1 Vulnerability and Policy Response: Unintended Consequences DISSERTATION Presented in Partial Fulfillment of the Requirements F

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Vulnerability and Policy Response: Unintended Consequences

DISSERTATION

Presented in Partial Fulfillment of the Requirements for the Degree Doctor of Philosophy

in the Graduate School of The Ohio State University

Will Georgic, B.A., M.S.

Graduate Program in Agricultural, Environmental and Development Economics

The Ohio State University

2019

Dissertation Committee

H. Allen Klaiber, Advisor

Sathya Gopalakrishnan

Tim Haab

Copyrighted by

Will Cameron Georgic

2019

Abstract

There are three general methods for enhancing flood risk resiliency and reducing expected damages: insurance, protection, and retreat. In the United States, the policy portfolio associated with each approach can stand substantial improvement and examples of shortcomings are numerous. In this dissertation, I use models of land use and spatial equilibrium to inform methods of causal inference in order to analyze observed responses to policies aimed at reducing vulnerability. I then offer insights which could help guide improved policies moving forward. Chapters 2 through 4 of this dissertation address economic behavior in response to a unique policy or approach associated with either insurance, protection, or retreat.

Chapter 2: In 2017, the National Flood Insurance Program exceeded its borrowing capacity. While half the debt was forgiven, more will be accrued due in large part to premium subsidies for older, vulnerable properties. Efforts to phase out subsidies are slow, with policymakers and constituents concerned over the impacts of subsidy removal on housing markets. Using an exogenous break in subsidy eligibility specified in the original legislation, I estimate nationwide and metro region specific difference-in- differences models to identify the capitalization of subsidy eligibility in home values.

Given the well-known finding that flood insurance uptake is imperfect in 100-year

ii floodplains and in accordance with the predictions of a hedonic model with asymmetric information, I find a rate of capitalization within the bounds of outcomes resulting from fully informed market participants and from buyers and sellers with heterogeneous awareness, averaging approximately $12,000 per eligible residence. I further find that during a temporary removal of subsidies in 2012-2014, the capitalization of subsidies diminished, providing additional evidence of my causal mechanism, and supporting the most recent, pertinent legislation, The Homeowners Insurance Affordability Act of 2014.

Chapter 3: “The Levee Effect” is the phenomenon by which efforts to reduce expected damages from flooding through the construction of physical capital may actually increase expected damages through induced development. Though this effect was first hypothesized in 1945, it has not been rigorously empirically tested. In this chapter, I consider the development patterns in southeastern and central Florida following the Flood

Control Act of 1948 to estimate the impact of discrete levee construction on rates of housing development using a fixed effect Poisson regression and a nonlinear difference- in-differences identification strategy. I find that newly constructed levees increased the rate of residential development by over 50 percent when compared to what would have occurred in these areas had the levees never have been built. Extending my analysis to the

21st century, I use a duration model to characterize the optimal stopping decision inherent to land conversion and a control function to account for price endogeneity, and I find that the protection provided by levees creates a lasting effect on residential development patterns. While this analysis only represents the first stage in empirically

iii testing “The Levee Effect”, it provides evidence that newly constructed levees significantly increase housing construction without proper regulatory restrictions, potentially increasing (rather than decreasing) expected damages from flooding.

Chapter 4: Floodplain buyout programs across the country are plagued by low levels of adoption. While federal funds are available to support locally targeted efforts at reducing vulnerability, proposals must pass a cost-benefit analysis with limited scope for externalities. In this chapter, I show that accounting for spillovers from vulnerable property acquisitions significantly changes the cost-benefit calculation, potentially permitting more generous offers to be made. Using a novel and exhaustive dataset for housing transactions in Harris County, Texas, I find that a 200 meter reduction in the distance to the nearest buyout is associated with a $365 increase in the price of the average home, similar to the finding of $320 from the most similar study. However, this average effect masks important heterogeneity, suggesting that positive effects are likely in higher quality neighborhoods while negative effects are likely in lower quality neighborhoods. These results are robust to measurement and identification strategy variation and indicate that while more generous buyout offers may be permissible in higher quality neighborhoods, there may be unintentional inequities in how acquired land is processed across neighborhoods.

Dedication

To my parents, who have each sacrificed on a daily basis so that their sons could be truly

and positively free

Acknowledgments

“You have done such good to me I would do the same to you” – Walt Whitman

I have so enjoyed my graduate education that I cannot possibly fully express my gratitude in a few short paragraphs; still I will try. I owe my deepest thanks to my home department and the Graduate Studies Committee for providing every opportunity for me to succeed. Ultimately, any success that comes my way is a testament to my advisor,

Allen Klaiber, whose patient guidance has continually made me a better economist. I have received similar professional and academic mentorship from my committee members Sathya Gopalakrishnan and Tim Haab. I do not take these relationships for granted and I consider myself fortunate to have studied under such exemplary scholars.

I will always be grateful for the lifelong friends that I have made while at Ohio

State. My officemates David Wolf, Tim Jaquet, Xiao Dong, and Xiaoyu Li improved both the quality of my research and the quality of my life over the past several years. In addition to Dr. Wolf, I would like to thank Julio Acuna, Bo Feng, and Mark Rembert for their support, insight, and camaraderie in the early years of my education. We will forever be bound by our shared experiences and our common values.

I would not have found my calling in studying environmental economics without the advice and assistance of my undergraduate advisor, Ted Burczak, as well as Denison

University economics professors Fadhel Kaboub and Jessica Bean. Professors Xiao Jiang,

Andrea Ziegert, and Katherine Snipes have also helped me realize my professional goals, and for that I am sincerely thankful. Finally, I would be remiss if I did not thank my father-in-law, Dr. Steven Joyce, for so aptly demonstrating the daily fulfillment that accompanies a pursuit of the life of the mind.

The path to the completion of this degree has been long, and perhaps most treacherous before it even formally began. No one can attest to that more than my wife, and partner of nearly ten years, Genevieve. It is to her that I owe my greatest thanks for her undying support and faith in my potential. The flukes are at peace.

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Vita

2007...... Buckeye Valley High School

2011...... B.A. Philosophy, Political Science, and Economics, Denison University

2015...... M.S. AED Economics, The Ohio State University

Fields of Study

Major Field: Agricultural, Environmental and Development Economics

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Table of Contents

Abstract ...... ii Dedication ...... v Acknowledgments...... vi Vita ...... viii List of Tables ...... xi List of Figures ...... xii Chapter 1: Introduction ...... 1 Chapter 2: Do NFIP Subsidies Matter to Homebuyers? Evidence from Nationwide Housing Sales...... 4 2.1 The NFIP Experiment ...... 9 2.2 Capitalization with Potential Information Asymmetry ...... 13 2.3 Identification Strategy ...... 18 2.3.1 Hedonic Model of Subsidy Capitalization ...... 18 2.3.2 Difference-in-Differences Identification ...... 19 2.3.3 Fixed Effects in Hedonic Regressions ...... 22 2.4. Data and Summary Statistics ...... 24 2.5 Results ...... 26 2.5.1 The Capitalization of Pre-FIRM Subsidy Eligibility ...... 26 2.5.2 Spatial Heterogeneity ...... 30 2.6 Biggert-Waters: A Policy Experiment ...... 32 2.6.1 Background Literature and Identification ...... 32 2.6.2 Triple Difference Results ...... 34 2.7 Summary and Concluding Remarks ...... 40 Chapter 3: A Flood of Construction—An Analysis of the Role of Levees in Urban Floodplain Development ...... 43

3.1 Background ...... 47 3.2 Methodology ...... 53 3.2.1 The Poisson Model ...... 54 3.2.2 Difference-in-Differences Identification in Nonlinear Models ...... 56 3.2.3 Fixed Effects in Count Data Models ...... 58 3.3 Data ...... 62 3.4 Results ...... 64 3.5 Enduring Effects ...... 70 3.6 Summary and Concluding Remarks ...... 78 Chapter 4. A Consideration of Floodplain Buyout Capitalization Heterogeneity in Harris County, Texas ...... 80 4.1 Background ...... 85 4.2 Methodology ...... 90 4.2.1 Hedonic Regression and Specification ...... 90 4.2.2 Repeat Sales Model...... 92 4.3 Data ...... 94 4.4 Results ...... 98 4.5 Discussion and Conclusion ...... 106 Chapter 5: Conclusion...... 110 5.1 Contributions...... 112 5.2 Future Work ...... 113 References ...... 115

List of Tables

Table 1: Difference-In-Differences Results and Robustness to Fixed Effects ...... 27 Table 2: Difference-In-Differences Robustness ...... 30 Table 3: Triple Difference Results and Robustness to Fixed Effects ...... 36 Table 4: Falsification ...... 38 Table 5: Central and Southern Florida Project Levees ...... 51 Table 6: Difference-In-Differences Estimation of the Impact of Levee Construction on Housing Development with Fixed Effect Robustness ...... 65 Table 7: Difference-In-Differences Estimation Robustness to Varying Spatial and Temporal Sample Restrictions ...... 66 Table 8: Difference-In-Differences Estimation Robustness to Modelling Frameworks .. 69 Table 9: Control Function First Stage Results for Instruments and Relevant Neighborhood Characteristics ...... 75 Table 10: Results for Naïve and IV Duration Models ...... 77 Table 11: Property Buyout Descriptive Statistics ...... 98 Table 12: Hedonic Regression of the Impact of Buyout Proximity on Housing Values with Fixed Effect Robustness ...... 100 Table 13: Hedonic Regression of the Impact of Buyout Proximity on Housing Values with Neighborhood Quality Heterogeneity (Continuous)...... 102 Table 14: Hedonic Regression of the Impact of Buyout Proximity on Housing Values with Neighborhood Quality Heterogeneity (Discrete) ...... 103 Table 15: Repeat Sales Model Estimation of the Impact of Buyout Proximity on Housing Values with Neighborhood Quality Heterogeneity ...... 104 Table 16: Hedonic Regression of the Impact of Buyout Proximity on Housing Values with Distance Heterogeneity ...... 106

List of Figures

Figure 1: Capitalization Matrix ...... 16 Figure 2: Hedonic Equilibria with Multidimensional Information ...... 17 Figure 3: Price Gradient of Homes Relative to Flood Risk and Build Year ...... 21 Figure 4: Spatial Heterogeneity in Subsidy Eligibility Capitalization ...... 31 Figure 5: Public Curiosity Concerning Flood Insurance Subsidies and Reform ...... 40 Figure 6: Central and Southern Florida Project Levees ...... 47 Figure 7: Parallel Trends of Residential Development ...... 57 Figure 8: Levee Construction Fixed Effects ...... 61 Figure 9: Duration Model Scope of Study and Spatial Units ...... 73 Figure 10: Houston, Harris County, and the United States...... 84 Figure 11: County-Defined Buyout Target Areas ...... 89 Figure 12: Relative Intensity of Buyouts and Arms’ Length Transactions by Year ...... 95 Figure 13: Location of Buyouts and Neighborhood Heterogeneity ...... 96

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Chapter 1: Introduction

Floods are the most damaging natural disaster in the history of the United States, with

90% of all presidentially declared natural disasters involving some form of flooding. In the US and throughout many parts of the rest of the world, economic losses attributable to floods are increasing and are only expected to further grow with climate and socioeconomic changes (Aerts et al. 2014; Alfieri et al. 2016). Societies are not helpless in the face of increasing vulnerability. Rather, communities across the world and at various levels of organization have developed a broad range of policies to mitigate flood risk. These policies can generally be categorized as either providing insurance, protection/prevention/adaptation, or retreat/relocation.

In the United States, the primary approaches associated with insurance, protection, and retreat are the National Flood Insurance Program, the construction of levees, and federally funded property buyout programs. Each of these approaches is failing by at least one metric. The National Flood Insurance Program is chronically insolvent. The national levee system has routinely received a D grade from the American

Society of Civil Engineers. Vulnerable property acquisition programs struggle to encourage participation. This list of shortcomings is non-exhaustive and the totality of these deficiencies leaves significant room for improvement through informed policies.

Dating back as far as Earth Day I in 1970, and at least to President Ronald

Reagan’s signing of Executive Order 12291 in 1981 (requiring cost-benefit analysis for all major government interventions), the insights, models, and tools of economists have served as invaluable assets for improving policies at the intersection of the environment and human welfare (Freeman 2002). In the age of the “credibility revolution” (Angrist and Pischke 2010), economists have even greater resources for influencing and improving policies and programs. Insights gained through theory-guided methods of causal inference have informed environmental policy improvements with real, measurable benefits (Duflo et al. 2013). Efforts to enhance flood risk resiliency could likewise benefit from such analysis.

Recent, original work and comprehensive meta-analyses have greatly enhanced our understanding of the determinants of flood insurance uptake (Zahran et al. 2009;

Petrolia et al. 2013; Gallagher 2014; Atreya et al. 2015; Landry et al. 2019) and the impact of flood risk on housing prices (see Beltran et al. [2018] for a synthesis of the literature), among other topics. However, significant knowledge gaps remain.

In this dissertation, I use insights and estimation techniques associated with models of spatial equilibrium and land use to evaluate particular policies related to the three primary approaches for mitigating flood risk. Specifically, I consider the capitalization of flood insurance premium discounts, induced development attributable to levee construction, and externalities associated with property buyouts using national, state, and county level analyses. In addition to answering questions of critical policy importance, I uncover a pattern of unintended (although not necessarily unanticipated)

2 consequences, most of which are counterproductive with regard to the stated goals of the respective intervention.

To briefly preview the new insights created in this dissertation, I summarize the policy relevance of the chief results from each of the three primary chapters. My analysis of the National Flood Insurance Program yields the first estimate of the impact of a 50- year-old subsidy on housing values and can help inform current policy debates regarding the rate of phasing out such subsidies. I also produce the first causal estimate of the impact of levee construction on rates of residential development. These findings suggest that levees should only be built if strong zoning restrictions can be enforced, conditional on an intended outcome of minimized expected damages. Finally, I provide the first estimate of the capitalization of vulnerable property buyouts on neighboring housing values. These results indicate that more generous offers can be made in higher quality neighborhoods as the acquired parcels lead to positive externalities for their neighbors.

While this dissertation is primarily concerned with applying economic insights and methods of causal inference to evaluate programs with the goal of informing policy, it also offers an advancement of the interpretation of results from a foundational model of non-market valuation: the hedonic regression. By introducing the concept of multidimensional information, I improve upon a series of similar extensions to the model from the past decade and potentially influence the evaluation of policies well outside the scope of this dissertation.

Chapter 2: Do NFIP Subsidies Matter to Homebuyers? Evidence from Nationwide Housing Sales

The National Flood Insurance Program (NFIP) was never intended to be actuarially sound, and indeed it is not. Debts associated with NFIP reached $30 Billion immediately preceding landfall of Hurricanes Harvey and Irma in 2017 (Eastman 2015; Government

Accountability Office 2017). To encourage the initial adoption of flood insurance, discounted premiums were and continue to be offered to preexisting structures in communities that choose to participate in NFIP. The properties eligible for these subsidies are classified as Pre-FIRM, indicating they existed prior to the establishment of the initial Flood Insurance Rate Map for that area.1 Though highly heterogeneous (largely due to variation in the difference between the base flood elevation (BFE) and structural elevation), the average annual discount provided by these subsidies is approximately 55 to 60 percent of the premium, or $1,467 to $1,800 per year (Brown 2011).2 The sum of all such discounts across the United States represents a significant reduction in revenue needed to cover losses on insured properties, up to $1.05 Billion per year for single family residences alone.

1 While other policies exist that offer discounted premiums through NFIP, this is the largest in terms of scope and expenditure. As such, I do not consider the other primary discounted premium policy of “Grandfathered Rates”. 2 Given the loss in premiums associated with subsidized rates represents about 40 to 45 percent of what would be expected from full flood risk policies, and the average Pre-FIRM policy cost $1,200 in 2011, the average full risk rate should have been $2,667 to $3,000. 4

A short-lived attempt to address this deficiency occurred when recent legislation

(The Biggert-Waters Flood Insurance Act of 2012 [BW12]) was passed to rapidly phase out subsidized rates. This change in subsidization was immediately met by pushback from NFIP stakeholders so that subsequent legislation (The Homeowner Flood Insurance

Affordability Act of 2014 [HFIAA]) was enacted to not only reintroduce subsidies to affected primary residences, but to refund the higher premiums paid for subsidy-eligible properties in the time between the two acts. Subsidies for businesses, non-primary residences, and structures that were rebuilt were not refunded and remain on pace to be phased out within the next several years. While subsidized premiums for primary residences are slowly increasing, some qualifying homeowners are likely to continue to pay less than full-risk rates for at least 20 more years (Kousky, Lingle, and Shabman

2016).3

The recent hurricanes to hit the Gulf and Atlantic coasts have brought with them a wave of media attention and scrutiny on NFIP, its insolvency, and the incentives it creates. While much of NFIP’s debt can be explained by the creation of adverse selection through systemic low compliance (only 50 percent of properties required to have flood insurance actually participate [Kriesel and Landry 2004; Kousky and Michel-Kerjan

2012]) as well as a disproportionate amount of claims filed by severe repetitive loss properties (totaling 1 percent of all policies, but claiming 30 percent of all losses

[Eastman 2015]), nearly 600,000 single-family homeowners still benefit from paying

3 The exact expected duration of these benefits depends on property-specific freeboard and the annual premium increase set by FEMA. The 20 year estimate is based on an annual rate increase of 5 percent for a maximum-coverage, minimum-deductible policy for a non-coastal, single family home without a basement and with a lowest floor elevation two feet below the BFE. 5 flood insurance premiums that do not reflect the expected damages from potential floods

(BW12 Fact Sheet).

As political calls for a more immediate phase-out of NFIP subsidies, specifically, and even the program, entirely, are increasing, FEMA faces pressure to raise premiums at an increasing pace for subsidy eligible properties. While much of the attention being paid to the socioeconomic consequences of achieving greater fiscal solvency of NFIP has focused on premium affordability (National Research Council 2015; Congressional

Budget Office 2018) of equal concern is the impact that subsidies have on the value of the typical American’s greatest asset: their home equity. In fact, included in the reforms of the HFIAA was a repeal of a provision in BW12 that terminated premium subsidies upon the transfer of property ownership. This reform was intended to protect homeowners from “significant and unanticipated increases in flood insurance costs that could impact their property sales” (HFIAA Fact Sheet). Given this concern, and that Pre-

FIRM subsidies were originally justified in part on the grounds of maintaining property values (Michel-Kerjan 2010), understanding the expected impact of changes in subsidized rates on capitalized values of homes is a critical input into ongoing policy discussions.

Identification of the capitalization of flood insurance premiums is challenging as homeowners internalize both the net present value of future payments, as well as the “risk signals” flood insurance mandates may confer (Nyce et al. 2014). Still, the attempt to disentangle the capitalization of risk and flood insurance provision has a long history in the economics literature dating to at least the 1980s (Shilling, Sirmans, and Benjamin

1989). Despite this history, the extent of premium capitalization remains unsettled.

Whereas some studies report the negative capitalization of mandated flood insurance to be less than one (Bin et al. 2008), others find that the reductions in housing values exceed the complete capitalization of flood insurance premiums (Atreya, Ferreira, and Kriesel

2013). Though the latter case may indicate a co-mingling of risk signals and high premium capitalization, both indicate that lower premiums, and therefore Pre-FIRM subsidies, should capitalize positively in property values.

While the direction of the impact of subsidy eligibility on housing values is unambiguously positive, it is more challenging to confidently predict the magnitude of this effect. Despite the vast majority of studies suggesting that fiscal programs tend to fully capitalize in housing values,4 recent analyses have found that such programs may under-capitalize if there is an increase in the housing supply (Lutz 2015), if there is imperfect competition (Kirwan 2009), or if homebuyers are unaware of the value of the program (Bradley 2017). Though the supply of Pre-FIRM subsidy eligible homes is fixed by design, and housing markets are generally considered to be competitive aside from information asymmetries, the assumption of complete information is unlikely to be satisfied and an under-capitalization of subsidy eligibility is therefore plausible. While the aggregate impact of removing Pre-FIRM subsidies may be large, it may not be as sizeable as would be implied by the full capitalization of subsidy eligibility.

4 See Hilber (2017) for a literature synthesis and Do and Sirmans (1994) and Palmon and Smith (1998) for specific examples of findings of full capitalization of taxation. 7

In this chapter I causally identify the extent to which Pre-FIRM subsidized flood insurance premiums are capitalized into housing values. Specifically, I use an exogenously determined subsidy eligibility threshold to estimate the causal impact of

NFIP subsidies on housing values using a hedonic difference-in-differences approach for

49 of the 50 largest primary statistical areas (PSAs) in the United States for the years

2005-2012.5 Considering a nationally pooled model, I find an average capitalized value of $11,807 for subsidy eligible properties. That this value lies between rates of capitalization that would be predicted from markets with symmetrically informed market participants holding various levels of information, implies that it is the outcome of transactions between asymmetrically informed buyers and sellers. This finding and rationale are supported by a similar analysis disaggregated by markets. Extending my primary model to a triple difference estimator further validates my difference-in- differences results by quantifying the loss in capitalization due to the passage of BW12. I find that the BW12 legislation reduced property values by $8,996, or approximately 76 percent of the capitalized value of subsidy eligibility.6 While flood insurance is most prevalent among the states bordering the Gulf of Mexico, beneficiaries of these subsidies are dispersed heterogeneously throughout the country and the aggregate loss in property value could be as high as $7 Billion, should the existing subsidies be completely, immediately, and permanently eliminated.

5 Primary statistical areas are the most extensive statistical areas for county or county equivalents that still share labor and housing market linkages. The population estimates within these areas constitute 66 percent of the national population. The record of transactions occurring in New Orleans was incomplete. 6 Though the transference of subsidy eligibility wasn’t fully reinstated until the implementation of the HFIAA in March of 2014, it was reported that Biggert-Waters would be repealed in October of 2013 and subsequent legislation relaxed various components of the law in January of 2014. My results are robust to the usage of any of these moments for the bookend of my analysis. 8

My findings contribute to the literature in three significant ways. First, I extend prior literature by analyzing NFIP subsidies using a nationwide dataset of over 4.5 million housing transactions, which minimizes the likelihood that there are local economic shocks or national building codes driving my results since initial community participation dates are highly heterogeneous across markets. Second, I build on the model of asymmetric information in hedonic analysis by introducing the possibility of imperfectly informed sellers. Finally, I provide the first targeted and nationwide analysis of the impact of BW12 on affected housing values, informing and evaluating the amendment of this policy through the HFIAA in 2014.

2.1 The NFIP Experiment

The provision of flood insurance in the United States has evolved considerably over the past 50 years. The history of this evolution is most succinctly described in three phases: the period prior to the establishment of NFIP, the period prior to Hurricane Katrina, and the period following Hurricane Katrina. The following section briefly discusses the regulatory and environmental changes that defined each of these phases and the importance of policy aspects in these epochs for my empirical identification strategy. For more information on the history and structure of NFIP, in depth discussion of these changes is explored by Kunreuther and Roth (1998) and Michel-Kerjan (2010).

Flood insurance was originally provided via homeowners’ insurance, but due to the low profitability associated with adverse selection and systemic losses, it was eventually excluded and sold separately (Gerdes 1963). As individuals underinsured in response to the high premiums necessary for actuarially sound coverage, the onus was placed on the

9 government to provide relief aid after catastrophic events if they wished to avoid long- term humanitarian and economic consequences in locales such as New Orleans. This essentially provided “free” flood insurance (Pasterick 1998). Recognizing this inefficiency and the inability to provide 100 percent protection from flood related damages, The Southeast Hurricane Disaster Relief Act of 1965 commissioned a study to reevaluate floodplain management. This led to a report to the department of Housing and

Urban Development (HUD) in 1966 which eventually provided the grounds for the establishment of NFIP in 1968.

Recognizing the importance of community intervention in residential development and disaster preparedness, for a household to purchase insurance under

NFIP (though directly through an independent agent), the community in which it was located had to formally join NFIP. This required the adoption of federally determined regulations for new construction (relating to the lowest floor elevation, treatment of enclosures and basements, location of utilities, and construction materials) and the mapping of areas at high risk of sustaining flood related damages (Federal Emergency

Management Agency [FEMA] 2010). Seeking to avoid replicating the lack of participation in the private flood insurance market prior to 1968 which priced actuarially sound premiums, structures pre-existing the date of adoption of community flood rate maps were granted premium discounts to incentivize community participation in NFIP.

Faced with low community participation, in addition to the “carrot” of subsidized premiums, The Flood Disaster Protection Act of 1973 added the “stick” of mandating

NFIP community participation for federal relief aid eligibility. While this alone would

10 have greatly increased the number of communities enrolled in the program, it would have had little effect on the household-level decision of whether or not to purchase flood insurance because homes without flood insurance would still be eligible to receive relief aid in participating communities, thereby preserving adverse selection within the pool of policyholders.

To mitigate this market failure, the legislation also mandated the purchase of flood insurance for all flood-prone properties bought with a mortgage sold by a federally insured lender. This designation was made on the basis of whether an improved structure was located within the Special Flood Hazard Area (SFHA) that each community was required to have mapped upon entrance into the program.7 Pre-FIRM subsidized rates were eventually extended to any structures in participating communities that received construction permits before 1975. The combination of these conditions led to more than

80 percent of eligible communities joining NFIP between 1973 and 1994.

The flood-insurance program remained well within its borrowing limits until

Hurricane Katrina devastated New Orleans in 2005. Having previously never exceeded

$1 Billion, the cumulative debt of NFIP approached $17 Billion in 2006 and has not dropped below $15 Billion since (King 2013). Currently, NFIP continues to suffer from the same problems that plagued private flood insurance providers in the previous century; namely, that claims following disasters greatly outweigh collected premiums.

7 Special Flood Hazard Areas have been mapped to reflect an annual risk of flooding of one percent. Though properties may be located in areas carrying a 0.2 percent risk of flooding annually, because the mandate to buy flood insurance only applies to property- owners in SFHAs, I refer solely to these areas when discussing flood risk and use the terms “SFHA” and “floodplain” interchangeably. 11

The pattern of extreme weather events over the past 19 years suggest that this problem is likely to worsen (Kousky and Shabman 2014). Adjusted for inflation, 15 of the 20 costliest storms to have hit the mainland of the United States since 1900 have occurred in the past 19 years (Blake and Gibney 2011). The recent increase in annual expected damages presents a significant challenge which the current structure of NFIP may not be equipped to confront without incurring hundreds of billions of dollars in debt

(Blake and Gibney 2011; Rao 2017).

To combat this problem, Congress enacted BW12. In addition to immediately terminating Pre-FIRM subsidy eligibility for properties which were sold after implementation, provisions were included to address inefficiencies with regard to the treatment of severe repetitive loss properties and to strengthen the penalties for noncompliance. Though the eliminated subsidies were reinstated through HFIAA, a slower path to achieving fiscal solvency was granted, with annual rate increases of up to

18 percent permitted for all Pre-FIRM eligible properties. However, since raising premiums for Pre-FIRM primary residences by 15 percent in 2015, FEMA has set the rate increase for these properties at the minimum required level of 5 percent for 2016 and

2017, with a slight increase to 7 percent in 2018.8 Using this lower premium increase results in a shortfall of $0.75 Billion in collected premiums when compared to the premiums paid under annual increases of 18 percent as permitted by legislation. Because

8 WYO Program Bulletin: W-14053. 2014. Washington, DC. Federal Emergency Management Agency. WYO Program Bulletin: W-15046. 2015. Washington, DC. Federal Emergency Management Agency. WYO Program Bulletin: W-16071. 2016. Washington, DC. Federal Emergency Management Agency. WYO Program Bulletin: W-17061. 2017. Washington, DC. Federal Emergency Management Agency. WYO Program Bulletin: W-18021a. 2018. Washington, DC. Federal Emergency Management Agency. 12 this pattern of setting rate increases at 5 percent prolongs an institution that rewards risky investments and significantly curtails the collectable premiums needed to approach solvency, benefits received by those with subsidy eligible homes are expected to be significant.

2.2 Capitalization with Potential Information Asymmetry

While one would expect subsidy eligibility to capitalize positively and significantly into housing values, one would only anticipate full capitalization under a particular set of assumptions regarding market participant awareness. I highlight these assumptions by considering the well-known first-stage hedonic approach to explain the observed equilibrium prices for housing attributes (Rosen, 1974). The hedonic model specifies an individuals’ utility function as a concave function of property characteristics and a composite numeraire good.

푘 푘 (2.1) 푈푖푗 = 푈(푐, 푋푖, 푁푗, 푍푖, 훼 )

In this case, the property characteristics of home i consist of home-specific features, 푋푖, common traits within neighborhoods, 푁푗, and subsidy eligibility, 푍푖. Assuming households, k, are utility-maximizing agents that are constrained only by their budgets and differ with regard to their preferences for characteristics, 훼푘, then competition amongst buyers (and amongst sellers) should result in an equilibrium price schedule:

(2.2) 푃푖푗 = 푃푖푗(훽, 푋푖, 푁푗, 푍푖)

Here the price schedule represents a continuous set of equilibria for homes of various qualities and prices determined by the upper envelope of the buyers’ bid functions and the lower envelope of the sellers offer functions. As demonstrated by Pope (2008), when

13 there is one measure of information regarding the value of attribute Zi and this information is distributed asymmetrically between the buyer and the seller, and holding all other attributes constant at their equilibrium levels, the hedonic price equilibrium for attribute Zi will lie somewhere between the equilibrium price schedules resulting from transactions between symmetrically informed and symmetrically uninformed market participants, depending on the fraction of uninformed buyers in the market. In this model, full capitalization is only possible when all buyers and sellers are perfectly informed.

However, by introducing the concept of multidimensional information and relaxing the assumption that sellers are perfectly informed, I show that full capitalization is possible with asymmetric information and with uninformed sellers, although partial capitalization in proportion to the distribution of information is still the predicted result when imperfect information is present.

To better understand this model, let us first contrast multidimensional information with the traditional conceptualization of information in similar models. While an uninformed buyer in implicit markets for poor water quality, flood risk, or noise pollution is defined by being unaware of the presence of these disammenities, an uninformed buyer in a multidimensional information model need not be unaware of the presence of the attribute, but is unaware of the value of the attribute. When this attribute is NFIP subsidy eligibility, value depends on two types of information. Type I information concerns the mandate to purchase flood insurance and type II information concerns the substitutability of relief aid for insurance (charity hazard). The value of subsidy eligibility exists only in relation to flood insurance premiums. If a homeowner plans on purchasing flood

14 insurance in perpetuity, the value of subsidy eligibility is the discounted value of the future stream of annual savings on flood insurance premiums. If a homeowner never plans on purchasing flood insurance, subsidy eligibility has much more limited value to them. Therefore, if a homeowner is aware that mandate to purchase flood insurance is only weakly enforced beyond the first year of homeownership (High Type I information) and the homeowner is unaware that relief aid is not an acceptable substitute for flood insurance (Low Type II information), then this homeowner will only value subsidy eligibility in so far as it reduces their flood insurance premiums in the first year of homeownership, the only year in which they will buy flood insurance.9 If all market participants symmetrically held this imperfect level of information, Pre-FIRM subsidy eligibility would capitalize at its one year annual value of approximately $1,500 to

$1,800, on average. However, if all market participants were completely informed of the value of subsidy eligibility, meaning that despite awareness of the lack of enforcement of the insurance mandate after the first year of homeownership, they were also aware that relief aid is a poor substitute for flood insurance, they would purchase flood insurance in perpetuity and value subsidy eligibility by the discounted sum of reduced future flood insurance payments. To convert capitalized values to annualized values and vice versa, the value can be adjusted by a user cost. Applying a user cost of ten percent

9 A 2015 interview with government officials and policy experts revealed that even after BW12 and HFIAA, the mandate to purchase insurance for properties in SFHAs may not be well enforced and there is no punishment for noncomplying homeowners (Kousky and Shabman 2015). This is supported by case studies finding low compliance for mortgage holders within SFHAs and the stylized fact that the median tenure of flood insurance ownership is two to four years (Michel-Kerjan 2010; Michel-Kerjan et al. 2012). Interviewees in the Kousky and Shabman analysis also indicated a mistaken belief of some homeowners that even the most generous aid packages will satisfactorily remediate damages. While total flood insurance claims are capped at $350,000 for a household, FEMA’s Individual and Household Program grants are capped at roughly $30,000 with an average value of $5,508 for individual assistance grants received between 2005 and 2004 (Kousky and Shabman 2012). Still, multiple studies have found that the possibility of receiving relief aid negatively impacts flood insurance uptake (Raschky et al. 2013; Davlasheridze and Miao 2019). 15

(approximately the average value in the range of user costs highlighted by Glaeser and

Gyourko [2007]), the capitalized value of subsidy eligibility in a perfectly informed

market should be between $15,000 and $18,000. Interestingly, while transactions

between symmetrically informed participants can only yield an average capitalized value

of $1,500 and $1,800 when both buyers and sellers are High Type I and Low Type II, all

other symmetric combinations of information typologies yield full capitalization.

Figure 1: Capitalization Matrix

BUYER I NFORMATION TYPE

HIGH I HIGH I LOW I LOW I WHERE CAPITALIZATION HIGH II LOW II HIGH II LOW II LIKELY TO RATE OCCUR

HIGH I NO AREAS WITH FULL FULL FULL HIGH II TRANSACTION FLOODING

HIGH I AREAS

LOW II PARTIAL 1 YEAR PARTIAL PARTIAL WITHOUT

FLOODING SELLER INFORMATION TYPE LOW I NO UNLIKELY FULL FULL FULL HIGH II TRANSACTION THAT

LOW I SELLER NO LOW II FULL FULL FULL WILL BE TRANSACTION LOW TYPE I

The complete range of capitalization possibilities is depicted in Figure 1 with outcomes resulting from symmetric distributions of information displayed on the main diagonal. Here it is noted that outcomes involving sellers with Low Type I information are unlikely as all sellers who have owned their house for at least a year should be aware of the lack of the enforcement of the mandate. However, sellers may very well be unaware of the poor substitutability of relief aid for insurance, especially if they reside in markets where flooding is a less common occurrence. Therefore, we’d expect full capitalization where flooding poses a greater risk or is more common, and partial capitalization in markets where flooding is less common. Partial capitalization is then defined by an equilibrium price schedule resulting from transactions between buyers and sellers in markets where the upper envelope of the buyers’ bid functions exceeds the lower envelope of sellers offer functions according to their information types, as illustrated by any curve which could exist in the dotted region in Figure 2.

Figure 2: Hedonic Equilibria with Multidimensional Information

2.3 Identification Strategy

In this section, I present the difference-in-differences hedonic model used to estimate the capitalization effect of NFIP subsidy eligibility before describing my strategy for causal identification.

2.3.1 Hedonic Model of Subsidy Capitalization

I estimate the capitalization of Pre-FIRM subsidy eligibility with a first stage hedonic regression and introduce non-linearities into price schedule (2.2) by estimating a double- logarithmic model as shown in equation (2.3), noting that my empirical results are robust to alternative functional forms.

(2.3) ln(푃푖푗,푐푡) = 훼0 + 훽ln (푋푖) + 휌푃푟푖표푟푖푗 + 휋푆퐹퐻퐴푖 + 훿(푆퐹퐻퐴 ∙ 푃푟푖표푟)푖푗 + 휇푗 +

휃푐푡 + 휀푖푗푡

Explanatory variables consist of the property-specific observable attributes represented by 푋푖, an indicator for whether the structure was permitted for construction prior to the year the host community first joined NFIP, an indicator for whether the structure was built in an SFHA, and an interaction term between the two previous indicators, which serves as my difference-in-differences estimator. 휀푖푗푡 is an idiosyncratic error term,

훽, 휌, 휋, and 훿 are vectors of parameters, and my neighborhood and community by time controls, or fixed effects, 휇푗 and 휃푐푡, are described in more detail below.

Taking the derivative of the price function with respect to any of the observable attributes and isolating the derivative of the dependent variable with respect to the independent variable yields the change in capitalized values associated with changes in that attribute. As Kuminoff and Pope (2014) show, due to time-varying changes in

18 hedonic equilibria, I interpret these effects as capitalized values. The resulting expressions for these effects for my discrete and continuous variables, respectively, are

휕푃 휕푃 푃̅ 푖푗푡 = 푃̅훽 and 푖푗푡 = 훽 . The resulting marginal effect for my key difference-in- 휕푋푖 휕푋푖 푋푖 differences parameter measures the capitalization of Pre-FIRM subsidies.10

2.3.2 Difference-in-Differences Identification

To consider the intuition for my quasi-experimental identification let type A homes be built inside floodplains and prior to the eligibility cutoff, type B homes be built inside floodplains but after the eligibility cutoff, type C homes be built outside floodplains and after the eligibility cutoff, and type D homes be built outside floodplains, but before the eligibility cutoff. Identification relies on the unique nature in which subsidy eligibility was established by legislation, and later changed by BW12. To see this quasi- experimental logic, define P(Y) as the price of home Y (conditional on structural and proximal characteristics). Then P(A)-P(D) = P(A-D) and, holding all else equal, this difference represents the capitalized value, either positive or negative, of residence within a floodplain for homes permitted before initial NFIP participation or 1975. Similarly,

P(B)-P(C) = P(B-C) and represents the capitalized value of residence within a floodplain for homes permitted after initial NFIP participation. While I am ambivalent toward the signs on these values and do not seek to directly identify them for the reasons described below, I expect P(A-D) > P(B-C) and therefore P(A-D)-P(B-C)>0, or in words, I expect

10 As my variable of interest is an interaction of two binary indicators and is itself a 0/1 dummy variable, the marginal effects for my discrete variables require a correction: 푃푟푖푐푒 푆푒푚푖푒푙푎푠푡푖푐푖푡푦 = 푒훿 − 1 (Halvorsen and Palmquist 1980)

19 floodplain location to be more valuable for homes with lower flood insurance costs, all else equal. This forms the basis for my primary difference-in-difference specification.

As with all quasi-experimental analyses, validity of the difference-in-differences research designs depends on several assumptions. The first is that the initial date of FIRM adoption is exogenous to community development. While not purely random, the FIRM date can be thought of as random to the community in terms of planning. Rate maps were not immediately available for all communities upon the establishment of NFIP and it was not feasible to instantly create such maps for each of the 22,000 communities nationwide.

The Federal Insurance Administration (FIA) hired engineering firms to create the maps and upon completion, the FIA would notify the communities that the maps were available and would strongly recommend participation. The order in which communities were mapped depended in part upon projected community growth, but also a host of other factors such as the availability of flood data and the potential for catastrophic floods.

Descriptive evidence shows little connection between past economic growth and the timing of NFIP participation (Browne et al. 2019). In addition, my empirical analysis focuses only on communities adopting FIRMs prior to the beginning of my data period to avoid contemporaneous correlations.

The second assumption is that of common trends; that conditional on controls and absent the treatment, the relationship between the expected value of the treated observations and the non-treated observations would be the same over time. I follow standard practice (Mastromonaco 2015; Muehlenbachs, Spiller, and Timmins 2015;

Haninger et al. 2017) to visually assess this condition by first parametrically regressing

20 logged prices on the same set of explanatory variables in equation (2.3) (except for those pertaining to treatment), and then non-parametrically plotting the residuals over a running variable with a discrete threshold that indicates treatment using a local linear polynomial estimator. Figure 3 provides evidence in support of this assumption.

Figure 3: Price Gradient of Homes Relative to Flood Risk and Build Year

The running variable represents the difference of the build year of the home and the year of initial NFIP participation, so that a home built one year before its host community joined NFIP would have a value of negative one, while a home built one year after its host community joined NFIP would have a value of positive one. As Pre-FIRM designation depends on the date which the home was permitted for construction rather

21 than the date construction was completed or it was first assessed or appraised, I include in my treatment group homes which were built in the same year as their host community joined NFIP to account for the time spent between the issuance of the permit and the completion of construction.

Several patterns are immediately evident in Figure 3. First, homes built inside

SFHAs and homes built outside SFHAs share similar conditional price dynamics across build years relative to initial NFIP participation. Specifically, as the build year becomes closer to the year of participation, both categories of properties appear to follow parallel trends. Secondly, while homes built inside of SFHAs are either conditionally more valuable than homes built outside SFHAs or indistinguishable from those homes in terms of value when subsidy eligible, they are less valuable than non-SFHA homes when built after subsidy eligibility expired in their community, providing visual evidence of my causal effect.

2.3.3 Fixed Effects in Hedonic Regressions

Within the context of hedonic valuation, this quasi-experimental design is the preferred approach for identifying capitalization effects over cross-sectional analysis (Parmeter and

Pope 2013). While this strategy controls for observable differences across properties and unobservable differences associated with floodplain location and construction year, there are likely additional important characteristics that factor into the decision of which home to purchase, such as school quality, open space, crime, water quality, air quality, and noise. As these amenities or disammenities are typically highly spatially correlated, I can

22 control for them by restricting my identification to come from variation within spatial groupings, otherwise known as fixed effects.

My preferred set of spatial fixed effects is at the level of Census Block Group by

SFHA. With the data at my disposal, the selection of Census Block Group fixed effects, typically containing under 500 individuals, over broader Census Tract or County fixed effects is intuitive, as it requires identification to arise from variation within smaller neighborhoods and thus minimizes the possibility of spatial omitted variable bias. The inclusion of floodplain designation in my fixed effects controls for the average value of location within an SFHA as this source of capitalization is subsumed by the fixed effect.

This level of spatial control avoids longstanding concerns that homes in floodplains are systematically different than those outside of floodplains, potentially confounding analyses of risk related effects and has been the focus of a substantial literature on capitalization (Speyrer and Ragas 1991; Harrison et al. 2001; Bin and Polasky 2004;

Hallstrom and Smith, 2005; Carbone, Hallstrom, and Smith 2006; Smith 2008; Posey and

Rogers 2010). Furthermore, recent work has found that the negative capitalization of floodplain location may only be present in communities which have suffered a significant flooding event within the years immediately preceding the sale of the home (Bin and

Landry 2013; Atreya, Ferreira, and Kriesel 2013; Bakkensen et al. 2019). By allowing the capitalization of floodplain location to vary across neighborhoods, I avoid contaminating my parameter of interest if cross-sectional variation in floodplain risk perceptions is present.

My preferred set of temporal fixed effects, at the NFIP community (or CID), c, by year level, also removes any concern of contamination from the potential dual subsidization of the Community Rating System (CRS)11. As premium discounts available from CRS range from 5 to 45 percent and have the potential to change annually for each community, the failure to account for such discounts could significantly bias my estimate of the capitalization of floodplain location, thereby impacting my causal estimate of Pre-

FIRM subsidy capitalization. By restricting identification to come from within NFIP community by year groupings, all households face the same CRS subsidies, thus eliminating this possible source of bias.

2.4. Data and Summary Statistics

I compiled 4.5 million single-family housing transactions spanning 49 of the 50 largest

Primary Statistical Areas in the United States sold from September 2005 through March

2014. The data was purchased from information intelligence provider CoreLogic, Inc.

This data consists of county-level assessor’s office records of real estate transactions, spanning the entire country and includes transaction prices, sale dates, construction dates, mortgage information, property centroid geographic coordinates, and structural characteristics of the properties.

The cleaning of the hedonic data follows standard practices in the literature.

Observations with significant outliers in terms of structural characteristics are removed in order to minimize the leverage of extreme and atypical observations. I further restrict

11 The CRS provides premium reductions for community level decisions that lower aggregate risks beyond the point required by NFIP. 24 sales of homes by removing cash purchases and by censoring observations at the 1st and

99th percentiles for the respective sale year in every market to reduce the possibility of mislabeled values or non-arms-length transactions. I remove foreclosures and homes that benefited from significant repairs that would disqualify them from receiving subsidized flood insurance premiums and built-to-order homes sold in the same year as they were built. To purge the potential for omitted variable bias associated with quality changes, I don’t consider homes that were “flipped” or had other unobservable characteristics associated with frequent turnover by dropping homes sold multiple times in the same year and those sold more than three times over the duration of my sample. Finally, I removed transactions for homes sold for less than $1 per square foot.

I also exclude communities not participating in NFIP by choice or sanction and I do not include communities for which the flood insurance rate maps have not been updated or digitized. I further limit the difference between build year and year of initial participation to be no less than -60 and no greater than 40 for a more balanced sample.

My preferred hedonic functional form is logarithmic in continuous variables as controlled simulations suggest that a double logarithmic specification minimizes bias in a differenced model (Kuminoff et al. 2010).

In addition to housing data, I obtained information on flood risk using the

National Hydrography Dataset, FEMA’s National Flood Hazard Layer, and the NFIP

Community Status Book. I use the National Hydrography Dataset to determine the proximity of each property centroid to the nearest permanent lake, river, and coastal body of water. The locations of Central Business Districts were obtained from Holian and

Kahn (2015). The National Flood Hazard Layer helps me determine whether a home was built in a 100-year floodplain, thus requiring full flood insurance coverage. Finally, I determine whether a home is eligible for subsidized flood insurance premiums by comparing the year the home was built with the year that the community in which it is located joined NFIP by using the NFIP Community Status Book.

2.5 Results

In this section I estimate the average capitalization of Pre-FIRM subsidy eligibility in addition to considering spatial heterogeneity. All transactions occur prior to the passage of BW12.

2.5.1 The Capitalization of Pre-FIRM Subsidy Eligibility

Table 1 displays the results for five different models, each with the same logarithmic functional form but with different sets of fixed effects. These become progressively more restrictive reading from left to right. Though the estimate of subsidy eligibility capitalization becomes greater in magnitude as the scope for omitted variable bias is diminished through tighter fixed effects, a positive and significant capitalization of subsidy eligibility is detectable even without spatial fixed effects, as indicated in column

(1). Subject to the appropriate correction, the coefficients for the discrete variables are interpreted as percent changes in the dependent variable associated with a binary change in the independent variable.

Table 1: Difference-In-Differences Results and Robustness to Fixed Effects

Variables (1) (2) (3) (4) (5) SFHA 0.022*** -0.009** -0.011***

(0.002) (0.003) (0.003) Built Prior 0.154*** -0.031*** -0.031*** -0.032*** -0.039***

(0.001) (0.002) (0.001) (0.001) (0.001) Subsidy Eligible 0.018*** 0.015*** 0.017*** 0.041*** 0.039*** (Built Prior x (0.004) (0.004) (0.004) (0.006) (0.006) SFHA) Property Yes Yes Yes Yes Yes Characteristics

Spatial Fixed BG x SFHA BG x SFHA N/A Tract (28,225) BG (74,714) Effects (83,506) (83,265)

Temporal Fixed NFIP Comm. x Year (8) Year (8) Year (8) Year (8) Effects Year (29,334)

Observations 4,553,190 4,551,742 4,548,530 4,543,643 4,541,325 R2 0.354 0.819 0.830 0.831 0.863 Notes: ***, **, * indicates significance at the 1%, 5% and 10% level, respectively. Standard Errors have been clustered at the listed spatial fixed effect level. All models also include quarterly indicators. All models also include quarterly indicators. Property characteristics include acres, age, bathrooms, square footage of living space, stories, distance to the central business district, the coast, the nearest lake, river, and indicators for the presence of a garage, fireplace, basement, and pool.

As I move from Census Tract fixed effects in model (2) to Census Block Group fixed effects in model (3), I see an increase in the magnitude of the subsidy eligibility estimate, and an improvement in the model fit of both models when compared to that of model (1). Importantly, the inclusion of spatial fixed effects also results in the positive estimate of floodplain location capitalization in model (1) becoming negative in models

(2) and (3). Without fixed effects, the proximity of floodplain locations to viewscapes and recreational opportunities spatially correlated with proximity to bodies of water conflates the amenity values with the risk premium. When holding such proximity 27 relatively constant and forcing identification to come from within spatial groups, the omitted variable bias of the amenity value is removed, revealing a negative capitalization of floodplain location. In both models (2) and (3), the value of floodplain location is approximately -1.0 percent, not substantially different than the average estimate of -0.6 percent found in a 2009 meta-analysis of 19 independent studies (Daniel, Florax, and

Rietveld 2009).

Models (1), (2), and (3) are the only specifications in which the impact of floodplain location on housing prices is separately identified from my use of fixed effects. When allowing floodplain location to capitalize flexibly across space through the inclusion of Block Group by SFHA fixed effects in model (4), I subsume floodplain location in my fixed effects and can no longer identify its impact, but I increase model fit and find that my estimate of subsidy eligibility capitalization more than doubles in magnitude. By further restricting identification to also come from price differences within

NFIP community by year groupings, I purge the potential for omitted variable bias from

CRS premium discounts and increase the explanatory power of my regression. With an average transaction price of $294,356 for flood prone homes, I estimate the average treatment effect on the treated to be $11,807, well within the bounds of the predicted outcomes from transactions between symmetrically informed participants holding varying degrees of information.

My difference-in-differences results are robust to considerable sensitivity analyses as shown in Table 2. One potential concern is whether my results could be biased by the inclusion of homes which were built long before or long after initial NFIP participation in

28 their community, and thus differ in unobservable ways from those homes built in closer proximity to the date of NFIP participation. I find no evidence that this is the case, as displayed in models (1) and (2) of Table 2. As I restrict the sample to only include homes built within tighter and tighter bandwidths of years before and after initial NFIP participation, the capitalized value of subsidy eligibility remains consistent, even as the number of observations decreases by over 50 percent. A further threat to proper identification is the possibility of the hedonic pricing gradient changing as the economy transitioned from boom to bust to recovery from 2005 through 2012. Once again, the difference-in-differences estimate is largely unchanged by restricting the sample to only include homes sold after the official end of the Great Recession according to the NBER, as in model (3). Finally, the exclusion of homes built in the same year as their community first joined NFIP has no impact on my results, as demonstrated in model (4).

Table 2: Difference-In-Differences Robustness

Variables (1) (2) (3) (4) (5) Built Prior -0.040*** -0.032*** -0.041*** -0.042*** -0.039*** (0.001) (0.001) (0.001) (0.001) (0.001) Subsidy Eligible 0.038*** 0.037*** 0.029*** 0.025** 0.039*** (0.006) (0.008) (0.009) (0.010) (0.006)

Maximum 30 Years Before 15 Years Before 60 Years Before 30 Years Before 60 Years Before Difference Participation / Participation / Participation / Participation / Participation / Between Year 30 Years After 15 Years After 40 Years After 30 Years After 40 Years After Built and Participation Participation Participation Participation Participation Community NFIP Participation

Time of First Following Following Following Great Following Great Following Sale in Sample Hurricane Hurricane Recession Recession Hurricane Katrina Katrina Katrina Including Yes Yes Yes Yes No Homes Built in the Year of NFIP Participation Spatial Fixed BG x SFHA BG x SFHA BG x SFHA BG x SFHA BG x SFHA Effects (74,846) (55,384) (72,050) (63,223) (83,134) Temporal Fixed CID x Year CID x Year CID x Year CID x Year CID x Year Effects (27,486) (23,332) (14,372) (13,430) (29,278) Observations 3,877,296 1,812,179 1,609,275 1,366,278 4,485,257 R2 0.863 0.864 0.877 0.879 0.863 Notes: ***, **, * indicates significance at the 1%, 5% and 10% level, respectively. Standard Errors have been clustered at the listed spatial fixed effect level. All models also include quarterly indicators and property characteristics. Property characteristics include all features listed in Table 1.

2.5.2 Spatial Heterogeneity

To examine heterogeneity of subsidy capitalization, I decompose the pooled sample into separate, statistical area specific samples. Figure 4 displays the spatial distribution of the results from the logarithmic model estimated separately for each statistical area. Several patterns are evident from this visual depiction. First, 37/49 primary statistical areas were 30 associated with positive capitalization values, though only 16/37 of these were statistically significant at the 10 percent level. Importantly, the majority of these positive and significant results are observed in areas where flooding is more common and where buyers and sellers are more likely to be better informed regarding the generosity of relief aid. Three of the four primary statistical areas in Florida produced positive and significant results at the 5 percent level (the fourth, Tampa, produced positive results not quite significant at the 10 percent level) and approximately 35 percent of all NFIP policies are associated with properties in Florida. The state with the second most policies in force,

Texas, had two of four statistical areas associated with positive and significant capitalization values. The number of policies in these two states constitute approximately half of the total for the whole country.

Figure 4: Spatial Heterogeneity in Subsidy Eligibility Capitalization

While statistically significant capitalization is also evident in riverine areas such as Portland and Minneapolis-St. Paul, as well as the heavily leveed Sacramento, the second most noticeable geographic concentration of Pre-FIRM rate capitalization is found along the eastern seaboard, from Boston to Washington, D.C. In total, 8/15 coastal statistical areas were associated with significant results, supporting my hypothesis that capitalization would be greater in markets where buyers and sellers have more familiarity with flooding and thereby more information regarding the value of subsidy eligibility.

2.6 Biggert-Waters: A Policy Experiment

To further examine the causal mechanisms driving subsidy capitalization, I use the recently enacted, and repealed, Biggert-Waters elimination of subsidies as a policy experiment. In the process, I provide the first targeted micro level analysis of this policy. I first discuss my identification strategy and the emerging associated literature before providing my results

2.6.1 Background Literature and Identification

Given that Pre-FIRM subsidies capitalize positively, their complete and immediate removal should negatively affect property values. Finding evidence of such an effect using the same data and empirical strategy as employed in my primary regression would further validate that my difference-in-differences estimates identify capitalization of Pre-

FIRM subsidies and do not represent a spurious correlation due to omitted variables. I return to my type A through type D classification of homes to update my identification strategy.

In addition to differences in location and the year the home was permitted for construction, I can construct a third difference using the year the home was sold, or more precisely, whether the home was sold before or after the implementation of BW12. If I now let P(Y0) represent the price of home Y if sold before BW12 and P(Y1) represent the price of home Y if sold after the implementation of BW12, then P(Y1)-P(Y0)=P(Y1-

Y0)=P(∆Y), or the change in price of a home when sold before and after BW12. Using property specific fixed effects, I restrict identification to come from variation in transaction prices for the same home sold before and after BW12, thereby greatly reducing the potential for omitted variable bias as I perfectly control for all time-invariant characteristics of each home. The triple difference estimator is then P(∆A-∆D)-P(∆B-

∆C), which I would expect to be negative as home A loses subsidy eligibility due to the

BW12 legislation. This causal effect is estimated as shown in equation (2.4). The triple interaction term is the causally identified variable of interest and the other variables which weren’t present in equation (2.3) are necessary controls for identification.

(2.4) ln(푃푖푗푡) = 훼0 + 훽ln (푋푖) + 휌푃푟푖표푟푖푗 + 휋푆퐹퐻퐴푖 + 휔퐵푊푖푡 + 훿(푆퐹퐻퐴 ∙

푃푟푖표푟)푖푗 + 휑(퐵푊 ∙ 푃푟푖표푟)푖푗푡 + 휆(퐵푊 ∙ 푆퐹퐻퐴)푖푡 + 훺(퐵푊 ∙

푆퐹퐻퐴 ∙ 푃푟푖표푟)푖푗푡 + 휇푖 + 휃푗푡 + 휀푖푗푡

I include two sets of fixed effects; property-specific fixed effects, μi, to control for time- invariant structural and spatial characteristics, and Census Tract by sale year fixed effects, 휃푗푡, to allow for spatial heterogeneity with regard to time-varying unobservables.

Despite the straightforward estimation strategy, identification is challenging. Bakkensen and Barage (2017) note that the short lifetime of the policy and the near dual incidence of

33 its enactment and the landfall of Superstorm Sandy, complicate causal inference. This is perhaps why recent attempts to estimate the capitalization of BW12 via hedonic difference-in-differences estimation in Rhode Island and New York City yield negative, yet statistically insignificant results (Bakkensen and Barrage 2017; Gibson, Mullins, and

Hill 2018). A third study, using a repeat sales model, finds impacts of BW12 similarly indistinguishable from zero in Virginia Beach and Miami-Dade County, but reveals a statistically significant capitalization of negative eight to thirteen percent in New York

City (Indaco, Oretga, and Taspinar 2018). However, all three of these studies estimate the impact of BW12 on the sale price of all SFHA properties in their respective samples despite the fact that BW12 was not designed to impact all SFHA properties. The only properties in SFHAs at the time of enactment which were to be impacted were severe repetitive loss properties or those which were eligible for subsidized premiums, either through Pre-FIRM rates or the less common grandfathered rates. As only 20 percent of all NFIP premiums were calculated using subsidized rates at the time of implementation, it is likely that the impact of BW12 is conflated with the price dynamics and “risk signals” of floodplain location, especially in New York following Sandy. Differentiating between subsidy eligible and non-eligible SFHA properties further complicates analysis and requires a triple difference estimation strategy. With a larger, more geographically diversified sample, I am able to assuage many of these concerns.

2.6.2 Triple Difference Results

Table 3 displays the results of my triple difference model similar to Table 1, with alternative sets of fixed effects becoming increasingly more restrictive from left to right.

Column (1) estimates the impacts of BW12 using the preferred fixed effect specifications from my difference-in-differences analysis, Census Block Group by floodplain and NFIP community by year. In addition to revealing a significantly negative result for my parameter of interest, Subsidy Removal, as this specification yields an estimate of subsidy eligibility capitalization essentially identical to that produced from the difference-in- differences estimator, it further supports my assertion that the parallel trends assumption is satisfied in my primary results.12 Restricting my spatial fixed effects to the property level removes the potential for any time-invariant omitted variable bias and leads to an estimate of subsidy removal capitalization nearly twice the magnitude of that from the specification in column (1), but subsumes time-invariant property characteristics, such as subsidy eligibility, in the fixed effect. As NFIP communities can span entire counties, I introduce Census Tract by year temporal fixed effects for my preferred model (3).

12 Triple differencing to resolve non-parallel trends dates back in theory to Moffit (1991) and in practice to Bell et al. (1999) with Wagstaff (2010) among a multitude of others utilizing this technique since. 35

Table 3: Triple Difference Results and Robustness to Fixed Effects

Variables (1) (2) (3) Built Prior -0.034*** (0.001)

Subsidy Eligible 0.038***

(0.006) Biggert-Waters 0.057*** 0.043*** 0.042*** (BW)

(0.001) (0.002) (0.002) BW x SFHA -0.008* -0.003 0.015*

(0.004) (0.007) (0.008) BW x Built Prior -0.033*** 0.017*** 0.016***

(0.001) (0.002) (0.002) Subsidy Removal -0.013** -0.020* -0.031** (Biggert- Waters x Subsidy (0.006) (0.011) (0.013) Eligible) Property Yes Yes Yes Characteristics Spatial Fixed BG x SFHA Property Property Effects (89,208) (596,847) (564,169) Temporal Fixed CID x Year CID x Year Tract x Year Effects (36,342) (25,481) (146,247)

Observations 5,639,103 1,226,470 1,159,056 R2 0.863 0.944 0.960 Notes: ***, **, * indicates significance at the 1%, 5% and 10% level, respectively. Standard Errors have been clustered at the spatial fixed effect level. All models include quarterly indicators. Property characteristics include all features listed in Table 1.

I consider nearly identical robustness tests as those used in the difference-in- differences models and I find that my triple difference estimator is highly robust. To lend further credence to my results, I subject my estimates to falsification tests for each term in the interaction as indicated in Table 4. All falsification tests replace treated observations with nearly treated observations to demonstrate that the treatment itself is

36 properly identified. Model (1) and model (4) remove all homes which have geographic property centroids located within floodplains and instead assigns floodplain location to homes located anywhere from 25 meters to 100 meters outside of a floodplain for the triple difference and difference in differences models, respectively. When interacted with the actual “Built Prior” half of the treatment effect, the estimate of the causal parameter in each model is imprecise and insignificant by any traditional measure. This suggests, as one would expect, that there is no conditional benefit for homes located near, but outside of floodplains built before NFIP participation in their community when compared to homes in the same location but built after participation. I find similar results when falsifying the “Built Prior” half of my treatment in model (2) and model (4). Excluding all homes which were built before their community first joined NFIP and before 1975, I instead assign “Built Prior” treatment to homes built one to twenty years following initial

NFIP participation in their communities. This preserves the same incidence as in the true sample of about half the homes qualifying as “Built Prior”. When interacted with true floodplain location, I find that homes in floodplains do not sell at a premium if they are built one to twenty years after their community joined NFIP compared to homes in the same floodplains built twenty one to forty years after NFIP participation. Falsifying the dates of implementation for BW12 in model (3) similarly yields no effects of BW12 on subsidy eligible properties during the two years prior to implementation, as one would expect.

Table 4: Falsification

Variables (1) (2) (3) (4) (5)

Built Prior -0.039*** -0.016***

(0.001) (0.001)

Subsidy Eligible -0.002 -0.012

(0.003) (0.007)

Biggert-Waters (BW) 0.042*** 0.046*** -0.240

(0.002) (0.002) (0.240)

BW x SFHA -0.005* 0.017 0.012

(0.003) (0.011) (0.010)

BW x Built Prior 0.016*** -0.002 -0.006*

(0.002) (0.002) (0.002)

Subsidy Removal (BW x 0.000 -0.008 0.006 Subsidy Eligible) (0.006) (0.015) (0.015)

SFHA Designations 25 to 100 Meters to 0 Meters to Nearest 0 Meters to Nearest 25 to 100 Meters to 0 Meters to Nearest Nearest SFHA SFHA Boundary SFHA Boundary Nearest SFHA SFHA Boundary Boundary Boundary

Pre-FIRM Designation Built Before NFIP Built Up To 20 Built Before NFIP Built Before NFIP Built Up To 20 Participation Years After NFIP Participation Participation Years After NFIP

Biggert-Waters Designation July 2012- July 2012- January 2010- January 2014 January 2014 December 2011

Spatial Fixed Effects Property Property Property SFHA x BG SFHA x BG (549,677) (330,429) (340,189) (99,969) (52,323)

Temporal Fixed Effects Tract x Year Tract x Year Tract x Year CID x Year CID x Year (143,354) (78,983) (108,750) (28,954) (22,024)

Notes: ***, **, * indicates significance at the 1%, 5% and 10% level, respectively. Standard Errors have been clustered at the spatial fixed effect level. All models include quarterly indicators.

While I find that BW12 led to an average loss in property value of approximately three percent for subsidy eligible properties, I do not observe a complete dissipation of the subsidy eligibility capitalization that one may expect to result from a direct transition to nonsubsidized rates. In accordance with my consideration of imperfectly informed market participants in the difference in differences model, a potential explanation for the disparity in magnitude between the positive capitalized value of subsidy eligibility and the negative impact of BW12 is a lack of awareness of the BW12 legislation. While homebuyers are able to compare flood insurance rates for different properties before closing, there is significant anecdotal evidence that suggests that homebuyers were not aware of the looming increases in flood insurance costs due to BW12.13,14,15 Because homebuyers inherit the remaining term of the flood insurance policy from the previous owner and because the policies have no regulated time at which they need to be renewed for the coming year, many homebuyers were likely unaware that the cost to maintain insurance would increase prior to receiving a bill for renewal. Figure 5 provides graphical evidence of this lack of awareness by plotting the relative incidence of three internet search terms related to BW12 over time and it shows that the intensity of all three of these terms peaked in October of 2013, over a year after the subsidies were eliminated for new homeowners. While this is in part due to the activation of additional components of

13 Anderson, Jenny. 2013. “Outrage as Homeowners Prepare for Substantially Higher Flood Insurance Rates.” The New York Times: https://www.nytimes.com/2013/07/29/nyregion/overhaul-and-a-hurricane-have-flood-insurance-rates-set-for-huge-increases.html 14 Liston, Barbara. 2013. “Coastal, Riverbank Homeowners Brace for U.S. Flood Insurance Hike.” Reuters: https://www.reuters.com/article/us-usa-florida-flood-insurance/coastal-riverbank-homeowners-brace-for-u-s-flood-insurance-hike- idUSBRE98N0EW20130924 15 Olorunnipa, Toluse. 2013. “Flood Inusrance Price Affecting Home Sales.” Insurance Journal: https://www.insurancejournal.com/news/national/2013/10/24/309110.htm 39

BW12 occurring at this time, such as the gradual rate increase for non-transferred subsidy eligible properties, the months leading up to October of 2013 show little signs of concern about the law. Though not exclusive of other explanations for the discrepancy between the difference in differences and the triple difference estimates, in addition to the anecdotal evidence, this trend in searches is suggestive of a general lack of full awareness of pertinent legislation.

Figure 5: Public Curiosity Concerning Flood Insurance Subsidies and Reform

2.7 Summary and Concluding Remarks

This analysis provides the first causal evidence that Pre-FIRM premium discounts capitalize and that suddenly terminating them is likely to result in a significant loss in property values. While the potential negative impact of subsidized premiums on housing values is cited as the reason for repealing a key provision of BW12 that eliminated subsidies for new property owners, little formal evidence informed this concern. I fill this

40 void in the literature by utilizing a large, nationwide dataset and quasi-experimental framework to compare property values across floodplain boundaries and temporal eligibility designations via difference-in-differences and triple difference identification strategies.

This research demonstrates that while HFIAA is often criticized for catering to rent seekers and imprudently repealing rare, fiscally-sound, bipartisan-backed legislation, its crafters were accurate in their concern that immediately terminating subsidies for new homeowners would decrease the price sellers command in the market. This predicted loss of $11,800 per affected household is well within the range of results which a model of asymmetrically informed market participants would predict. My identification strategy and the hypothesized absence of perfect information are both supported by my regional level analysis as well as the combination of the nearly complete dissipation of subsidy capitalization evident in my triple difference results with anecdotal evidence and the

Google Trends data associated with the BW12 legislation.

Two final comments bear mentioning for interpretation. First, though I can unambiguously identify which metropolitan regions will suffer the most from complete subsidy removal in terms of losses in housing values, I do not have information regarding property specific incomes or demographics and can thus not comment on who most confronts these losses within markets. For considerations of equity, readers are directed to recent work by Smith and Kahn (2017) which suggests that low-income property owners are not the primary beneficiaries of subsidized flood insurance premiums along the Gulf Coast or the structural modelling of residential sorting behavior and potential

41 flood insurance reform in the Miami area by Bakkensen and Ma (2019). Secondly, while

I do not have the data to compare the capitalization of Pre-FIRM subsidies following the implementation of HFIAA with the periods prior and thus offer any definitive analysis of the impact of premium escalation on the capitalized value of Pre-FIRM eligibility, as immediate and full elimination of subsidized rates is tantamount to approximately a 100 percent rate increase and results in only a three percent decrease in price, I expect smaller losses associated with gradual increases as have been implemented to date.

Chapter 3: A Flood of Construction—An Analysis of the Role of Levees in Urban Floodplain Development

The 2019 spring floods in the Midwest of the United States provided a reminder of how heavily we rely on levees to mitigate damages from flooding and what can happen when they fail. Though managed by levee districts, many of the levees in this area were independently constructed in the early to mid-20th century and have little federal oversight. When faced with 50 percent more water than the previous high in 1952, it’s not surprising that dozens of levees failed. In fact, 62 levees breached across the

Midwest in March of 2019, with hundreds of miles of levees sustaining damage.16 While the total damage from these floods may not be known for months or years, early estimates predict losses totaling $3.5 Billion in Nebraska and Iowa, alone.17

While states such as Nebraska and Iowa have been the most recent victims of levee failures, exposure to similar risk is dispersed throughout the U.S., with the most notorious example occurring in New Orleans following Hurricane Katrina, and with many projecting a similar fate for Sacramento, California.18 As the 2017 Infrastructure

Report Card assessed the quality of the national levee system to be at a D level (with

16 Smith, M. and Schwartz J. “’Breaches Everywhere’: Flooding Bursts Midwest Levees, and Tough Questions Follow.” New York Times, March 31, 2019. https://www.nytimes.com/2019/03/31/us/midwest-floods-levees.html 17 Eller, Donnelle. “Farm Losses Drive Iowa’s Flood Damage to $2 Billion, Farm Bureau Economists Estimate.” Des Moines Register, April 3, 2019. https://www.desmoinesregister.com/story/money/agriculture/2019/04/03/iowa-flooding-nebraska-missouri- river-farm-losses-damage-2-billion-ag-group-bureau-crop-insurance/3351972002/ 18 Craig, Tim. “A Massive Storm Flooded Houston. Experts Say California’s State Capital Could Be Next.” October 29, 2017. https://www.washingtonpost.com/national/a-massive-storm-flooded-houston-experts-say-californias-state-capital-could-be- next/2017/10/29 43 many individual levees receiving failing grades), crucial and expensive repairs and maintenance are needed throughout the country to ensure these levees are effective.19

When prioritizing these improvements, it is essential to consider the impact that levee provision has on residential development. It is possible that by increasing the physical protection of vulnerable areas, the government may inadvertently induce perverse sorting behavior or moral hazard and encourage greater development of the leveed area. Although the levee reduces the annual risk of flooding, the increase in development may counteract this effort and ultimately increase the expected damages from a flooding event. This can occur in several ways. First, no levee provides 100 percent risk reduction. If the increases in protected value outpaces the reduction in the residual risk, total exposure to damages will be greater than before the levee was constructed or improved. Secondly, real flood risk isn’t as discrete as flood insurance maps would suggest and there is a greater gradient of risk than the purported spectrum of a 1 percent chance in a given year, a 0.02 percent chance or a 0 percent chance. If levees induce greater development and initiate agglomeration economies, peripheral development could be pushed to areas toward the edge of the protected area and could put more homes in vulnerable locations. Finally, by increasing the relative quantity of impervious surfaces and decreasing the absorptive capacity in leveed areas, induced development may increase the base flood elevation in leveed areas, leading to greater damages if a flood were to occur.

19 US American Society of Civil Engineers. 2017 Infrastructure Report Card. https://www.infrastructurereportcard.org/cat- item/levees/ 44

Collectively, these potential outcomes comprise “The Levee Effect” (Tobin

1995). Awareness of this phenomenon dates back to at least Gilbert White’s 1945

“Human Adjustments to Floods” and despite its history and intuitive rationale, empirical estimation of the relationship between levee construction and residential development has been limited. Prior work has largely relied on aggregated macro-level analysis to yield correlations of increased populations (Di Baldassarre et al. 2013; Hutton et al. 2018), increased conversion of forests to agricultural land (Stavins and Jeffe 1990) and increased number of structures within floodplains (White 1958; Montz 1986) with the construction of levees. Causal identification of the impact of levees on rates of residential development requires both a counterfactual estimate of the rate of development that would have occurred had the levee not been constructed and an explicit control for the highly endogenous determination of levee construction (i.e., levees are often built to protect areas expected to experience growth). I overcome these challenges and fill a hole in the literature using micro-level housing data in a difference-in-difference model of new housing development and a duration model of the timing of new housing development.

In this chapter I use the discrete construction of the Central and Southern Florida

Project levees in the mid-20th century and a count-data difference-in-differences identification strategy to causally identify the extent to which newly constructed levees impact the rate of residential development. The location of these levees is shown in

Figure 6. While minimizing the potential for omitted variable bias by relying on narrow spatial and temporal buffers as well as precise fixed effects, I find that the level of new housing construction per year increased by 57 percent in newly leveed areas.

Recognizing that the average age of federally affiliated levee systems is 55 years old, I extend my analysis to consider the enduring effect of historically constructed levees on current residential development patterns. Using a proportional hazard duration model, I find that the location of a parcel within an area receiving flood-risk protection from a levee increases development likelihood, albeit smaller in magnitude. My results suggest that not only do newly constructed levees significantly induce greater residential development, potentially increasing exposure, but also that housing markets may take decades to equilibrate following a relaxation of a constraint on developable land.

The results of this analysis are of both practical and theoretical significance.

While providing the first causal estimate of the impact of flood risk reduction from levees on residential development informs more accurate modeling of the levee effect, it also provides a critical input into ongoing policy discussions regarding floodplain reconnection and whether levees should be maintained and reconstructed or whether buyouts should be offered to rural residents behind their walls and some levees be removed to ease the burden on levees up and downstream. Overlooking the possibility that the maintenance, construction, or improvement of levees induces development and potentially increases vulnerability and exposure, biases the cost benefit analysis of flood risk management policy alternatives toward structural solutions. The results have the potential to better inform such comparative evaluations.

Figure 6: Central and Southern Florida Project Levees

3.1 Background

The history of flood prevention in the United States is long, with the earliest artificial levees being built before the arrival of European settlers. While decentralized and uncoordinated planning of earthen embankments along waterways characterized

American flood risk mitigation strategies up until the mid-19th century, the Swamp Land

Acts of 1849 and 1850 established a new precedent for government involvement in land reclamation and flood control. In addition to securing revenue to finance the construction of drainage canals and levees, these acts gave rise to the organization of levee districts with substantial autonomy, including eminent domain (White 1945). By the end of the

1800’s, publicly funded projects had begun lining the entire lower Mississippi River and had managed to desiccate Tulare Lake in central California, at the time, the largest freshwater lake west of the Mississippi.

Still, floods occasionally overwhelmed these levees, often with catastrophic consequences. Episodes of severe flooding led to a series of federally enacted Flood

Control Acts (FCA). The first of which, the FCA of 1917, represented the first act of

Congress to exclusively target flood protection (with no mention of land reclamation).

However, it was two later acts, the FCA of 1928 and the FCA of 1936, which established the federal government’s role as the primary provider of flood protection, putting federal spending on flood control on par with other public works projects. With nine more FCAs authorized following 1936 and with floods overcoming levees on an annual basis, levee heights have seen sustained growth over the years, with the typical Mississippi levee growing from a height of three feet in 1717 to eight feet in 1882 to twenty two feet in

1914 to thirty feet following the FCA of 1927.20 Considering this non-exhaustive history of growth for a representative section of a levee along the lower Mississippi and taking

20 US Army Corps of Engineers. “The Mississippi River & Tributaries Project: History of the Lower Mississippi River Levee System Information Paper.” October 2017. https://www.mvd.usace.army.mil/Portals/52/docs/Levees%20info%20paper.pdf 48 into account the fact that many of the more than 9,000 levee systems across the U.S. have experienced similar patterns of modernization, it often is more appropriate to consider the construction of levees to be a continual process rather than a discrete one. This renders the estimation of the impact of levee construction on residential development challenging.

Fortunately, historical accident yields at least one notable case of a more discrete pattern of levee construction. Due to the harsh conditions for development, the Civil War, and financial mismanagement of earlier efforts, by 1913, flood control infrastructure in

Florida did not exceed drainage canals and modest levees on the southern shore of Lake

Okeechobee. These levees were revealed to be woefully inadequate by the Hurricane of

1928 which caused the lake to overflow, killing 2,600 people in what is still the fourth deadliest natural disaster in U.S. history (Ogden and Davis 1994). While an improved levee was then built to contain Lake Okeechobee, it wasn’t until another period of intense flooding in 1947 that the impetus for systematic flood control was realized. Over a 25 day period, intense rains and hurricanes led to 90% of south eastern Florida being underwater, directly resulting in the FCA of 1948, authorizing a system of levees in southern and central Florida. With the universal flooding the summer before, and with the FCA of

1936 requiring all federally funded levees to pass a cost-benefit analysis, the levees authorized by the FCA of 1948 were to be constructed as soon as possible and specifically to protect existing populations, reducing the scope for endogeneity from levees potentially being located where populations were already expected to grow.

This system of levees, known collectively at the time as the Central and Southern

Florida Project for Flood Control and Other Purposes (C+SF), stretches nearly 1,000 miles and was constructed in several phases, with individual projects generally undertaken in order of urgency. The construction dates, impacted counties, and estimated protected value for these levees can be found in Table 5. In general, the East Coast

Protective Levees were constructed first followed by the levees surrounding of Lake

Okechobee and in the Everglades Agricultural Area (EAA).21 Finally, The L-31 levees were constructed in what is now southern Miami-Dade County. In total, there are 161 levee systems in Florida catalogued by the National Levee Database. The 20 included in my analysis are the subset of the larger population which have documented construction completion dates and were built in response to an FCA authorized between 1948 and

1968.

21 The EAA levees stand out as outliers when compared with the other C+SF Project levees as they were opportunistically constructed to reclaim and cultivate land south of Lake Okeechobee. Today, this area is the nation’s largest supplier of sugarcane, rice, and winter vegetables (EAA 2018 Pre-Harvest Celebration). My results are not sensitive to the inclusion or omission of these levees and are included for a more exhaustive account of the impact of the C+SF Project. 50

Table 5: Central and Southern Florida Project Levees

Leveed Protected Year of Levee System Name Area (Sq. Property County Completion Miles) Value East Coast Protective 1951 17 L $37 B Broward Levees, L-36, L-35A East Coast Protective 1952 11 L $9.73 B Broward Levees, L-35, L-37 East Coast Protective Levees, L-40, L-85, STA- 1952 116 $14.6 B Palm 1E East Coast Protective Miami- 1952 67 $2.04 B Levee, L-30 Dade East Coast Protective 1952 55 $11.7 B Broward Levee, L-33 L-8 North 1953 9 $1.74 M Martin L-8 East 1953 9 $132 M Palm EAA Ocean-Hilsboro 1955 33 L $2.46 M Palm L-14 1955 145 $1.65 B Palm L-20 1956 32 $1.72 B Palm L-25 West 1956 8 $2.54 M Palm L-8 West, L-10, and L-12 1956 47 L $40.4 M Palm North Central EAA 1956 39 $552 M Palm Southeast EAA 1957 174 $3.19 M Palm South Central EAA 1959 95 L $850 K Palm L-61 1961 11 $44.5 M Glades L-59 1962 33 $100 M Glades L-60 1962 19 $55.3 M Glades L-29 1966 868 $28 M Collier Miami- L-31 North 1967 75 $11.4 B Dade Miami- L-31 East 1968 55 $413 M Dade Miami- L-31 West 1970 12 $1.22 M Dade L-62 1973 15 L $2.66 B Okeechobee Notes: Only levees with identifiable dates of construction completion and located in counties with residential construction data are included in my analysis. L represents the length of the levees (in miles) when official data concerning the square mileage is unavailable.

While these federally authorized levees have provided sufficient protection to withstand decades of hurricanes and avoid catastrophic failures similar to those that plagued New Orleans in 2005 or the Midwest in 2019, concerns over structural integrity persist. As of 2015, the levees surrounding Lake Okeechobee were deemed to be

“critically near failure” and of “extremely high risk”.22 Though efforts are underway to repair this levee system and mitigate this increased risk, the remaining levees exist in a state of such disrepair that Florida lawmakers have requested additional federal funding to modernize and improve 68 other projects. Concurrently, pressure from environmentalist interest groups to restore the everglades has given rise to the possibility of removing some levees instead of maintaining or improving them.23 While Florida faces unique challenges in the face of climate change, this decision between preserving preventative infrastructure and reconnecting floodplains is shared by many municipalities across the country.

In response to The Flood of 1993, Congress authorized a study to formulate a comprehensive plan for flood risk management along the upper Mississippi River.

Though existing flood risk management facilities prevented up to 97% of the potential damages from The Flood of 1993, Hurricane Katrina highlighted the importance of preparing for residual risk. With this in mind, the study formulated, evaluated, and compared fourteen alternative plans for minimizing flood risk. The plans were generally distinguished by either supporting levee improvement without floodplain reconnection, supporting floodplain reconnection without levee improvement, supporting both, or maintaining the status quo. However, no mention was made of induced residential development attributable levee improvements or the limited number of new levees that

22 Mitnik, John. “Herbert Hoover Dike Rehabilitation Project.” South Florida Water Management District, February 10, 2016. http://my.sfwmd.gov/webapps/publicMeetings/viewFile/8673 23 US Army Corps of Engineers, South Florida Water Management District. “Comprehensive Everglades Restoration Plan Project Management Plan: WCA-3 Decompartmentalization and Sheetflow Enhancement Project Part 1.” March 2002. http://141.232.10.32/pm/pmp/pmp_docs/pmp_12_wca/decomp_main_apr_2002.pdf 52 could be constructed.24 San Franciscans may have similarly overlooked this important question as they recently authorized the construction of up to 20 miles of new levees at the expense of a greater amount of restored wetlands.25,26

Though there are important differences between areas vulnerable to riverine flooding and areas vulnerable to coastal or marsh and swamp flooding that may limit external validity, analyzing revealed behavior in Florida in response to the construction of levees provides insight into the housing supply response attributable to a perceived reduction in vulnerability. A critical input into the policy decision of whether to improve or remove levees is knowledge of the impact that such improvement or construction will have on the housing stock in the protected area. While several studies have found that those living in leveed areas underestimate their risk of flooding or take fewer protective measures (Atreya et al. 2015; Ludy and Kondolf 2012), this could reflect confirmation bias or a selection process which would render these residents unrepresentative of the greater population. To determine the average treatment effect on the treated (leveed) areas, I use a difference-in-differences identification strategy and a fixed effect Poisson model as described in the following section.

3.2 Methodology

There are three key components to my identification strategy. In this section I discuss them in turn, beginning with the count data specification necessary to account for the

24 US Army Corps of Engineers. 2008. “Upper Mississippi River Comprehensive Plan: Main Report.” https://www.mvr.usace.army.mil/Portals/48/docs/FRM/UpperMissCompPlan/UMRCPMainReport14Aug08update 25 Bay Area Council Economic Institute. “Surviving the Storm: Bay Area Council”. 2015 http://www.bayareaeconomy.org/files/pdf/SurvivingTheStorm.pdf 26 The San Francisco Bay Area Wetlands Goals Project. 2015. “The Baylands and Climate Change, What We Can Do: Baylands Ecosystem and Habitat Goals Science Update 2015”. The California Coastal Commission. 53 discrete and non-negative distribution of the data before moving on to the feasibility of difference-in-difference identification in nonlinear models. Finally, I address the stringent fixed effects needed to explain development patterns from the most recent decade back to the 1920s.

3.2.1 The Poisson Model

Models of development and land use change generally begin with a utility maximizing landowner deciding how to secure the greatest possible discounted return from their land

(Bockstael 1996, Irwin and Geoghegan 2001). However, while these models explicitly consider the individual behavior which gives rise to aggregate outcomes, the conversion of predicted probabilities of development into predicted development, itself, is not obvious and may require more information (Bockstael 1996). While I return to the atomistic model of development in my auxiliary analysis, as my ultimate goal is to estimate predicted development and its determinants, I explicitly consider a conceptual framework where development (or land use change) is characterized by the locally aggregated decisions of an undefined quantity of individual landowners. Following previous studies with similar emphases on predicting aggregate development outcomes, I recognize the count-data nature of my measure of development (Kline 2003; Towe et al.

2017). The Poisson regression model is the standard approach used to predict aggregate behavior when the distribution of the outcomes is characterized by smaller, positive integers and zero values (Greene 2002). This model originates from the premise that every outcome, yi, is drawn from a Poisson distribution:

푒−휆푖휆푦푖 (3.1) 푃푟표푏(푌푖 = 푦푖|푥푖) = 푦푖! 54 where yi are nonnegative integers and λi specifies the Poisson distribution, most commonly a loglinear model so that: ln λi = 휷Xi. Given this distribution, the expected number of events per period is:

훽푋 (3.2) 퐸[푦푖|푥푖] = 푉푎푟[푦푖|푥푖] = 휆푖 = 푒 so

휕퐸[푦푖|푥푖] (3.3) = 훽휆푖 휕푥푖

While the equivalence of the conditional mean and the conditional variance implied by equation (3.2) is an unrealistic assumption, it is nonconsequential for my stated goal of estimating the marginal effects of the covariates and their robust standard errors (Wooldridge 1999). To predict the conditional mean and thus produce unbiased estimates of the covariates, the only assumption required by the fixed effect Poisson model is that the conditional mean is correctly specified. Following Pregibon (1979), I test whether the square of the predicted values have any explanatory power when included in the regression. As I fail to reject the null that this value is equal to zero, I determine that the conditional mean is correctly specified.

I predict the number of homes built in year t, outside levee l, and in Census Block

Group BG according to the equation below:

(3.4) 퐸[푦푡,푙,퐵퐺|푥푡,푙,퐵퐺] = exp (훼 + 훽1퐿푒푣푒푒푑푡,푙,퐵퐺 + 훽2퐴푓푡푒푟푡,푙,퐵퐺 +

훽3퐿푒푣푒푒푑 ∗ 퐴푓푡푒푟푡,푙,퐵퐺 + 휇푡,푙,퐵퐺) where each of the included variables are 0/1 indicators (described more in subsection

3.2.2) and 휇푡,푙,퐵퐺 are fixed effects (described in detail in subsection 3.2.3). 55

3.2.2 Difference-in-Differences Identification in Nonlinear Models

I follow the canonical difference-in-differences estimation strategy where the required variables are comprised of two treatment effects and the effect of their interaction. In my case, these treatment effects are captured by whether an area is protected by a levee, whether the homes built in a given year were built after the construction of the levee. The interaction term captures whether an observation unit is in an area protected by a levee after the levee was built. The standard depiction of parallel trends is provided in Figure 7.

Here, the vertical axis represents the average number of homes built within a unit of analysis, while the horizontal axis represents the build year of the home relative to the year of levee completion (for example, the x-axis value for the count of homes built five years before the construction of the nearest levee would be -5. Several patterns are evident in this figure. First, the number of homes built in both permanently unleveed areas (represented by the grey line) and eventually leveed areas (represented by the black line) increase at a similar rate as the date of levee construction draws nearer, with growth in permanently unleveed areas consistently outpacing growth in eventually leveed areas.

Secondly, upon completion of the levee, growth in the now leveed areas accelerates and the number of homes built in these areas in a given year eventually eclipses the number of homes built in still unleveed areas. While the growth in the number of homes in permanently unleveed areas may slightly exceed that in eventually leveed areas prior to

56 the construction of a levee, the effect appears to be minimal and if a bias exists, it implies that my results are overly conservative.

Figure 7: Parallel Trends of Residential Development

Despite the popularity of the difference-in-differences estimation strategy, identification is controversial when this strategy is applied to nonlinear models such as the Poisson regression described by equation (3.4). Those who have argued against its validity have noted that because the expectation of the outcome variable is bounded, the treatment effect cannot be constant across treated populations and the cross difference of the potential outcome is not zero, which is the identifying assumption in a linear model

(Ai and Norton 2003; Athey and Imbens 2006). However, by applying the difference-in- differences identifying assumption to the unobserved latent linear index of a nonlinear model, identification comes not from the cross difference of the expectation of the 57 potential outcome being zero, but by the nonlinear parametric restriction on the cross difference (Puhani 2012). Therefore, the treatment effect is not simply the cross difference of the expectation of the observed outcome as it is in a linear model, but the difference of the cross differences of the expectations of the observed and potential outcomes, as shown in equation (3.5):

2 0 휕2퐸[푌|퐴,퐿,휇] 휕 퐸[푌 |퐴, 퐿, 휇] (3.5) 휏(퐴 = 1, 퐿 = 1, 휇) = − = [exp(훽 + 훽 + 훽 + 휇) − 휕퐴 휕퐿 휕퐴 휕퐿 1 2 3

exp(훽1 + 휇)] − [exp(훽2 + 휇) − exp(휇)] − [exp(훽1 + 훽2 + 휇) − exp(훽1 + 휇)] +

[exp(훽2 + 휇) − exp(휇)] = exp(훽1 + 훽2 + 훽3 + 휇) − exp(훽1 + 훽2 + 휇) where L = Leveed, A = After, and 휏 is the treatment effect of the difference-in-differences model. The treatment effect is then the incremental effect of the interaction term coefficient. As this is not 훽3, the coefficient on the interaction term, I report these two effects separately.

3.2.3 Fixed Effects in Count Data Models

As the nature of my historical identification strategy limits the availability of variables which I can include in my model, it is necessary to account for spatial amenities via the inclusion of fixed effects. Requiring identification to come from variation within small enough spatial groupings should hold most variables constant, including the price of land.

While it is possible that sharply delineated boundaries within some neighborhoods

(possibly elevated roads or drainage canals) demarcated areas where the price of land was susceptible to discrete changes over continuous measures of distance before the construction of levees, by considering 20 different levee systems covering more than

1,300 square miles, I don’t expect that this particular concern would result in systematic bias over estimates from the entire area covered by the C+SF Project levees.

The need for fixed effects also motivates the choice of the Poisson model over a negative binomial model. Despite the flexibility gained through the relaxation of the assumption that the conditional mean is equal to the conditional variance, negative binomial models are incompatible with traditional fixed effects when estimated by conditional maximum likelihood (Greene 2005; Guimaraes 2008). While it is possible to condition out the incidental parameters for each fixed effect group in a negative binomial regression, because this model allows for group-specific variation in the dispersion parameter, time-invariant variables are not necessarily subsumed under the fixed effect

(Hausman et al. 1984). This results in the fixed effect negative binomial model not providing a true “within-group” estimator and an inability to properly control for neighborhood level unobservable. It also results in the separate identification of covariates which are subsumed in the fixed effect (as demonstrated in Table 8 and discussed in Section 3.4). For these reasons, the fixed effect Poisson model is my preferred specification.

The creation of my preferred set of fixed effects is shown in Figure 8. The insert at the top-left of the image illustrates the location of the L-31 levees in southern Miami-

Dade County as bold lines. Behind these bold lines are the areas protected from flood risk by the levees, represented by white areas outlined by thin grey lines. As I want to hold as many spatial amenities constant across leveed and unleveed areas as possible, I restrict identification to come from changes within a mile of the boundary of the leveed area, as

59 depicted in the insert at the top right of Figure 8. Similarly, I disregard development patterns deep in the leveed areas, represented by the light grey in the insert at the bottom- left of Figure 8, restricting identification to come from differences in development patterns between the white and dark grey bands surrounding the levees. Following previous empirical work (Zhou et al. 2008; Kuminoff and Pope 2012; Turner et al. 2014), limiting my analysis to areas in close proximity to the border of leveed and unleveed land helps to ensure that unobservable attributes of the land and of the economic agents will vary continuously rather than discretely as the boundary between leveed and unleveed land is crossed.

Figure 8: Levee Construction Fixed Effects

Finally, to control for neighborhood specific amenities which may vary along the length of a given levee, I include Census Block Group fixed effects in the bottom-right insert of Figure 8. Identification is then required to come from changes in development patterns between the white and dark grey bands within Block Groups. In my preferred model, I further interact the set of fixed effects depicted in the bottom-right insert with a set of year dummy variables, which the requires identification to come from within only the Block Groups which have leveed and unleveed areas within a mile of a leveed area boundary. With this set of fixed effects, any time varying unobservables are controlled for at the neighborhood level. While this provides a high level of control, it also comes with a sizeable reduction in the observations included in my sample, as any Block Group which does not include both leveed and unleveed areas provides no variation for the within-group estimator. The impact this restriction has on my sample size is demonstrated in Table 6 in Section 3.4.

3.3 Data

There are two primary datasets necessary to implement this methodology: a detailed record of property transactions for the state of Florida purchased from national real estate information provider CoreLogic, and the National Levee Database. The record of property transactions consists of county-level assessor’s office data, providing information on spatial, structural, and sale characteristics of the property. For a property to appear in this dataset, it must have sold during the first decade of the 21st century.

While this may not provide the complete universe of residential structures in Florida, it is challenging to imagine a correlation between selection into this subset of the population

62 of residential structures and the residual component of the predicted count of homes per group in my model. I calculate the number of homes in each group by recording the year of initial construction for every home in my dataset as well as the geographic coordinates of the property centroids before aggregating them by the spatial and temporal groupings discussed in the previous section.

The National Levee Database is a congressionally authorized, publicly available, and continually updated record of the location and condition of the levees in the United

States. The database currently provides the location of over 8,000 levee systems covering approximately 30,000 linear miles. However, there are only complete records of risk and condition for 2,000 of these systems and these are primarily levees affiliated with the

United States Army Corps of Engineers. This inconsistency results in a number of levees with unidentifiable dates of construction or boundaries of protected area, rendering them potentially unusable for my analysis. Fortunately, the levees constructed in response to the FCAs of 1948 to 1968 are generally well documented, allowing for a more exhaustive analysis.

While other variables aside from levee protection likely influence the decision of when and where to build a home (see Section 3.5), in my primary analysis, I rely on the fixed effects to control for these other factors. This is partially in response to the availability of such data. Because I am restricting identification to come from within

Census Block Group by year groupings, differentiated only by whether they receive flood risk protection from a levee, and discarding transactions occurring more than a mile from the leveed area boundary, the scope for omitted variable bias is minimized and would

63 need to come from differences within neighborhoods. Table 6 demonstrates how the precision of my fixed effects removes a downward bias in my causal estimate.

3.4 Results

The four columns in Table 6 represent four models which have progressively more restrictive fixed effects when read from left to right. While the spatial unit of analysis is the same for all four models (the portion of the Block Group that is leveed or to be leveed in the future) and the counts are calculated for every year, the fixed effects range from the year level to the specific levee by Block Group by Year level. With the exception of model (2), which may suffer from an omitted variable bias related to the exclusion of temporal controls, the range of models demonstrates the magnitude and direction of the bias attributable to a failure to control for spatial and temporal omitted variables. Most importantly, the estimated impact of the treatment effect increases significantly from model (1) to model (4) and the tighter fixed effects also reveal the upward bias in the estimate of levee location (both before and after levee construction) when failing to control for annual effects at the neighborhood level. My preferred set of fixed effects also results in the failure to uniquely identify the effect of being built after the construction of the nearest levee due to collinearity with the fixed effect. As the fixed effect restricts identification to come from counts within the same levee system and year, there is no longer any variation in the year the home was built relative to the year the levee was built. However, even the less stringent fixed effects of models (2) and (3) illustrate the lack of significance for this estimate, as one would expect when controlling for annual effects at the neighborhood level.

While more restrictive fixed effects are essential in a model as parsimonious as mine, they come at the cost of a decrease in the effective sample size as many observations may belong to singleton groups, without any other observations sharing enough in common to help identify within-group variation. This effect is evident in Table

6, as my number of observations (levee-bifurcated Block Groups for every year) decreases from over 20,000 in model (1) to 3,000 in model (4). To assess the sensitivity of my estimates my controls for spatial and temporal proximity, I turn to Table 7.

Table 6: Difference-In-Differences Estimation of the Impact of Levee Construction on Housing Development with Fixed Effect Robustness

Variables (1) (2) (3) (4) Built in Leveed 0.551*** 0.570** 0.380*** 0.316*** Area (0.088) (0.156) (0.049) (0.045)

Built After Levee 0.537*** 1.203 0.662 Construction Completed (0.069) (0.202) (0.210)

Built in Leveed 2.112*** 1.651* 2.39*** 2.805*** Area After Levee Construction Completed (0.365) (0.424) (0.384) (0.494)

Treatment Effect 0.330*** 0.446*** 0.348*** 0.570*** (0.051) (0.177) (0.119) (0.102)

Fixed Effects Year (79) Block Group Block Group by Levee by Block (540) Year (2,212) Group by Year (1,568)

Observations 20,140 19,727 4,866 3,136

Spatial Proximity One Mile One Mile One Mile One Mile Temporal 30 Years Before 30 Years Before 30 Years Before 30 Years Before Proximity and After and After and After and After Notes: ***, **, * indicates significance at the 1%, 5% and 10% level, respectively. Reported coefficients represent the incidence rate ratios for all covariates. Robust standard errors are calculated according to Wooldridge (1999).

The four models in Table 7 each use the same preferred set of fixed effects from model (4) of Table 6, but manipulate either a spatial or temporal restriction on the data to assess whether my results are an artifact of how I select my sample. Importantly, the causally identified parameter is significant at the 1 percent level in all specifications, suggesting that while seemingly arbitrary restrictions to the temporal and spatial scope of my analysis may influence the magnitude of the point estimate, there is a qualitatively robust effect underlying my estimation.

Table 7: Difference-In-Differences Estimation Robustness to Varying Spatial and Temporal Sample Restrictions

Variables (1) (2) (3) (4) Built in Leveed 0.288*** 0.316*** 0.322*** 0.296*** Area (0.054) (0.064) (0.043)) (0.038)

Built in Leveed 2.409*** 2.360* 2.100*** 2.733*** Area After Levee Construction Completed (0.636) (0.654)) (0.328) (0.446)

Treatment Effect 0.405*** 0.430*** 0.353*** 0.514*** (0.140) (0.155) (0.070) (0.090)

Levee by Block Yes (628) Yes (532) Yes (2,972) Yes (1,709) Group by Year Fixed Effects

Observations 1,256 1,064 5,944 3,418

Spatial Proximity One Mile One Mile One Mile Five Miles Temporal 15 Years Before 15 Years Before 74 Years Before 30 Years Before Proximity and After and After, and 64 Years and After Excluding 2 After Years Before and After Notes: ***, **, * indicates significance at the 1%, 5% and 10% level, respectively. Reported coefficients represent the incidence rate ratios for all covariates. Robust standard errors are calculated according to Wooldridge (1999).

In models (1) and (2), the temporal restriction is minimized to 15 years, meaning that only rates of residential construction 15 years before or after the completion of the levee are compared. This allows me to rule out the possibility that my results are driven by changes in residential development attributable to factors unrelated to levee protection more than two decades before or after levee construction. This reduces the scope for time varying omitted variable bias. In model (2), the additional restriction is made to exclude observations in the two years before and after the completion of levee construction to allow for miscoded dates of levee completion or anticipatory effects. The results are not noticeably different from those in model (1).

Model (3) adjusts the temporal restrictions in the opposite direction, removing them completely and allowing identification to come from differences in rates of residential development within Block Groups up to 74 years before the construction of the levee or 64 years after the construction of the levee. This relaxation of the restriction to the sample almost doubles the number of observations from my preferred specification, but potentially introduces omitted variables bias, as evident in the significant decrease in the magnitude of the estimate of the causal effect. These results suggest that my preferred estimates are not an artificial product of arbitrary bounds on the temporal scope of my analysis. Finally, model (4) takes a similar approach with regard to the spatial restriction, allowing Block Groups up to 5 miles from the boundary of the levee-protected area to be included in the analysis. While the increase in the sample size isn’t quite as noticeable, neither is the decrease in the estimate of the causal effect, suggesting that the development in Block Groups 1 mile from the boundary of the levee-

67 protected area didn’t differ considerably from the development 5 miles from the boundary. This finding offers further evidence that my primary set of results are not attributable to the selection of arbitrary temporal and spatial thresholds.

In addition to probing the robustness of the results to the specification of the fixed effects or temporal or spatial restrictions to the sample, I can also assess the robustness of my estimates to modelling assumptions. First, when using the same fixed effects and sample restrictions as in my preferred specification, but using a negative binomial model instead of a Poisson model, I see little change in the estimates of my covariates when compared to the results in model (4) of Table 6. Because of the critiques mentioned in

3.2.3 and because use of a negative binomial fixed effect model results in the identification of a parameter which should be subsumed under the fixed effect, my preferred model is the fixed effect Poisson regression.

In addition to a fixed effect Poisson regression and a fixed effect negative binomial regression, I consider a fixed effect zero-inflated Poisson regression. The results from this specification and with annual fixed effects are displayed in model (2) of Table

8. I model the inflation of zero counts to arise from a panel of indicator variables representing every spatial unit of analysis to allow for the possibility of some Block

Groups remaining undeveloped for much of the sample timeframe. That the results from this specification are similar to those from model (1) in Table 6 suggests that the potential for bias attributable to zero-inflation is of minimal concern. This would be only more likely with my preferred set of fixed effects because only the Block Groups bifurcated by a levee would be included in the sample.

Table 8: Difference-In-Differences Estimation Robustness to Modelling Frameworks

Variables (1) (2) (3) Built in Leveed 0.319*** 0.597*** -0.537 *** Area (0.109) (0.011) (0.121)

Built After Levee 0.238* 0.850*** Construction Completed (0.196) (0.012)

Built in Leveed 2.660*** 1.768*** 0.413*** Area After Levee Construction Completed (0.836) (0.033) (0.135)

Fixed Effects Levee by Block Year (79) Levee by Block Group by Year Group by Year (1,568) (2,329)

Observations 3,136 20,140 4,658

One Mile and 30 Yes Yes Yes Year Sample Restrictions

Model Negative Zero Inflated Linear Binomial Poisson Regression Notes: ***, **, * indicates significance at the 1%, 5% and 10% level, respectively. Reported coefficients represent the incidence rate ratios for all covariates. Standard errors clustered at the Block Group by levee level.

Model (3) in Table 8 reports the results from a linear regression of the difference- in-differences estimator. To account for the skew in the data which arises from the discrete and non-negative distribution of the number of homes built in a given place and year, I consider logarithmically transforming my dependent variable to estimate a model similar to one which estimated the impact of political ideology on housing development

(Kahn 2011). However, since there are a non-negligible number of observations for which the number of homes built is zero, and as the log of zero is undefined, I instead

69 employ an inverse hyperbolic sine transformation. As the interpretation of a coefficient on a dummy variable in a model with an inverse hyperbolic sine transformed dependent variable is identical to the interpretation of a coefficient on a dummy variable in a model with a log transformed dependent variable, the coefficients on both variables should be interpreted as approximate semi-elasticities, subject to the transformation below

(Bellemare and Wichman 2019).

(3.6) 훽̃ = exp(훽̂) − 1

After making the appropriate correction, the linear model results suggest that newly constructed levees increase the rate of residential development by 51 percent, an effect similar in magnitude to that obtained from the fixed effect Poisson model difference-in- differences estimate.

In summary, the results suggest a highly robust, positive and significant causal impact of the construction of levees on rates of residential development. While the effect is less precisely estimated when the sample size nears 1,000 or when annual trends aren’t controlled for at the state or Block Group, the effect is still discernable and consistent.

3.5 Enduring Effects

While knowledge of the impact of levee construction on rates of residential development is imperative to understanding the relationship between protective infrastructure and vulnerability, as the average age of a levee is 55 years old, an equally policy-relevant question concerns what impact levees continue to have on patterns of housing construction. I supplement my primary findings by addressing this question using,

70 largely, the same data sources and a recent innovation in the land use and development literature.

To estimate the continued impact of 50 year old levees on rates of residential development, I face an identification tradeoff. As there is no longer a temporal dimension to my measure of flood protection provided by levees, I lose the ability to estimate the traditional, event-study style, difference-in-differences model. However, I benefit from the availability of contemporary data, specifically, property transaction prices. This allows me to more explicitly model the optimal stopping decision which characterizes the landowner’s choice of whether or not to develop a parcel of land (Capozza and Helsley

1989). This model operates under the premise that land should be converted to residential use at the time when the annualized value of the previous use of the land plus the expectation of the conversion capital opportunity cost equals the annualized value from residential development. While this has been a workhorse model of evaluating sprawl

(Irwin and Bockstael 2004; Livanis et al. 2006), agricultural land value forecasting

(Plantinga and Miller 2001; Guiling et al. 2009), and the tracking of real prices and speculative bubbles in metropolitan housing markets (Abraham and Hendershott 1994;

Goodman and Thibodeau 2008) for the past 30 years, it also assumes that price is exogenous. If price is endogenous and correlated with my variable of interest, then my estimate will be biased. I overcome this potential barrier to unbiased estimates by instrumenting for price with a control function.

As explained by Wrenn et al. (2017) there are several channels through which endogeneity could manifest in the real estate options value framework. However, because

71 this process is estimated with a nonlinear duration model, standard two stage least squared instrumental variable approaches are inconsistent. Wrenn et al. solve this problem by including the residuals from a first stage regression of the neighborhood price index on neighborhood-specific attributes and a weighted average of exogenous distant- neighborhood-specific attributes in the second stage duration model. The inclusion of this residual should effectively purge the model of correlation between the latent profitability of development within the given neighborhood and unobservable neighborhood attributes.

The instrumental variables needed to generate the residuals are derived from the theory of spatial equilibrium and take the form of a geographically weighted average of the exogenous neighborhood characteristics for neighborhoods outside a given buffer distance from the focal neighborhood. This decision proceeds from the logic that the exogenous characteristics from distant neighborhoods will impact the development in those neighborhoods (positively or negatively), which will in turn impact the price in those neighborhoods, which will either expedite or slow development in substitutable neighborhoods, potentially including the focal neighborhood. The process by which my instrumental variable is created is illustrated in Figure 9. The left panel depicts the

Census Tracts used to model neighborhoods in this auxiliary analysis. To be consistent with my difference-in-differences investigation, I only consider development southeast of

Orlando. The right panel in Figure 9 illustrates the Census Tracts in Broward County.

This panel details the difference between the focal neighborhood of interest, the local neighborhoods excluded from the calculation of the instrument to ensure exogeneity, and

72 the area weighted neighborhoods outside of the buffer. When calculating the instruments, the values of the exogenous neighborhood attributes for all neighborhoods outside of the local neighborhood buffer are averaged, weighted by their area.

Figure 9: Duration Model Scope of Study and Spatial Units

Because of the variance in the size of the Tracts, the local neighborhoods are not defined by a Euclidean distance, but by whether they are one of the N nearest neighbors.

The appropriate number of nearest neighbors to be omitted from calculating the instrument is determined by examining the size of the local neighborhood group which produces the strongest instrument. Instrument strength is assessed via the F-statistics for a series of first stage regressions with varying numbers of local neighborhoods omitted to calculate the instrument. These statistics are reported in the bottom row of Table 9.

Omitting 16 neighbors from the calculation of the instrument leads to the largest F- statistic, decreasing practically monotonically as the number of neighbors omitted both

73 increases and decreases. As this F-statistic is greater than 10, previous analysis suggests that this instrument is strong enough to be considered valid (Stock et al. 2002). The remaining rows of Table 9 illustrate how the area weighted instruments have opposite effects on price than the same variables in the focal neighborhoods. While a greater rate of development from 1990 to 2000 in the focal neighborhood has a negative and significant impact on price, greater development outside of the focal and local neighborhoods has a positive and significant impact on price in the focal neighborhood, as one would expect, lending further credibility to my instrument. The same can be said for the maximum slope for the dominant soil class.

Table 9: Control Function First Stage Results for Instruments and Relevant Neighborhood Characteristics

The results for both a naïve survival analysis and a duration model with a control function are shown in columns (1) and (2), respectively, of Table 10.27 As the coefficient on the control function residual is significant, it suggests that there is a downward bias on the estimation of price in the naïve analysis attributable to endogeneity. This is supported by the sizeable difference in the estimated impact associated with price, which increases by more than an order of magnitude when the residual from the control function is included in the analysis. The resulting estimate of the price elasticity of land supply is

1.08, within the bounds of previous estimates for such measures in Miami (0.60) and

Orlando (1.12) (Saiz 2010). Of most concern to this auxiliary model, accounting for endogeneity in price also reveals a slight upward bias regarding the impact of being leveed in the naïve analysis. However, this bias appears to be minimal and regardless of whether or not price endogeneity is accounted for, both models indicate that protection provided by levees increases the likelihood of being developed.

27 I supplement the data from my primary analysis with a variety of sources to calculate the parcel and neighborhood specific attributes. These sources include the National Hydrography Dataset, SSURGO data from the Natural Resource Conservation Service (NRCS), The University of Wisconsin-Madison’s Spatial Analysis for Conservation and Sustainability (SILVIS LAB), The Homeland of Infrastructure Foundation-Level Data (HIFLD) database, and Holian and Kahn’s (2015) database of Central Business District (CBD) coordinates. 76

Table 10: Results for Naïve and IV Duration Models

Variables (1) (2) Price 0.0001*** 0.007*** (0.000) (0.000) Residual -0.007*** (0.000) Leveed 0.025*** 0.021*** (0.004) (0.003) Flood Prone -0.170*** -0.159*** (0.003) (0.003) Distance to Lake 0.007*** 0.007*** (0.000) (0.000) Distance to River -0.005*** -0.005** (0.000) (0.000) Distance to Coast 0.001*** 0.001*** (0.000) (0.000) Distance to Park -0.014*** -0.015*** (0.000) (0.000) Distance to CBD -0.001*** -0.001** (0.000) (0.000) Distance to Road 0.011*** 0.011*** (0.000) (0.000) Distance to -0.022*** -0.021*** School (Private) (0.000) (0.000) Distance to 0.015*** 0.015*** School (Public) (0.001) (0.000) Maximum Slope 0.010*** 0.010*** (0.001) (0.001) Minimum Slope -0.125*** -0.112*** (0.013) (0.001) Soil Rank 0.002*** 0.006*** (0.001) (0.001) Development 0.0003*** 0.0003*** Growth 1999- (0.000) (0.000) 2000 (percent)

Percent of 2010 Housing Stock 0.255*** 0.099*** Undeveloped in (0.004) (0.004) 1990

Average -0.013*** -0.050*** Maximum Slope (0.001) (0.001)

Log-Likelihood -1,322,599 -1,309,166 Instrument No Yes Notes: ***,**,* indicate significance at the 1%, 5%, and 10% level, respectively. The standard errors are generated with a bootstrap procedure with 500 replications clustered at the parcel level 77

Overall, my exploration of enduring effects of historically leveed areas on rates of residential development suggests that the perceived protection afforded by levees in

Florida is still associated with a faster rate of residential development, conditional on price and other factors impacting the transition to the residential use of land. To consider how flood risk and levee protection jointly influence development, I can run the same model and include an interaction term between a variable capturing flood risk and a variable capturing the presence of a levee. Then, I can estimate the marginal effects of levees on the likelihood of development in areas where flood risk is effectively remediated and in areas still at risk of a 100-year flood. Doing so reveals that while levees increase the likelihood of development by 2.2 percent in safer areas, there actually appears to be a negative impact attributable to levees of 3.3 percent in areas at risk of a

100-year flood. This could reflect a greater concern for levee integrity in areas that would be most likely to suffer damage from a levee failure.

3.6 Summary and Concluding Remarks

This analysis provides the first causal estimate of the impact of the construction of levees on the rate of residential development. This relationship constitutes half of “The Levee

Effect”, a phenomenon that had been theorized for over 70 years yet had not been empirically tested beyond case studies of single levee systems. My findings suggest that the construction of levees induced residential development, increasing the number of new homes built in a given year by over 50 percent. This result is robust to various specifications and modelling decisions, lending further credibility to my causal estimate.

I also show that the positive impact of levee construction on residential development persists, in the case of southern Florida, up to 70 years after the levees were built. Though levee protection was not the causally identified parameter in this supplementary analysis, by controlling for the endogeneity of price, I reveal a slight upward bias in the naïve estimates. Contrary to the results from an analysis of the impact of levees on the value of commercial properties, I find that differences in flood risk and levee protection are distinctly incorporated into the sorting equilibrium (Fell and Kousky

2015). While more detailed data on the condition of individual levee segments could help further tease out heterogeneity in this effect, this result suggests that, on average, the mere existence of a levee does not lead to the oversight of all flood risk for land developers.

Together, these results inform both policymakers and scholars. In the broadest terms, my causal estimates justify the fear of “Field of dreams” levees: levees, which when built, induce greater development in the area they protect (Sun 2011). With this is mind, planners across all levels of government need to recognize the immediate and enduring effect that levee construction will have on residential development.

Chapter 4. A Consideration of Floodplain Buyout Capitalization Heterogeneity in Harris County, Texas

Of the three general approaches to mitigating flood risk, retreat is the least utilized.

However, in certain circumstances, it may be most cost effective to pay homeowners to abandon their residences in vulnerable areas rather than continuing to issue relief aid and pay flood insurance claims. This solution is particularly appealing along the coasts, and with looming sea level rise, the only option for reducing flood risk in some areas will be managed retreat (Kousky 2014).

As the use of eminent domain is often viewed as a last possible resort in the

United States, retreat is most commonly achieved through compensated buyout offers to homeowners. Buyouts are funded and authorized across multiple levels of government and the degree of public participation in these programs varies considerably across the areas in which they are implemented. While a higher rate of buyout offer uptake could be encouraged with more generous offers made to homeowners, as the costs of buyouts increase, the relative value of these programs relative to the status quo decreases.

Informing the structuring of these incentives is thus imperative to improving the efficiency of flood risk mitigation strategies across the country; an area which has seen little improvement over the past 30 years (Greer and Binder 2016).

In its simplest form, the decision to buyout a home is made if the expected costs associated with future floods (insurance claims, relief aid, etc.) are greater than the sum 80 of the costs of paying the homeowners to abandon their residences in vulnerable areas, razing the existing structures, and preparing the land for future use as either a vacant lot or part of a park.28 However, the comparison of total costs and benefits may not be this straightforward. Buyouts may be more or less advantageous if one considers potential economies of scale associated with spatially clustered buyouts29, if one accounts for the role of social capital and the use of extra incentives to encourage early adopters, or if one considers externalities that arise from buyout participation. This last consideration is especially interesting as it has the potential to increase or decrease the net costs associated with buyouts. If acquired parcels of land are left unimproved, they could become breeding grounds for mosquitos, gathering places for vagrants, or simply signs of community blight. In this case, floodplain buyouts would likely decrease nearby property values, thus increasing the real cost of the buyout. On the other hand, these unimproved lots may still provide positive amenities through increasing access to open space, improving flood risk resiliency via increasing absorptive capacity and decreasing impervious surface, and they can even be incorporated into local parks. If this were the case, the net cost of property buyouts would be less than it naively appears, possibly permitting more generous offers to be made and further increasing buyout participation.

In this chapter, I estimate the impact of floodplain property acquisitions on nearby housing values to better understand the overall costs of property buyouts.

28 FEMA (2016) Mitigation best practices: Buyouts a win-win for Harris County and residents. FEMA, Washington, D.C. 29 The Nature Conservancy (2019) Strategic Property Buyouts to Enhance Flood Resilience: Creating a Model for Flood Risk Reduction, Community Protection and Environmental Gains. The Nature Conservancy, Arlington, VA. 81

To lend greater external validity to my evaluation of floodplain buyout programs,

I also consider heterogeneity in the treatment effect. Heterogeneous impacts along sociodemographic lines would be consistent with findings from studies of related environmental changes. In general, poorer households often stand to lose from environmental gentrification, as richer households migrate into areas with improved environmental quality and poorer households are displaced into communities where the increased housing prices are not fully offset by environmental improvements (Sieg et al.

2004). Specific examples of richer households benefitting from environmental changes and poorer households becoming worse off include the response to ozone concentration reduction in Southern California, hazardous waste site remediation, and relocation into risk-differentiated areas in the aftermath of a catastrophic hurricane (Sieg et al. 2004;

Smith et al. 2006; Gamper-Rabindran and Timmins 2011). Similarly, environmental interventions often have heterogeneous impacts across space, for example, stream restorations (Towe et al. 2019; Polyakov et al. 2017), shale gas exploitation (Klaiber and

Gopalakrishnan 2013; Balthrop and Hawley 2017), and wind farm development (Krueger et al. 2011; Heintzelman and Tuttle 2012).

There have been few attempts to estimate the capitalized value of floodplain property acquisitions, and none which have accounted for heterogeneous effects according to neighborhood quality. Valuation of the Meramec Greenway outside St.

Louis, MO (an amalgamation of acquired properties, public, and private lands) found that for homes located within five miles of the Greenway, for every 1,000 feet closer a home was to any park, transaction prices increased by 1 percent (Kousky and Walls 2014).

Similarly, a survey of 250 residents of Lexington, KY found that only 18 percent of respondents thought that their property values were positively affected by nearby floodplain buyouts (Zavar 2014). However, not accounting for heterogeneous treatment effects across spatial and socioeconomic boundaries limits the external validity of estimation of externalities from floodplain property buyouts. By explicitly allowing neighboring buyout decisions to capitalize differently as neighborhood quality changes, I can better inform where property buyouts are most cost-effective.

Using a hedonic pricing model with property level, annual, and quarterly fixed effects, I find that the distance to the nearest buyout has a statistically significant price elasticity of -2.9 percent in my study area, Harris County, Texas (Figure 10). For the average home in my sample, this translates to an implicit price of $556 for a 1,000 foot reduction in the distance to the nearest buyout.30 However, this impact differs across neighborhoods of varying quality and in proximity to the buyout. Results from property fixed effect models and a repeat sales model all indicate that buyouts have negative effects on housing values in lower quality neighborhoods (as measured by local unemployment rates, poverty rates, median income, and average housing prices). This heterogeneity is especially pronounced when considering buyouts within the same housing development or block. Using various distances to capture whether a buyout would be visible from a home or whether the homeowners are likely to see the buyout on a frequent basis, I find that intra-development buyouts may decrease housing values by as

30 Following Bin 200, Mahan et al. 2000, and Bin et al. 2016, among others, I find the marginal implicit price for a logged distance variable by multiplying the price by the distance coefficient and dividing by the distance. Using the average transaction price of $226,472 and the average distance to the nearest buyout of 3.6 kilometers, this yields an implicit price of $556 for a 1,000 foot reduction, similar to estimates of the implicit price for the same reduction in distance to the nearest wetland ($436-$485). 83 much as 15 percent in low quality neighborhoods, but this effect diminishes, even becoming positive, as neighborhood quality improves.

Figure 10: Houston, Harris County, and the United States

The contributions of this work are threefold. By providing the first hedonic analysis of the impact of property buyouts on nearby housing values which uses official municipality provided information to identify buyout properties, I avoid conflating the average impact of a buyout with the value of open space or parks. Secondly, by relying

84 on temporal variation to identify treatment in addition to cross-sectional variation, I am able to limit the scope for endogeneity biasing my treatment effect. Finally, I provide the first estimates suggesting that property buyout externalities may benefit wealthier homeowners while harming poorer homeowners. While this finding may justify more generous offers and thereby move more homeowners out of vulnerable areas, it also raises red flags about the equity of floodplain property buyout programs.

4.1 Background

The process of acquiring properties in floodplains in the US typically transcends multiple layers of government. While local or state governments ultimately have the final say in selecting which properties are to be acquired, the majority of the funding is typically sourced from a federal governmental program. This funding permits a degree of oversight from the federal government which often results in limitations on the use of the funds.

The intent is to direct resources toward more efficient and environmentally sound activities.

The primary federal programs responsible for funding floodplain property buyouts are the Federal Emergency Management Agency (FEMA) and the Department of

Housing and Urban Development (HUD). Following disasters, state or local governments may apply for Hazard Mitigation Grant Program (HMGP) funding from FEMA or

Community Development Block Grants for Disaster Recovery (CDBG-DR) from HUD, with standard Community Development Block Grant (CDBG) funding as well as funds from FEMA’s Flood Mitigation Assistance (FMA) program and Pre-Disaster Mitigation

(PDM) program being available on a less restricted basis. All requests for federal funds to

85 be used for buyouts must satisfy a cost-benefit analysis as well as program-specific requirements (e.g., CDBG/CDBG-DR funds must be used to benefit low or moderate income (LMI) households and FMA funds should be directed toward projects which will reduce or eliminate future National Flood Insurance Program (NFIP) claims, such as for severe repetitive loss properties). Program specific incentives may be included to further a variety of goals including relocation, participation, or social equity.

Following approval of the federal funds request, offers are made to the locally suggested properties based on fair market value (FMV) for the property according to a licensed appraiser. While some programs such as the HMGP require offers to be made for the pre-disaster FMV to increase participation, some programs such as the CDGB allow for offers to be made for the post-disaster FMV to help suppress costs. Though applications for HMGP and CDBG-DR funds follow a Presidential major disaster declaration, the process may not be completed for up to three years. Conversely, real estate investors may offer to buy damaged properties within a few weeks of a flooding event, with the intention of rebuilding structures on the often valuable land. Though these offers are unlikely to match the pre-disaster FMV offered through a buyout, they provide a more immediate escape for households with limited means while increasing rather than decreasing exposure to future damages. The ramifications of this competition were evident in the aftermath of Hurricane Harvey in 2017. Before properties could be

86 acquired with governmental funds, within six months of the storm, between 5,500 and

12,000 homes flooded by Hurricane Harvey were sold on the private market.31

Despite the inability to completely fend off such opportunistic speculation, the

Harris County Flood Control District (HCFCD) has maintained one of the most successful floodplain property acquisition programs in the country, having purchased roughly 3,000 properties in the past 30 years and restored over 1000 acres of absorptive capacity.32 The need for buyouts in Harris County can be attributed to the topography- driven floodplain prevalence and the rapid development experienced by the county over the past half century.33 With developable land becoming more and more scarce and with the boundary of the commuting zone growing further away, flood prone areas became more palatable to developers and there now exist 20,000 parcels worth upwards of $13.5 billion in Harris County floodways, the innermost vulnerable section of the floodplain.34

Following the combined $1.7 Billion in damages wrought by Tropical Storm Claudette in

1979 and Hurricane Alicia in 1983, as well as intense flooding events in 1984, the

HCFCD began offering buyouts to homes “hopelessly deep” in the floodplain in 1985.

Since this time, the HCFCD has acquired more flood prone properties than any other

31 Hunn, David and Matt Dempsey. 2018. “In Houston’s flooded neighborhoods, real estate investors see an opportunity.” Houston Chronicle: https://www.houstonchronicle.com/news/houston-texas/houston/article/houston-harvey-flood-homes-real-estate-investor- 12901718.php 32 Harris County Flood Control district. 2018. “Home Buyout Program: Benefits and accomplishments.” https://www.hcfcd.org/hurricane-harvey/home-buyout-program/benefits-accomplishments/ 33 Berke, Philip R. 2017. “Why is Houston so vulnerable to devastating floods?” The British Broadcasting Corporation: https://www.bbc.com/news/world-us-canada-41107049 34 Collette, Mark and Matt Dempsey. 2018. “What’s in Houston's worst flood zones? Development worth $13.5 billion.” Houston chronicle: https://www.houstonchronicle.com/news/houston-texas/houston/article/What-s-in-a-floodway-In-Houston-20-000- 12409821.php 87 community in the country.35 These buyout prevented as many 1,500 properties from being flooded in the Tax Day Flood of 2016.36

Still, the HCFCD buyout program has been less than perfect. In total, the HCFCD has identified 72 target areas (indicated by bullseyes in Figure 11) where they are focusing their acquisition efforts, with nearly 6,000 of the original 9,000 properties identified in these areas still owned by private households.37 These 6,000 homes are a small fraction of the estimated 162,000 buildings which still exist in floodplains and contributed to the 154,170 homes flooded by Hurricane Harvey.38,39 4,000 households have made voluntary requests for their residences to be acquired, and of these 4,000, only

261 have been bought out due to higher priority properties and insufficient funds. In accordance with the apparent public desire for buyouts, in 2018, a $2.5 billion bond was passed in Harris County by a 70 point margin to finance nearly 240 flood control projects.40

35 Kinder Institute for Urban Research. 2018. “After Harvey, how can Houston improve the buyout process?” Rice University: https://kinder.rice.edu/2018/02/05/after-harvey-how-can-houston-improve-the-buyout-process 36 FEMA. 2018. “Mitigation Best Practices: Buyouts a win-win for Harris County and residents.” https://www.fema.gov/medialibrary-data/1476297832662-44ccff303de9557797d45edab1aa656f/41-Buyouts_a_Win-Win_web-r.pdf 37 Anchondo, Carlos. 2019. “Report: Harris County buyouts of flooded homes have been less than strategic.” The Texas Tribune: https://www.texastribune.org/2019/03/01/harris-county-buyouts-flood-prone-hurricane-harvey-homes-strategy/ 38 Morris, Mike and Matt Dempsey. 2018. “Even after Harvey, Houston keeps adding new homes in flood plains.” Houston Chronicle: https://www.houstonchronicle.com/news/houston-texas/houston/article/Even-after-Harvey-Houston-keeps-adding-new- homes-13285865.php 39 Lindner, Jeff. 2018. “Memorandum: Immediate Report—Final Hurricane Harvey Storm and Flood Information.” Harris County Flood Control District: https://www.hcfcd.org/media/2678/immediate-flood-report-final-hurricane-harvey-2017.pdf 40 Smith Morgan and Kiah Collier. 2018. “Harris County voters pass historic $2.5 billion for flood control.” The Texas Tribune: https://www.texastribune.org/2018/08/25/Harris-County-flood-control-vote/ 88

Figure 11: County-Defined Buyout Target Areas

Despite the number of volunteers for buyouts and the degree of public support for funding flood control projects, without the power of eminent domain or drastically increased flood insurance premiums, the HCFCD’s only option for acquiring the 6,000 holdouts in the target areas before the next flooding event is to increase the generosity of the buyout offer. As these more generous offers would be susceptible to a cost-benefit analysis. While the Hazard Mitigation Assistance Guidance (covering the HMGP, PDM, and FMA) offers insight into the values used to determine economic feasibility, there is no mention of spatial externalities or differences in how these externalities capitalize

89 according to neighborhood quality (FEMA 2015). The following section describes how I identify the heterogeneity of this effect and inform estimation of the benefits associated with floodplain property acquisition.

4.2 Methodology

In this section, I discuss my primary estimation strategy which utilizes both cross- sectional and temporal variation to estimate the treatment effect. To lend further credibility and assuage any concerns that are results are contaminated by spatial or temporal omitted variable bias, I also discuss an alternative estimation strategy.

4.2.1 Hedonic Regression and Specification

My primary model (and the foundation for my supplementary models) is the first-stage hedonic regression (Rosen, 1974). This model follows from the assumption that observed property transaction prices represent an equilibrium between the offers of homes for sale and the bids for those homes made by utility maximizing households. Every point of tangency between the bids and offers of the sellers and buyers represents a transaction and contributes to the model of the equilibrium price below:

(4.1) 푙푛푃푖푗푡 = 훼0 + 훽푙푛(푋푖푡) + 훿푍푖푡 + 휃퐵푢푦표푢푡푖푡 + 푢푖푗푡 + 푒푖푗푡

Where Pijt is the price of home i sold in year t and in neighborhood j, X and Z are matrices of continuous and discrete attributes, respectively, for home i, a is a constant, uijt represents my set of spatial and temporal fixed effects (discussed in greater detail below), and eijt is an error term. The average effect of a buyout is captured by the coefficient on the variable, Buyout, which is zero if there is not a floodplain buyout within a tenth of a mile from home i at time t and a value of one if a buyout is located within this proximity

90 to home i at time t.41 Both the dependent variable and continuous independent variables are logged as this functional form has been demonstrated to offer the greatest reduction of bias in the estimate of spatial characteristics in the presence of time-varying omitted variables when compared to linear, box-cox linear, quadratic, and box-cox quadratic functional forms in a simulated analysis (Kuminoff, Parmeter, and Pope 2010). In this specification, the estimated parameters represent elasticities for continuous variables and approximate semi-elasticities for discrete variables.42

To consider heterogeneous treatment effects I introduce a variable which roughly measures the quality of the given neighborhood. I then add an interaction term between this variable and my measure of proximity to a buyout to estimate how the impact of a buyout on housing values differs in richer and poorer neighborhoods. The final specification for my hedonic regression is then:

(4.2) 푙푛푃푖푗푡 = 훼0 + 훽푙푛(푋푖푡) + 훿푍푖푡 + 휃퐵푢푦표푢푡푖푡 + 휌푄푢푎푙푖푡푦푖푡 +

휋푄푢푎푙푖푡푦 ∗ 퐵푢푦표푢푡푖푗푡 + 푢푖푗푡 + 푒푖푗푡

The fixed effects, uijt, in both equations (4.1) and (4.2) are essential to my identification strategy. I consider a variety of fixed effect specifications including sale year, school district and sale year, census tract and sale year, census tract by sale year, property and sale year, and property and census tract by sale year. Each set of fixed effects introduces a tradeoff of identification. While narrower, more fine-scale fixed effects require

41 When assessing robustness to alternative specifications of my treatment effect, continuous measures of distance to a buyout are logged for consistency with the treatment of my other continuous variables 42 To obtain the semi-elasticity for the discrete variables, one exponentiates the parameter and subtracts 1 from this term (Halvorsen and Palmquist 1980) 91 identification to come from within smaller areas, thus possibly ignoring capitalization of distances which may span across spatial fixed effect boundaries, they also provide greater control for spatially varying unobservables which could bias the results if otherwise unaccounted (Abbot and Klaiber 2011). My preferred sets of fixed effects include property level as well as annual and quarterly controls. With property level fixed effects,

I require identification to come from temporal variation in the treatment effect, i.e., whether a buyout occurred in the vicinity of the reference property in the time between earlier and later sales of the same reference property. This strategy holds all time- invariant attributes (property acreage, home size, location to the central business district, etc.) constant, reducing the scope for omitted variable bias.

4.2.2 Repeat Sales Model

A similar method to the property fixed effect hedonic regression is the repeat sales model

(Palmquist 2005). First developed by Bailey, Muth, and Nourse in 1963, this class of models has become a standard tool of environmental valuation following modifications by Palmquist in 1982 and relies on perfect control for time invariant attributes through repeated observations to reduce the potential for omitted variable bias. To derive the repeat sales model, specify a hedonic price function for property i selling at time t as:

(4.3) 푃푖푡 = 푓(푋푖푡, 퐸푖푡, ℰ푖푡)

Where Pit represents a vector of transaction prices, Xit, a matrix of locational and structural characteristics at time t, Eit measures time-variant environmental attributes, and

εit is an idiosyncratic shock.

Applying the standard assumption of a semi-logarithmic functional form and geometric depreciation, yields:

(4.4) 푃푖푡 = 훾 exp (훽푋푖푡 + 훿퐸푖푡 + 휏1푇푖1 + 휏2푇푖2 + ⋯ + 휏푁푇푖푁 + ℰ푖푡)

Such that the Ti’s are dummy variables equal to one when t = T and zero for all other values of t.

With multiple transactions, occurring in period s and again in period t, the following analogues emerge from equation (4.4):

(4.5) 푃푖푠 = 훾 exp (훽푋푖푠 + 훿퐸푖푠 + 휏1푇̃푖1 + 휏2푇̃푖2 + ⋯ + 휏푁푇̃푖푁 + ℰ푖푡)

(4.6) 푃푖푡 = 훾 exp (훽푋푖푡 + 훿퐸푖푡 + 휏1푇푖1 + 휏2푇푖2 + ⋯ + 휏푁푇푖푁 + ℰ푖푡)

Taking the ratio of (4.5) and (4.6) then eliminates time-invariant characteristics and results in the following estimable equation:

푃푖푡 (4.7) 푙푛 ( ) = 훿(퐸푖푡 − 퐸푖푠) + 휏1(푇푖1 − 푇̃푖1) + 휏2(푇푖2 − 푇̃푖2)+. . 푃푖푠

+휏푁(푇푖푁 − 푇̃푖푁) + 휎푗 + 푣푖푡푠

Where Eit, captures the environmental attribute, in this case whether a property has been bought out within a tenth of mile from the respective home at time t. As Eit takes on a dichotomous 0/1 value then (Eit – Eis) is also either 0 or 1. Because t > s, (Eit – Eis) is always nonnegative, enforcing the condition that a property bought out at time s can’t be resold at time t. On the other hand, (푇푖퐾 − 푇̃푖퐾), is not necessarily nonnegative. If t = T then the term takes a value of 1 to indicate when the property last sold. If t = 푇̃ then the term takes a value of -1 to indicate when the property first sold. For all other values of t, the bracketed term will equal 0. To capture variation in appreciation by neighborhood, I 93 can also include spatially delineated fixed effects, 휎푗. Finally, the difference of the error terms, vits = εit – εis, is itself an idiosyncratic shock. Interpretation of 훿 mirrors the interpretation of the treatment effect in the hedonic regression with property fixed effects.

While traditional repeat sales models were restricted to only using two sales of the same property, I follow recent advancements and use all possible transaction pairs from my cleaned sample (Case et al. 2006).

4.3 Data

My primary dataset comes from CoreLogic, a national information intelligence provider, and consists of structural, spatial, and sale characteristics for properties sold in Harris

County, Texas from 2000 until early 2016. While this timeframe notably excludes properties sold following Hurricane Harvey in 2017, Houston, and greater Harris County, were subjected to multiple intense flooding events over these 17 years including Tropical

Storm Allison in June of 2001, Hurricane Rita, shortly after Hurricane Katrina in 2005 and the Memorial Day flood of 2015.

Figure 12 depicts the relative incidence of private market sales and government buyouts for single family residences in every year in my sample. For both types of transactions, the majority of purchases occur prior to the Great Recession which appears to have significantly suppressed the traded volume of homes. Furthermore, although the majority of buyouts occur in the three years following Tropical Storm Allison, because I consider both homes acquired with FEMA’s HMGP funding and homes acquired using

FMA, PDM, or CDBG funding, there is a non-negligible number of properties acquired during years in which there have been no recent flooding events.

Figure 12: Relative Intensity of Buyouts and Arms’ Length Transactions by Year

Figure 13 depicts the location of 3,158 properties classified as “buyouts”. As the

CoreLogic data contains information regarding the buyer and seller of each parcel, the properties highlighted in Figure 13 were identified as the treatment if they were purchased by the Harris County Flood Control District. Though there are some isolated buyouts, there are also evident clusters of property buyouts, potentially providing greater cost savings by allowing the local government to delete utility lines to these areas and potentially combine the vacated parcels to form parks. Figure 13 also displays the spatial heterogeneity of neighborhood quality.43 The combination of these two elements reveals

43 Neighborhood Quality is measured with the poverty rates, unemployment rates, and median incomes for the 2000 Decennial Census Tracts. Tracts with values in the top quartile of the distributions for each variable (unemployment and poverty rates below 2.1 percent and median income above $72,000) are illustrated in charcoal, while Tracts with values in the top half of the distributions for 95 that while many of the properties acquired by the Flood Control District are in lower quality neighborhoods immediately north of Houston, there is a considerable number of buyouts in the wealthier and more prosperous neighborhoods to the northwest of

Houston, an area that has experienced substantial growth over the previous decades.

Figure 13: Location of Buyouts and Neighborhood Heterogeneity

each variable (unemployment rate below 3 percent, poverty rate below 4.5 percent, and median income above $56,000) are illustrated in dark gray. “Lower quality” neighborhoods have values above or below these thresholds and are illustrated in light gray. 96

Following customary hedonic regression cleaning processes, non-buyout property transactions were included in the final sample if they were single family residences which were not built to order. Transactions that were likely the result of real estate flipping or county auditor coding errors were discarded be removing sales occurring twice within 12 months and sales of the same property for the exact same value. Homes sold for more than $5,000,000 or less than $5,000 were also removed from the sample to prevent non- standard transactions and outliers from driving the results.

Though time-invariant distances drop out of my hedonic models with property fixed effects and the repeat sales model, supplementary datasets include the National

Hydrography Dataset, FEMA’s National Flood Hazard Layer, and The Homeland of

Infrastructure Foundation-Level Data (HIFLD) database. These sources help me determine proximity to the nearest body of water, floodplain, and park and school, respectively. I also use US Census data to measure neighborhood quality. The resulting distribution of data for all homes in my sample, as well as for only the homes which sold multiple times, is displayed in Table 11. While property fixed effect hedonic models and repeat sales models are susceptible to critique for only utilizing data from homes selling more than once, Table 11 indicates that these differences are minor in my dataset, suggesting that the repeat sales don’t differ considerably from non-repeat sales and are not lemons or “starter homes” (Clapp et al. 1991; Clapp and Giacotto 1992).

Table 11: Property Buyout Descriptive Statistics

All Sales Repeat Sales

Variable Mean Std Dev Mean Std Dev

Sale Price $194,814 $180,222 $199,438 $184,104

Year Built 1984 19.9 1984 19.5 Year Sold 2007 4.68 2007 4.65

SFHA (0/1) 0.08 0.27 0.08 0.27

Distance to Buyout (KM) 3.56 2.79 3.58 2.81

Distance to Lake (KM) 29.8 13.8 29.8 13.8 Distance to River (KM) 7.62 6.01 7.60 5.97

Distance to Coast (KM) 21.2 12.8 21.3 12.7

Distance to CBD (KM) 25.1 10.8 25.2 10.8

Distance to Park (KM) 1.92 1.70 1.92 1.69

Acres 0.30 61.7 0.31 67.2

Bathrooms 2.32 0.76 2.33 0.76

Square Feet (100s) 26.8 10.7 27.1 10.7

Stories 1.38 0.48 1.40 0.48

Pool (0/1) 0.12 0.32 0.13 0.33

Quality (1,2,3,4) 2.36 0.67 2.38 0.67

N = 499,144 transactions N = 420,728 transactions

4.4 Results

The importance of controlling for spatially varying unobservables is demonstrated in

Table 12. Because distance to the nearest buyout is measured continuously, I log the distance so that the estimates are interpreted as elasticities. To ensure consistency in the interpretation of the results across the hedonic and repeat sales models, I have multiplied the estimates of the continuous distance effects in the hedonic regression by negative one

98 so that a positive impact of proximity is indicated by a positive estimate.44 When no spatial fixed effects are included in the model, a decrease in the distance to a buyout appears to decrease the value of a home by more than four percent. This is not surprising given that buyouts often follow flooding events and the effect of being close to a buyout may be conflated with proximity to damages from flooding when failing to control for spatially varying unobservables. While models (1), (2), and (3) include annual fixed effects for both areas in floodplains and areas not in floodplains to allow for the capitalization of flood risk to dissipate over time as homeowners “forget the flood”

(Atreya et al. 2013; Bin and Landry 2013), flooding in Houston is not confined to the

100-year floodplains. In fact, up to three quarters of the homes flooded by Harvey were located outside of the 100-year floodplain.45 Therefore, without controlling for neighborhood level unobservables with spatial fixed effects, it is challenging to disentangle proximity to flood damages and proximity to buyouts.

44 A positive impact of proximity on housing values will typically yield a negative estimate in a hedonic regression as greater distances will be associated with lesser prices. 45 Hunn, David, Dempsey, Matt, and Mihir Zaveri. 2018. “Harvey’s floods: Most homes damaged by Harvey were outside flood plain, data show.” Houston Chronicle : https://www.houstonchronicle.com/news/article/In-Harvey-s-deluge-most-damaged-homes- were-12794820.php 99

Table 12: Hedonic Regression of the Impact of Buyout Proximity on Housing Values with Fixed Effect Robustness

Variables (1) (2) (3) (4) Distance to -0.042*** 0.009** 0.029*** 0.014*** Nearest Buyout (0.001) (0.003) (0.002) (0.005)

Age -0.040*** -0.080*** -0.081*** -0.067***

(0.001) (0.003) (0.002) (0.003)

Fixed Effects SFHA by Year Tract (638) and Property (96,632) Property (95,905) (34) SFHA by Year and SFHA by and Tract by Year (34) Year (34) (8,718)

Observations 486,327 486,321 214,883 213,302

R-squared 0.6707 0.766 0.893 0.913 Notes: ***, **, * indicates significance at the 1%, 5% and 10% level, respectively. Reported coefficients represent elasticities for continuous variables and approximate semi-elasticities for discrete variables. Models (1) and (2) include property specific characteristics listed in Table 1. All models also include quarterly fixed effects. Standard errors are clustered at the time-invariant fixed effect level.

The effect of enhanced proximity to a buyout becomes positive when neighborhood unobservables are absorbed with Census Tract fixed effects in model (2).

While both models (1) and (2) include the covariates listed in the Table 11, all time invariant attributes drop out of the model with the inclusion of property specific fixed effects in model (3). This greatly reduces the scope for omitted variable bias and results in a more precise estimate of the impact of proximity to a buyout. Model (4) introduces

Tract by sale year fixed effects in addition to the property level fixed effects to allow for annual housing market trends to vary across space. As noted by Muehlenbachs et al. in their analysis of the impact of shale gas development on property values, while Census

Tract by year fixed effects are generally preferable to county by year fixed effects, because of the sheer explanatory power of census tract by year fixed effects,

100 identification of other parameters becomes considerably more challenging (2015). I follow their example and use property level and county by year fixed effects for my primary model while also noting the qualitative similarities produced by the property level fixed effect models with county by year and Census Tract by year fixed effects in columns (3) and (4).

These qualitative similarities are also evident when considering heterogeneous treatment effects across neighborhoods of varying quality. Panel A of Table 13 displays results from a model with property level and county by year fixed effects while Panel B displays results from a model with property level and Tract by year fixed effects. Despite differences in magnitude and significance, seven of the eight models demonstrate that proximity to a buyout is more beneficial to homeowners in higher quality neighborhoods than in lower quality neighborhoods. Models (1) through (4) each utilize a different measure of neighborhood quality. Model (1) indicates that proximity to a buyout has a negative effect of 1.5 percent on property values in Census Tracts where the average housing price is equal to the sample average Census Tract mean housing price of

$208,000, but that this effect becomes positive by 1.7 percent for every $100,000 the average housing price in a Census Tract exceeds $208,000. Similarly, proximity to a buyout has a positive effect on housing prices in Tracts with average rates of unemployment, but this effect is diminished in Tracts with greater rates of unemployment. Model (3) indicates that proximity to a buyout is associated with a positive effect on housing values in Tracts where the median income is approximately

$60,000 and this effect is only amplified as the median income increases. While Model

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(4) suggests that a greater incidence of poverty is associated with a more beneficial impact of buyout proximity in Panel A, the results in Panel B are more in accordance with the pattern revealed by the other measures of neighborhood quality.

Table 13: Hedonic Regression of the Impact of Buyout Proximity on Housing Values with Neighborhood Quality Heterogeneity (Continuous)

Variables (1) (2) (3) (4) Panel A. SFHA-year fixed effects Distance to -0.015*** 0.043*** 0.017*** 0.015*** Buyout (0.003) (0.005) (0.005) (0.003)

Distance to 0.017*** -0.004*** 0.002*** 0.002*** Buyout x Neighborhood (0.001) (0.001) (0.001) (0.000) Quality

Observations 214,883 214,772 214,865 214,772 Measure of Average Housing Unemployment Median Income Percent of Neighborhood Price in $100,000 Percent in $10,000 Households in Quality (Average (2.08) (3.26) (5.92) Poverty (7.33) Value)

Panel B. Census tract-year fixed effects Distance to -0.011 0.019 -0.018 0.019*** Buyout (0.010) (0.013) (0.018) (0.007)

Distance to 0.011** -0.002 0.005* -0.001 Buyout x Neighborhood (0.005) (0.004) (0.003) (0.001) Quality

Observations 212,963 212,873 212,963 212,873 Measure of Average Housing Unemployment Median Income Percent of Neighborhood Price in $100,000 Percent in $10,000 Households in Quality (Average (2.08) (3.26) (5.92) Poverty (7.33) Value)

Notes: ***, **, * indicates significance at the 1%, 5% and 10% level, respectively. Reported coefficients represent elasticities for continuous variables and approximate semi-elasticities for discrete variables. All models also include quarterly fixed effects. Standard errors are clustered at the property level.

These patterns are more evident when consolidating and discretizing the measure of neighborhood quality as is done in Figure 13. Of the four models in Table 14, three 102 affirm the pattern of the additional benefit of buyout proximity in higher quality neighborhoods. Taken together, the results in Table 13 and Table 14 indicate that the positive average impact of buyout proximity is being driven by the effect in the highest quality neighborhoods.

Table 14: Hedonic Regression of the Impact of Buyout Proximity on Housing Values with Neighborhood Quality Heterogeneity (Discrete)

Variables (1) (2) Panel A. SFHA-year fixed effects Distance to Buyout in Lower 0.026*** 0.029*** Quality Neighborhoods (0.002) (0.002)

Distance to Buyout in Higher 0.066*** -0.028*** Quality Neighborhoods (0.001) (0.003)

Observations 214,883 214,883

Threshold for Defining High Top Quartile Top Half Quality Neighborhood

Panel B. Census tract-year fixed effects Distance to Buyout in Lower 0.012** 0.001 Quality Neighborhoods (0.004) (0.001)

Distance to Buyout in Higher 0.029* 0.023*** Quality Neighborhoods (0.016) (0.008)

Observations 213,302 213,302

Threshold for Defining High Top Quartile Top Half Quality Neighborhood

An alternative estimation strategy to the hedonic regression is the repeat sales model. Table 15 demonstrates the robustness of the primary set of results from Panel A of 103

Table 14 to the adoption of this estimation technique. The repeat sales model yields estimates similar in magnitude and precision to the hedonic regression. Supporting the pattern indicated in Table 14, the communities benefitting the most from property buyouts are within the top quartile of the distributions for unemployment, poverty, and median household income in Harris County.

Table 15: Repeat Sales Model Estimation of the Impact of Buyout Proximity on Housing Values with Neighborhood Quality Heterogeneity

Variables (1) (2) Distance to 0.025*** 0.028*** Buyout (0.002) (0.002)

Distance to 0.038*** -0.003 Buyout x Neighborhood (0.006) (0.003) Quality

Observations 135,222 135,222 Threshold for Top Quartile Top Half Defining High Quality Neighborhood

Notes: ***, **, * indicates significance at the 1%, 5% and 10% level, respectively. Reported coefficients represent elasticities for continuous variables and approximate semi- elasticities for discrete variables. Standard errors are clustered at the property level.

In addition to considering heterogeneous effects by neighborhood quality, I also account for how property buyouts may capitalize differently across space. Columns (1) through (3) of Table 16 show how my binary indicator of buyout proximity is robust to variation in the distance to the nearest property acquired by the Harris County Flood

Control District. In all models, the continuous measure of the change in the distance to the nearest buyout is replaced with a binary indicator for whether a buyout has occurred

104 within 0.05 miles from the home (model (1)), within 0.1 miles from the home (model

(2)), or within 0.2 miles from the home (model (3)), between sales of the home. As I am interested in both the potential negative effect of blight and the potential positive effect of improved access to open space or nature, distances were chosen in accordance with those used to identify the capitalization of neighboring foreclosures and urban stream restoration projects (Campbell et al. 2011; Jarrad et al. 2018). While the effects are less precisely estimated when using a binary measure of distance than a continuous measure, the results indicate the same general pattern found in Table 14 and Table 15; floodplain buyouts have positive impacts on the value of neighboring properties in higher quality neighborhoods and potentially negative impacts in lower quality neighborhoods.

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Table 16: Hedonic Regression of the Impact of Buyout Proximity on Housing Values with Distance Heterogeneity

Variables (1) (2) (3) Buyout Within -0.045 0.05 Miles (0.026)

Buyout x Top 0.130** Quartile (0.063)

Buyout Within -0.032* 0.1 Miles (0.018)

Buyout x Top 0.183 Quartile (0.112)

Buyout Within -0.010 0.2 Miles (0.012)

Buyout x Top 0.168*** Quartile (0.050)

Observations 214,885 214,885 214,885

Notes: ***, **, * indicates significance at the 1%, 5% and 10% level, respectively. Reported coefficients represent elasticities for continuous variables and approximate semi-elasticities for discrete variables. Standard errors are clustered at the property level.

4.5 Discussion and Conclusion

This analysis represents the first investigation of neighborhood externalities from floodplain property buyouts to use data from individually acquired properties. This novel dataset allows me to both avoid conflating the value of proximity to a park with proximity to a buyout and to exploit temporal variation as well as cross-sectional variation to identify the treatment effect, allowing for greater control for omitted variables. Furthermore, by accounting for the heterogeneity in neighborhood quality, I find that regardless of the level of control for unobservable variation, the definition of

106 proximity, or the categorization of neighborhood quality, more valuable neighborhoods tend to benefit from floodplain property acquisition while homes in less valuable neighborhoods tend to be harmed by a buyout. Though I cannot speak to the exact mechanism behind this effect, it is in accordance with other work finding an association of vacant lots with crime, blight, and neglect (Accordino and Johnson 2000; Bowman and

Pagano 2004; Alexander and Powell 2011; Garvin et al. 2012).

The implications of these findings are significant. While my hedonic regression with property, annual, and quarterly fixed effects yields an implicit price of $365 for a

200 meter reduction in the distance to the nearest buyout, strikingly similar to the $320 premium for a similar reduction in distance to the Meramec Greenway in St. Louis, this average effect masks important heterogeneity. In terms of policy efficiency, as neighboring property values increase following a nearby buyout in wealthier neighborhoods, more generous offers can be made to the owners of these homes as the net costs of the buyout will be moderated by the benefit they confer to their neighbors.

Conversely, my results suggest that buyouts in neighborhoods with lower value homes may be less beneficial than previously thought. Absent greater efforts to maintain or improve the vacant land, municipalities may be harming the neighbors of acquired properties by introducing a greater degree of blight into the local community. In terms of equity, these results suggest that policymakers face a paradox. While more buyouts in low quality neighborhoods may exacerbate poor economic conditions, allocating fewer buyouts to lower quality neighborhoods will lead to a larger share of the homes that are

“hopelessly deep in a floodplain” being located in lower quality neighborhoods, meaning

107 that the burden of repeat flooding will be shouldered even more disproportionately by the socioeconomically disadvantaged.

Together, these findings suggest that the cost-benefit analysis of vulnerable property acquisitions would be more accurate if externalities from buyouts were calculated as benefits in higher quality neighborhoods and as costs in lower quality neighborhoods. While this makes the possibility of more generous offers less likely in lower quality neighborhoods, greater participation can still be encouraged through more targeted offers. It is possible that economies of scale exist in lower quality neighborhoods and that externalities may still be positive if buyouts are clustered and the quality of the acquired property is improved, permitting more generous offers to be made for high density acquisition efforts. The role of social capital in buyout program participation is also worth investigating. Recent work suggests that a disproportionate number of participants are non-Hispanic homeowners living in neighborhoods becoming majority-

Hispanic in occupancy (Loughran et al. 2019). If these homeowners are more willing to leave their former neighborhood because of a diminished stock of social capital, then perhaps buyout programs can become more efficient by considering the role of social connections. Possible solutions could either try to chip away at this inertia in vulnerable neighborhoods by offering extra incentives for early adopters, or could attempt to maintain social capital by enhancing group relocation opportunities. Future research concerning the roles of social capital and economies of scale in buyout program outcomes has the potential to greatly mitigate exposure to flood damages.

108

Finally, it is worth remembering that the acquisition of vulnerable properties does not occur in a bubble; it is necessarily in relation to the state of NFIP, the existence of protective capital, and the possibility of sea level rise. As flood insurance premiums rise with updated flood risk maps and changes to NFIP, buyouts may become less necessary and less prevalent in non-coastal areas. The net costs of future damages to these homes will be diminished by the higher premiums collected thus making buyouts relatively more costly and thereby less likely. However, this may imply an even greater need to address socioeconomic vulnerability as those stuck in these neighborhoods will be less able to afford their flood insurance premiums and unable to recover value through the sale of their home on the private market. Ultimately, while this concern over acquisition externalities and the consequences they have for equity is highly relevant to urban settings, it is irrelevant in the context of sea level rise or floodplain reconnection. In both such scenarios, property buyouts cannot be selective, leaving pockets of parks or vacant lots. When confronted with floodplain reconnection and sea level rise, entire communities must be relocated, thereby leaving few to zero neighbors for which the buyouts could capitalize, positively or negatively.

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Chapter 5: Conclusion

Flood risk mitigation has been a national priority for over 100 years and is growing in importance as behavioral, technological, and climatological changes increase our collective exposure to damages. With more data available now than ever before, there is a golden opportunity to use evidence based practices to improve our policy response to vulnerability. However, it remains an open question whether we are learning from previous policy shortcomings or whether we are doomed to repeat the failures of prior approaches, indefinitely.

In this dissertation, I rely on the theory of spatial equilibrium to inform causal inference identification strategies and provide the first evaluations of three separate approaches to mitigating flood risk. In addition to providing answers to questions of critical policy importance, I uncover a pattern of counterproductive outcomes resulting from the flood risk mitigation policy portfolio of the United States. Before concluding, I summarize the discoveries of these unintended consequences as well as the primary contributions of my dissertation. Finally, I consider potential extensions to the work herein.

5.1 Unintended Consequences

While the primary findings in this dissertation represent policy outcomes which were unintended, they should generally not have been unforeseen. Ultimately, while the 110 implementation of the Biggert-Waters legislation was not as counterproductive as “The

Levee Effect” and didn’t impose a catch-22 like the Harris County Flood Control District buyout program, it largely sewed the seeds of its own demise through a predictable capitalization of higher flood insurance premiums. While Biggert-Waters was meant to help the National Flood Insurance Program achieve fiscal solvency through higher premiums, it was repealed in less than two years’ time due to anecdotal evidence suggesting that there were significant an unanticipated impacts to housing markets. I provide the first causal evidence suggesting that this phenomenon was widespread and that it largely erased the capitalized value of Pre-FIRM flood insurance premium discounts in housing values.

On the other hand, “The Levee Effect” was more explicitly self-defeating. The

Central and Southern Florida Project levees were built to decrease expected damages from flooding and protect existing development. However, by essentially relaxing a physical constraint on development, the construction of levees increased residential development by more than 50 percent in the years following their construction. In some cases where the levees only provided a 90 percent level of protection from flooding in a given year, the increase in exposure would have outpaced the decrease in vulnerability, thereby increasing expected damages.

In this dissertation, I also reveal a social equity paradox regarding vulnerable property acquisition programs. Property buyouts are generally considered a more equitable solution to addressing flood insurance insolvency than raising insurance premiums to actuarially fair rates. However, while property acquisitions are preferable

111 for those receiving the buyout, they impose negative externalities on the surrounding neighbors in lower quality neighborhoods. Therefore, without a conscious effort to improve the condition of the acquired land, property buyouts appear to be less equitable than previously thought.

5.2 Contributions

The primary contribution of this dissertation is in the answers it provides to open policy debates. Did the Biggert Waters legislation cause a decrease in housing values for recipients of Pre-FIRM flood insurance premium discounts? Do levees induce accelerated development, sometimes to a greater degree than the reduction in flood risk they provide?

Do floodplain property buyouts impose externalities on neighboring properties? The findings in this thesis answer each of these question affirmatively, providing input and yielding warnings for future policy designs.

This dissertation also lends an economic perspective to problems studied more attentively in other disciplines in the social sciences. “The Levee Effect” has rarely been mentioned outside of the geography literature though it represents a textbook case of moral hazard. Similarly, sociologists have taken the mantle of evaluating floodplain buyouts despite models of land use classically falling in the domain of applied economists. Our understanding of each of these issues is enriched by interdisciplinary approaches and this dissertation provides an overdue comment from the field of economics.

Lastly, this dissertation builds on the model of incomplete information in hedonic regressions. This work suggests that even in settings with entirely asymmetrically

112 informed buyers and sellers, the amenity or disammenity in consideration may be fully capitalized in the presence of multidimensional information. Similar to policy prescriptions from “the theory of the second best” (Lipsey and Lancaster 1956), if a policy goal is for housing markets to internalize risk or another disammenity, it may be equally as effective to misinform market participants along a dimension of their information set as it would be to perfectly inform them. Furthermore, given the popularity of using hedonic regressions to value nonmarket goods, and given the likelihood of imperfectly informed market participants, researchers may be tempted to attribute lower-than-anticipated capitalized values to information asymmetries. However, as fully capitalized values are also possible in such settings, scholars should carefully consider how other dimensions of information may affect the equilibrium price schedule before claiming that the respective good is undercapitalized.

5.3 Future Work

There is a greater need than ever for ex-post policy analysis and the complexity of the flood risk management policy portfolio in the US provides abundant opportunities for further evaluation.46 Each policy considered in this dissertation could be further explored and greater meaningful insights could be gained. Since the passage of the Homeowners

Flood Insurance Affordability Act of 2014, Pre-FIRM flood insurance premiums have seen a more gradual rate escalation. As this rate varies annually, current policy could be further improved by estimating the capitalization of annual rate changes. Similarly, a

46 Taken from comments by Ruben Lubowski, Chief Natural Resource Economist of the Environmental Defense Fund, during an organized symposium at the 2018 Agricultural & Applied Economic Association annual meeting. 113 thorough and complete investigation of “The Levee Effect” would require coupling the estimates from chapter 3 with a hydrological model of flood risk for the Central and

Southern Florida Project levees. Finally, a possible extension to the body of knowledge pertaining to the optimal bid structure for property buyouts could address the spatial contagion of participation.

Still, an integrated model of the three approaches (insurance, protection, and retreat) would provide the most interesting and informative extension of my work. As property buyouts are most often offered based on a strict cost-benefit analysis and levees are built, at least implicitly, according to cost-benefit principles, common inputs into these calculations may make prevention and retreat alternatives more or less likely.

Specifically, greater housing values enter the cost-benefit calculation for levee construction/improvement decisions strictly as benefits while they present greater costs for property buyouts. As eliminating Pre-FIRM subsidies decreases housing values, it should theoretically make levee construction/improvements less likely and make property buyouts more likely. A robust and integrative model testing this prediction would be of value to policymakers at regional and national levels.

114

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