Essays on Measuring Dynamic Community Responses to Environmental Events

One of the things that makes economics such an interesting social science subfield to study is the analysis of unintended or unforeseen consequences. In order for policies to be efficient and equitable, it is important to first understand how endogenous policy decisions and exogenous events can affect communities either directly or indirectly. In this dissertation research, I examine how communities react to discrete environmental events over time. I do so in the context of tropical storm and hurricane activity in U.S. counties and media markets as well as land conservation spending decisions in Massachusetts and New Jersey municipalities. Using micro-level data on environmental events and behavior in difference-in-differences and dynamic regression discontinuity frameworks, I test whether: (1) hurricane strikes affect poverty levels in impacted counties, (2) tropical storms and hurricanes create a window of opportunity where the affected population is interested in taking action to mitigate against future costs, and (3) local municipal conservation actions cause crowd-in or crowd-out conservation behavior from the state and neighboring local governments. The use of micro-level data (at the sub-state level) allows for the possibility of rigorous treatment identification that hold important implications for policymakers in all three settings.


INTRODUCTION
Natural disasters such as hurricanes, tornadoes, wildfires, droughts, and freezes cause enormous environmental and economic damage in the United States. Since 1980, there have been 212 weather events where the overall damages have reached or surpassed $1 billion. In 2017 alone, there were 15 weather and climate disaster events with 282 deaths and financial losses over $1 billion (NCEI, 2017). Despite the magnitude of these losses, we lack full understanding of the complete economic effects of natural disasters.
Growing research has shown that a person's socioeconomic status often determines vulnerability to natural disaster impacts (Fothergill and Peek 2004). This link between income and natural disaster impact leads to such questions asdo natural disasters affect the poverty levels in the areas they occur? What happens to economic activities? How do natural disasters affect the population of areas they hit over time?
We address these questions in the context of hurricanes that strike the United States. We use a panel of coastal counties in states that border the Atlantic Ocean and Gulf of Mexico to identify the dynamic effect hurricane strikes have on poverty levels over a course of seven to eight years after a storm. To give context to our findings, we also investigate the effect hurricane strikes have on per capita personal income, per capita wages and salaries, per capita total employment, and population. We find evidence that hurricane strikes reduce overall county level poverty and the number of children in poverty up until one and three years after the initial strike, respectively. We also observe that hurricane strikes increase personal income per capita, and decrease wages and salaries per capita, total employment per capita, and the population in the counties that get hit. Finally, we test the robustness of our results and observe that families around the poverty line may be more vulnerable to hurricane strikes than families in other income groups.
The relationship between an area's income and poverty with the costs that are incurred from natural disasters is well established. Many studies explicitly control for a country's income level and in general find a negative relationship between income and natural disaster vulnerability, damages, and fatalities (Kahn 2005;Anbarci, Escaleras, and Register 2005;Toya and Skidmore 2007;Masozera, Bailey, and Kerchner 2007;Kellenberg and Mobarak 2008). Other studies note the importance of normalizing natural disaster damages by wealth when making comparisons over time (Pielke and Landsea 1998, Brooks and Doswell 2000, Pielke et al. 2003, Pielke et al. 2008. Others investigate the role income has in adaptation to natural disaster damages as countries develop (Nordhaus 2010, Hsiang and Narita 2012, Fankhauser and McDermott 2014, Bakkensen and Mendelsohn 2016. Most studies agree that richer areas are not as negatively impacted by natural disasters as poor areas. While these studies are important for understanding the link between natural disasters and income, there are surprisingly few analyses that examine the direct effect natural disasters have on various poverty, income inequality, and human development measurements (Karim and Noy 2016). Studies that have done so either look at a single environmental event or measure poverty changes at a single point in time. These studies include the effect of El Niño on poverty at the household level in the Philippines (Datt and Hoogeveen 2003), the effect of experiencing a natural disaster on household poverty in Vietnam (Bui et al. 2014), the effect of Hurricane Mitch on people in poverty in the rural areas of Honduras (Morris et al. 2002), and the effect of a drought on poverty and income inequality at the household level in Burkina Faso (Reardon and Taylor 1996). In a study that looks at the dynamic effects of natural disasters, Yamamura (2015) uses a panel of countries to observe changes in inequality over time. Yamamura observes floods increase a country's Gini coefficient up until one year after the occurrence but does not find a dynamic effect for storms and earthquakes.
Very few studies investigate the dynamic effect natural disasters have on poverty measurements within a single country. One study that is most related to this study in that regard is Rodriguez-Oreggia et. al (2013). The authors look at the effect of natural disasters on human development and poverty indices over time at the municipal level in Mexico. Using a two-period panel dataset, the authors use a fixed-effects model to estimate the treatment effect of a municipality experiencing a natural disaster on a human development index and various poverty indices. They find the occurrence of a natural disaster between 2000-2005 reduce the human development index by about 1% and increases poverty between 1.5 and 3.7% depending on the measure.
Unfortunately, their dataset was not rich enough to disentangle the effects of individual natural disaster incidents instead of aggregate natural disaster treatment between 2000-2005. This means their treatment effect estimates could be influenced by events of different magnitudes or multiple natural disaster events hitting the same municipalities over their sample period. Their estimates might also not account for any recovery that happens after natural disasters that occur earlier in their sample. In this study, we overcome these limitations by observing effects on our dependent variables from individual storms, conditioned on past hits, while observing the dynamic effects over seven to eight years after the strike.
The main contribution of this study is to examine the dynamic effects multiple hurricanes have on poverty levels within a country over time. Other studies have looked at the dynamic effect hurricanes on employment and earnings (Belasen and Polachek 2009), government fiscal outcomes (Ouattara and Strobl 2013, Dai 2014, Deryugina 2017), fertility (Evans, Hu, and Zhao 2010), economic and personal income growth (Strobl 2011, Hsiang and Jina 2014, Bakkensen and Barrage 2016, and of a single hurricane on economic impacts (Coffman and Noy 2011). However, to the best of our knowledge our study is the first to measure the effects of hurricanes on poverty levels over time within a single country. We follow in the footsteps of these studies by using a difference-in-differences approach that identifies the within-county variation of poverty levels and other outcome variables over time.

DATA
This section describes the data sources we used for the different parts of our analysis: 1) dependent variables at the county level and 2) hurricane wind model for identifying "treated counties." Data were collected for all coastal counties in the US states that border the Atlantic Ocean and Gulf of Mexico where dependent variables were compared between counties that were hit by a hurricane and those that were unaffected but are geographically close. 1

County Level Dependent Variables
The main dependent variables in our analysis are county level poverty estimates from the Small Area Personal Income and Poverty Estimates (SAIPE). SAIPE reports estimates of the amount of people in poverty of all ages, ages 0-17, ages 5-17, and under the age of five, as well as household median income. Data are reported at school district, county, and state levels for years 1989, 1993, and 1995-2015 To help give context to any observed changes to county poverty levels after a hurricane strike, we also investigate how hurricanes affect county level per capita personal income, wages and salaries per capita, total employment per capita, and population. We collected per capita personal income, wages and salaries, and total employment from the Bureau of Economic Analysis (BEA). From 2005-2014, average per capita personal income in coastal counties was about $40,500, average per capita wages and salaries was about $17,050, and average per capita total employment was about 0.5 (Table 1.1). Population data was collected from the National Cancer Institutes' Surveillance, Epidemiology, and End Results Program (SEER). From 2005-2014, the 2 The US Census Bureau cautions against making year-to-year comparisons between certain years in the SAIPE dataset due to estimations based off different data sources (e.g. estimates based on the Census, Current Population Survey (CPS), or American Community Survey (ACS) surveys). Therefore, we limit our analysis to either years 2005-2014 or 2006-2014 depending on the dependent variable to reduce the probability identified variation in the data is coming from different survey methodologies.
average county had about 213,800 residents (Table 1.1). Again, the coastal counties in our sample have higher values than the national averages for per capita personal income ($37,200), per capita wages and salaries ($14,580), and population (99,220). Average per capita total employment is right in line with the national average of 0.52, however. Extended Best Track Dataset to identify which US coastal counties were affected by hurricanes from 1998-2014. Studies that identify hurricane strikes at a sub-national level in the United States typically either only identify treatment based on the area directly around the storm's eye (e.g. Belasen and Polachek 2007), the radius of maximum wind (e.g. Deryugina 2017) or limits their analysis to hurricanes of category 3 or higher on the Saffir-Simpson scale (e.g. Strobl 2011). This could lead to some counties being misidentified as control units when they could have been affected by hurricanes further outside the radius of maximum wind or hurricane eye or by weaker hurricanes. Instead, we used the RAMMB's Extended Best Track Dataset to estimate a complete wind field to identify the treatment of counties by hurricanes during the sample period. 3

Hurricane Strike Treatment
The Extended Best Tracks Dataset reports the latitude, longitude, maximum wind intensity, and minimum central pressure of the center of tropical cyclones as well as information about the storm structure such as the maximum radial extent of 34, 50, and 64 knot winds in four quadrants at six-hour intervals from 1988-2015. We used the latitude and longitude coordinates of the center of the storm and the reported radial wind distances to approximate the path of a complete wind field through the life of a hurricane 4 . We assumed the storm track and wind quadrant radii are linear between consecutive points and interpolated the storm path and wind strength radii to half hour intervals. We then used ArcGIS to create a hurricane wind field by interpolating between central storm maximum wind measurements and the 34, 50, and 64 knot wind extents. As an illustration, Figure 1.2 shows the complete wind field for the 2005 storm Katrina. We then determined the maximum wind speed each county was exposed to in a given year during our sample and qualified hurricane treatment as a county that was estimated to experience a hurricane strength of at least 64 knots. With our simulated wind fields, we are also able to identify coastal counties surrounding those that are affected by hurricane strength intensity that experience tropical storm strength intensity. 5

METHODOLOGY
To estimate the impact hurricane strikes have on poverty levels in coastal counties, we use a difference-in-differences framework that compares the outcome variables of interest between treatment counties that get hit by a hurricane and unaffected coastal control counties over time. We observe yearly changes in our dependent variables either up to seven or eight years after a hurricane strike due to the dependent variable data restrictions mentioned in Section 1.2. 4 Any missing values for the radial extent of the 34, 50, and 64 knot winds were interpolated based from the minimum central pressure of the storm. 5 Storm classification is based off the Saffir-Simpson scale which considers tropical storms wind speeds to be 34-63 knots and hurricane wind speeds to be above 64 knots.
While observing changes in poverty levels over time, we assume conditional convergence where counties with initially high levels of poverty will decrease faster over time than those with lower levels of poverty. Studies show that there is conditional convergence in global poverty levels (Cuaresma, Klasen, and Wacker 2016) and in personal income among counties within the United States (Higgins, Levy, and Young 2006;James, Harrison, and Campbell 2013). In the context of the effects of hurricanes, we follow Strobl (2011) and use a conditional convergence growth equation for our econometric model. Our model takes the following form: where ℎ( ,( −1)→ ) is the growth rate of the dependent variable for county from time ( − 1) to time , ,( − ) is the maximum wind speed of a hurricane county experienced in a − window, ,( − ) is the maximum tropical storm wind speed county experienced in a − window if they did not experience hurricane intensity, is a county fixed effect, is a time fixed effect, and × is a county-specific time trend. 6 , 7 We perform a log(x + 1) transformation on ,( − ) and , ( − ) in order to preserve the "zero" values of the control coastal counties that neither 6 ℎ( ,( −1)→ ) was calculated as the difference between log ( , ) and log ( ,( −1) ).
experience hurricane nor tropical storm intensity winds from the hurricanes in our sample.
The parameters of interest are the coefficients which show the marginal effect of maximum wind of a hurricane on the growth of our dependent variables in a − window, conditioned on past hurricane strikes. Though they are of secondary importance to , the parameters ( = 0, … , ) serve two purposes in our analysis. First, they allow us to examine and variation in the data between the unaffected control counties and counties that are further away from the hurricane intensity but are still affected by the tropical storm intensity parts of the hurricanes in our dataset. These coastal counties may not sustain the same wind damage of the counties that experience hurricane strength winds, but they still are at risk of flooding which could affect the outcome variables.
Second, counties affected by the tropical storm intensity portion of hurricanes surround the counties that are affected by hurricane intensity. Allowing these counties to have their own slope gives us the opportunity to examine if counties that surround the ones affected by hurricane intensity experience upticks in population or business activities to compensate for those lost in the hurricane stricken coastal counties.
We take careful considerations in our analysis to control for issues that can arise from correlations between geographically close locations and using the same treatment and data to test multiple hypotheses. We use an Ordinary Least Squares estimator and correct the standard errors for spatial and time correlation (Conley 1999, Hsiang 2010. We follow Deryugina (2017) and allow for serial correlation of up to 5 years and spatial correlation between counties of up to 200 km. We also adjust the p-values of our coefficient estimates to reduce the probability of false rejection of null hypotheses across a family of dependent (our outcome variables) and independent variables (the lags associated with hurricane strikes) (Veazie 2006). 8 We adjust the p-values using a free step-down resampling method as outlined in Anderson (2008). 9

RESULTS
We first use Equation (1)

Changes in Poverty After a Hurricane Strike
We find that hurricane strikes dynamically affect county poverty levels in the United States (Table 1.  Counties that miss getting hit by hurricane intensity winds but still get hit by the tropical storm strength winds further away from the eye of the storm also experience changes in poverty levels (Table 1.2 and Figure 1.3). These surrounding coastal counties do not experience the same initial dip in overall poverty as the counties that got hit by hurricane intensity, but they do experience similar increases in poverty levels that hurricane-stricken counties do five and six years after. Coastal counties also seem to experience an initial dip in the number of children in poverty after experiencing the tropical storm intensity winds of a hurricane.
The initial decreases in poverty levels in coastal counties that are affected by hurricanes is a new finding in the literature. Most studies that investigate the effect natural shocks have on poverty and inequality find they decrease human development (Rodriguez-Oreggia et al. 2013), increase poverty (Datt and Hoogeveen 2003), and increase inequality (Reardon and Taylor 1996, Bui et al. 2014, Yamamura 2015 in the areas they occur. To investigate why we observe different poverty outcomes than what is typical in the literature, we observe the effect hurricanes have on other outcome variables.

Changes in Personal Income after a Hurricane Strike
We find that hurricane strikes affect per capita personal income, wages and salaries, and total employment (

Changes in Salaries and Wages and Total Employment after a Hurricane Strike
Per capita wages and salaries (Column 4) and per capita total employment (Column 5) follow a similar trend as personal income per capita by initially increasing after a hurricane strike before decreasing over time. Applied to the means of wages and salaries per capita and total employment per capita from Table 1.1, a one standard deviation increase in the maximum wind speed of a hurricane would increase wages and salaries by about $730 per capita the year of the strike before annual decreases between $440-$1,175 per capita from two to eight years after. Also, total employment per capita would increase between 0.014 and 0.017 jobs per capita up to one year after a hurricane strike before annual decreases between 0.006 and 0.012 jobs per capita between three and eight years after a hurricane strike. Surrounding coastal counties that experience tropical storm intensity winds also experience initial increases in wages and salaries and total employment, though at a lower magnitude, before experiencing decreases later.
The gradual decrease in employment and wages in areas directly hit by hurricanes is consistent with other findings in the literature. Coffman and Noy (2011) find Hurricane Iniki decreased private sector employment in the county that was affected. Belasen and Polachek (2009) find that Florida counties that are directly hit by a hurricane experience an immediate growth in earnings and employment before a downturn. Unlike Belasen and Polachek, we find surrounding counties that experience tropical storm intensity of the hurricanes follow the same general pattern as the counties hit by hurricanes, but at a smaller magnitude.

Changes in Population after a Hurricane Strike
We also find that hurricane strikes affect county level population ( We use a difference-in-differences model, while correcting standard errors for spatial and time correlation, to observe within county variation in poverty levels after a hurricane strike over time.
We find hurricane strikes cause statistically significant changes to poverty at the county level. Results suggest overall county level poverty decreases between 0.5 to 1% for each year from the hurricane strike until two years after and the poverty levels of children between the ages of 5 and 17 decrease between 0.6 and 1.1% for each year from the hurricane strike until three years after. We also show there is somewhat of a "rebound effect" later on where the number of people in poverty and children in poverty increase starting five years after a hurricane hit.
Drawing any broad conclusions from analysis using aggregated data inevitably requires a certain level of ecological inference. With hurricanes also affecting income per capita, wages and salaries per capita, total employment per capita, and population, it is not entirely clear if county poverty levels decrease at first due to spurring business activity involved with initial cleanup or by displacing people that are poor to other counties. Our robustness analysis on how hurricanes affect the income distribution of families in counties that are hit suggests it is the latterperhaps there is a reduction in the number of people and children in poverty because families around the poverty line face more incentive to leave damaged areas to seek employment elsewhere.     Standard errors are shown in parentheses and are corrected for spatial correlation up to 200 km around a county's centroid and time correlation up to 5 years. P-values are further adjusted for multiple hypothesis testing. Controls include county fixed effects, year fixed effects, and a county-year time trend. *, **, and *** indicate statistical significance at the 10%, 5%, and 1% levels, respectively. Standard errors are shown in parentheses and are corrected for spatial correlation up to 200 km around a county's centroid and time correlation up to 5 years. P-values are further adjusted for multiple hypothesis testing. Controls include county fixed effects, year fixed effects, and a county-year time trend. *, **, and *** indicate statistical significance at the 10%, 5%, and 1% levels, respectively. Var. (t-1) -0.734*** -0.972*** -0.916*** -0.924*** -0.912*** -0.941*** -0.917*** -0.923*** -0.945*** -0.903*** (0  Var. (t-1) -0.828*** -0.970*** -0.903*** -0.929*** -0.919*** -0.938*** -0.935*** -0.927*** -1.027*** -0.930*** (0 strategies will need to be enacted at both the individual and community levels and depend on supportive and engaged voters and stakeholders to be effective. We test whether storm experience increases the attention a common cost mitigating strategy is given in a panel of media markets. We find that tropical storm and hurricane strikes cause statistically significant positive and dynamic changes to the relative internet search popularity of flood insurance in the areas they affect. We believe these results are useful to policymakers that want to take advantage of a window of opportunity to propose environmental damage mitigating policies where people are more engaged and willing to learn about mitigation measures soon after experiencing a storm.

INTRODUCTION
Every  Atreya et al. 2015). This low market penetration rate has been one of the primary reasons why the relationship between weather and events and flood insurance preferences has been studied extensively in the literature.
We examine this relationship from a different perspective than the previous literature. While exploring the determinants of flood insurance purchases is undoubtedly valuable at a time when extreme weather events cause billions of dollars in costs, there are disadvantages to conclusions drawn from studies that examine people's willingness to pay for flood insurance in contingent markets (e.g. Botzen et al. 2009, Botzen et al. 2013, Raschky et al. 2013 or insurance purchasing patterns following weather events (e.g. The use of Google Trends data in our context allows us to examine if public attention shifts to future cost mitigating strategies, like information seeking behavior about flood insurance, after experiencing a weather event. We are able to measure changes of attention in a cost mitigating strategy relative to all other searched topics, regardless if the individuals seeking information can afford insurance or not, and for how long this attention is maintained for. We believe this information is useful to policymakers that want to know if there is an optimal time period (window of opportunity) after an environmental event to propose individual or community level mitigating actions against future environmental damages.

DATA
This section describes the two data sources used in our analysis: 1) Google Trends data used as the dependent variable, and 2) Storm data used to identify hurricane and tropical storm treatment of DMAs.

Google Trends Data
We use Google Trends data for aggregate searches for the term flood insurance as the dependent variable in our analysis. Google Trends is a service provided by Google Inc. that allows users to analyze the search activity of words or phrases over a specified time frame in the form of a relative popularity index. This index shows how often a word

Storm Treatment Data
Since our dependent variable is observed at the DMA-month level, we define storm treatment as the maximum intensity a DMA experiences each month from tropical storms and hurricanes. We follow the methodology of Prendergast and Uchida (2018) and

METHODOLOGY
To estimate the impact hurricane and tropical storm strikes have on Google Trends search data, we use a difference-in-differences framework that compares the search volume of flood insurance between treatment DMAs that get hit by hurricanes and tropical storms and unaffected DMAs over time. We observe monthly observations of our dependent variable for each DMA and estimate storm treatment effects up to one year afterwards. Our econometric model takes the following form: where , , is the relative search rate for searches related to "flood insurance" in DMA for month in year , ,( − ) is the maximum wind speed that DMA experiences in an − window, is a DMA fixed effect, is a month fixed effect, and is a year fixed effect. We test the robustness of coefficient estimates using different combinations of month and year fixed effects, which is why they are expressed as a function in the Equation (1). We perform a log(x + 1) transformation on ,( − ) in order to preserve the "zero" values of the months when a DMA does not experience a storm. The parameters of interest are the coefficients which show the marginal effect of maximum wind of a storm on the monthly relative search volume of flood insurance in a − window.
We also investigate whether there is heterogeneity in the effect storm strength has on Google search share by testing whether hurricanes and tropical storms have differing effects. Our second econometric model takes the following form: We perform multiple regressions to identify storm treatment effects on Google searches for flood insurance. Models (1) and (2)  increase in maximum wind of an average storm of 46.83 knots translates to an overall level of relative flood insurance search volume between 10.5 and 11.1 points during the month of and two months following a storm strike (using coefficient estimates from Column 3).
Table 2.2 also shows some interesting dynamic results further down the line after a storm hits. After months of no discernible effect on the flood insurance search index, there are statistically significant and robust coefficient estimates 11 to 12 months after a storm strike. This may seem curious at first, but the seasonal nature of hurricane and tropical storm activity may explain the pattern of treatment effects shown. The coefficient estimates between the concurrent month and up to two months after a storm strike shows that people that directly experience a tropical storm or hurricane may be interested in things like the availability and price of flood insurance in their area for a short time period after as a reaction to that experience. The positive coefficients at the 11 and 12month time lags show that after people experience a storm, they may be anticipating the consequences of an upcoming hurricane season by searching for information about flood insurance. Unfortunately, we do not have the data to test whether this later uptick in relative search activity is an artifact of individuals that experience flooding from a previous storm, or if interest is driven by media coverage of the fallout of a tropical storm or hurricane near the anniversary of the event.

The Effect of Storm Heterogeneity on Flood Insurance Search Volume
The results presented from Equation (1)  DMAs that experience storms. Coefficient estimates also follow intuition that hurricanes have a larger impact on search volume than tropical storms do. On average, a hurricane will increase the flood insurance search index between 13.4 and 16.9 points in a DMA during the month of the strike and between 10.9 and 14 points in the following month.
Tropical storms, on the other hand, increase relative search volume between 2.9 and 4.3 points during the month of a strike, on average, and between 2 and 2.3 points the following month (although the coefficient estimate is not statistically significant in Column (3) that uses month-year fixed effects). Interestingly, results still show statistically significant longer lags, but mainly with the tropical storm dummy variables.  (1) and Equation (2)  although the results are not as robust as they were in Table 2.4.

Coastal DMA Analysis
Results for the heterogeneity of storm effects on search activity is presented in and 2.5 points in the following month. Again, there are signs that people in DMAs that experience a tropical storm may be anticipating the consequences of future storms 11 and 12 months afterwards (although the coefficient of the 12-month lag is not statistically significant in the model that uses month-year fixed effects).

Comparison of Results with Related Studies
Although we are the first to examine the effect of tropical storm and hurricane treatment on the relative popularity of flood insurance Google searches, it is informative to compare our results with studies that used similar settings. In a study that looks at how

CONCLUSION
A growing literature has been using Google Trends search activity as a "revealed preference" for environment and climatic concerns (    Observations are at the DMA-month level. DMA Google search share of queries that include flood insurance is the dependent variable and a log transformation of monthly maximum wind strength with lags are the independent variables. *, **, and *** represent statistical significance at the 10%, 5%, and 1% levels, respectively. Observations are at the DMA-month level. DMA Google search share of queries that include flood insurance is the dependent variable and dummy variables indicating hurricane and tropical storm strength wind strikes with lags are the independent variables. *, **, and *** represent statistical significance at the 10%, 5%, and 1% levels, respectively. Observations are at the DMA-month level. DMA Google search share of queries that include flood insurance is the dependent variable and a log transformation of monthly maximum wind strength with lags are the independent variables. *, **, and *** represent statistical significance at the 10%, 5%, and 1% levels, respectively. Observations are at the DMA-month level. DMA Google search share of queries that include flood insurance is the dependent variable and dummy variables indicating hurricane and tropical storm strength wind strikes with lags are the independent variables. *, **, and *** represent statistical significance at the 10%, 5%, and 1% levels, respectively.

Appendix 1: Supplemental Analysis for Manuscript 2
This appendix provides information and analysis that supplements the analysis done in the main paper.
As discussed in the main paper, Google Trends search activity data for flood insurance is censored at zero for geographies where the raw number of searches for the population does not exceed an undisclosed threshold. With many zero values, logical estimators to use in our analysis could be the negative binomial or the tobit model. We are interested in within DMA variation over time, however, and the use of negative binomial and tobit estimators in panel data settings are controversial. For completeness, we present results from negative binomial and tobit models that included the full set of fixed effects that we use in the main analysis but refrain from exact interpretation of coefficients or marginal effects. Instead, we focus on coefficient direction and significance.  (3) present results using negative binomial models and Columns (4) to (6) present results using tobit models. Results confirm those found in the main paper. Both sets of models show positive and significant treatment effects during the month of the storm strike until one month after. The tobit models also show robust evidence that flood insurance interest also increases leading up to the one-year anniversary of a storm strike. Table A1.2 serves as a robustness check to Table 2.3 in the main text that examines the heterogeneity of the effect of storm strikes on flood insurance search activity for all DMAs in the sample by separating storms into discrete indications of whether they were hurricanes or tropical storms. Columns (1) through (3) present results using negative binomial models and Columns (4) to (6) present results using tobit models. Results confirm those found in the main paper. Both sets of models show positive and significant treatment effects for hurricane strikes during the concurrent month until one month after. Both sets of models also show positive and significant treatment effects for tropical storms, although the magnitudes are smaller than for hurricane strikes.  (1) to (3) are from three separate negative binomial regressions while results in columns (4) to (6) are from three separate tobit regressions. Observations are at the DMA-month level. DMA Google search share of queries that include flood insurance is the dependent variable and a log transformation of monthly maximum wind strength with lags are the independent variables. *, **, and *** represent statistical significance at the 10%, 5%, and 1% levels, respectively.  (1) to (3) are from three separate negative binomial regressions while results in columns (4) to (6) are from three separate tobit regressions. Observations are at the DMA-month level. DMA Google search share of queries that include flood insurance is the dependent variable and a log transformation of monthly maximum wind strength with lags are the independent variables. *, **, and *** represent statistical significance at the 10%, 5%, and 1% levels, respectively.

INTRODUCTION
One of paramount roles of government is the provision of public goods. In the United States, there are 30,000 municipal governments, and nested on top of that are county, state, and federal governments. When multiple governments can provide the same or similar public good, it is critical to understand if governments behave strategically with respect to other governments' actions. A wide variety of research focuses on how competition can cause government entities to react to the public good decisions of others which in turn affects the overall provisioning of public goods including charitable donations (Heutal, 2014), public school inputs (Millimet and Rangaprasad, 2006), and property tax rates (Bruickner and Saavedra, 2001) The overall production of conservation goals depends on, in part, the size and connectivity of conservation lands. The way governmental conservation agents react to the actions of other agents in conservation provisioning decisions holds implications for how successful we are at protecting our natural resources, supplying ecosystem services, providing outdoor recreational opportunities, and maintaining a representative sample of the full variety of biodiversity (Margules and Pressey 2000). In this paper, we test whether the passage of a conservation referendum in a municipality affects state level conservation activity in that and surrounding municipalities. We also test if there are spatial spillover effects among municipalities where local government activity influences the local government conservation activity of surrounding municipalities.
We build a panel dataset of conservation activity of multiple agents for Massachusetts and New Jersey. Both Massachusetts and New Jersey have state programs the Community Preservation Act for Massachusetts and Green Acres for New Jerseythat incentivize municipal land conservation. This makes Massachusetts and New Jersey ideal places to study because of their substantial amount of conservation activity and available data. We collect state level conservation spending for Massachusetts from the Conservation Almanac and local government conservation referendum activity for Massachusetts and New Jersey from the Trust for Public Land, both at the municipal level.
Since residents vote on local government conservation referendums, we utilize the regression discontinuity (RD) framework developed by Cellini et al. (2010) to test whether the relationship between conservations agents among different levels of government and across space are causal. 17 Past studies in the conservation literature that test for spillovers of conservation activity typically use models that rely on correct 17 Cellini et al. (2010) study how housing prices respond referendums authorizing school infrastructure spending in California. The dynamic RD method has been applied in a handful of papers since (e.g., Isen 2014, Martorell et al. 2016. Lang (2018) uses the same open space referendums data in this paper and examines housing price responses to authorization of conservation spending. covariate selection to produce unbiased results (see Parker andThurman, 2011 as examples). Omission of key covariates in these instances may lead to results that are indicative of correlations instead of causal relationships. We believe we are the first to use a causal framework that controls for both observed and unobserved municipal characteristics to estimate conservation spillover effects that do not suffer from omitted variable bias. To highlight the importance of using a causal framework such as the dynamic RD model, we also produce cross-sectional (XS) and difference-indifference (DID) estimates and contrast results.
Results from the dynamic RD framework suggest there is not a causal relationship between municipal level conservation referendum activity and state level conservation in the municipalities that pass conservation referendums and neighboring municipalities.
We also do not find a causal relationship between municipal level conservation referendum activity among neighboring municipalities in both Massachusetts and New Jersey. There are two main implications of our findings. First, municipal governments may not need to be concerned about whether their conservation referendum activity crowds-out state level conservation and neighbor municipality conservation referendum activity in their town and surrounding areas. Conversely, they should not expect the state and surrounding municipalities to crowd-in additional conservation land in the area after a conservation referendum passage. Second, land conservation provisioning may be at an efficient level where surrounding towns do not need to compete with their neighbors through the allocation of conservation areas in order to attract residents. Our main results differ with results we obtain from XS and DID estimates, which show positive and statistically significant crowding-in effects between local and state conservation activity, as well as neighboring conservation activity. We interpret these differences as evidence of bias in the XS and DID estimates.
We contribute to the literature in two important ways. First, we believe we are the first to investigate whether the actions of conservation agents at different levels of government affect each other. Many papers in the public finance literature have investigated the dynamics between different levels of government in the context of setting consumption taxes (Besley and Rosen 1998), income and wealth taxes (Brülhart and Jametti 2006), and funding decisions for public schools (Cascio et al. 2013).
Prominent papers in the land conservation literature have analyzed the effects public conservation activity has on private conservation activity (Parker and Thurman 2011;Albers, Ando, and Chen 2008;Lawley and Yang 2015). We extend this idea and test whether there is a reactionary dynamic between local and state governments when it comes to land conservation activity because such reactions can hold important implications for conservation efficiency.
Second, we use a causal framework to investigate the relationships between conservation agents instead of investigating spatial correlations that previous studies have identified. According to the public finance literature, public good decisions by a local government may cause a reaction to neighboring local governments because people can choose to move to a community with a level of public goods that fit their preferences (Tiebout 1956) or voters may judge their public officials based on the tax performance of politicians in surrounding areas in what is referred to as a yardstick competition Case 1995, Bordignon et al. 2003). In addition, spatial spillovers often result due to strategic competition between neighboring jurisdictions when setting property tax rates (Brueckner and Saavedra 2001), school inputs (Millimet and Rangaprasad 2006), and other public finances (Baicker 2005, Isen 2014. Similarly, studies in the land conservation literature find evidence of spatial clustering between conservation agents and voting outcomes (e.g., Albers and Ando 2003, Heintzelman et al. 2013, Altonji et al. 2016), but tend not to make causal claims either due to dataset limitations or the scope of the study.
We aim to add to the valuable insights provided by the land conservation literature by analyzing a novel dataset that allows us to identify conservation activity spillover effects in a quasi-experimental manner. We do not find evidence of the positive spillover effect between conservation agents that many studies find.

DATA
This section describes the four sources of data used in our analysis: 1) municipal level referendums and associated spending, 2) state government conservation spending, 3) land use characteristics, and 4) municipal demographics.

Land Conservation Referendum Data
Land conservation referendum data come from The Trust for Public Land's LandVote Database (The Trust for Public Land, LandVote, 2016) and spans the years 1996-2016. The data include proposed municipal level referendum information such as date, financial mechanism, total funds at stake, total funds approved, conservation funds at stake, conservation funds approved, as well as percentage of yes and no votes. Tables   Massachusetts, there appears to be spatial patterns of referendum activity in New Jersey with activity being concentrated to the northern and western part of the state. Our analysis will allow us to determine if the spatial clustering of conservation referendum activity is caused by municipalities reacting to the conservation activity of their neighbors or is a function of observable and unobservable population characteristics that are spatially correlated.

State Conservation Spending Data
Due to data availability, we are only able to observe historical state conservation By comparing state conservation and referendum activity, we can get an initial assessment of how municipal and state conservation actions relate to one another.
Referendum activity appears to have a few distinct pockets with a lot of activity in the entire eastern part of the state, where state spending is sparse, and a smaller concentration in the western part of the state right before the highest concentration of state spending.
Visually, there seems to be a substitution effect of conservation vehicle where state conservation spending reacts to municipality referendum activity by increasing spending in municipalities that do not hold referenda or vice versa. 20 This may lead to the conclusion that referendum activity crowds-out state conservation spending where Massachusetts conservation funds are focused on communities that may not have the resources or support to conserve on their own. Our main analysis allows us to investigate whether this relationship is causal.

Land Use Data
Municipalities that hold referendums are matched with land cover control variables. Acres available in each municipality for open space is calculated using GIS and the National Land Cover Database (NLCD) (Homer et al., 2015). The NLCD creates a

Demographic and Partisanship Data
Finally, municipalities that hold referendums are matched with municipal level socioeconomic data from the 2000 Census, 2010 Census, and 2010 American Community Survey. We collect data on municipal level median household income, population density, median house price, and proportion of residents under 18, over 65, white, black, and with a bachelor's degree or higher. Sociodemographic values were interpolated for years between 2000 and 2010 and extrapolated for years before and after.
We use presidential election outcomes as a proxy for political ideology. For Massachusetts, we gathered results for each election at the municipal level between 1996 and 2016 from the Elections Division of the Secretary of the Commonwealth. For New Jersey, the same data was only available between 2004 and 2016 (from the Division of Elections). With this data, we calculate the Democrat share deviation, which equals the share of votes the Democrat candidate received in a given municipality minus the statewide Democrat vote share. This measurement accounts for changing candidate popularity and provides a better accounting of changes to partisanship over time (Lang and Pearson-Merkowitz 2015). As with census data, we interpolate Democrat share deviation for years between elections.

Links Between State and Local Conservation Activity
An important assumption in our analysis is that locally raised conservation funds and state conservation spending by state departments like MDAR, DCR, and DFG can be either complements (that could crowd-in each other) or substitutes (that could crowd-out each other). If the types of conservation projects that each funding source typically supports are not related to each other at all, then we would expect to see insignificant estimation results regardless of the appropriateness of methodology used. Massachusetts municipalities that adopt the Conservation Preservation Act (CPA) are incentivized to fund projects that preserve open space, affordable housing, historical sites, and recreation. Completed projects have funded agricultural preservation, bike trails, fish ladders, shellfish population preservation, among many others. 21 There are no overt policy mechanisms that link voting behavior to state spending or neighboring municipality activity. There is very limited information about the motivations of individual towns. The Land Vote database provides the wording that is listed on the ballot and does not indicate explicit coordination with neighboring towns or with the state spending activity that we observe. Because of this, we fundamentally view municipal referendums as discrete activities between municipalities rather than coordinated. At the state level, however, we do see evidence of coordinated efforts in the Conservation Almanac dataset. For example, the state may partner with the federal U.S. Fish and Wildlife and a municipality to purchase a land easement. In the end, however, it is unclear if state efforts are attracted or repulsed by municipal efforts in a causal way. We believe projects funded by towns using the CPA are related enough to what state departments MDAR, DCR, and DFG would focus on that it is plausible to test for crowding-in or crowding-out activity, and this is ultimately an empirical matter.

Outcome Variable Construction
To assess the effect that municipal open space conservation has on other government decision making, we construct and test empirical models with four different outcome variables. The first outcome variable is the amount of state government conservation spending per capita in the municipality that passed the referendum. To form this variable, we sum state level spending for each municipality by year and normalize it by population. The second dependent variable is state government spending per capita in neighboring municipalities. To form this variable, we calculate annual state level conservation spending per capita and then calculate a weighted average of all municipalities that share a border with a given municipality with weights proportional to the length of border in common. 22 The third dependent variable is the number of open space referendums passed by neighboring municipalities. The last dependent variable is the amount of open space funding per capita approved by referendums held by 22 The intuition behind this construction is that there is more likely to be strategic behavior between municipalities that share a longer border. Results are qualitatively similar with different weights. neighboring municipalities. Both of these neighbor averages are similarly weighted by length of border.

Dynamic Regression Discontinuity Model
We begin with a simple model and build up to our preferred specification in order to build intuition. We are interested in whether municipal conservation decisions have any effect on state and neighboring municipality conservation decisions. We observe municipality j hold an open space referendum, and the measure passes if the vote margin, which equals the percent approval minus the percent required to pass, is greater than zero, i.e., = 1 if > 0. We also observe our four outcome variables for government i that is linked to municipality j, denoted . Government i can be the state government or a municipality that neighbors j. A simple bivariate regression of the outcome on referendum passage would be: Since voting outcomes are correlated with observable and unobservable municipality characteristics that are also likely correlated with state and neighbor actions, it is likely that ̂ will be biased.
This endogeneity problem can be mitigated by applying the RD framework originally proposed by Thistlethwaite and Campbell (1960) that takes advantage of the continuous nature of vote margin. By flexibly controlling for the vote margin, we can essentially compare outcomes just below the passing threshold (the control group) and just above (the treatment group) where both observable and unobservable characteristics of municipalities holding referendums are most likely very similar. Transforming Equation (1) into an RD model, we get: where (•) is a flexible polynomial and signifies the corresponding parameter. We use a cubic polynomial of vote margin in our main analysis, but also present results with linear and quadratic polynomials in the online appendix as a robustness check. 23 Comparing outcomes for municipalities that are just below and just above the threshold results in a quasi-experiment where referendum passage is as good as randomly assigned, and the causal effect of referendum passage on other government conservation spending can be isolated. Election outcomes in an RD framework have been used to examine causal relationships between incumbency and election advantage in the House of Representatives (Lee, 2008), electoral support and legislator's voting behavior (Lee et al. 2004), political party affiliation and land use policies (Solé-Ollé and Viladecans-Marsal, 2013), legislator partisanship on city policing and fire protection expenditures (Gerber and Hopkins, 2011), and the spillover effects of incumbency in mixed election systems (Hainmueller and Kern, 2008).
While RD is a powerful research design for causal inference, we must further modify Equation (2) for this specific setting. Municipalities can and do hold more than one referendum, which necessitates incorporating dynamics into the model. Following the model developed by Cellini et al. (2010), we implement a dynamic RD estimator that conditions treatment effects on other referendums a community has held. Our preferred specification is: 23 Gelman and Imbens (2014) argue that high order polynomials can lead to biased inference and should be avoided. We chose to use a cubic polynomial in our main specification because Cellini et al. (2010) and Lang (2018) use a cubic in similar setting. We admit this is ad hoc, which is why we present estimates using linear and quadratic polynomials in the online appendix (Tables A3 and A4). Results are similar regardless of polynomial order choice.
where t indicates the year of observation, is the number of years since a referendum, , − is a binary indicator for municipality j passing a referendum years prior to year t, , − is a binary indicator for municipality j holding a referendum (this acts as an intercept to separate municipalities that do versus do not hold referendums in a given year), is a municipality fixed effect, and is a year fixed effect. Additionally, this specification allows the polynomial in vote margin to vary across lagged years. By controlling for the vote margin, past referendum activity, and municipality and year fixed effects in Equation (3), no longer suffers from the endogeneity problem that plagued Equation (1) and is interpreted as the causal effect that passing a conservation referendum has on another government years after the referendum is passed for municipalities that are near the vote margin threshold. Additionally, Equation (3) models time paths of government responses. Conserving land parcels or placing items on the ballot is not immediate, and thus the effect may be delayed or heterogeneous over time. 24

REGRESSION DISCONTINUITY DIAGNOSTICS
The RD framework aims to replicate the identification of treatment effects from randomized experiments in settings where treatment is not randomly assigned. This is done by focusing regression analysis to observations just below and just above an arbitrary threshold where treatment assignment is as good as randomized due to the 24 In the context of U.S. state capital tax policy, Chirinko and Wilson (2017) find that a dynamic specification is critical for understanding strategic responses. similarity of observation characteristics and the inability of observations to affect the treatment outcome.
The key identifying assumption of the framework is the continuity of the conditional expectations of counterfactual observations below and above the threshold.
This assumption may not be valid, however, if observations can manipulate their treatment status. Though very unlikely in our setting where municipalities use thousands of votes to determine the passage of a referendum, we can test for manipulation in a few ways. One way is to look at the density of observations around the threshold. If municipalities cannot manipulate their treatment status, we would expect a relatively smooth density of observations across the passage threshold. Another way is to analyze the similarity of municipality characteristics around the passage threshold. Municipalities can be similar in observable and unobservable ways. Although it is impossible to explicitly test for similarities in unobservable characteristics, we can compare observable municipality characteristics for municipalities that fail a referendum and municipalities that pass a referendum.   percentage of population that is black, population density, number of acres that are available for conservation, and median house price. Column 3 shows the results of a t-test between the means presented in Columns 1 and 2. There is a statistically significant difference between the two groups of municipalities when it comes to the percentage of population over the age of 65, the proportion of populations that have a bachelor's degree or higher, and Democrat share deviation.

Sociodemographic Balance
RD makes a comparison at the threshold, and it is most important that there is balance, and hence no manipulation, at that point rather than across the whole distribution. Lee and Lemiuex (2010) suggest a way to test this balance, which is to estimate the RD model with the sociodemographic variables as the dependent variables and inspect for discontinuity at the threshold. Since we have many covariates, we follow Lee and Lemiuex's suggestion to perform a chi-squared test for the discontinuity to be zero for all covariates after running a Seemingly Unrelated Regression (SUR). Column (4) of Table 3.1 shows the results of the SUR model where each sociodemographic variable is a dependent variable with a dummy variable indicating a passed referendum and a cubic polynomial for vote margin as the independent variables. Individual coefficient estimates for the pass dummy variable are mostly not statistically different than zero, with the exception of proportion over age 65 (at the 10% level). However, a postestimation Chi 2 test does not allow for the rejection of the null hypothesis that each of the coefficients are equal to zero. Together with the results of the vote margin manipulation test, we are comfortable proceeding with the RD framework to analyze Massachusetts referendum data. Table 3.2 repeats the same columns as in Table 3.1, but for New Jersey. Democrat share deviation is not included because those data are only available 2004 and after, which removes about one-third of observations. Column (3) shows that there are statistically significant differences in means between towns that have ever failed a conservation referendum and those that have ever passed a referendum in the proportion of population under the age of 18 and median house price. Estimation results of the SUR model in Column (4) show a statistically significant discontinuity for the proportion of the population over the age of 65, but the Chi 2 test shows the same conclusions as those for Massachusetts. This suggests we can use a RD framework to analyze New Jersey referendum data as well.
The strength of the regression discontinuity design is that it eliminates the endogeneity issue of omitted variable bias by analyzing outcomes in a way that makes variation in treatment exogenous. Omitted variable bias is not the only contributor of endogeneity, however. Reverse causality is also a concern for endogeneity in econometric settings. In our context, reverse causality would be a concern if regression results were being driven by the influence of state activity or neighbor conservation activity on a municipality passing a referendum instead of the other way around.
Although regression discontinuity does not explicitly control for reverse causality (which is typically addressed through instrumental variables), we are not worried about it in our analysis due to the exogenous nature of treatment assignment in the regression discontinuity setting.
Reverse causality may be a concern in our setting if our dependent variables are influencing where towns fall on the vote margin spectrum. By analyzing treatment effects in a small neighborhood around the referendum passage threshold where municipalities are similar in observable and unobservable ways, the independent variables in our model are unlikely to be influenced by the dependent variables. We have already shown that town demographic characteristics do not influence vote margin outcomes around the passage threshold using SUR models. In the appendix, we use the same approach to show that prior state and neighbor conservation activity is not influencing referendum passage among municipalities close to the threshold, diminishing concerns of reverse causality.  reported in the online appendix and have similar coefficient variation and standard errors.

RESULTS
We proceed cautiously with the interpretation that there is no causal effect of municipal conservation on other governments' actions.

TESTING THE IMPORTANCE OF THE RESEARCH DESIGN
To better understand the importance of our dynamic RD modeling strategy, we also estimate cross-sectional (XS) and difference-in-differences (DID) models that address the same questions, and then we compare the results to our preferred results to assess bias in XS or DD models. The DID model analysis is performed on the same dataset as the dynamic RD model. The specification does not control for the referendum vote margin, but is otherwise identical to Equation (3), namely the specification still conditions on past referendum activity to account for municipalities that hold more than one referendum. For the XS analysis, we sum our outcome variables across years and the independent variable of interest is a binary indication of whether the municipality passed at least one conservation referendum over the whole time period. In the XS specification, we lose municipality fixed effects, but instead include a rich set of socioeconomic variables that are averaged across years. When the outcome variable measures actions taken in a neighboring municipality, the socioeconomic variables are averaged across neighbors, using the same weights (border length) as the dependent variable construction (see Section 3.1). Lastly, for the XS model, we include all municipalities, not just those that hold a referendum, though results are similar if we do not expand the sample in that way. and New Jersey (columns 5-6). All models regress the outcome variable (identified at the column header) on an indicator for referendum passage and a suite of socioeconomic variables.

Cross-Sectional Analysis
Columns 1 and 2 of Table 3 Table 3.5 presents regression results from the DD analysis for Massachusetts (columns 1-4) and New Jersey (columns 5-6). Columns 1-2 of Table 3.5 estimate the dynamic relationship between passing a conservation referendum and the amount of state conservation expenditure in the municipality that held the referendum and neighboring municipalities. These results have both positive and negative coefficients, and most are insignificant. Columns 3-4 show positive and statistically significant coefficients in the concurrent year, as well as a lag of seven years, which indicates some support for a crowd-in effect for neighboring municipalities. This finding is bolstered and more pronounced in New Jersey (columns 5-6), which shows positive and statistically significant coefficients in the concurrent year through a four year lag.

Comparison to the main results
The main results using the dynamic RD indicate that no causal effect of municipal open space referendums on other government conservation actions. The intuitive appeal of the dynamic RD model is that it controls for time-invariant and time-varying unobservables, which could lead to biased inference if not controlled for. However, the extent of bias is an empirical question for this given setting.
Both the XS and DD models do not find evidence of municipal actions affecting state actions in the municipality that holds a referendum, the same conclusion as the dynamic RD. Thus, in this case, we find no evidence of bias in this setting.
In contrast, XS and DD models do find evidence that municipal actions positively affect neighboring state and municipal actions, whereas the dynamic RD models indicated no effect. We interpret these differences as evidence of bias in the XS and DID estimates. We hypothesize that the XS and DD results reflect spatial correlations that are not adequately captured by socioeconomic control variables or municipality fixed effects.
Supporting this idea, the DD models estimate a statistically significant positive effect in the concurrent year, which is near impossibly causal given that it takes time to strategically respond.

CONCLUSION
We use local government conservation referendum data from Massachusetts and New Jersey, two states with land conservation incentive programs, as well as state government conservation spending data from Massachusetts, to investigate the relationship between public conservation agents at different levels of government and across space. Using a RD framework, our results suggests there is not a causal relationship between the conservation referendum activity of local and state governments as well as between neighboring local governments.
By investigating whether there are spillover affects among public conservation agents at different levels of government and neighboring governments, we make two main contributions to the literature. First, we believe we are the first to investigate whether conservation agents in different layers of government react to each other. Prior literature investigates externalities between different levels of governments for other public goods, but not for land conservation. Second, our methodology allows us to investigate these relationships between public conservation agents in a more causal manner than what has been done in the past.
As urban sprawl in the United States continues to damage biodiversity and natural resources, communities can use land conservation as a tool to curb urban sprawl. The types of agents involved in conservation and how they react to each other will determine how efficient conservation actions will be. Our empirical setting is unique in that extensive municipal conservation voting allows for causal identification, however this may impact external validity. We choose to study two states that have state-level incentives for municipalities to take conservation actions. Results found here may not 90 hold in states without these types of policies. One could imagine that state-level policies increase positive responses because municipalities face the same incentives and their state institutions see conservation as a priority. On the other hand, municipalities in states without conservation incentives may, in the face of scarcer resources, be more proactive in building off of neighbors' actions to enhance conservation benefits. Future research that examines states without strong land conservation incentive programs or uses a causal framework to examine the relationship between public conservation agents and private land trusts can also aid in the understanding of the efficiency of land conservation provisioning.     (4) are from seemingly unrelated regressions where the error terms are assumed to be correlated between individual regression equations where municipality demographics were the dependent variable and the exogenous explanatory variables were a dummy variable for a passed referendum and a cubic vote margin polynomial. Coefficient estimates for the pass dummy variable are shown. *, **, and *** indicate statistical significance at the 10%, 5%, and 1% levels, respectively.  (3) are from t-tests between municipalities that have ever failed a conservation referendum and municipalities that have ever passed a referendum. Demographic data is for the year the referendum was held. Values were interpolated/extrapolated from the 2000 Census and 2010 Census or ACS, NLCD database for 2001 and 2011. Results for Column (4) are from seemingly unrelated regressions where the error terms are assumed to be correlated between individual regression equations. Municipality demographics were the dependent variables and the exogenous explanatory variables were a dummy variable for a passed referendum and a cubic vote margin polynomial. Coefficient estimates for the pass dummy variable are shown. *, **, and *** indicate statistical significance at the 10%, 5%, and 1% levels, respectively.  Notes: Each column is a separate regression where the independent variables include a dummy variable indicating whether a municipality passed at least one referendum and municipality or neighbor demographic variables. "Own" demographic characteristics are the demographic variables for the municipality that holds a referendum averaged over the years indicated. "Average neighbor" demographic characteristics are the average of demographics variables of towns that border the municipality that holds a referendum, weighted by border length. Standard errors are shown in parentheses. *, **, and *** indicate significance at the 10%, 5%, and 1% levels, respectively.

Appendix 2: Supplemental Analysis for Manuscript 3
This appendix provides supplemental figures, statistics, and results to our main paper. Figure A2.1 shows Massachusetts referendum activity from 2008 to 2011 for a more direct comparison to our state spending data. The map looks almost identical to Studies that use RD in their analysis typically present RD plots that fit separate lines to the relationship between a running variable, such as vote margin, and the dependent variable in question below and above a threshold to show the discontinuity in the outcome variable that results from treatment. While this is a good practice to build intuition for interpreting statistically estimated results, it is harder to do in our situation where a dynamic framework would call for multiple plots across time. The use of municipality and year fixed effects in our model further complicates the visualization of the relationships we estimate in one graph. Regardless, we present RD plots which are more akin to cross-sectional results than dynamic results for Massachusetts and New Jersey referendums that were held in the previous year in Figure A2.2.  Table A2.3 serves as a robustness check to Table 3.3 in the main paper by controlling for different vote margin polynomials for Massachusetts. In general, these regressions confirm the insignificant results found with a cubic polynomial. The regressions that use a linear polynomial of vote margin show positive and significant crowding-in results for neighboring conservation activity 1-2 years after a passed referendum, but this result is not robust to controlling for quadratic and cubic vote margin polynomials. Table A2.4 serves as a robustness check to Table 3.3 in the main paper by controlling for different vote margin polynomials for New Jersey. Controlling for linear and quadratic vote margin polynomials do not reveal any statistically significant results other than a significant coefficient for neighbor referendums passed two years after at the 10% level. This estimate is not robust to controlling for linear and cubic vote margin polynomials, however.  Table A2.7 serves as a test of reverse causality in the dynamic regression discontinuity setting. If our dependent variables are influencing treatment status, then we would expect to see prior state and neighbor conservation activity to influence municipality vote margins around the threshold. To test this, we use SUR models to see if there are discontinuities between towns that barely fail and barely pass a conservation referendum based on prior (and concurrent year) state and neighbor conservation activity.
SUR models for each state are the same models run in Table 3.1 for Massachusetts and Estimates for Massachusetts show that there are statistically significant discontinuities between municipalities that barely fail and barely pass conservation referendums based on the number of referendums passed by their neighbors during the year a municipality holds a referendum (Column 1) and the number of referendums passed by their neighbors the year before the municipality holds a referendum (Column 2). A postestimation Chi 2 test does not allow for the rejection of the null hypothesis that each of the coefficients are equal to zero, however. A similar story is seen with New Jersey where there is a statistically significant discontinuity between municipalities that barely fail and barely pass a conservation referendum based on the amount of conservation funds passed by their neighbors during the year they hold a referendum (Column 4). A postestimation Chi 2 test does not allow for the rejection of the null hypothesis that each of the coefficients are equal to zero, as well.  Yes Notes: Each column is a separate regression. Standard errors are shown in parentheses and are clustered at the municipality level. *, **, and *** indicate statistical significance at the 10%, 5%, and 1% levels, respectively. Notes: Each column is a separate regression. Standard errors are shown in parentheses and are clustered at the municipality level. *, **, and *** indicate statistical significance at the 10%, 5%, and 1% levels, respectively. Notes: Each column is a separate regression. Standard errors are shown in parentheses and are clustered at the town level. *, **, and *** indicate significance at the 10%, 5%, and 1% levels, respectively. Notes: Each column is a separate regression. Results are from seemingly unrelated regressions where the error terms are assumed to be correlated between individual regression equations where municipality demographics were the dependent variable and the exogenous explanatory variables were a dummy variable for a passed referendum and a cubic vote margin polynomial. SUR regressions include the same municipal demographic variables that were included in Table 3.1 and  Table 3.2 in the main text.

CONCLUSION
Communities in the United States have a complex relationship with the environment.
For instance, if a municipality has been experiencing rapid development, they could conserve land around the municipality to curb urban sprawl. However, this may cause a "free-rider" problem where surrounding towns are less likely to conserve land on their own and consequently miss out on the ecological benefits of connected conservation land. Another example is the physical threat that counties along the East Coast and Gulf of Mexico face from strong tropical storms and hurricanes. When a hurricane hits, both people and businesses may be affected. The policies that communities adopt will govern how successful they will be at maximizing future benefits and minimizing future costs related to both types of environment-related events.
In order for communities to efficiently manage responses to environmental events such as severe weather and land conservation decisions of surrounding communities, it is important first to quantify and understand how these events affect communities over time. In my dissertation research, I conduct three independent studies to examine how environmental events such as hurricane strikes and land conservation decisions affect communities in the United States.
In the first chapter, I examine how hurricane strikes affect the economy in U.S. counties, including poverty levels, public business accounts, and population trends. The main hypothesis tested in this chapter was that hurricane strikes increase poverty levels and the effect persists over multiple years after the strike. Interestingly, we see that hurricane strikes decrease poverty levels in affected counties using a difference-in-differences methodology. There are two vehicles that can be causing this decrease after a strikean increase in business activity (including per capita personal income, wages, and employment) as well as a decrease in population. Supplementary analysis on shifts of income distribution shows that the decrease in poverty is most likely due to displacement of families around the poverty line.
In the second chapter, I examine if there is a "window of opportunity" in communities that experience a tropical storm or hurricane strike where people are more interested in taking preventative action against future storm damage costs. The main hypothesis tested in this chapter is that hurricane strikes cause an increase in interest activities used to mitigate against future hurricane damage costsmeasured by relevant Google search termsduring the month of a hurricane strike and a short duration afterwards. Results using a difference-in-differences methodology reflect this relationship. Populations in media markets that experience tropical storms and hurricanes show increased popularity of internet searches of flood insurance during the concurrent month up to a few months after. This suggests there may be a window of opportunity in which stakeholders are more likely to be engaged and support policies aimed at reducing future damage costs from environmental events like tropical storms and hurricanes.
In the third chapter, I examine whether municipalities that pass land conservation referenda cause state and neighboring municipalities to crowd-in or crowd-out land conservation spending. The main hypothesis tested in this chapter is that municipalities that pass conservation referenda are more likely to receive additional state land conservation funding and encourage neighboring towns to pass conservation referenda (i.e. a crowd-in effect). Results from a dynamic regression discontinuity methodology do not show a consistent causal effect in any of the relationships testedpassing a referendum does not result in any patterns of state spending in the focal municipality, state spending in neighboring municipalities, or referendum activity in neighboring municipalities. Results indicate that municipalities need not worry that their own conservation activity will crowd-out state and neighboring municipality conservation spending. Conversely, they should not expect crowding-in activity as well.
Discrete environmental events such as storm experience and natural resource decisions have the potential to have widespread consequences. Most of the research in this dissertation focuses on the impacts of environmental events in directly affected communitiesalthough neighboring counties to those that experience hurricane strength intensity are identified in the first chapter conservation activity in neighboring municipalities was examined in the third chapter. Future research can focus on examining if willingness to mitigate against future environmental damages is shown in neighboring communities. Future research can also examine individual data instead of aggregate data, which was the focus of this dissertation.