Abstract
More than 80 governmental entities concerned about sprawl, open space, and farmland have implemented purchase of development rights (PDR) programs preserving 2.23 million acres at a cost of $5.47 billion. Are PDR programs effective in slowing the rate and acres of farmland loss? Employing propensity score matching methods and a 50-year, 269-county data set for six Mid-Atlantic states, we find empirical evidence that PDR programs have had a statistically significant effect on farmland loss. Having a PDR program decreases a county’s rate of farmland loss by 40% to 55% and decreases farmland acres lost by 375 to 550 acres per year. (JEL Q24, Q28)
I. INTRODUCTION
Concerns about suburban sprawl, open-space loss, and farmland conversion have led states, counties, municipalities, and regional groups to institute programs that arrest or slow land conversion. Beginning in 1978, purchase of development rights (PDR) programs have been removing the rights to convert undeveloped lands, to promote a continued resource use. These programs usually attach an easement to a property that restricts the right to convert the land to residential, commercial, and industrial uses in exchange for cash payments and/or tax benefits. The PDR programs are justified on various grounds such as promoting efficient development of urban and rural land, securing local and national food supplies, maintaining the viability of the local agricultural economy, and protecting rural and environmental amenities (Gardner 1977; Hellerstein et al. 2002). While from society’s perspective, the viability of the agricultural sector, retaining a critical mass of land, and protecting the value of environmental amenities are all important, they cannot be achieved in the long run without slowing or arresting farmland loss. Therefore, we focus on the impact of PDR programs in reducing farmland loss.1
Twenty-three states have state-level PDR programs, and 57 local governments operate PDR programs (American Farmland Trust [AFT] 2008, 2009); over 2.23 million acres are in preserved status as a result. Spending in both state and local programs to purchase these acres was $5.47 billion (AFT 2008, 2009). Citizens continue to pass ballot initiatives to generate funds to retain open space including farmland: in 2002, $5.7 billion in conservation funding was authorized; in 2006, $5.73 billion, and in 2008, $8.4 billion (Land Trust Alliance and Trust for Public Lands 2008). In 1996, the federal government developed the Farmland (and Ranchland) Protection Program to provide funding for state and local preservation programs.
While some evidence exists that PDR programs provide net benefits to society (Feather and Barnard 2003; Duke and Ilvento 2004), little evaluation has been conducted on their effectiveness in preventing the conversion of farmland. Several studies have evaluated the impact of (nonpermanent) use-value taxation programs that aim to arrest farmland loss (Blewett and Lane 1988; Gardner 1994; Lynch and Carpenter 2003; Parks and Quimio 1996). Those studies found that these programs can impact farmland loss, but their impact may be small and short term. Few studies examine the impact of the permanent easements conferred by the PDR programs. Two of these, by Lynch and Carpenter (2003) and Hailu and Brown (2007), find no impact of PDR programs on reducing farmland loss.
We study whether PDR programs reduce farmland loss in the Mid-Atlantic states using a unique 50-year, 269-county panel data set on the existence of PDR programs and farmland loss.We include both state and local PDR programs and measure farmland loss in two ways: as the rate of loss and as the number of acres lost at the county level. We find strong empirical evidence that PDR programs have slowed farmland loss.
Assessing the impact of permanent preservation through PDR programs on farmland loss can be empirically challenging. It is hard to construct the proper counterfactual, in other words, one would like to know what would have happened to the rate and acres of farmland loss in a county with a PDR program (hereafter, a PDR county) had it not implemented a PDR program. However, a PDR county cannot be in two states simultaneously, nor can a researcher randomly assign which county has a PDR program and which does not. If PDR programs are established in those counties with the highest rates of farmland loss and/or the lowest number of farmland acres, the very existence of the PDR program itself may be predicated on farmland loss. Thus assuming the program’s existence was exogenous to the rate of loss, as was implicitly done by Lynch and Carpenter (2003) and Hailu and Brown (2007), may be an explanation for the insignificant results.
Nor is simply examining acres preserved sufficient for assessing a program’s impact on farmland loss. If the PDR programs do not preserve the parcels that would be converted and instead enroll those parcels unlikely to be converted, their impact on land conversion may be insignificant. An example can be seen in a study by Lynch and Liu (2007) who find that a preservation program increases the number of acres preserved within designated preservation areas, but it had no impact on the rate of land conversion in these areas. In addition, recent evidence suggests that the positive amenities generated by preservation programs may increase the demand for housing (and thus land) near the preserved parcels. This demand may create more conversion pressure and higher housing prices, leading to even further farmland conversion. For example, Roe, Irwin, and Morrow-Jones (2004) find that preservation efforts themselves could induce further residential growth. Geoghegan, Lynch, and Bucholtz (2003) and Irwin (2002) find that housing prices adjacent to preserved parcels can increase due to the permanency of adjacent open space.
We suggest some of the empirical difficulties related to the incomplete information may be overcome by using a propensity score matching (PSM) method to estimate the impact of PDR programs on farmland loss. This method has several benefits: First, the matching protocol ensures that the PDR counties will be matched to the non-PDR counties that are most similar in terms of observable characteristics. This provides a more transparent means of decreasing the influence of outliers and dissimilar counties. Second, because not all counties are equally likely to have PDR programs, PSM incorporates covariates that may influence the existence of such a program, as well as the farmland loss, into the propensity score calculation. It can therefore avoid the weak instrument issue experienced in an instrumental variable approach. Third, a specific functional form is not assumed for the outcome equation, the decision process, or the unobservable terms. Therefore, the PSM method requires fewer assumptions than an instrumental variable approach.
II. PROPENSITY SCORE MATCHING METHOD
Assessing the impact of PDR programs is difficult because of incomplete information. While one can identify whether a county has a PDR program or not and the level of farmland loss conditional on the PDR existence, one cannot observe the counterfactual. That is: what would have happened had the county not had a PDR program. Thus, the fundamental problem in identifying the impact of PDR programs is constructing the unobservable counterfactuals for the PDR counties.
We employ the PSM method developed by Rosenbaum and Rubin (1983). PSM methods have been adopted both in studies using microlevel and aggregated data to evaluate the effect of various policies and social programs. 2 They have been used to evaluate the land value effects of farmland preservation easement restrictions (Lynch, Gray, and Geoghegan 2007, 2009), and the impact of designated preservation zones on the rate of preservation and conversion (Lynch and Liu 2007).
Define an indicator variable, D, equal to 1 if a PDR program is in operation in a county and equal to 0 otherwise. For a specific county, denote Y1 as the farmland loss if a PDR program is in operation (D = 1) and Y0 otherwise (D = 0). If one could observe the farmland loss for a county in both states, the effect of having a PDR program would equal (Y1 − Y0). Unfortunately, only Y1 or Y0 is observed for each county in reality. In a laboratory experimental context, researchers solve this problem by randomly assigning counties to be PDR or non-PDR counties, then construct an unobserved counterfactual using the randomly assigned non-PDR counties. In a natural setting, however, whether a county is a PDR county or a non-PDR county can depend on many factors and, therefore, is not randomly assigned. Matching methods construct a counterfactual, Y0, for the PDR counties using the non-PDR counties that are similar in their observed characteristics X that affect the outcome Y0. The average impact of the PDR programs on the farmland loss in the PDR counties, or the average treatment effect on the treated (ATT), is the difference in the means of the farmland loss between the PDR counties and their constructed counterfactuals.
Matching similar counties based on observed characteristics, X, becomes practically infeasible when the dimension of X is large. The PSM method proposed by Rosenbaum and Rubin (1983) addresses this issue by matching the non-PDR counties with the PDR counties based on their probability of having a PDR program. The estimated probability of having a PDR program, 
, is calculated using the observed characteristics X and serves as a summary indicator of the conditional variables. The estimated ATT thus is the expected difference in the mean farmland loss between PDR counties and their corresponding counterfactuals constructed from the matched non-PDR counties that have the same estimated propensity scores, P(D = 1⎪X):
[1]In the above equation, E(Y0⎪D = 1) is the expected unobserved farmland loss in PDR counties, and E{E(Y0|D = 0,P(D = 1|X))| D = 1} is the mean constructed counterfactual using the matched non-PDR counties with the same estimated propensity scores.
The validity of the matching method is based on the conditional independence assumption (CIA), which in our context states: whether counties have a PDR program or not is random after controlling for observed characteristics, X. The CIA requires that we include in X all factors that affect both whether a county has a PDR program and its farmland loss. Heckman, Ichimura, and Todd. (1998) relax the strong CIA condition by proposing a conditional mean independence (CMI) assumption. This assumption implies that the mean farmland loss of the PDR counties had the PDR programs not existed is the same as that of their matched non-PDR counties given the set of characteristics, X, or the estimated propensity score, P(D = 1|X). CMI holds as long as possible unobservable factors had the same impact on the farmland loss in the PDR and non-PDR counties. This condition is no stricter than the assumption from an ordinary least squares regression. It still requires us to choose a set of conditional variables that affect both farmland loss and whether a county has a PDR program. However, unobservable factors do not introduce any inconsistency as long as these factors have the same effect on the farmland loss in both PDR and non-PDR counties.
We include in our conditional variable set, X, the factors that affect both the farmland loss and the probability that the counties have PDR programs, such as agricultural profitability and viability, demand on land for nonagricultural purposes and open space, and alternative employment opportunities for farmers. By matching non-PDR counties to PDR counties with similar estimated propensity scores, P(D = 1|X), we are controlling for the effect of these factors on farmland loss. After matching, we conduct balancing tests to check if the matched counties are indeed the same on their observed characteristics. The estimated impacts of PDR programs are then calculated by taking the difference in the means of farmland loss between the two matched groups.
We first conduct matching without restriction. Specifically, we match the PDR county observations with non-PDR ones over the full sample. Using the full sample may provide the best matches, since counties in different geographic locations (states) may reach the same development stage at the same time, while counties within the same state may be at different development stages at any given time. For example, counties close to metropolitan areas may have experienced development pressure at an earlier period than more rural counties, all else the same.
Because our panel data involves a long time span, we are concerned that the economic conditions of a county, such as housing value, family income, and population density, could be very different between early and late periods. The large differences in economic conditions across periods imply that, for example, a county observation in 1973 may not serve as a good counterfactual for itself in 1992. Hence, we impose restrictions on matching to be within the same time period to check and minimize the potential bias from unobservable factors related to time.3 This restriction, however, may result in fewer PDR counties having similar non-PDR counties.
III. BACKGROUND AND DATA
Six Mid-Atlantic states (Delaware, Maryland, New Jersey, New York, Pennsylvania, and Virginia) experienced a 47% decrease in farmland between 1949 and 1997. These states were also among the first to implement a PDR program at the state or local level. The city of Southampton and Suffolk County, New York, created the first local PDR programs in the early 1970s. Maryland introduced a state-level PDR program in 1977, and by 1997, five of the six states had state-level PDR programs under which landowners could enroll their land.
PDR programs use easements to remove from farmland the right to convert to residential, commercial, and industrial uses and typically compensate landowners with monetary payments and/or income and estate tax benefits. The easements applied are perpetual and restrict all future owners from converting the parcels. The institutional structures of the PDR programs vary by the minimum criteria needed for enrolled farms (soil quality, acreage, proximity to preserved parcels), by payment mechanisms (auctions, installment payments, points earned based on parcel attributes [point systems]), by the source of funding (taxes or bonds), and by geographic specificity of the programs’ target areas. However, the easement restrictions are similar across the programs. Easement restrictions to date have been upheld by the courts (Danskin 2000), and thus these programs prevent conversion of enrolled land to developed use.
We examined both state and local PDR programs and estimate whether these programs reduce farmland loss. Data on which counties had state or local PDR programs by 1997 was collected from American Farmland Trust (AFT 2008, 2009). States and counties with PDR programs were contacted via email, regular mail, and telephone to collect information on how many acres they had enrolled in 1974, 1978, 1982, 1987, 1992, and 1997. We assign counties as being treated (a PDR county) in any time period if the county had preserved at least one acre under a PDR program. In 1974, no county had a PDR program in place and by 1997, 115 out of the 263 counties had at least one acre enrolled in a PDR program. We measure farmland loss as the rate of farmland loss and as the total acres lost at the county level.4 The two variables are calculated using the number of farmland acres5 collected from the Census of Agriculture (USDA NASS 1999, 2001) for each county and every agricultural census period6 from 1949 through 1997.7 Specifically, the number of farmland acres lost was calculated as (Lt+1 = Lt), where Lt is the number of acres in initial period and Lt+1 in the following period. The rate of farmland loss is calculated as [(Lt+1 − Lt)/Lt].
We compiled additional information from the Census of Agriculture on agricultural activities at the county level. We collected demographic information at the county level for the years 1950 through 2000 from the Census of Population and Housing (U.S. Department of Commerce 1950–1992, 1950–2000).8 Demographic variables that are calculated as a percentage change set the initial agricultural census period as the ending period of the percentage change calculation. For example, the percentage change in median housing value for time period t was calculated as (HUt – HUt − 1)/Hut − 1, where HUt is the median housing value at time t. Our analysis uses data on 263 counties and 10 agricultural census periods, which results in a total of 2,606 observations during the 50-year period.9
We hypothesize that three primary factors affect both the existence of the PDR programs and farmland loss at the county level. The first of these factors is the profitability of farming and the viability of farming sector. To proxy this, we calculate net agricultural returns per acre using the average sales value minus average expenditures. If agricultural profits are sufficiently large, landowners will continue to farm rather than converting their land. If agricultural sector is strong and viable, farmland owners may think agricultural activities have a future in the county. This confidence may decrease land conversion and increase enrollment in the PDR programs. In addition, a strong agricultural presence may result in a higher level of governmental support for a PDR program. We use the percentage of labor force in the agricultural sector, the number of farms, the total acres of farmland in a county, and the percentage of farms operated by someone who owns all of the farmland he or she farms to proxy the viability of the farming sector.
The second factor is off-farm income. Off-farm income may ensure cash flow and decrease income fluctuations. The extra security may reduce a farm household’s incentive to convert its land and increase the incentive to enroll that farm’s land in a PDR program. Off-farm income levels are proxied by the percentage of operators with more than 100 days off-farm work and the percentage of the population with a high school education.
The third factor affecting the existence of a PDR program and farmland loss is the demand for housing, that is, land conversion (nonagricultural net return), and the county residents’ willingness to pay for land preservation. We have data on whether a county has been in a metropolitan area since 1950, the county’s population density, median family income, and median housing value to proxy for this factor. On the one hand, metropolitan counties may face a higher demand for land conversion and lose farmland due to shorter commuting distance to employment centers. On the other hand, urban proximity may increase the profitability of farmland due to both the reduction in transportation costs and reallocation of land to high-value crops (Livanis et al. 2006). Furthermore, farmland may become more valuable to metropolitan counties as farmland and the related amenities become increasingly scarce. As a result, metropolitan counties may be more likely to establish PDR programs than other counties. Higher median incomes may have two impacts. First, as median family income increases, people demand larger houses on larger parcels, increasing the demand for farmland conversion. Second, residents with higher incomes may be willing to pay more to preserve the farmland amenities and support PDR programs. Densely populated counties face a high demand on housing and, thus, larger net returns to residential and commercial uses. Higher median housing value serves as an indicator for land prices and, thus, returns to farmland conversion.
Tables 1 and 2 provide the names and descriptive statistics for the variables included in the analysis for the full sample, for the counties with PDR programs, and for those without PDR programs. Table 1 presents the descriptive statistics for the entire time frame of our study (1949–1997), and Table 2 presents the data for just the period of 1978–1997. The first two columns of the tables present the descriptive statistics of the two variables that measure farmland loss for all counties. The average number of acres lost in PDR counties was 4,406 acres per agricultural census period, smaller than the 10,423 acres in non- PDR counties during 1949–1997. Similarly, the rate of farmland loss is 4.12% in the PDR counties, which is lower than the 7.51% in the non-PDR counties. Interestingly, for the 1978–1997 periods, the rate of farmland loss is 4.12% for the PDR counties but only 3.3% in the non-PDR counties, which implies that counties that have higher rates of farmland loss are more likely to have PDR programs. The PDR counties have 110,436 acres of farmland, which is fewer than the 144,169 acres in the non-PDR counties during 1949–1997.
Descriptive Statistics by the Full Sample, Counties with and without Purchase of Development Rights (PDR) Programs, 1949–1997, for Six Mid-Atlantic States
Descriptive Statistics by the Full Sample, Counties with and without Purchase of Development Rights (PDR) Programs, 1978–1997, for Six Mid-Atlantic States
We also created binary variables and include them in our conditional variable set X for the agricultural census periods 1978–1982, 1982–1987, 1987–1992, and 1992–1997. The period 1992–1997 is the excluded category. Because no counties had a PDR program before 1978, we cannot include time variables for the early years.
IV. EMPIRICAL ESTIMATION
Propensity Score Estimation
As mentioned above, the CIA (or CMI) condition requires that we choose a set of variables that affects both the existence of PDR programs and farmland loss in the PDR counties had these programs not existed. No mechanical algorithm exists that can automatically choose a set of variables that satisfies the identification conditions (Smith and Todd 2005b). Smith and Todd (2005b) summarize two types of specification tests motivated by Rosenbaum and Rubin (1983) that help choose the correct variables to be included in the vector X. The first test examines whether there are differences in the means of the variables in X between the counties that have PDR programs (D = 1) and ones that do not (D = 0) after conditioning on P(D = 1|X). The second test requires dividing the observations into strata based on the estimated propensity score. These strata are chosen so that there is not a significant difference in the means of the estimated propensity score between PDR counties and non-PDR counties within each stratum (Dehejia and Wahba 1999). We estimate our propensity scores using a random effects logit model controlling for county effects and using the variables outlined in the previous section. We use the second specification test as proposed by Dehejia and Wahba (1999, 2002).
Table 3 reports the estimation results for random effects logit model using the conditional variables. After controlling for county and time effect, our results show that the counties with high agricultural profits and more farms are more likely to establish PDR programs. The opportunities to earn off-farm income seem to positively influence the establishment of a PDR program as well. Counties with higher housing value are also more likely to establish PDR programs, as are metropolitan counties with higher median family income.
Estimated Coefficients from a Random Effects Logit Model to Compute Propensity Scores
We predict the propensity score for each county observation for each agricultural census period using the estimated coefficient from the random effects logit model. Figure 1 depicts the distributions of the estimated propensity for all 2,606 PDR and non-PDR county observations.10 The x axis indicates the estimated propensity score, and the y axis indicates the percentage of PDR and non-PDR county observations with the estimated propensity scores falling in each range. Our predictions reflect reality. The estimated propensity scores for the majority of non-PDR counties cluster around zero, while they tend to be more evenly distributed but slightly clustered around 0 and 1 for the PDR counties. Our estimated propensity scores for the PDR and non-PDR counties, therefore, are not very compatible. They are more evenly distributed for the PDR counties, but asymmetric for the non-PDR counties. For example, the estimated propensity scores for more than 60% of the non-PDR county observations fall in the interval between 0 and 0.00002, but none of PDR county observations fall in this range. The common support in which the estimated propensity scores of the two groups overlap ranges from 0.00002 to 0.999.11 Given the varying distributions of the estimated propensity score for our PDR and non- PDR counties, we need to select our matching method carefully to improve the efficiency of the estimated treatment effect.
Distributions for the Estimated Propensity Scores for Full Sample
Matching Methods and Bandwidth Selection
Several different matching methods are available. All matching estimators have the generic form for estimated counterfactuals: 
, P(D = 1|X)), where j is the index for a non- PDR county that is matched to a PDR county i based on their estimated propensity scores (j = 1, 2, …, J). The matrix, w(i,j), contains the weights assigned to the jth county that is matched to the ith county. Matching estimators construct an estimate of the expected unobserved counterfactual for each PDR county by taking a weighted average of the farmland loss for the matched non-PDR counties. What differs among the various matching estimators is the specific form of the weights. The estimators are asymptotically the same among all matching methods. However, in a finite sample, different methods can provide different estimators.
The formula for calculation of average impact of PDR programs on the farmland loss in the PDR counties, or the ATT, is 
. In the equation, N is the number of the PDR county observations, Yi1 is the farmland loss rate and acres in a PDR county i, and 
is the constructed counterfactuals for county i. The average impact of the PDR program is therefore the mean difference in the farmland loss between the PDR counties and counterfactual farmland loss from the matched non-PDR counties.
Nearest-neighbor matching pairs a non- PDR county with a PDR county whose propensity score is closest in absolute value. We use a non-PDR county repeatedly if it is “observably identical” to multiple PDR counties, given that both Dehejia and Wahba (2002) and Rosenbaum (2002) found that matching with replacement performs as well as or better than matching without replacement. Therefore, the non-PDR county observations used to compute the treatment effect are those most similar to the PDR county observations in terms of their observable characteristics.
Kernel matching and local linear matching techniques match each PDR county with all non-PDR counties whose estimated propensity scores fall within a specified bandwidth (Heckman, Ichimura and Todd 1997). The bandwidth is centered on the estimated propensity score for the PDR county. The matched non-PDR counties are weighted according to the density function of the kernel types.12 The closer a non-PDR county’s estimated propensity score is to the matched PDR county’s propensity score, the more similar the non-PDR county is to the matched PDR county, and therefore it is assigned a larger weight calculated from a kernel function defined in each method. More non-PDR counties are utilized under the kernel and local linear matching as compared to nearest-neighbor matching.
Selection of matching methods depends on the distribution of the estimated propensity scores. Kernel matching operates well with asymmetric distributions because it uses the additional data where it exists but excludes bad matches. McMillen and McDonald (2002) suggest that the local linear estimator is less sensitive to boundary effects. For example, when many observations have 
near one or zero, it may operate more effectively than other standard kernel matching. Nearest-neighbor matching, however, is more likely to lead to biased estimation if the distribution of the estimated propensity scores between PDR and non-PDR groups is not very compatible. Given that the estimated propensity scores for the non-PDR county observation are asymmetrically distributed, while for the PDR county observations are more evenly distributed for our sample, we expect kernel matching or local linear matching to perform better than nearest-neighbor matching.
Bandwidth and kernel type selection are an important issue in choosing a matching method. Generally speaking, a large bandwidth leads to a larger bias but smaller variance of the estimated average treatment effect of the PDR programs; a small bandwidth leads to a smaller bias but a larger variance. The differences among kernel types are embedded in the weights they assign to non-PDR county observations whose estimated propensity scores are farther away from those of their matched PDR county observations. As the selection of bandwidth and kernel type involve a trade-off between bias and variance, we use the leave-one-out cross-validation mechanism proposed by Racine and Li (2004) and utilized by Black and Smith (2004) to determine the best balance between variance and bias. This method helps choose the “best” matching method (a combination of matching method, kernel type, and bandwidth) that minimizes mean squared error (MSE) for the estimators given the distribution of our data, taking into account balancing objectives.
We consider three alternative matching estimators: nearest-neighbor estimator, kernel estimator, and local linear estimator. We calculate the MSEs for all the possible combinations of the three matching methods, five kernel types (epan kernel, biweight kernel, uniform kernel, tricube kernel, and Gaussian kernel), and six bandwidths (bandwidth = 0.01, 0.02, …, 0.05, 0.1). The leave-one-out cross-validation mechanism suggest that the uniform kernel matching method with bandwidth 0.02 and epan kernel matching method with bandwidth 0.02 are superior methods for constructing counterfactuals when matching without restriction or within agricultural census periods. For a detailed discussion of leave-one-out cross-validation results, see the Appendix.
Balancing Test
After matching, we check again whether the two matched groups are the same on their observed characteristics. If unbalanced, the estimated ATT may not be solely the impact of PDR programs. Instead, it may be a combination of the impact of the PDR program and the unbalanced variables. We rely on two of the balancing tests that exist in the empirical literature: the standardized difference test and a regression-based test.13 The first method is a t-test for the equality of the means for each covariate in the matched PDR and non-PDR counties. The regression test estimates coefficients for each covariate on polynomials of the estimated propensity scores, 
for l = 1, 2, 3, and the interaction of these polynomials with the treatment binary variable, 
. If the estimated coefficients on the interacted terms are jointly equal to zero according to an F-test, the balancing condition is satisfied.
The two balancing tests give us similar results. The balancing criteria are satisfied for most of our key covariates for matching without restriction. However, when matches are restricted to within the same time period, balancing is achieved only when matching within the common support [0.00002, 0.999]. The only variable that fails the balancing test for the matching protocol using the full sample is the number of farms. For details of balancing test results for the periods 1949–1997 and 1978–1997, see Tables A1 and A2 in the Appendix.
V. RESULTS
We compute the estimated impacts of PDR programs, the ATTs, for two time periods: 1978–1997 and 1949–1997. Between 1949 and 1978, states began to introduce preferential or use-value property taxation programs but did so at varying points in time. By 1978, all six states had some type of preferential taxation program. The introduction of these preferential taxation programs could confound the results for the 1949–1978 time frame. In addition, prior to 1978, no state had established and enrolled land in a PDR program. Therefore, we believe that a better ATT estimate that is not confounded by these factors could be derived from the post-1978 time period and focus on the results from this subsample. Our ATT estimates for the rate of farmland loss and the number of acres lost appear in Table 4 (see Table A3 in the Appendix for the results for 1949–1997). The bootstrapped standard errors are reported in parentheses under each estimated treatment effect of the PDR programs in Table 4.14
Average Treatment Effect of Purchase of Development Rights (PDR) Programs on the Rate of Farmland Loss and Farmland Acres Lost during 1978–1997: Matched over Full Sample and Restricted to within Same Time Period
For the rate of farmland loss under all the matching strategies, the estimated average impacts of PDR programs range from −0.031 to −0.041. The results suggest that the existence of a land preservation program in a county reduces the rate of farmland loss by 3 to 4 percentage points on average. Given that the average rate of farmland loss per time period is 7.35% in the full sample, this is a 40% to 55% change in the rate. The change is an even larger percentage for the subsample of 1978–1997, which has an average rate of farmland loss of 3.4%.
For the number of acres lost, the average treatment effects of PDR programs in PDR counties during 1978–1997 period range from −1,876 to −2,753 acres per agricultural census period. This suggests that the PDR counties lost fewer acres per year, 375 fewer acres on the low end and 550 fewer on the high end, than similar non-PDR counties.15 This effect is equivalent to stopping two or three farms in our study area from being converted, given that the average farm size is around 180 acres. Compared to the average acres lost per county per agricultural census period, 10,000 acres, the PDR programs reduce the farmland acres lost by 20% to 30%.
The average treatment effects of the PDR programs during 1949–1997 are very similar to those from 1978 through 1997 and are reported in Appendix Table A4. The average reductions in the rate of farmland loss of each matching protocol from 1949 to 1997 are the same as those from 1978 to 1997. The average reduction in the acres of farmland loss ranged from −2,600 to −2,900 for matching without restriction. The results for restricting matches within time period for 1949 to 1997 are exactly the same as those from 1978 to 1997, which is not surprising since all the counties established their PDR programs after 1978. The similarity of the average treatment effect from 1949 to 1997 and from 1978 to 1997 suggests that unobserved factors varying across the time period before 1982 did not have a significant impact on farmland loss. Given that no county had a PDR program with enrolled acreage before 1978, we had some concerns about the potential unobservable factors related to the early period when computing the propensity scores. However, beyond the similar estimated propensity scores for the earlier observations, these earlier observations tended to be assigned small weights in calculating the counterfactuals.16
VI. CONCLUSIONS
The two existing studies that look at the effectiveness of PDR program found no impact of PDR programs on farmland loss. If a high rate of farmland loss is the reason that a county implements a PDR program, one must take into account the identification problem that this simultaneity generates. Using the PSM method to compare farmland loss among counties with and without PDR programs, this analysis finds that PDR programs have reduced farmland loss.
Our specification includes variables that affect both farmland loss and the existence of a PDR program. The standardized difference test and balancing in a regression framework suggest that the average treatment effects are estimated using balanced counties, that is, the PDR counties and non-PDR counties that have similar characteristics on variables of interest. Our empirical results provide strong and robust evidence that PDR programs reduce the rate of farmland loss by about 3.5 to 4.5 percentage points (40%–55%) for each agricultural census period in the Mid-Atlantic area. Similarly, between 1,900 and 3,000 farmland acres were retained in farming per census period, or 375 to 550 acres (two to three farms) a year, in counties with PDR programs.
Our estimate is the average impact on the counties with PDR programs. Given that counties may have different underlying causes for their farmland loss, our results do not guarantee that instituting a PDR program will arrest farmland loss in all areas.17 Some farmland could have converted to forest, tourism, or recreational uses rather than residential or commercial uses. However, most counties with PDR programs were losing farmland to residential and commercial uses. Unfortunately, the county-level data precludes us from knowing more about the spatial distribution or fragmentation of the remaining farmland, which may have an impact on the pattern of suburban development, the open-space amenities, and the long-run viability of the agricultural sector.
Further research into the impact and the underlying reasons why these programs may impact farmland loss is important. One future research program would be to study whether the PDR programs, which focus on preserving farmland, shift developers to convert forest land at an increased level, and whether PDR programs increase or decrease the net loss of open space. Second, as we find that PDR programs reduce farmland loss in the counties that have these programs, it would be interesting to understand through what channel the PDR programs reduce farmland conversion— specifically, whether PDR programs impact the density of housing on the farmland that a county continues to convert and/or induce rejuvenating cities and local towns and/or stimulate in-fill development. Third, as preserved farmland stays in agriculture forever, it would be interesting to find out if the preserved land has remained in active farming and thus the programs have had some impact on agricultural viability.
Acknowledgments
Support for this project was provided by the Harry Hughes Center for Agro-Ecology, Inc., and the Center for Smart Growth Education and Research. We would like to thank Liesl Koch and Janet Carpenter for their research assistance. In addition, the project has benefited from the comments of John List, Jeffrey Smith, Andreas Lange, Erik Lichtenberg, Barrett Kirwan, Laura Taylor, Daniel Phaneuf, and Wally Thurman. As always, any errors remain the full responsibility of the authors.
Appendix
Results for Using the Cross-Validation Method to Choose the Matching Method, Bandwidth, and Kernel Type
We find several interesting results for matching without restriction. First, the nearest-neighbor estimator performs worse than the kernel matching and local linear matching for all kernel types. The MSEs for nearest-neighbor matching, which are around 0.037, are much larger than those for the other matching methods, which range from 0.013 to 0.017. This result is consistent with other empirical exercises that found the nearest-neighbor matching provided a worse result with an asymmetrically distributed estimated propensity score for the control group. Second, while tricube local linear matching with bandwidth 0.04 and above performs a bit better than kernel matching (0.013), local linear matching with other kernel types performs worse than kernel matching with all kernel types. However, the difference in MSE is very small, especially for epan kernel matching and uniform kernel matching with bandwidth 0.02 (0.015). This suggests that the two methods perform similarly even though the distributions of our estimated propensity score are clustered around 0 and 1.
For matching within time period, we find again that the MSEs for nearest-neighbor (0.037) are much larger than those for most kernel and local linear matching (0.012 to 0.11). However, the local linear matching generally performs worse than kernel matching for all kernel types. The MSEs for local linear matching (0.0123 to 0.11) are larger than those for kernel matching (0.0121 to 0.0126) for all kernel types except for kernel type tricube. Third, the MSEs for kernel matching across different bandwidths are very similar. Due to the similarity in performance for matching without restriction and that local linear matching performs worse for matching within time period, we rely on the uniform kernel matching with bandwidth 0.02 and epan kernel matching with bandwidth 0.02 to construct counterfactuals for both matching scenarios.
Balancing Test for the Distribution of the Variables between Matched Purchase of Development Rights (PDR) Counties (X1) and Non-PDR (X0) Counties for Observations 1949–1997: Covariates That Are Not Balanced
Balancing Test for the Distribution of the Variables between Matched PDR (X1) and Non-PDR (X0) Groups for Observations after 1978: Covariates That Are Not Balanced
Sensitivity Analysis
The PSM method potentially provides more reliable results than a standard regression method by comparing PDR and non-PDR county observations that are similar to each other, explicitly excluding outliers, and estimating the treatment effect on the treated non parametrically. However, the PSM method can provide biased estimators if there are unobservable variables that are not included, and these unobserved factors have a differentiated impact on counties with and without PDR programs. Therefore, we also conduct a sensitivity analysis by looking at Rosenbaum bounds and hidden bias equivalents (Rosenbaum 2002; DiPrete and Gangl 2004).18
Average Treatment Effect of PDR Programs on Rate of Farmland Loss and Farmland Acres Lost during 1949–1997: Matched over Full sample and Restricted to within Same Time Period
Rosenbaum bounds is a signed rank test that assesses the potential impact of hidden bias arising from potentially unobserved variables associated with both having a PDR program and the rate of farmland loss variables. It assumes that the strength of the impacts from unobservable factors on having a PDR program and farmland loss is the same. Thus this approach is relatively conservative and will find bias even if the strength of unobservable factors on the farmland loss is not as strong as the test assumes.
The estimated propensity score of a PDR county and non-PDR county with identical characteristics (X) should be equal if all the relevant characteristics that affect both having a PDR program and farmland loss are included in the propensity score model. The presence of the unobserved variables leads to differences between the propensity scores of PDR and non-PDR county observations with identical characteristics. As a result, the odds ratio of a matched pair of PDR and non-PDR county observations based on these characteristics will no longer be equal to one. The larger the effect of an unobserved variable on having a PDR program, the larger the difference between the odds ratio and one will be.
Rosenbaum shows that the odds ratio for matched pairs is bounded by the function of the strength of the effect. Therefore, a signed rank statistic of each strength level has its upper and lower bounds and their corresponding p-values. One can determine a critical level of the strength of effect for a 95% confidence interval. If the unobserved variables affect having a PDR program and/or farmland loss to a higher degree than the critical effect strength, the average treatment effects could include zero. (see Rosenbaum [2002] and DiPrete and Gangl [2004] for more information).
Beyond finding the upper and lower bounds, following DiPrete and Gangl (2004), we also calculate the hidden bias equivalents on key covariates. Table A4 reports the upper and lower bounds for kernel matching with epan kernel type with bandwidth equal to 0.02 for matching without restriction, as well as the hidden bias equivalents.19 The threshold gamma measures the effect strength of unobservable variables on treatment assignment and equals 1.92 for the rate of farmland loss. Thus the statistical significance of the ATT for the rate of farmland loss would be called into question if the odds ratio of having a PDR program between the treated and control groups differs by more than 1.92. However, the ATT can still be significant if the effect of the unobservable variables on having a PDR program is greater than the effect on farmland loss.
We calculate the hidden bias equivalents on three key variables: total acres of farmland in a county, net agricultural profit per acre, and median housing value. At the critical level of gamma for the rate of farmland loss, any unobserved variable would have to have the same impact as changing these three key variables by 31,000 acres (22%) for total acres of farmland, by $800 (36%) for net profit per acres, and by $5,810 (10%) for median housing value. For farmland acres loss, the critical threshold gamma is 1.72. The hidden bias equivalents would be similar to a change of 24,000 acres (17%) in total acres of farmland, $600 (29%) in net profit per acre, and $4,710 (8%) in median housing value. These hidden bias equivalents suggest our ATT results are not very sensitive to changes in key variables or potential unobserved variables.
Rosenbaum Bounds and Hidden Bias Equivalents: Epan Kernel Matching with Bandwidth=0.02 and Matching without Restriction
Average Treatment Effect Estimation Using Wooldridge Approach (2002)
Regression Estimation and Average Treatment Effect
While the ATT effect is significant, it cannot be generalized to the entire population due to self-selection concerns. An average treatment effect (ATE) is an expected effect of treatment on a randomly selected county, but it requires more restrictive assumptions. To check how general our estimators are and how well our estimation of ATT addresses the self-selection issue, we estimate the ATE of PDR programs in a regression framework following Wooldridge (2002). This model includes the binary variable indicating whether a county has a PDR program, the estimated propensity scores, and a set of variables that affect outcomes. The estimated propensity score is expected to control all the information in the variables that is relevant to estimating the treatment effect.
We specify a random effects model and include time dummies for periods after 1978 to control for time effects. We estimate the random effects regression for both the full sample and a post-1978 subsample. We do not remove outliers or those observations that fall out of the range in which the estimated propensity scores for PDR and non-PDR counties overlap in this exercise (the common support).
For the rate of farmland loss, the estimated coefficient for the PDR program indictor is −0.024 (standard error is 0.011) for the full sample compared to the ATTs of −0.034 to −0.040 (Table A5). The PDR program coefficient is −0.015 for the post-1978 subsample regression compared to the ATTs of −0.035 to −0.045. The estimated coefficient on the PDR program indicator in the random effects model for acres of farmland lost is insignificant for the full sample. For the post-1978 subsample, it is statistically significant and equals −1,487 acres compared to the ATT of −2,013 to −2,284 acres.
On the whole, the results under both approaches are similar, with the ATE being slightly smaller. We therefore conclude that our estimation can be generalized to the whole population, and the self-selection issue is well addressed.
Footnotes
The authors are, respectively, postdoctoral research associate, Center for Environmental and Resource Economic Policy, Department of Agricultural Economics, North Carolina State University; and professor, Department of Agricultural and Resource Economics, University of Maryland.
↵1 While citizens may support these programs to retain open space rather than farmland or forest per se, they are willing to pay to retain the implicit services provided by these (open-space) lands.
↵2 2 The PSM method has been applied to job training programs (Heckman, Ichimura, and Todd 1997; Dehejia and Wahba 2002; Smith and Todd 2005a), labor market effects of college quality (Black and Smith 2004), impact of business improvement districts on crime rates (Brooks 2008), the county-level plant birth effects of environmental regulations (List et. al 2003), and land market effects of zoning (McMillen and McDonald 2002; Liu and Lynch 2011).
↵3 We also attempted to match within each state in order to control for heterogeneity across states. Our matching exercise failed to meet balancing tests because PDR counties within states that have state-level programs could find few or no similar non-PDR counties. For example, all 3 of the 3 counties in Delaware had farmland preserved by 1997, 20 out of 23 counties in Maryland had farmland preserved by 1987, 15 out of 20 counties in New Jersey had farmland preserved by 1992. The estimated ATTs could be biased when matching within state but are larger than the estimated ATTs when matching without restriction and matching within time period. It is possible, after controlling for state and unbalanced covariates, a significant impact of farmland preservation on the rate of farmland loss would be found; we just cannot definitely assign causality to the PDR programs using the available data.
↵4 The agricultural census does not report to what use farmland has been converted once it leaves agriculture. Some farmland may have reverted to forest, tourism, or recreational uses, thus the loss of farmland cannot be automatically attributed to the loss of open space, and in some cases this land could be returned to farmland without excessive cost. Therefore, the farmland loss here may be highly correlated with but is not equivalent to farmland conversion to a developed use.
↵5 Farmland is defined by the U.S. Agricultural Census to consist of land used for crops, pasture, or grazing. Woodland and wasteland acres are included if they were part of the farm operator’s total operation. Conservation Reserve and Wetlands Reserve Program acreage is also included in this count.
↵6 For the ease of exposition, we refer to an “agricultural census period” but recognize that these periods represent either four or five years.
↵7 7 We attempted to extend our data to the 2002 Census of Agriculture. However, because the census is now adjusting the data to deal with nonresponses, the data in 2002 were not comparable to those in 1949 through 1997.
↵8 Because the Census of Population and Housing is conducted every 10 years, we adjusted their data to coincide with the years of the Census of Agriculture, for which data are collected every four to five years. We assumed that the variables changed at a constant rate between the population and housing census data years. This constant change assumption was used to interpolate the data to the year the agricultural census was collected.
↵9 Counties with fewer than five farms in 1949 were excluded from the entire analysis: Bronx, Queens, Richmond, Kings, and New York counties of New York state, and Arlington County of Virginia. Independent cities of Virginia are also included in the analysis. In several cases, due to either aggregation in data or actual boundary changes during the study period, counties and/or independent cities have been combined for this analysis.
↵10 The diamond and square lines reflect the percentage of county observations whose estimated propensity scores fall in each range for PDR and non-PDR county observations. More than 60% of the estimated propensity scores for the non-PDR counties fall in the range of 0–0.05. In order to improve the visibility of the frequencies in other ranges, the y axis is limited to 0–0.08.
↵11 The lower bound for common support is the maximum of the minimum of estimated propensity scores for PDR and non-PDR county observations; the upper bound is the minimum of the maximum of the estimated propensity scores for PDR and non-PDR county observations.
↵12 A kernel function is a weighting function used in nonparametric estimation techniques. It is usually used to estimate random variables’ density functions, or the conditional expectation of a random variable. The following are the five kernel functions that are widely used: epan kernel, normal kernel, biweight kernel, tricube kernel, and Gaussian kernel.
↵13 Another test that has been used in the literature is the Hotelling test, which tests the joint null of equal means of all of the variables included in the matching between the PDR counties and the matched non-PDR counties. Smith and Todd (2005b) found that in some cases this test incorrectly treats matched weights as fixed rather than random. Therefore we do not use this balancing test.
↵14 We use a bootstrapping procedure to construct the standard errors for the average treatment effect. We make 2,000 independent draws from the participating and nonparticipating observations and form new estimates of the treatment effect for each draw. The bootstrap standard error estimate is the standard deviation of the 2,000 new values for the estimated treatment effect of the PDR programs on the PDR counties.
↵15 Recall that these census periods could be four or five years. For the period of 1978–1997, one out of four agricultural census periods was four years (1978–1982) and the remainder were five years each. We thus divide our estimated ATTs by five to compute average annual effects.
↵16 We also calculate Rosenbaum bounds, which is a sensitive analysis proposed by Rosenbaum (2002) and hidden bias equivalent suggested by Diprete and Gangl (2004) for our matching with the no-restriction scenario. Our sensitivity analysis suggests that key characteristics that affect farmland loss would have to change from 8% to 36% to call the results into question. We also calculate an average treatment effect or the impact of PDR program on the farmland loss for both PDR and non-PDR counties using the approach proposed in Wooldridge (2002). The regression approach returns smaller but similar impacts as our estimated ATTs for the PDR counties. Both analyses therefore suggest that our results are robust, and unobserved factors, if any, do not have much impact on our estimations (For details of the sensitivity analysis and regression results, see the Appendix.)
↵17 For example, some counties in the analysis lost farmland because they lost population, rather than because the land was being converted to housing.
↵18 There are other strategies that assess the impact of hidden bias, including the IV approach proposed by DiPrete and Gangl (2004), which is less conservative than Rosenbaum bounds approach. We use Rosenbaum bounds as it is the most appropriate for our problem.
↵19 Given that fact the Rosenbaum bounds approach does not deal with stratified or cluster samples, we are unable to conduct a sensitivity analysis for our matching within time periods.
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