supply increases from keeping pace with rising demand in cities. While others have estimated the price/rent elasticity of investment (Case and Shiller (1989); Topel and Rosen (1988); Green et al. (2005); Meese and Wallace (1994); Glaeser, Gyourko, and Saiz (2008); Saiz (2010)), my paper estimates this elasticity with respect to the future property tax in a quasi-experimental setting. Third, in addition to estimating the effect of property taxes on rental prices, my paper provides empirical evidence that changes in amenities, such as the entry of businesses, have consequences for who bears the tax burden. 8 9 Though a vast literature in public finance investigates the effect of general property taxes on house prices (e.g., Oates (1969)) and renters (e.g., Orr (1968); Carroll and Yinger (1994)), finding causal estimates is challenging. Some reasons include the lack of experimental variation in tax cuts and unavailability of comparable city-level property tax rates

7A recent paper by Li (2019) uses a similar dataset from New York City. She finds that rents in existing buildings decline after the completion of a new high-rise within 500 feet. My paper does not restrict the sample to high-rise buildings and estimates the rent effects at the announcement of new construction. Consistent with her finding, I find that the rents decline post-completion, but this decline does not compensate for the initial rent increase. 8Some papers that study the disrtibutional effects of amenity changes include Albouy and Staurt (2016); Albouy and Zabek (2016). See England (2016) for a survey of empirical papers that estimate the relationship between property taxes and rents. 9Even doing a simple cross-section OLS is not trivial. An extended panel of city-level rents is challenging to obtain, and there is no dataset of effective city-wide tax on rental properties across the US. Surveys such as AHS report property tax for owner-occupied homes but not for renter-occupied units. I circumvent these issues by performing a within-city analysis. All rental properties face the same marginal tax rate. Moreover, assessed valuations proxy net rental income of landlords.

108 and rents data. Loffler and Siegloch (2018) make progress in this regard and find that in Germany the property tax is entirely shifted to renters in the long run. Additionally, my paper adds to a burgeoning literature in public finance which investigates taxes in the housing market in empirical settings using microdata (Kopczuk and Munroe (2015); Best and Kleven (2018); Slemrod et al. (2017); Dachis et al. (2011); Besley et al. (2014)). The paper is organized as follows. Section 3.1 describes the property tax reform and the datasets used in the study. Section 3.2 estimates the excess housing starts triggered by the tax reform. Section 3.3 describes and implements the empirical strategies to estimate the local rent effects of new residential investment. Section 3.4 explores the mechanisms. Section 3.5 provides back-of-the-envelope calculations of welfare effects. Section 3.6 concludes.

3.1 Background and data

3.1.1 Property tax reform in New York City

The key change in the property tax on new residential investment in New York City was caused by the 2006 reform of a tax policy called “421a" for the section of New York Real Property Tax law, that exempts developers of new construction from property taxes. Generally, new construction increases the assessed valuation, which increases tax payments even when the tax rates are unchanged. In contrast, the 421a property tax exemption provides tax relief for new investment by restoring the assessment to preconstruction value.10 All new project starts on “underutilized" land with at least three or four proposed units are generally eligible for the exemption 11, which is the single most extensive tax expenditure program in New York City. In 2015, foregone taxes on exempt units cost the city $1.1 billion and represented 15% of all tax expenditures of the city. The property tax is a signiﬁcant cost for new residential investment. The statutory property tax rate on a rental building with at least 10 units in New York is around 5.5%. The “rate" here

10This does not imply that the post-construction tax liability is zero. If the assessed value of the existing structure is nonzero, then the tax liability is most likely positive. 421a Tax Exemption prevents steep increases in property taxes due to large increments in assessed value because of construction. 11§6-02 of Title 28 of the Rules of the City of New York [link].

109 is defined as a fraction of the annual market valuation, as opposed to annual rental income.12 This is because the property tax is supposed to be a tax on the capitalized income and not actual annual income. I show, in Appendix B.2, that as a share of annual rental income, property tax costs are much larger. For instance, a 5.5% tax on annual market valuation is equivalent to a tax rate of 33% on annual gross rental income. An exemption that reduces the tax bill, therefore, is attractive. Because city governments across the United States use varied approaches to impute market valuation of rental properties, in this paper I report tax elasticities as measured responses to changes in the statutory tax rate on market valuation (5.5%) as opposed to actual rental income (33%).13 The Department of Finance’s market valuation serves as a good proxy for the income of large rental buildings. This is because annual market valuation for a given fiscal year is based on net operating income minus expenses times a capitalization factor. Information on rental incomes and expenses is collected through the mandatory filing of Real Property Income and Expense (RPIE) reports by large rental building owners each year.14 For a more detailed description of the administration of property tax in New York City, refer to Section B.2. The program originated in 1971, when New York City was suffering from steep economic and physical decline. People fled to the suburbs as manufacturing and housing quality declined in the city. In response, the state legislature enacted the 421a Real Property Tax Exemption in 1971 to stimulate new multi-family housing development. Between 1971 and 1984, around 30% of construction claimed 421a exemption (Report (2014)). The program continues to be popular; Figure 3.31 shows that more than half of the units built each year between 2001 and 2012 claimed the tax exemption. The property tax exemption stimulates investment by increasing the net of tax return. This occurs through two channels. First, the availability of the tax exemption directly lowers the tax liability for a significant period, which increases the return to new investment. Second, there is

12Property owners are also subject to an income tax, either corporate or individual. 13The use of the term “annual market valuation" in this paper refers to the value as assessed by the Department of Finance for taxation purposes, as opposed to the actual sale value of the property on the market. 14A “Large" rental building contains at least 10 residential units.

110 evidence that developers often face liquidity constraints.15 The increased market valuation of the proposed project on receipt of the tax exemption can help developers to raise capital and build more.16 There are also several reasons why a developer does not apply for the exemption. First, if the project is located in the “exclusion regions" as discussed next, mandatory provision of affordable units adds significant costs for the developer. Second, even when developers are not required to provide affordable units, non affordable units in the project are subject to rent stabilization and maximal rent (Cohen (2009)). Third, project starts on land that previously contained an income- producing property are not eligible for the exemption. Finally, projects with at least three or four residential units are eligible for the tax break, which effectively limits the tax break to condos and rental buildings. The 2006 reform expanded the existing exclusion regions i.e., regions with restricted property tax benefits thereby reducing generosity of the tax benefits in key neighborhoods. Table 3.1 summarizes key changes in the three regions. It discontinued the offsite provision of affordable units in existing exclusion regions (light blue shaded region in Figure 3.1). Before the reform, developers in these regions were required to provide affordable housing to obtain the exemption.17 Because these were high-rent regions, developers could save costs by providing affordable housing in offsite low-rent regions. After the reform, developers were required to provide affordable housing onsite. I estimate, in Appendix B.3, that removal of the offsite option increased developers’ costs equal to a property tax rate increase of 2.3 pp.18

15Topel and Rosen (1988) document the high volatility of housing starts. Stein (1995) suggests the liquidity constraints faced by developers as a possible explanation. Higher wait times constrain the start of new projects, as developers must sell the current project to obtain cash for the next project, and resort to a “fishing for liquidity" strategy. 16Best and Kleven (2018) provide similar evidence for highly leveraged homeowners. A cut in transaction taxes eases borrowing constraints for such homeowners and increases trade of existing housing stock. Zwick and Mahon (2017) show that financially constrained firms respond more to a tax stimulus than financially unconstrained firms. 17Affordable units are restricted to households with 30% to 100% of the area median income (AMI), with a rent limit at 30% of the income of the tenants in the affordable units. AMI is calculated each year by the U.S. Department of Housing and Urban Development (HUD). The 2017 AMI for NYC was $85,900 for a three-person family, constant across all regions within the metropolitan area. 18Earlier, the developers could fulfil this option by providing affordable units offsite in low-rent regions. This was achieved through the use of a negotiable certificate program. Under the negotiable certificate program, affordable housing developers receive 4 to 5 certificates for each unit they produce, which then can be sold to market-rate developers.

111 After the reform, in the newly added exclusion regions (unshaded dark blue regions), developers could no longer opt for the short exemption—-a 15-year property tax exemption without any affordability requirement. As I show in Appendix B.3, in low-rent neighborhoods where providing affordable units onsite is inexpensive, the reform largely did not alter tax incentives. In contrast, in high rent neighborhoods within the newly excluded regions, the reform took away the tax benefit by increasing the costs associated with the property tax exemption. This suggests that depending on the project location, either the reform did not affect tax liability or it increased the tax rate, ranging from 0 to 5.5%.19 Elsewhere in the city, in general, the reform largely did not affect the tax incentives. This is because low rents in these regions made onsite affordable units inexpensive, and the reform did not affect its benefits significantly. The short 15 year exemption without affordable housing condition continued to exist, but its benefits were capped. Specifically, a citywide cap of $65,000 per unit was imposed on units with a 15-year exemption.20 Because a developer could obtain a 25-year exemption at practically no cost before and after the reform, the tax change in this region was minimal. Finally, the reform introduced more changes that were applicable everywhere. First, the minimum number of units in the project to be eligible for the exemption was increased from three to four. Second, conditions attached to affordable units in buildings with the 25-year exemption were made stricter. All affordable units were rent stabilized for 35 years. Also, affordable units were required to have either the number of bedrooms comparable to market-rate units or a specified mix.

The time notch

The time notch arose from the delay in implementation of the tax change. In February 2006, discussions to reform the exemption policy began with the creation of a task force that identiﬁed

19Even in high-rent regions, it is possible that developer prefers an onsite long exemption. This is the case when the same set of affordable units allows a developer to fulﬁll affordability requirements for multiple state support programs such as 421a, LIHTC, and Mitchell-Llama. This is referred to as “double dipping." This could also explain why we observe nonzero response in long 25-year exemption in newly excluded regions. In such a case, removal of a short 10-year exemption would have no effect on the effective tax rate. 20The annual tax beneﬁt for a 15-year exemption was capped at [tax rate × 65,000]per unit.

112 additional regions to be included in exclusion regions.21 The task force submitted the final report to the City Council in October 2006. However, the proposal faced political resistance. Both the city and the state legislature added more regions. Figure 3.30 shows the initial regions picked by the task force (shown in red) and the regions added by the city council (blue) and state legislature (yellow). The mayor signed the local law on Dec. 28, 2006, and the legislature expanded/amended the local law. The final version of the new 421a law was signed by the governor on February 19, 2008. I refer to the period between December 2006 and June 2008 as the time notch, where the “notch" arises from the fact that investment in the notch period is associated with a strictly higher property tax, compared to investment after the notch period. A developer who obtained a permit, or installed a metal or concrete load-bearing structure before July 2008 was eligible for exemption benefits under the old law. Figure 3.32 outlines the key steps a developer must go through before obtaining the permit.

3.1.2 Data

I collected and organized several datasets from city government agencies. Detailed information on the sources of these datasets can be found in Appendix B.1. Here I provide a brief summary of the datasets used in this paper:

1. Rents: MapPLUTO provides geo-coded location and details about the structures on each parcel in the city. Each parcel is identified using a unique identification number called the BBL (Borough, Block, Lot). Along with the building classification, and number of residential and commercial units, this dataset provides information on the actual assessed value (equal to the assessment ratio times the market valuation). As discussed in Section B.2, the market valuation of rental buildings serves as a proxy for their rental income.

2. Permits data: An important measure of the ﬂow of residential investment is the issuance of

21To identify such neighborhoods, the task force calculated the return to developers for each neighborhood and building type, using land acquisition cost, hard construction costs, and sale prices. This analysis was carried out with and without the exemption. The task force picked regions where the sales price covered costs without the exemption (see OMB (2008)).

113 permits for new construction. The Department of Buildings provides data on the universe of permits issued at a monthly level from 2003. The type of permit depends on the nature of alteration sought. Relevant permit types for new construction are DM (demolition), NB (New Building) and A1 (major alteration that changes occupancy of the building). Each permit is linked to a building identiﬁcation number (BIN). I use the BIN and a crosswalk between the BIN and the BBL provided by the property address directory to merge this dataset with MapPLUTO. See Figure B.1 for an explanation of the relationship between the BIN and the BBL.

3. 421a beneficiaries: Buildings/units that benefit from a 421a tax exemption are identified through their BBL using 421a lists provided by Department of Finance. While these lists are exhaustive, they do not identify whether the beneficiary obtains a 10-year or a 15-year exemption. For this reason, I use 2015 property tax returns of owners residing in these buildings to obtain the type of exemption claimed.

4. Selling price: The Department of Finance provides information on sale date, sale price, and characteristics of the property for every arms-length transaction in the city. The sample period covers 2003-2018. This dataset is merged with other datasets using BBL to identify the effects on landowners and developers.

5. Demographics data: The Census 2000, and the 2009 and 2017 Americal Community surveys provide information about homeownership, tenure, race, rent, and income at the census tract level. New York City has 2,168 census tracts in total.

6. Local businesses: I use two main datasets to estimate the effects on business activity.

(a) Department of Consumer Affairs license dataset: New York City requires certain businesses to apply for a DCA (Department of Consumer affairs) license. This includes businesses such as sidewalk cafes, laundries, and home improvement contracts. This dataset provides information on license creation date and the geocoded location of the

114 business. Because it covers a fraction of the industries that operate in the city, I complement the analysis with the Zip code-level business counts dataset as described below.

(b) County Business Patterns data: This dataset provides information on the number of establishments by industry-Zip code-year. New York City contains approximately 200 Zip codes. Counts are available at the 6-digit NAICS industry level.

3.2 The time notch and residential investment

Because the increase in property taxes on new residential investment in 2008 was known in advance by developers, this created incentives to move their investments ahead in time. In this section, I use a simple framework to show that with the uncertainty and irreversability of investment, an increase in the future property tax stimulates current residential investment by reducing the return to waiting. The forward movement of investment provides exogenous variation in the arrival time of new projects, which is useful for estimating their local price effects. As a by-product, the excess bunching in exclusion regions provides an estimate of the timing elasticity of residential investment with respect to the property tax. Consider the case in which the investment decision for developers is characterized by irre- versibility and uncertainty in future return (Dixit and Pindyck (1994)). If things go badly, developers can not destroy the building and fully recover the initial cost of investment. This implies that the decision to invest in any period is equivalent to exercising an option. Each period, developers choose to invest or wait, given the uncertainty in future returns. Waiting is proﬁtable when developers expect future prices to be higher. In contrast, a future increase in the property tax stimulates current investment by decreasing the return to waiting. Consider two periods: today and tomorrow

j ∈ {0,1}. Developers decide in period 0 whether to invest today or tomorrow. Assume the period

0 capitalized return is known to be R0. Next period return is distributed according to function G(R˜). Period 1 returns are discounted at the rate β.

22 A developer i has perfect knowledge of investment cost Ci. These costs are heterogeneous

22These costs could include the costs of acquiring land and/or the cost of materials and labor.

115 across developers, distributed according to a cumulative distribution function F(·). 23 With no time

notch and no property tax, a developer i invests in period 0 if (i) the net present value of investing today is greater than the net present value from investing tomorrow; and (ii) the capitalized current

return R0 is greater than costs Ci. If he invests today, his return is R0 −Ci. If he waits till tomorrow,

he can expect a return of βEG max(R˜ − Ci,0). Clearly he invests in period 0 when

R0 − Ci > βEG max(R˜ − Ci,0) (3.1)

R0 − Ci > 0.

For developers with a period 0 return lower that the cost, the period 0 vs 1 investment trade-off is trivial and their period 0 investment does not respond to any changes in the distribution of period

1 return. This is because when R0 − Ci < 0, investment condition requires βEG max(R˜ − Ci,0) <

R0 − Ci, which is less than 0. For other developers, the decision to invest today is a function of (i)

investment cost Ci; (ii) distribution of period 1 returns G(·); and (iii) discount factor β.

When β < 1, there exists a k˜ that satisﬁes equation 3.1 such that when Ci < k˜, developer i

24 invests in period 0. It is easy to see that k˜ is a function of R0, β and the distribution of period 1 return G(·). A higher return in period 0 makes it worthwhile for developers to invest in period

0. When R0 increases, k˜ decreases. With a higher β, developers are patient and willing to wait till period 1 to reap any future rewards. When β increases, the right-hand side increases and k˜ falls. Therefore, period 0 investment falls. Finally, a higher mean in period 1 return lowers period 0 investment. For instance, an increase in period 1 mean increases the right-hand side of equation 3.1 and lowers k˜. This reduces period 0 investment. Similarly, a mean-preserving spread that increases the variance in R˜ reduces period 0 investment by lowering k˜. This is because with a

23It is reasonable to assume that land and zoning regulations (Gyourko and Molloy (2014)) and geographical constraints (Saiz (2010)) affect the cost distribution. For instance, we can imagine that zoning regulations make the variance of the probability distribution low. Only a few low-cost developers are able to invest when most developers have high costs. 24When β < 1, the slope of the convex function on the right hand side is less than 1, whereas the left hand side is a linear function with slope 1.

116 higher variance, larger R˜ values are more likely and waiting is worth more. The total period 0 investment is given by

N Õ I(0) = 1(Ci < R0&Ci < k˜) i=1

= NF(min(R0, k˜)).

The time notch introduced a property tax t on period 1 return, which implies that the devel- R˜ ˜ opers’ net of tax period 1 return falls to 1+t should they choose to wait. This increases k, and therefore the period 0 investment. Investment with a tax is given by

I(t) = NF(min(R0, k˜t)), where k˜t > k˜, and therefore I(t) ≥ I(0). The increase in period 0 investment corresponds to the excess bunching in the time notch.

B = I(0) − I(t) = NF(min(R0, k˜t)) − NF(min(R0, k˜)). (3.2)

If we normalize quantity 3.2 with I(0) and the property tax change t, we obtain the timing elasticity of investment with respect to the property tax. The reduced form estimate is given by

Bˆ t = (3.3) I(0)t where Bˆ represents the empirical estimate of excess bunching in the notch period.25 It is important to distinguish two kinds of elasticities: timing elasticity, which is the response of current investment to future increase in property tax, and long-run or contemporaneous elasticity, which is the

25Instead, if we normalize by housing starts, we obtain the property tax elasticity of housing starts:

Bˆ p = P0(0)t

where P(0) denotes counterfactual starts in the notch period.

117 response of long-run investment to a permanent property tax increase, given by

0 ∆I R0 F(R0) − F( ) l = I = 1+t , (3.4) t ∆t t F(R0) 0 where R0 is the equilibrium tax-inclusive rent with a nonzero property tax. In general, elasticities 3.3 and 3.4 are not equal. Unfortunately, while the reform sheds light on the timing elasticity, it does not inform the long-run rent elasticity. Nevertheless, to the extent that short-term increases in investment can stimulate the local economy, timing elasticity is a crucial parameter for empirical estimation. 26

3.2.1 Anticipated tax increase and short term outcomes

The time notch is equivalent to an anticipated permanent property tax increase. This implies that the trajectory of the outcomes in the short term differ when the tax increase is anticipated, compared with the case when not. Here I provide a simple intuition. Refer to Appendix B.4 for a simple framework. Figure 3.4c illustrates the time path of rents and investment in two scenarios: (i) Policy 1, in which the permanent tax increase is unanticipated; and (ii) Policy 2, where the same tax increase is anticipated. The long-run decline in investment and net-of-tax rent is equal in the two scenerios. However, the short term outcomes differ starkly. Investement quickly drops to long-run value at the policy implementation in the unanticipated tax increase case (Panel a), whereas it increases in the time notch in the anticipated tax increase case as developers move investment forward. Similarly, net of tax rents fall following the announcement (and implementation) in the unanticipated case, but increase over time as future investment falls and landlords are able to shift some of the tax burden onto tenants. In contrast, in the anticipated case, the bunching of investment in the time notch

1 increases net rents received by landlords when amenities are sufﬁciently elastic (i.e. a > 1 + .). t Rents slowly begin to approach the long-run equilibrium once the high tax rate is implemented.

26Please refer to Saiz (2010); Mayer and Somerville (2000); and Green et al. (2005) for an estimation of the rent (price) elasticity of investment.

118 Two points are worth noting. First, while the results in this paper do not inform long-term outcomes, they highlight the role of endogenous amenities in the incidence of the property tax: short-term increase in investment increases local prices. Second, when depreciation is low, the

period up to T0 is long. This implies that there is an extended period in which the net of tax rents are high despite a higher property tax. The government beneﬁts in this period from larger revenues stemming from a larger property tax base and economic activity.

3.2.2 Estimating excess housing starts in the time notch

This section uses a bunching framework to estimate excess tax-exempt housing starts in the time notch. I also provide estimates of timing elasticity of residential investment with respect to the property tax. The Housing Type

New York City offers a wide array of housing types. These include rental units, which consti- tute buildings of types C (walk-ups) and D (buildings with elevator), and owner-occupied condos and coops, classiﬁed as type R and family homes. However, the 421a property tax exemption only applies to rentals and condos. As Figure 3.35 illustrates, both types are fairly popular with the exemption. Because we can expect that tenants care about the stock of rental housing available at a point in time, the relevant policy parameter to estimate is the rental housing starts/investment elasticity. Therefore, this paper focuses on the rental investment response. 27 Nevertheless, note that the response of condo starts in the notch period was not insigniﬁcant. They account for one-third of total starts in the notch period. The Counterfactual

Standard bunching estimation in public ﬁnance deals with notches in income distribution (Saez (2010); Chetty et al. (2011)) or price distribution (Kopczuk and Munroe (2015)). Bunching estimates are calculated as the difference between the actual distribution and the counterfactual in 27In all bunching graphs, I plot the response of investment in rental units, which includes permits for building types C and D. Figure 3.34 shows bunching results including condos. The estimation is less clean due to a clearly preexisting rising trend in condo starts.

119 the notch region (or time in the context of my paper). Similarly, the difference between the actual distribution and the counterfactual to the right of the notch region is the missing mass. A key input in the calculation of excess bunching and missing mass estimates is choice of counterfactual. One choice is a high-degree polynomial fit of the actual distribution that uses data outside the notch region. Estimation using this approach is sensitive to the choice of upper bound and lower bound, in addition to the choice of the degree of the polynomial (Kleven et al. (2011)). An issue with ex- tending this methodology to time notch is that this counterfactual does not account for any global time shocks during the time notch. Therefore, similar to Best and Kleven (2018) and Kopczuk and Munroe (2015), I use an empirical counterfactual. Specifically, I pick a comparison group whose housing starts time series serves as the counterfactual for tax-exempt housing starts. The lower bound is fixed at the announcement date. I choose non-tax-exempt housing starts in exclusion regions as the comparison group, instead of housing starts in the non-exclusion region (either tax-exempt or non-tax-exempt), for two reasons: (i) it ensures that actual and counterfactual distributions represent the same geographic area; and; ii) it helps to alleviate concern that the recession, which started in 2007, had differential effects on housing starts in the exclusion and non-exclusion regions. Aggregates are sensitive to the magnitude of the shock, therefore using housing starts in non-exclusion regions could overstate the bunching observed in the exclusion region, for instance, if the recession had a larger impact on housing starts in the non-exclusion regions. For instance, Figure 3.41 plots the spatial distribution of foreclosures in the city in 2008. Foreclosures are concentrated in non-exclusion regions. The identification assumption is that in the absence of the time notch, trends in aggregate tax-exempt housing starts are parallel to non-tax-exempt starts within the exclusion regions.

3.2.3 Bunching results

Figure 3.5 plots the quarterly number of tax-exempt permits issued in New York City in the raw data, split by exclusion and non-exclusion regions. Dotted green lines indicate the quarter-year when changes to the policy were announced and implemented. The graph uses permits data from

120 Department of Buildings merged with 421a exemption lists to identify completed tax-exempt units. The time stamp in the permits data indicates the date the permit for construction of a new building was issued. A key thing to note is that these do not include actual tax-exemption applications. If some developers intended to apply for the property tax exemption but failed to obtain approval, or if they proved the eligibility of "commencement of construction" requirement by installing new metal or concrete structure instead, the bunching estimates would underestimate the actual response. Figure 3.6 shows the spatial distribution of tax-exempt non-condo projects. The top panel presents the distribution for the period, 2005q2 to 2006q4,which is the same length as the time notch. Each project is weighed by number of the residential units. The top panel shows that the tax-exempt projects in Manhattan tend to be fewer but bigger. However, there is no speciﬁc spatial pattern in the pre-notch period. In contrast, the bottom panel shows that more and larger tax-exempt projects are started in exclusion regions in time notch, and Manhattan and Brooklyn in particular. This is consistent with the concentration of residential investment in exclusion regions in the time notch. To see what exemption type developers sought, Figure 3.33 splits the bunching by exemption type, separately for exclusion and non-exclusion regions. As expected, the largest spike occurs for short exemptions in the exclusion region; this exemption provides a 15-year beneﬁt without a requirement to provide affordable housing. There is also a smaller spike in the long 25-year exemption preceding the 2008q2 spike, which is driven by removal of the offsite long exemption in old-exclusion regions (shaded regions). Figure 3.7 plots tax-exempt housing starts in each borough in this time period. We see that Manhattan, Brooklyn, and Queens see sharp increases in housing starts that are not completely reversed post-reform, despite the start of the recession in 2008.28 The magnitude of bunching varies across boroughs. Finally, estimates of bunching are higher by 80% if we include the response of tax-exempt condo starts (Figure 3.34). Comparing 3.7 and 3.34 suggests that a large share of condo starts in the time notch were concentrated in Manhattan and Brooklyn. The magnitude of bunching in the number of tax-exempt units uncovers the elasticity of the

28I exclude Staten Island, because it largely consists of family homes. Correspondingly, housing starts for type C or D buildings (rental) are small and noisy.

121 current residential investment to future increase in the property tax. The empirical analog of equation 3.3 can be estimated as follows:

Í2008 ( ftax_exempt − fc f ) ˆt = 2006 , (3.5) ∆t 2007 1+t S where the numerator, Excess bunching, is calculated as the difference in the quarterly distribution

of tax-exempt rental units starts, ftax_exempt, and the counterfactual, fc f , in the notch period. The excess bunching estimate is divided by the existing housing stock in 2007 in the exclusion region to obtain percentage change in housing supply due to the time notch. It is then further divided by the percentage change in the (one-plus) property tax rate to obtain the elasticity, which was equivalent to 2.5 percentage points; this is the average property tax rate change caused by the reform. Note that these estimates capture elasticity with respect to the tax rate on the market valuation rather than annual rental income. I estimate the numerator by running a simple regression on the counts data of the following form:

ct = β0 + γt + β1(Tax_E xempt)t × Notcht + β2(Tax_E xempt)t + t

where t denotes the quarter, ct denotes aggregate quarterly starts in the quarter t, and (Tax_E xempt)t indicates the total tax-exempt housing starts in quarter t. The omitted dummy is the indicator for the counterfactual, which in this case includes non-tax-exempt housing starts. β1 provides an estimate of the average per-quarter excess bunching in the time notch, which is scaled by 7, to estimate the total bunching observed in the time notch. (The time notch includes Dec q4 to June q2, a total of 7 quarters.) Figure 3.7 reports the excess bunching estimates for the exclusion regions in New York City, using non-tax-exempt housing starts as the counterfactual. We observe that while the two distributions are fairly parallel in the pre-reform period, there is a large spike at the notch, for both tax-exempt units (the left panel) and tax-exempt buildings (the right panel). Reassuringly, there is no spike in non-tax-exempt starts, which supports the assumption of an absence of regional non-

122 tax-exempt-related shocks in the exclusion regions in this period. Overall, construction of around 10,735 tax-exempt units and 270 buildings began in the exclusion regions in the time notch. Fig- ure 3.8 reports the distribution of excess bunching estimates across the four boroughs (Manhattan, Brooklyn, Queens, and the Bronx). Table 3.5 summarizes excess housing starts in the time notch citywide and by borough. Excess housing starts in the time notch correspond to 1% of the city’s rental housing stock in 2007. There is substantial variation in relative housing starts across boroughs. Manhattan had approximately 3,000 excess housing starts, Brooklyn 5,000, Bronx 200, and Queens 2,500. These correspond, respectively, to approximately 0.4%, 2.1%, 0.8% and 6.8% of the existing rental housing stock in the region. While the differential excess housing starts across boroughs could reﬂect borough- wide differences in tax elasticities, they also partially reﬂect borough-wide differences in shock intensity.29 Nevertheless, the estimates suggest that the housing supply is inelastic with respect to the property tax rate. Assuming that the excess housing starts in the time notch are in response to

1 a property tax increase of 2.5%, we obtain an elasticity of 2.5 = 0.4. Specifically, a 1% increase in the future property rate for new housing increases current residential investment by about 0.4% in New York City. The first concern in the excess starts estimation is the possibility that developers substituted from non-tax-exempt to tax-exempt housing in the time notch. In such a case, using non-tax- exempt starts as a counterfactual leads to overestimation of true excess bunching. To alleviate this concern, I check robustness with respect to alternative distributions as counterfactual. Estimates are fairly robust when I use either housing starts in non-exclusion regions (Figure 3.42), or ineligible and non-housing starts in exclusion regions as the counterfactual (Figure 3.43).30 In either case, the excess bunching estimate is close to 10,500 tax-exempt units. The second concern relates to the time to completion of the proposed projects. While the bunching estimates only include units that were finished by 2015, it is nevertheless possible that

29Recall that the tax reform made it mandatory to provide affordable housing onsite, the cost of which depends on rents that vary across neighborhoods. 30These include commercial and family homes.

123 the tax-exempt units were not completed in a timely fashion. This is even more relevant because the recession started in 2008. As a matter of fact, a rule change in 2013 extended the "undue delay" period from 36 months to 72 months for projects that were subject to mortgage foreclosure or other lien enforcement litigation before May 14, 2012.31 To address this concern, Figure 3.36 uses the PLUTO data to identify completion year of buildings started in the time notch. While a large share of the buildings finished by 2009, a small share of projects took more than three years to finish. The excess housing starts observed in the time notch had significant effects on the magnitude and composition of housing stock in the exclusion regions. The reform increased the concentration of new tax-exempt investment. This has two effects. First, it implies that a greater share of housing in the exclusion regions is newer. Second, because most of the new housing stock benefits from the property tax exemption, the effective tax on these new units is lower. For instance, the top right panel in Figure 3.26 depicts the effect of the time notch in Brooklyn, a region that will be useful for investigating mechanisms later. Dashed lines denote the stock of units built after 1990 in the exclusion and non-exclusion regions within Brooklyn. Thin lines denote the stock of tax- exempt units in either region. We see that the stock of new tax-exempt units increased sharply in the exclusion regions after 2006, which coincides with the investment shock in the time notch. Finally, Figure 3.9 shows that the increases in the total housing starts in the exclusion regions are not immediately reversed after the time-notch.

3.3 Effect of new residential investment on rents

We are interested in estimating the effect of a tax-exempt project arrival within a small distance from an existing building on its rents. Consider rings of a ﬁxed radius of 150 meters around an existing rental building.32 A naive estimation is to compare the rent growth of buildings that receive tax-exempt projects within that radius with buildings that do not. A concern with this approach is that the location of new investment is likely endogenous to trends in building rents. On the one hand, a developer is more likely to build near a building where he expects higher future

31See §11-245.1 of Title 2, New York City Administrative code. 32An average block in New York City is between 150 and 250 meters.

124 rents (such as gentrifying neighborhoods), leading to a positive bias in the OLS estimation. On the other hand, a high expected rent growth increases the land acquisition cost and therefore reduces the probability that an expensive rental building receives a tax-exempt project close by. This leads to a negative bias in the OLS estimation. In either case, whether a building receives a tax-exempt project nearby is plausibly endogenous to its rent growth. The property tax reform and the setting provide key sources of exogenous variation in project arrival in both location and time. While the time notch provides exogenous variation in the time of project arrival, the availability of vacant land within a small distance from an existing building provides exogenous variation in project location (an instrument similar to that of Saiz (2010)). The idea is to compare the rent growth of buildings that had a positive number of vacant parcels within a small distance with that of the buildings that had no vacant parcels within the same distance. When the availability of vacant parcels acts as a constraint on investment, buildings with a larger number of vacant parcels receive more tax-exempt projects in the time notch. Figure 3.10 illustrates the empirical strategy. In this case, the instrument—land vacancy at the baseline—turns on for buildings in Rings 1 and 4 and is turned off for others. The empirical approach implies that the instrumental variables estimate captures the effect of the arrival of a tax-exempt unit within 150 meters from the rental building. The "reduced-form" captures the difference in the average rent growth of buildings in rings 2 and 3 (which are more affected by the tax reform) and the rent growth of buildings in rings 2 and 3 (which are less affected by the tax reform) before and after the reform. Identiﬁcation : The validity of the instrumental variables approach requires two main assumptions: exogeneity and the exclusion restriction. Exogeneity requires that the baseline availability of a vacant parcel within a small distance from a building is uncorrelated to its rent growth. The exclusion restriction requires that the baseline land availability does not directly affect the building’s rent growth. A way in which the exogeneity assumption would fail is when exactly those vacant parcels are undeveloped where developers expect lower future returns. This leads to a negative correlation between the baseline vacancy and the expected rent growth. Similarly, the exclusion

125 restriction fails when a positive number of vacant parcels at the baseline signals lower future rent growth in that neighborhood. This would be the case, for instance, when a positive land supply signals low neighborhood quality. 33 The empirical strategy I propose circumvents these issues in the following ways. First, the comparison of buildings within a small census tract broadly controls for trends in expected rent growth, which are common to all buildings within a census tract. This is achieved by inclusion of the census-tract times year fixed effects. 34 Second, the inclusion of building-fixed effects controls for any fixed unobserved neighborhood differences across buildings within a census tract. Similarly, year fixed effects control for any rent trends common to all buildings within New York City. Third, the main specification is restricted to buildings that had at most one vacant parcel. This helps address the concern that buildings with a larger number of vacant parcels signal low future rent growth. Consequently, within a census tract, which buildings had a vacant parcel nearby is an outcome of historic development patterns and whether a vacant parcel was up for sale, which I expect is outside developers’ control. Fourth, the time notch provides exogenous variation in the timing of project arrivals. As discussed earlier, the decision to invest in a vacant land is a function of the current rent, developers’ cost, and the expected return from investment in the parcel. In periods in which there is no notch, time-varying factors affect both the investment decision and expected rent growth. To the extent that the expected and the actual rent growth are correlated, investment and actual rent growth are also correlated. However, the time notch led to a decline in the expected return by an amount exogenous to the actual rent growth. This implies that after controlling for expected rent, current rent, and costs, the decision to invest in the time notch is uncorrelated with the actual rent growth. I perform two tests to check the validity of assumptions. First, a signaling mechanism predicts that the first stage is negative; that is, buildings with a vacant parcel receive a lower number of

33If buildings with positive land nearby differ from buildings with no land only in terms of ﬁxed unobserved characteristics, those differences are absorbed by the building ﬁxed effects. The assumptions are violated when unit land buildings differ from no-land buildings in terms of time-varying factors correlated with rent growth. 34There are on average 48 rental buildings in a census tract in New York City. This number varies across boroughs: 76 in Manhattan, 34 in the Bronx, 21 in Brooklyn, 18 in Queens, and 5 in Staten Island. A Zip code is larger and has on average 332 rental buildings.

126 tax-exempt units. The data do not support this. Figure 3.14b shows that if anything, a higher number of vacant parcels is associated with a higher number of tax-exempt projects in the time notch. Second, in the presence of signiﬁcant correlation between the baseline number of vacant parcels and rent growth, we expect rents in buildings with a unit land supply nearby to grow slower in the pre-reform period, compared with the buildings with no land nearby. An implication is an observable lack of parallel pre-trends in the event study graphs of rent growth on baseline land availability. Before presenting the results, I provide key summary statistics here.

3.3.1 Summary statistics

Figure 3.2 illustrates the distribution of the baseline 2007 total housing stock as reported in the PLUTO data. Each observation in the PLUTO data is a parcel, which refers to a piece of land containing one or more structures. Typically, a parcel in the city contains a building. Exclusion and non-exclusion regions together had around 3.3 million housing units, which is quite close to the official statistics reported in 2018 (Survey (2005)). Rental units form around 90% of the total units in the exclusion regions, but only one-half in non-exclusion regions. Family homes form a significant share of housing in non-exclusion regions. Table 3.2 illustrates the average differences between tax-exempt and non-tax-exempt parcels. For each variable, the first and second rows denote statistics for non-tax-exempt and tax-exempt projects, respectively. Because all exempt parcels have been developed in the past 15-25 years, for comparison purpose, I restrict the sample to parcels developed after 1990. The table shows that tax-exempt and non-tax-exempt projects differ significantly along many dimensions. Tax-exempt projects are slightly larger in terms of residential units, and square footage and lot size, and are more expensive, and more likely to be condos, and less likely to be located in a high-income region. In contrast, both are almost equally likely to be located in exclusion regions. Table 3.3 provides summary statistics for rental buildings in New York City in the PLUTO data in 2007, a year before the tax reform. Rental buildings are identified as those that have (i) more than 10 units and (ii) are classified C or D across all years in the sample period. Data are

127 truncated to include buildings with at least 10 units, because the market valuation of such buildings reflects their rental income. Exclusion and non-exclusion regions are far from comparable in terms of housing characteristics. First, exclusion regions are denser. An average lot in this region is small—around 11,000 square feet—and has, on average, one building that contains approximately 50 units. Non-exclusion regions, on the other hand, have almost the same number of residential (rental) units but are located on a lot more than two times the size of a lot in exclusion region. Housing stock, as measured by the number of residential units, is similar across the two regions. Second, the rents in exclusion region are high. Compared with an average per unit monthly rent of about $686 (USD 2015) in non-exclusion region, exclusion region rent is more than two times that amount. In either region, an average parcel contains one building. Table 3.4 illustrates the average differences in rental buildings in exclusion and non-exclusion regions within Brooklyn, which is useful when exploring the mechanisms in Section 3.4. Base- line differences in exclusion and non-exclusion regions are less pronounced within Brooklyn than within New York City overall. An average lot in exclusion region in Brooklyn has fewer units (44 compared to 57) and a smaller lot area. Monthly rent differences between exclusion and non-exclusion region in Brooklyn are only about $200, compared to $700 within New York City overall. Finally, Table 3.10 illustrates differences in the tax-exempt housing starts in the time-notch and the tax-exempt housing starts outside the time notch. The table suggests that the projects started in the time notch are larger in terms of building area, residential units and lot area, are more likely to locate in the high-income region,and are more expensive in terms of monthly rent. This is consistent with the fact that tax exemption makes it profitable to bring more expensive and larger projects ahead in time to benefit from generous benefits in the time notch.35

35Recall that the exemption applies to only new units constructed and excludes land.

128 3.3.2 Results: Effect of tax-exempt investment on rents

Figure 3.13 shows that a non signiﬁcant share of vacant parcels at the start (i.e. 2006), were converted into new tax-exempt projects in the time notch, suggesting that the baseline vacancy affects development. A key observation is that many tax-exempt project starts in the time notch occupied previously non-vacant parcels, despite the fact that the tax-exemption is restricted to vacant parcels. Zoning changes and lobbying sometimes allow developers to build on non-vacant parcels. Figures 3.14a and 3.14b show why the choice of a binary instrument—0 vs 1 vacant parcel—as opposed to a continuous variable that admits all values is a good idea. Figures 3.14a and 3.14b present the baseline number of vacant parcels within 150 meters from an existing rental building and mean tax-exempt projects in the time notch respectively. Two observations are worth noting. First, a majority of buildings in the city do not have a single vacant parcel available within 150 meters, consistent with the fact that New York City is fairly dense. Additionally, almost all buildings contained fewer than two parcels within 150 meters. Some 3% of buildings contained more than two vacant parcels. Second, Figure 3.14b reveals that the mean tax-exempt units received within 150 meters in the time notch jump drastically as the number of available vacant parcels increases from 0 to 1. This is equivalent to a supply shock of approximately 1%, given that an average building contained 97 rental units within 150 meters at the beginning of the reform. Figure 3.15 restricts the sample to buildings with at most one available vacant parcel within 150 meters. We see that the probability a building with a vacant parcel receives a tax-exempt unit in the time notch within 150 meters is higher by 90% compared with buildings with no vacant parcel within that distance. The main IV speciﬁcation uses the dummy variable that takes value 0 for buildings with 0 vacant parcels and 1 for buildings with one vacant parcel within 150 meters. This helps address the concern that the investment patterns differ starkly between buildings that had a larger number of vacant parcels nearby and buildings that had none. For example, Figure 3.38 shows that while the total investment trends in buildings with one vacant parcel nearby are similar to those for buildings with exactly one vacant parcel in the pre-reform period, the investment

129 patterns differ signiﬁcantly for buildings surrounded by more than one vacant parcel within 150 meters.

Sample construction

This requires three steps. First, I restrict the sample to rental buildings built prior to the reform period. The PLUTO data provide the building classification and geographic coordinates of each parcel in the city. Using QGIS, I draw rings of 150 meters radius around each rental building in this sample. Second, using PLUTO data, I intersect vacant parcels with the rings to identify rental buildings that contained a vacant parcel within 150 meters in 2005. 36 Finally, I restrict the sample to rings that contained at most one vacant parcel at baseline for reasons discussed above. To measure rents, I obtain the annual market valuation, number of residential units, geographic coordinates, and other building characteristics from PLUTO for each building–year. Because the Department of Finance assesses all buildings every year, this facilitates analysis of a balanced panel of buildings, which ensures that the composition of parcels in the sample is unchanged over the years in the sample. Figure 3.12 illustrates the spatial distribution of rental buildings in the final sample. Figure 3.44 shows that the market valuation of a building serves as a good proxy for rental income: The regression coefficient of (log) market valuation on (log) rental income is not significantly different from 1, and R2 is 0.94. 37 38 Furthermore, to ensure that the estimation captures spillover effects on existing rental buildings and not the mechanical effects of new tax-exempt investment, 39 I restrict the parcels to (i) non- tax-exempt rental units, (ii) rental buildings constructed prior to 2007, and (iii) parcels that are observed each year in the sample. Additionally, I drop buildings if they report residential area less

36In particular, I identify parcels that were classiﬁed V (Vacant) in calendar year 2005 and project them into QGIS using parcel coordinates. 37This information is obtained for large rental buildings, for which information on both market valuation and rental income is made publicly available. These buildings are used to assess comparable condos and coops. 38I lagged the assessed valuation in PLUTO data by a year. This is because the assessed valuations of a year y in the PLUTO data are based on rental income in year y − 1 (Link). 39Including newer units in the sample mechanically increases the rents, because new units are pricier than old units, all else equal.

130 than 10 sq ft at least once in the sample period, which is likely a reporting error. 40 This leads to a sample consisting of balanced panel of 26,300 rental parcels. Finally, I convert market valuations to 2015 USD using CPI tables provided by the Bureau of Labor Statistics.

Reduced-form results

Figure 3.16 illustrates the reduced-form effect of the binary instrument—existing rental buildings with exactly one vacant parcel within 150 meters vs buildings with no vacant parcel within the same distance—on log rents. The outcome variable is the logarithm of gross rents divided by total square footage in the parcel (where I proxy the rental income by the market valuation by the Department of Finance for the year). Figure 3.16a plots trends in the raw data in buildings with no available land and rents in buildings with exactly one vacant parcel. We see that while there are no clear pre-trends in differences between rent growth in buildings with land and without land nearby, the trends begin to diverge after 2006, which coincides with the year when the instrument—land

availability—becomes active. Figure 3.16b plots the βk coefﬁcients from the following event study regression:

Õ ln(rbt) = β0 + βk1(Vacant == 1)p × γk + γb + γt + γrt + bt (3.6) k∈{2001,2015},k,2005

where b denotes the existing rental building, t the year, and γrt 2000 census tract–year ﬁxed effects. 1(Vacant == 1) is a dummy that takes value 1 if the existing building had one vacant parcel available within 150 meters at the beginning of the reform. I weight the regression by the total residential units to account for heteroskedasticity in the outcome variable (Solon 2013). A plot of rent residuals against residential units in Figure 3.40 conﬁrms heteroskedasticity in the rent outcome variable, which is a group average. The estimates suggest that the rent increased by almost 10% in the time notch in buildings that had a vacant parcel available within 150 meters, compared with the buildings that had none.

40Rental properties are identiﬁed in the PLUTO data according to the following criteria: (i) The structure on the parcel is classiﬁed either C or D in all the years in the data. (ii) The structure on the parcel had at least 10 residential units in all the years.

131 The lack of pre-trends provides evidence in favor of the exogeneity assumption. The rent growth exhibits dynamics whereby the initial impact is larger than the impact later. I propose two explanations. First, the majority of housing starts in the time notch came to market beginning in 2009 (Figure 3.36), which put downward pressure on the initial rent impact. Second, the investment in affected buildings increased following the time notch rent increase, as shown in Figure 3.39. The figure compares the trends in yearly permits issued for alterations and renovations near buildings with positive vacant parcels within 150 meters, with buildings near rental buildings with zero vacant parcels within the same distance. The 2010 spike puts downward pressure on rents by relieving downward pressure. Finally, Figure 3.37 plots coefficients from a specification similar to 3.6, but the vacant parcel dummy is replaced with a dummy that takes value if the building received a project in the notch. Figure 3.37 is the OLS equivalent of Figure 3.16. The OLS event study suggests that rents are higher by 5% in buildings that received a new tax-exempt project in the time notch, compared to buildings that did not receive any project.

Instrumental variables (IV) results

To capture the effect on buildings where land availability increased tax-exempt units, I calculate the IV estimate.41 Intuitively, the IV estimate is the reduced-form effect normalized by the probability of receiving a tax-exempt unit. I measure the IV estimate using the following two-stage least squares regression:

ln(rbt) = α0 + α1(ExemptUnits)b × Postt + γp + γt + γrt + bt (3.7)

where the ﬁrst stage is given by

(ExemptUnits)b × Postt = ζ0 + ζ11(Vacant == 1)b × Postt + γb + γt + γrt + ωbt

41In the heterogeneous treatment framework, the buildings around which vacant land availability increases the number of tax-exempt units are referred to as "compliers". The IV estimate captures the local average treatment effect, which is the treatment effect on compliers.

132 where b denotes the existing rental building, r denotes the region, and t denotes the year.

(ExemptUnits)b denotes the number of tax-exempt units a building receives within 150 meters in the time notch. The point estimate αˆ denotes the semi-elasticity—the percentage change in rents in response to an additional tax-exempt unit received within 150 meters from existing buildings in the time-notch. The regression is a panel IV in which inclusion of building fixed effects controls for constant unobserved differences across buildings, and year fixed effects control for time trends common to all buildings. Similar to the reduced-form specification, I weight the regression by the number of residential units in the buildings. There are 24,718 unique rental buildings containing at most one vacant parcel. In the baseline specification, I cluster standard errors at the building level and add census tract-year fixed effects. The latter allows me to compare rent growth of buildings within a same census tract and controls for any time-varying shocks at the census tract level. The second column of Table 3.6 reports IV results. We see that the presence of a vacant parcel within 150-meter radius from an existing rental building increases the number of tax-exempt units within 150-meter by approximately 1. The IV estimate in Column 2 suggests that an additional tax-exempt unit in the time notch increased gross rents by around 2.3 log points. The Cragg- Donald F-stat not adjusted for clustering is 982. The Kleibergen-Paap rk Wald F statistic adjusted for clustering is 12. The Stoko-Yogo weak identification critical values for 10% and 15% maximal IV size are 16.38 and 8.96, respectively. This suggests that while we reject 15% maximal bias in the IV estimate, we cannot reject 10% maximal bias. The third column reports the OLS estimate at 0.0006—much smaller than the IV estimate—which suggests the presence of a negative omitted variables bias. The last three columns of Table 3.6 replace the census tract-year fixed effects with Zip code-year fixed effects. We see that, understandably, both the reduced-form and the IV estimate are larger. A usual concern in spatial estimation is that standard errors are correlated across space and clustering at the building level ignores such correlation. The standard errors clustered at the building level will be biased in the presence of meaningful spatial correlation. The direction of the bias in the standard errors depends on whether this spatial correlation is positive or negative (Conley

133 (2016)). In Table 3.13, I report estimates with the standard errors adjusted for both spatial correlation a la Conley (2016) and serial correlation at building level.42 I use the distance cutoff of 1 kilometer and a uniform kernel. This implies that rent-error terms of buildings located within 1 kilometer distance from each other are assumed to be spatially correlated, and rent-error terms of buildings located farther than 1 kilometer are uncorrelated. Table 3.13 shows that the standard errors for the reduced form effect are unchanged whereas the errors for the IV and OLS estimate are smaller when adjusting for both serial and spatial correlation.43 Table 3.14 presents the elasticity estimates. The elasticity estimates are obtained by replacing ExemptUnits (ExemptUnits)b × Postt by ( H )b × Postt in specification 3.7. H denotes the number of rental units within 150 meter from the building b at the start of the reform. αˆ represents the causal estimate of a 1% increase in the rental stock within 150 meters of existing buildings. p-values with standard errors adjusted for spatial (1km) and serial correlation are reported in parantheses. I also report p-values with standard errors that only account for serial correlation at the building level. The point estimate of 1.86 suggests that a 1% increase in the local rental stock in the time-notch increased rents of existing buildings by 1.8% which is significant at 1% level of significance. In contrast, the elasticity is higher at 4.95 in the specification which replaces tract-year fixed effects with Zip code-year fixed effects. The latter is consistent with the idea that treatment effects are larger when buildings in the control group are farther away from the treated group, such as a comparison of buildings within a Zip code as opposed to buildings within a census-tract.

3.3.3 Robustness checks

The main empirical strategy discussed above uses a ring of radius 150 meters around an existing rental building. Figure 3.17 plots IV estimates for other radii. As expected, positive spillover effects are larger when we consider investment at smaller distances from the existing rental build-

42I am grateful to Yi Jie Gwee for providing a modified version of the code written by Thiemo Fetzer and Solomon Hsiang, which calculates IV estimates adjusted for spatial correlation and admits high-dimensional fixed effects. See Hsiang (2010) for the original code. 43This suggests the presence of negative spatial correlation in building–rent error terms. Griffith and Arbia (2010) explain that one reason for negative spatial correlation includes local spatial competition for tenants/customers.

134 ing. Figure 3.45 plots the marginal causal response. We see that the marginal effect decreases as we increase the radius, suggesting that the rent effects of new investment are larger when the investment is closer. Interestingly, the change in the point estimate is insignificant for an increase in the radius beyond 200 meters, suggesting that the amenity effects of a new unit are highly local. Similarly, while the main specification uses the number of units received within 150 meters as the treatment variable, one might argue that the relevant margin is the number of projects as opposed to the number of units. Therefore, Table 3.11 presents IV estimates when we use the alternative treatment—the number of tax exempt projects. We see that the cluster robust first-stage

F-stat is larger at around 37. The IV estimate is also higher: 0.65 compared with 0.02 in the main specification. This is consistent with the fact that a project typically contains many units (Table 3.2 suggests that an average tax-exempt project has 16 units). Similarly, while we used a dichotomous IV with sample restricted to buildings with 0 or 1 vacant parcel within 150 meters in the baseline, it is useful to check robustness to using an IV that allows all possible values. Table 3.12 reports estimates for a full IV. We see that the instrument is stronger with an F-stat of 15. Additionally, both the reduced-form and IV estimates are higher at 0.045 and 0.048, respectively. Broadly, the full IV supports the hypothesis that an additional tax-exempt unit in the time notch within a small distance from an existing rental building increased its rents by 2%. Another concern is that the recession confounds the rent effect estimation. This is the case if, for instance, the probability of a foreclosure is correlated with the presence of a vacant parcel nearby. Figure 3.41 shows the spatial distribution of foreclosures. A large share of foreclosures were concentrated in Queens and Brooklyn. I check whether the results are robust to leaving either of the two boroughs out. Table 3.15 presents the IV estimates when we drop each borough one by one. The IV estimate is stable but underpowered when we drop Manhattan (Column 1), partly driven by the fact that the sample size is halved when Manhattan is dropped, reflected in the low KP F-stat (7.35). Nevertheless, the estimates are largely stable and significant when any of the other four boroughs is dropped (Columns 2 to 5), which suggests that it is less likely that the recession confounds the estimates. Finally, while the main IV specification includes rental buildings in both

135 exclusion and non-exclusion regions, Table 3.7 presents IV estimates separately for exclusion and non-exclusion subsamples. Because the non-exclusion regions did not receive an investment shock in this period, presence of significant rent effects in these regions casts doubts on the validity of the instrumental variables strategy. Fortunately, Figure 3.7 shows that while both the reduced-form and IV estimates are insignificant at the 10% significance level in the non-exclusion subsample, they are significant in the exclusion region subsample. This suggests that the rent effects are present only in the exclusion regions which received a large investment shock in this period.

3.3.4 Heterogeneity in rent effects

I perform four heterogeneity tests to better understand the drivers of the rent effect. Figure 3.18 estimates the IV estimate (Specification 3.7) separately for two subsamples in the data: below- median income census tracts and above-median income census tracts. I present 95% confidence intervals, in addition to the first-stage cluster robust F-stat with standard errors clustered at the building level. We see that the positive rent effect is driven by below-median income census tracts. In fact, the rent effect is negative in above-median income census tracts. This demonstrates that whether new investment increases or decreases local rents plausibly is a function of neighborhood income. Figure 3.19 tests whether the rent effect differs by the baseline building rent. No clear pattern emerges, partly because of low first-stage F-stats. Figure 3.20 tests whether the effect differs by baseline building age. The median age of a building in the sample is 80 years. The point estimate is negative and insignificant for older buildings (below-median age) and positive and underpowered for younger buildings. A large share of older pre-war buildings in New York City is subject to either rent stabilization or rent control which could explain why their rents do not respond significantly to new investment nearby. Note that the first-stage F-stat is low for older buildings, which suggests that they are less likely to receive a new project in their neighborhood. Finally, Figure 3.21 tests whether point estimates depend on homogeneity in housing quality within the census tract. Interestingly, the rent effect is driven by tracts in which housing quality is less homogeneous, as measured by the mean deviation in building rents in the tract.

136 3.3.5 Differences-in-differences estimate of the rent Effect

Exclusion regions received a significant investment shock in the time notch, which in principle allows us to estimate price effects by using a simple differences-in-differences (DID) strategy. A concern with this approach is that policymakers plausibly assigned those regions to treatment that were expected to gentrify in any case.44 A simple comparison of gross rents trends in the exclusion and non-exclusion regions would then lead to overestimation of the rent effect. Nevertheless, it is informative to estimate DID effect for two reasons: (i) it allows us to corroborate the findings from the IV approach above, and (ii) we estimate the effect on other prices, such as the sales price of owner-occupied homes, and land price. 45 Gross rent The specification for the event analysis is as follows:

Õ ln(ybrt) = β0 + γb + βk1(Region = Exclusion) × γk + γt + brt (3.8) k∈{2001,2015},k,2005 where b and t denote the building and year, respectively. The dummy for non-exclusion is omitted. The outcome variable is the same as in IV specification—the logarithm of building annual market valuation divided by the gross square foot residential area. The sample is similarly restricted to preexisting buildings. I omit the dummy for one year before the reform. Standard errors are clustered at the borough-year level. Figure 3.22a plots the differences in trends in log rental income per square foot between exclusion and non-exclusion regions, using specification 3.8. We see that there is a positive and significant increase in the rental income of existing buildings in the exclusion region compared with the non-exclusion region after 2006. The effect is large: about 20% five years after the reform. Pre-treatment coefficients are insignificant at 5% confidence level. Home prices Owner-occupied homes include one/two/three unit family homes and condos/coops. To estimate the effect on prices of owner-occupied units, I use transactions data from the Depart-

44For instance, as then-Assemblyman Voto Lopez stated, the legislature “picked areas that were being gentriﬁed [to be included in the zone], parts of Williamsburg [for example]" (Cohen (2009)). 45Sales data is thin at the ring level which prevents us from implementing a similar IV strategy for sales price.

137 ment of Finance, which include the universe of property sales in New York City. I estimate the same specification as 3.8 in which building fixed effects are replaced by address fixed effects. This is because a single building has multiple owner-occupied units on its premises. I restrict sales data to properties that consists of family homes and condos/coops.46 In addition, I restrict the sample to sales of non-tax-exempt properties. The inclusion of address fixed effects in the regression implies that the estimate βt captures the effect on repeated sales of homes. This allows us to control for fixed unobserved characteristics of the apartment/home/building despite a smaller estimation sample. Figure 3.22b shows the effect on owner-occupied homes. We see that although the pre-trends are insignificant, the sales price increased in exclusion regions by around 20% after 2006. Land price Landowners and developers, who are responsible for new residential investment, are crucial actors in the real estate industry. Obtaining the exact land price is difficult, because there are very few vacant land sales. To circumvent this issue, I use the same transactions data but restrict to sales that also transfer land.47 There are around 101,000 sales with nonzero sale of land in the sample period. The specification with the logarithm of sale price per land square foot is as follows:

Õ ln(ylrt) = β0 + βk1(Region = Exclusion region) × γk + γl + γt + lrt (3.9) k∈{2001,2015},k,2005 where γl, γt denote land parcel and year fixed-effects, respectively. I cluster standard errors at the borough-year level. Figure 3.22c shows the event study on the land price. We again find evidence of no significant pre-trends. While the initial effect of the reform is 20%, it increases to more than 40% seven years after the reform. Commercial rents In addition to the users and suppliers of residential capital, suppliers of commercial capital are also affected. To estimate the effect on commercial rents, I use the PLUTO data but restrict to parcels containing only commercial space. 48 I estimate the same regression

46Specifically, these include properties that belonged to the building classifications A, B, C, D, R, and S at the time of the sale. For buildings of type R, S, C, and D, I restrict to sales of one-unit properties. 47This includes sales of parcels with building classification C, D, R, S, and V at the time of sale. 48These include parcels of types K, O, and S.

138 as 3.8, weighted by commercial units on the parcel. Figure 3.22d shows that commercial rents in exclusion regions increased after the tax reform in 2006. After 9 years, the commercial rents in exclusion regions are higher by about 5%, compared with non-exclusion regions.

3.3.6 Differences in regression discontinuity

One feature of the property tax reform is the presence of a clean boundary between exclusion and non-exclusion regions in Brooklyn—a major borough in the city—which can be used to perform a differences-in-regression discontinuity to provide supplementary evidence for the rent effects of new residential investment. Intuitively, this approach compares the growth in rents on either side of the boundary, where one side of the boundary is more affected by the tax-reform than the other side. An advantage of this approach is that by comparing neighborhoods close to the border but on the other side of the border, we are able to control for local economic shocks. The tax reform led to significant new tax-exempt residential investment in exclusion regions in Brooklyn. Figure 3.8 shows that the excess starts in Brooklyn comprised about half of the total excess starts in the city. The stock of tax-exempt new units increased dramatically in exclusion regions in Brooklyn after the reform (Figure 3.26). Consistent with results in previous subsections, we expect rents to be higher in the exclusion regions in Brooklyn after the reform. The sample is constructed as follows. I split the geographic boundary into segments and select those segments that have rental properties on either side of the boundary. I exclude boundary segments that coincide with parks (Prospect Park). Using QGIS, I draw buffers of varying distance from the boundary. For instance, Figure 3.23 denotes parcels in the sample within 1,300 meters from the boundary. Figure 3.24 plots the yearly differences in average rents in exclusion and non- exclusion regions within b meters from the boundary in which b ranges from 100 to 1,500 meters in 200 meter increments. Figure 3.24 reveals that there are no significant pre-trends in the rent growth differences in the two regions at any bandwidth. Additionally, for neighborhoods within a small distance from the border, the change in rent differences between exclusion and non-exclusion regions is insignificant.

139 This is consistent with amenity changes being uniform within small distances. The rent effects are signiﬁcant for bandwidths larger than 1,100 meters. Rents are higher by 10% in the exclusion regions within 1,100 meters from the boundary after the reform, compared with non-exclusion regions 1,100 meters outside the boundary. Together, the estimates in this section corroborate the ﬁnding that a larger residential investment increased rents in exclusion regions after the reform.

3.4 A mechanism: Gentriﬁcation

As more market-rate housing becomes available on the waterfront, current upland landlords are looking to maximize their proﬁts. This is a situation where supply is actually driving demand. Waves of émigrés from Manhattan. — Martin Needelman, Project Director of Brooklyn Legal Services Corporation A

The empirical exercise so far has yielded two key results. First, current investment responded to increases in the future property tax. Second, an additional new tax-exempt unit within 150 meters from an existing rental building increased the buildings’ rent. In this section, I show that this result is consistent with the hypothesis that new residential investment has positive consumption spillovers, which allows landlords of nearby buildings to impose higher rents. A key point is that housing is a durable good that depreciates in quality over time. All else equal, richer tenants spend more on housing, which implies that they prefer better quality housing. An increase in the market supply of new housing filters over time from high-income to low-income tenants, as new housing depreciates (Sweeney (1974); O’Flaherty (1995); O’Flaherty (1996)). Rosenthal (2014) documents that at any given point in time, high-income tenants tend to occupy newer housing, which provides empirical support for the presence of filtering in tenant-occupied homes. Figure 3.3 depicts the negative relationship between age and (residualized) rental income per square foot of buildings in 2016. Because several factors determine a building’s rental income, I first obtain residuals from a regression of rents on census tract fixed effects, total units, lot area, building area, residential area, number of floors in a sample of buildings developed in the past

140 100 years. The R2 is 0.7. Figure 3.3 plots residualized rents against age. The figure reveals that older units have lower rents, and that this negative relationship is stronger in the first 25 years of development. This is in line with Rosenthal (2014), who uses nationwide data to show that occupant income falls with the age of the rental unit. All else equal, tenants in the newer rental units pay higher rents. Consider that the introduction of a tax-exempt property in a neighborhood has two effects, both of which move in opposite directions. First, a lower property tax on the new properties creates standard downward pressure on rents of nearby properties and increases gross rents from rT to r¯ (Figure 3.25). I refer to this as a supply effect. Second, the introduction of a new project increases the amenity value of the neighborhood. This has two parts: New development directly improves the amenity value of the neighborhood by increasing the aesthetic appeal, and indirectly it increases consumption amenities by attracting affluent tenants. These two channels together form the amenity effect. In contrast to the competition effect, which leads to movement along the supply curve, the amenity effect shifts up the demand curve (see Figure 3.25), leading to an increase in rents. The net effect on rents depends on which effect dominates. As a motivation for empirical exploration of the mechanisms, consider the effect on two types of businesses in the Brooklyn following the tax reform. The second panel of Figure 3.26 shows that the stock of new tax-exempt housing drastically increased in the exclusion regions in Brooklyn following the tax reform in 2006. The second row of Figure 3.26 plots the flow of new businesses in the exclusion and non-exclusion regions within Brooklyn in this period. We see that while there is a stark increase in the number of new sidewalk cafés (associated with high-income customers) in the exclusion regions after the reform, the number of new laundromats (associated with low- income customers) declined. This is consistent with the hypothesis that new residential investment attracts local businesses that cater to more affluent households. The following sections explore consumption amenities and demographics changes more rigorously.

141 3.4.1 Evidence 1: Demographic changes

A key channel by which new residential investment affects amenities is through changes in the average neighborhood income level. In this subsection, I present demographic changes in the neighborhoods that received residential investment in the time-notch. The lowest available geographic level for such data is census tract at 2000 boundaries. The data come from the 2000 Census and 5-year estimates from the 2005-09 and 2013-17 American Community Survey (ACS) and.49 I obtain information on a host of outcomes such as rent, income, race, education, and age of the household head. Details of data construction can be found in Appendix 3.9. The estimating equation is

log(Yrt) = β0 + β11(ExemptProjects ≥ 1)r × Postt + γr + γt + rt (3.10)

where 1(ExemptProjects ≥ 1) is a dummy that takes value 1 if the number of tax-exempt project starts in the census tract r in the time notch were non-zero; Yrt denotes the outcome variable;

γr and γt denote census-tract and year fixed effects, respectively. The coefficient of interest here is β1, which I estimate using an IV approach. Specifically, I instrument 1(ExemptProjects ≥ 1) × Post with the (VacantParcels) × Post. (VacantParcels) denotes the total number of vacant parcels available in the census tract at the start of the reform. Post takes value 1 when observation belongs to ACS 2005-09 and ACS 2013-17, and zero for Census 2000. I cluster standard errors at the census-tract level, which is level of the treatment.50 Table 3.8 reports IV estimates. We see that the census tracts that received at least one tax- exempt project in the time-notch have 763 additional occupied units after the tax reform (Column 1), the median rent is higher by 33% (Column 2), and the income is higher by 24% (Column 3). The number of tenants with at least a Bachelor’s degree is higher by 20 percentage points (Column 4), the number of white households is higher by 17 percentage points, and the number of young

492005-09 ACS represents an average over the 2005-09 period. 50I use the treatment variable —the number of projects—- as opposed to the number of units, because the instrument is a weak predictor of the number of units at the level of the census tract.

142 renter households is higher by 7 percentage points (Columns 5 and 6). The heteroskedasticity robust Kleibergen-Paap F-statistic is 20.78, which rejects the weak IV test.

3.4.2 Evidence 2: Changes in amenities

This section provides direct evidence on the entry of businesses that cater to the demands of high-income tenants following new residential investment in the time notch. The main dataset I use comes from County Business Patterns (CBP) data. This dataset provides Zip code-level counts of establishments at 6 digit NAICS level. I estimate how the increase in the log establishments varies by industry-level income elasticity. The income elasticity captures how likely it is that a particular industry caters to high-income demand. To obtain this income elasticity, I regress the log number of establishments at 4-digit industry level in a Zip code in 2001 on mean Zip code renter income in 2000, by each 4-digit NAICS industry. This produces approximately 300 industry income elasticities. A high income elasticity suggests that the industry caters to high-income tenants, which is reﬂected in its high concentration in high-income Zip codes in 2000. I order industries by income elasticity into deciles. We expect the effect on establishments to be higher for industries with high income elasticity. Figure 3.17 lists selected industries with high and low income elasticities. Some investment services such as NAICS 5231, 5239, and restaurants/ drinking places have high income elasticity whereas manufacturing such as NAICS 3323, ship and boat building NAICS 3366 have low income elasticity. I estimate the following speciﬁcation, separately for each decile.

log(Nirt) = β0 + β11(ExemptProjects ≥ 1)r × Postt + γr + γi + γt + rt (3.11)

where 1(ExemptProjects ≥ 1) is a dummy that takes value 1 if the Zip code r received at least one tax-exempt project in the time notch. The outcome variable is the number of establishments in industry i in region r in year t. I instrument 1(ExemptProjects ≥ 1) × Post with the (VacantParcels) × Post. This speciﬁcation is similar to the one used for demographic outcomes. Post dummy takes value 1 for all years after 2006. The sepeciﬁcation includes region, industry

143 and year fixed effects. Standard errors are clustered at Zip code level. Figure 3.27 shows that the first stage exists when we consider Zip codes as a unit of geography. The figure plots the average number of tax-exempt projects received by a Zip code in the time notch against the baseline number of vacant parcels. Zipcodes with a higher vacancy at the time of the reform received a larger number of projects in the time notch. Figure 3.28 plots the trends in the log number of establishments in the high-land Zip codes (Zip codes with a baseline number of vacant parcels above 75th percentile, and hence expect to receive larger investment in the time notch) and low-land zipcodes (Zip codes with a baseline number of vacant parcels below 25th percentile, and hence expect to receive smaller investment). We see that trends for high-land Zip codes begin to diverge, particularly after 2006, for industries such as retail/wholesale and restaurants, which coincides with the time notch. The IV estimates in Figure 3.29 confirm that residential investment increased establishments in industries more likely to locate near high-income tenants. The x-axis denotes the industry income elasticity decile. Point estimates are insignificant for industries with below-median income elasticity and significant and positive for above-median income elasticity, consistent with the hypothesis that higher residential investment increased establishments in industries that are more likely to locate near high-income tenants. Finally, the first-stage is stable for each decile subsample.

3.5 Discussion

This section uses reduced-form estimates to provide back-of-the-envelope calculations for welfare changes for local high- and low-income tenants, building owners, local government, and total efﬁciency gains as a result of investment in the time notch. Time notch is equivalent to a tempo- rary reduction in property taxes on new units in the time notch in exclusion regions. The estimates provided in this section do not incorporate city-wide aggregate welfare changes.

144 3.5.1 Incidence of tax-exempt investment in the time-notch

I use a simple spatial equilibrium model with homogeneous preferences across regions but that is hetereogenous across income types. I make the following assumptions: (i) utilatarian aggregate welfare function; (ii) perfect competition and free entry among developers and providers of amenities; and (iii) the social marginal cost of government funds is equal to 1. Additionally, for simplicity, I assume there are two types of tenants, high-income (h) and low income (l). The mean utility of tenant of income type k in region j is given by

k k k k Vj = w + α Aj − rj where j ∈ e, n denotes exclusion/non-exclusion region and k ∈ h, l denotes high-income/low-

k income. rj denotes the tax-inclusive rents paid by tenant of income type k in region j. Unless speciﬁed, I suppress the subscript j to refer to exclusion regions. The average wage is independent of location choice which is a reasonable assumption in the current setting.51 The relative valuation for amenities differs between high- and low-income tenants. For instance, it is reasonable to assume that αh > αl. That is, high-income tenants have greater preference for local amenities than low-income tenants. For simpliﬁcation, I normalize αh = 1, which implies αl < 1.52 Tenants:

The effect of the time notch on high-income tenants in exclusion regions is given by

h h h ∆V = Nt ( −∆r + ∆A ) |{z} |{z} Rent change Amenities change

h where Nt denotes the number of high-income tenants in the exclusion region before the reform. 51Tenants can commute to any neighborhood within the city. In contrast to the models in which tenants choose to locate across cities and city-speciﬁc productivity differences are important, this is not a relevant factor in this case, where the analysis is within city. 52 Note it is possible that αl < 0, which is the case when low-income tenants have a strong dislike for local consumption amenities. Otherwise, a more sensible approach is to assume αl ∈ [0,1]. This implies that in general, low-income tenants’ valuation of local amenities is a fraction of high-income tenants’ valuation with the extreme case of αl = 0, in which they do not care about such amenities at all.

145 Thus, to the first order, the impact of a tax cut on new investment in region t equals the impact on gross rents and amenities (weighted by the tenant’s preference parameter) times the share of high- income tenants residing in region e. The first term captures the change in high-income welfare due to a change in gross rent. The second term captures the change in their aggregate welfare due to amenity changes. When amenities are fixed, the first term is positive while the second term is

∆A = 0 and high-income welfare necessarily increases following a property tax cut. When there is inﬁnite mobility and homogenous preferences within an income group, any rent increases in the exclusion regions must be compensated by an equivalent amenity increase to make a marginal high-income tenant indifferent between exclusion and non-exclusion regions.53 In that

case, a change in gross rents reﬂects changes in amenities (i.e., ∆r h = ∆A), and thus the net gains to high-income tenants is zero. Low-income tenants are affected by the changes in local amenities and changes in rents, if any. The effect on low-income tenants’ welfare (in exclusion regions) is given by

l l l l ∆V = Nt ( −∆r + α ∆A ) |{z} |{z} Rent change Amenities change

where rl denotes the tax-inclusive rent on the units occupied by low-income tenants. Low- income tenants beneﬁt from amenity changes if and only if they place strictly positive valuation on them. In the extreme case in which αl = 0, which happens when the new amenities include sidewalk cafes and art galleries—which these tenants do not value—low-income tenants are strictly worse off following the tax change, because their out-of-pocket rent cost increases. To provide an

54 upper bound on low-income welfare loss, I assume αl = 0 and that they are completely immobile. The effect of the investment in the time notch on low-income tenants’ welfare is given by ∆V l =

53Another interpretation is that the change in rent on high-income units is entirely driven by changes in consumption amenities, when the supply effect on high-income units due to additional new units in the neighborhood is minimal. 54For instance, low-income tenants occupy rent-stabilized units and moving implies that they lose that status, or credit constraints prevent low-income tenants from paying ﬁxed costs of moving.

146 l l l 55 56 τ Nt ∆r = 1.15 × 521,748 × ∆r = 521,748 × 1,050 = −$547mn. Owners of rental buildings: There are two kinds of owners. One group owns low-income rental units, and therefore obtains net-of-tax rents rl. The other group owns high-income rental units, and obtains rents r h. The total per annum proﬁt accruing to owners is given by

O h l V = r Nh + r Nl − Ch − Cl

where Ci denotes the ﬁxed cost of maintaining high-/low-income units. Assuming that these costs are unaffected by the time notch, the effect of a tax cut on owners’ welfare is given by ∆VO =

h l h l Nh∆r + Nl∆r . Continue to assume ∆r = ∆r , H¯ = Nh + Nl; then the welfare gains to the owners are ∆VO = H¯ ∆r h = 1043496 × 1050 ≈ $1b. Local government: Another component of the welfare includes the government. Increased construction activity has two effects on government. On the one hand, government loses property tax revenues on exempt units started in the time notch. On the other hand, the addition of new units to the rental stock has positive spillovers to rents of existing units because of higher rents, which increases the tax base for the government. 57

h ∆R = −th∆Hr¯ + th∆rH¯ | {z } |{z} Revenue lost Revenue gains The revenue gains to the government, therefore, are ∆R = −0.15 × 17,520 × 10,735 + 0.15 ×

1,043,496 × 1,050 = 164mn, which is around 2.4% of annual city real property tax revenues from rental units. 58 55Using a capitalization rate of 6, a property tax rate of 2.5% on the assessed valuation is equal to a tax rate of 15% on the rental income. 56Where I have used the higher of the two estimates in Table 3.6, which allows us to calculate the upper bound of the welfare losses to low-income tenants. The average monthly rent in exclusion regions at the start of the reform was $1,462 (Table 3.3). A 6% increase in rents suggests that the tenants’ annual rent payments increased by $1,050 a year. Table 3.5 suggests that there existed 1,043,496 units in 2005. I assume that half of the total rental stock was occupied by low-income (or below median income) tenants. This is conﬁrmed in Table 3.16, which shows that the number of low-income tenants was fairly close in exclusion and non-exclusion regions at the start of the reform. 57I continue to assume an equal increase in rent of high-income and low-income tenants. 58The New York City government collected around $6.85 billion (USD 2015) in property taxes from class 2 properties in 2006; see Furman (2011), page 9. Total revenues in 2006 ($16 b) are multiplied by 0.36, the share of class 2

147 3.5.2 Efﬁciency effect of the time-notch

As pointed out by Kleven (2018), for small tax reforms and utilitarian aggregate welfare function, the difference between total and mechanical changes in tax revenues is a sufficient statistic for measuring efficiency loss (or gain in the case of the tax cut), in the absence of externalities. With externalities, as in our case, we add an extra term that corresponds to the benefit accruing to high-income and low-income tenants because of larger amenities due to the tax reform. The aggregate efficiency gains consists of two parts:

˜h ¯ h l l ∆W = thr ∆H + (Nt + α Nt )∆A | {z } | {z } ∆Housing supply ∆Amenities

The efﬁciency gains come from two sources: (i) the tax-exemption on new investment stimulates construction and reduces the deadweight loss associated with the property tax; and (ii) new investment increases economic activity and consumption amenities. The increase in aggregate welfare depends on the weight placed on the amenities by low- and high-income tenants. With- out knowledge of preference parameters for amenities, we can not calculate total efﬁciency change.

However, when αl = 0, we can easily use the empirical estimates to obtain the efﬁciency estimates. Note that annual r˜h = $17,520 (USD 2015), ∆H¯ = 10,735, ∆A = ∆r˜h we get:

∆W = 0.15 × 17,520 × 10,735 + 521,748 × 1,050 ≈ $576million

Given that the New York City government collected around $6.8 billion (USD 2015) in property taxes from an equivalent tax class in 2006, the aggregate annual efﬁciency gains from the time notch correspond to 0.5 billion dollars, which is equivalent to about 7.3% of total revenues. Note that back-of-the-envelope calculations in this section use local-reduced form estimates and do not incorporate any general equilibrium changes. properties in total revenues (page 10), which is then further multiplied by 1.19 to convert into 2015 USD.

148 3.6 Conclusion

This paper estimates the local effects of property tax incentives for new construction. I leverage the New York Ciy property tax reform of 2006-08, which reduced tax benefits on new investment. The delay between announcement and implementation led to a time notch in which investment before the deadline was associated with a lower property tax, compared with investment just after the deadline. I exploit the bunching of tax-exempt projects in the notch period in a bunching framework to estimate the elasticity of current residential capital with respect to future property tax. I find that a 1% increase in future property tax increased current residential rental stock by 0.4%. Importantly, I find that an additional new tax-exempt rental unit within 150 meters in the time notch from an existing rental building increased its gross rental income by 2.3%. I hypothesize that the positive effect on gross rents can be explained by the fact that new tax-exempt investment attracted high-income individuals who increased the average income of the neighborhood, boosted local businesses, and therefore further increased the amenity value of nearby rental buildings. Through event studies and an instrumental variables approach, I document that changes in demographic composition and business composition are consistent with the above hypothesis. Residents are more educated, white, and richer in regions that received larger investment after the reform. Changes in business composition are consistent with the improved amenity hypothesis. The number of sidewalk cafes (associated with high-income consumers) increased after the reform in regions with larger investment shock while laundromats (associated with low-income consumers) declined. The papers’ results have policy implications. They suggest that rent effects at the local level do not necessarily mirror aggregate effects. That said, future work will explore the aggregate effects of new residential investment. A first step in that direction is to estimate the displacement of existing low-income tenants in exclusion regions and neighborhood changes in regions of origin of tenants in new buildings developed in the time notch.

149 3.7 Figures and tables

Figure 3.1: 421a property tax reform 2006-08

Notes: The figure shows the changes in the "Exclusion region" that were part of the 421a property tax exemption 2006-08 reform. The light blue shaded region indicates the original exclusionary region, where prior to December 2006, developers were required to provide affordable housing, either offsite or onsite to be eligible for 421a benefits. The dark blue unshaded region indicates newly added excluded regions. After 2008, developers in new regions could only obtain long exemption, which requires provision of onsite affordable housing. In addition, 421a developers in the old exclusion region must provide affordable onsite, a more expensive requirement. Together, light and dark blue regions formed the ‘exclusion regions’ and were to see a loss of generous tax benefits beginning 2008. Note that the blue regions in Manhattan and Brooklyn represent ‘Hudson Yards’ and ‘Williamsburg’ region respectively where special provisions applied.

150 Figure 3.2: Distribution of housing stock type in New York City in 2007

Notes: This ﬁgure plots the distribution of the housing stock in exclusion and non-exclusion regions in 2007—a year before the implementation of the tax reform. Data: Primary Land Use Tax Output, 2002-16.

151 Figure 3.3: Correlation between age and rent of a housing unit

Notes: This figure plots the relationship between the age of a rental unit and its rent price in New York City. Sample includes cross-section of parcels in 2016 and developed in past hundred years. The thick line denotes the lowess fit obtained through a regression of residualized rent on age. Triangles denote average residualized rent for each discrete value of age variable. Residualized rent includes residuals from a regression of rent on total units in the building, census tract fixed effects, lot area, building area, residential area, number of floors and number of buildings on the parcel. Data: Primary Land Use Tax Output 2016.

152 Figure 3.4: Effect of time notch on short term and long term outcomes

(a) Policy 1: Unanticipated Tax increase (b) Policy 2: Anticipated Tax increase

(c) Rents path under the two policy scenerios Notes: This figure illustrates how the short term outcomes, as defined by the net-of-tax rents, differ under the two policy scenerios: Unanticipated property tax increase (Policy 1), and anticipated property tax increase (Policy 2). The long term outcome, determined by long run amenity and housing supply elasticity is the same under the two scenerios. The long run elasticities are such that the net rents decline. In Policy 1, the landlord rents decrease but slowly increase to the long-run value as lower investment allows them to shift some burden onto the tenants. In contrast, in Policy 2, the effect on rents is different due to a short term increase in new residential investment following the tax-reform. The figure illustrates the case when the amenities are sufficiently elastic so that the net-of-tax rents increase. These trends are reversed in the long-run where the time it takes to reach the long run depends on how long it takes the housing to depreciate.

153 Figure 3.5: Aggregate quarterly tax-exempt housing starts in New York City, blue and yellow regions

154 Figure 3.6: Spatial distribution of tax-exempt projects in the time notch

Notes: This ﬁgure presents the spatial distribution of tax-exempt project starts before and in the time-notch. Each project is weighed by the total number of residential units built. The top panel includes permits issued during 2005q2 to 2006q4. The bottom panel includes permits issued during 2006q4-2008q2 (the time notch). Data: Department of buldings permits, 2001-15 and Primary Land Use Tax Output 2002-16.

155 Figure 3.7: Bunching estimation of tax-exempt housing unit starts

Notes: Diamonds denote the empirical distribution of tax-exempt housing starts. Squares denotes the counterfactual: empirical distribution of non-tax-exempt housing starts in the blue region. Data: Department of Buildings permits, 2001-15.

156 Figure 3.8: Bunching of tax-exempt housing starts in exclusion regions, by boroughs

Notes: Diamonds denote the empirical distribution of tax-exempt housing starts. Squares denotes the counterfactual: empirical distribution of non-tax-exempt housing starts in the exclusion region. Data: Department of Buildings permits, 2001-15.

157 Figure 3.9: Effect on aggregate housing starts in exclusion vs non-exclusion regions

158 Figure 3.10: Empirical design to estimate the effect of the 2006-08 Tax reform on the Rents

Notes: This picture highlights the main empirical strategy to estimate the effect of new residential investment on existing building rents. The availability of a vacant parcel within 150 meters radius from a building acts as an instrument for the magnitude of investment received by an existing building in the time-notch. Time notch refers to a period between announcement and implementation of property tax increase on new residential projects.

159 Figure 3.11: Spatial distribution of vacant parcels in 2005

Notes: This figure shows the spatial distribution of vacant parcels across New York City in 2005. A parcel is classified ‘vacant’ if it was classified as ‘V’ in 2005. The reform effectively increased property tax on new units in the exclusion (shaded blue) regions beginning July 2008.

160 Figure 3.12: Spatial distribution of existing rental buildings in 2005

Notes: This ﬁgure presents the spatial distribution of existing rental buildings in the sample. The sample includes 25,000 buildings observed for 15 years.

161 Figure 3.13: Classiﬁcation of parcels developed in the time notch

Notes: This ﬁgure shows the distribution of the types of parcels that were developed in the time-notch, that is, during 2006-08 and obtained 421a property tax exemption. Data: Primary Land Use Tax Lot Output, 2002-16 and Department of Finance 421a Exemption list 2015.

162 Figure 3.14: First stage

(a) Vacant parcels at baseline (b) Mean tax-exempt units during the time-notch Notes: This ﬁgure shows the ﬁrst stage for the instrument—baseline number of vacant parcels available within a 150 meters radiius from an existing rental building in 2005. Panel 3.14a shows the distibution of number of vacant parcels within 150 meters and mean tax-exempt units within the same distance in the time-notch. Panel 3.14b presents the mean tax exempt units received within 150 meters from an existing rental building that had 0 vacant parcels and 1 vacant parcels within that distance in 2005. The latter forms the main dichotomous instrumental variable used for estimating the effect on rents.

163 Figure 3.15: Probability that a building receives a tax-exempt unit within 150 meters in the time notch

Notes: This ﬁgure presents the difference in the mean tax exempt units received within 150 meters from an existing rental building with 0 vacant parcel and existing rental buildings with 1 vacant parcel within the same distance.

164 Figure 3.16: Rents in buildings with vacant parcel vs buildings with no vacant parcel within 150 meters

(a) Raw data (b) Regression estimates Notes: This figure plots the trends in (log) rents of existing buildings that had a vacant parcel available within 150 meters and buildings that had no vacant parcel available within 150 meters, in the beginning of the notch period. Panel 3.16a presents trends in the raw data, obtained by taking the weighted average of building–year rent where each building is weighted by the number of residential units. Panel 3.16b presents the event study coefficients with 5% confidence interval using specification 3.6. Specifically, this equation estimates the differential trends in buildings with zero and one vacant parcel within 150 metres and controls for building, year and 2000 census tract–year fixed effects.

165 Figure 3.17: IV estimate as a function of the ring radius

Notes: This figure presents the IV estimate—-the effect of an additional tax-exempt unit in the time-notch within r radius from an existing building on its rents—-as a function of ring radius. r varies from 50 meters to 300 in increments of 50 meters. The instrumental variable is a dummy that takes value 1 if the building had a single parcel available within 150 meters radius at the start of the reform. All specifications include building, year and census tract-year fixed effects. Bars denote 5% confidence interval with standard errors clustered at the building.

166 Figure 3.18: IV Estimate as a function of census-tract income

Notes: This figure presents the IV estimate—-the effect of an additional tax-exempt unit in the time-notch within 150 meters radius from an existing building on its rents—as a function of income of the census-tract in 2000. The instrumental variable is a dummy that takes value 1 if the building had a single parcel available within 150 meters radius at the start of the reform. All specifications include building, year and census-year fixed effects. Bars denote 5% confidence interval with standard errors clustered at the building. Cluster-robust (AP) F-Stat are reported.

167 Figure 3.19: IV Estimate as a function of baseline building rent

Notes: This figure presents the IV estimate—-the effect of an additional tax-exempt unit in the time-notch within 150 meters radius from an existing building on its rents—as a function of income of building’s rent in the baseline. The instrumental variable is a dummy that takes value 1 if the building had a single parcel available within 150 meters radius at the start of the reform. All specifications include building, year and census-year fixed effects. Bars denote 5% confidence interval with standard errors clustered at the building. Cluster-robust (AP) F-Stat are reported.

168 Figure 3.20: IV Estimate as a function of baseline building age

Notes: This figure presents the IV estimate—-the effect of an additional tax-exempt unit in the time-notch within 150 meters radius from an existing building on its rents—as a function of building age at the baseline. The instrumental variable is a dummy that takes value 1 if the building had a single parcel available within 150 meters radius at the start of the reform. All specifications include building, year and census-year fixed effects. Bars denote 5% confidence interval with standard errors clustered at the building. Cluster-robust (AP) F-Stat are reported.

169 Figure 3.21: IV estimate as a function of census-tract housing quality heterogeneity

Notes: This figure presents the IV estimate—-the effect of an additional tax-exempt unit in the time-notch within 150 meters radius from an existing building on its rents—as a function of variation in housing quality within the census tract. The latter is measured by mean deviation in rents across buildings within a census tract in 2006. The instrumental variable is a dummy that takes value 1 if the building had a single parcel available within 150 meters radius at the start of the reform. All specifications include building, year and census-year fixed effects. Bars denote 5% confidence interval with standard errors clustered at the building. Cluster-robust F-Stat are reported.

170 Figure 3.22: New residential investment and prices: Prices in exclusion and non-exclusion regions

(a) Effect on gross rents (b) Effect on sale price of homes

171 Figure 3.23: Parcels used in differences-in-geographic regression discontinuity

172 Figure 3.24: Differences in regression discontinuity at varying bandwidths

Notes: This ﬁgure plots yearly differences in log rent per square feet within and outside the exclusion regions in Brooklyn. ‘Within r meters’ includes parcels within r meters from the boundary on either side where r varies from 100 to 1500.

173 Figure 3.25: Mechanism

Land/Owner price Rent D00 D D00 0 new new D S Snew D r¯0 0 PL rT PL r¯ rL

0 O Q O QL QL New housing new Quantity Land/Owner Market Rental Market Notes: This ﬁgure depicts the effect of increase in tax-exempt residential investment in an open economy with endogenous amentities. The reform increased supply of tax exempt units which was equivalent to reduction in average property tax paid by the tenant. While the reduction in average property tax reduces gross rents (supply effect 0 PL → PL) on incumbent units, there is also an amenity effect, which can be divided into two parts. First, addition of new units directly increases amenity value of the region by introduction of new units in the neighborhood. Second, newer units attract relatively richer households and increases average income of the region. This in turn, increases local demand for local goods and services, further increasing the amenity value of the region. Together, these two channels imply that the amenity value of old units go up. This is what I refer to as amenity effect of tax-exempt unit. If amenity effect dominates competition effect, then local rents rise instead of falling, landlords pocket larger net rents and landowners beneﬁt from even larger land prices.

174 Figure 3.26: New tax-exempt residential investment and consumption amenities in Brooklyn

Notes: These ﬁgures illustrate the case study of Brooklyn—a major borough in New York City— that witnessed a signiﬁcant investment shock due to the property tax reform. The top-left panel shows the exclusion regions where the property tax was set to increase beginning 2008. The delay in implementation increased housing starts. Consequently, new tax-exempt housing in exclusion regions increased drastically (top-right). There was also a shift in composition of businesses in the exclusion regions. Sidewalk cafes (associated with high-income tenants) increased while laundromats (associated with low-income tenants) fell, as illustrated by bottom-left and bottom-right panel respectively.

175 Figure 3.27: First stage: Tax exempt projects in the time notch against baseline land intensity in the zipcode

Notes: This ﬁgure illustrates the number of projects started in the time notch as a function of baseline number of vacant parcels available in a Zip Code at the start of the notch period.

176 Figure 3.28: Log establishments by high land and low land availability

Notes: This ﬁgure illustrates the raw-trends in the log number of establishments by whether the zipcode belongs to highest quartile (more likely to receive new tax-exempt residential investment in the time-notch) or lowest quartile (less likely to receive new tax-exempt residential investment in the time-notch) in terms of baseline number of vacant parcels at the start of the reform period. This is shown for six broad industry categories.

177 Figure 3.29: Business activity: Estimates by industry income elasticity

Notes: This figure provides estimates of the effect of new residential investment on the log number of establishments, as a function of 4-digit industry’s income elasticity. The x-axis denotes the industry income elasticity decile. Figure in the left panel shows the first stage—effect of baseline vacant parcels on number of projects in the zipcode in the time notch. Each point represents estimate from a separate regression using industries in the same decile. Industry income elasticity is obtained by regressing log number of establishments in the zipcode in 2001 against log mean renter income in the zipcode in 2000, separately for each 4-digit industry. This produces 300 industry elasticities which are ordered into ten deciles. The figure in the right panel shows the IV estimate, ordered by income elasticity of industries. Data: County Business Patterns 2001-16, and Census 2000.

178 Table 3.1: Changes brough by 2006-08 property tax reform

Period Light-blue region Dark-blue region Yellow (Old-exclusion region) (New Exclusion) (Non-exclusion) Offsite Long Exemption Before 2006-8 Avail NA NA After 2006-8 NA NA NA Short Exemption Before 2006-8 NA Avail Avail After 2006-8 NA NA Avail but capped Onsite Long Exemption Before 2006-8 Avail Avail Avail After 2006-8 NA Avail Avail

Notes: This table summarizes temporal and spatial variation in the tax incentives created by the 421a property tax- reform. Bold represents most preferred exemption type before the tax reform in the speciﬁed region. In newly excluded regions, either the reform did not alter the tax incentives or it effectively removed the tax exemption, depending on local neighborhood rents. The latter is going to be true for high rent-regions within new-exclusion regions. See Appendix B.3 for the underlying calculations.

179 Table 3.2: Summary statistics for non-tax-exempt and tax-exempt parcels in 2015

Mean Median SD N t-test Building area 14062.65 3887 53699.92 8613 19265.76 4959.5 58284.65 7280 -5.8 Res units 13.50 3 51.82 8613 16.98 4 52.88 7280 -4.17 Lot area 4675.71 2450 14430.12 8613 5737.86 2502 16690.42 7280 -4.25 No. Buildings 1.12 1 1.39 8613 1.29 1 2.51 7280 -5.12 Rent 1316.14 704.15 1766.24 863 1927.60 1636.68 1558.80 708 -7.28 If Condo .08 0 .285 8613 .26 0 .43 7280 -28.56 If High-income region .58 1 .49 8613 .45 0 .50 7280 17.25 Age 12.71 11 5.99 8051 10.55 10 3.95 7216 26.44 Exclusion region .30 0 .45 8613 . .28 0 .45 7280 2.17 If Manhattan/Brooklyn .54 1 .49 8613 . .48 0 .50 7280 7.94

Notes: This table summarizes key variables for non-tax-exempt (ﬁrst row) and tax-exempt (second row) buildings. Sample restricted to buildings developed after 1990. Building area refers to the gross square feet residential area developed in the building. High income is a dummy that takes value one if the parcel is located in above median income census tract. Imputed Rent is inferred using Department of Finance’s market valuation. If condo is a dummy that indicates if parcel also contains condonium units. Exclusion region is a dummy indicating if the building is located in exclusion regions which experienced tax increase as part of the tax reform. Data: Primary Land Use Tax Lot Output, 2015 and Department of Finance 421a exemption list 2015.

180 Table 3.3: Descriptives: Rental parcels in New York City in 2007

Mean SD Min p25 p50 p75 Max N Non-exclusion region Assessed value land 436195.25 1441824.5 2373.3333 74000 149000 375000 80300000 13134 Residential area 60771.53 176127.41 1173.9131 17400 34330.17 63237 13498063 13134 Residential units 63.69 154.8 11 21 39 65 10914 13134 Lot area 26586.48 103171.12 1208 5300 10000 18000 5048550 13134 No. Buildings 1.82 5.39 1 1 1 1 109 13134 Market value per sqft 57.09 33.23 .56 36.94 48.55 68.11 689.83 13134 Imputed Rent 686.05 392.77 5.75 459.63 594.34 805.13 8604.19 13134 Rental stock 836575 0 836575 836575 836575 836575 836575 13134 Exclusion region Assessed value land 1307870.5 4871917 2562.2222 129000 351000 866000 3.148e+08 16643 Residential area 46875.48 132196.81 100 9860 17281.77 42000 8897465 16643 Residential units 49.860 137.36 11 16 23 43 8756 16643 Lot area 11104.04 54368.63 825 2564 4800 9372 4444613 16643 No. Buildings 1.23 1.28 1 1 1 1 54 16643 Market value per sqft 129.94 137.84 .57 61.86 107.74 178.58 14094.16 16643 Imputed Rent 1462.98 1514.71 3.185 644.05 1037.23 1703.94 31936.91 16643 Rental stock 829826 0 829826 829826 829826 829826 829826 16643 Notes: Summary statistics of rental buildings in 2007. Rental buildings include parcels classiﬁed as type C, D or S and having at least 10 units. Imputed Rent is obtained by dividing annual full market value by 12 times the number of residential units in the parcel times the average capitalization rate during this period- which is 6%. Imputed Rent and Market Value are expressed in 2015 US dollars using urban CPI tables provided by BLS. Rental stock denotes total rental units stock in buildings with at least ten units. Data: Primary Land Use Tax Lot Output, New York City, 2001-15.

181 Table 3.4: Descriptives: Rental parcels in Brooklyn in 2007

Mean SD Min p25 p50 p75 max N Non-exclusion region Assessed value land 415871.81 1141634.1 4400 78000 184000 395000 22600000 4487 Residential area 55626.24 109740.99 1173.91 16640 31480 60000 1788439.3 4487 Residential units 57.77 104.59 11 19 36 60 1760 4487 Lot area 21296.154 67464.586 1500 5300 10000 15717 1410820 4487 No. Buildings 1.40 2.55 1 1 1 1 78 4487 Market value per sqft 54.92 29.20 6.22 37.73 46.474 63.997 689.83 4487 Imputed rent 681.81 389.84 11.57 480.36 595.28 773.97 8604.19 4487 HS 259246 0 259246 259246 259246 259246 259246 4487 Exclusion region Assessed value land 261069.5 784087.79 3951.1111 48250 80000 195500 14400000 2444 Residential area 40003.16 91482.79 1008.33 11751 18521 35190 1466751 2444 Residential units 43.5 98.56 11 16 22 38 1836 2444 Lot area 14339.81 47532.54 1296 4000 5750 10200 1079791 2444 No. Buildings 1.34 1.99 1 1 1 1 54 2444 Market value per sqft 78.71 52.66 2.34 44.640656 65.1 97.62 550.8 2444 Imputed rent 893.31 707.75 24.36 499.58 725.05 1078.9497 16172.89 2444 HS 106311 0 106311 106311 106311 106311 106311 2444 Notes:Summary statistics of rental parcels in 2007. Sample restricted to parcels in Brooklyn. Rental parcels include parcels classiﬁed as type C, D or S and having at least 10 units. Imputed Rent is obtained by dividing annual full market value by 12 times the number of residential units in the parcel times the average capitalization rate during this period- which is 6%. Imputed Rent and Market Value are expressed in 2015 US dollars using urban CPI tables provided by BLS. Rental stock denotes the total rental units stock situated in buildings with at least ten units. Data: Primary Land Use Tax Lot Output, New York City, 2002-16.

Table 3.5: Excess housing starts in the time-notch

2007 Btotal Region Btotal Hs 2007 × 100 Hs New York City 10735 1043496 1% Manhattan 3097 661940 0.4% Brooklyn 5016 234866 2.1% Bronx 213 24380 0.8% Queens 2541 37336 6.8%

2007 Notes: Hs denotes the stock of rental housing (buildings classiﬁed types C ,D and S) in 2007 in the exclusion region in the speciﬁed borough. Btotal denotes excess bunching in property tax exempt unit housing starts in the notch period, 2006-2008. Excess bunching is calculated as the difference in bunching mass and the counterfactual.

182 Table 3.6: Effect of new tax-exempt residential investment on rents: IV estimates

RF IV OLS RF IV OLS 1(Land == 1) × Post 0.0251 0.0685 [0.018] [0.000] NotchUnits × Post 0.0239 0.000692 0.0690 0.00122 [0.052] [0.099] [0.003] [0.001] Constant 4.097 4.098 4.092 4.095 K-Paap F Stat 12.58 12.00 Cragg-Donald F Stat 982.93 982.93 First stage 1.049 0.993 Observations 341651 341651 341651 344794 344794 344794 Rings 24718 24718 24718 24718 24718 24718 Region F.E. Census tract Census tract Census tract Zipcode Zipcode Zipcode Notes: p-values in brackets. Outcome variable is building-year log rent per square feet. The endogenous treatment variable is the number of tax-exempt units within 150 meters from an existing rental building at the time-notch. The instrument is a dummy which indicates whether the building had one or zero vacant parels availlable within 150 meters a year before the reform. Standard errors are clustered at the building level. All regressions include building, year and regionXyear ﬁxed effects with the region as speciﬁed in the ‘Region’ row. Regressions are weighed by the number of residential units in the building. Please refer to Section 3.3.2 for the measurement of rental income and sample construction. Data: Primary Land Use Tax Lot Output, New York City, 2002-16.

Table 3.7: Effect of new tax-exempt residential investment on rents: Exclusion vs non-exclusion regions

Reduced Form IV Estimate OLS Estimate Non-exclusion Exclusion Non-exclusion Exclusion Non-exclusion Exclusion 1(Land == 1) × Post 0.0162 0.0305 (0.224) (0.058) NotchUnits × Post 0.0660 0.0176 0.000477 0.000881 (0.358) (0.102) (0.490) (0.068) Constant 3.743 4.473 3.744 4.475 (0.000) (0.000) (0.000) (0.000) Kleibergen-Paap Stat 2.038 11.15 First stage 0.246 1.733 Observations 149685 191669 149685 191669 149685 191669 Buildings 10899 13819 10899 13819 10899 13819 Notes: p-values in brackets. Outcome variable is building-year log rent per square feet. The endogenous treatment variable is the number of tax-exempt units within 150 meters from an existing rental building at the time-notch. The instrument is a dummy which indicates whether a building had one or zero vacant parels available within 150 meters a year before the reform. Standard errors are clustered at the building level. All regressions include building, year and regionXyear ﬁxed effects. Regressions are weighed by the number of residential units in the building. Please refer to Section 3.3.2 for the measurement of rental income and sample construction. Data: Primary Land Use Tax Lot Output, New York City, 2002-16.

183 Table 3.8: Effect of new tax-exempt residential investment on demographics: IV estimates

Log Log %%%% Units Median Rent Income Educ White HH Young HH New (Tax-exempt Projects≥ 1) X Post 762.5 0.334 0.242 20.83 17.28 7.496 0.212 [0.000] [0.001] [0.044] [0.000] [0.010] [0.066] [0.348] First stage F-stat 20.78 20.78 20.78 20.78 20.78 20.78 20.78 Dep Var. Mean 1459.9 6.938 10.74 27.02 47.40 22.07 0.625 OLS Estimate 109.4 0.0893 0.110 6.417 3.650 3.688 0.126 OLS SE 16.27 0.0104 0.0158 0.717 0.800 0.572 0.0279 Observations 4503 4503 4503 4503 4503 4503 4503 Notes: Units denote total occupied units in the census tract. Variables in Column 2 and 3 denote log of median rent and income respectively. Educ denotes % population with at least a Bachelor’s degree. White denotes % of households where the household head is white. Young HH denotes % population with household head age less than 35 years. New takes value 1 if the tract median move in year lies in past 10 years. All regressions include census tract and year ﬁxed effects. p-values in brackets. Standard errors clustered at the 2000 census tract level. Data source: Census 2000, American Community Survey 2005-09, 2012-17.

Table 3.9: Effect of new tax-exempt residential investment on rents: Short-term vs long term

RF IV RF IV RF IV RF IV Short-term 1(Vacant = 1)xYear ∈ (2006,08) 0.0466 0.0944 (0.002) (0.000) 1(NotchUnits)xYear ∈ (2006,08) 0.0445 0.0952 (0.063) (0.001)

Long-term

1(Vacant==1)xYear ≥ 2010 0.0154 0.0568 (0.296) (0.000) 1(NotchUnits)xYear ≥ 2010 0.0146 0.0569 (0.345) (0.006) Kleibergen-Paap Stat 6.533 6.534 11.98 12.03 Region Tract Tract Tract Tract Zipcode Zipcode Zipcode Zipcode Observations 219797 219797 244123 244123 221818 221818 246361 246361 Notes: p-values in brackets. Outcome variable is building-year log rent per square feet. The endogenous treatment variable is the number of tax-exempt units within 150 meters from an existing rental building at the time-notch. The instrument is a dummy which indicates whether a building had one or zero vacant parels available within 150 meters a year before the reform. Standard errors are clustered at the building level. All regressions include building, year and regionXyear ﬁxed effects with region speciﬁed in the ‘region’ row. Regressions are weighed by the number of residential units in the building. Please refer to Section 3.3.2 for the measurement of rental income and sample construction. Data: Primary Land Use Tax Lot Output, New York City, 2002-16.

184 3.8 Marginal response as a function of distance calculation

Each point in Figure 3.17 provides the average causal response (ACR) of rents to the arrival of a tax-exempt unit, within a small distance s from the building, where s goes from 50 to 300 meters. In practice, we are often interested in the marginal change in rent effect of tax-exempt unit as the distance from the site increases by a small amount (MCR). We can infact use ACR to obtain MCR using the standard trapezoid approximation for the intergral. To see this, consider the relationship between MCR(s) and ACR(s) for small changes in distance ∆s:

ACR(s + ∆s) − ACR(s) MCR(s) = lim ∆s→0 ∆s

Each point s in Figure 3.17 represents one point on the ACR curve. Therefore, the above formula identiﬁes MCR(s) for each s ∈ {100,150,200,250,300}. The standard errors can be obtained through the delta method. 5960 Figure 3.45 shows that the IV estimate decreases the most as we move from 50 to 100 meters. MCR approaches 0 when the radius increases to 250 meters. This is consistent with the fact that the positive spillovers of new 421a construction on a rental building are higher when the construction is not too far away.

3.9 Data construction: Demographic outcomes

The data for demographic outcomes comes from Census 2000, American Community Survey (ACS) 2005-09 and 2013-17. Putting these datasets together faces three challenges. First, while Census 2000 and ACS 2005-09 uses census tract at 2000 boundaries, ACS 2013-17 uses census tract at 2010 boundaries. To make the tracts comparable, I obtain the relationship ﬁles from Census Bureau website. Using the percentage of population in 2010 tract contained in 2000 tract, I assign each 2010 to an equivalent population weighted 2000 tract.

59 1 In particular, V(MCR(s)) = 4 (V(ACR(s)) + V(ACT(s + ∆s)), assuming the two ACR estimates are uncorrelated.) 60See Diamond and McQuade (2016) for a non-parametric method to measure the effect of LIHTC on prices, as a function of distance.

185 The second challenge comes from missing outcome values for some census tracts in certain years. A statistic for a census tract is generally omitted if it falls below 10. This could lead to a biased sample. I circumvent this issue in two steps: i) I drop any census tract which is missing any outcome variable observation in any year; and ii) I restrict to census tracts that are observed each year, leading to a balanced panel of census tracts at 2000 boundaries. These sample restrictions imply that the ﬁnal sample is representative of relatively larger census tracts. Finally, the distribution of baseline vacant parcels in a census tract is skewed. 90% of the census tracts have less than 33 vacant parcels. But there are some parcels with number as high as 593. To keep the sample of census tracts comparable, I exclude census tracts with the number higher than the 90th percentile.

186 3.10 Supportive tables and ﬁgures

Figure 3.30: Political process for selection of the exclusion regions

Notes: This ﬁgure presents the political process by which new exclusion regions (or dark exclusion regions in Figure 3.1) were decided. Data source: New York City Independent Budget Ofﬁce.

187 Figure 3.31: 421a property tax exemption use over time

Notes: Sample restricted to Class 2 residential buildings (deﬁned 3 units and above)— only those that are eligible for the 421a property tax exemption.

Figure 3.32: Steps required for a work permit in New York City

Notes: This ﬁgure outlines the key steps in obtaining a work permit in New York City. Source: Department of Buildings

188 Figure 3.33: Quarterly tax-exempt housing starts by exemption type

189 Figure 3.34: Bunching estimates including CONDOS

190 Figure 3.35: Distribution of tax-exempt projects across building types

(a) Before the time-notch

(b) In the time-notch

191 Figure 3.36: Completion year of notch projects

Notes: The graph plots the distribution of the year of completion of tax-exempt projects that started in the time-notch. Data: Permits data matched with Primary Land Use and Tax Output 2002-16.

192 Figure 3.37: Effect of new residential investment on rents: OLS estimates

Notes: The graph plots the event study of the effect of a new tax-exempt project in the notch within 150 meters radius from an existing rental building on its rents. The regression includes building, year, and zipcodeXyear ﬁxed effects. It is weighted by the number of residential units in the building. 5% conﬁdence interval clustered at the building level are plotted on the graph. Please refer to Section 3.3.2 for the measurement of rental income and sample construction. Data: Primary Land Use Tax Output, 2002-16 and Department of Buildings permits, 2001-15

193 Figure 3.38: Total investment in within 150 meters from the building

Notes: This ﬁgure plots the total investment within 150 meters radius from an existing rental building. The buildings sample is divided into three subsamples i) rental buildings that did not have a single vacant parcel within 150 meters distance; ii) buildings that had exactly one vacant parcel within the same distance; and ﬁnally, iii) buildings that had more than one vacant parcel available within the same distance. The y-axis denotes the average yearly logarithm of permits issued for any building/parcel. The permits include application for New Building (NB), Demolition (DM) or a major renovation that changes occupancy (A1). Data: Primary Land Use Tax Output, 2002-16 and Department of Buildings permits, 2001-15.

194 Figure 3.39: Alterations and renovations

Notes: This ﬁgure plots the difference in permits for minor alterations and renovations (designated as ‘A2’) issued for buildings located near rental buildings with zero vacant parcels within 150 meters and buildings near existing buildings with one or more vacant parcels within 150 meters. Data: Primary Land Use Tax Output, 2002-16 and Department of Buildings permits, 2001-15.

195 Figure 3.40: Heterogeneity test

Notes: Data trunacted to less than 500 units. Figure 3.41: Foreclosures in 2008 in New York

Notes: Figure from NYU Furman center report 2008

196 Figure 3.42: Alternative counterfactual: Commercial and family homes starts

Figure 3.43: Alternative counterfactual: Non-tax-exempt starts in the non-exclusion regions

197 Figure 3.44: Relationship between market valuation and rental income of the building

Notes: This ﬁgure plots the relationship between (log) rental income per square feet from a building and (log) market value per square feet. The latter assessed by the Department of Finance is used to determine annual property tax liability of a building. R2 = 0.94. Data: Comparable condos and coops, Department of Finance 2009-15.

198 Figure 3.45: Marginal rent effect as a function of distance

199 Table 3.10: Summary statistics for non-notch and notch properties in 2015

Mean Median SD N T-test Building area 13152.702 4146 48192.697 4644 21344.83 5118 64792.689 745 -3.3073834 Res units 12.128984 3 45.001232 4644 20.296644 4 63.895911 745 -3.3579692 Lot area 3912.1051 2437 6996.7107 4644 4806.9987 2500 7289.0423 745 -3.1278333 No. Buildings 1.1302756 1 .65041666 4644 1.0939597 1 .33081607 745 2.3540461 Imputed Rent 1819.5576 1477.0795 1485.3728 556 2322.8212 2032.8167 1751.3924 152 -3.2385606 If High-income region .2459087 0 .43067105 4644 .35436242 0 .478641 745 -5.8183106 Age 11.300195 11 4.1481946 4607 7.0175676 7 1.3459565 740 54.46332 Exclusion region .22200689 0 .41564051 4644 .38389262 0 .486659 745 -8.5907678 If Manhattan/Brooklyn .32988803 0 .47022285 4644 .52751678 1 .49957765 745 -10.103428 Notes: This table summarizes key differences in parcels that started outside the time-notch (ﬁrst row) and those that started during the time-notch (second row) as of 2015. Sample restricted to parcels that contain non-condo buildings and that were built after 1990. Building area refers to the gross square feet residential area developed on the parcel. High income is a dummy that takes value one if the parcel is located in above median income census tract. Imputed Rent is inferred using Department of Finance’s market valuation. Exclusion region is a dummy indicating if the parcel is located in exclusion regions which experienced tax increase as part of the tax reform. Data: Primary Land Use Tax Lot Output, 2015 and Department of Finance 421a exemption list 2015.

200 Table 3.11: Effect of new tax-exempt residential projects on rents: IV Estimates

Reduced Form IV Estimate OLS Estimate 1(Land == 1) × Post 0.0251 (0.018) NotchProjects × Post 0.659 0.0285 (0.029) (0.060) Constant 4.097 4.098 (0.000) (0.000) Kleibergen-Paap Stat 37.20 First stage 0.0381 Observations 341651 341651 341651 Rings 24718 24718 24718

Notes: p-values in brackets. Outcome variable is building-year log rent per square feet. The endogenous treatment variable is the number of tax-exempt units received by an existing rental building within 150 meters in the time-notch. The instrument is a dummy which indicates whether a building had one or more than one vacant parels within 150 meters a year before the reform. Standard errors are clustered at the building level. All regressions include buiding, year and regionXyear ﬁxed effects. Regressions are weighed by the number of residential units in the building. Data: Primary Land Use Tax Lot Output, New York City, 2002-16.

Table 3.12: Alternative instrument 0 and ≥ 1 vacant parcels: IV Estimates

RF IV OLS RF IV OLS 1(Land >= 1) × Post 0.0454 0.0942 (0.000) (0.000) NotchUnits × Post 0.0488 0.000700 0.107 0.00128 (0.003) (0.088) (0.000) (0.001) Constant 4.092 4.094 4.088 4.093 (0.000) (0.000) (0.000) (0.000) Kleibergen-Paap Stat 15.04 15.36 First stage 0.930 0.882 Observations 355146 355146 355146 358218 358218 358218 Rings 25681 25681 25681 25681 25681 25681 Region F.E. Census tract Census tract Census tract Zipcode Zipcode Zipcode

Notes: p-values in brackets. Outcome variable is the building-year log rent per square feet. The endogenous treatment variable is the number of tax-exempt units received by an existing rental building within 150m in the time-notch. The instrument is a dummy which indicates whether a building had one or more than one vacant parels within 150 meters a year before the reform. Standard errors are clustered at the building level. All regressions include the buiding, year and regionXyear ﬁxed effects. Regressions are weighed by the number of residential units in the building. Data: Primary Land Use Tax Lot Output, New York City, 2002-16.

201 Table 3.13: Adjusting for spatial correlation: IV Estimates

Reduced Form IV Estimate OLS Estimate 1(Land == 1) × Post 0.02 (0.02) [0.02] NotchUnits × Post 0.023 0.0006 (0.01) (0.07) [0.052] [0.09]

Observations 341069 341069 341069

Notes: p-values adjusted for spatial correlation in parantheses. p values with standard errors clustered at the building level are reported in the square-brackets. Standard errors are adjusted according to Conley (2016). Distance cutoff (for spatial correlation) = 1km, Lag cutoff (for serial correlation) = 15. Yi Jie Gwee provided the code to adjust IV estimates. The code builds upon Conley (2016), Hsiang (2010), and Fetzer [link]. Observations are at building- year. Outcome variable is log rent per square feet. The endogenous treatment variable is the number of tax-exempt units within 150 meters from an existing rental building at the time-notch. The instrument is a dummy which indicates whether the building had one or zero vacant parels available within 150 meters a year before the reform. All regressions include building, year and 2000 census-tractXyear ﬁxed effects. Regressions are weighed by the number of residential units in the building. Please refer to Section 3.3.2 for the measurement of rental income and sample construction. Data: Primary Land Use Tax Lot Output, New York City, 2002-16.

Table 3.14: Effect of new residential investment on rents: Elasticity estimates

RF IV OLS RF IV OLS 1(Land == 1) × Post 0.02 0.05 (0.02) (0.00) [0.02] [0.00] NotchUnits H × Post 1.86 0.033 4.95 0.05 (0.01) (0.01) (0.00) (0.00) [0.075] [0.01] [0.008] [0.00] Constant 4.096 4.097 4.092 4.093 (0.000) (0.000) (0.000) (0.000) First stage 0.0129 0.0135 Observations 341069 341056 341056 344212 357623 357623 Buildings 25639 25639 25639 25639 25639 25639 RegionXYear F.E. Census tract Census tract Census tract Zipcode Zipcode Zipcode Notes: p-values with standard errors adjusted for spatial (1km) and serial correlation (15 periods) are reported in parantheses. p-values with standard errors clustered at building level in square brackets. Outcome variable is building-year log rent per square feet. The endogenous treatment variable is the number of tax-exempt units within 150 meters from an existing rental building at the time-notch, expressed as percentage of existing rental stock. The instrument is a dummy which indicates whether a building had one or zero vacant parels available within 150 meters a year before the reform. All regressions include building, year and regionXyear ﬁxed effects. Regressions are weighed by the number of residential units in the building.

202 Table 3.15: Leave a borough out: IV Estimate

(1) (2) (3) (4) (5) 1(Land == 1) × Post 0.0207 0.0263 0.0227 0.0246 0.0241 (0.289) (0.086) (0.067) (0.050) (0.051) Kleibergen-Paap Stat 7.352 8.249 10.66 12.23 12.55 First stage 0.687 1.099 1.273 1.072 1.053 Observations 190521 270077 262145 304590 339271 Rings 24718 24718 24718 24718 24718 Borough removed Manhattan Bronx Brooklyn Queens Staten Island

Notes: p-values in brackets. Outcome variable is log rent per square feet. Observations are building-year. The endogenous treatment variable is the number of tax-exempt units received within 150 meters from an existing rental building in the time-notch. The instrument is a dummy which indicates whether a building had one or zero vacant parels available within 150 meters a year before the reform. Standard errors are clustered at the building level. All regressions include building, year and 2000 census-tractXyear ﬁxed effects and are weighed by the number of residential units. Please refer to Section 3.3.2 for the measurement of rental income and sample construction. Data: Primary Land Use Tax Lot Output, New York City, 2002-16.

Table 3.16: Demographics statistics: Exclusion and non-exclusion regions

Non-Exclusion region Exclusion region Mean SD Mean SD Monthly rent 991.49 430.08 1415.50 1063.67 Total Income 44783.87 43024.10 75165.60 118052.94 Non-white household .49 .50 .36 .48 Above median income .43 .49 .55 .49 Persons in household 2.49 1.54 2.07 1.31 Tenure .47 .49 .48 .50

Notes: This table reports key demographics statistics in exclusion and non-exclusion regions in 2005. Sample restricted to include Manhattan, Brooklyn and Bronx because they allow better identiﬁcation of sub-boroughs that were affected by the property tax reform. Monthly rent denotes the contractual rent reported in the survey. Total income refers to the sum of wage and non-wage household income. Non-white household is a dummy that takes value 1 if the household head is non-white. Above median income is a dummy that takes value 1 if the total household income is greater than the city median income. Tenure takes value 1 if the household moved into the current residence within past ﬁve years. Both monthly rent and Total income variables are expressed in 2015 US dollars. Data: New York Housing and Vacancy Survey, Occupied Units, 2005.

203 Table 3.17: Selected high and low income elasticity industries

4-Digit NAICS Code Description Industry Income Elasticity Industries with High Income Elasticity 6223 Speciality Hospitals (except Psychiatric and Substance Abuse) 2.4 5239 Other Financial Activities 2.2 5231 Securities and Commodity 2.18 5122 Sound Recording Industries 1.83 7114 Agents and Managers for Artists, Sports, Entertainers and Other Public Figures 1.58 7139 Other Amusement and Recreation Industries Industries 1.02 7224 Restaurants and Drinking Places 0.92 Industries with Low Income Elasticity 3323 Architectural and Structural Metals Manufacturing -0.46 6241 Individual and Family Services -0.51 3366 Ship and Boat Building -0.56 4859 Other Transit and Ground Passenger Transportation -0.63 5622 Waste Treatment and Disposal -0.63 4451 Grocery Stores -0.69 8111 Automative Repair and Maintenance -0.93

Notes: This table presents income elasticities for 4-Digit industries. Income elasticity for an industry reﬂects the strength of association between zipcode renter income and the number of industry establishments in the zipcode. Intuitively, establishments belonging to an industry with high income elasticity are more likely to be located in a high-income zipcode. Each industry’s elasticity is obtained as a coeffcient on log renter income in a regression of log number of establishments in an industry on the zipcode’s mean log renter income in 2001. There are approximately 300 industries observed in New York City sample in 2001. Data: County Business Patterns 2001 and Census 2000.

204 Bibliography

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217 Appendix A: Safer Elections, Women Turnout, and Political Outcomes:

Evidence from India

A.1 Data Construction

A.1.1 Booth-level turnout by gender

This subsection discusses the construction of the ﬁnal dataset used in the voting outcomes analysis. This dataset primarily uses information provided on each constituency’s "Form 20" released after the election. This form provides information on registered total number of voters, turnout by gender, votes polled for each candidate for every booth in the constituency. The original ‘Form 20’ provided by ECI was downloaded from the UP elections website in the summer of 2015. Putting the data together required few things. First, we harmonized excel sheets for 403 constituencies , separately for years 2009 and 2012. Second, we merged 2009 booth-level data with 2012 data using booth id. As we discuss below, this process was a non-trivial process. Here I document key issues that arose during the data construction process and how I addressed them.

Issues with individual excel ﬁles

1. Loading issues: For many constituencies, the excel files can not be loaded directly into STATA. Some of the reasons include irregular organization of the excel sheet, use of Hindi characters not picked up by STATA. To harmonoze these files, an RA manually opened each excel file and harmonized rows and columns which allowed for automated and direct import of these files into STATA. Nevertheless, some of the excel files were corrupt and hence were discarded altogether.

2. Missing columns: Some of the constituencies do not report either turnout by gender or reg-

218 istered voters (For example, AC 22, 27, 172, 174, 230, 269, 318). Unfortunately, the only solution was to drop such booths from the analysis. The ﬁnal dataset has 352 out of 403 constituencies.

3. Booth-id variable: There does not exist any pre-defined booth variable for booth identification. However, these files do report the ‘booth number’. I constructed a unique "booth_id", obtained by joining the reported booth number and the assembly contituency. Between 2009 and 2012, though the majority of the booths retained their number, some split into two or more. 1

4. Odd values in the booth number column: This issue arose when creating unique booth_id for each booth. Some of the booth numbers had string characters unreadable to STATA. This was manually checked and corrected to ensure that the booth number contains valid numbers only.

5. Inconsistent column values: There were two inconsistencies observed in turnout columns. First, for some booths, reported turnout was greater than the registered voters. Second, female turnout was negative in four booths. We retained the booths in the former category and replaced with the absolute value in the latter category. Finally, there were still cases where the maximum vote share in 2009 dataset was greater than 1 (around 355 observations). This was because either (i) the reported turnout was 0 (20% cases), or (ii) the max vote share variable had a missing value (49% cases) or (iii) the maximum vote share was greater than the total reported turnout (32%). The booths in category i) and ii) were dropped. I retained booths belonging to category (iii) because outcomes in such booth could indicate capture and they are more likely to beneﬁt from the intervention. There are 107 such booth observations.

Table 1.3 summarizes variables in the final dataset. 1In some files, there also exists a column for "booth name" which reports the establishment (generally a school) where the ballots are cast. However, this column is not available for all the booths and is often reported in local language which made it not very useful for the booth identification.

219 Issues with merging

In an ideal dataset, one could merge booth level voting outcomes in 2012 with those in 2009 through a booth_id. However, there is no such unique pre-defined variable in either dataset. In- stead, there does exist a booth number and an assembly constituency number which can be combined to create a psuedo booth_id variable. An issue arising with this exercise is that going from 2009 to 2012, three kinds of changes may occur for any booth: (i) a booth splits into two (more common); (ii) two booths split into three (very rare) and iii) two booths combine into one (again pretty rare but observed at least once). The newly added booths are often distinguished by a suffix such as ‘v’ or ‘b’. While booths with no suffix are a straightforward merge across the two years, it is not obvious how to merge a consolidated parent booth in 2009 with its split child booths in 2012. The number of booths with a suffix in each year is not non-substantial, around 7% of booths in 2009 data have a suffix. Among the parent booths which were already split in 2009 (and hence that booth number was accompanied with a child booth with a suffix), I assume that the order of the booths is unchanged across the years (even though the suffix might be different for the child booth in 2012), I create a unique identifier for the child booth in either case and merge them. I dropped the booths which underwent a merge between 2009 and 2012 but retained all the booths which underwent a split. This is because intervention in 2012 depends on the polling outcomes in 2009 and the probability of intervention is clearly identified for booths that descend from the same parent booth.

220 Appendix B: Do Property Tax Incentives for New Construction Spur

Gentriﬁcation? Evidence from New York City

221 B.1 Data

Tax-Pluto Data

PLUTO and MapPLUTO provide a detailed record of every piece of land in New York City, referred to as a tax-lot. An average tax plot in NYC consists of 1.26 buildings. PLUTO (short for “Property Land Use Tax [Lot] Output”) lists properties at borough-block-tax lot level and provides useful information regarding the property such as address, number of residential and total units, residential and commercial square footage, year built, lot and building area, owner name and number of floors. MapPLUTO provides shape files containing precise geographic location of properties on the map. Note that under NYC real property law, condos are assessed separately from the traditional tax lot (or a parcel) and are represented by a condonium tax-lot that is different from a traditional tax-lot. A traditional parcel may contain serveral buildings, each comprising of several condos. PLUTO data lists information at the traditional tax-lot level and not condonium unit level. Each parcel in NYC is uniquely identified by its borough-block-tax lot (referred to as a BBL). BBL consists of three numbers: the borough, which is one digit (coded alphabetically 1-5); the block number, which is upto five digits; and the lot number, which is upto four digits. Each condo, on the other hand is identified by borough-block- condo tax lot (referred to as condonium BBL). To identify all condos that share the same parcel, PLUTO data can be merged with another dataset called Property Address Directory (PAD) which contains the directory of condos and their billing BBLs. The Pluto and Map-pluto data was accessed from NYC’s website in March 2018 and provides data updated as of October 2016. The link is as follows: https://www1.nyc.gov/site/planning/data-maps/open-data/dwn-pluto-mappluto. page

Geographic Exclusion Boundaries

I obtained the map of exclusion regions from NYC’s website. I digitized the map using QGIS to create a shape ﬁle which I then merged with PLUTO data to identify whether a parcel (identiﬁed

222 by its BBL) is located in exclusion or non-exclusion regions. The original map can be found at the following address: https://www1.nyc.gov/assets/hpd/downloads/pdf/GEA_Map.pdf

Property Address Directory

While PLUTO contains rich information at the billing-lot or building level and not at tax- lot level. While tax-lot and billing-lot are essentially same for all rental properties and coops, they differ for condos which are individualy owned and assessed separately from the building. To identify condos within a building, I use PAD (Property Address Directory) which provides a crosswalk between billing BBLs and tax BBLs. This directory also provides corresponding BIN (Building Identiﬁcation Number) for each BBL which is useful in merging permits data with PLUTO and 421a dataset. The 2018 version of this dataset was downloaded from the following website in May 2018. https://www1.nyc.gov/site/planning/data-maps/open-data.page

Investment or permits dataset

While PLUTO provides characteristics of properties in stock, more important to my analysis is daily permit issuance data, maintained by the Department of Buildings, which provides information on permits issued at the parcel-month level. This dataset contains universe of permits issued for any parcel in New York City from 2003 to 2014. A parcel undergoing any major alteration or construction must ﬁrst obtain a permit from the Department of Buildings. These include permits issued for demolition (permit type denoted as ‘DM’), for new building construction (permit type denoted as ‘NB’) and major alteration (permit type denoted as A1) that changes occupancy structure of the building. I restrict my analysis to DM, NB and A1 type permits only. Also, I focus on ‘initial’ issuance of permits and ignore ‘renewal’ permits in all my analysis. See: https://data.cityofnewyork.us/Housing-Development/Historical-DOB-Permit-Issuance/ bty7-2jhb/data

Properties with 421a exemption or ‘421a dataset’

I downloaded the NYC Department of Finance’s report on all properties receiving the 421a

223 partial tax exemption listed by borough, block, tax-lot, neighborhood, building class, tax class and address. This dataset lists all condos and buildings that received the 421a Tax Exemption in ﬁscal year 2015-16. The combination of borough, block and tax-lot forms the unique property identiﬁer (tax-BBL) which I use to merge this dataset with others. See: https://www1.nyc.gov/site/finance/benefits/benefits-421a.page Sales data

The department of ﬁnance makes available the date on every transaction of a property located in NYC. This dataset is hosted on their website and covers the period 2003 to today. Each property, whether a condo, co-op or a building is identiﬁed by its unique tax BBL in this dataset. See: https://www1.nyc.gov/site/finance/taxes/property-annualized-sales-update. page

Data on establishments and local businesses

An important part of the exercise is to determine how local businesses react to the new residential investment brought by the reform. For this purpose, I use two main datasets. New York City requires certain businesses to apply for DCA (Department of Consumer Affairs) license before beginning operations. These include businesses such as sidewalk cafes, laundries, home-improvement contractors The dataset provides information on license creation date and the geocoded location of the business. This allows me to measure changes in licenses granted over time and space. A disad- vantage of this dataset is that it includes selected businesses and major businesses such as retail and restaurants are excluded because they do not require a Department of Consumer Affairs license. Therefore, I supplement the analysis by using County Business Patterns 2001-15, which lists the total number of establishments in each 6-digit NAICS (North American Industry Classiﬁcation System) industry located in a zipcode-year. New York City Housing and Vacancy Survey

New York City’s Housing and Vacancy survey (NYCHVS), sponsored by the New York City Department of Housing Preservation and Development (HPD), is conducted every three years to comply with New York state and New York City’s rent regulation laws. The survey uses most

224 recent census data to survey households living in the city, either as tenants or homeowners. For each household, it provides information such as tenure, current and previous place of residence, income and race. The lowest geographic unit is sub-borough, which is a group of census tracts summing to at least 100,000 residents, determined by NYC HPD. The boundaries of sub-borough areas often approximate community districts.

Figure B.1: Geographies in New York City datasets

Notes: This figure shows relevant identifiers in . BBL denotes a parcel (billing-tax-lot) which may contain one or more buildings. Each building is associated with a unique identification number called BIN. Investment (permits) data is at the building level (identified by unique BIN) whereas rents/market valuation dataset is at the parcel level (BBL). Further, sales dataset is either at the apartment (identified by the ‘tax’ BBL) or building level (identified by ‘billing’ BBL). A parcel contains approximately a building. The unit of analysis in the paper is a parcel (identified by a billing BBL).

225 B.2 Property taxes in New York City

Property tax for all classes, is determined according to the following formula:

Annual tax = tax rate×[assessment rate × Annual Market Value −Exemption]−Abatement (B.1) | {z } AssessedValue

There are several components that determine a landlord or homeowner’s annual property tax bill. First, assessment ratio determines the fraction of market valuation subject to property tax. For instance, this ratio is 6% for one-family homes and 45% for rental buildings. 1 Second, exemptions reduce the assessed value. Some of the available exemptions include STAR, Enhanced STAR, Senior Citizen and Disabled Homeowners’ exemption. 421a property tax exemption, available for larger residential buildings with at least 3-4 units reduces assessed value to the pre-contruction assessed for a signiﬁcant period.. Finally, abatements, similar to a tax credit, reduce the tax bill dollar for a dollar. Condo-coop abatement is a major abatement available to owners of condos and coops who use it for their primary residence. 2 Tax rate, assessement ratio, market valuation determination and the availability of various abatements and exemption depend on the tax class a property belongs to. Properties in New York City are divided into four tax classes. Class 1 properties include one-to-three family homes. Class 2 properties include large rental buildings, condos and coops, properties that are focus of the analysis in this paper. Class 3 properties include utilities. Class 4 properties include commercial buildings, ofﬁces, factories and warehouses. Though both owner occupied units and apartments buildings are residential, they are subject to different tax rates and assessment ratios. While Class 1 properties are assessed at 6% of their full market value, class 2 properties are assessed at 45%. The process of development in the city is quite similar to elsewhere. Developers buy vacant land and raise money; obtain permit from Department of Buildings to begin construction. They

1This implies that at the tax rate of say 20%, a household living in a one-family home valued at $100,000 will pay an annual tax of $1,200. 2See https://www1.nyc.gov/site/finance/taxes/property-assessments.page for more details.

226 can chose to build family homes, purely rental buildings, or mixed condo buildings. 3

Property taxes on rental rroperties in New York City

Property taxes form a signiﬁcant share of operation costs of rental developments in New York. Tax rates, assessment formula and assessment rate all contribute to the high property tax. Rental buildings are assessed on the basis of their net rental income, where net rental income is deﬁned as the difference between gross income and operating expenses 4 For this reason, all landlords of rental buildings greater than 10 units are required to submit Real Property Income and Expense form annually where they declare their annual revenues and expenses. The Department of Finance adjusts the net rental income for risk, liquidity and capitalization to obtain their annual market valuation. In general,

1 Annual market value = [Rental Income - Expenses] × (B.2) Capitalization rate

Capitalization rate is determined annually on the basis of risk, liquidity and management costs. It is equal to 16% on average which suggests a capitalization factor of around 6. Using equations B.1 and B.2, tax rate of 12% and capitalization factor of 6, we can determine the net tax burden on rental income (net of expenses) generated by the property tax. The effective tax rate on net rental income is given by:

12 × 0.45 × 6 × NOI ETR = = 32.4% NOI

This suggests that upto 33% of the landlord’s net rental income is spent towards the payment of the property tax, quite high.This suggests that the 421a property tax exemption that reduces the tax on new investment is quite valuable to a developer of rental property. Figure 3.35 shows that a large share of buildings that beneﬁt from 421a tax exemption are classiﬁed as C (rental walk-ups),

3There are almost no new co-ops built in recent decades. A co-op is an LLC where the owner of each unit owns shares equivalent to the size of his unit. The co-op board is responsible for the maintainence of the common spaces. 4In contrast, family homes are assessed on the basis of sales price of similar properties nearby.

227 D (rental buildings with elevator) or R (condos). Finally, Figure 3.44 shows that the correlation between log rental income and log market valuation of rental properties is strong and close to 1. 5 This implies that annual market valuation serves as a good proxy for the rental income buildings.

B.3 Effect of the tax reform on property tax across regions

In this section, I illustrate that 2006-08 tax reform of 421a property tax exemption had differential impact on the three regions in Figure 3.1: Light shaded region (old-exclusion region, blue colored), dark unshaded region (new-exclusion region, dark blue colored), and light unshaded region (non-exclusion region, yellow colored). In particular, I show that in the light shaded region, the reform effectively removed the tax exemption by making onsite provision of affordable units mandatory. In dark unshaded region, the reform either did not affect tax incentives or it completely removed them, depending on the cost of providing affordable housing onsite. Finally, in the light unshaded regions, the reform did not alter exemption beneﬁts signiﬁcantly. Light shaded regions (old exclusion region)

Prior to the reform, the developers were required to provide affordable housing but they could choose to do so offsite. By allowing the developer to build offsite in relatively low-rent regions, the ofﬁste option provided signiﬁcant cost savings to the developer. In fact, I show here that taking away the option to provide affordable housing offsite imposed compliance costs under the property tax exemption equivalent to an increase of property tax between 4 and 5 percentage points. Given the statutory property tax rate of around 5.5% faced by a developer with no exemption, the tax- reform effectively made the property exemption in light shaded regions regions unattractive. To see why this is the case, consider that an average rental building in light shaded region has 56 units and can expect to get at least $34,820 (2015) USD per year from a single market rent unit. In contrast, a developer can expect to get at most $14,013 from an affordable unit in the building. This is because for a 4 person family, the 50% Area Median Income (AMI) is $38,400

5This uses ‘comparable rental properties’ data provided by DoF. This dataset provides comparable rental properties used to determine market valuation of nearby condos and coops. Condos and coops in NYC are assessed on the basis of their ‘imputed rental income’ instead of recent sales that family homes are assessed on.

228 and therefore, the maximum rent the developer can charge is 30% of this income limit (See HUD source for a list of AMI for different years.) 6. Note that the maximum rent the developer can charge in an affordable unit is ﬁxed throughout the city, irrespective of variation in local rents across neighborhoods within the city. With onsite affordability requirement, the developer must keep 11 out of 56 units affordable with a discount of $34820 − $14013 = $20807 on each affordable unit. Total cost imposed by onsite affordability requirement is therefore, $228,877, which suggests an effective tax rate of

228877 5∗56∗34820 × 100 = 2.3%. If we use a higher capitalization factor (such 6), we get an effective tax rate of up to $1.9%. Previously, with the offsite affordability option, this tax rate was effectively zero. Therefore, the 2006-08 reform removed the tax break and therefore, increased the effective property tax rate on future projects in light-shaded regions. Dark unshaded regions (new exclusion region)

The major change brought by the reform in dark unshaded regions included the elimination of short exemption which provided exemption from property taxes for 15 years without affordable housing requirement. Whether or not the reform effectively altered the tax benefits in these regions depends on whether the second best option—long exemption with onsite affordable housing requirement—–is a worse option than obtaining no exemption at all. This in turn depends on how local rents compare with the affordable rent. In low-rent regions, the long exemption would still be a better deal because of low discount on affordable rents. On the other hand, in high-rent regions, long exemption with affordable housing requirement is less lucrative because of high discount on affordable units. This is because the rent a developer can expect from an affordable unit is fixed throughout the city, irrespective of variation in rents across neighborhoods within the city. To see why location of a neighborhood within the dark region matters in determininng whethere long exemption is profitable, consider the following case. According to the raw data, an average rental building 7has an annual market value of $ 3,088,948 in 2015 US dollars. This implies an

6Because AMI varies from year to year, all calculations are based on 2008 AMI which is converted to 2015 USD. Additionally all calculations are based on income limit for a 4 person family, earning 50% of area median income. After 2012, all affordable units are advertised through online portal called nycconnect. 7i.e. a building classiﬁed as type C, D or S.

229 average annual property tax payment=$166,803. Net present value of this sum is given by:

166803(1 − (1 + i)−T ) NPV = i

For T = 25 and i = 15%, and no costs, the net present value of long tax exemption is $1,078,239.8 However, a developer must keep 20% of the units affordable to households with income between 30 and 100% of area median income, which adds to the cost under long exemption. The average annual income from a market rate rental unit in the dark regions in 2008 was about $12,187 and a building had on average 46 units. For an affordable unit, the developer can expect annual rental income of atmost $14,013. This is actually higher than the expected income from the market-rate unit, which suggests on average the costs under long exemption are minimal. However, the average masks substantial heterogeneity in rents within the dark regions. For instance, 95th percentile average annual rental income is about $34,423, which is much higher than the affordable rent limit. Annual cost of imposed by an affordable unit is then = 34,423−14,013. = 20,410 and total number of affordable units to be provided = 9. Using the net present value formula, we can see that the annual cost of long exemption for developer is then= $183,690, higher than the property tax savings under exemption. Therefore, we can expect the reform to drastically cut beneﬁts in high rent regions with no signiﬁcant change in low rent region within the dark unshaded region. This further suggests that the future marginal tax in dark regions either did not change or increased by 5.5% (the statutory tax rate) after the reform. Unshaded light regions (non exclusion region)

The only change brought by the reform in unshaded light regions was the introduction of a cap on beneﬁts under the short exemption. Because these regions are low-rent, the discount on

8I use i = 15 because this interest rate is consistent with the average capitalization rate used by Department of Finance in calculating market valuation of apartment buildings. DoF uses the capitalization rate to calculate the present discounted value of the annual rental income, which serves as the tax base for the property tax calculations for that year. See here, for example. In general, with capitalization rate of 15%, market valuation of a property with rental R income R is equal to 0.15 = 6.6 × R. Capitalization rate changes over the years, but is largely in the range of {13,17}.

230 an affordable unit is minimal and the long exemption is the most preferred option which was effectively unaffected by the reform. For instance, an average rental building in light unshaded region has an annual market valuation of about 2,755,881 US 2015 dollars and has around 65 units. This suggests that the rental income of the average building is about $459,313 or around 7000 per rental unit, much lower than the average income from an affordable unit. Therefore, long exemption imposes non-zero costs and the exemption lasts for a longer duration implying that long exemption is a clear winner in these regions. This further suggests that the change in effective property tax here as a result of the reform was insigniﬁcant.

231 B.4 Short Term Outcomes in the Time Notch

Let us suppose there are three periods j ∈ {0,1,2}. The world ends in period 2 and outcomes in period 2 refect the long-run. While there is uncertainty in periods 0 and 1, it disappears in period 2 (the long-run). Consider a region where the demand for housing in each period is increasing in

the level of amenities and decreasing in the net-of-tax rent Rj:

Aj Dj = Rj(1 + t)

The region starts with the baseline stock S0. Assume a depreciation rate of δ. Housing stock in any period is given by: Sj = Ij−1 + (1 − δ)Sj−1. The timing and long-run investment elasticities

(with respect to the property tax) are given by t and l respectively. Given a property tax t, the equilibrium in period j is given by Rj such that Dj = Sj. An important piece is that the amenities in region j, Aj respond to the current investment. New residential investment attracts more businesses to the region which makes it more attractive for investment in the future. Similar to Diamond (2016), I assume that amenities respond to the stock of residents at a point in time with a constant elasticity a,

a Aj = (Sj)

Policy 1: Unanticipated property tax increase

First, consider the when the tax increase is announced and implemented in period 1. This is illustrated in Figure 3.4a. Period 0 investment is unchanged because the developers are not aware of the policy change in period 0. Consequently, the decline in the net-of-tax rents in period 1 is equal to the tax increase.

∆logR1 = −∆log(1 + t) < 0 (B.3)

In the short-run, landlords bear the entire burden of the property tax increase as the supply does not

232 adjust quickly. However, in the long-run, developers shift some of the incidence onto the tenants through changes in investment. In fact, the lower net-of tax returns decreases period 1 investment

l l by ∆logR1, where is the rent elasticity of investment as discussed in the previous section. Lower period 1 investment affects period 2 rents through two channels: lower housing stock (the standard supply channel) and amenities (the indirect demand channel). In particular, the rent paid by the tenants in the long-run is given by:

∆ g ∆ − ∆ ( − ) ∆ ( ) logR2 = logA2 logS2 = a 1 l log 1 + t

= (a − 1)l∆log(1 + t) (B.4)

The rent paid by the tenants in the long-run is higher because a higher property tax reduces the long-run housing stock (a standard public ﬁnance result). However, this result holds with endogenous amenities only when the amenities in the region do not decline drastically in response to a lower long-run housing stock, that is a < 1. In fact, the rents paid by the tenants decrease in response to a property tax increase when a drop in the amenities makes the region less desirable. Tenants in that case must be compensated in the form of lower rents. In the end, which effects dominate (amenity effect which decreases the rent paid vs the supply effect which increases the rents paid) depends on the relative elasticities. Policy 2: Anticipated property tax increase

Now suppose that in period 0 the government announces that the property tax will increase, beginning period 1. In the long run, any short-term investment timing responses are reversed and

the long-run housing stock falls by l∆log(1 + t) and,

∆ g ( − ) ∆ ( ) logR2 = a 1 l log 1 + t (B.5)

While the long term outcomes B.4 and B.5 are the same, the medium term outcomes, characterized by rents in period 1 differ. Because the developers are aware of the future tax increase, they

233 have incentives to move the projects from period 1 to period 0 as illustrated in Figure 3.4b. High

t investment in period 0 increases the period 1 housing stock given by, ∆logS1 = ∆log(1 + t), where t > 0 denotes the timing property tax elasticity of residential investment, as discussed in the previous section. The period 1 net-of tax rent is given by:

t ∆logR1 = (a − 1) ∆log(1 + t) − ∆log(1 + t)

1 The above equation is positive when: a > 1 + . t

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