Real Estate Research
Real Estate Research provides analysis of topical research and current issues in the fields of housing and real estate economics. Authors for the blog include the Atlanta Fed's Kristopher Gerardi, Carl Hudson, and analysts, as well as the Boston Fed's Christopher Foote and Paul Willen.
October 04, 2011
The uncertain case against mortgage securitization
The opinions, analysis, and conclusions set forth are those of the authors and do not indicate concurrence by members of the Board of Governors of the Federal Reserve System or by other members of the staff.
Did mortgage securitization cause the mortgage crisis? One popular story goes like this: banks that originated mortgage loans and then sold them to securitizers didn't care whether the loans would be repaid. After all, since they sold the loans, they weren't on the hook for the defaults. Without any "skin in the game," those banks felt free to make worse and worse loans until...kaboom! The story is an appealing one and, since the beginning of the crisis, it has gained popularity among academics, journalists, and policymakers. It has even influenced financial reform. The only problem? The story might be wrong.
In this post we report on the latest round in an ongoing academic debate over this issue. We recently released two papers, available here and here, in which we argue that the evidence against securitization that many have found most damning has in fact been misinterpreted. Rather than being a settled issue, we believe securitization's role in the crisis remains an open and pressing question.
The question is an empirical one
Before we dive into the weeds, let us point out why the logic of the above story need not hold. The problem posed by securitization—that selling risk leads to excessive risk-taking—is not new. It is an example of the age-old incentive problem of moral hazard. Economists usually believe that moral hazard causes otherwise-profitable trade to not occur, or that it leads to the development of monitoring and incentive mechanisms to overcome the problem.
In the case of mortgage securitization, such mechanisms had been in place, and a high level of trade had been achieved, for a long time. Mortgage securitization was not invented in 2004. To the contrary, it has been a feature of the housing finance landscape for decades, without apparent incident. As far back as 1993, nearly two-thirds (65.3 percent) of mortgage volume was securitized, about the same fraction as was securitized in
2006 (67.6 percent) on the eve of the crisis. In order to address potential moral hazard, securitizers such as Fannie Mae and Freddie Mac (the government sponsored enterprises, or GSEs) long ago instituted regular audits, "putback" clauses forcing lenders to repurchase nonperforming or improperly originated loans, and other procedures designed to force banks to lend responsibly. Were such mechanisms successful? Perhaps, perhaps not. It is an empirical question, and so our understanding will rest heavily on the evidence.
The case against securitization
Benjamin Keys, Tanmoy Mukherjee, Amit Seru, and Vikrant Vig released an empirical paper in 2008 (revised in 2010) titled "Did Securitization Lead to Lax Screening? Evidence from Subprime Loans" (henceforth, KMSV) that pointed the finger squarely at securitization. The paper won several awards and, when it was published in the Quarterly Journal of Economics in 2010, it became that journal's most-cited paper that year by more than a factor of two. In other words, it was a very well-received and influential paper.
And for good reason. KMSV employs a clever method to try to answer the question of securitization's role in the crisis. Banks often rely on borrowers' credit (FICO) scores to make lending decisions, using particular score thresholds to make determinations. Below 620, for example, it is hard to get a loan. KMSV argues that securitizers also use FICO score thresholds when deciding which loans to buy from banks. Loan applicants just to the left of the threshold (FICO of 619) are very similar to those just to the right (FICO of 621), but they differ in the chance that their bank will be able to sell their loan to securitizers. Will the bank treat them differently as a result? This seems to have the makings of an excellent natural experiment.
Figures 1 and 2, taken from KMSV, illustrate the heart of their findings. Using a data set of only private-label securitized loans, the top panel plots the number of loans at each FICO score. There is a large jump at 620, which, KMSV argues, is evidence that it was easier to securitize loans above 620. The bottom panel shows default rates for each FICO score. Though we would expect default to smoothly decrease as FICO increases, there is a significant jump up in default at exactly the same 620 threshold. It appears that because securitization is easier to the right of the 620 cutoff, banks made worse loans. This seems prima facie evidence in favor of the theory that mortgage securitization led to moral hazard and bad loans.
Reexamining the evidence
But what is really going on here? In September 2009, the Boston Fed published a paper we wrote (original version here, updated version here) arguing for a very different interpretation of this evidence. In fact, we argue that this evidence actually supports the opposing hypothesis that securitizers were to some extent able to regulate originators' lending practices.
The data set used in KMSV only tells part of the story because it contains only privately securitized loans. We see a jump in the number of these loans at 620, but we know nothing about what is happening to the number of nonsecuritized loans at this cutoff. The relevant measure of ease of securitization is not the number of securitized loans, but the chance that a given loan is securitized—in other words, the securitization rate.
We used a different data set that includes both securitized and nonsecuritized loans, allowing us to calculate the securitization rate. Figures 3 and 4 come from the latest version of our paper.
Like KMSV, we find a clear jump up in the default rate at 620, as shown in the bottom panel. However, the chance a loan is securitized actually goes down slightly at 620, as shown in the top panel. How can this be? It turns out that above the 620 cutoff banks make more of all loans, securitized and nonsecuritized alike. This general increase in the lending rate drives the increase in the number of securitized loans that was found in KMSV, even though the securitization rate itself does not increase. With no increase in the probability of securitization, it is hard to argue that the jump in defaults at 620 is occurring because easier securitization motivates banks to lend more freely.
The real story behind the jumps in default
So why are banks changing their behavior around certain FICO cutoffs? To answer this question, we must go back to the mid-1990s and the introduction of FICO into mortgage underwriting. In 1995, Freddie Mac began to require mortgage lenders to use FICO scores and, in doing so, established a set of FICO tiers that persists to this day. Freddie directed lenders to give greater scrutiny to loan applicants with scores in the lower tiers. The threshold separating worse-quality applicants from better applicants was 620. The next threshold was 660. Fannie Mae followed suit with similar directives, and these rules of thumb quickly spread throughout the mortgage market, in part aided by their inclusion in automated underwriting software.
Importantly, the GSEs did not establish these FICO cutoffs as rules about what loans they would or would not securitize—they continued to securitize loans on either side of the thresholds, as before. These cutoffs were recommendations to lenders about how to improve underwriting quality by focusing their energy on vetting the most risky applicants, and they became de facto industry standards for underwriting all loans. Far from being evidence that securitization led to bad loans, the cutoffs are evidence of the success securitizers like Fannie and Freddie have had in directing lenders how to lend.
With this in mind, the data begin to make sense. Lenders, following the industry standard originally promulgated by the GSEs, take greater care extending credit to borrowers below 620 (and 660). They scrutinize applicants with scores below 620 more carefully and are less likely to approve them than applicants above 620, resulting in a jump-up in the total number of loans at the threshold. However, because of the greater scrutiny, the loans that are made below 620 are of higher average quality than the loans that are made above 620. This causes the jump-up in the default rate at the threshold.
Figures 5 and 6 show that this pattern also exists among loans that are kept in portfolio and never securitized. The change in lending standards causes these loans, as well as securitized loans, to jump in number and drop in quality at 620 (and 660). However, as figure 3 shows, the securitization rate doesn't change because securitized and nonsecuritized loans increase proportionately. The FICO cutoffs are used by lenders because they are general industry standards, not because the securitization rate changes. This means the cutoffs cannot provide evidence that securitization led to loose lending.
But the debate does not end there. In April 2010, Keys, Mukherjee, Seru, and Vig released a working paper (KMSV2), currently forthcoming in the Review of Financial Studies, that responded to the issues we raised. According to the paper, the mortgage market is segmented into two completely separate markets: 1) a "prime" market, in which only the GSEs buy loans, and 2) a "subprime" market, in which only private-label securitizers buy loans. KMSV2 argues that only private-label securitizers follow the 620 rule and, by pooling these two types of loans in our analysis, we obscured the jump in the securitization rate in that market.
The latest round in the debate
We went back to the drawing board to investigate these claims. We detail our findings in a new paper, available here. In the paper, we demonstrate that the pattern of jumps in default—without jumps in securitization—is not simply an artifact of pooling, but rather exists for many subsamples that do not pool GSE and private-label securitized loans. For example, we find the pattern among jumbo loans (by law an exclusively private-label market), among loans bought by the GSEs, and among loans originated in the period 2008–9 after the private-label market shut down. Furthermore, as figure 7 shows, the private-label market boomed in 2004 and disappeared around 2008, while the size of the jump in the number of loans at 620 continued to grow through 2010, demonstrating that use of the threshold was not tied to the private market.
What's more, KMSV's response fails to address the fundamental problem we identified with their research design: following the mandate of the GSEs, lenders independently use a 620 FICO rule of thumb in screening borrowers. Even if some subset of securitizers had used 620 as a securitization cutoff, one would not be able to tell what part of the jump in defaults is caused by an increase in securitization, and what part is simply due to the lender rule of thumb. Consequently, the jump in defaults at 620 cannot tell us whether securitization led to a moral hazard problem in screening.
To put this in more technical jargon, KMSV use the 620 cutoff as an instrument for securitization to investigate the effect of securitization on lender screening. But the guidance from the GSEs that caused lenders to adopt the 620 rule of thumb in the first place means that the exclusion restriction for the instrument is not satisfied—the 620 cutoff affects lender screening through a channel other than any change in securitization.
We also found that the GSE and private-label markets were not truly separate. In addition to qualitative sources describing them as actively competing for subprime loans, we find that 18 percent of the loans in our sample were at one time owned by a GSE and at another time owned by a private-label securitizer—a lower bound on the fraction of loans at risk of being sold to both. Because the markets were not separate, the data must be pooled.
Our findings, of course, do not settle the question of whether securitization caused the crisis. Rather, they show that the cutoff rule evidence does not resolve the question in the affirmative but instead points a bit in the opposite direction. Credit score cutoffs demonstrate that large securitizers like Fannie Mae and Freddie Mac were able to successfully impose their desired underwriting standards on banks. We hope our work causes researchers and policymakers to reevaluate their views on mortgage securitization and leads eventually to a conclusive answer.
By Ryan Bubb, assistant professor at the New York University School of Law, and Alex Kaufman, economist with the Board of Governors of the Federal Reserve System
April 21, 2010
What role (if any) did the federal government and the GSEs have in the housing boom?
The government-sponsored enterprises (GSEs) have recently come under fire for possibly contributing to the housing and foreclosure crisis that has plagued our economy over the past few years. The GSEs are particularly appealing targets because of their controversial place at the forefront of the U.S. housing finance system over the past half century or so. (See background.) One argument focuses on the government's role in mandating that Fannie and Freddie extend mortgage credit in areas where they otherwise would not have, thus "forcing" the GSEs to make loans to borrowers likelier to default because of insufficient income, poor credit histories, or both. Namely, the GSE Affordable Housing Goals that Congress stipulated in the 1992 GSE Act requires Fannie and Freddie to use specific fractions of their loan purchase activity for certain underserved segments of the population.
The complicated issue of market factors versus Affordable Housing Goals
While this argument certainly sounds plausible, actually determining whether the federal government, through its regulation of GSE activities, had a causal effect on the mortgage boom and housing bubble is an extremely difficult task. GSE decisions about the number and type of loans to purchase and the locations of these purchases are almost surely influenced by market factors such as house prices, so it's quite possible that these market factors and not government mandates were what influenced Fannie and Freddie to expand their purchases into the underserved areas. Thus, in order to shed any light on this issue, one must first come up with a strategy to disentangle the effect of GSE activity on market variables due to government mandates from the effect of those variables on GSE activity.
In a recent paper, Federal Reserve Board economist Neil Bhutta has taken a stab at solving one aspect of this difficult issue: identifying the effect of government legislation on GSE activity. Bhutta's study, like several previous studies in the literature, exploits a discontinuity in the data caused by one of the GSE Affordable Housing Goals that was stipulated by Congress in the 1992 GSE Act. However, unlike the previous studies, Bhutta uses a more robust estimation technique and superior data coverage to arrive at a very different conclusion: He finds that one of the Affordable Housing Goals—the Underserved Areas Goal (UAG)—positively affected GSE loan purchase activity without crowding out other market participants such as the Federal Housing Administration (FHA) and private subprime mortgage lenders. In our opinion, Bhutta's analysis is very careful, and has provided an important first step toward answering the question of how much the GSEs contributed to the mortgage boom that preceded the crisis.
According to the UAG, Fannie and Freddie must purchase a certain fraction of their loans in low-income or minority census tracts. To be specific, a loan qualifies for the UAG if it is originated in a tract with median family income less than or equal to 90 percent of median family income in the metropolitan statistical area (MSA), or in a tract with minority population share of at least 30 percent and median family income less than or equal to 120 percent of the MSA median. Figure 1 in the Bhutta paper shows the UAG began at just over 20 percent in the mid-1990s and increased over time to almost 40 percent in 2006. Bhutta, and other authors who have studied this issue, hypothesize that to the extent that the UAG is binding, it will increase GSE loan purchases in the qualifying census tracts. This, in turn, may increase the supply of mortgage credit to low-income and minority households, depending on whether or not increased GSE purchases "crowd out" other lenders such as FHA and private, subprime originators.
Bhutta’s paper draws different conclusion
The previous literature on this topic found little evidence of much of an effect. An et al. (2007) and An and Bostic (2008) previously studied the link between the UAG and housing market outcomes using a two-stage econometric approach and data from the 1990s. Their first stage results showed only weak evidence of a causal link between the UAG and GSE purchase activity. In fact, An et al. (2007) found lower GSE market shares in census tracts that qualified for the UAG. Gabriel and Rosenthal (2008) also studied the link between the UAG and GSE purchase activity using data through 2000, and found no statistically significant effect. So then what exactly distinguishes Bhutta's paper from these previous studies, and why does he come to a different conclusion?
First, and most importantly, Bhutta uses a different and, we would argue, superior econometric approach. He employs a regression discontinuity strategy that solves a serious misspecification issue in the studies mentioned above. Those studies essentially compared GSE purchase activity in qualifying census tracts to non-qualifying tracts, and controlled for a host of potentially important census tract variables like demographic trends and housing market characteristics.
However, the studies did not control for the fact that GSE purchase activity is correlated with the variable that the UAG is based on—the ratio of census tract median income to MSA median income, which we will refer to as the "assignment variable." Since the correlation is positive (higher median income, on average, makes an area more attractive to a potential lender), not controlling for it will lead to a negative bias in the estimated effect of the UAG on purchase activity. For example, holding all else constant, the GSEs are more likely to purchase a higher volume of loans in a census tract with an assignment ratio of 110 percent compared to a qualifying tract with a ratio of, say, 90 percent.
Bhutta controls for this effect in a couple of different ways. In one specification, he focuses on tracts that have assignment ratios within 5 percentage points of the qualifying ratio, and explicitly controls for the correlation between the assignment ratio and GSE purchase volume assuming a linear correlation structure. In a second specification, he uses census tracts with assignment ratios within 2 percentage points of the qualifying ratio, and does not control for the correlation (note that most of the prior studies used a window of 10 percentage points without controlling for the correlation).
The second difference is the data coverage used by Bhutta compared to the previous studies. Unlike those studies, Bhutta uses data through the mid-2000s, which is important because much of the increase in the UAG came after the year 2000. Thus, it is possible that the UAG was not binding before 2000, which would also explain the different conclusions.
When all is said and done, Bhutta finds a statistically significant, positive effect of the UAG on GSE purchases, but the magnitude of the effect is quite modest, at around 4 percent. That is, all else being equal, the GSEs purchase approximately 4 percent more loans in census tracts with assignment ratios just below the qualifying ratio versus tracts just above the ratio. In addition, he finds no evidence of crowding out, which suggests that the UAG may exert a causal impact on access to mortgage credit (as long as it is not a simple compositional effect whereby the GSEs are simply offsetting their increased purchases in qualifying tracts by lowering their purchases in non-qualifying census tracts).
Findings, though accurate, may not paint complete picture
While we believe the Bhutta paper is a very careful and rigorous analysis, there is some reason to suspect that its findings are a lower bound for the impact of the UAG. Bhutta uses Home Mortgage Disclosure Act (HMDA) data for his analysis, which is likely to under measure the number of loans purchased by the GSEs. HMDA identifies only mortgages purchased in the same calendar year of origination, so it is possible, if not likely, that a non-trivial fraction of GSE purchases take place with a significant lag from the date of origination. Bhutta attempts to address this issue by looking at the sample of loans eligible to be purchased by the GSEs separately, rather than considering only the loans that are actually purchased. However, the difficulty of determining which loans are eligible and which are not likely creates a significant amount of measurement error in this exercise.
A second, possibly more serious source of mismeasurement comes from the fact that the HMDA data don't contain information on the loans backing mortgage-backed securities that the GSEs purchased for their retained portfolios. These were not a trivial fraction of their total purchase activity and, if accounted for, could significantly add to the estimated effect of the UAG on GSE secondary market activity. Unfortunately, one would need to use loan-level GSE data, which is virtually impossible to obtain, at least up to now.
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