Which of the following claims is most likely to suffer from reverse causality?

2.3 Identifying and Discussing the Endogeneity Problem

Before discussing how to address endogeneity problems, we want to emphasize a more practical matter. A necessary first step in any empirical corporate finance study focused on disentangling alternative hypotheses or identifying causal effects is identifying the endogeneity problem and its implications for inference. Unsurprisingly, it is difficult, if not impossible, to address a problem without first understanding it. As such, we encourage researchers to discuss the primary endogeneity concern in their study.

There are a number of questions that should be answered before putting forth a solution. Specifically, what is the endogenous variable(s)? Why are they endogenous? What are the implications for inferences of the endogeneity problems? In other words, what are the alternative hypotheses about which one should be concerned? Only after answering these questions can researchers put forth a solution to the endogeneity problem.

5.4.2 Endogeneity issues

We now detail the various endogeneity problems that can occur and approaches that have been proposed to solve them. When the effect of local characteristics on individual outcome is estimated, endogeneity can occur both at the individual level and at the local economy level. To see this, we rewrite Equation (5.6) as

(5.51)yi,t=ui+ Xi,tθ+∑cZc,tγ+ηc,t1{ci,t=c }+ϵi,t,

where 1{ci,t=c} is a dummy variable equal to 1 when individual i locates in c at date t. This expression involves local effects related to observables, Zc,t, and unobservables, ηc,t, on every local market, and makes explicit the location choice 1{ci,t=c} which is made at the individual level.

There is an endogeneity issue at the local level when a variable in Zc,t, density for instance, is correlated with the local random component ηc,t. This can happen because of reverse causality or the existence of some missing local variables that affect directly both density and wages. Reverse causality is an issue when higher local average wages attract workers, as this increases the quantity of local labor and thus density. In that case, one expects a positive bias in the estimated coefficient of density (provided that density has a positive effect on wages owing to agglomeration economies).

There is a missing variable problem when, for instance, some local amenities not included in Zc,t are captured by the local random term and they determine both local density and wages. Productive amenities such as airports, transport infrastructures, and universities increase productivity and attract workers, which makes the density increase. In that case, a positive bias in the estimated coefficient of density is also expected. In line with Roback (1982), consumption amenities such as cultural heritage or social life increase the attractiveness of some locations for workers and thus make density higher. Such amenities do not have any direct effect on productivity, but the increase in housing demand they induce makes land more expensive. As a result, local firms use less land relatively to labor, and this decreases labor productivity when land and labor are imperfect substitutes. This causes a negative bias in the estimated coefficient of density since density is positively correlated with missing variables that decrease productivity.

Finally, the unobserved local term captures among other things the average of individual wage shocks at the local level. This average may depend on density as workers in denser local markets may benefit from better wage offers owing, for instance, to better matching. One may consider that matching effects are part of agglomeration economies and then there is no endogeneity issue. Alternatively, one may be interested solely in the effects of knowledge spillovers and market access for goods captured by density, in which case there is an expected positive bias in the estimated effect of density owing to the contamination by matching mechanisms.

Endogeneity concerns can also arise at the individual level when location dummies 1{ci,t=c} are correlated with the individual error term ϵi,t. This occurs when workers sort across locations according to individual characteristics not controlled for in the specification such as some of their unobserved abilities. We emphasize in Section 5.2.1 the importance of considering individual fixed effects ui to capture the role of any individual characteristic constant over time. However, workers might still sort across space according to some time-varying unobserved characteristics entering ϵi,t.

Endogeneity at the individual level also emerges when workers’ location choices depend on the exact wage that they get in some local markets, typically when they receive job offers associated with known wages. Notice that this type of bias is closely related to matching mechanisms although there is here an individual arbitrage between locations, whereas the matching effects mentioned earlier rather refer to a better average situation of workers within some local markets. Importantly, as long as individual location decisions depend only on the explanatory terms introduced in the specification, which can go as far as the individual fixed effect, some time-varying individual characteristics such as age, and a location-time fixed effect, there is no endogeneity bias. Combes et al. (2011) detail these endogeneity concerns.

2.3.3 Endogeneity of Corporate Tax Status

Even if measured by a precise technique, tax rates are endogenous to debt policy, which can have important effects on tax research. If a company issues debt, it reduces taxable income, which in turn can reduce its tax rate. In essence, the more of the left tail of the income distribution that is negative, the lower the expected MTR; and, each incremental dollar of interest deduction pushes more of the left tail into (or closer to) negative territory. The more debt issued, the greater the reduction in the expected marginal tax rate. Therefore, if one regresses debt ratios on marginal tax rates, the endogeneity of corporate tax status can impose a negative bias on the tax coefficient. This could explain the negative tax coefficient detected in some specifications (e.g. Barclay and Smith, 1995b; Hovakimian, Opler, and Titman, 2001). Note that endogeneity can affect all sorts of tax variables, including those based on NOLs, or those based on the average tax rate (i.e. taxes paid/taxable income).

There are two solutions to the endogeneity problem. MacKie-Mason (1990) proposed the first solution by looking at (0,1) debt versus equity issuance decisions (rather than the debt level) in his influential examination of 1747 issuances from 1977 to 1987. Debt levels (such as debt ratios) are the culmination of many historical decisions, which may obscure whether taxes influence current-period financing choices. Detecting tax effects in the incremental approach only requires that a firm make the appropriate debt-equity choice at the time of security issuance, given its current position, and not necessarily that the firm rebalance to its optimal debt-equity ratio with each issuance (as is implicit in many debt-level studies). This approach also only requires that the incremental tax rate, for the next dollars of debt, is measured correctly (and of course, this is what marginal tax rates are designed to do). To avoid the endogenous effect of debt decisions on the marginal tax rate, MacKie-Mason uses the lagged marginal tax rate to explain current-period financing choice.22 He finds a positive relation between debt issuance and tax rates. Graham (1996a) follows a similar approach and examines the relation between changes in the debt ratio and lagged simulated MTRs. He finds positive tax effects for a large sample of Compustat firms.23

If taxes exert a positive influence on each incremental financing decision, the sum of these incremental decisions should show up in an analysis of current debt levels—if one could fix the endogenous negative effect on tax rates induced by cumulative debt usage.24 The second approach to fixing the endogeneity problem is to measure tax rates “but for” financing decisions. Graham et al. (1998) measure tax rates before financing (i.e. based on income before interest is deducted). They find a positive relation between debt-to-value and (endogeneity-corrected) “but for” tax rates. (They also find a “spurious” negative correlation in an experiment that uses an endogenous after-financing tax rate.)

3.1.1 What we know: firms with more cash and less debt invest more

According to the Modigliani–Miller (1958) paradigm, a firm’s investment should depend only on the profitability of its investment opportunities as measured, e.g., by its value of Tobin’s (1969) q. Nothing else should matter: not the firm’s mix of debt and equity financing, nor its reserves of cash and securities, nor financial market “conditions”, however defined. Perhaps the one clearest empirical finding emerging from research on investment over the last 15 or so years is that this theoretical proposition is false. In fact, controlling for investment opportunities, firms with more cash on hand invest more, as do firms with lower debt burdens.

The literature that establishes these results is by now very large, and includes important contributions by Meyer and Kuh (1957), Fazzari, Hubbard and Petersen (1988), Hoshi, Kashyap and Scharfstein (1991), Whited (1992), Schaller (1993), Bond and Meghir (1994), Calomiris and Hubbard (1995), Chirinko (1995), Gilchrist and Himmelberg (1995), Hubbard, Kashyap and Whited (1995) and Lang, Ofek and Stulz (1996). This work is surveyed in detail by Hubbard (1998), so I will confine myself to a few brief observations.

First, it is important to recognize that the evidence speaks to the effect of financial slack on a wide range of investments, not just expenditures on plant and equipment. These include investments in inventories [Carpenter, Fazzari and Petersen (1994), Kashyap, Lamont and Stein (1994)], in R&D [Hall (1992), Himmelberg and Petersen (1994)], in pricing for market share [Chevalier (1995a,b), Chevalier and Scharfstein (1995, 1996), Phillips (1995)], and in labor hoarding during recessions [Sharpe (1994)].

Second, taken as a whole, the literature has convincingly dealt with a fundamental endogeneity problem, namely that a firm’s cash position or its debt level may contain information about its investment opportunities. For example, firms will tend to accumulate cash when they are abnormally profitable, and high profitability may be an indicator that marginal q (which is hard to measure accurately) is high as well.24 Or firms may take on debt precisely at those times when they plan to cut investment, so that it can be tricky to infer causality from, e.g., the finding that dramatic increases in leverage are associated with sharply reduced investment [Kaplan (1989)].

Different papers have addressed this endogeneity problem in different ways, and there has been some debate as to the merits of various approaches to identification. But at this point, even a skeptic would have to concede that the case has been made. Perhaps the cleanest evidence comes from a series of “natural experiments” which isolate shocks to firms’ financial positions that appear obviously unrelated to (at least a subset of) their investment opportunities. For example, Blanchard, Lopez-de-Silanes and Shleifer (1994) show that firms’ acquisition activity responds to large cash windfalls coming from legal settlements unrelated to their ongoing lines of business. Peek and Rosengren (1997) document that declines in the Japanese stock market lead to reductions in the USA-lending-market share of USA branches of Japanese banks, with these reductions being larger for banks with weaker balance sheets. Similarly, Froot and O’Connell (1997) find that reinsurance companies cut back on their supply of earthquake insurance after large hurricanes impair their capital positions.25

A related natural-experiment approach to identification, pioneered by Lamont (1997), involves looking at how investment in one division of a firm responds to shocks originating in another, ostensibly unrelated division. As has been found by Lamont (1997), Lang, Ofek and Stulz (1996), Houston, James and Marcus (1997), Shin and Stulz (1998) among others, increases in cashflow or decreases in leverage attributable to one of a firm’s divisions translate into significant increases in the investment of other divisions. As these papers ultimately speak more to the topic of the second part of this essay–within-firm investment allocation – I defer a more complete discussion of them until later. For the time being, suffice it to say that they represent one more nail in the coffin of the Modigliani–Miller null hypothesis that a firm’s investment is unrelated to its liquidity position or its leverage ratio.

From correlation to causation

It is reasonably straightforward to establish whether there is an association between two variables using standard statistical methods. Understanding whether such a statistical correlation can be interpreted as a causal effect of one variable, the treatment, on the other, the outcome, is, however, another question. The problem is that there may well be other reasons why this association comes about. One reason would be “reverse causality”, which describes a situation where the outcome of interest asserts a causal effect on the treatment of interest. Another example of alternative reasons for the association is that of “omitted variables”, where a third variable affects both treatment and outcome.

Whenever other reasons exist that give rise to a correlation between a treatment and an outcome, the overall correlation cannot be interpreted as a causal effect. This situation is commonly referred to as the endogeneity problem. The term originates from the idea that the treatment cannot be viewed as exogenous to the model determining the outcome, as it should be, but that it is rather endogenously determined within the model—depending on the outcome or being jointly determined with the outcome by a third factor. Because of the problem of endogeneity, simple estimates of the association between treatment and outcome based on correlations will be biased estimates of the causal effect of treatment on outcome.2

Standard approaches such as multivariate regression models try to deal with this problem by observing other sources of a possible correlation and by taking out the difference in outcomes that can be attributed to these other observed differences. This allows estimating the association between treatment and outcome conditional on the effects of observed factors. The required assumption for the identification of a causal effect in this case is often called selection-on-observables assumption. It implies that the conditional estimate identifies the causal effect of interest if selection into treatment is sufficiently described by the observed variables included in the model. However, more often than not, one cannot observe all relevant and non-ignorable variables. But as long as part of the omitted variables stay unobserved, the estimated conditional association will not necessarily warrant a causal interpretation.

Over the past two decades, it has become increasingly apparent in the literature on the economics of education that there are myriad important factors that remain unobserved in our models of interest, often rendering the attempts to control for all relevant confounding factors in vain. Just think of such factors as innate ability of students, parental preferences for certain outcomes, the teaching aptitude of teachers, or the norms and values of peers and neighborhoods. Even if one manages to obtain observable measures of certain dimensions of these factors, others—often important ones—will remain unobserved. Even more, controlling for observable factors does not solve the endogeneity problem when it is due to plain reverse causality, in that the outcome causes the treatment. The only solution is to search for variation in treatment that is not related with other factors that are correlated with the outcome.

The same caveats that apply to the traditional models also apply to other techniques that ultimately rely on a selection-on-observable assumption such as propensity score matching. The central idea of this technique is to find matching pairs of treated and untreated individuals who are as similar as possible in terms of observed (pre-treatment) characteristics. Under certain assumptions, this method can reduce the bias of the treatment effect. But as long as relevant factors remain unobserved, it cannot eliminate the bias (see, e.g., Becker and Ichino (2002)). In this sense, matching techniques cannot solve the endogeneity problem and suffer as much from bias due to unobserved factors as traditional models.3

In this chapter, we turn to techniques, increasingly applied by economists, that aim to provide more convincing identification of causal effects in the face of unobservable confounding factors. In medical trials, only some patients get treated, and the assignment to the group of treated and non-treated patients is done in a randomized way to ensure that it is not confounded with other factors. The non-treated patients constitute a so-called control group to which the treated patients are compared. The aim of the discussed techniques is to mimic this type of experimental design, often using data not generated by an explicitly experimental design. The techniques aim to form a treatment group (that is subject to the treatment) and a control group (that is not subject to the treatment) which are exactly the same. That is, they should not have been sub-divided into treatment and control group based on reasons that are correlated with the outcome of interest. Ideally, one would like to observe the same individuals at the same point in time both in the treated status and in the non-treated status. Of course, this is impossible, because the same individual cannot be in and out of treatment at once. Therefore, the key issue is estimating what would have happened in the counterfactual—which outcome a treated individual would have had if she had not been treated.

The central idea of these techniques is that if the separation of the population into treatment and control group is purely random and a sufficiently large number of individuals is observed, then randomness ensures that the two groups do not differ systematically on other dimensions. In effect, the mathematical law of large numbers makes sure that the characteristics of those in the treatment group will be the same as those in the control group. Thus, the causal effect of the treatment on the outcome can be directly observed by comparing the average outcomes of the treatment group and the control group, because the two groups differ only in terms of the treatment. The aim of the empirical methods discussed in this chapter is to generate such proper treatment and control groups and thus rule out that estimates of the treatment effect are biased by unobserved differences.

4.2.2 Instrumental variables

As observed above, in many contexts social capital is endogenous social capital. The problem of endogeneity is obvious in many contexts; when one talks about membership in organizations, one must account for the fact that membership is a choice variable. In other cases, the endogeneity problem is more subtle. Measures of trust are often used to characterize social capital. Since trust presumably is related to trustworthiness in actual behavior, such measures will exhibit endogeneity problems as well.

Many researchers have recognized that social capital is endogenous and so have employed instrumental variables to allow for consistent estimation of parameters. Leaving aside issues of self-selection that are not often not appropriately addressed by instrumental variables approaches, the use of instrumental variables in social capital studies can be subjected to criticism. Specifically, in many social capital studies the choice of instrumental variables often appears to rely on ad hoc and untenable exogeneity assumptions.

For example, Narayan and Pritchett (1999), using village level data, argue that measures of village level trust can instrument for measures of group memberships. In their analysis social capital effects are argued to occur when one individual’s ‘associational life’ affects others in his village; measures of associational life include factors such as the number of group memberships. Since associational life may be a consumption good and thereby an increasing function of individual income, Narayan and Pritchett argue that it must be instrumented if one wants to identify how social capital causally affects income. Yet, there is little reason that such a variable is a valid instrument. As pointed out above, if trust is related to trustworthiness, as presumably is the case, then there is no reason why trustworthy behavior is any different than membership in an organization in terms of whether it is a choice variable. And without a theory of what determines trustworthy behavior, there is little hope of identifying credible instrumental variables for it in these types of regressions.

The choice of instrumental variables is often one of the most difficult problems in empirical work. In social capital contexts, the absence of explicit modeling of the process by which groups are formed and social capital created means that an empirical researcher is forced to rely on intuition and guesswork. While this does not condemn all studies using instrumental variables, we do believe that inadequate attention has been paid to justifying instrumental variables in social capital contexts.

5 The Endogeneity Problem

All probabilistic statistics require conditional independence, namely that the values of the predictor variables are assigned independently of the dependent variable. The basic problem of endogeneity occurs when the explanans (X) may be influenced by the explanandum (Y) or both may be jointly influenced by an unmeasured third. The endogeneity problem is one aspect of the broader question of selection bias discussed earlier.

The endogeneity issue has been debated intensely within the economic growth literature in terms of the causal relationship between technology and growth. But it applies equally to many fields. For example, comparativists often argue that left power explains welfare state development. But are we certain that left power, itself, is not a function of strong welfare states? Or, equally likely, are both large welfare states and left power just two faces of the same coin, different manifestations of one underlying, yet undefined, phenomenon? Would Sweden have had the same welfare state even without its legendary social democratic tradition? Perhaps, if Sweden's cultural past overdetermines its unique kind of social democracy and social policy. If this kind of endogeneity exists, the true X for Sweden is not left power but a full list of all that is ‘Sweden.’ The vector of the X's becomes a list of all that is nationally unique.

The endogeneity problem becomes easily intractable in quantitative cross-national research because we observe variables (Y's and X's) that represent part of the reality of the nations we sample. Our variables are in effect a partial reflection of the society under study, and the meaning of a variable score for one nation may not be metrically equivalent to that of another—a weighted left cabinet score of 35 for Denmark and 40 for Sweden probably misrepresents the Danish–Swedish difference if, that is, the two social democracies are two different beasts.

A related, and equally problematic, issue arises in the interpretation of coefficient estimations. In the simple cross-sectional regression, the coefficient for left power, economic development or for coordinated bargaining can only be interpreted in one way: as a constant, across-the-board effect irrespective of national context. If Denmark had 5 points more left power, its welfare state should match the Swedish (all else held constant). In fixed-effects panel regressions, the X's are assumed to have an identical impact on Y, irrespective of country. Often we cannot accept such assumptions.

The reason that we cannot is that it is difficult to assume that variables, say a bargaining institution or party power balance, will produce homogenous, monotonically identical, effects across nations for the simple reason that they are embedded in a more complex reality (called nation) which has also given rise to its version of the dependent variable. In this case, the bias remains equally problematic whether we study few or many N's; it will not disappear if we add more nations. Quantitative national comparisons rarely address such endogeneity problems. Studies of labor market or economic performance routinely presume that labor market regulations or bargaining centralization are truly exogenous variables, whose effects on employment is conditionally identical whether it is Germany, Norway, or the United States. The same goes for welfare state comparisons with their belief that demography and left power are fully exogenous and conditionally unitary.

There exist several, not necessarily efficient, ways of correcting for the endogeneity bias. If we have some inkling that the bias comes from variable omission, the obvious correction entails the inclusion of additional controls. An example of this kind was Jackman's (1986) argument that Norway's North Sea Oil was over-determining the results in the Lange and Garrett (1985) study. Small N studies with strong endogeneity have little capacity to extend the number of potentially necessary controls. A second approach is to limit endogeneity in X by reconceptualizing and, most likely, narrowing Y. The welfare state literature provides a prototypical example: aggregate social expenditure increasingly was replaced by measures of specific welfare state traits.

Controls, no matter how many, will however not resolve the problem under conditions of strong sampling bias. As discussed above, the best solution in such a situation is to concentrate more on the theoretical elaboration of causal relations between variables. If we can assume that our estimations are biased because Y affects the values on X, or because both are jointly attributable to a third underlying force, thinking in counterfactual terms (‘would Sweden's welfare state be the same without Sweden's social democracy’) will force the researcher to identify more precisely the direct or derived causal connections (Fearon 1991). If bias can be assumed to come from the assumption of monotonically homogeneous effects of the X across all nations, the researcher's attention should concentrate on identifying more precisely the conditional mechanisms that are involved in the causal passage from an X to a Y (why and how will a 5-point rise in left power make the Danish welfare state converge with the Swedish?).

6.3.5 Endogenous variables

An endogenous variable is an explanatory variable whose value is determined or influenced by one or more variables in the model. In contrast, exogenous variable values are not determined or affected by changes in the other variables of the model. Carson and Mannering (2001) studied the endogeneity problem by exploring the effectiveness of ice-warning signs in reducing the frequency of ice-related crashes. An indicator variable for the presence of an ice warning sign is typically used when developing a crash-frequency model. As ice-warning signs are more likely to be placed at locations with high numbers of ice-related crashes, this indicator variable may be endogenous (the explanatory variable will change as the dependent variable changes). If this endogeneity is ignored, the parameter estimates will be biased. In the case of the ice-warning sign indicator, ignoring the endogeneity may lead to the erroneous conclusion that ice-warning signs actually increase the frequency of ice-related crashes because the signs are going to be associated with locations of high ice-crash frequencies. Kim and Washington (2006) studied the effectiveness of left-turn lanes at intersections on the angle crashes. Left-turn lane is considered an endogenous variable because it is more likely to be placed at intersections with a high number of left-turn related crashes. To address the endogeneity problem, Kim and Washington (2006) used a limited-information maximum likelihood estimation approach. First, they developed a logistic regression model with a left-turn lane presence indicator as a dependent variable and angle crash frequency as one of the explanatory variables. The estimation results for the left-turn lane indicator were then used as an explanatory variable in the crash count model. Their study results showed that left-turn lanes increase crashes when not accounting for endogeneity; however, this variable showed a negative effect on angle crash frequencies when endogeneity is considered in the model.

Spatial Weights and the Spatial Lag Operator

In spatial econometrics, the neighbor relation is typically expressed by the means of a nonnegative matrix, known as spatial weights matrix. In a spatial weights matrix, often indicated by W, the rows and columns correspond to the cross-section observations (e.g., individuals, regions, or countries), and the generic element, wij, can be interpreted as the strength of potential interaction between units i and j. The specification of W is generally arbitrary, typically based on some measures of distance between units, using, for example, contiguity or geographic proximity, or more general metrics, such as economic, political, or social distance. To avoid nonlinearity and endogeneity problems, spatial weights should be exogenous to the model, a condition that is not guaranteed when using more general distance metrics. By convention, the diagonal elements of the weighting matrix are set to 0, implying that an observation is not a neighbor to itself. Further, to facilitate the interpretation of estimates in spatial models, W is typically row-standardized so that the sum of the weights for each row is 1, ensuring that all the weights are between 0 and 1. Finally, although most empirical works assume that weights are time-invariant, these can vary over time.

An important role in spatial econometrics is played by the notion of spatial lag operator. Let zit be the observation on a variable for the ith cross-section unit at time t for i=1, 2,…, N; t=1, 2,…, T. Let zt=(z1t, z2t,…, zNt)′, and W={wij} be a time-invariant N×N spatial weights matrix. The spatial lag of zt is given by Wzt, with generic ith element

∑j=1Nwijzjt

Hence, a spatial lag operator constructs a new variable, which is a weighted average of neighboring observations, with weights reflecting distance among units. The incorporation of these spatial lags into a regression specification is considered in the next section.

14.4.4.3 The impact of the affordable housing goals

Continued evidence of redlining in the 1960s and 1970s led the federal government to pass laws aimed at increasing lending to low-income households. The most important of these laws were the CRA in 1977 and the GSE Act of 1992. These laws mandated qualifying banks and the GSEs to meet minimum purchase requirements of mortgages held by low-income and minority households. These are referred to as the affordable housing goals.

For qualifying banks, the most common way of meeting the CRA goals was by originating or buying residential mortgages for properties in low- to moderate-income census tracts, those where median family income is less than 80% of area median income in their assessment areas (usually counties in which they have deposit-taking offices/branches). Loans to low-to-moderate-income borrowers also qualify for meeting the CRA goals. Low-to-moderate-income status is determined using the decennial census. Independent mortgage banks and credit unions are not covered under CRA. Plus, more than half of loans made or purchased by CRA-covered institutions were made outside of their assessment areas, further limiting the number of loans covered under CRA (Avery and Brevoort, 2011).

HUD sets the affordable housing goals for the GSEs related to (1) low- and moderate-income families, (2) purchasers of properties located in historically underserved areas (underserved area goal), and (3) low-income families living in low-income areas and very low-income families (the “special affordable” goal). The low- and moderate-income goal defines a low- or moderate-income household as one whose income is less than or equal to the area median household income. For metropolitan areas, “underserved areas” are defined as census tracts with either (1) at least 30% minority population and with a median family income at or below 120% of the area median family income or (2) a median family income at or below 90% of the area median family income. The “special affordable goal” defines a very-low-income household as a household whose income is less than or equal to 60% of the area median income. For a list of the targets for these three affordable housing mandates, see An et al. (2007).

In this subsection, we look at the effectiveness of the CRA and GSE affordable housing goals in increasing the homeownership rate of low-income households. We also consider indirect evidence about how the affordable housing goals affected loan volume since this is a necessary condition for there to be an effect on the overall homeownership rate. The issue of loan quality is also discussed since this has received so much attention in relation to the financial crisis and because it is tied in so closely with credit supply.

Some studies blame the CRA and the GSEs for their role in perpetrating the financial crisis by motivating originators to lower their standards and extend credit to risky borrowers to meet the affordable housing goals.39 To put this issue in context, as reported by Bhutta and Canner (2009) using HMDA data for 2005 and 2006, only 6% of subprime mortgage originations qualified under CRA and the performance of CRA-related subprime loans was similar to other subprime loans. For the most part, subprime mortgages were not conforming loans so they were not eligible to be directly purchased by the GSEs whether or not they could be used to meet their affordable housing goals. So the task is to show how CRA and the GSEs could have had such a large impact on the financial crisis given that they were involved in such a small percentage of subprime originations. The GSEs did purchase PLMBS tranches that included subprime mortgages that could be used to meet their affordable housing goals. We will also look at this avenue as a potential way that the GSEs could have contributed to the financial crisis.

Credible investigations into the impact of the affordable housing goals on the homeownership rate and their role in the financial crisis require controlling for the numerous sources of omitted variable bias that can contaminate the results. Hence, the evidence on the impact of the affordable housing goals on homeownership, loan supply, and loan quality to which we give the most weight is based on some application of the quasi-experimental methodology.40

A common approach to coming up with plausible causal estimates of the affordable housing goals on the homeownership rate, loan volume, and loan performance is to use their cutoffs in terms of census tract median household income relative to area median income or individual household income relative to area median income as the basis for a RD analysis or as a source of exogenous variation to construct valid instruments for GSE or CRA activity. In the rest of this subsection, we discuss such estimates of the impact of the affordable housing goals on the homeownership rate, loan volume, and loan quality.

Papers that estimate the impact of the affordable housing goals on the homeownership rate include Bostic and Gabriel (2006), An et al. (2007; henceforth ABDG), and Gabriel and Rosenthal (2009). All three papers use 1990 and 2000 decennial census data at the census tract level and the latter two use tract-level HMDA data (ABDG from 1995 to 2000 and Gabriel and Rosenthal from 2000). All three use an informal RD approach to compare CRA and/or GSE activity in census tracts just on either side of the affordable housing goal cutoffs (e.g., census tracts with median family income that is 80% and 90% of area median income for CRA and the GSEs, respectively). For the CRA target, Gabriel and Rosenthal found that there is a positive and significant impact on the supply of nonconforming loans and limited evidence of a positive impact on the homeownership rate. They claimed that this is evidence of the effectiveness of CRA in increasing mortgage supply in targeted areas. Otherwise, the results show little evidence that GSE eligibility had any effect on changes in homeownership rates.

ABDG looked more directly at the GSE effect by using the percent of mortgages in a census tract that were purchased by GSEs and the change in this variable as explanatory variables. They instrumented for these two variables using the GSE target indicators and the total number of conforming loans in 1995. They found that GSE intensity has a significantly positive impact on the change in the homeownership rate and the percent change in GSE intensity had a significantly negative impact on vacancy rates and a significantly positive impact on house prices. This is evidence that GSE intensity is related to neighborhood improvements.

Gabriel and Rosenthal (2010), Avery and Brevoort (2011), Bhutta (2011, 2012), Ghent et al. (2013), Moulton (2014), and Bolotnyy (2014) are the best studies that attempt to show a causal impact of the affordable housing goals on loan volume (subprime or prime). The central theme of these papers is to use the affordable housing goals in a RD framework to estimate their causal impact on the quantity and quality of loans. The main takeaway from these studies is that, for the period from the mid-1990s to 2007, there is little evidence that the affordable housing goals had a significant impact on any of these factors. Agarwal et al. (2012b) estimated that CRA led to a decline in loan quality using plausibly exogenous variation in banks' incentives to meet CRA goals around regulatory exams. But Reid et al. (2013) and Foote et al. (2013) criticized the exogeneity assumption used by these authors to obtain their estimates.

One reason for the lack of an impact of the affordable housing goals on the mortgage market is crowd out. That is, the activities of the GSEs just displace mortgage supply that would have occurred in their absence. Gabriel and Rosenthal (2010) showed that crowd out in the home purchase market (most relevant for the homeownership rate) is positively related to the level of market activity; it was most prevalent during the 2003–2006 period when it reached the 50% level. Little crowd out existed in periods prior to and subsequent to this market boom, particularly during the 2007–2008 period when private intermediaries essentially pulled out of the market. Gabriel and Rosenthal concluded that the government takeover of the GSEs was effective in providing liquidity to the mortgage market during the financial crisis.

Ghent et al. (2013; henceforth GH-MO) estimated the impact of the affordable housing goals on subprime mortgage volume, pricing, and performance. The focus on subprime loans is key to answering the question “did GSE or CRA affordable lending goals contribute to the financial crisis?” since it was the subprime market and not the prime market that imploded. Subprime loans typically cannot be directly purchased by the GSEs since they are nonconforming loans and the majority of subprime loans are not purchased by CRA-eligible entities, so GH-MO focused on the holdings of PLMBS by the GSEs and CRA-eligible depository institutions that are made up of subprime loans.

GH-MO found that while 70% of mortgages in their sample satisfy the affordable housing goals, none of the PLMBS pools that they examined were CRA-qualified. This is because there are very strict guidelines for MBSs to satisfy CRA goals (only loans from a CRA-eligible institution's assessment area count toward the goal). On the other hand, if a GSE purchases a PLMBS and only 20% of the loans in this security satisfy GSE goals, the GSE can count this 20% toward its affordable housing goals. But it is also questionable that the GSEs were primarily buying the PLMBS to satisfy the borrower-related affordable housing goals since the average borrower income to area median income ratio was 1.73. It appears that the CRA-eligible institutions and the GSEs were buying PLMBSs only for investment purposes.

GH-MO found no significant impact of affordable housing goals (via either CRA or the GSEs) on subprime mortgage volume, pricing, or performance (90 + days delinquent or foreclosures within 2 years of origination). They concluded that it is still possible that the GSEs affected the subprime market by purchasing large numbers of PLMBS since this may have increased credit supply that was used to buy even riskier mortgages.

In summary, a few studies find significant effects of the affordable housing goals on the homeownership rate (An et al., 2007; Gabriel and Rosentha, 2009). But generally, there is little evidence of a significant impact of the GSE and CRA affordable housing goals on the homeownership rate, loan volume, or loan performance. This is the case for both prime and subprime loans. The latter result found by Ghent et al. (2013) is the strongest evidence that the affordable housing goals had no impact on the financial crisis since this was fueled by the poor performance of subprime loans.