Does federal disaster assistance crowd out flood insurance?

Author’s Accepted Manuscript Does Federal Disaster Assistance Crowd Out Flood Insurance? Carolyn Kousky, Erwann O. Michel-Kerjan, Paul A. Raschky www.elsevier.com/locate/jeem

PII: DOI: Reference:

S0095-0696(17)30347-9 http://dx.doi.org/10.1016/j.jeem.2017.05.010 YJEEM2035

To appear in: Journal of Environmental Economics and Management Received date: 29 March 2016 Revised date: 26 May 2017 Accepted date: 26 May 2017 Cite this article as: Carolyn Kousky, Erwann O. Michel-Kerjan and Paul A. Raschky, Does Federal Disaster Assistance Crowd Out Flood Insurance?, Journal of Environmental Economics and Management, http://dx.doi.org/10.1016/j.jeem.2017.05.010 This is a PDF file of an unedited manuscript that has been accepted for publication. As a service to our customers we are providing this early version of the manuscript. The manuscript will undergo copyediting, typesetting, and review of the resulting galley proof before it is published in its final citable form. Please note that during the production process errors may be discovered which could affect the content, and all legal disclaimers that apply to the journal pertain.

Does Federal Disaster Assistance Crowd Out Flood Insurance? Carolyn Kouskya, Erwann O. Michel-Kerjana, Paul A. Raschkyb a

The Wharton School, University of Pennsylvania

b

Department of Economics, Monash University

[email protected] [email protected] [email protected]

Abstract We empirically analyze whether federal disaster aid crowds out household purchase of disaster insurance. We combine data on annual household flood insurance purchases for the United States over the period 2000-2011 with data from the two main U.S. post-disaster federal aid programs (FEMA’s Individual Assistance grants and SBA’s low interest disaster loans). Estimating both fixed-effects and instrumental variable models to account for the endogeneity of disaster assistance grants, we find that receiving individual assistance grants decreases the average quantity of insurance purchased the following year by between $4,000 and $5,000. The reduction we find is roughly 3% of the mean insurance coverage in the sample but larger than the average flood-related IA grant in our sample, which is $2,984. IA is currently limited and larger grants could have different impacts. The crowding out is on the intensive margin; we find no impact on take-up rates, likely because there is a requirement that recipients of disaster aid purchase an insurance policy. We do not know how take-up rates might change without such a requirement. Low interest post-disaster government loans have no systematic effect on insurance purchases.

Keywords: Natural Disasters and Extreme Events, Flood Insurance, Disaster Relief

JEL Classification: Q54, Q58, G22, H84

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1. Introduction Of all natural disasters, floods have been the most damaging and have affected more people; this is true worldwide and in the United States. Between 1954 and 2014, over 80% of presidential disaster declarations were for flood and storm events (Lindsay and McCarthy 2015). Such declarations have been increasing, from 15 to 20 per year in the 1950s to roughly 60 per year in the 2000s, reaching a peak of 99 in 2011. Losses from flooding have also been growing over time, largely due to growth of populations and assets in risky locations. Climate is change is projected to further increase flood losses (e.g., Kollat et al. 2012; Hallegate et al. 2013; Mallakpour and Villarini 2015). If disaster losses escalate, so may federal outlays in response (Michel-Kerjan 2013). Although spending on these declarations is quite spiky, with outlier years such as 2005 (Hurricanes Katrina, Rita and Wilma) and 2012 (Hurricane Sandy) dominating any analysis (OMB 2011; 2015), federal aid is now routinely offered following most disasters. Since early theoretical work on the Samaritan’s dilemma by Buchanan (1975), scholars have been interested in the potential for underinvestment in financial protection by economic agents in response to government assistance (e.g., Coate 1995; Kim and Schlesinger 2005). In the context of financial protection against natural disasters, theoretical models predict, first, that if households or managers of a firm expect government relief following a disaster, they will invest less in reducing their risk ex ante. Second, post-disaster government relief may crowd out insurance purchases if individuals treat federal aid as a (partial) substitute for insurance and fail to insure or underinsure (Lewis and Nickerson 1989; Kaplow 1991; Kelly and Kleffner 2003).1 Related concepts using a variety of terms have been discussed in the literature, so a brief comment on terminology is warranted. The term “crowding out” is often used to refer to situations in which government spending reduces private investment or spending. Similarly, in this article, we use the term “crowding out” to

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Note that we are focused on financial assistance for repairing or replacing damaged property, not emergency relief for health and safety in the immediate occurrence and aftermath of an event.

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refer to a reduction in insurance purchases as a response to the receipt of federal disaster aid. The term “charity hazard,” also used in the literature, would refer more generally to the impact of charitable donations (whether public or private) on the demand for disaster insurance (Browne and Hoyt 2000; Raschky and WeckHannemann 2007). Testing theoretical propositions of crowding out has been the subject of a small, but growing body of work. In the context of natural disasters, from floods to wildfires, tests have been limited for the most part, however, to laboratory experiments (e.g., Brunette et al. 2013; Prante et al. 2011) and surveys (Kunreuther et al. 1978; van Asseldonk, Meuwissen, and Huirne 2002; Botzen and van den Bergh 2012a; Petrolia, Landry, and Coble 2013; Raschky et al. 2013).2 Actual disaster aid often differs from the assumptions made in these papers and, in the U.S. at least, is tied to requirements, some related to insurance (discussed in detail below). Furthermore, while surveys provide important insight on how variables that are unobservable in actual markets impact decision-making, survey responses do not always capture actual decision-making. Thus, we do not yet have a good understanding of the influence of post-disaster government aid on households’ financial protection decisions. The objective of this paper is to provide the first causal estimates of the crowding-out effect of governmental, post-disaster relief on households’ demand for insurance, using flood insurance as our context.3 In particular, we examine the influence of disaster grants from FEMA’s Individual Assistance (IA) program (details below) provided directly to affected households for uninsured property losses related specifically to flood events.4

We are also able to control for low interest disaster loans from the Small Business

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Similar ideas have been empirically tested or theoretically explored in diverse contexts apart from disasters, such as long-term care insurance (Brown and Finkelstein 2008), intrahousehold transfers (e.g., Alger and Weibuill 2010), savings and retirement (e.g., Homburg 2000; Lagerlof 2004; Crossley and Jametti 2013), health insurance (e.g., Herring 2005), foreign aid (Raschky and Schwindt 2016, Svensson 2000; Torsvik 2005), and federal terrorism insurance (Brown et al. 2004). These papers all find some degree of crowding out of a private activity when it is publicly provided. 3 As we explain in more detail below, residential flood insurance is available almost exclusively through the federally run National Flood Insurance Program (NFIP), which was established in 1968 as a result of a lack of availability of flood insurance in the private market; this federal program covers more than $1.2 trillion of assets today. 4

To test predictions regarding ex ante expectations of disaster aid, individuals’ expectations of such aid must be observed on a large scale—something very difficult to do in practice. We can, however, observe how insurance purchases change after the receipt of aid.

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Administration (SBA) —another important source of federal aid to households. Our analysis answers the following questions: Does the receipt of government disaster aid by households impact their demand for flood insurance? If it does, what is the direction and magnitude of the effect? Is it on the intensive or extensive margin? What is the overall effect of that governmental intervention on flood insurance purchased? Do federal grants and federal loans have different impacts on householders’ insurance behavior? Several studies have examined the relationship between disaster aid and insurance.5 Browne and Hoyt (2000) use data aggregated to a state level and estimate a fixed-effects (FE) model of the determinants of the demand for flood insurance. Contrary to theoretical predictions, they find a positive correlation between flood insurance purchases and the amount of disaster aid received by a state from FEMA.6 More recently, Petrolia et al. (2013) administered a survey to roughly 1,000 residents in Gulf Coast states and found a positive relationship between expectation of future aid and insurance: those who thought disaster aid was at least somewhat likely were more likely to have flood insurance. Botzen et al (2016) show that the expectation of disaster relief depends on several factors, including political affiliation. They found that 50% more Democrats than Republicans in New York City in the aftermath of Hurricane Sandy expected to receive federal disaster relief after a major flood. Kousky (2016a) examines purchases of flood insurance after hurricane events for counties on the Atlantic and Gulf coasts and finds that while take-up rates increase after hurricanes and disaster declarations, most of the bump can be explained by the requirement that recipients of FEMA disaster aid grants purchase flood insurance. Although not related to flood insurance, a recent working paper finds a crowding-out effect of federal disaster assistance on crop insurance demand of U.S. farmers (Deryugina and Kirwan 2015). For our analysis, we compile a novel dataset from various sources. First, we collected yearly information on flood insurance policies and claims at the ZIP code level over the period 2000 to 2011 from the federally-run National Flood Insurance Program (NFIP), by far the largest provider of residential flood insurance in the 5

Several studies have examined the demand for flood insurance in the United States but have not addressed the influence of disaster aid on demand (Landry and Jahan-Parvar 2011; Kousky 2011; Gallagher 2013; Atreya, Ferreira and Michel-Kerjan, 2015). 6 This might be explained by the fact that their aid variable is correlated with objective flood risk. Other factors might be the inability to address problems of endogeneity, legal requirements to purchase insurance after receiving federal relief money, possible measurement error in their aid variable (their analysis included all types of aid for all disaster types, and that is given to a state), and that they use a high level of aggregation.

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United States. We combine this panel dataset with information on Individual Assistance (IA) grant payments from the Federal Emergency Management Agency (FEMA) (if any) due to flood-related events in a given year and with data on low-interest post disaster loans from the Small Business Administration (SBA) (if any). We also obtained socio-economic controls from the U.S. Census and Bureau of Economic Analysis.

As an

extension, we obtained data on the amount of IA grants and SBA loans given for the period 2004-2011. This lets us examine the impact of the average disaster grant/loan, total dollars and numbers of grants/loans, as well as how the approval rate for the FEMA grants affects household demand for insurance, for this more limited time period. Our empirical analysis also needs to account for a potential two-way causality problem between disaster aid and insurance: a higher penetration of flood insurance could reduce the amount of aid needed after an event.7 In addition, there may be omitted variables which are not captured in spatial and time fixed effects, and are likely to be correlated with both aid received and insurance purchases, such as expectations about aid, risk perceptions concerning flooding, or demographic variables for which we do not have data. For that reason, we perform both fixed effects (FE) and instrumental variables (IV) analyses. For the instrumental variables approach, we exploit an exogenous source of variation in governmental aid that was initially highlighted by Garrett and Sobel (2003): provision of federal disaster aid is partially politically motivated, which we detail further in the methodology section below. Their study reveals that more federal aid is spent in election years and in states that are considered more important for the outcome of the election (“swing states”). Based on those insights we implement an instrumental variables (IV) approach inspired by Nunn and Qian (2014). Our IV is an interaction term between a dummy variable that indicates whether the county is a “swing county” and the timing of Presidential elections. Intuitively, our identification strategy implements a difference-in-differences approach in the first stage estimation. We compare the effect of

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Indeed, a RAND report prepared for the Federal Emergency Management Agency (FEMA) after Hurricane Katrina, examines a question that is the inverse of our own; that is, does insurance penetration influence amounts of aid (Dixon et al. 2006)? Their data is aggregated at the state level and they do not address endogeneity.

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Presidential election years on the likelihood of receiving any level of Individual Assistance from FEMA between counties of relatively high political importance (and thereby a higher probability of receiving discretionary IA) compared to counties of relatively lower political importance (and a lower probability of receiving discretionary IA). The identifying assumption is that, after controlling for time-invariant factors through a vector of fixed effects and any county-wide shocks through year fixed effects, the political importance of a county during election years has no effect on demand for flood insurance other than through governmental relief. To our knowledge, we are the first to apply this IV approach to analyze the effect of government intervention in the market of disaster insurance. We perform our analysis for ZIP codes in the United States. We find that that when a ZIP code receives any IA for flood-related events the previous year, the average amount of insurance coverage in that ZIP code decreased by between $4,000 and $5,000 (IV models). This corresponds to approximately 3% of the mean policy-level insurance coverage in the sample. Yet, the decrease we find is larger than the average size of flood-related IA grants in our sample of $2,984. In alternative specifications, we find that a $1,000 increase in the average IA grant decreases insurance coverage by roughly $1,600 per policy in the IV model (and under $100 in the FE model). Total IA spending or total number of approved grants have negligible impacts on demand. We find that a one standard deviation in the approval rate of IA grants (an approximately 20% increase) decreases average coverage by insured household by around $1,400 in the IV model. SBA postdisaster loans do not appear to have a crowding out effect, maybe because they must be repaid. The total number of SBA loans does seem to increase coverage levels slightly in the IV model. Important for policy considerations, we find no impact on take-up rates after we eliminate from the data the policies that were required as a criterion for receiving federal assistance. Our results therefore suggest that this requirement seems to be working as intended, preventing a drop in take-up rates after the receipt of disaster aid. We cannot speculate on how take-up rates might be impacted absent a mandate to insure as a condition of getting federal aid. Our findings are robust to a range of alternative specifications and pass a falsification test.

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The remainder of the article proceeds as follows. Section 2 provides background on federal disaster aid and on the National Flood Insurance Program in the United States. Section 3 describes our data. Section 4 outlines our empirical strategy. Section 5 discusses our baseline findings, several robustness checks and falsification tests, as well as our extension for the 2004-2011 period. Section 6 concludes.

2. Background on Federal Disaster Aid and the National Flood Insurance Program The current framework for federal disaster relief in the United States is provided by the Stafford Disaster Relief and Emergency Assistance Act, passed into law in 1988. When a disaster occurs, if managing and financing the disaster is judged to exceed the affected state’s capacity, the Governor of the affected state may request a declaration from the President. The President may authorize one of two programs: Public Assistance—aid to local governments—and/or Individual Assistance to help households. The Government Accountability Office (GAO) (2012) has found that for declarations between 2004 and 2011, only 45% authorized Individual Assistance, but 94% authorized Public Assistance.

Once authorized, the Federal

Emergency Management Agency (FEMA) can activate these different aid programs, spending money from the Disaster Relief Fund. The U.S. Congress appropriates funds into this account every year, but for truly devastating disasters further appropriations from Congress are needed, and often granted. Our baseline analysis examines the impact of a ZIP code receiving any IA in the previous year. As noted in the introduction, the number of U.S. presidential disaster declarations has increased dramatically, over time. There was a total of 191 declarations during the decade 1961–1970 to 597 for the decade 2001–2010. Evidence shows that many of the years with the highest number of declarations are presidential election years, and several studies confirm that aid is politically motivated to some extent (Garrett and Sobel 2003; Sylves and Búzás 2007). Among all disaster declarations, roughly two-thirds are related to

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flood events. Over the period January 1960 to December 2011, there were 1,955 disaster declarations, with 1,258 related to flooding (roughly two thirds).8 The majority of disaster aid in the United States is given through the Public Assistance program to state and local governments to pay for debris removal, emergency response, and restoration of damaged infrastructure and public buildings (Dixon et al. 2006). The focus of this paper is not on Public Assistance, but rather, on grants to households who have experienced a disaster. While a recent working paper finds evidence that nondisaster aid programs, such as food stamps and unemployment insurance, can be important safety nets after a disaster (Deryugina 2011), we restrict our analysis to direct grants that are given solely as a result of the flood.9 FEMA’s IA program funds several types of assistance.10 The one relevant for our analysis is the Individual and Households Program which provides grants for both Housing Assistance and Other Needs Assistance. The former covers temporary housing or home repairs, and the latter covers damage to personal property, medical or funeral expenses from a disaster, and other costs not related to housing. It is the Housing Assistance grants that are of relevance to this paper, since they fund repairing damaged property, as insurance

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Data on disaster declarations is publicly available on FEMA’s website. Note that it is not just the number of declarations that has increased, but also the proportion of total economic losses covered by federal aid to individuals, businesses, and state and local governments. For instance, in the wake of Hurricane Diane and the associated flooding in 1955, federal relief spending covered only 6.2 percent of total damages (Moss 2010). In contrast, federal relief for the 2005 hurricane season and other disasters occurring through 2008 was roughly 70 percent of total estimated damages (Cummins, Suher, and Zanjani 2010). Most of these funds, however, do not go to individuals to compensate for property damage, but to local governments for reconstruction and mitigation. 9

Note that we do not examine the impact of being able to deduct disaster damage from one’s taxes, and we do not examine the Federal Housing Administration’s section 203(h) program, which insures mortgages made to disaster victims. The former, we believe, would have small incentive effects, and the latter is protection for lenders against the risk of default. In addition, after certain major disaster events, Congress has appropriated funds for stricken communities through the US Department of Housing and Urban Development’s Community Development Block Grant - Disaster Relief (CDBG-DR) Program; this, for instance, funded The Road Home Program in Louisiana. Over our time period, the only substantial CDBG appropriations for flood events were for the 2005 hurricanes and the 2008 hurricanes (see: https://www.hudexchange.info/programs/cdbg-dr/cdbg-dr-grantee-contact-information/#alldisasters). Louisiana and Mississippi did choose to use these dollars as grants for households; this is another way Katrina is an outlier. We test for this in Table A.4 of the appendix; excluding the year 2005 from our analysis does not alter the results. Most of the time, however, CDBG-DR funds are not used to reimburse homeowners for damages and are thus not a substitute for insurance. Getting any CDBG-DR funds is also high uncertain – they may not be funded post-disaster, as it takes special appropriations from Congress— and even if they are, the local government may not choose to use them for households. Because of this, we do not believe there is reason to suspect CDBG-DR funds would have any crowding out effects on private insurance. 10

For more details, see: https://www.fema.gov/media-library/assets/documents/124228

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does. Those grants do not need to be repaid and are not counted as income on tax returns, but they cannot exceed $31,900 (as of 2012; this amount is indexed to inflation). Of note, however, the average grant for the repair of a damaged home is around $4,000—significantly less than the cap (McCarthy 2010). Our extension for the time period 2004 – 2011 examines the average and total amounts of Housing Assistance a ZIP code receives, as well as the approval rate for these grants. Note, we use the term IA to refer to these grants throughout the paper, but for the specification with dollar values of grants, they are limited to Housing Assistance since these grants fund repair of damaged homes. Aid is available to U.S. citizens, noncitizen nationals, and qualified aliens. Housing assistance is available only for primary residences. Aid is supposed to be a last resort; thus a homeowner must first file an insurance claim (if she or he has insurance), and FEMA will not duplicate these benefits. Aid is intended only to make a home safe and inhabitable, not to bring a home back to predisaster conditions. Individuals in high-risk areas are required to purchase a flood insurance policy to receive aid, a point we return to below. Many of these requirements may limit the extent of any crowding out effect. (See Kousky and Shabman (2012) for an overview of IA grant eligibility requirements). Another limitation is that disaster victims are often first referred to the SBA for a loan. Despite its name, the SBA offers loans not only to small businesses but also to homeowners. Loans are available for up to $200,000 for homeowners to repair or replace their primary residence and for up to $40,000 to repair or replace contents damaged or destroyed in the disaster. For the period we study, the interest rate on SBA loans was not to exceed 4% for applicants unable to obtain credit elsewhere (as determined by the SBA). For those who could obtain credit elsewhere, the interest rate would not exceed 8%.11 Loans are usually 30 years in length. SBA recipients are also required to purchase flood insurance. Flood insurance for homeowners in the United States is generally not available from private sources but has been available through the National Flood Insurance Program (NFIP) since the program’s creation in 1968.

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For disasters after July 2010, these two ceilings were decreased to 2.5 percent and 5 percent, respectively, to reflect lower interest rates.

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The NFIP is designed to be a partnership between the federal government and communities. Communities may voluntarily join the program by agreeing to adopt minimal floodplain management regulations; in exchange, their residents become eligible to purchase flood insurance policies through the NFIP. There are currently over 22,000 communities in the program, covering almost all areas of flood risk in the country. In 2011, the last year of our data, there were over 5.6 million NFIP policies in force nationwide representing $1.278 trillion dollars of coverage and paying over $3.2 billion in premiums. The NFIP provides insurance up to a maximum residential limit of $250,000 for building coverage and $100,000 for contents coverage. Over our study period, the menu of deductibles ranged from $500 to $5,000. Premiums for the NFIP vary according to the flood zones defined by FEMA (Kousky et al. 2016). Premiums within a zone are the same nationwide, but in high risk zones, they also vary by structural characteristics of the house, such as its elevation. By law, FEMA is allowed to raise rates only once a year; over the period we study, rate increases averaged across all zones could not exceed 10 percent. As the zones are national in scope, rates are not adjusted locally in response to extreme events and rates are not adjusted for homeowners based on their loss history (see Michel-Kerjan (2010) and Kousky (2016b) for overviews of the program).

3. Data We compiled the data for this study from multiple sources. We discuss each in turn. First, the data on IA grants is obtained from FEMA’s Open Data initiative on fema.gov.12 We obtained data on all federally declared disasters and whether or not Individual Assistance was authorized for each declaration. This dataset let us identify disasters that were for flood-related events (floods, coastal storms, hurricanes, severe storms, and dam/levee breaks) for the period 2000-2011. This data is used for our base specifications. As shown in Table 1, in our sample, roughly 20% of the ZIP code year observations received some amount of IA.

12

FEMA and the federal government cannot vouch for analyses derived from these data after the data have been retrieved from the Agency's website(s) and/or data.gov.

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We also obtained data on Individual Assistance (Housing Assistance grants, as discussed in the previous section) provided to both single-family homeowners and renters (we combined these) and limited this again to flood-related disasters for the years 2004-2011. This dataset let us determine the average amount of IA grants to a ZIP code, the total given in a year to a ZIP code, and the approval rate of IA grant applications within a ZIP code. Including all ZIP codes in our sample (whether or not they received aid or a loan) and years, the mean of the average IA grant received is $350. As mentioned previously, for many ZIP code–years, no aid payment occurred at all and these zeros pull down the average across all ZIP codes. For those ZIP codes that had at least a positive IA payment, the average IA grant was $2,984. We also obtained data on SBA disaster loans to match the IA data. For the period 2000-2011 we have an indicator of whether the ZIP code received any SBA disaster loans. For the period 2004-2011, we have average and total dollar value of SBA disaster loans in a given ZIP code and year. The SBA data was collected from the National Institute for Computer-Assisted Reporting, which obtained the data from a Freedom of Information Act request.13 This data includes all declared disaster events, not just floods, and includes all recipients, both households and businesses. We use it as an additional control variable. As shown in Table 1, the mean number of ZIP code-years receiving SBA loans is just slightly less than those receiving IA at 18.6%. The average SBA per loan, including the many ZIP codes with no loans at all in a given year, is roughly $530. The average individual loan amount conditional on receiving such a loan, is around $48,500. The average total loan amount in our ZIP code in our sample (again, including those not getting any loans) is $47,100 and the mean of the total number of loans received is 1 (this is low since again, it includes the zeros). Conditional on receiving any SBA loan, the average total loan amount spend in a ZIP code is $671,296 and the average number of loans is 12. For our dependent variable (demand for flood insurance), we obtained data directly from the National Flood Insurance Program on both policies-in-force and claims for every state for the years 2001–2011 (we start our analysis on policies-in-forces in 2001 but we have aid data from 2000 since this variable is lagged). We 13

Available on their website: https://ire.org/nicar/database-library/databases/sba-disaster-loans/

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extract policies and claims for single-family residences for our analyses. This data is at the policy level, however, due to privacy concerns, more detailed location information has been removed and the smallest geographic identifier we can use is the ZIP code. The NFIP policy data contains variables related to the insurance contract, such as the coverage level, premium, and deductible. It also tells us if the policy was required due to receipt of federal disaster aid. The claims dataset includes information on the claim, such as the date of the loss and the amount of the insurance payment. We construct two different dependent variables for our analysis. The first is the average coverage per policy. This variable is the ratio of total building and contents coverage limits for each policy in a ZIP code over the number of policies-in-force in that ZIP code. The second variable is the ratio of policies-in-force in each ZIP code per 100 inhabitants. This is a measure of the take-up rate of NFIP insurance for single-family households in each ZIP code.14 The former has a mean of $151,716 and the latter has a mean of 1.6. Our independent variable for the cost of insurance is calculated as the sum of premiums in the ZIP code divided by the total coverage purchased, minus the deductibles for our sample of single-family houses.15 We include this variable as a control; however, for two reasons we do not interpret the coefficients on this variable as, nor estimate, a price elasticity. First, we observe premiums only for policies that are actually bought and, as such, our premium variable does not truly capture the average price of insurance in the ZIP code. Second, the premium variable is highly correlated with risk. As stated earlier, the premium for NFIP policies is set nationally based on annual average loss calculations for each flood zone. The premium varies only by flood zone and by a limited set of characteristics of the house, such as height of the ground floor above base flood elevation, whether the house has a basement, and when the house was built. Given this, we cannot fully separate risk levels from premiums, and the impact of both is probably conflated in our price coefficients. 14

Note that there is no publicly available database on the number of dwellings in flood-prone areas across the country, let alone how many of those have insurance coverage in place. 15 The cost variable used here is an average rate for $1 of coverage. NFIP premiums, however, are reduced when a higher deductible is chosen. The amount of that deduction is captured in the rate calculated here. In essence, NFIP premiums are the amount of coverage multiplied by the rate and then multiplied by a deductible factor.

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We further obtained a number of additional control variables. Population at the ZIP code level is obtained from GeoLytics, which generates annual estimates at a range of geographic scales for many demographic and socioeconomic variables based on U.S. Census data. Per capita income at the county level is derived from the Bureau of Economic Analysis Regional Economic Accounts (https://www.bea.gov/regional/). Mean per capita income is $34,052. Educational attainment, measured as the percent of adults in the county with a Bachelor's degree or higher is taken from the U.S. Census. Because this data is available only for the years 2000 and 2010, we have linearly interpolated it for the years in between Census estimates. The average percentage of adults in a ZIP code with a Bachelor’s degree or higher is just under 24% in the sample. Our empirical approach described below includes ZIP code and year FEs to control for time-invariant influences at a ZIP code level, as well as ZIP code–variant influences over time. Finally, data for our instruments is obtained from the Atlas of U.S. Presidential Elections (http://uselectionatlas.org). Data on the outcomes of U.S. presidential elections is normally collected at the level of the electoral district. Disaggregated data that assigns election data to ZIP codes is not available. To our knowledge, the Atlas of U.S. Presidential Elections provides the most disaggregated form of voter registration and election data, and it is at a county level. We combine these different datasets into an unbalanced panel dataset where the panel unit is the ZIP code i in county c and year t. As stated, IA data, population data, data on insurance demand, premiums, and claims are all available at the ZIP code level i. We merge county level data on income per capita, educational attainment, and election outcomes in county c to each of the ZIP codes i that are located in the corresponding county using Geographic Information System software. We assign each ZIP code to its corresponding county (if ZIP code borders cross county borders, we assign the ZIP to the county that contains the majority of its land area). In cleaning the data, we had to drop several observations of IA grants and SBA loans where the ZIP code was entered incorrectly or was not found in our other datasets. We also dropped ZIP codes that never had

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any insurance policyholder over our sample period. We further excluded ZIP codes with fewer than 100 inhabitants. Our analysis focuses on the remaining 23,150 ZIP codes.

4. Empirical Methodology We first specify the following FE model using our panel dataset with i indexing ZIP codes, c indexing counties, and t indexing years: .(1) The dependent variable, FI, as noted above, is either the average coverage level per NFIP policy or the take-up rate of flood insurance. ZIP code FEs,

, control for any time-invariant aspects of the ZIP code, such as

its exposure to flood hazards. Year FEs, given by

, control for shocks and changes that are common to all ZIP

codes within a given year. IA, our variable for FEMA grants, is a dummy variable that switches to one if county c received any IA in year t and zero otherwise. The resulting dummy variable is labeled Positive IAit. We also control for flood damage in the ZIP code using flood insurance claims in the ZIP code in the previous year, noted Cict-1, measured as the average flood insurance claim per policyholder. Claims should also control for the extent of damage, such that we capture responses to aid and no other impacts of the event. Our other controls, represented by vector X, include premium per policy and population at the ZIP code level and median income and educational attainment at the county level. We cluster our standard errors at the county level. In extensions, we examine the average and total amount of IA grants and SBA loans and the approval rate for IA grants. Since the FE model might be biased due to reverse causality (aid can influence insurance, but insurance penetration and coverage levels could also influence the amount of aid given) and that there could be correlated omitted variables, such as demographic variables (for example, highly educated households may be more likely to insure and also better able to navigate the bureaucratic red tape necessary to receive federal aid) we also estimate the impact of IA grants on insurance purchases using an IV model. As indicated in the introduction, our identification strategy exploits an exogenous source of variation in governmental relief. A key characteristic of governmental relief in the United States is that it depends on 14

discretionary political decisions. Garrett and Sobel (2003) show that, compared to other years, federal disaster relief is, on average, $140 million higher in election years. They also show that states with greater importance for the election outcome have, on average, a higher rate of disaster declarations, everything else being equal. Hence, election years and variation in the political importance of an area can generate variation in federal aid payments. While Garrett and Sobel use states as their unit of analysis, presidents and respective governors have some discretion over which counties receive a declaration and it is not implausible that political influence plays some role at a finer geographic scale, as well. Using this source of exogenous variation, we implement an IV-approach that is inspired by Nunn and Qian (2014). In particular, we specify the following first stage equation: .(2) In equation (2), variable, and

and

represent the vectors of ZIP code and year fixed effects,

is the vector of other covariates.

, is the claims

is a dummy variable that switches to one if the county is

a swing county and zero otherwise. This variable is time-invariant and defines a swing county if the winning margin in any presidential elections between 2000 and 2011 was <5%16 and the county is located in a swing state.17

a dummy indicating that year t-1 was a Presidential election year. As mentioned above, our identification strategy basically applies difference-in-differences approach. In

the first stage, we compare the effect of Presidential election years on the likelihood of receiving any FEMA IA between counties of relatively high political importance (and thereby a higher probability of receiving discretionary IA) and counties of relatively lower political importance (and a lower probability of receiving

16

There is no theoretical guidance about the definition of the cut-off point that would define a swing county. Thereby, the level of the cut-off point was an empirical question. Table A.1 in the appendix presents the results for alternative cut-off points. For cut-off points at 1% and 3%, the first stage F-stat slightly decreased, while for a 7% cut-off point slightly increases. The estimated secondstage coefficients are within a similar range, however, they are less precisely estimated if those alternative cut-off points are used. Our IV strategy estimates local average treatment effects and therefore only provides consistent estimates for the subgroup of counties with a particular winning margin. This robustness check now compares the LATE for different subset of counties based on winning margins. While it shows that the size of estimated effect is very similar within the 1-7% range of winning margins, the statistical significance of the estimates varies by the winning margin. 17 Swing states are Colorado, Florida, Iowa, Michigan, Minnesota, Ohio, Nevada, New Hampshire, North Carolina, Pennsylvania, Virginia, and Wisconsin.

15

discretionary IA). In a reduced form setting, we compare the difference in insurance demand in (the first lag of) election years versus other years in counties that are politically more important to counties that are politically less important. The identifying assumption is that, conditional on the other control variables, the interaction between a county’s political importance in election years affects insurance demand only through governmental aid. One concern with this assumption is that increased public expenditure on flood protection or through other subsidies during election years can impact flood insurance demand. While we view this as unlikely in our setting, we include year fixed effects in our specification to flexibly capture any year-specific changes in flood insurance over time. Another concern regarding the violation of the exclusion restriction is that the political importance of a county might directly affect the demand for flood insurance. For example, counties that are more politically important could differ in terms of demographic variables that are also related to insurance demand. For example, flood insurance demand might plausibly differ by age of the population and their level of education. Alternatively, those counties could invest more in flood protection, and outreach and information efforts, which directly impact individuals’ flood insurance decision. However, we control for all the direct effects of political importance on insurance demand by including ZIP-code fixed effects. Nunn and Qian (2014) cluster standard errors at the level of the “treatment variable” part of the interaction term, which is the panel unit. In our case, the treatment variable is the swing county dummy, and it only varies at the group level (there are multiple ZIP codes within one county). This means that first-stage errors are likely to be clustered at the county level; clustering at the panel unit (ZIP code) could overstate the precision of the first-stage estimates (thus impacting first stage F-statistic results). Therefore, in our baseline regressions, we follow the suggestion by Bertrand et al (2014) and cluster the standard errors at the county level. As robustness checks, we also present results with standard errors clustered more conservatively at the county and state-year (two-way) level as well as at the disaster number level.

16

More importantly, however, our first stage regression is just-identified; using one IV for one endogenous variable. In general, the bias from potentially weak instruments increases in the number of instruments, therefore the bias is the smallest in a just-identified specification (Angrist and Pischke 2009a). In addition to the theoretical argument, Angrist and Pischke (2009b) show with a Monte Carlo simulation that with a sufficiently large first stage coefficient18, the estimated second stage coefficient from a just-identified IV is centered around the true coefficient. As an additional test, we also estimate a limited information maximum likelihood (LIML) model. The LIML estimator provides a finite-sample bias reduction so the estimated coefficients are less biased (econometrically defined) than the IV results; it is thus a useful benchmark for comparison with our IV results (Bekker 1994). If coefficients are similar, this will provide additional support for our findings. Our baseline analyses examine the impact of receiving any IA in a ZIP code the previous year on flood insurance demand in the ZIP code. We also undertake several robustness checks and extensions. First, we estimate a variety of other specifications and also undertake a couple falsification tests. We find our results to be robust to all these checks. We then limit the data to 2004 – 2011 to examine the impact of the average and total amounts of IA grants provided to a ZIP code, as opposed to just the binary measure used in the base specification.

5. Results The baseline results are presented in Table 2. The effect of receiving any IA on average household insurance coverage is given in columns 1-4. Column 1 contains the FE estimates of equation (1). The coefficient is negative and statistically significant at the 1% level. The estimated effect suggests that in counties that have received IA in the previous year, average flood insurance coverage per policy is consequently reduced by $350. Column 2 presents the reduced form estimates of the effect of our instrumental variable on the

18

Angrist and Pischke (2009b) suggest a coefficient between 0.1 and 0.2.

17

outcome of interest. The effect of the instrument on insurance demand is negative and statistically significant at the 1%-level. The results of the 2SLS estimates of equation (3) are presented in column 3. According to the estimates, receiving any IA in the previous year reduces average flood insurance coverage per household policy in that ZIP code by around $4,100. This is roughly 3% of the average insurance coverage per policy in our sample of almost $152,000. This is somewhat larger than the average size of flood-related IA grants, which during our sample period was $2,984. The first stage F-statistics (column 4) for our IV specification is 27.92 and above the critical value of the Stock-Yogo weak ID test for a 5% relative bias in the IV of 16.58. Once we account for potential clustering of the model errors at the county and state-year level and apply two-way clustering the value of the first stage Fstats decreases to 7.85. Despite being below the commonly used threshold, however, we are less concerned that our instrumental variable suffers from a potentially weak instrument bias. The first stage equation is only using one instrument for one endogenous regressor and is thereby just-identified. In general, the weak instrument bias increases in the number of instruments. Angrist and Pischke (2009) show that a just-identified 2SLS is “approximately unbiased.” Theoretically, in the case of a just-identified first stage. Results from a Monte-Carlo simulation suggest that with a sufficiently large first stage coefficient and falls in the range between 0.1 and 0.2, the estimated second stage coefficient from a just-identified IV is centered around the true coefficient (Angrist and Pischke 2009b). In our case, the first stage coefficient of the IV is 0.15. To check potential concerns about weak instruments in some specifications, we also estimate a limited information maximum likelihood (LIML) model. While less precise, these estimates are also less biased as mentioned before. Results presented in the appendix (Tables A.2) show that the estimated coefficients of IV and IV-LIML are very similar, which provides assurance that the IV approach is robust. Columns 5 to 8 show the results of Positive IA on the number of NFIP flood insurance policies-in-force per 100 residents. Of note, we exclude policies that were purchased as a requirement of receiving federal disaster aid (a household receiving an IA grant is required to carry flood insurance going forward; not doing so 18

would lead to the federal government denying further individual disaster assistance in the future). As such, we only examine changes that were not a result of the policy requirement. Both the FE and the 2SLS estimates yield positive coefficients that are, however, not statistically different from zero.

It appears, absent the

insurance purchase requirement imposed by the federal government, that receiving the limited FEMA IA grants has almost no impact on the extensive margin. Comparing the estimated coefficients for IA in columns 1 and 3 and columns 5 and 7 reveals large differences between the FE and IV models. One reason for the divergence could simply be in the bias from the time-varying endogeneity in the fixed effects model. Another reason could be our identification strategy that exploits exogenous variation in political factors as an instrument for IA. In general, the effect of IA on insurance demand is likely to be heterogenous among ZIP codes. Our IV explains why particular ZIP codes (i.e. ZIP codes in swing counties) in particular years (election years) are chosen to receive federal relief. The exogenous variation is driven only by this subpopulation of ZIP codes and years that receive IA for political reasons. Therefore, our approach captures the local average treatment effects (LATE) of a small and peculiar group of ZIP codes. In contrast, least square estimates approximate average treatment effects (ATE) for every ZIP code. Therefore, it is not uncommon that coefficients from IV estimates can largely exceed those of least square estimates (e.g. Card 2001, and Oreopoulos 2006). To investigate this further, we compare point estimates from restricted samples using the FE model.19 We find that the estimated coefficient is around twice as large if one compares the results between election and non-election years (-0.59 vs -0.31) as well as swing counties and other counties (-0.72 vs -0.33). Comparing the effect in a sample restricted only to swing counties in election years versus all other counties and years yields a large difference (-2.19 vs. -0.36). This suggests that the difference between the FE and the IV estimates can be partially attributed to estimating the LATE and partially to the time-varying endogeneity. Table 2 also shows the results for our other controls. Median income is negative, suggesting that, as incomes increases, households may tend to self-insure, but the coefficient is small in magnitude. Our premium 19

Results are available in the online appendix.

19

variable is negative and significant, as one would expect, but for the reasons discussed above, we do not interpret this as a price elasticity. As the percent of adults with a Bachelor’s degree or higher increases, average coverage, perhaps surprisingly, declines. There is not statistically significant impact of educational attainment on policies-in-force. Finally, the impact of higher average claims is very small. A number of factors may explain this result. The year and ZIP code FEs could be absorbing much of the impact of claims on insurance demand. Individuals might base their coverage levels on their mortgage or home values and may not adjust much after an event. It could also be that, in aggregated data, we cannot tease apart adjustments that are both upward and downward after a disaster event. This is worthy of further study. We are not able to explicitly control for damaged homes in our analysis. Some might argue that, in theory, if a home is severely damaged by a flood and is not immediately repaired, the homeowner may temporarily reduce coverage commensurate with the lower value of the property. For three reasons, we do not believe that this is the cause of the decrease in insurance purchased. First, the destruction is likely to be temporary (a few weeks or months). For example, Bin and Landry (2013) find that the effect of disasters on house prices is not persistent. Second, our data is aggregated to the ZIP code and there may be just as many residents who undertake upgrades with their rebuilding, such that their homes are now worth more. Finally, a decline in home value is usually caused by a decline in the value of the land and is not expected to alter insurance coverage designed to repair or replace damage to the structure. Table 3 presents the results of alternative estimators and specifications. Column 1 (5) estimates equation (1) for average coverage (policies in force) using a random effects (RE) model. The estimated coefficient is negative and of similar magnitude to the fixed effects model but the results of a Hausman Test clearly reject the RE model. Using first differences instead (columns 2 and 6), we do not find any statistically significant effects. In column 3 (7) we present specifications in that exclude the premiums and claims variables because they could be potentially endogenous regressors. Qualitatively, the results are similar to the baseline specification; the coefficients of the relief variable do not change their sign or level of statistical significance. However, the size of the estimated coefficients increases. For average coverage, getting any IA now decreases average coverage 20

by $12,300, or roughly 8% of the average insurance coverage level. The results from the first stage test statistics are also comparable to those in the baseline specifications. Finally, we evaluate the effect of IA over time by including the first, second and third lag in one specification (columns 4 and 8). The effect of IA on average coverage persists over time but seems to decrease with the third lag. Interestingly, for take-up rates we find a statistically significant and positive effect of the second lag of IA on policies in force. We are unclear what could be driving this. Those results indicate that investigating the dynamics of the crowding-out effect over time would be an interesting question for future research. We now provide additional evidence for the validity of the identification strategy by presenting the results from two falsification tests in Table 4. First, we estimate the reduced form equation but only for countyyears that have not received federal disaster assistance. If our identifying assumptions are valid, political importance in an election year should not have a direct relationship on flood insurance for those county and year combinations. Column 1 contains the reduced-form estimates for average coverage, while column 2 contains the reduced form estimates for policies in force. We do not find any statistically significant effect of the IV on the outcome variables in the restricted sample. In the second test, we estimate again the reduced form equation but instead of analyzing the link between a county’s political importance and flood insurance, we estimate the effect of a county’s political importance in election years and health insurance. The underlying idea of this test is that if our identifying assumptions are valid, political importance in an election year should not impact general individual insurance behavior in a county, for example through demographic changes, particular information or short-term policies driven by re-election concerns. Data on health insurance penetration (percentage of insured individuals) are obtained from the U.S. Census Small Area Health Insurance Estimates (SAHIE). This data is only available on the county level for the years 2006 to 2011. We merge the SAHIE data to our main dataset and aggregate the data up to the county and

21

year level for the years 2006 to 2011. The resulting dataset includes yearly observations for 2,750 counties.20 We then use the same specification as in our reduced form estimates in Table 2 column 2 but replace the flood insurance variable on the left hand side with the health insurance penetration variable. The estimates in Table 4 column 3 show that the coefficient of the IV for the placebo insurance is small and not statistically significant. Overall, we take these estimates as additional support for the validity of our IV.21 We turn now to two extensions. First, we add as another regressor whether the ZIP code received any SBA disaster loans in the previous year. This is shown in Table 5. Compared to the baseline specifications in Table 2, the coefficient for IA increases slightly, indicating that receipt of any IA grants lead to a $5,100 decline in average coverage (IV model). The estimated coefficient for the SBA dummy is positive and weakly significant at the 10% level in the IV model. This suggests that in contrast to IA, SBA loans do not appear to have a crowding out effect and they might even have a small crowding in effect (column 2). Adding SBA loans does not change the results for the take-up rates per 100 residents and, similar to IA, SBA loans do not have an impact on policies in force. As the final extension, we examine the effect of the magnitude of the IA grants and SBA loans on insurance demand. In Table 6, the first two columns look at the effect of the average IA grant and SBA loans the previous year with our FE (column 1) and IV (column 2) specifications. We find that as the average grant increases by $1,000, the average amount of coverage declines by roughly $1,600 in the IV specification. The coefficient of average SBA loan amount is positive and statistically significant at the 10% level, but essentially zero. Columns 3 and 4 replicate the approach but examine the total amount of IA grants and SBA loans given to a ZIP code the following year. For the IV specification, we find an increase in total IA grants has a negative impact on coverage, but it is only significant at the 17% level. The lower significance could be due to not being able to control for the number of households impacted, such that the average and binary IA measures are better predictors. The impact of total SBA loans is significant but close to zero. We find some statistically significant 20

A description of the data is included in the online appendix.

21

In a further robustness check we estimated our baseline specification and excluded individual years from the sample (Table A.4. in the online appendix). The estimated effect stayed qualitatively and quantitatively the same, showing that our results are not driven by observations from a particular year.

22

crowding out effect for the total number of IA grants made (columns 5 and 6) and a statistically significant crowding-in effect of total number of SBA loans. The IA approval rate also has a crowding out effect; in the IV specification we see a decline of $7,009 in average coverage for a 10%-point increase in the approval rate. Across all the measures of IA, we find the results to consistently be negative and economically modest in magnitude. In Table 7 we turn to examining the impact of the same independent variables on the take-up rate in a ZIP code. For the IV specifications, we never find a statistically significant effect of IA or SBA on policies in force per capita, after removing policies that were required to be purchased due to receipt of federal disaster aid.

6. Conclusion This article provides the first causal estimates of the effect of federal disaster aid on the demand for flood insurance. The possible crowding-out effects of federal aid have been raised by commentators after major disaster events yet empirical evidence on this topic had been lacking. Overall, we find that federal post-disaster grants provided to households for uninsured losses have a negative impact on average insurance coverage across all measures of IA, although significance levels vary. The amount appears economically modest, between $4,000 and $5,000 in the IV models (roughly 3% of the mean level of insurance coverage), yet this is greater than the average size of an IA grant of $2,940. The IA program provides limited amounts of aid to victims and yet we still find indication of a reduction in insurance coverage; while we cannot extrapolate findings to larger amounts of such aid, we would caution that crowding out could increase with increases in post-disaster grants. Further work, however, is warranted on possible heterogeneity in responses. SBA loans, by contrast, have almost no impact on insurance demand. Since loans need to be repaid, it is perhaps not surprising there is no indication of a crowding out effect on insurance. We find no impact on takeup rates after accounting for policies that are required to be purchased as a condition of receiving disaster aid. While we do not know whether those individuals would have failed to insure absent this requirement, it does seem that it is effective in preventing decreases in take-up rates after a disaster. 23

Our findings should be of value to ongoing discussions regarding disaster financing, a conversation that has become more critical in light of recent catastrophes that have strained federal resources.22 Increases in disaster damages, due to both more people locating in risky areas and potential impacts of a changing climate, are likely to continue on their upward trends (Gall et al. 2011; Barthel and Neumayer 2012); this could increase the financial burden of disasters on taxpayers. Our paper suggests that the federal policy of making SBA loans the primary form of government response and capping IA grants are important steps in limiting the perverse incentive effects federal disaster aid could create. To better manage perverse incentive effects, however, all residents of disaster-prone areas need to be educated about the limited nature of assistance before a flood occurs. We caution readers that there are two other areas that may have much greater crowding out effects that are worthy of complementary analysis. First, if recent aid spending is any guide, Congress is appropriating more disaster aid funds to the Department of Housing and Urban Development for post-disaster Community Development Block Grants, as opposed to FEMA; individuals may or may not receive large reimbursements for damage from programs implemented with these funds, as local governments have enormous flexibility in how they are spent. This is another area in need of more careful analysis, particularly if homeowners begin receiving much larger grants than given under the IA program and many more grants are actually approved than that is the case today. One reason this article finds limited crowding out effects is likely due to the small size of the IA grants. Second, the vast majority of disaster aid spending goes to local governments through Public Assistance. Future work should examine whether those dollars crowd out hazard mitigation at a local level, for example, by influencing land use, development, or building code decisions.23

22

Findings by Strobl (2011) suggest that natural catastrophes can lead to large short-run economic disruptions at the local level in the U.S. However, these effects tend to be netted out at the state level and do not appear to have a systematic impact on annual growth rates in the U.S. His findings are in line with other recent empirical studies on the effects of natural disasters on economic growth (e.g. Noy and Cavallo 2011, Cavallo et al. 2013). 23 A recent paper examines the impact of FEMA spending on hazard reduction (Davlasheridze et al. 2017), a somewhat different question that whether Public Assistance spending has perverse incentive effects.

24

Federal response will also need to address affordability issues and the distributional impacts of insurance and aid policies (National Research Council, 2016). Millions of Americans live below the poverty line with little financial capacity to purchase financial protection through insurance or to pay the up-front cost of flood risk reduction measures to make their residences safer. This has become a focus of Congressional action recently. Some observers have proposed that, rather than providing taxpayers aid money after a disaster, it would be more efficient to develop a means-tested flood insurance voucher program for low-income residents currently living in flood-prone areas so they can purchase that coverage and be more financially independent should they suffer a flood (Michel-Kerjan and Kunreuther 2011; Kousky and Kunreuther 2014). Furthermore, future work could better identify the relationship between uninsured homeowners and amounts of aid given.

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TABLE 1 DESCRIPTIVE STATISTICS, U.S. ZIP CODES, 2000-2011 Variable

Obs

Mean

Std. Dev.

Min.

Max.

Average coverage per policy in $1,000s

193,610

151.716

74.409

4.750

350.000

Policies-in-force per capita

193,610

1.657

4.928

0.002

99.985

32

Premium per $1,000 coverage

193,610

3.128

2.485

0.570

57.777

Positive IA

193,610

0.195

0.396

0.000

1.000

Positive SBA

193,610

0.186

0.389

0.000

1.000

Average claim(in $1,000s)

193,610

0.901

14.614

0.000

4166.372

193,610

34051.880

10156.100

10824.000

124088.000

193,610

13322.000

14673.840

100.000

113977.000

193,610

23.582

10.155

3.194

73.152

193,610

0.115

0.319

0.000

1.000

193,610

0.024

0.154

0.000

1.000

Average IA per grant (in $1,000)

136,290

0.393

1.384

0.000

44.421

Total IA grant amount (in $100,000s)

136,290

0.789

23.815

0.000

4181.283

Total number of IA grants

136,290

21.551

320.962

0.000

32127.00

IA grant approval rate

135,575

0.069

0.202

0.000

1.000

Average SBA per loan (in $1,000)

136,290

5.296

31.421

0.000

4491.05

Total SBA loan amount (in $100,000s)

136,290

0.471

13.049

0.000

2352.03

Total number SBA loans

136,290

0.979

18.597

0.000

County income per capita ($1,000s)

*

Population in ZIP % Adults with Bachelor deg.

*

*

Swing County

Swing County × Election Year

*

Notes:* Data only at county level

TABLE 2—IMPACT OF POSITIVE IA ON FLOOD INSURANCE DEMAND: BASELINE ESTIMATES, UNITED STATES, 2000-2011 Dependent Variable:

Average coverage in $1,000sict

Positiv e IAict-1

Reduced Form

First Stage

FE

Reduced Form

IV

First Stage

(4)

(5)

(6)

(7)

(8)

FE

Positive IAict-1

(1) 0.348*** (0.119 )

Swing Countyc ×

coverageict Average claim (in $1,000s)ict-1 Median income (in $1,000s)ct

Populationict

(3) 4.111** (1.879 )

(0.205) 2.183*** (0.061 ) 0.004*** (0.002 ) 0.230*** (0.058 ) -

-2.183*** (0.061) -0.005*** (0.002) -0.233*** (0.059) -0.220***

0.023 (0.019 ) 0.152 *** (0.02 9)

-0.654***

Election Yeart-1 Premium per $1,000 of

(2)

IV

2.190*** (0.061 ) -0.001 (0.002 ) 0.000*** (0.000 ) -

0.001 (0.00 1) 0.001 *** (0.00 0) 0.013 *** (0.00 3) 0.001

Positiv e IAict-1

Policies-in-forceict

0.117 (0.308 )

(0.009)

0.000 (0.001 ) 0.039* ** (0.010 )

0.152 *** (0.02 9) 0.001 * (0.00 1) 0.001 *** (0.00 0) 0.013 *** (0.00 3)

-0.039***

-

0.001

0.018 (0.047) 0.013** (0.006 ) 0.000 (0.000 ) 0.041* ** (0.009 ) -

-0.013** (0.006) 0.001 (0.000) 0.041***

0.013** (0.006 )

33

0.219***

% Adults with Bachelor deg.ct

0.000***

(0.036 ) 0.478*** (0.129 )

(0.036)

(0.000 )

-0.483*** (0.129)

0.039*** (0.00 1)

(0.007 )

0.009 (0.00 6)

-0.003 (0.016 )

0.039*** (0.007) -0.002 (0.016)

(0.007 )

(0.00 1)

-0.003 (0.016 )

0.009 (0.00 6)

ZIP FE

Yes

Yes

Yes

Yes

Yes

Yes

Yes

Yes

Year FE

Yes

Yes

Yes

Yes

Yes

Yes

Yes

Yes

First-stage F-stat

27.92

27.92

[7.21]

[7.21]

Notes: N = 193,610. This table contains: FE (columns 1 and 5) and IV (columns 3 and 7) estimates of the effect of IA on insurance demand, measured as average coverage in $1,000and policies-in-force per household; Reduced form estimates (columns 2 and 6) of the effect Swing Countyc × Election Yeart-1 on average coverage in $1,000and policies-in-force per household; First stage estimates (columns 4 and 8). Positive IA is a dummy variable that switches to one if the ZIP code received IA in t-1 and zero otherwise. All specifications include ZIP code and year FEs. Panel units are ZIP codes. The first lag of an interaction term between a dummy indicating that county c is a swing county and a dummy indicating that year t is a Presidential election year is used as an instrument for Positive IA it-1, in columns 3 and 7. First-stage F-stat based on c are reported in square brackets. Standard errors (in parentheses) are clustered at the county (c) level. Constants are included but not reported. *** Significant at the 1 percent level; ** Significant at the 5 percent level; * Significant at the 10 percent level.

TABLE 3—IMPACT OF POSITIVE IA ON FLOOD INSURANCE DEMAND: ALTERNATIVE ESTIMATORS AND SPECIFICATIONS, UNITED STATES, 2000-2011 Average coverage in $1,000sict

Dependent Variable:

Positive IAict-1

Policies-in-forceict

RE

FD

IV

IV

RE

FD

IV

IV

(1)

(2)

(3)

(4)

(5)

(6)

(8)

0.022 (0.020 )

0.003 (0.017 )

(7) 0.2 63 (0.2 82)

0.468*** (0.121 )

-0.152

-12.335***

-6.928***

(0.195)

(1.727)

(2.524)

Positive IAict-2

-8.208*** (2.533)

Positive IAict-3

-4.338*

0.021** * (0.006 )

0.028** * (0.010 )

-0.560 (0.879 ) 0.031** * (0.010 )

0.001 (0.001 )

0.001 (0.001 )

0.000 (0.001 )

193610

162841

(2.352)

Premium per $1,000 of coverageict Average claim (in $1,000s)ict-1

2.291*** (0.061 ) 0.004*** (0.002 )

3.537***

-2.316***

(0.111) 0.028***

Obs.

(0.006) 16308 193610 3

Hausman Test

165.74

(0.076) -0.002 (0.002) 193610

142255

0.072 (0.588 ) 1.229 ** (0.559 )

19361 0

142078

161.03

Notes: This table contains: FE (columns 1 and 5) and IV (columns 3 and 7) estimates of the effect of IA on insurance demand, measured as average coverage in $1,000 and policies-in-force per household; Reduced form estimates (columns 2

34

and 6) of the effect Swing Countyc × Election Yeart-1 on average coverage in $1,000and policies-in-force per household; First stage estimates (columns 4 and 8). Positive IA is a dummy variable that switches to one if the ZIP code received IA in t-1 and zero otherwise. All specifications include median income, population, educational attainment, ZIP code and year FEs. Panel units are ZIP codes. The first lag of an interaction term between a dummy indicating that county c is a swing county and a dummy indicating that year t is a Presidential election year is used as an instrument for Positive IA it-1, in columns 3 and 7. Standard errors (in parentheses) are clustered at the county (c) level. Constants are included but not reported. *** Significant at the 1 percent level; ** Significant at the 5 percent level; * Significant at the 10 percent level.

TABLE 4—FALSIFICATION AND PLACEBO TEST, UNITED STATES, 2000-2011 Average Dependent Variable:

Swing Countyc × Election Yeart-1 Premium per $1,000 of coverageict

Coverageict

Health Insurance

PIFict

penetrationct

(1)

(2)

(3)

-0.574

-0.002

0.013

(0.367)

(0.062)

(0.090)

-2.159***

-0.015**

(0.067)

(0.007)

Premium per $1,000 of

-0.004

coveragect

(0.013)

Average claim (in $1,000s)ict-1

-0.004***

0.000

(0.001)

(0.001)

Average claim (in $1,000s)ct-1

-0.003* (0.001)

N

160,110

159,919

14,998

Notes: This table contains reduced form estimates of the effect of IV (Swing County × Election Year) on insurance demand, measured as average coverage in $1,000 and policies-in-force per household for a sample that excludes all ZIP code-years with positive IA relief. All specifications include median income, population, educational attainment, ZIP code and year FEs. Panel units are ZIP codes. Standard errors (in parentheses) are clustered at the county (c) level. Constants are included but not reported. *** Significant at the 1 percent level; ** Significant at the 5 percent level; * Significant at the 10 percent level.

TABLE 5—IMPACT OF POSITIVE IA AND SBA ON FLOOD INSURANCE DEMAND: ALTERNATIVE ESTIMATORS AND SPECIFICATIONS, UNITED STATES, 2000-2011 Average coverage in $1,000sict

Policies-in-forceict

FE

IV

FE

IV

(1)

(2)

(3)

(4)

-0.312***

-5.153**

0.021

0.136

(0.119)

(2.386)

(0.019)

(0.393)

Positive SBAict-1

-0.220**

1.264*

0.007

-0.028

(0.090)

(0.731)

(0.013)

(0.122)

Premium per $1,000 of

-2.183***

-2.175***

-0.013**

-0.013**

(0.061)

(0.061)

(0.006)

(0.006)

Positive IAict-1

coverageict

35

Average claim (in $1,000s)ct

-0.004***

-0.002

0.000

0.000

(0.002)

(0.002)

(0.000)

(0.001)

-0.228***

-0.175***

0.040***

0.039***

(0.058)

(0.057)

(0.009)

(0.010)

-0.220***

-0.210***

-0.039***

-0.039***

(0.036)

(0.036)

(0.007)

(0.008)

-0.477***

-0.445***

-0.003

-0.003

(0.129)

(0.133)

(0.016)

(0.017)

ZIP FE

Yes

Yes

Yes

Yes

Year FE

Yes

Yes

Yes

Yes

Median income (in $1,000s)ct Populationict % Adults with Bachelor deg.ct

First-stage F-stat Notes: This table contains: FE (columns 1 and 2) and IV (columns 2 and 4) estimates of the effect of positive IA and SBA on insurance demand, measured as average coverage in $1,000 and policies-in-force per household; Positive IA (SBA) is a dummy variable that switches to one if the ZIP code received IA (SBA) in t-1 and zero otherwise. The first lag of an interaction term between a dummy indicating that county c is a swing county and a dummy indicating that year t is a Presidential election year is used as an instrument for Positive IA it-1, in columns 2 and 4. Standard errors (in parentheses) are clustered at the county (c) level. Constants are included but not reported. *** Significant at the 1 percent level; ** Significant at the 5 percent level; * Significant at the 10 percent level. TABLE 6 —IMPACT OF AVERAGE, TOTAL IA GRANT AMOUNT, TOTAL IA GRANTS AND IA GRANT APPROVAL RATE ON AVERAGE COVERAGE, UNITED STATES, 2004 - 2011

Average coverage in $1,000s

Average IA per grant ict-1 Average SBA per loan ict-1

FE

IV

FE

IV

FE

IV

FE

IV

(1)

(2)

(3)

(4)

(5)

(6)

(7)

(8)

0.067**

1.585**

(0.033)

(0.801)

0.000

0.006*

(0.001)

(0.003) 0.003*

Total IA grant amount

**

(in $100,000s) ict-1

-2.140 (0.001) 0.002*

Total SBA loan amount

**

(in $100,000s) ict-1

(1.552) 1.244

(0.001)

(1.017)

Total IA grants ict-1

0.000* (0.000) 0.002*

Total SBA grants ict-1

**

0.024* (0.012) 0.164*

(0.000)

(0.087)

IA grant approval rate ict-1

Premium per $1,000 of coverageict Average claim (in $1,000s)ict-1

0.510***

-7.009*

2.583***

2.580***

2.584***

2.331***

2.584***

2.574***

(0.192) 2.586***

(3.674) 2.581***

(0.078) 0.007***

(0.068)

(0.078) 0.007***

(0.240)

(0.078) 0.007***

(0.068) 0.008**

(0.078) 0.007***

(0.068)

(0.001)

(0.005)

(0.001)

(0.046)

(0.001)

(0.003)

(0.001)

(0.003)

0.001

0.038

-0.003

First-stage Estimates

36

Swing Countyc ×

0.406 (0.088)* ** [0.195]* * 21.41[4. 35]

Election Yeart-1

First-stage F-stat

0.868 (0.452)* *

48.016 (21.976) **

[0.667] 3.69[1.7 0]

[33.091] 4.77[2.1 1]

0.085 (0.019)* ** [0.040]* * 20.57[4. 49]

Notes: N = 148,498. This table presents FE (columns 1, 3, 5, and 7) and IV (columns 2, 4, 6, and 8) estimates of the effect of Average and Total IA amount, Total IA grants, and HA grant approval rate on insurance demand, measured as average coverage in $1,000. All specifications include median income, population, educational attainment, ZIP code and year FEs. Panel units are ZIP codes. The first lag of an interaction term between a dummy indicating that county c is a swing county and a dummy indicating that year t is a Presidential election year is used as an instrument for the IA variables, in columns 2, 4, 6, and 8. First-stage F-stat based on disaster declaration number are reported in square brackets. Standard errors (in parentheses) are clustered at the county (c) level. Constants are included but not reported. *** Significant at the 1 percent level; ** Significant at the 5 percent level; * Significant at the 10 percent level.

Table 7 —Impact of Average, Total IA Grant Amount, Total IA Grants and IA Grant Approval Rate on Average Coverage, United States, 2004 - 2011 Policies-in-forceict

Average IA per grant ict-1 Average SBA per loan ict-1

FE

IV

FE

IV

FE

IV

FE

IV

(1)

(2)

(3)

(4)

(5)

(6)

(7)

(8)

0.000 (0.000) 0.003* **

-0.000 (0.002)

(0.000)

(0.015)

0.009

-0.002

(0.007)

(0.152)

0.000

0.000

(0.000)

(0.001) 0.001* **

Total IA grant amount (in $100,000s) ict-1 Total SBA loan amount

(0.000) 0.004* **

(in $100,000s) ict-1

(0.000)

-0.013 (0.205 ) 0.012 (0.119 )

Total AA grants ict-1 Total SBA grants ict-1

0.005

IA grant approval rate ict-1

Premium per $1,000 of coverageict Average claim (in $1,000s)ict-1

0.034***

0.034***

0.034***

(0.009)

(0.008)

(0.009)

0.000

0.000

-0.000

(0.000)

(0.001)

(0.000)

-0.033 (0.026 ) 0.000 (0.004 )

0.079***

-0.175

0.034***

0.034***

(0.025) 0.034***

(0.700) 0.034***

(0.009)

(0.008)

(0.009)

(0.008)

-0.000

-0.000

0.000

0.000

(0.000)

(0.000)

(0.000)

(0.001)

First-stage Estimates Swing Countyc × Election Yeart-1

First-stage F-stat

0.406 (0.088)* ** [0.195]* * 21.41[4. 35]

0.868 (0.452) **

48.016 (21.976) **

[0.667] 3.69[1. 70]

[33.091] 4.77[2.1 1]

0.085 (0.019)* ** [0.040]* * 20.57[4. 49]

37

Notes: N = 148,498. This table presents FE (columns 1, 3, 5, and 7) and IV (columns 2, 4, 6, and 8) estimates of the effect of Average and Total IA amount, Total IA grants, and HA grant approval rate on insurance demand, measured as policies per capita. All specifications include median income, population, educational attainment, ZIP code and year FEs. Panel units are ZIP codes. The first lag of an interaction term between a dummy indicating that county c is a swing county and a dummy indicating that year t is a Presidential election year is used as an instrument for the IA variables, in columns 2, 4, 6, and 8. First-stage F-stat based on disaster declaration number are reported in square brackets. Standard errors (in parentheses) are clustered at the county ( c) level. Constants are included but not reported. *** Significant at the 1 percent level; ** Significant at the 5 percent level; * Significant at the 10 percent level.

38