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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.

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February 11, 2011

Other conceptual and data issues

1. The border-discontinuity approach is not a true regression-discontinuity exercise
A regression-discontinuity design in this context would correspond to a scenario in which there is a discontinuous treatment effect of foreclosures at the state border. However, this does not necessarily appear to be the case. There is no reason to expect that foreclosures on one side of the border will not influence prices (or other outcomes) on the other side of the border. If the story is about foreclosure contagion effects, this will certainly not be the case. A cluster of foreclosures in Florida that is right next to the Florida/Georgia border should be expected to exert the same effect on property values 1/10 of a mile from the border on the Georgia side as it will 1/10 of a mile from the border on the Florida side.

If the story is instead about a supply effect from foreclosures (i.e. that a cluster of foreclosures increases the supply of houses in a market, which puts downward pressure on prices), then one would have to argue that the housing market immediately across the Georgia side of the border is separate from the housing market immediately across the Florida side of the border. But if homes on either side of a state border really are part of the same housing market, then foreclosures on one side of the border will influence prices on the other side of the border. To be clear, this logic does not invalidate the authors' border regressions; it just points out that the regression discontinuity label is misguided.

Furthermore, as Van der Klauw puts it, in a regression discontinuity context, "under certain comparability conditions, the assignment near the cut-off can be seen as behaving almost as if random." In other words, it must be the case that the properties and neighborhoods on one side of the border have the same characteristics as those on the other side of the border, so that the only difference between the two sides comes from the different foreclosure laws. Arguably, this might be the case if one were focused on a very short radius from the border, say 1/10 of a mile. But the authors' shortest radius is 5 miles. This means that part of the comparison includes homes that are close to 10 miles apart from each other! In many cities, travelling only 1 or 2 miles is sufficient to move from a wealthy, up-scale neighborhood, to a poor, downtrodden area, so a 5 mile radius is much too long to impart confidence that the border sample is uncontaminated by unobserved heterogeneity. Thus, it is likely the case that the authors' results are simply picking up the fact that they are comparing completely different housing markets with different foreclosure rates (and average durations) stemming from something that is not related to differences in foreclosure laws.

The authors could try to shorten the radius, but in doing so they would run into a couple of issues. First, they would need very detailed and disaggregated data (likely loan-level data on foreclosures and values), and they would need a large enough sample of foreclosures very close to the borders between judicial and nonjudicial foreclosure states to be able to estimate the regressions. Second, based on our logic above, it isn't clear that we should expect foreclosures close to one side of the border to exert a discontinuous treatment effect on housing values on that side of the border relative to the other side of the border.

2. Are differences in laws expected to generate differences in foreclosure numbers or timelines?
Assume that a borrower simply stops paying his mortgage in a judicial state. It is not likely that judicial requirements will prevent a foreclosure from ever taking place. The borrower will lose his house eventually, though the judicial requirements may stretch out the "foreclosure timeline" longer than it would be in a nonjudicial state. If so, the authors might find in some given year that there are fewer foreclosures, relative to delinquencies, in judicial states. But these foreclosures are coming eventually, and if they are, it's hard to see how forward-looking agents would ignore them when setting housing prices, as the authors implicitly assume.

3. State laws do not necessarily make a foreclosure out of a delinquency
Another issue concerns the link between state laws and the probability that a delinquency turns into a foreclosure. The authors implicitly assume that they can isolate variation in the probability of transition from delinquency using state laws. But these transitions (called "roll rates" in the industry) often change over time within states, even when the relevant state laws stay the same. What's worse, there is both theoretical and empirical support for the idea that these changes are driven by changes in housing prices. The standard "double-trigger" theory of default predicts that borrowers become delinquent when they have financial problems (like job loss), but that delinquencies don't turn into foreclosures unless house prices have fallen and owners have negative equity. As we have found, the predictions of double-trigger theory are borne out strikingly in Massachusetts data. Bay State delinquency levels were similarly high in the recessionary years of 1991 and 2001, but there were far more foreclosures in the first recession than in the second. Why? Prices were in free fall in 1991 but rising ten years later. The causality clearly went from the prices to the foreclosures, not the other way around. In short, the claim that foreclosure-delinquency ratios stem from state-specific and constant "propensities to foreclose," which are themselves driven by state laws, is simply wrong.

4. The use of problematic datasets further impedes ability to identify causality
The conceptual issues we just outlined raise serious doubts about whether it is even possible to identify the direct effect of foreclosures on prices with the authors' approach. But even without these issues, confidence in the authors' results is further reduced by some serious issues with their datasets, most notably the foreclosure data from As we have found in our research, measuring foreclosures is tricky even within a state. It is no doubt harder to come up with consistent measures of foreclosures across state lines. Lenders often file multiple foreclosure deeds for the same property (a very common practice with Fannie Mae), and courts occasionally compel lenders to refile. (One such instance has achieved a great deal of attention in the now-famous U.S. Bank v. Ibañez case, litigated in Massachusetts. Details of this case appear in "Is Massachusetts a judicial state?") Figuring out whether a property has actually been transferred from the delinquent borrower to the lender (and become real-estate owned, or REO) is also a nontrivial effort, because a foreclosure deed does not distinguish whether the buyer at the auction was the lender or some third-party buyer. Even subsequent sales may reflect transfers within different legal incarnations of the bank and not true transfers of property.

The authors claim that they dealt with the problem of multiple deeds by looking at the last filing in a given year:

To avoid double-counting filings for the same property, provided us totals for the last filing in the process for a given property in a given year. For example, if a borrower received a notice of default and a notice of trustee sale in the same year, records one notice of trustee sale for the property. (p. 7)

This procedure only addresses multiple filings within a given calendar year, which is hardly the only problematic scenario. The Ibañez case in Massachusetts (see the discussion below) clearly illustrates one of many other potential issues. U.S. Bank foreclosed on the Ibañez property in July 2007. Because the Massachusetts Land Court invalidated that foreclosure, the bank will at some point have to foreclose on the property again. Only a very careful search of the documents reveals that the new foreclosure on the property is in fact a do-over and that one should subtract a foreclosure from 2007 and add one to 2011. The authors here would simply count the two deeds as two different foreclosures. And this is true for any set of repeat foreclosure deeds that occur over two or more years.

To make matters worse, the authors do not simply look at foreclosure deeds:

Our measure of total foreclosures in a zip code is the total number of notices of trustee sale, foreclosure sales, or real estate owned. (p. 7)

Given the length of the foreclosure process, it is likely that two of these events for a single property will take place in different years, and the authors will consequently count them twice. If foreclosure procedures were the same across state and time, this double-counting wouldn't be a big deal; the parameters may not be estimated as well. However, it seems quite likely that the legal variation in foreclosure process could vary the number of duplicative filings. For example, nonjudicial states may be more amenable to automated foreclosure procedures that reduce the cost of multiple filings but also the error rate and thus the need for amended filings, to take just one example.

And none of this considers the overwhelming problem of comparing records across states, each with different laws and different recording requirements.