Glennon and Stengel (1995) and Buist, Linneman, and Megbolugbe (1997) argue that an analysis that pools lenders may not be able to isolate disparate treatment discrimination. Furthermore, the analysis by Buist et al. casts some doubt on the standard specification of a loan denial equation. In particular, if each lender uses a hard-and-fast rule that automatically determines acceptance or rejection, then the standard specification, which treats loan denial as probabilistic, is incorrect.
We disagree with Buist et al.’s second point, for two reasons. First, there is no evidence that lenders use hard-and-fast rules for loan denial. Decisions are based on judgments and interpretations and compensating factors that inevitably vary from case to case. Second, Buist et al.’s approach substantially limits the power of the analysis. The dummy variable they include, which indi- cates that an application fails the lender’s implicit underwriting criteria, is set equal to 1 for 265 of the 410 denied applications in their sample. This approach eliminates the influence of these observations on any of the other estimated coefficients, including the minority-status coefficient. Including this variable lowers the minority status coefficient from 0.485 to 0.330 and renders it insignificant. But one cannot determine whether these results reflect a real behavioral effect or simply the decline in effective sample size.
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Table 2. The Distribution of Application Quality for White and Minority Applications
Application Quality* Number of White Number of Minority Minority Share of (1 = highest) Applications Applications Applications (%)
1 11 0 0.0 2 80 3 3.6 3 459 48 9.5 4 758 167 18.1 5 470 161 25.5 6 210 101 32.5 7 96 68 41.0 8 56 36 39.1 9 32 30 48.4 10 29 15 34.1 11 13 11 45.8 12 15 12 44.4 13 2 3 60.0 14 6 8 57.1 15 7 6 53.3 16 1 6 85.7 17 0 4 100.0 18 0 4 100.0 19 1 0 0.0 25 1 0 0.0
*This application quality index is the predicted propensity to be denied from an econometric model of loan denial, based on the public-use version of the Boston Fed Study’s data and scaled so that it falls between 1 (highest quality) and 25 (lowest quality).
We agree, however, with the conclusion that a regression analysis that pools all lenders may not be able to isolate disparate treatment discrimination. This puts us at odds with Munnell et al. (1996), who argue that they can isolate disparate treatment discrimination with their pooled approach. If lenders do, in fact, use different underwriting guidelines, then a pooled regression cannot sep- arate cases in which individual lenders apply different guidelines to minority and white applicants from cases in which minority and white customers apply to lenders with different guidelines.
Even so, we do not think that regressions for individual lenders should replace pooled regressions as the primary method for studying discrimination, for two reasons. First, regressions for individual lenders inevitably involve fewer observations than pooled regressions. Given the often high correlation between applicant characteristics and minority status, a researcher may not be able to isolate the effect of minority status without pooling the data. Thus, for example, Glennon and Stengel’s (1995) finding of an insignificant minority- status coefficient in separate regressions for two lenders should not be taken as convincing evidence that these lenders do not practice discrimination.34
Second, as Buist, Linneman, and Megbolugbe (1997) make clear, scholars and policymakers are concerned about discrimination based on disparate impact as well as discrimination based on disparate treatment. To precisely iso- late disparate impact discrimination, one would have to know the exact rela- tionship between loan and applicant characteristics and expected loan profitability. This relationship might vary across lenders. With this knowledge, one could estimate the relationship between loan denial and expected loan profitability. Discrimination would exist by the disparate treatment standard if minority applications were more likely to be denied than white applications with the same expected loan profitability. Discrimination would exist by the disparate impact standard if the weight given to loan or applicant characteris- tics in a lender’s actual underwriting standards differed from the impact of those variables on expected loan profitability.
Although no study has yet estimated the relationship between loan and applicant characteristics and loan profitability with a data set that includes applicant credit history, one could argue that lenders have an incentive to figure out this relationship and to incorporate it into their actual underwriting standards.35 After all, lenders can make more money if they can accurately
forecast the profitability of each loan application. Because the data do not exist to make this type of forecast with much precision, individual lenders will forecast with error, but lenders may get the relationship about right, on average. If so, then deviations from average standards could indicate “errors” (perhaps intentional) by individual lenders that may impose a disparate impact on minority applicants—and may therefore be discrimination by the disparate impact standard. In this case, a pooled regression, which controls for average actual underwriting standards (using loan and applicant charac- teristics), might capture both disparate treatment discrimination and disparate impact discrimination. Switching to separate regressions for indi- vidual lenders might provide a better estimate of disparate treatment dis- crimination (assuming that sample sizes are large enough), but only at the cost of ignoring disparate impact discrimination.
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One cannot be confident that controlling for loan and applicant character- istics accurately captures disparate impact discrimination, however. First, lenders may not get the relationship between these variables and loan prof- itability right, on average. If that is the case, this approach hides disparate impact discrimination by some lenders and mistakenly finds disparate impact discrimination by others. Second, the relationship between loan and applicant characteristics and loan profitability might differ across lenders. In this case, deviations from the average relationship might be legitimate, that is, they might not involve disparate impact discrimination. At best, therefore, the standard, pooled regression approach provides a rough approximation for the sum of disparate impact and disparate treatment discrimination. No more accurate approach has yet appeared in the literature.
Another way to deal with possible variation in legitimate underwriting stan- dards across lenders is to assume that the lenders to which minority and white customers apply have different underwriting standards but each set of lenders gets the underwriting model right, on average. In this case, the appropriate pro- cedure is to estimate a separate model for minority and white applicants. As noted earlier, however, one cannot reject the hypothesis that the coefficients of the explanatory variables are the same for the minority and white applicants (Munnell et al. 1996), and splitting the sample in this way does not alter the esti- mated impact of minority status on loan denial (Glennon and Stengel 1995). Moreover, Horne’s (1997) claim that the Boston Fed Study’s results are driven by two minority-owned lenders is not compelling because it is based on a nonran- dom subsample of the Boston Fed Study’s data. Results from the whole sample indicate that these results do not depend on the behavior of a few lenders, minority-owned or otherwise. These findings provide further support for the use of a pooled model as a useful, if approximate, way to estimate the combined impact of disparate impact and disparate treatment discrimination.
As several scholars have emphasized (see, for example, Yinger 1996; Van Order and Zorn 1995), a more accurate estimate of overall discrimination would require a two-part analysis—one part to identify legitimate underwriting stan- dards for each lender and the second part to determine discrimination by both the disparate impact and disparate treatment standards. Legitimate underwrit- ing standards are those with an empirically verified link to loan profitability. disparate impact discrimination would exist if a lending institution used stan- dards that were not legitimate in this sense and if the differences between its actual standards and legitimate ones placed minority applicants at a disadvan- tage. Disparate treatment discrimination would exist if it used different stan- dards for minority and white applicants. Two-part studies of this type are clearly needed.
The lending industry appears to be moving toward the use of so-called credit-scoring schemes, which involve relatively mechanical translations of loan and applicant characteristics into a measure of creditworthiness, and toward other types of automated underwriting. Although it may not be possi- ble to completely eliminate human judgment in the application of these proce- dures, they are designed to make certain that, to the extent possible, all applicants are treated the same way. As pointed out by Lindsey (1995) and Buist, Linneman, and Megbolugbe (1997), among others, this implies that these
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schemes help to eliminate disparate treatment discrimination. The problem, which Lindsey does not recognize but others do (including Yezer [1995] and Buist, Linneman, and Megbolugbe), is that credit-scoring or automated under- writing schemes also could institutionalize disparate impact discrimination. To the best of our knowledge, no scholar has published a formal analysis of the link between loan profitability and a full list of loan and applicant characteris- tics. Institutions that have produced credit-scoring schemes may have con- ducted such an analysis, but it has not yet been subjected to the scrutiny of scholars.36Without this type of analysis, it is impossible to determine whether
any particular credit-scoring scheme does or does not involve disparate impact discrimination. Given the growing interest in credit scoring, shedding light on these issues should be one of the highest priorities of future research on mort- gage discrimination.
Conclusions
Most of the specification changes discussed in the literature have little or no impact on the Boston Fed Study’s main result. As in other cases, this result seems remarkably robust. There are, however, two possible exceptions: reverse regressions and the use of different regressions for each lender.
Our investigation of the reverse-regression approach indicates that it is not appropriate for analyzing discrete dependent variables. Thus, reverse regres- sion does not provide a legitimate alternative to a loan denial regression, and one cannot legitimately reject the Boston Fed Study’s findings on the basis of reverse-regression results.
Separate regressions for each lender might provide a clearer picture of disparate treatment discrimination if the number of applications from each individual lender is large. With only a few applications for each lender, how- ever, this approach cannot provide any useful information. Moreover, even if this approach sheds light on disparate treatment discrimination, it does so at the cost of hiding disparate impact discrimination. The same issue arises in any credit-scoring scheme, which may minimize disparate treatment discrimination at the cost of promoting disparate impact discrimination. Pooling all lenders, as in the Boston Fed Study, provides the best approach currently available for measuring discrimination by both the disparate treatment and the disparate impact standards. However, this approach depends on several untested assumptions, and further research is needed on these important issues.