April 26, 2012
Can home loan modification through the 60/40 Plan really save the housing sector?
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In a recent article in the Federal Reserve Bank of St. Louis Review, Manuel Santos, a professor at the University of Miami, claims to offer a simple solution to "save the housing sector." Called the "60/40 Plan," his proposal is the centerpiece of a business called 60/40 The Plan Inc. Santos’s article is, in our opinion, written less like an academic article and more like promotional material.
The developer of the 60/40 Plan, Gustavo Diaz, is seeking a patent for the proposal. Unfortunately for the stressed mortgage market, his idea is simply a specific variant of a long-standing mortgage-servicing practice known as "principal forbearance." In general, principal forbearance occurs when the mortgage lender grants a temporary reduction of a borrower’s monthly mortgage payment, often reducing the payment by a significant fraction, with the stipulation that the borrower repay this benefit, with interest, at a later date.
Principal forbearance is a loss-mitigation tool that mortgage lenders and servicers have been using for decades. In fact, Fannie Mae and Freddie Mac are currently using this technique as a loss mitigation tool and alternative to principal forgiveness (which Federal Housing Finance Agency Acting Director Edward DeMarco discussed here). Private mortgage lenders have also widely used principal forbearance, especially in the first few years of the recent foreclosure crisis.
As articulated in Diaz’s 60/40 Plan, principal forbearance simply splits a distressed borrower’s current principal balance into two parts: a 60 percent share that will fully amortize over 30 years and be subject to interest payments at market rates, and a 40 percent share that is treated as a zero-interest balloon loan due at the time of sale.
Of course, in practice, the optimal shares and other terms of a principal forbearance program should be, and often are in practice, based on a given household’s financial situation. One size does not fit all. Professor Santos advocates the 60/40 Plan in large part because it is, in the language of economists, "incentive compatible." What this means is that borrowers who need assistance with their mortgage payments will find the program helpful and borrowers who do not need assistance will not find the program very appealing and thus will have little incentive to pretend to be a borrower in need of help in order to qualify for the program.
He writes: "It is important to understand that the 60/40 Plan builds on financial postulates and incentive compatible mechanisms that can be firmly implemented. It is designed as a first-best contract between the homeowner and the lender by holding onto some basic principles of incentive theory."
We agree completely with this sentiment. In fact, one of us wrote an article almost five years ago that advocated a policy of principal forbearance over principal forgiveness for exactly these reasons. Thus, the 60/40 Plan is not a novel concept, as Professor Santos seems to believe. But even more problematic, principal forbearance, as we have come to realize over the past few years, is not a panacea for the housing market for several reasons. First, it is really only helpful and appealing to borrowers that have temporary cash-flow problems who do not wish to move. This is because under the 60/40 Plan and principal forbearance in general, a borrower remains in a position of negative equity, which makes it virtually impossible to sell, since the borrower would need to come up with the amount of negative equity in cash to repay the entire principal balance of the mortgage at closing. For example, in the numerical example that Professor Santos works through to illustrate how the 60/40 Plan would work in practice, the borrower remains in a position of negative equity for 15 years. Thus, if a cash-strapped borrower needs to move immediately, or even a few years down the road, default (or re-default) is very likely.
Second, carrying 40 percent of the mortgage at a zero (or below market) interest rate imposes significant costs on the lender or investor. (These costs are viewed as being offset by savings from avoiding foreclosure.) Nevertheless, principal forbearance is not always going to be a positive net-present-value proposition; this depends on the share being protected (40 percent is quite high), the amortization schedule (30 years is very long), the discount rate, and the re-default rate. Indeed, Professor Santos seemingly assumes no re-default despite the fact that under the plan a borrower would remain in negative equity for a very long time, as we discussed above.
Third, most distressed mortgages are not held by depository institutions as whole loans. Fannie Mae and Freddie Mac have been able to selectively employ principal forbearance because they make investors whole in terms of the original promised principal and interest payments. This is not true for private-label securitizations, and there have been ongoing disagreements between investors and servicers as to optimal loss-mitigation strategies. (And there is no reason to think this proposal would not be similarly controversial.) The 60/40 Plan also seemingly ignores the significant complications posed by existing second liens and mortgage insurance policies.
Finally, Professor Santos claims that the 40 percent zero-coupon balloon shares—typically nonrecourse loans to severely distressed homeowners—will have a deep secondary market to pull liquidity back into the housing market. This seems far-fetched given that these assets have little or no yield and will have high default rates with no recourse. However, reading further, it appears that the proposal assumes a Federal Deposit Insurance Corporation (FDIC) insurance wrap for these assets to facilitate their sale. The cost of this insurance would likely be expensive and require a controversial new program, with premiums expected to cover losses or a congressional appropriation. However, it also ignores the fact that FDIC-insured depository institutions only hold about 25 percent of all mortgages.
Principal forbearance can be a useful loss-mitigation tool, although its value depends on economic circumstances. The 60/40 Plan that Professor Santos advocates is an example of principal forbearance and not a novel concept. Moreover, the 60/40 Plan does not consider a number of important institutional factors that have hampered loss-mitigation activities since the onset of the mortgage foreclosure crisis. Simply put, the 60/40 Plan will not save the housing market.
By Scott Frame, financial economist and senior policy adviser, and
Kris Gerardi, financial economist and associate policy adviser at the Federal Reserve Bank of Atlanta
February 14, 2011
New study claims to solve the econometric problem of the link between foreclosure and house prices
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Many policymakers are now concerned about how the next wave of foreclosures will affect the housing market. Analysts have cited a large "shadow inventory" of homes, referring to the mass of delinquent mortgages that have yet to make their way through the foreclosure process. When these foreclosures occur, they could raise the number of homes for sale and put downward pressure on house prices. They could also impose negative externalities to other homes in the same neighborhoods, sending house prices even lower. (We recently blogged about the so-called contagion effects of foreclosures on surrounding properties.)
These potential effects seem intuitive, but measuring them is not easy. The main problem is what economists call "simultaneity." Foreclosures lead to an increased supply of homes for sale, which can lower prices—but lower prices also increase the probability that borrowers have negative equity, which can lead to foreclosure. Thus, there is simultaneous causality: foreclosures can reduce prices, and lower prices can cause the negative equity that leads to foreclosure. As a result, simply showing a correlation between foreclosures and falling house prices is not sufficient to measure—or even establish—a causal effect of foreclosures on prices.
A new study by Atif Mian, Amir Sufi, and Francesco Trebbi claims to have solved this econometric problem. Their paper reports a substantial causal impact of foreclosures on not only house prices, but also residential investment and automobile purchases. However, the authors make a major data error that, in our opinion, invalidates a large part of their analysis. In addition, there are important conceptual issues that raise deep questions about their identification strategy, even if it is possible to correct the data error.
Can simultaneity be solved by classifying states as judicial, nonjudicial?
The authors attack the simultaneity problem with a classic method: they use differences in state laws as an instrumental variable. The essential idea is that states vary randomly as to whether they are judicial or nonjudicial. Judicial states are typically characterized by longer foreclosure durations, since the mortgage servicer must navigate through the legal system to get court approval, which usually entails a significant amount of time (see Pennington-Cross 2010 for a nice discussion). If the judicial/nonjudicial classification is random with respect to the health of state-level housing markets, then state laws will generate random variation in the number of foreclosures across states. Under these assumptions, using the classification as an instrument yields consistent estimates of the effect of foreclosures on house prices.
Of course, the classification of states into judicial and nonjudicial groups may not be random. It turns out that there is a strong regional component to this classification. Figure 3 in the Mian-Sufi-Trebbi paper shows that states in the Northeast and Midwest tend to be judicial, while the states in the South and West are mostly nonjudicial. It's no secret that problems in the U.S. housing market also have a strong regional character, with housing markets in Arizona, California, Florida, and Nevada (all located in the South and West) in particularly bad shape.
One way to check for the possibility of confounding effects across the two classifications of states is to compare their observable variables. The authors do this, and then claim that "states with a judicial foreclosure requirement are remarkably similar to other states in all attributes of interest except the propensity to foreclose" (p.3). But eyeballing their Figure 3 should give a reader pause. Nevada and Arizona, which are nonjudicial states, include the number one and two MSAs for new construction and for house price appreciation in the two years prior to the collapse of the mortgage market.1
Cross-state differences challenge regressions
Regional patterns in both state laws and housing markets cause problems for the authors' identification strategy. If we find that foreclosures tend to be more frequent in the nonjudicial states, this might be because foreclosing on delinquent homeowners is easier in those states, as the authors' identification strategy assumes. But high foreclosure rates in the nonjudicial states could also stem from negative shocks to housing demand in the parts of the country where the nonjudicial states happen to be located. Consequently, if we find that housing prices are lower and foreclosure rates are higher in nonjudicial states, then we can't be sure what's causing what. The high foreclosure rates could be causing the falling prices, as the authors' claim. But it could also be true that low regional demand and falling prices in the South and West are causing the high foreclosure rate—the very possibility that the authors were hoping to rule out.
The authors recognize that unobserved cross-state differences make the state-level experimental approach problematic so they propose an alternative set of regressions that are not subject to such criticism. In addition to estimating the first set of regressions—which, in the manner described above, uses all the states in the country—they estimate a second set that includes only ZIP codes adjacent to borders between judicial and nonjudicial states. The idea is that while unobserved heterogeneity across states could potentially invalidate the first set of regressions, this heterogeneity is less likely to be a problem in the second. In other words, the housing market in Arizona may differ markedly from the housing market in Maine and not just because Arizona is a nonjudicial state while Maine is judicial.
However, the ZIP codes just north of the Massachusetts-Rhode Island border are likely to have similar housing markets to the ZIP codes that are just south of this border. So, if the border ZIP codes in Massachusetts, which the authors label a judicial state, are experiencing higher foreclosures than the border ZIP codes in Rhode Island, a nonjudicial state, then differences in the two state's laws—and not unobserved differences in demand— are probably the reason why. And if the state laws are generating random variation in foreclosures, then the authors claim that this variation can be used to get a clean estimate of the causal effect of foreclosures on housing prices.
Problems in the data: Massachusetts, Wisconsin are misclassified
The authors find similar results in both sets of regressions. This similarity gives them some confidence that they have truly pinned down the direct effect of foreclosures on other economic outcomes. But here's where the data error comes in: the authors make a mistake in classifying at least two states as judicial or nonjudicial, which has major implications for their results. Specifically, they misclassify Massachusetts as judicial and Wisconsin as nonjudicial.2 Most sources, including the National Consumer Law Center (NCLC), reverse those classifications.
(For readers interested in the gory details, we show that for Massachusetts, there is no question that the NCLC is right.)
While the misclassification of two out of 50 states may seem minor, it turns out that Wisconsin and Massachusetts dominate the samples for the "border discontinuity" regressions. As the table shows, depending on the sample, using the alternative classification from the NCLC invalidates between 58 and 78 percent of the ZIP codes the authors use. Consider the sample that uses ZIP codes in 5-mile bands around state borders. Because it uses homes closest to state borders, this sample is least susceptible to unobservable differences between geographic areas, although we argue below that even 5-mile bands are inadequate to obtain clean identification. In this sample, classifying Massachusetts—correctly—as nonjudicial eliminates 70 percent of the comparisons.3
One response to this criticism would be to reclassify the states correctly and then reestimate both sets of regressions. The problem for the border regressions is that Massachusetts's and Wisconsin's borders with judicial and nonjudicial states respectively are sparsely populated and do not meet the authors' criteria for inclusion in the border sample. For example, farms and weekend homes comprise most of the properties in border ZIP codes between western Massachusetts and southern Vermont.
Misclassification proves detrimental to the identification strategy
As the authors have written the paper, they claim to find big differences in ZIP-code-level outcomes based on the judicial/nonjudicial classification. However, they use regressions with the wrong classification for most of the comparisons. If the identification strategy worked as the authors had hoped, their regressions would have implied that there are no important differences on either side of most judicial/nonjudicial borders because these borders in fact separated states with similar laws. However, because the regressions instead reported significant differences, some other important sources of heterogeneity across the state lines must exist—and if the authors can't control for heterogeneity across, say, the Massachusetts–Rhode Island border, the reader can't be expected to have confidence in their ability to control for unobserved differences between Massachusetts and Nevada.
Another way of putting this is that the authors have inadvertently performed and failed a falsification, or placebo, test on their data. They estimated their regressions on a sample of borders that are, for the most part, not characterized by differences in foreclosure laws, at least in terms of the judicial/nonjudicial classification, and found large effects where they should have found none. In our opinion, this is very strong evidence against their claim that judicial/nonjudicial foreclosure laws are a valid instrument for foreclosure rates. Even if the authors correctly reclassify the states and reestimate the IV regressions for the border sample, this failed falsification test still sheds doubt on the entire empirical strategy.
In addition to this primary critique, we also found some other important drawbacks in the analysis. For readers that are interested in learning more about these issues, here is a detailed discussion.
We remain unconvinced by the authors' claim that exogenous increases in foreclosures substantially reduce housing prices. This issue, of the link between foreclosure and house prices, is of first-order importance to policymakers, who struggle not only with the foreclosure problem itself but also with the potential effects of foreclosures on the economic recovery. However, the authors' research strategy is unlikely to be helpful in addressing these problems given the deep conceptual issues it did not deal with and the poor data on which it is based.
Research economist and assistant policy adviser at the Federal Reserve Bank of Atlanta
Research economist and policy adviser at the Boston Fed
1 Moreover, one of the main stylized demographic facts about the United States in the last 50 years has been the spread of population south and west across the country. Indeed, for the past 25 years, population has consistently and steadily grown twice as fast in the states the authors identify as nonjudicial compared to the states they identify as judicial.
2 Arguably, the authors misclassify as many as six states: the two listed plus Maryland, Nebraska, New Mexico, and Iowa. However, as we explain below, it's the misclassification of Massachusetts and Wisconsin that dramatically affects their results.
3 The authors are aware that there are alternative classifications but view the discrepancies as minimal, relegating the following comment to a footnote: "The only states that differ across these three classifications are Massachusetts, Nebraska, Oklahoma, Rhode Island, and Wisconsin." It is unclear whether they were aware that two of those states accounted for most of their border sample and that their border sample specification was not robust to the alternatives.
May 05, 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.
*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.