Estimating the Impact of Critical-Habitat Designation on the Values of Developed and Undeveloped Parcels

Saleh Mamun, Erik Nelson and Christoph Nolte

Abstract

We used the quasi-experimental difference-in-differences method to estimate the impact that the Endangered Species Act’s critical habitat (CH) regulation had on developed and undeveloped parcel prices throughout the United States between 2000 and 2019. At the national level we find that, on average, the prices of parcels in CH areas were not statistically different from the prices of similar nearby parcels not in CH. However, limiting our analysis to specific subsets of CH areas, we find mixed results. Previous empirical estimates have consistently found that the regulation reduces parcel prices. We offer several potential explanations for our contradictory results.

1. Introduction

Efforts to conserve biodiversity have increasingly focused on the role that working landscapes can play in such efforts (Garibaldi et al. 2021). As undeveloped area around the world dwindles due to pressures such as economic development and climate change, farms, managed forests, rangelands, and even suburbs will increasingly become the habitats and migration corridors that species rely on for survival (Kremen and Merenlender 2018). In some cases, efforts to make working landscapes more supportive of biodiversity will require restrictions on land use and management that could impose economic costs on private landowners. Understanding the magnitude and patterns of the costs created by biodiversity protection measures in working landscapes is integral to designing effective programs (Hanley et al. 2012). Unfortunately, estimates of the private cost of biodiversity protection on working landscapes—typically measured by programs’ impacts on private land values—are few (Fois, Fenu, and Bacchetta 2019). Those estimates that do exist focus on a landscape or two; they do not examine the issue at the regional or continental scales. Effective biodiversity protection will require planning at these larger scales.

In this article, we estimate the impact that the critical habitat (CH) regulation of the Endangered Species Act (ESA) has had on observed parcel values in landscapes across the continental United States. When a species is listed under the ESA as threatened or endangered, the U.S. Fish and Wildlife Service (FWS)1 is directed to concurrently designate CH for the species (ESA 1973).2 CH is defined as geographic areas occupied by the species that are “essential to the conservation of the species” and “may require special management considerations or protection” and areas outside the geographical area occupied by the species at the time of listing but determined essential for the conservation of the species (ESA 1973; USFWS 2017).

While decisions to list a particular species cannot deviate from the conservation objective of the ESA regardless of economic costs, the FWS can exclude areas defined as a species’ CH from the species’ final CH designation if the agency determines that the economic cost avoided by exclusion outweighs the biological benefits of designating the area as CH (ESA 1973). Economic costs generated by CH can include forgone development, reduced economic growth, or the negative impact on industrial activity (Fosburgh 2022).3 A species’ CH designation can also exclude defined CH areas if the area already contains a conservation project that aids the species in question, to maintain good relations with Native American tribal entities, or for national security (Fosburgh 2022).

In most cases, a species’ CH area is first proposed in the Federal Register (FR). The proposed boundaries of the area are typically set by conservation biologists in accordance with the CH definition and permitted exclusions (Fosburgh 2022). Often the FWS responds to public comments on the proposed CH designation with additional exclusions. For example, in an analysis of 90 CH designation processes, Fosburgh (2022) found that 62.9% of finalized CH designations covered less area than their initial proposed boundaries, and only 12.1% of CH processes added land between initial proposal and final CH designation. The most often cited reasons for removal of proposed CH areas in final CH designations were reconsideration of what qualified as habitat, preexisting conservation projects, and tribal land considerations (Fosburgh 2022).

Final CH designation does not affect land ownership or create a conservation area. Final CH designation does not require implementation of restoration, recovery, or enhancement measures on nonfederal lands (USFWS 2021a). However, federal funding or authorization of any activity in a designated CH area is not supposed to proceed unless it is deemed consistent with the conservation goals of the ESA (USFWS 2017). Although most designated CH area is on public or tribal land, millions of private acres across the United States could be subject to CH regulations (Fosburgh 2022).4 Therefore, the CH regulation is a biodiversity protection program with the potential to create significant private economic cost.

Activities on private land that require U.S. federal authorization or use U.S. federal dollars—and therefore could be affected by the CH regulation—are numerous. For example, many private development projects require a water-discharge permit from the U.S. Army Corps of Engineers (Auffhammer et al. 2020), affordable housing developers often use federal funds (Wallace 1995), and farmers can receive Conservation Reserve Program payments from the U.S. Department of Agriculture by making their land more biodiversity-friendly (Melstrom 2021).

Private land activities in CH areas that rely on federal permits or funding and that are initially found to be in noncompliance with CH regulations must be modified in accordance with regulations or risk being canceled (Yagerman 1990). Either outcome generates additional costs for the private landowner. Even when private activities in CH areas are found to be following CH regulations, the delays associated with the additional federal scrutiny could mean higher land development costs in a CH area relative to those in nearby non-CH areas (Sunding 2003).

The possibility of higher land development costs and restrictions in CH areas might encourage local land developers to focus on developable land immediately outside the CH area instead of equivalent land inside it (List, Margolis, and Osgood 2006).5 Basic economic theory suggests that such a dynamic would make undeveloped land inside CH areas less valuable relative to the undeveloped land immediately outside these areas, all else equal (e.g., Bošković and Nøstbakken 2017).

Conversely, development restrictions in CH areas could have a positive effect on prices of already developed parcels in CH areas for two reasons. First, CH regulations could slow, reduce, or in some cases stop the development of surrounding open space. In other words, homebuyers in CH areas might reasonably expect their surrounding open space to be preserved indefinitely, while homebuyers in the nearby non-CH area are more likely to see adjacent open land developed. Second, CH designation signals that the houses in the CH area are more likely than equivalent non-CH houses to be surrounded by unique wildlife conditions. Therefore, given that people are willing to pay a premium for houses adjacent to open space and in unique wildlife areas (e.g., Geoghegan 2002; Kiel 2005; Black 2018), homebuyers may be willing to pay extra to purchase a property in CH-designated areas.

In this article, we used 2000–2019 parcel sales data from across the continental United States to estimate the impact of CH regulation on undeveloped and developed parcel prices. We created these estimates by comparing trends in parcel prices in areas “treated” by CH to trends in parcel prices on landscapes immediately adjacent to CH areas. Our analysis allows us to determine whether, as we speculated, the CH regulation reduces the value of undeveloped parcels. Our empirical modeling allows us to determine whether homebuyers are willing to pay more in CH areas relative to nearby nonregulated areas. Our analysis contributes to the sparse but growing literature on the economic impacts of biodiversity protection programs on U.S. working landscapes.

We believe that our estimates of the economic impact of CH on private undeveloped and developed parcel values improve on the few previously published estimates in several ways. First, the parcel sales data we used covers most states in the contiguous United States, allowing us to expand the scope of CH analysis to a very broad range of working landscapes. Every other study that estimates the impact of CH on land values has focused on one or two much smaller regions, often in California or Arizona. Second, we restricted our analysis to parcel sales that took place when the parcels were in at least one ESA-listed species’ geographic range. Therefore, we are explicitly measuring the economic impact of CH above and beyond the economic impact of the ESA in general. Previous studies of CHs’ impact have not confronted this regulatory-impact identification problem and appear to estimate the economic impact of an amalgam of CH and broader ESA regulations. Third, we estimated the impact of CH designation on developed and undeveloped parcel prices separately given that the CH regulation could affect the value of each asset type differently. Aside from Klick and Ruhl’s (2020) analysis of four counties in Arizona, every previous empirical analysis of CH policy has focused exclusively on undeveloped parcel values. We improved on Klick and Ruhl’s (2020) analysis by using parcel-level data and specific CH boundaries to identify the economic impact of CH on housing prices; Klick and Ruhl’s (2020) identification of CH impacts is likely imprecise, as it relies on county-level median housing prices and coarse definitions of CH area.

2. Previous Literature on the Economic Impacts of Critical-Habitat Regulation

Past theoretical and empirical work has investigated the impact of CH on parcel values and the pace at which vacant or undeveloped parcels are developed. On the theoretical side, Quigley and Swoboda (2007) used a regional economic model to predict that CH designation prompts the development of some of a region’s non-CH area parcels that would have otherwise remained undeveloped. The model’s assumption of a complete restriction on housing construction in designated CH areas (a very unrealistic assumption; see Zabel and Paterson 2006) causes regional housing prices in general to increase, thereby raising the prices in the region’s designated CH areas. The anticipated increase in housing prices due to the regional supply shock also applies to the regional market’s non-CH areas, eliminating any developed land price differential between the region’s regulated and unregulated areas. Their model does not consider the possibility that housing prices could differ in regulated versus unregulated areas within the region due to a general preference for living near protected open space and unique wildlife.

Based on a survey of developers and a regional economic model, Sunding (2003) and Sunding, Swoboda, and Zilberman (2003) predicted that the California gnatcatcher’s CH would create an additional cost of $4,000 per housing unit, delay housing projects by one year, and reduce project output by 10% in the regulated area due to CH-related permitting, redesign, and mitigation. They also predicted that CH regulations would add $10,000 to the cost of each housing unit and delay completion of housing projects by one year in the CHs of several vernal pool species. Using the same survey data, they predicted that the equilibrium housing price in vernal pool species CHs would increase by $30,000 as developers would charge more to cover their regulation-induced costs and the reduction in the region’s housing supply would increase local equilibrium prices. In other words, their model suggests that undeveloped parcel prices in CH areas would be lower than comparable parcel prices outside CH areas because development costs and delays are higher in CH areas. However, as with Quigley and Swoboda (2007), their prediction that the regulation-induced housing shock would equally affect housing prices in and outside CH areas in the same region means that they did not consider the possibility that developed land prices could differ (all else equal) on either side of a CH border.

Several previously published empirical studies have corroborated the widely accepted hypothesis that CH regulations decrease the sale price of undeveloped parcels relative to the price of nearby unregulated undeveloped parcels. For example, looking at two CH areas in California, Auffhammer et al. (2020) found that the average price of undeveloped parcels in the CH areas fell relative to undeveloped parcel prices in nearby non-CH areas. List, Margolis, and Osgood (2006) found that prices of undeveloped parcels in the proposed (but not yet finalized) pygmy owl CH fell relative to prices for undeveloped parcels in nearby areas not proposed for CH regulation. Unlike Auffhammer et al. (2020), List, Margolis, and Osgood (2006) used propensity score matching to construct a control set of non-CH undeveloped parcels.6

Klick and Ruhl (2020) also investigated the impact of the pygmy owl CH on housing values (i.e., developed parcel values), instead of undeveloped parcel values. They found that the CH designation reduced housing values relative to synthetic controls. However, they used a housing price index, the Zillow Home Value Index, that only reports county-level medians. In our opinion, this dataset generates unreliable estimates of the treatment effect for several reasons. First, the pygmy owl CH does not align with county boundaries, which means that authors used a housing price summary statistic that is informed by properties that were not part of the CH. Second, by using a county-level summary value for housing prices, Klick and Ruhl (2020) were not able to use the full distribution of observed housing prices and were not able to control for the impact of property attributes on transaction prices.

Finally, Zabel and Paterson (2006) tested the hypothesis that CH designation depresses development activity in treated areas by comparing 1990–2002 building permit issuances inside and outside California CH areas. The treated area consisted of 39 designated CHs finalized between 1979 and 2003, and the control area included the non-CH areas of various administrative units in the state. The authors found that a median-sized California CH area experienced a 23.5% decrease in the supply of housing construction permits in the short term and a 37.0% decrease in the long term relative to the control area. Zabel and Paterson (2006) surmised that development in CH areas decreased because of the higher development costs and developmental barriers created by CH regulations. Their finding that housing development was depressed in CH areas is consistent with the widespread contention that developers are less interested in CH-regulated land and therefore prices for undeveloped land in CH areas will be lower than for undeveloped land in nearby non-CH areas.

3. Data

The unit of analysis in this study is the sale of a single tax-assessor parcel. We obtained sales records from Zillow’s Transaction and Assessment Database (ZTRAX), which contains dates, prices, and parcel identifiers of millions of property sales for most U.S. states back to the 1980s (Nolte et al. 2024 [this issue]). If the sold parcel contained a house, then ZTRAX may also report the house’s numbers of rooms, bedrooms, and bathrooms as of the last modification or renovation, the date of the last modification or renovation (if applicable), and the year the house was built (these data are not available for every county that ZTRAX covers). ZTRAX also indicates how each parcel was being used (e.g., “single-family home”) at the time of its sale.

We obtained digital maps of tax-assessor parcels from 12 open-source, state-level datasets and two commercial providers (Regrid, formerly Loveland, and Boundary Solutions). The years of the parcel maps vary by state and county; most parcel maps we used are from 2019. ZTRAX records have been linked to digital parcel boundaries based on assessor parcel numbers, using a customized algorithm for syntax pattern matching and conversion (Nolte 2020). We did not use ZTRAX transaction data that cannot be linked to parcels on our parcel map (e.g., if a parcel that sold in 2010 was subdivided in 2016, then ZTRAX will include the 2010 sale, but our parcel maps will likely have no record of the parcel that existed in 2010). We also did not use transactions that were unlikely to sell at market value, such as interfamily property transfers, foreclosures, or undervalued public transactions (Nolte et al. 2024 [this issue]).

We used multiple additional data sources to generate a suite of variables that describe each parcel’s physical characteristics and the conditions in the landscape surrounding the parcel. We used an open-source building-footprint dataset (Microsoft 2018) to compute each parcel’s number of buildings and percentage of area covered by buildings, circa 2012. We used the same data to compute the density of building footprints within 5 km of each parcel’s centroid. Land cover on each parcel as of 2011 was estimated using the National Land Cover Database (Homer et al. 2015). We extracted average slope and elevation for each parcel from the National Elevation Dataset (USGS 2017a). We used the National Hydrography Dataset (USGS 2017b) to estimate water (lake, river, and reservoir) frontage for each parcel as of 2017. We computed the percentage of each parcel’s area in wetlands as of 2018 with the National Wetlands Inventory Seamless Wetlands Dataset (USFWS 2018). Each parcel’s proximity to coastal waters is measured as a percentage of ocean area within a 2,500 m radius circle centered on the parcel (Esri 2009). We used the U.S. Census Bureau’s 2019 TIGER/Line Shapefiles to measure each parcel’s distance to the nearest paved road and highway (USCB 2019). We computed the percentage of area within 1 km of each parcel that is protected via fee simple ownership or an easement as of 2010 (USGS 2018; Colorado Natural Heritage Program 2019; Trust for Public Land and Ducks Unlimited 2020; Harvard Forest 2020).

Finally, we downloaded every digital map of finalized CH areas available at the FWS website (USFWS 2020) other than those found in Alaska, Hawaii, and U.S. territories. For species that have had multiple finalized CH areas over time, the FWS only makes digital maps of their most recent designations available. All maps were current as of spring 2020. The dates of all CH proposals and final designations were available in the FR notices cataloged at the FWS website (USFWS 2020).

4. Methods

Dataset Construction

We estimated the impact of the CH regulation on private parcel values with the difference-in-differences (DD) quasi-experimental method (Greenstone and Gayer 2009). For potential treated sales in our study, we used sales of developed parcels (classified as residential in ZTRAX with building code RR and with a positive building footprint) and sales of undeveloped parcels (parcels with no buildings) that took place within a finalized CH boundary before or after the CH’s boundary had been published in the FR. In contrast, potential control sales in our study were sales of developed or undeveloped parcels that have never been inside a finalized CH boundary but are within 5 km of a finalized CH boundary (even if the boundary did not exist at the time of the sale). We prefer the term “potential” as many otherwise eligible treatment and control sales were not included in our final dataset because their inclusion would unnecessarily complicate our efforts to identify the impact of CH designation on parcel values. We explain the order and rationale for each exclusion. Table 1 indicates the precise number of treated and control sales that were dropped from our analysis due to each exclusionary step.

Table 1

Data Exclusion Steps

Our initial dataset included 1,050,452 sales (over 599,021 parcels) potentially eligible for treatment status and 14,385,092 sales (over 7,635,373 parcels) potentially eligible for control status.7 Our first exclusionary step was to drop all parcel sales that took place before 2000. The farther we go back in time for parcel transaction data, the more difficulty we have matching these data to parcels on 2019 parcel maps. Transactions before 2000 were particularly difficult to match and thus were dropped. The use of the 2000 cut-off also required excluding all treatment and control sales associated with CHs that were finalized in 2000 or earlier given that we no longer had pretreatment sales for these CHs in our dataset.

Second, we eliminated all remaining sales associated with “complex” CHs. A CH is complex if its finalized and/or proposed boundaries changed at least once.8 We did not include these sales because their complex regulatory processes complicate causal identification. Consider a species that had its finalized CH area changed at least once. Suppose a species had its CH first finalized in 2010 and then had it updated in 2015. In this case, we cannot discern which parcels were part of the finalized CH area or its 5 km buffer from 2010 to 2015 because the FWS does not provide digital maps of now-defunct finalized CH boundaries. Therefore, for species that have had multiple finalized CH areas, we cannot reliably determine whether they were treated for at least some years.

Now consider a CH with two or more rounds of proposed boundaries before finalization (the other type of “complex” CH). Across all “simple” CHs, by which we mean CHs with just one proposed boundary and just one finalized CH boundary, there is a uniform time-event pattern that begins with a “preproposal period” and transitions to a “proposal period” before arriving in a “postfinalization period.” If we pooled CHs with different prefinalization patterns, for example, those with simple CH processes and others with the treatment pattern preproposal period—first proposal period—revised proposal period—postfinalization period, then a portion of the estimated DD coefficients value could be attributed to differences in the CH establishment process. Therefore, only sales associated with simple CHs are included in our final dataset.

Third, we eliminated all remaining sales associated with finalized CHs whose digital maps were obviously incorrect. For example, the Topeka shiner’s digital CH map on the FWS website as of 2020 included several whole counties as part of its finalized CH. However, the FR that finalized the Topeka shiner’s CH clearly states that only a few stretches of streams are included in its CH area.

Fourth, we excluded any remaining treated parcel sales that were covered by multiple CHs at any point between 2000 and 2019, and at least two of the CHs were established at different times.9 We excluded treated sales from areas covered by multiple, nonsynchronous CHs because their inclusion could complicate identification of the CH’s impact on parcel value. Suppose a sale of a parcel took place when it was in one CH, but its next sale took place when it was in two CHs.10 We believe that these two treated sales are not comparable given that they took place under different levels of regulatory pressure. By eliminating these successively treated sales from the final dataset, we make it more likely that all treated sales used in our analysis took place under similar levels of regulatory pressure.

Fifth, several remaining sales had price data but no other information about the transaction in the ZTRAX transaction file (ZTRAX lists sale price data in one file and related transaction data in another). We eliminated these sales from the final dataset because of missing data. Sixth, because we only observe building characteristics on developed parcels after the last known modification, we excluded from our final dataset any remaining sales of developed parcels that occurred before the last recorded modification to the parcel’s building(s). If we had not done this, our DD analyses would have included developed parcel sale prices regressed on a set of building characteristics that may not have existed at the time of sale. Seventh, we restricted our final dataset to parcel sales that took place when the parcels were in at least one ESA-listed species’ geographic range (USFWS 2021b). Therefore, the estimated DD coefficients only measure the economic impact of CH above and beyond the economic impact of the ESA regulation in general.

Our last few exclusionary steps were conditional. For the dataset that we used to estimate a repeated sales panel model, the last elimination steps were to (1) delete any remaining sales associated with a CH that did not have both treated and control sales, and (2) delete any sales from parcels with just one sale in the remaining dataset. The final dataset that we used for the repeated sales panel model includes 36,637 treated developed parcel sales from 87 CHs and 1,409,811 associated 5 km buffer developed parcel sales. This dataset includes 12,814 treated undeveloped parcel sales from 82 CHs and 151,866 associated 5 km buffer undeveloped parcel sales.

For the dataset that we used to estimate a pooled sales model, our last elimination steps were to (1) delete any sales associated with a CH that did not have both treated and control sales, and (2) delete any sales missing any parcel-level covariate data. In the end, the dataset used for the pooled sales model includes 45,726 treated developed parcel sales (over 30,986 parcels) from 94 CHs and 1,616,291 associated 5 km buffer developed parcel sales (over 971,339 parcels). It includes 19,693 treated undeveloped parcel sales (over 14,117 parcels) from 109 CHs and 284,076 associated 5 km buffer undeveloped parcel sales (over 200,955 parcels). See Appendix Table D1 for the universe of CHs with parcel sales in our final datasets.

Control Sales

In some DD analyses we used all 5 km buffer sales in our final dataset that also met the other restrictions (e.g., California-only CHs) as control sales. In other DD analyses we used as controls the subset of 5 km buffer sales that best matched treated sales and that met whatever other restrictions we used (e.g., California-only CHs).11

The algorithm we used to find the matched- control set for each CH consisted of the following steps. First, we defined the set of control sales for each parcel type (parcel type is either developed or undeveloped) that could be matched to treated sales. If the CH’s 5 km buffer contained at least five times the number of developed and undeveloped parcel sales as the CH area itself, sales in the 5 km buffer defined the pool of potential matches.12 For a few CHs, the 5 km buffer sales count did not meet the fivefold threshold for developed and/or undeveloped sales. In these cases, the set of potential developed and/or undeveloped sale matches included sales from the CH’s entire host county and, if the number of potential matches was still short of the threshold after step, adjacent counties (Appendix A). Second, after establishing the pool of untreated sales from which the matches would be drawn, we used the Mahalanobis algorithm to match up to two untreated sales to each treated sale (the variables described in the data section are the covariates used in the matching algorithm; Appendix A).13

We find that the average matched control sale, and therefore the average treated sale, had more lake frontage, was larger, was closer to a highway, was in a less building-dense area, and was nearer the coast than the average unmatched control parcel sale (the unmatched set includes all sales from the 5 km buffers). Furthermore, the average matched control sale of a developed parcel, and therefore the average treated sale of a developed parcel, had a house with 31.0% more gross area than the average unmatched control sale of a developed parcel (see Appendix Table D2 for covariate differences in means between the entire 5 km buffer and matched control sales pools).

We prefer the DD analyses that used matched controls rather than unmatched controls because the matched set reduces potential confounding and the severity of omitted variable bias in our DD estimators (Ferraro and Miranda 2017; Daw and Hatfield 2018; Melstrom 2021). Regarding the issue of confounding variables, by matching treated sales with control sales we reduce the possibility that differences in confounding variables caused the variation in outcomes between treated and control sales given that, on average, confounding variables’ values are the same for both treated and control sales.

To illustrate why matching reduces the threat of omitted variable bias in our DD estimator, consider the following scenario: suppose an otherwise CH-eligible parcel was excluded from CH designation by the FWS due to its extraordinarily productive soil. In other words, this parcel is excluded from the CH because it is highly valuable for agricultural uses. Recall that we do not observe soil quality. Suppose the parcel with the productive soil is also very flat, while all other parcels in the area—treated and untreated—have less productive soils and steeper slopes. The sale of the parcel with the productive soil would then be part of our unmatched control sales set and could bias our DD estimator because its value-explaining variable is omitted from our model. However, this CH-excluded parcel would likely not be part of our matched control set because it has a slope value dissimilar to the parcels in the CH area. In other words, if at least some observed covariates are systematically related to unobserved parcel value-explaining variables, matching helps us exclude parcels whose treatment status is explained by unobserved variables. Therefore, matching allows us to credibly claim that the control set is a treatment counterfactual along both observed and unobserved covariate dimensions.

Treatment Timing

In all of our DD analyses we considered treated and control sales associated with CH k that occurred before the date of k’s proposal in the FR as pretreatment sales. We considered all treated and control sales associated with CH k that occurred after k’s finalization in the FR as posttreatment sales. Therefore, we ignored sales in our final dataset that occurred between CH proposal and finalization dates.14 We suspect that real estate market dynamics during these transition periods are very different from those after CH finalization. The sudden imposition of a deadline on regulatory-free development could cause developers to make land purchasing decisions they would not otherwise make (List, Margolis, and Osgood 2006). Further, landowners in proposed areas looking to sell undeveloped parcels before boundary finalization might accept the first offer they receive, even if the offer price is significantly below market value. These deadline-induced behaviors should disappear once the CH is established. Therefore, if we included transition period sales in our analyses, we would have to use a more sophisticated time-event study model that accounted for three distinct stages of real estate market dynamics. We opted to focus on the long-run impact of CH on parcel values by comparing only the preproposal sales to postregulatory sales.

Heterogeneous Treatment Effects

An estimate of the DD coefficient using every treated and related control sale in our final dataset—a national-level analysis—assumes that the impact of CH regulations on parcel values did not differ across the spectrum of CH types. However, there are various reasons to suspect that CH groups differ in parcel value impacts. For example, might regulators enforce CH regulations more strictly in the CHs of species that they perceive as more popular or that are more sensitive to changes in their habitat? If this were the case, we would expect the parcel value impact of treatment to be more substantial than in an average case. On the other hand, might regulators be less inclined to strictly regulate in CHs where the economic impact of regulation could be very high or the species protected by the CH is not well known? If this were the case, we would expect the parcel value impact of treatment to be less severe than in an average case. Some state land use regulators may be more inclined to use CH as a guide for imposing additional state-level regulations. For example, the California Environmental Quality Act requires state-level scrutiny of proposed projects in CH areas (Auffhammer et al. 2020).

CH parcels tend to be drawn with two distinct CH shapes, which we suspect will differentially impact the parcel value impact of the CH. One class of CHs follow the contours of streams and coastlines. These types of CHs, typically designated for fish, clams, and snails, will only affect stream- or coastal-front parcels. CH shapes in the other class, those that follow the contours of terrestrial features, are more likely to affect a wider variety of parcels.

Finally, we suspect that the impact of CH on parcel values for some individual CHs can vary dramatically from the average impact across all CHs. For example, a CH that covers an idiosyncratic landscape may engender very different parcel value effects from the average or representative CH.

To examine whether these different sets of CHs generate different economic impacts, we estimated our DD models across various subsets of treated sales and their related control sales, including those just from California, riparian species CHs, plant CHs, amphibian CHs, and terrestrial animal CHs (mammals, birds, and reptiles). Finally, we estimated our economic model for sales treated by a single prominent CH, including the jaguar, the Gunnison sage-grouse, and the Atlantic salmon. We chose these individual CHs because the number of 2000–2019 treated and related control sales in each case was large enough to generate DD model estimates.

Pooled Two-Way Fixed-Effects Ordinary Least Squares Model

We measured the impact of CH on developed and undeveloped parcel prices with both pooled two-way fixed-effects (FE) ordinary least squares (OLS) and FE panels. The pooled two-way FE OLS (pooled OLS) estimation approach, Embedded Image 1 uses the log of the real ha−1 sale price of parcel j sold on date t (2019 US$) as the dependent variable (Vjt). The first explanatory term, φjc × σt, fixes the county location (φjc) and year of each sale (σt). The term βjrtXjt + γjrtZj is the hedonic price function. In some cases, one hedonic function was used to estimate equation [1]. In other cases, all variables in Xjt and Zj were multiplied by region-year dummies (region r can index U.S. Census divisions or counties). In these latter estimations, βjrtXjt + γjrtZj controls for idiosyncratic real estate market conditions in each region-year rt (Bishop et al. 2020). The indicator variable 1[T]j indicates whether parcel j is in an area that became a CH sometime between 2000 and 2019. For treated sales, 1[A]jt indicates whether the sale of j at time t occurred before the proposal of the CH or after the establishment of the CH that houses j. For control sales the variable 1[A]jt indicates whether the sale of j at time t occurred before the proposal of the CH or after the establishment of the CH with which j is associated.

The vector Xjt contains, where available, variables on parcel j’s housing characteristics at the time of the house’s last known modification, including the number of rooms, the number of baths, the gross area of the house and related buildings, and the age of the structure in sale year t. The vector Xjt is empty when we estimated equation [1] over undeveloped parcel sales. The vector Zj contains variables on parcel j’s land characteristics, including its area, its average slope, its average elevation, whether it has lake frontage, and its percentage of area in wetlands as of 2018. The vector Zj also contains information on land characteristics near parcel j, including the percentage of area within 2.5 km of j that is in coastal waters, the percentage of the area within 1 km of j that was protected as of 2010, the percentage of area within 5 km of j that was built up as of circa 2012, the distance between j and the closest highway as of 2019, and the distance between j and the nearest paved road as of 2019.

Finally, μ, the coefficient on 1[T]j1[A]jt, measures the average impact of the CH regulation on the sale price of treated parcels relative to price trends on control parcels where all sales, treated and control, are subject to broader ESA regulations.15 The DD estimator μ̂ is the unbiased estimator of the average treatment effect on the treated (ATT): Embedded Image 2 if several assumptions are met. When we estimated model 1 over just one CH (e.g., the jaguar’s CH) or over a pool of CHs that were established at the same time, these assumptions include (a) conditional parallel trends, (b) homogeneous treatment effects in X,Z, (c) no X,Z-specific trends across sales grouped according to every unique combination of 1[T]j and 1[A]jt, and (d) “common support” across treated and control sales (Angrist and Pischke 2009; Daw and Hatfield 2018; Cunningham 2021). When we estimated model 1 over a pool of CHs with staggered establishment dates (e.g., our national and California-level analyses), two more conditions must be met for μ̂ to be an unbiased estimator of ATT: (e) variance-weighted parallel trends are zero and (f) no dynamic treatment effects (Cunningham 2021).

In the results section we verify conditional parallel trends in the data. “Common support” across treated and control sales was likely to be met when we use matched controls; otherwise, we simply assume assumptions (b) and (c) were met. While we also assume (e) and (f) were met (when needed) in our topline results, we also estimated equation [1] using subgroups of CHs that were established at approximately the same time and then compared these estimates’ DD coefficients to the DD coefficients estimated with our larger pool of CHs to look for evidence of staggered-treatment time impacts (see Section 6). As we show later, the estimated DD coefficients over subgroups of parcel sales from similarly timed CHs are not systematically different from those estimated over parcel sales from variously timed CHs.

Repeat Sales Panel Model

In the pooled OLS model, we do not explicitly link multiple sales of the same parcel. However, we can rewrite equation [1] so multiple sales from the same parcel are explicitly linked. This rewritten model is estimated over treated and control parcels j that sold at least twice: Embedded Image 3 Here, ρj is the parcel FE, φjc × σt is the county-year FE, and ω is the panel DD estimator. In the panel model, the term ρj + φjc × σt controls for all time-invariant parcel-level characteristics, local land market conditions, and market conditions over time. Again, the DD panel estimator measures the average impact of the CH regulation on the sale price of treated parcels relative to price trends on control parcels where all sales, treated and control, are subject to broader ESA regulations. As before, ω̂ is the unbiased estimator of the ATT as long as ATT assumptions (a)–(d), and (e)–(f) when needed, are met.

Addressing potential omitted variable bias in the pooled OLS model was our primary motivation for using a repeat sales panel DD model (Kolstad and Moore 2020). The panel model better supports the causal interpretation of the DD coefficient than the pooled OLS model because it controls for all time-invariant parcel-level variables, including those that were omitted in the pooled OLS model and may be sources of bias in the pooled OLS model’s DD coefficients. However, we view the repeat sales panel model as a complement rather than a replacement for the pooled OLS model. Compared with the FE panel model, the pooled OLS model has several superior features. First, we can estimate the pooled OLS model over a larger set of observations than we can with the panel model. Second, we can use it to test whether our sales data are consistent with hedonic price theory because it contains variables that characterize each parcel.

Table 2

Estimates of the Pooled Model’s Difference-in-Differences Coefficient μ̂ across All Critical Habitats (CHs) (National Analysis)

5. Results

Estimates of the Pooled OLS Model over All CHs

In the first set of the pooled OLS model’s estimates, we used all treated sales in our final dataset (national-level analysis). Initially, we used all 5 km buffer sales in our final dataset as controls (Table 2, column (1); Appendix Figures D1 and D2). We added the estimation modifications sequentially to gauge the impact of each modification on the estimated DD coefficient μ̂. In the first estimation modification, we used hedonic price functions specific to each year in each U.S. region instead of a national, time-invariant hedonic price function (Table 2, column (2)). Next we reverted to a national, time-invariant hedonic price function but used matched controls instead of all available controls (Table 2, column (3)). Last, we used the combination of region-year hedonic price functions and matched controls (Table 2, column (4)).

When there are no estimation modifications, national-level estimates of the pooled OLS model indicate that CH treatment, all else equal, did not have a statistically significant impact on 2000–2019 developed or undeveloped parcel prices relative to nearby controls. Alternatively, when we used hedonic functions specific to region and year instead of the national, time-invariant hedonic function, we find that treated developed parcels across the continental United States were, on average, 8.9% less valuable than they would have been if they had been spared CH treatment like their nearby, ESA-species range space controls.16

Figure 1
Figure 1

Mean of Log of Price ha−1 by Years before or since Critical-Habitat Establishment: (a) Developed Parcel Sales; (b) Undeveloped Parcel Sales

Conversely, estimates of model 1 at the national level with matched control sales indicate that CH treatment did not have a statistically significant impact on developed and undeveloped parcel prices, regardless of the structure of the hedonic function. Our national estimates of model 1 did lose significant degrees of freedom when we relied on matched control sales versus nonmatched control sales. However, as we noted already, the matched controls better mirror the tendency for treated parcels to be larger, to have more lake frontage, to be closer to the coast, and if developed, to have larger houses than the typical 5 km buffer parcel (Appendix Table D2). Given the likelihood of confounding bias in estimates of model 1 with unmatched controls and the fact that hedonic functions specific to region-year can capture some of the idiosyncratic real estate market conditions across regions and years, we put the most weight on the national results captured in Table 2, column (4). Moving forward, we continue to emphasize results generated with matched controls and regional, time-variant matched controls.

Plots of the mean of log(Vjt) against treatment timing across all treated and matched control sales (sales used to estimate model 1 as summarized in Table 2, columns (3) and (4)) support the conclusion that, at least at the national level, CH treatment had little impact on parcel prices relative to the nearby control sales. As Figure 1a indicates, the pretreatment parallel trends in national-level developed parcel Embedded Image was maintained for six years after treatment. Parallel trends in national treated and matched-control Embedded Image, both pre- and posttreatment, are also seen for undeveloped parcels (Figure 1b). As we mentioned already, parallel trends in the dependent variable prior to treatment are necessary (but not sufficient) for μ̂ to be considered an unbiased estimator of ATT.

While national trends in pre- and posttreatment prices are parallel for both parcel types, the trends are not flat. Across both parcel types, national treated and matched control Embedded Image fell just before CH proposal (indicated by the x-axis value of 0) and then rebounded strongly soon after final CH designation (indicated by the x-axis values of 1, 2, and 3). At year t = 0 the statistic Embedded Image is almost entirely made up of sales that occurred just before a CH proposal. The similar dips in Embedded Image at t = 0 across both parcel types and treatment conditions could indicate that rumors of an impending CH regulatory process caused land market uncertainty in the affected landscape, temporarily depressing both developed and undeveloped land prices in the treated and the nearby control area. The similar posttreatment rebounds in parcel prices across both parcel types and treatment conditions could be explained by several dynamics. We offer one plausible explanation for similar posttreatment rebounds in treated and control undeveloped parcel prices below.

Suppose treatment causes most demand for undeveloped land in CH areas to be displaced into the CH’s 5 km buffer as developers are no longer interested in parcels that may have limited developable opportunities. At the same time, suppose the supply of undeveloped parcels in treated areas falls following CH establishment, as owners may have either already sold their parcels in anticipation of the designation or removed their properties from the market in response to diminished demand (List, Margolis, and Osgood 2006). All in all, the number of undeveloped parcels for sale post–CH establishment could have fallen dramatically. Therefore, increased undeveloped parcel demand in areas surrounding CHs and decreased undeveloped parcel supply in the local land markets defined by CH boundaries could explain the spikes in Embedded Image for control and treated undeveloped parcels after t = 0. Data on the number of undeveloped sales across time and treatment condition particularly supports the first part of this narrative (i.e., demand for undeveloped parcels was driven into the buffers). Across all treated undeveloped sales in our final dataset, 48.9% occurred after the final CH designation. Conversely, across all 5 km buffer undeveloped sales in our final dataset, 67.6% occurred after treatment (Table 2). In other words, if market activity and undeveloped land prices are higher in the buffer areas posttreatment then demand for these parcels must have risen faster than their supply in these areas.

Estimates of the Pooled OLS Model over Subsets of CHs

At the individual CH level, we find partial evidence of parcel values being negatively affected by the CH regulation (Table 3, panel A; Appendix Figures D3–D5). Four of the six pooled OLS model estimates over sets of parcel sales defined by individual CHs and their matched controls returned a null treatment effect. However, for developed parcels in the Atlantic salmon CH and undeveloped parcels in the jaguar CH, the same model estimates negative price effects of 41.24% and 42.02%.

Pretreatment parallel trends in Embedded Image are only satisfied for developed parcel sales in the jaguar and grouse CHs (Appendix Figures D6–D8). Aside from these two cases, our estimates of the ATT of individual-species CHs on parcel values are potentially biased. Given FWS’s documented efforts to exempt some “developable” vacant parcels from CH regulation (Fosburgh 2022), we believe that if μ̂’s associated with undeveloped parcel sales for each individual CH are biased then they are so in the upward direction (see Appendix B for an explanation). We are not sure of the direction in bias if the μ̂’s associated with developed parcel sales are biased.

Estimates of model 1 over sales grouped by CH type also indicate that CH designation has occasionally had a negative effect on parcel prices (Table 3, panel B). In our preferred model, which uses matched controls and distinct region-year hedonic functions, developed parcels in terrestrial animal and plant CHs were, on average, 1.75% and 48.60% less valuable, respectively, than they would have been if spared CH treatment (Table 3, panel B, column (2)). Furthermore, consistent with the hypothesis that the CH regulation depresses undeveloped parcel values, undeveloped parcels in plant CHs were, on average, 6.26% less valuable than matched controls (Table 3, panel B, column (4)). However, treatment had the opposite effect on undeveloped parcel prices in terrestrial animal CHs as undeveloped parcels in these CHs were, on average, 5.95% more valuable than the matched controls (Table 3, panel B, column (4)).

We find parallel pretreatment trends in Embedded Image for the terrestrial and riparian species groups (Appendix Figures D9–D12). However, this necessary condition for μ̂ being an unbiased estimate of the ATT does not hold for parcel sales associated with amphibian and plant CHs. Therefore, we are more confident in the causal interpretations ascribed to terrestrial animal CHs than those associated with plant CHs. As before, we believe μ̂’s associated with undeveloped parcel sales are biased in an upward direction, if at all (Appendix B).

Table 3

Estimates of the Pooled Model’s Difference-in-Differences Coefficient μ̂ across Different Subsets of Critical Habitats (CHs) Defined by Species or Species Type

Estimates of the Pooled OLS Model over California CHs

When using our preferred matched control sales and county-year hedonic functions combination, model 1 estimates that the impact of California CHs on parcel values has been null (Table 4, columns (3) and (5)). Model 1 only returned statistically significant μ̂’s in the California case when we replaced county-year specific hedonic functions with a time-invariant, state-wide hedonic function and limited the pool of CHs to four amphibian CHs found in the state. Specifically, developed and undeveloped parcels in California amphibian CHs were, on average, 14.05% and 48.22% more valuable, respectively, than they would have been if spared CH treatment (Table 4, column (3)).17 Finally, plots of California’s trends in treated and matched control Embedded Image pretreatments are largely parallel (Appendix Figures D13 and D14). Therefore, the necessary pretreatment parallel trend assumption for μ̂ being an unbiased estimate of CH’s ATT in California are generally met.

Table 4

Estimates of the Pooled Model’s Difference-in-Differences Coefficient μ̂ in California Critical Habitats (CHs)

Estimates of the Repeat Sales Panel Model

All estimates of the repeat sales panel model suggest that the CH regulation, at least when considering all CHs in our dataset, including those missing Xjt and Zj data, had no statistically significant effect on parcel prices regardless of the type of parcel (developed or undeveloped) and control method (matched or not) used (Table 5, panel A). To compare repeat sales panel model DD coefficients to those generated by the pooled OLS model, we limited the sample of sales to those that would not be excluded by either model type: sales with complete Xjt and Zj data from parcels that sold at least twice (Table 5, panel B). This subset of repeated sales also generated null ω̂’s (compare panel A to panel B ω̂’s). Furthermore, only one of the four estimated μ̂’s in Table 5, panel B noticeably diverges from the μ̂’s generated with the national dataset of all sales (compare Table 5, panel B, to Table 2). Therefore, we conclude that the national repeated sales dataset does not contain parcel price trends at odds with the parcel price trends in the pooled dataset (parcels with and without repeated sales).

Assuming the panel model has a stronger claim to causal interpretation because it controls for all time-invariant parcel-level variables, including those omitted in the pooled OLS model, we are even more confident in the conclusion that the CH regulation, at least at the national level, has had little impact on parcel values.

Hedonic Price Function Sanity Checks

The pooled OLS model 1 is a hedonic price model with DD controls. Therefore, if the signs on Xjt’s and Zj’s estimated coefficients tend to be consistent with the larger hedonic price model literature, we have further evidence that the pooled OLS model is correctly specified. According to past hedonic price model research, parcels near lakes and oceans (e.g., Dahal et al. 2019), urban and suburban amenities (Ardeshiri, Willis, and Ardeshiri 2018), transportation networks (Seo, Golub, and Kuby 2014), and protected areas (e.g., Kling et al. 2015) are more valuable, all else equal, than parcels further from these landscape features. In addition, parcels higher in elevations (e.g., Wu, Adams, and Plantinga 2004; Sander, Polasky, and Haight 2010) but on flat land are more valuable than low-lying land that is sloped (e.g., Ma and Swinton 2012). Finally, houses that are larger, have more rooms and bathrooms, and are newer are more highly valued than smaller and older houses (e.g., Morancho 2003; Sander and Polasky 2009).

Table 5

Estimates of the Repeated Sales Panel Model’s Difference-in-Differences Coefficient ω̂ across All Critical Habitats (CHs) (National Analysis)

In Table 6, we indicate the fraction of times an estimated pooled OLS model’s coefficient on a parcel or structural variable had the expected sign (a variable’s hit rate). Each column of Table 6 gives overall hit rates for estimates of model 1 with identical model permutations (e.g., “all CHs, region-year hedonic functions, and matched controls;” “CH subsets, one time-invariant hedonic function, and matched controls”).

The house structural variables in vector Xjt consistently shifted developed parcel prices in ways that aligned with expectations. As has been found by the larger hedonic literature, estimates of model 1 generally predict that larger and newer homes with more rooms and bathrooms sold at higher prices, all else equal. Furthermore, the land characteristic variables of lake frontage, proximity to coastline, nearby building footprint (a proxy for proximity to urban and suburban amenities), and parcel size also shifted developed and undeveloped parcel prices in expected ways. Overall, these results suggest that the pooled OLS model is properly specified.

Table 6

Fraction of Estimated Hedonic Price Function’s Variable Coefficients of Expected Sign in Estimates of the Pooled Model

We were surprised to see that proximity to protected areas and distance to highways and paved roads did not affect parcel prices in expected ways.18 Given that most of the treated and control parcels in our final database are on exurban and rural landscapes in the western United States, nearby protected open space is likely to be relatively abundant and therefore would not generate the price premium in our model as it does in hedonic models estimated over urban and suburban landscapes.19 The unexpected finding for distance to highways and paved roads might be explained by multicollinearity in the data because nearby building footprint, distance to nearest paved road, and distance to nearest highway are all highly collinear.

6. Robustness Checks

In many cases, particularly at the national level, we found that the CH regulation has had no meaningful impact on parcel prices. In other cases, we found a statistically significant impact but with a sign contrary to previous literature. To test whether these unexpected results could be explained by default modeling choices, we reestimated model 1 under several alternative modeling assumptions. We also transform model 1 into a spatial regression discontinuity model to test for heterogeneous spatial effects. In general, these robustness checks verify what we have already found: the CH regulation has had an inconsistent impact on parcel prices, including many null impacts.

Placebo Test for Treatment Effect

Theoretically, if we estimated model 1 over a set of parcel sales with no sales from a CH area (but all from ESA-listed species range space) then μ̂ should be statistically equivalent to zero given the absence of the CH regulation in the data. To test this hypothesis, we reestimated model 1 where all 5 km buffer sales were the treated sales (the placebo) and sales that occurred at least 5 km beyond CHs acted as controls. If the placebo μ̂’s are different from the actual μ̂’s, an explanation is needed or modeling assumptions need to be reexamined. At the national and California levels, using matched controls and a single, time-invariant hedonic function, the actual and placebo μ̂’s are all statistically equivalent to zero (compare Table 2, column (3) to Appendix Table D6, column (1) and Table 4, column (1) to Appendix Table D6, column (2)). At least at the national and California levels, there is no reason to question model 1’s specification or assumptions.

Alternative Control Sets

In our default DD analysis, most matched control sales were drawn from the 5 km buffers surrounding finalized CHs. We reestimated model 1 at the national level and across various CH subsets using matched controls drawn from 3 km buffers and 10 km buffers to determine whether the 5 km buffer choice led to anomalous results. In general, the signs and level of statistical significance associated with the various μ̂’s do not change as buffer size changes (Appendix Tables S7 and S8). Therefore, the size of our control buffer does not appear problematic.

However, the chosen location of our control sale areas could have hampered our ability to identify CH’s economic impact. As we noted, immediately after CH establishment the average sale price of treated and matched control parcels across the nation jumped in a very similar manner (see Figure 1). Similar jumps in average sales price regardless of treatment status led us to conclude that CH has had little to no effect, at least at the national level, on treated sales relative to matched control sales. We have already described how market equilibrium adjustments on both sides of CH borders could explain this similar discontinuous change. Another possible explanation for this similar discontinuous jump is parcel buyers and sellers treating most of the land within 5 km of CHs as part of designated CH areas. For example, market participants may have mistakenly considered some buffer areas as regulated areas because a proposed CH map, but not the finalized map, included these buffer areas. Alternatively, if market participants were unsure of the exact finalized CH boundaries they may have erred on the side of caution and treated all parcels in the CH’s immediate area, including land within 5 km of the actual borders, as regulated. If either case accurately describes market participant behavior, our default DD approach violates the stable unit treatment value assumption (SUTVA) needed to identify the causal impact of CH on land prices.

Therefore, the impact of CH on parcel value may best be detected by using control sales that are between 5 and 10 km from CH borders. In this alternative analysis we are more likely to use control sales not affected by CH-generated local market effects and not mistakenly treated as regulated by market participants. We reestimated model 1 with matched control sales that occurred at least 5 km from CH borders (Appendix Table D6, columns (3) and (4)) to determine whether creating a control set meant to deal with potential SUTVA violations changed our topline results (all matches were still within ESA-species range space). In the national and California-only analyses, this alternative control set did not result in undeveloped parcel μ̂’s that deviated from default μ̂’s; all are statistically equivalent to zero (compare Appendix Table D6, column (3) to Table 2, column (3) and Appendix Table D6, column (4) to Table 4, column (1)). Furthermore, this alternative control set generated developed parcel μ̂’s that had the same signs as the default developed parcel μ̂’s. However, unlike the default μ̂’s, the alternative μ̂’s are both statistically significant. In other words, if sales at least 5 km from CH borders are the appropriate controls, then our default results may underestimate the impact of CH regulation on developed parcel prices.

Controlling for Staggered Timing of Treatment

Recent econometric literature has discussed the possibility of biased DD estimators when treatment timing is staggered (Goodman-Bacon 2018; de Chaisemartin and d’Haultfoeuille 2020). Staggered-treatment bias cannot be an issue in our individualspecies CH estimates of model 1 (Table 2, panel A) but is a potential problem in all other model estimates because the date of treatment varies across any set of CHs. Per Callaway and Sant’Anna (2019), we eliminate the potential of bias in the pooled OLS model’s DD estimator due to staggered treatment by estimating the model over three distinct cohorts of similarly timed CH designations (Appendix Tables D9–D11). To further reduce the potential impact of unobserved policy changes affecting parcel prices in these CHs and their relevant controls, we only included treated sales and matched control sales that occurred within the first two years of treatment (pretreatment sales are not limited by time).

For three CH cohorts, we estimated developed parcel and undeveloped μ̂’s first using a single, time-invariant hedonic function and again using region-time hedonic functions. In each case we used matched controls. Of the 12 μ̂’s (3 CH cohorts × 2 parcel types × 2 hedonic function types), only two are statistically significant at the p = 0.05 level. Both statistically significant cases indicate that CH has had a negative impact on the prices of developed parcels. The large fraction of null results generated when using cohorts of similarly timed CHs is consistent with the large fraction of null results we found in the national and California-level analyses, where we did not control for staggered-treatment timing. These results suggest that staggered-treatment timing bias is not a significant issue in our default estimates of model 1.

Alternative Definitions of Developed Land

Some parcels flagged as developed in our database (zoned as rural-residential with positive building footprint) were likely to be viewed by developers as still “developable.” For example, consider a rural-residential 40-acre parcel with a small, older dwelling on it. If the construction of one or more houses on this “developed” parcel would have generated substantial net revenue, then this “developed” parcel would have been very attractive to a developer (Newburn and Berck 2006). Therefore, we experimented with dividing our developed parcels into two types: those with 0.063 or lower building-footprint-to-parcel-area ratio (BPR), like the illustrative example above, and those with BPR higher than 0.063. (A BPR of 0.063 is the 90th percentile of the BPR distribution across all rural residential sales in our final dataset.) We assumed developed parcels in the former category had high potential for redevelopment and parcels in latter category were generally too costly to redevelop and their new owners would, for the most part, use the parcels as is.

Using all CHs (national dataset), a single, time-invariant hedonic function, and matched controls, the estimates of model 1 with sales of high BPR developed parcels and again with sales of low BPR developed parcels returned null μ̂’s (Appendix Table D12). Recall the that national estimates of model 1 with a single, time-invariant hedonic function, and matched controls across all developed parcels and again across all undeveloped parcels also returned null μ̂’s (Table 2, column (3)). Therefore, the subdivision of developed parcels into two sets based on building footprint does not change our assessment of national results.

Spatial Regression Discontinuity

An alternative quasi-experimental method for identifying the impact of a regulatory border on economic outcomes is spatial regression discontinuity (SRD) (Shenoy 2018; Gonzalez 2021). In our pooled OLS and repeated sales panel models, a CH border’s economic impact is uniform inside the border and potentially different but uniform outside the CH area. Up to this point, we have assumed a treated sale that took place 100 m from a border and another treated sale that occurred 2 km from the same border are impacted equally by the regulation. Similarly, a control sale that took place 100 m from a border and another control sale that took 2 km from the same border are equally affected or unaffected by the regulation in our model.

Therefore, a regulation that had economic impact at the immediate border but quickly dissipated might not be identified by a DD analysis that does not allow for heterogeneous spatial effects in treated and control areas. However, SRD can capture any hyperlocal CH economic impacts that quickly dissipate in space. The SRD version of model 1 is Embedded Image 4 where Dj indicates the shortest distance (in km) from sale j’s location to the CH boundary (Dj is negative if j is a control sale) and all other variables are as before. Any discontinuity in parcel values at the CH border, all else equal, is given by γ̂ and the marginal effect of distance from the border on sale price is measured with η̂ + λ̂ and η̂ for treated and control sales, respectively. Because an SRD model requires borders, we estimated equation [4] only over sales that took place after CH establishment (all j, treated and control, have 1[A]jt = 1). We used sales that took place before CH border establishment (all sales j, treated and control, have 1[A]jt = 0) for an SRD placebo test. If CH establishment reduced the value of treated parcels relative to control parcels at the border, then γ̂1[A]=1 will be negative and γ̂1[A]=0 ≈ 0 (where the subscript 1[A] = 0 indicates that this is the placebo test of the spatial RD).

To increase the likelihood of finding a border effect in the spatial RD, we limited the analysis to areas of the landscape where the opportunity cost of CH on development was likely to be highest. Between 2012 and 2016, U.S. land prices were positively correlated with building density (Wentland et al. 2020). We limited the CHs used in the spatial RD to those in the top 25th percentile of the mean of the variable “density of building footprints within 5 km of each parcel’s centroid” across all the CHs’ 2000–2019 sales. Finally, we used a single, time-invariant hedonic function and matched controls in our SRD estimates (Appendix Table D13).

The estimates of the SRD model are easiest to interpret when we plot γ̂1[T]j + η̂Dj + λ̂1[T]jDj for developed and undeveloped parcel sales against a range of Dj before CH proposal (placebo) and after CH establishment (Appendix Figure D15). First, the average marginal effect of distance on parcel value in the control sale zone was essentially equal to zero (η̂Dj ≈ 0) before CH proposal (1[A] = 0) and after CH establishment (1[A] = 1) for both types of parcels across the nation and in California, all else equal. Second, the average marginal effect of distance on both developed and undeveloped parcel value in CHs was positive and economically significant posttreatment (i.e., η̂Dj + λ̂1[T]jDj increases rapidly in Dj when 1[A] = 1). Third, at least at the national level, the average marginal effect of distance on parcel value in the treated areas was greater after treatment than it was pretreatment (i.e., η̂Dj + λ̂1[T]jDj is greater at all Dj when 1[A] = 1 versus when 1[A] = 0), suggesting that CH treatment boosted the value of developed and undeveloped parcels in CH area interiors. Finally, these plots make very clear that the economic significance of any border effect (γ̂1[A]=1) was very small relative to the distance from the border effects (at least for the subset of CHs in the most building-dense landscapes). This SRD analysis reinforces our topline result that the impact of CH on parcel prices varies depending on the analytical context and the CH regulation’s impact on parcel values cannot be reduced to a simple, consistent narrative.

7. Conclusion

We find that under some conditions, CH treatment can have a statistically significant impact on parcel values. We also find that the direction of the impact is inconsistent. In some cases, the CH regulation had a negative impact on the price of parcels; in other cases, the impact was positive. The scale of analysis greatly affected the magnitude, sign, and statistical significance of the DD estimators. National-level analyses indicated little to no effect of the CH regulation on parcel values, while some more focused analyses (e.g., terrestrial animal CHs only or California amphibian CHs only) suggested that CH has had an impact on parcel prices. Moreover, our models did not generate a pattern of noticeably different estimated DD coefficients when we used regional, time-variant hedonic functions rather than global, time-invariant hedonic functions (Appendix Table D14). All in all, we conclude that the impact of CH on parcel prices cannot be reduced to a simple, consistent narrative. Determining the reasons that some CHs create positive economic impacts, others create negative economic impacts, and still others have no apparent economic impact at all are the questions that future CH economic research must answer.

Previous work has consistently found that the CH regulation had a negative impact on undeveloped parcel prices. There are multiple reasons that could explain why this analysis only occasionally finds similar impacts. First, across all treated and matched control sales in our final dataset, 95.4% of developed and 95.3% of undeveloped parcel sales were not from California, whereas almost all other previous CH impact analyses have focused on that state (e.g., Auffhammer et al. 2020). Therefore, unlike previous CH analyses, we were able to account for the economic impact of CH on a varied set of landscapes from all regions of the United States. Second, we emphasized the DD results we obtained with a matched control set. Only a few of the previous CH impact analyses used matched (or synthetic) controls, an approach that many researchers have found improves causal identification (Daw and Hatfield 2018). Third, we measured the impact of the CH regulation on parcel prices, not the impact of a mixture of CH and broader ESA regulations on land prices, by ensuring that every parcel sale in our dataset, treated or control, occurred when the parcel was in the geographic range of at least one listed species. Previous empirical studies of CH economic impact have not separated these different regulatory impacts.

Several reasons could explain why undeveloped land prices are mostly not negatively affected by the CH regulation. The most obvious explanation is that the CH regulation, especially when separated from the broader ESA regulation, does not have much regulatory bite. For example, many development projects in many CH areas may not require federal permits or use federal funding, thereby never triggering CH-related regulation. Even in cases where there is federal involvement, it could be that required changes or activity delays are often minor, creating little effect on prices. In fact, past FWS administrators have claimed that the CH regulation is superfluous given the broader ESA regulations (Armstrong 2002).20 Also recall that the FWS can exclude parcels from CH designation for economic purposes. Therefore, the undeveloped parcels worth the most on the market may not be subject to the same CH regulations as their immediate neighbors. Another possible explanation for higher-than-expected undeveloped parcel prices in CH areas is that housing developers may be willing to put up with the hassle and uncertainty of developing land in CH areas if they believe that homeowners will be willing to pay a premium for houses in these regulated areas.

Alternatively, undeveloped parcel prices could have fallen less than expected in CH areas because of local land-supply effects. For example, if some undeveloped parcels in a CH area became undevelopable due to CH regulations but the remaining undeveloped parcels in the CH can be developed at little additional cost or delay, the difference in development cost between treated (but “developable”) and control undeveloped parcels will be minor. In this case, the total supply of developable land has fallen across the CH and its 5 km buffer, thereby keeping undeveloped parcel prices in both zones elevated, but the similar cost of development across the two zones means no price differential across zones. The temporal pattern of average undeveloped parcel prices pre- and posttreatment in Figure 1b comport with this story: notice that for five years after CH establishment, both treated and control average undeveloped parcel prices are elevated relative to their average prices before treatment.

On the other hand, a demand-side shock could help explain why undeveloped land prices in some CH areas are higher than expected. For example, suppose conservation organizations become interested in buying undeveloped land in CH areas because of their high biodiversity value. This new source of demand for undeveloped land in the CHs could maintain prices despite the additional regulatory scrutiny of private development activities in the same area (Armsworth et al. 2006).

The conclusion that the CH regulation does not have much actual regulatory bite could also explain why we did not consistently find higher developed parcel prices in CH areas after treatment. For example, if CH designation does little to prevent development, then open spaces adjacent to homes in CH areas are just as susceptible to development as open spaces adjacent to homes in nearby, non-CH areas. If this is true, then homes in CH areas would not command a premium relative to homes in unregulated areas. Alternatively, assuming CH does make the preservation of open space more likely, homes in the 5 km buffer will be near unique open spaces. For many homeowners, being near these unique open spaces could be just as valuable as being within them, thereby explaining the fact that we find no evidence of a housing premium in CH areas.

Finally, supply-side dynamics could help explain any null effects we find for developed parcels. For example, housing prices could rise in the region that hosts a CH because of (anticipated) reductions in regional housing supply (Sunding, Swoboda, and Zilberman 2003; Kiel 2005). Given that most CHs and their 5 km buffers make up a small part of a regional housing market, this market price adjustment would cover the CH, its buffer, and the area beyond. In other words, an empirical analysis based on our definition of nearby non-CH areas can identify any price premium among home buyers wanting to live within a CH area versus immediately outside the CH area but will not be able to identify the more geographically widespread price impacts of any anticipated reduction in the region’s future housing supply.

To summarize, when using land prices as a metric of regulatory impact, the CH regulation has inconsistent impacts. The CH regulation is a biodiversity protection program that—when evaluated separately from the larger ESA regulation it is part of—only sporadically creates the costs that theory suggests it can generate. We wonder whether the regulation creates much biodiversity protection at all. We assume that an effective biodiversity protection regulation would consistently generate observable costs; we are skeptical of the efficacy of a regulation that appears to create little to none.

Analysis Caveats

We already noted that our DD estimators are unbiased estimators of the CH’s ATT if and only if various data and modeling assumptions hold. If the data we use in this analysis consistently violate the various assumptions needed for causal identification, we may simply be unable to reveal any “true” negative unbiased DD estimators. As we also noted, if the CH regulation generally does not generate immediate border effects but tends to affect regional market prices via changes in regional demand and supply of land and houses, then our modeling approach will register little to no regulatory impact. In other words, our approach to modeling CH regulatory impacts may not match the regulation’s actual pattern of economic impacts.

However, even if all the assumptions needed for causal identification hold and our modeling approach is consistent with CH regulation dynamics, there are other reasons to suspect that the DD estimators generated by our models do not precisely measure the true economic impact of the CH regulation. We detail some of these reasons below for the sake of transparency. Future research on the economic impact of CH would be more accurate and precise if it corrects these problems.

Many have claimed that the CH’s regulations and requirements dampen developer willingness to pay for undeveloped land in CHs. However, a more nuanced model of CHs’ impact on undeveloped parcel values would surmise that only some developable parcels would likely require the developer to implement reasonable and prudent alternatives to avoid destruction or adverse modification of CH, and therefore only these parcels would have dampened prices. Therefore, a critical unobserved variable in our analysis of undeveloped parcel prices in CH areas is Mjt, parcel j’s probability of triggering CH regulations if considered for development (Appendix B).

An additional identification problem is created by the uneven overlap of CH and the ESA’s other regulations. The destruction or modification of occupied habitat is also prevented by ESA regulations. Therefore, CH regulations would be superfluous in occupied habitat. However, CH can also cover unoccupied habitat. The take and jeopardy provisions of the ESA are less relevant in unoccupied habitat (Maura Flight, pers. comm., June 25, 2021). Therefore, in unoccupied habitat areas, the CH regulation may be the only relevant barrier to habitat destruction or modification. A potentially more regulation-appropriate version of our model would treat CH areas that include unoccupied habitat as treated areas and all other ESA-affected areas, including CH areas encompassing occupied habitat, as the control areas. Unfortunately, we are not aware of maps that delineate occupied and unoccupied habitat in CH areas. (These maps could also help in the construction of the currently unobserved Mjt, parcel j’s probability of triggering CH regulations if considered for development.)

Selection bias likely affects our model estimates. CH proposals or finalizations that have been revised several times (what we call complex CHs) due to new information, new scientific data, political pressure, or court cases are not included in our study, because we do not have the data to identify all treated sales over time. However, we suspect that these complex CHs are likely to have had a greater impact on land prices than the simple CHs that we currently include in our study (see Klick and Ruhl 2020). Presumably, their imposition of high economic cost is one of the main reasons for complex CHs’ unsettled path to finalization (Appendix C).21 Therefore, because we do not include the potentially more expensive CHs, our estimates of the DD coefficients μ and ω may underestimate the actual penalty that CH imposes on parcel values.

Furthermore, almost all undeveloped parcels that were bought for subdivision are not included in our dataset because most of our parcel maps date from 2019. Therefore, we were not able to link the sale of an undeveloped parcel in ZTRAX, for example, from 2011, that was later developed by 2016 into 10 five-acre plots, each with a house (we only observe the sales of the five-acre plots). If the CH regulation tends to adversely affect the prices of undeveloped parcels that are later subdivided, then our model may underestimate the actual penalty that CH imposes on undeveloped parcel values.

Imprecise digital CH maps may also hamper our ability to precisely identify the impact of CH on parcel prices. During our research, we learned that some of the digital maps of CH areas available from the FWS’s website only approximate the actual CH areas (Maura Flight, pers. comm., June 25, 2021). Designated CH areas are described with coordinates and printed maps in FR notices. In some cases, the digital representation of these areas does not exactly follow official boundaries as laid out in the FR. Our analysis likely has some false positives (sales we classified as treated that were not) and false negatives (sales that we classified as not treated that were).

We believe some of these estimation issues could be resolved if the FWS expanded on the data it makes available to the public. First, the FWS should publish digital maps of every proposed CH, every proposed revision, and every final CH, not just the latest final CH. This would allow future researchers to identify the impact of CH more precisely on parcel prices. Second, the FWS should verify that the digital maps on their website exactly adhere to the boundaries published in FRs. This would reduce measurement error in our estimated models. Third, each published CH map should specify known habitat areas, occupied habitat, and unoccupied habitat. This addition could better align our DD models to CH’s regulatory impact.

Acknowledgments

The authors acknowledge the Minnesota Supercomputing Institute at the University of Minnesota for providing resources that contributed to the research results reported in this article. Christoph Nolte acknowledges support from the Department of Earth and Environment at Boston University, the Junior Faculty Fellows program of Boston University’s Hariri Institute for Computing and Computational Science, the Nature Conservancy, and the National Science Foundation (grant 2149243). The authors also acknowledge the insights provided by Katherine Fosburgh, Maura Flight, Robert W. Paterson, the participants in the 2021 and 2022 PLACES webinars, and two anonymous reviewers. Data are provided by ZTRAX. More information on accessing the data can be found at http://www.zillow.com/ztrax. The results and opinions are those of the authors and do not reflect the position of Zillow Group.

Footnotes

  • Supplementary materials are available online at: https://le.uwpress.org.

  • 1 The U.S. National Marine Fisheries Service in the case of marine species.

  • 2 While the regulating agencies are supposed to designate a CH concurrently with listing, in many cases this does not happen. As of 2019, only 891 of the listed 1,600 species had finalized CHs. Listed vertebrates are significantly more likely to have designated CH than are listed invertebrates or plants (Fosburgh 2021). In addition, Langpap (2022) found that a listed species is more likely to have designated CH if a lawsuit claiming inadequate protection of the species has been filed.

  • 3 An example of an exclusion due to the latter type of cost is the FWS’s decision to exclude some defined Canadian lynx CH area from final designation in Maine to maintain a “good relationship” with the state’s forest industry (Fosburgh 2022).

  • 4 Fosburgh (2022) found that 90 final designated CHs areas covered 54,353,125 acres, of which 9,263,698 acres or 17.04% was private land. Federal government, local government, and tribal land made up the rest of CH areas. Given that there were 891 CH designations as of 2022, it would be safe to assume that at least 100 million acres of private land are currently subject to CH regulations.

  • 5 Or race to develop land inside a proposed CH area before the CH is finalized.

  • 6 Auffhammer et al. (2020) describe a matching algorithm in one of their appendices. However, results with matched controls are not discussed in their main text.

  • 7 The initial dataset does not include sales that involved multiple parcels and those from Alaska and Hawaii.

  • 8 For example, the California population of the peninsular bighorn sheep (Ovis canadensis nelson) had its CH first proposed in the FR on July 5, 2000 (USDOIFWS 2000), and had this proposed CH finalized in the FR on February 1, 2001 (USDOIFWS 2001). However, on August 26, 2008, the FWS proposed reducing the population’s CH area by approximately 189,377 ha (USDOIFWS 2008). This proposed change was finalized on April 14, 2009 (USDOIFWS 2009).

  • 9 This exclusion does not include parcels covered by a multiple-species CH. We do not eliminate these parcels and their related sales because the degree of regulatory scrutiny did not change over time as it did for parcels affected by multiple, nonsynchronous CHs. Of the 45,726 treated developed parcel sales in the final dataset, 5,588 took place in multiple-species CHs. Of the 19,693 treated undeveloped parcel sales in the final dataset, 2,371 took place in multiple-species CHs.

  • 10 In this illustrative case, retention of a parcel’s sale when it was in just the first CH would be consistent with the event pattern we exploit in our causal analysis (preproposal period—proposal period—postfinalization period). However, the data-cleaning task was made simpler by eliminating all sales of parcels that were successively treated.

  • 11 By limiting our controls to those within 5 km of CH boundaries (with a few exceptions; see the text) we are not able to detect any regulatory effects that extend beyond the CH area and its buffer. For example, suppose housing prices in the larger region that hosts a CH rise because of (anticipated) reductions in regional housing supply (Sunding, Swoboda, and Zilberman 2003, Kiel 2005). Although our empirical analyses can identify any price premium among home buyers to live within a CH area versus immediately outside the CH area, all else equal, it cannot identify a uniform increase in housing prices across the wider regional real estate market that hosts the CH.

  • 12 For example, suppose CH area k had 50 and 20 developed and undeveloped parcel sales, respectively, between 2000 and 2019. Suppose k’s 5 km buffer had 300 (greater than 50 × 5) and 150 (greater than 20 × 5) developed and undeveloped parcel sales, respectively, between 2000 and 2019. In this example, CH area k’s matched control set was drawn entirely from its 5 km buffer.

  • 13 Our matching procedure means that some CHs with 5 km buffer sales have no matched control sales. Therefore, our analyses with matched controls span fewer CHs and parcel sales than our DD model estimates with unmatched controls.

  • 14 On average, the period between proposal and finalization in the FR is 501.2 days (SD = 343.9 days, median = 389 days, n = 61 CHs) for “simple” CHs with treated and matched control developed parcel sales. On average, the period between proposal and finalization in the FR is 503.9 days (SD = 341.0 days, median = 375 days, n = 70 CHs) for “simple” CHs with treated and matched control undeveloped parcel sales. See Appendix Table D1.

  • 15 µ (hat) = (E[V | X,Z,1[A] = 1[T] = 1] – E[V | X,Z,1[A] = 0,1[T] =1]) – (E[V | X,Z,1[A] = 1,1[T] = 0] –E[V | X,Z,1[A] = 1[T] = 0]). The first term represents impact of treatment on treated and the second term represents impact of treatment on control.

  • 16 Because Vjt is the log of the per-hectare real sale price, the impact of a change in 1[T]j1[A]jt is, on average, a 100[eμ-1] percent change in Vjt (in 2019 US$), all else equal.

  • 17 This finding does not necessarily contradict Auffhammer et al. (2020), as our roster of California amphibians does not include the amphibian that was the focus of their study, the red-legged frog. We dropped the red-legged frog from our study because it is a complex CH. The red-legged frog CH was first finalized in 2001, vacated in 2003, and then a new, extensively revised CH was finalized in 2006. We do not have copies of defunct CH maps, so we do not know exactly which parcel sales were treated between 2001 and 2006 in the landscape that hosts red-legged frog habitat. We dropped the red-legged frog CH and its related sales from our study.

  • 18 Similar to our general results, Geoghegan, Wainger, and Bockstael (1997) also found a positive marginal effect of distance to the nearest major road.

  • 19 For example, Kling et al. (2015) found that proximity to national forest land has no meaningful effect on housing prices on an exurban-rural landscape in Colorado. They suspect that this lack of impact is explained by the relative abundance of national forest land in their study landscape.

  • 20 Some FWS administrators state that CH does not add any additional protection for species and therefore CH designation is unnecessary and merely administrative (Armstrong 2002). According to this line of argument, the additional federal scrutiny that development activities are supposed to generate in CH areas is applied across a listed species’ entire geographic range, not just its CH area.

  • 21 Not every complex CH case is driven by economic concerns. For example, Preble’s meadow jumping mouse’s original “final” CH area was expanded 75% as a result of “habitat considerations.”

References