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Real Estate Research provided analysis of topical research and current issues in the fields of housing and real estate economics. Authors for the blog included the Atlanta Fed's Jessica Dill, Kristopher Gerardi, Carl Hudson, and analysts, as well as the Boston Fed's Christopher Foote and Paul Willen.

In December 2020, content from Real Estate Research became part of Policy Hub. Future articles will be released in Policy Hub: Macroblog.

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May 5, 2010

Can we identify foreclosure contagion effects?

Negative externalities of foreclosures are the primary reason that policymakers focus on implementing policies to avert foreclosures and keep families in their homes. If the costs of foreclosures were completely internalized by the households experiencing them, then the focus would likely be on a different set of policies—for example, providing rental housing assistance or counseling on how to rebuild credit histories. Despite their importance, the empirical evidence of negative externalities is extremely tenuous, because they are so difficult to measure accurately. The papers that have tried have, for the most part, found huge effects. One of the most-cited papers in the literature was written by Dan Immergluck and Geoff Smith. They looked at the Chicago housing market in the late 1990s and found significant negative effects of foreclosures on nearby property values: *

Cumulatively, this means that, for the entire city of Chicago, the 3,750 foreclosures that occurred in 1997 and 1998 are estimated to have reduced nearby property values by more than $598 million, for an average of $159,000 per foreclosure. This does not include effects on the value of condominiums, multifamily rental properties, and commercial buildings.

This is an enormous effect, and right away it should make us slightly skeptical because, like most papers that have attempted to estimate these externalities, it is based on a hedonic regression model. For readers who are not close to the academic housing literature, a hedonic regression model is simply a cross-sectional regression of housing transaction prices on characteristics of the house and neighborhood. The methodology can be very useful for measuring the price of certain housing characteristics (for example, how much an extra bathroom or bedroom is worth), but it is not so useful in measuring the contagion effect of foreclosures because it does not solve two severe econometric issues: a reverse causality problem stemming from the fact that declines in housing prices result in higher foreclosure rates (the recent crisis for example!), and the problem that there are likely many unobserved neighborhood characteristics that are correlated with both housing prices and the number of foreclosures in a given neighborhood.

In a recent paper published in the Journal of Urban Economics, John Harding, Eric Rosenblatt, and Vincent Yao try to overcome these econometric issues by employing the repeat-sales methodology that is usually used to estimate house price indices. This model uses the difference in sale prices for repeat transactions of the same properties to estimate the average trend of house prices in a given area. By taking differences, all of the characteristics of a property and neighborhood that do not change between the sales drop out, and so we do not need to account for them. The only characteristics that we need to worry about are those that vary over time (between sales).

Harding et al. make a slight modification to the repeat-sales methodology by including as an additional covariate the number of foreclosures surrounding a property in the regression. In this respect, the model becomes a hybrid between a repeat-sales regression and a hedonic regression. Most importantly, this methodology can control for the average trend in prices in an area to at least partially address the reverse causality issue—price declines, through their effect on equity positions, are causing increased foreclosures. In addition, because time-invariant property and neighborhood characteristics fall out of the regression, omitted variable bias (the possibility that there are unobserved variables correlated with foreclosures and house prices) is less of an issue, although it could still be a problem if there are time-varying unobserved variables that are correlated with both foreclosures and house values.

Findings support significant but reduced negative externalities
Using data from seven markets—Los Angeles, Atlanta, St. Louis, Charlotte, Las Vegas, Columbus, and Memphis—the authors find significant negative effects of foreclosures on property values, but the effects are smaller than those previous studies have found. According to the authors' estimates, the peak discount of a property's value due to a nearby foreclosure is about 1 percent, and this effect diminishes quickly as the distance to the foreclosure increases. The authors interpret these results to be contagion effects that largely come from poor aesthetics resulting from the deferred maintenance and neglect of properties in the state of foreclosure. In the conclusion, they state (p. 178): "We interpret these different patterns as suggesting that the negative externality from immediate neighbors is attributable to property neglect and uncertainty about the future owner."

In our opinion, this paper is a significant improvement over the previous literature, as it includes a number of methodological improvements over and above its use of the repeat-sales method. With their data, the authors are able to pinpoint two aspects of foreclosed properties that the previous literature has not been able to identify. First, the authors can identify the particular legal phase of any foreclosure proceeding. That is, they know when a lender has filed the initial foreclosure documents, when it has taken legal possession of a house, and when it has sold a house to a new owner. Second and perhaps most important, the authors are able to geocode the location of each foreclosure relative to any house that contributes observations to the repeat-sales dataset. The authors then draw four concentric rings with different radii (0–300 feet, 300–500 feet, 500–1,000 feet, and 1,000–2,000 feet) around each repeat-sales transaction and count the number of foreclosures in each ring. Consequently, in their empirical regressions, the authors can control for the distance between a repeat-sales transaction and any surrounding foreclosures, as well as account for the particular phase of the foreclosure process for each house in each ring. Consistent with the intuitive concept of contagion, the authors find that the negative effect of a foreclosure on the prices of other homes diminishes with distance. Moreover, the negative effect is strongest around the time of the foreclosure auction/sale and the real-estate owned (REO) sale, as opposed to the time period before the auction/sale. This finding also makes sense because the time after the formal foreclosure and before the REO sale is when the property is most likely to be in a state of deferred maintenance.

True contagion effects may be even smaller
The paper's empirical findings that both distance and the phase of the foreclosure process matter are not only very intuitive, but they also provide quite a bit of evidence in support of the contagion hypothesis. But for reasons we describe below, we believe the true effects of contagion may be even smaller than the reduced effects that the authors find.

First, there could be significant measurement error causing an upward bias in their estimates of the contagion effect. The authors estimate separate regressions for each of the seven Metropolitan Statistical Areas (MSAs) in their sample and are thus able to control for average price appreciation at the level of the MSA. However, an MSA is a relatively large geographical area that includes many heterogeneous areas. For example, in the Boston/Cambridge metro-area there are wealthy areas like Brookline and very poor areas like Dorchester. House price trends were very different in these areas, and foreclosure levels were also extremely different. Not controlling for these different trends could bias the estimates of the contagion effect. For example, since Dorchester experienced significantly more house price depreciation than the average area in Boston, the residuals corresponding to properties in Dorchester in the regression will be mostly large and negative. In addition, Dorchester experienced significantly more foreclosures. If the larger price declines caused the increased foreclosures in Dorchester (and likewise the smaller price declines caused the lower foreclosure numbers in Brookline), then the residuals will be correlated with the number of foreclosures, and the contagion estimate will be biased upward. One way to try to address this problem would be to estimate the repeat-sale regressions at a more disaggregated level, such as the town/city level or even at the ZIP code level.

Another potential problem comes in the way the authors treat REO sales. REO sales are not used in the construction of the repeat-sales pairs and thus are not reflected in the independent variable in the regressions. This is a normal assumption to make when constructing repeat-sales price indices, with the rationale being that distressed sales may not reflect true market prices. This approach implies that the estimates of the average MSA price trends in the regressions do not reflect foreclosure sales. But, if foreclosure sales do lower sale prices of non-distressed properties through channels independent of contagion, such as by increasing the supply of houses on the market, and the price declines result in more foreclosures (through the channel discussed above), then the estimated contagion effect will be biased upward. Basically, this would introduce measurement error into the price trend, which would in turn be correlated with the foreclosure contagion variables in the regression. However, the authors could easily check for error by simply including REO sales in the repeat-sales sample to see how the contagion estimates are affected.

Finally, as the authors acknowledge, there could be some omitted time-varying property or neighborhood characteristic that is correlated with both the residuals and the number of foreclosures surrounding a property. The authors try to deal with this issue by placing restrictions on their sample of repeat-sale pairs to eliminate properties that have likely changed significantly over time, and find the results to be robust to such changes. This finding certainly takes care of property characteristics that may be changing significantly over time and adding (or subtracting) value from the property, but it does not control for neighborhood characteristics.

The authors also use an instrumental-variables (IV) strategy whereby they try to find variables that explain the number of foreclosures but that aren't correlated with unobserved variables explaining house values in a given area. For instruments, they use FICO scores (90th percentile of the distribution), loan-to-value (LTV) ratios (90th percentile of the distribution), homeowner income (median), property size, and the stock of housing. They estimate the IV regression for one MSA (Los Angeles) and find that their results do not substantially change. Based on the results of the IV estimation, the authors conclude that omitted variables are not a problem. However, this particular exercise isn't completely convincing, because if the first critique above is a problem (not having a disaggregated measure of average house price appreciation), then the instruments will likely be correlated with the regression residuals. To see this, think about our Dorchester/Brookline example from above. Properties in Dorchester will have large negative residuals in the regression. In addition, since Dorchester is a lower-income area, the credit score distribution of its homeowners is likely lower than the average area in the Boston metro-area, the LTV distribution likely higher, and median income likely lower. In contrast, Brookline is probably the opposite in terms of the credit score, LTV, and income distributions of its homeowners. Thus, the regressions residuals will be correlated with the instruments, and the IV estimation will not solve the underlying econometric issues.

Paper is a nice starting point
Despite these econometric issues, the pattern of the findings seems to imply a contagion effect, even if the quantitative magnitude might not be measured accurately. As we discussed above, the authors go to great lengths to control for the distance from foreclosed properties as well as for the different phases of the foreclosure process, and estimate a very flexible specification for these variables. For example, they find very little effect from properties that are a year away from foreclosure and a much larger effect between the time of foreclosure sale/auction and the eventual REO sale. In addition, they find that the effects from foreclosures near the property (within 300 feet) are much stronger than the effects from foreclosures farther away (beyond 500 feet).

As a whole, we think this paper is an important contribution to the literature, as its econometric specification is much more robust and flexible than prior externality studies. There are still important econometric issues that future research must address in order to really pin down the quantitative magnitude of the effect of nearby foreclosures on the value of a non-distressed property, but this paper provides a nice starting point.

By Kris Gerardi, research economist and assistant policy adviser at the Atlanta Fed (with Boston Fed economists Christopher Foote and Paul Willen)

*In addition to effects on surrounding property values, foreclosures have been found to have negative impacts on other neighborhood characteristics such as vacancy rates and crime rates.