Debt Relief or Debt Restructuring? Evidence from an Experiment with Distressed Credit Card Borrowers

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1 Debt Relief or Debt Restructuring? Evidence from an Experiment with Distressed Credit Card Borrowers Will Dobbie Princeton University and NBER Jae Song Social Security Administration May 2016 Abstract This paper reports results from a randomized field experiment that offered distressed credit card borrowers more than $50 million in debt forgiveness and over 27,500 additional months to repay their debts. The experimental variation effectively randomized financing charges and repayment periods for debts held by eleven large credit card issuers. Merging information from the experiment to administrative tax and bankruptcy records, we find that the lower financing charges increased debt repayment and decreased bankruptcy filing. The lower financing charges also increased employment rates for the most financially distressed borrowers. In contrast, we find little impact of a longer repayment period on debt repayment, bankruptcy, or employment. We show that this null result can be explained by the positive short-run effect of increased liquidity being offset by the negative long-run effect of exposing borrowers to more default risk. We are extremely grateful to Ann Woods and Robert Kaplan at Money Management International, David Jones at the Association of Independent Consumer Credit Counseling Agencies, Ed Falco at Auriemma Consulting Group, and Gerald Ray and David Foster at the Social Security Administration for their help and support. We thank Tal Gross, Matthew Notowidigdo, and Jialan Wang for providing the bankruptcy data used in this analysis. We also thank Hank Farber, Roland Fryer, Paul Goldsmith-Pinkham, Tal Gross, Larry Katz, Ben Keys, Patrick Kline, Alex Mas, Jesse Shapiro, Andrei Shleifer, Crystal Yang, Jonathan Zinman, Eric Zwick, and numerous seminar participants for helpful comments and suggestions. Daniel Herbst, Disa Hynsjo, Samsun Knight, Kevin Tang, Daniel Van Deusen, and Yining Zhu provided excellent research assistance. Financial support from the Washington Center for Equitable Growth is gratefully acknowledged. Correspondence can be addressed to the authors by [Dobbie] or [Song]. Any opinions expressed herein are those of the authors and not those of the Social Security Administration.

2 During the financial crisis, U.S. policymakers implemented a series of reforms to encourage lenders to forgive or restructure distressed mortgage debt in an attempt to stimulate the broader economy. 1 Over the same time period, credit card issuers reduced the financing fees and lengthened the repayment periods of their most financially distressed cardholders, while both card issuers and consumer advocates lobbied U.S. officials for regulatory changes that would have allowed for even more generous concessions. 2 In theory, forgiving or restructuring distressed debts can increase aggregate consumption and employment by decreasing debt overhang, potentially making these policies ex-post efficient during economic downturns (e.g. Hall 2011, Eggertsson and Krugman 2012, Mian, Rao, and Sufi 2013, Mian and Sufi 2014). Debt relief programs can also be ex-post efficient in regular economic conditions if debt contracts are incomplete (e.g. Bolton and Scharfstein 1996, Bolton and Rosenthal 2002) or there are negative spillovers of loan default (e.g. Campbell et al. 2011, Mian, Sufi, and Trebbi forthcoming). 3 To date, however, there is little empirical evidence on how reducing or restructuring distressed debt affects borrower behavior. This paper provides new evidence on the impact of debt relief and debt restructuring using information from a large randomized field experiment matched to administrative tax and bankruptcy records. The experiment was designed and implemented by the largest non-profit credit counseling organization in the United States. One of the most important services offered by the non-profit organization is a structured repayment program that allows eligible borrowers to simultaneously repay all of their credit card debts over three to five years. In exchange for voluntarily enrolling in the repayment program, creditors will typically stop recording the debt as delinquent on credit reports, reduce or eliminate interest payments and late fees, and lower the required monthly payments by lengthening the repayment period. 4 In the experiment, eleven large credit card issuers agreed to offer more favorable terms on this 1 These reforms included the Hope Now initiative that asked lenders to prevent adjustable-rate mortgages from increasing to higher rates at the first mortgage rate reset, the Home Affordable Refinancing Program (HARP) that provided federal guarantees on refinances of eligible mortgages, and the Home Affordable Modification Program (HAMP) that provided financial incentives to modify distressed mortgages. See Agarwal et al. (2012) for estimates of the ex-post effects of mortgage modifications made through HAMP. 2 In the United States, credit card issuers are not allowed to simultaneously reduce a borrower s original principal and lengthen his or her repayment period without classifying the debt as impaired. In cases where the original principal can be reduced without the debt being classified as impaired, credit card borrowers are normally required to pay off the remaining debt in just a few months. The Financial Services Roundtable, which represents more than 100 large financial companies, and the Consumer Federation of America, a large consumer rights advocate, proposed amending these regulations to allow issuers to, on a trial basis, forgive up to 40 percent of a credit card borrower s original principal, restructure the remaining principal to be repaid over a number of years, and defer any income taxes owed on the forgiven principal. Reports indicated that many large credit card issuers were interested in participating in the proposed pilot program. For example, see banks-asking-for-credit-c_n_ html 3 There may also be important ex-ante effects of allowing ex-post loan modifications. See Bolton and Rosenthal (2002) for a discussion of the ex-ante and ex-post efficiency of debt relief when debt contracts are incomplete, and Mayer et al. (2014) for estimates of the ex-ante response to the announcement of a mortgage modification program. 4 To help ensure that creditors also benefit from participation in the repayment program, credit counseling agencies screen borrowers so that participants (1) have a sufficient cash flow to repay their debts over the three to five year period of the plan and (2) cannot reasonably repay their debts without a repayment program. Historically, creditors have given credit counseling agencies the incentive to effectively screen potential participants using a combination of monitoring and payments in proportion to the recovered debt. See Section I for additional details. 1

3 repayment program to a random subset of credit card borrowers that contacted the non-profit organization between January 2005 and August Specifically, control borrowers were offered the standard repayment program, while treated borrowers were offered a repayment program with significantly more generous interest rate reductions and repayment period extensions. The median interest rate reduction in the experiment decreased the typical borrower s financing charges by $1,712, a percent reduction, by reducing the number of repayment periods by about four months, a 7.99 percent decrease. The interest rate treatment did not affect the monthly payment amount, however, meaning that short-run liquidity constraints were not affected by the rate reduction. As a result, the interest rate treatment is likely to increase enrollment in the repayment program only if borrowers value debt forgiveness three to five years in the future. The interest rate treatment is therefore unlikely to change enrollment rates if short-run liquidity constraints, and not long-run debt overhang concerns, are the most important determinants of borrower behavior on the margin. Conditional on enrolling in the program, however, the interest rate treatment may increase the probability of completing the repayment program by mechanically reducing the treatment group s default rates to zero during the approximately four month time period when their payments are forgiven. Conversely, completion rates will be relatively unaffected if default risk is concentrated in the first one to three years of the repayment program. The median repayment period increase lengthened the typical borrower s term length by just over four months, a 7.99 percent increase, by reducing the required minimum payment by $26.68, a 6.15 percent reduction. The repayment period treatment is therefore likely to decrease liquiditybased defaults at the beginning of the repayment program by lowering the required payments, but increase defaults at the end of the repayment program by increasing the exposure to default risk. Thus, the repayment period treatment is likely to increase repayment rates only if liquidity constraints bind early in the repayment program and default risk is relatively low at the end of the repayment program. 5 If liquidity constraints are not the primary driver of borrower behavior or there is persistent default risk at the end of the repayment program, the combination of a longer repayment period and lower minimum payments is unlikely to benefit borrowers. In total, treated borrowers were offered more than $50 million in reduced financing charges and over 27,500 additional months to repay their debts as a part of the experiment. While most treated borrowers were offered some combination of both treatments, we can separately identify the effects of being offered lower interest rates and longer repayment periods by exploiting the fact that there is significant across-borrower variation in potential treatment intensity, that is, the borrower-specific difference between the treatment repayment program offer and the control repayment program offer. To do this, we first use our data to calculate each borrower s hypothetical treatment and control repayment program offers. This calculation makes it possible to exactly identify individuals with 5 The combination of lower minimum payments and a longer repayment period also changes the option value of repayment, and hence the incentive to strategically default. The direction of this strategic effect is ambiguous as lower payments both increase future flexibility, increasing the option value of repayment, and transfer a portion of the debt burden into the future, decreasing the option value of repayment. We assume throughout that the liquidity effect net of these indirect strategic effects is positive. See Section II for additional details. 2

4 identical treatment intensities but different treatment statuses. We then isolate the effects of each treatment by comparing the impact of the randomized experiment across borrowers that differed in their potential treatment intensity. 6 We measure the effects of the randomized experiment using three administrative datasets matched for the purposes of this study. Debt repayment is measured using administrative records from the credit counseling organization. Financial distress is measured using court bankruptcy records. Earnings, employment, and 401k contributions are measured using tax data from the Social Security Administration (SSA). The matched dataset allows us to estimate the mediumrun effects of the lower interest rates and longer repayment periods across a range of important outcomes. In our empirical analysis, we find that lower interest rates had significant ex-post benefits for both lenders and borrowers, particularly when given to the most financially distressed borrowers. The median interest rate reduction increased the probability of debt repayment by 1.33 percentage points, a 9.73 percent increase from the control group mean. Back-of-the-envelope calculations suggest that the interest rate reductions increased lender profits by at least $23 per borrower. We also find that lower interest rates also decreased the probability that the most distressed borrowers filed for bankruptcy protection in the next five years by 1.36 percentage points, an decrease, and increased the probability of being employed over the same time period by 1.69 percentage points, a 2.17 percent increase. The estimated effects of lower interest rates on both earnings and 401k contributions are small and not statistically significant for most borrowers, with the exception of borrowers unemployed just prior to the experiment. For these unemployed borrowers, earnings decreased by $2,077 and 401k contributions decreased by $ The employment effects are also negative for borrowers unemployed at baseline, but the point estimate is not statistically significant. These results suggest that debt relief may decrease labor supply for borrowers most on the margin of work, with negligible effects for most other borrowers. In sharp contrast, there are no economically or statistically significant benefits of being offered the combination of lower minimum payments and a longer repayment period. Lower minimum payments had no discernible impact on debt repayment, with the 95 percent confidence intervals ruling out treatment effects larger than 0.15 percentage points for the median payment reduction. The median payment reduction also increased the probability of filing for bankruptcy protection in the next five years by a statistically insignificant 0.70 percentage points, a 6.75 percent increase from the control group mean. There were also no detectable effects on employment, earnings, or 401k contributions for any borrowers in our sample. The second part of the paper explores the potential mechanisms driving the reduced form 6 The across-borrower variation in potential treatment intensity is driven by two factors: (1) the fact that that seven of the eleven participating issuers offered different combinations of interest rate and monthly payment reductions, and (2) the fact that individual borrowers in our sample owed different amounts to these issuers. The resulting across-borrower variation in treatment intensity is substantial. For example, the 75th percentile interest rate reduction decreases the typical borrower s financing charges by $1,521 more than the 25th percentile interest rate reduction. Similarly, the 75th percentile monthly payment reduction increases the typical borrower s repayment period by just over five months more than the 25th percentile monthly payment reduction. See Section III for additional details. 3

5 results. We show that it is possible to test the relative importance of competing mechanisms using treatment effects at different points during the repayment program. For example, for the interest rate treatment, we can test for forward-looking behavior using treatment effects early in the repayment program when both treated and control borrowers are still making monthly payments. The logic behind this test is straightforward because control borrowers and treatment borrowers with lower interest rates have identical monthly payments early in the repayment program, forwardlooking behavior is the only explanation for any observed differences between these two groups during this time period. Conversely, differences between the two groups at the end of the repayment program could be due to either forward-looking behavior or decreased exposure to default risk. A similar procedure allows us to examine the relative importance of increased liquidity versus increased exposure to default risk for the minimum payment treatment. Using this approach, we find that nearly all of the positive effects of the interest rate treatment can be explained by forward-looking behavior. Taken at face value, our point estimates suggest less than 14.8 percent of the interest rate effect can be explained by decreased exposure to default risk at the end of the repayment program. Unfortunately, however, we are unable to distinguish between the different types of forward-looking behavior that could be driving our results. For example, we cannot test whether borrowers are making rational forward-looking decisions based on the increase in future solvency, or non-rational or behavioral decisions based on some aspect of the experimental design, such as the framing of the interest rate decrease as a reduction in financing fees. Nevertheless, these results stand in stark contrast to the widespread view that distressed credit card borrowers are almost completely present-focused. Consistent with theory, we also find that the minimum payment treatment modestly decreased liquidity-based defaults early in the repayment program. However, any positive effect from the increased liquidity is nearly exactly offset by the negative effect of increased exposure to default risk late in the repayment program. These results help to reconcile our reduced form estimates with a large literature documenting the importance of liquidity constraints in a variety of settings (e.g. Gross and Souleles 2002, Johnson, Parker, and Souleles 2006, Agarwal et al. 2007, Parker et al. 2013, Di Maggio, Kermani, and Ramcharan 2014, Keys et al. 2014, Agarwal et al. 2015, Fuster and Willen 2015). For example, recent work by Zinman (2015) shows that approximately 75 percent of households are affected by debt and liquidity constraints. Yet, our findings suggest that the combination of lower minimum payments and a longer repayment period is an ineffective way to increase repayment rates when there is persistent default risk, at least in settings such as ours where the reduction in the minimum payment amount is relatively modest. Our results are also related to an emerging literature estimating the impact of mortgage modifications on borrower outcomes. There is evidence that mortgage modifications made through the Home Affordable Modification Program modestly decreased foreclosure rates and defaults on nonmortgage debt, although it is unclear whether the effects were driven by lower interest rates, principal reductions, or repayment period extensions (Agarwal et al. 2012). However, cross-sectional comparisons suggest that principal forgiveness is more effective than other types of mortgage mod- 4

6 ifications (Haughwout, Okah, and Tracy 2010), and recent theoretical work suggests that payment deferrals are likely to increase the probability of default unless paired with some sort of debt relief (Eberly and Krishnamurthy 2014). 7 We view our results as being broadly consistent with these findings, although in a very different setting. This paper is also related to recent work estimating the effects of consumer bankruptcy protection, which combines elements of both debt relief and debt restructuring. There is evidence that bankruptcy protection decreases recipients post-filing financial distress (Dobbie, Goldsmith- Pinkham, and Yang 2015) and increases recipients post-filing earnings and employment (Dobbie and Song 2015). There is also evidence that the consumer bankruptcy system provides implicit health insurance (Gross and Notowidigdo 2011, Mahoney 2015) and aggregate consumption insurance (Dobbie and Goldsmith-Pinkham 2014). Related work suggests that in the absence of any debt relief and debt restructuring, debt overhang can affect labor supply (Bernstein 2016), entrepreneurial activity (Adelino, Schoar, and Severino 2013), and home investment (Melzer forthcoming). However, none of these papers are able to identify the mechanisms through which debt relief or debt restructuring benefits debtors. The remainder of this paper is structured as follows. Section I describes the institutional setting and experimental design. Section II provides a simple conceptual framework for interpreting the experimental results. Section III describes our data and empirical design. Section IV presents our main results of how the randomized experiment affected debt repayment, bankruptcy, labor market outcomes, and savings. Section V explores the potential mechanisms driving our results. Section VI concludes. I. Background and Experimental Design A. Background The randomized experiment described in this paper was implemented by Money Management International (MMI), the largest non-profit credit counseling agency in the United States. In the early 1950s, major credit card issuers helped established the first non-profit credit counseling organizations, including MMI, in an effort to decrease the number of bankruptcy filings and increase recovery rates for delinquent card debt. Today, non-profit credit counseling organizations such as MMI provide a wide range of services to its clients via phone and in-person sessions, including general financial advice, credit counseling, bankruptcy counseling, and housing counseling. One of the most important products offered by non-profit credit counselors is the debt management plan (DMP), a structured repayment program that simultaneously repays all of a borrower s 7 Related work suggests that initial loan demand is price sensitive in the credit card (Gross and Souleles 2002) and home equity line markets (Bhutta and Keys 2014), but not the mortgage market (DeFusco and Paciorek 2014). Interest rates have also been shown to impact the number of borrowers but not total profits in a microcredit market in Mexico (Karlan and Zinman 2014), and there is evidence that loan demand is affected by both the down payment amount (Adams et al. 2009) and the available loan amount (e.g. Dobbie and Skiba 2013). See Zinman (2015) for a review of this literature. 5

7 unsecured creditors through a series of monthly payments over three to five years. 8 Under the DMP, the credit counseling agency negotiates directly with each of the borrower s creditors to reduce the monthly payments, interest payments, and late fees on each credit card account. In most cases, creditors will also stop recording debt as delinquent on the borrower s credit report. The borrower then makes one payment per month to the counseling agency that is disbursed to his or her creditors according to the terms of the restructured agreements. The minimum payment for each account typically ranges from two to three percent of the initial debt, although borrowers always have the option to pay more than this minimum requirement in order to reduce the term length. In our sample, the average monthly payment for the control group is 2.38 percent of initial debt, or about $437 per month, and the average term length is 52.6 months. If a borrower misses a monthly payment, most creditors will allow the borrower to resume payments in the next month with no additional penalties. If a borrower withdraws from the repayment program or is dropped for missing too many monthly payments, however, any remaining debts are typically sent to collection. Either the original creditor or a third-party debt collector will then attempt to collect the debt through collection letters or phone calls, in-person visits at home or work, wage garnishment orders, and asset seizure orders. Borrowers can make these collection efforts more difficult by ignoring collection letters and calls, changing their telephone number, or moving without leaving a forwarding address. Borrowers can also leave the formal banking system to hide their assets from seizure, change jobs to force creditors to reinstate a garnishment order, or work less so that their earnings are not subject to garnishment. As an alternative, borrowers can also choose to discharge any remaining debts through the consumer bankruptcy system. In exchange for the credit counselor s help in securing at least partial payment of the debt through the DMP, creditors typically pay the counseling agency a portion of the total monthly payment, known as a fair share payment. Fair share payments have become somewhat less generous over time, falling from about twelve to fifteen percent in the 1990s to about five to ten percent today. The borrower s monthly payment also includes a small administrative fee to the credit counselor of about $10 to $50 to help cover any remaining costs of administering the DMP (Wilshusen 2011). To the best of our knowledge, both the fair share payments and administrative fees remained relatively constant throughout the experiment. Creditor participation in a repayment program is completely voluntary, and creditors may choose to participate in only a subset of the repayment programs proposed by credit counseling agencies. In principle, a creditor will only participate in a repayment program if doing so increases the expected repayment rate, presumably because the borrower is otherwise likely to file for bankruptcy protection or default on his or her debts outside of the formal bankruptcy system (Wilshusen 2011). Consistent with this view, cross-sectional comparisons suggest that individuals enrolled in a DMP are less likely to file for bankruptcy (Staten and Barron 2006) and less likely to 8 Under current regulatory guidelines, the term length for a DMP cannot exceed five years. If borrowers cannot fully repay their credit card debts within this five year limit, they cannot participate in a DMP unless the creditor is willing to write off a portion of the original balance and recognize the loan as impaired. To date, creditors have typically been unwilling to do this (Wilshusen 2011). 6

8 report financial distress (O Neill et al. 2006) compared to otherwise similar individuals. Creditors can also directly refer borrowers to a credit counseling agency for a DMP if the risk of bankruptcy or delinquency is particularly high. In our sample, approximately 15.5 percent of individuals report that they were refered to MMI by a creditor, with another 33.7 percent of individuals reporting that they learned about MMI from an internet search, 19.8 percent from a family member or friend, and 20.0 percent from a paid advertisement. The remainder were refered by another counseling organization or learned about MMI through another source. To help ensure that creditors benefit from participation in the repayment program, credit counseling agencies screen potential clients to make sure that (1) the borrower has a sufficient cash flow to repay his or her debts over the three to five year period of the plan, and (2) that the borrower cannot reasonably repay his or her debts without a repayment program. Historically, creditors have given credit counseling agencies the incentive to effectively screen potential clients using a combination of monitoring and the fair share payments discussed above. To strengthen the counseling agencies incentive to effectively screen clients, many creditors also condition their fair share payments on completion of the program (Wilshusen 2011). Each year, MMI administers over 75,000 DMPs that repay nearly $600 million in unsecured debt. Nationwide, it is estimated that non-profit credit counselors administer approximately 600,000 DMPs that repay unsecured creditors between $1.5 and $2.5 billion each year (Hunt 2005, Wilshusen 2011). B. Experimental Design Overview: In 2003, MMI and eleven large credit card issuers agreed to offer lower interest rates and longer repayment periods to a subset of individuals interested in the structured repayment program. The purpose of the experiment was to evaluate the effect of more borrower-friendly loan terms on repayment rates and the average recovery amount, particularly for the most financially distressed borrowers. The eleven participating credit card issuers include many of the largest unsecured creditors in the United States, collectively holding over 50 percent of borrowers credit card debt in our sample. The resulting randomized experiment was conducted between January 2005 and August The experimental population consists of the approximately 80,000 prospective clients that contacted MMI during this time period. The experiment only included individuals contacting MMI for the first time during this time period; individuals who had already enrolled in a DMP before January 2005 are excluded from the randomized trial. Counselors with less than six months of experience were also excluded from the experiment. Sequence of Experiment: First, each prospective client was randomly assigned to a credit counselor conditional on the contact date, the client s state of residence, and the reference type. Credit counselors were then rotated between assigning every prospective client to either the control or treatment group in two week intervals. Specifically, for each counselor, the MMI computer system 7

9 would automatically switch from the control group concessions to the treatment group concessions every two weeks. Rotating counselors between the treatment and control groups in this way was meant to ensure that any counselor specific effects would not bias the experiment, and to help ensure that planned experimental procedures were followed as closely as possible. Counselors were also strictly instructed not to inform prospective clients of the randomized trial or tell individuals whether they were assigned to the treatment or control group. A senior credit counselor conducted frequent audits of the counselors to ensure that the experimental procedures were followed and that the treatment and control populations were similar. MMI administrators also conducted weekly audits to ensure that the treatment and control populations remained relatively constant. MMI worked with the participating creditors to design and implement the counselor rotation procedure, but none of the creditors were directly involved with the implementation of the experiment or the audit process. Following the assignment of individuals to counselors, the assigned counselor collected information on the individual s unsecured debts, assets, liabilities, monthly income, monthly expenses, homeownership status, number of dependents, and so on. Identical information was collected from both treated and control borrowers and there was no indication of treatment status communicated to the borrowers. The MMI computer system was then used to calculated the minimum payment, length of the repayment period, and total financing fees for that individual s DMP. These terms depend on the individual s specific debt holdings and whether the individual was in the treatment or control group. Next, the DMP terms were explained to the individual in the context of a number of other repayment options, as is typical for MMI. Importantly, the framing of these options was identical for the treatment and control groups. In most cases, the DMP was explained as follows. First, borrowers were told that they could liquidate their assets and repay their debts immediately, although relatively few distressed borrowers had enough assets to make this a viable option. Next, borrowers were told that they could file for Chapter 7 bankruptcy, which would allow them to discharge their unsecured debts and avoid debt collection in exchange for any non-exempt assets and any court fees. 9 Third, borrowers were told that if they were not interested in filing for bankruptcy protection, that they could continue making their current minimum payments on their credit cards. In a representative call provided to the research team, the MMI counselor explained that if you continue making the minimum payment of $350, it will take you 348 months to repay your credit cards and you will have to spend about $21,300 in financing charges. Finally, borrowers were told about their specific DMP. For example, in the same representative call, the MMI counselor explained that if the individual enrolled in the structured repayment program, her payments would drop to $301, and you would repay all of your credit cards in 56 months and only have $3,800 9 In practice, repayment rates in Chapter 7 average less than one percent (Sullivan et al. 1989) and Chapter 7 court fees averaged $921 before 2005 to $1,377 after 2005 (GAO 2008). In our data, 5.78 of the control group files for bankruptcy protection in the year following their first MMI counseling session. In comparison, percent of the control group enrolls in a DMP, and percent of the control group completely repay their debts through the program. 8

10 in financing charges. That is a savings of about $17, Finally, the individual would indicate whether or not they would like to enroll in the repayment program. Individuals could also call back at a later date and enroll in the repayment program under the same terms. Again, the framing of the alternative payment options was identical for treated and control borrowers; only the actual DMP terms varied across the two groups. As a result, the internal validity of the experiment is not affected by the details of this procedure. Of course, the effects of the randomized treatment may be mediated through the specific way the DMP terms were presented to borrowers. For example, it is possible that individuals view a reduction in financing charges as being more valuable than the equivalent interest rate reduction. It is also possible that individuals view a given reduction as more or less valuable after being told about their outside options. All of our results should be interpreted with these potential framing issues in mind. Treatment Intensity: Table 1 provides an illustrative example of how the randomized treatments impacted the typical borrowers DMP terms. Each row presents repayment program terms under different treatment conditions for a borrower with the mean level debt ($18,212), monthly payment requirement (2.38 percent of initial debt) and interest rate (8.50 percent). For this representative borrower, the control DMP requires monthly payments of $ for months, resulting in $3,482 in financing fees. The median interest rate reduction, conditional on having at least one debt with a participating bank, of 3.69 percentage points would, all else equal, shorten the repayment period by about four months, a 7.99 percent change, and decrease the financing charges by $1,712, a percent change. The median monthly payment reduction, conditional on having at least one debt with a participating bank, of 0.14 percent of initial debt would, all else equal, reduce the monthly payment about by $26.68, a 6.15 percent change, lengthen the repayment period by four months, again a 7.99 percent change, and increase the financing charges by $289, a 8.30 percent change. Yet, this simple example obscures significant across-borrower variation in treatment intensity. For example, the 75th percentile interest rate reduction decreases the representative borrower s financing charges by $1,521 more than the 25th percentile interest rate reduction. Similarly, the 75th percentile monthly payment reduction increases the repayment period by just over five months more than the 25th percentile monthly payment reduction. This sizable across-borrower variation is driven by two factors. First, seven of the eleven issuers participating in the experiment offered a different bundle of interest rate and monthly payment reductions, with interest rate reductions ranging from 4.0 to 9.9 percentage points and minimum monthly payment reductions ranging from 0.0 to 0.5 percent of the initial debt. The second factor driving across-borrower variation in potential treatment intensity is the amount owed to each of the participating and non-participating issuers, as over 78.2 percent of borrowers in our sample have debts with two or more creditors. See Appendix Table 1 for additional details on the treatment bundles offered by each issuer and Appendix Figure 1 for a graphical illustration of the potential treatment intensities for borrowers in our sample. In Section III.C, we discuss the sources of this across-borrower variation in greater 10 Private communication with MMI. 9

11 detail, and explain how we use this variation in potential treatment intensity to isolate the effects of each treatment. II. Conceptual Framework This section develops a simple economic model to better understand the randomized experiment. The model highlights two broad forms of default risk that may influence borrower behavior: (1) strategic, forward-looking default risk from debt overhang and (2) non-strategic, liquidity-based default risk from potentially binding liquidity constraints. We do not attempt to use the model to specify every possible mechanism that could affect debt repayment; i.e., whether forward-looking default decisions are due to strategic default or moral hazard in repayment effort. We also do not attempt to separate these more subtle types of mechanisms empirically. The conclusions we draw in this section should be interpreted with these modeling choices in mind. 11 The model shows how lower interest rates increase repayment by (1) decreasing individuals incentive to strategically default at the beginning of the experiment through increased solvency, and (2) by decreasing individuals exposure to default risk at the end of the experiment through a shorter repayment period. In contrast, lower minimum payments have an ambiguous impact on repayment rates due to two competing channels: (1) a decrease in non-strategic default and an ambiguous change in strategic default at the beginning of the experiment through increased liquidity, and (2) an increase in exposure to default risk at the end of the experiment through a longer repayment period. A. Model Setup We omit individual subscripts from the model parameters to simplify notation. Individuals are risk neutral and maximize the present discounted value of disposable income at a subjective discount rate β. In each period t, individuals receive earnings y t = µ + ɛ t, where ɛ are i.i.d. shocks drawn from a known mean zero distribution f(ɛ) and µ is assumed to be both known and positive. Debt payments begin at t = 0 and are set at a constant level d for the repayment program of length P, so that d t = d for t P and d t = 0 for t > P. In each time period 0 t P, individuals observe their income draw y t and decide whether to make the required debt payment d or default on the remaining debt payments. If an individual defaults on the remaining payments in period t for any reason, she loses her current income draw y t and receives a constant amount x in period t and all future time periods. To capture the idea of a potentially binding liquidity or credit constraint, we assume that individuals automatically default if net income y t d t falls below threshold v, regardless of the value of future cash flows. 11 A large literature examines the causes and consequences of individual default using quantitative models of the credit market. For example, see Chatterjee et al. (2007) for a general model of consumer default, and Benjamin and Mateos-Planas (2014) for a model that distinguishes between formal and informal consumer default. There is also an emerging literature that estimates the separate impact of different forms of hidden information and hidden action. See Adams, Einav, and Levin (2009) and Karlan and Zinman (2009) for examples of these approaches using observational and experimental data, respectively. 10

12 Let V q (t, y) denote the continuation value of making repayment decision q in period t given income draw y. For periods 0 t < P, the continuation value of default V d (t, y) is equal to the discounted value of receiving x in both the current period and all future periods: V d (t, y) = x 1 β (1) The continuation value of repayment V r (t, y) consists of the contemporaneous value of repayment y d and the option value of being able to either repay or default in future periods: [ { ( V r (t, y) = y d + β max V r t + 1, y ) } (, V d (t, y) df y ) ] + F (v + d) V d (t, y) v +d The contemporaneous value of repayment y d is unaffected by the time period t, while the option value of continuing repayment, and hence the total value of continuing repayment, is weakly increasing in t for t < P. This is because the option value of repayment increases as individuals become closer to the risk-free time periods after the completion of the repayment program. Repayment and default behavior is described by a path of cutoff values φ t, where an individual defaults if y t < φ t. The default cutoff φ t combines the optimal strategic response of liquid individuals to low income draws and the non-strategic response of illiquid individuals based on v that may or may not be optimal. Following the above logic, the strategic default cutoff is weakly decreasing over time, reflecting the decreased incentive to default as individuals remaining loan balances shrink. Appendix A provides additional details on the derivations of the above results. The reduced form treatment effects documented below likely combine a number of these potential channels. In Section V, we provide a more tentative discussion of which of these broad, competing channels are most important empirically. (2) B. Model Predictions Motivated by the experiment, we consider the comparative statics of lower interest rates and lower minimum payments on debt repayment. Interest Rate Prediction: The lower interest rate treatment increases debt repayment through two complimentary effects: (1) a decrease in treated individuals incentive to strategically default while both treatment and control individuals are enrolled in the repayment program, and (2) a decrease in treated individuals exposure to default risk while control individuals are still enrolled in the repayment program and treatment individuals are not. Proof See Appendix A. Recall that the median interest rate reduction decreased the typical treated borrower s financing charges by shortening the repayment period and holding the monthly payment constant. In other words, the interest rate treatment forgave treated borrowers monthly payments at the end of the structured repayment program. As a result, the interest rate treatment will increase debt repayment 11

13 to the extent that borrowers value debt forgiveness three to five years in the future. Conditional on enrolling in the program, it is also possible that the interest rate treatment will increase the probability of finishing repayment by decreasing exposure to any form of default risk at the end of the repayment program. This is because the interest rate treatment makes it impossible for treated borrowers to default when their payments have been forgiven. Formally, let d I and P I denote the monthly debt payment d and repayment period P for the interest rate treatment I, and d C and P C denote the monthly debt payment and repayment period for the control group C. In the context of the model, the interest rate treatment reduced overall financing charges by shortening the repayment period for treated individuals relative to control group individuals, P I < P C, without changing the monthly debt payments d I = d C = d. For 0 t P I, shortening the length of the repayment period brings individuals in any given period P C P I periods closer to finishing the repayment program, increasing the expected value of continuing the repayment program. This increase in the expected value of repayment decreases the strategic, forward-looking default cutoff for liquid individuals during this time period. However, disposable income for 0 t P I remains the same, so there is no difference in the probability that a individual defaults due to the liquidity constraint v during this time period. In other words, there will only be an increase in repayment for 0 t P I if the forward-looking default cutoff is the relevant margin for at least some individuals. For P I < t P C, default rates mechanically drop to zero for treated individuals as they have completed the repayment program. However, control individuals can still default on their debt if either the liquidity-based or forward-looking cutoffs bind over this time period. Lower interest rates can therefore increase debt repayment even if individuals never strategically default (i.e. if individuals only default due to a binding liquidity constraint) if there is sufficient default risk at the end of the repayment program. We refer to this channel as the exposure effect. Monthly Payment Prediction: The lower minimum payment treatment has an ambiguous impact on repayment rates due to three effects: (1) a decrease in treated individuals non-strategic or liquidity-based default while both treatment and control individuals are enrolled in the repayment program, (2) an ambiguous change in treated individuals incentive to strategically default while both treatment and control individuals are enrolled in the repayment program, and (3) an increase in treated individuals exposure to default risk while treated individuals are still enrolled in the repayment program and control individuals are not. Proof See Appendix A. The median repayment period increase in the experiment reduced the typical borrower s minimum payment by lengthening the repayment term. The repayment period treatment therefore decreases liquidity-based defaults at the beginning of the repayment program through the lower required payments, but increases defaults at the end of the repayment program through the increased exposure to all forms of default risk. In addition, the minimum payment treatment also changes the option value of repayment, and hence the incentive to strategically default. The direction of 12

14 this strategic effect is ambiguous as lower payments both increase future flexibility, increasing the option value of repayment, and transfer a portion of the debt burden into the future, decreasing the option value of repayment. Formally, let d M and P M denote the monthly debt payment d and repayment period P for the minimum payment treatment M. This minimum payment treatment lengthens the repayment period from P C to P M > P C, while keeping the total sum of the monthly debt payments the same P C t=0 d t = P M t=0 d t. Lower minimum payments therefore decrease the probability that the nonstrategic cutoff binds for illiquid individuals for 0 t P C, increasing repayment rates over this time period if that liquidity-based default cutoff is the relevant margin for at least some individuals. Second, the model shows that lower minimum payments can also affect the incentive to strategically default by changing the option value of repayment for 0 t P C. However, the direction of the effect is ambiguous as lower payments both reduce per-period repayment costs, increasing the option value of repayment, and increase the number of periods to repay, decreasing the option value of repayment. These two offsetting, indirect effects are not unique to a policy of lower minimum payments; other policies targeting liquidity constraints such as payment deferrals or higher credit limits will exhibit these effects. For this reason, we include both these indirect effects on strategic default and the direct effects on non-strategic default discussed above in what we call the liquidity effect. We assume throughout that this combined liquidity effect is positive, although the basic results of the model do not rely on this assumption. Finally, for P C < t P M, default rates mechanically drop to zero for control individuals, while treated individuals can still default on their debt if either the liquidity-based or strategic cutoffs bind over this time period. This exposure effect allows for the possibility that a longer repayment period will have no effect, or even a negative effect, on repayment rates. III. Data and Empirical Design A. Data Sources and Sample Construction To estimate the impact of the randomized treatments, we match counseling data from MMI to administrative tax and bankruptcy records. This section describes the construction and matching of each dataset. The counseling data provided by MMI include information on all prospective clients eligible for the randomized trial. The data include detailed information on each individual s unsecured debts, assets, liabilities, monthly income, monthly expenses, homeownership status, number of dependents, treatment status, enrollment in a repayment program, and completion of a repayment program. The data also include information on the date of first contact, state of residence, who referred the individual to MMI, the assigned counselor, and an internal risk score that captures the probability of finishing a repayment program. We normalize the risk score to have a mean of zero and standard deviation of one in the control group and top-code all other continuous variables at the 99th percentile. 13

15 We also use the data provided by MMI to calculate potential treatment intensity for each individual in our sample. Recall that there is significant variation in potential interest rate and monthly payment reductions as a result of the participating issuers offering different concessions to treated borrowers. To measure this variation in treatment intensity, we first calculate the interest rate and monthly payment for all individuals as if they had been assigned to the control group and as if they had been assigned to the treatment group. In this step, we use the exact calculation that MMI uses to calculate the actual program characteristics. However, we repeat this calculation under both the control and treatment scenarios. We then calculate the difference between the control interest rate and the treatment interest rate for each individual, and the control monthly payment rate and treatment monthly payment rate for each individual. These interest rate and monthly payment differences are our individual-level measures of potential treatment intensity. Importantly, we observe virtually all of the same information that MMI uses to calculate the terms of the structured repayment program. 12 In what follows, we use these constructed treatment intensities as controls in our main empirical specifications. Information on bankruptcy filings comes from individual-level PACER bankruptcy records. The bankruptcy records are available from 2000 to 2011 for the 81 (out of 94) federal bankruptcy courts that allow full electronic access to their dockets. These data represent approximately 87 percent of all bankruptcy filings during our sample period. 13 We match the credit counseling data to PACER data using name and the last four digits of the social security number. We assume that unmatched individuals did not file for bankruptcy protection during the sample period, and control for state fixed effects in all specifications to account for the fact that we do not observe filings in all states. We also pool Chapter 7 and Chapter 13 filings throughout the analysis. Results are similar if we limit the sample to borrowers living in states with PACER data coverage or only the more common Chapter 7 filings. Information on formal sector labor market outcomes and 401k contributions comes from administrative tax records from the SSA. The SSA data are available from 1978 to 2013 for every individual who has ever acquired a SSN, including those who are institutionalized. Illegal immigrants without a valid SSN are not included in the SSA data. Information on formal sector earnings and employment and annual 401k contributions come from annual W-2s. 14 The earnings and employment variables include all formal sector earnings, but do not include earnings from the informal sector. The 401k variable includes all conventional, pre-tax contributions, but does not include contributions to Roth accounts. Individuals with no W-2 in any particular year are assumed to have had no earnings or 401k contributions in that year. Individuals with zero earnings or zero 401k 12 Specifically, we have information on interest rates and minimum payments for the nineteen largest creditors in the sample, including all eleven of the credit card issuers participating in the experiment. For the 16.7 percent of debt holdings held by smaller creditors, we assume an interest rate of 6.7 percent and a minimum payment of 2.25 percent. These assumptions follow MMI s internal guidelines for calculating expected DMP payments. Results are also robust to a wide range of alternative assumptions. 13 See Gross, Notowidigdo, and Wang (2014) for additional details on the bankruptcy data used in our analysis. 14 The SSA data also include information on mortality and Disability Insurance receipt. Very few individuals in our data die or receive Disability Insurance during our sample period, and estimates on these outcomes are small and not statistically different from zero. 14

16 contributions are included in all regressions throughout the paper. We match the credit counseling data to the tax data using the full social security number. We are able to successfully match 95.3 percent of the counseling data to the SSA data. The probability of being matched to the SSA data is not significantly related to treatment status (see Panel C of Table 2). We make two sample restrictions to the final dataset. First, we drop individuals that are not randomly assigned to counselors because they need specialized services such as bankruptcy counseling or housing assistance. Second, we drop individuals with less than $850 in unsecured debt or more than $100,000 in unsecured debt to minimize the influence of outliers. These cutoffs correspond to the 1st and 99th percentiles of the control group, respectively. The resulting estimation sample consists of 40,496 individuals in the control group and 39,243 individuals in the treatment group. Our sample for the employment and 401k outcomes is further restricted to 76,008 individuals matched to the SSA data. B. Descriptive Statistics and Experiment Validity Table 2 presents descriptive statistics for the treatment and control groups. The average borrower in our sample is just over 40 years old with 2.15 dependents. Thirty-six percent of borrowers are men, 63.5 percent are white, 17.2 percent are black, and 8.9 percent are Hispanic. Forty-one percent are homeowners, 44.1 percent are renters, and the remainder live with either a family member or friend. The typical borrower in our data has just over $18,000 in unsecured debt, with about $9,600 of that debt being held by a credit card issuer participating in the randomized trial. Monthly household incomes average about $2,450, and monthly expenses average about $2,150. Panel B of Table 2 presents baseline outcomes for the year before contacting MMI. Individual earnings in the SSA data are approximately $23,500, slightly lower than the self-reported household earnings reported in the MMI data. These results suggest that either some individuals in our sample are not the sole earner in the household, or that there is upward bias in the self-reported earnings. Eighty-five percent of borrowers in our sample are employed at baseline according to the SSA data. Baseline bankruptcy rates are very low, 0.3 percent, likely because individuals are unlikely to contact a credit counselor if they have already received bankruptcy protection. Finally, baseline 401k contributions are $373 for borrowers in our sample. Panel D of Table 2 presents measures of treatment intensity calculated using the MMI data. Specifically, we calculate the interest rate, minimum payment as a percent of the original balance, and the program length in months for each borrower as if they had been assigned to the control group and as if they had been assigned to the treatment group. As would be expected given the random assignment, the treatment and control groups have similar potential program characteristics. If assigned to the control group, the typical treatment borrower would have had an interest rate of 8.5 percent, a minimum payment of 2.6 percent of the initial balance, and a program length of just over 52.6 months. Similarly, the typical control borrower actually had an interest rate of 8.4 percent, a minimum payment of 2.7 percent of the initial balance, and a program length of about 52.7 months. If assigned to the treatment group, those same control borrowers would have had 15

17 an interest rate of 6.0 percent, a minimum payment of 2.5 percent of the initial balance, and a program length of just 51.9 months, nearly exactly the program characteristics that the treatment group actually had. Column 3 of Table 2 tests for balance. We report the difference between the treatment and control group controlling for state by reference group by date fixed effects the level at which prospective clients were randomly assigned to counselors. Standard errors are clustered at the counselor level. The means of all of the baseline and treatment intensity variables in Panels A-D are similar in the treatment and control groups. Only one of the 24 baseline differences is statistically significant at the ten percent level and the p-value from a F-test of the joint significance of all of the variables listed is 0.807, suggesting that the randomization was successful. Appendix Table 2 presents additional tests for balance. Following our main specification described below, we regress each baseline variable in Panels A-D on the interaction of treatment eligibility and potential treatment intensity. All regressions control for potential treatment intensity and strata fixed effects, and cluster standard errors at the counselor level. Consistent with our results from Table 2, we find no statistically significant relationships between our baseline measures and the interaction of treatment eligibility and potential treatment intensity. Finally, Panel E of Table 2 presents measures of the actual program characteristics offered to borrowers in the treatment and control groups (i.e., the first stage of the experiment). Consistent with the results from Panel D, treated borrowers have interest rates that are 2.6 percentage points lower than control borrowers, minimum payments that are 0.1 percentage points lower, and program lengths that are 0.8 months shorter. Below, we describe how we estimate the effects of these changes. C. Empirical Strategy Overview: We begin our empirical analysis by estimating the impact of treatment eligibility using the following reduced form specification: y it = α 0 + α 1 T reat i + α 2 Rate i + α 3 P ayment i + γx i + ε it (3) where y it is the outcome of interest for individual i in year t, T reat i is an indicator variable equal to one if individual i was assigned to the treatment group, Rate i controls for the percentage point difference between the control and treatment interest rate for individual i, P ayment i controls for the percentage point difference between the control and treatment monthly payment for individual i, and X i is a vector of state by reference group by date fixed effects that account for the stratification used in the randomization of individuals to counselors. We cluster standard errors at the counselor level in all specifications. We also include the individual controls listed in Table 2 when estimating equation (3). Estimates without individual controls are available in Appendix Table 3. Estimates of α 1 measure the impact of being offered a (potentially) more generous structured repayment program. However, three important issues complicate the interpretation of these intentto-treat estimates. First, there is substantial variation in treatment intensity in our data, implying 16

18 that the intent-to-treat estimates are therefore likely to significantly understate the true impact of the debt modifications on borrower behavior. Over 25 percent of borrowers in our sample have no debt with a participating creditor, and are therefore offered an identical repayment program when assigned to the the control and treatment groups. Moreover, only 10.3 percent of borrowers in our sample have all of their debt with participating creditors, meaning that the remaining 89.7 percent of borrowers receive some less intensive treatment than originally intended. Second, treated borrowers are offered a repayment program calculated with some combination of lower interest rates and lower minimum payments. The intent-to-treat estimates from equation (3) measure the net effect of these combined changes, and therefore do not allow us to separately identify the impact of lower interest rates and lower minimum payments the parameters that are most relevant to both economic theory and policy. Finally, credit card issuers participating in the experiment offered different bundles of interest rate and monthly payment reductions, and individual borrowers in our sample owed different amounts to the participating issuers. The interest rate reductions offered by participating creditors ranged from 4.0 to 9.9 percentage points, and the minimum monthly payment reductions offered ranged from 0.0 to 0.5 percent of the initial debt. Moreover, over 78.2 percent of borrowers in our sample have debts with two or more creditors. These two institutional features create nearly 50,000 different bundles of interest rate and monthly payment reductions, or potential experiments. This multitude of potential treatment bundles makes it difficult to isolate specific subgroups that experience the same treatment, such as borrowers with a 9.9 percentage point reduction in interest rates and no change in the minimum payment requirement. Given the interpretation issues with the intent-to-treat estimates, our preferred specification leverages the unique institutional features of our setting to separately identify the effects of being offered lower interest rates and longer repayment periods. Specifically, we isolate the effects of being offered each debt modification by comparing the impact of the randomized experiment across borrowers that differed in their potential treatment intensity, or the difference between the interest rate and minimum payment offers that they would have received if assigned to the treatment group and the interest rate and minimum payment offers that they would have received if assigned to the control group. Recall that we are able to calculate the counterfactual interest rate and minimum payment offers for both the treatment and control groups, making it possible to identify borrowers with the same potential treatment intensities but different actual treatments. Formally, we estimate the impact of being offered lower interest rates and minimum monthly payments using the following reduced form specification: y it = β 0 + β 1 T reat i Rate i + β 2 T reat i P ayment i + β 3 Rate i + β 4 P ayment i + γx i + ε it (4) where we again include the individual controls listed in Table 2 and cluster standard errors at the counselor level to account for serial correlation at that level. We also include all borrowers even those with no debts with creditors participating in the experiment in order to identify all of the strata fixed effects. Results are similar if we restrict our sample to individuals with at least one 17

19 debt with a participating creditor. 15 Estimates of β 1 and β 2 isolate the effect of being offered each treatment by comparing the impact of the randomized experiment across borrowers that differed in their potential treatment intensities. We interpret any treatment effect differences across these borrowers as the causal effect of the different treatment intensities. Our empirical strategy is closely related to earlier work using variation in treatment exposure interacted with state or federal law changes. For example, Card (1992) estimates the impact of minimum wage laws on wages, employment, and education using across-state variation in the fraction of workers earning less than a new federal minimum wage. Similarly, Currie and Gruber (1996) estimate the impact of health insurance eligibility on health care utilization and child health using across-state and across-group variation in the number of children eligible for Medicaid. However, in contrast to these earlier studies, the treatment and control groups in our setting are determined by random assignment. One potential threat to our interpretation of the results is that the observed treatment effect differences may be the result of other, unrelated factors. For example, it is possible that individuals with greater sensitivity to interest rate or monthly payment changes are more likely to borrow from the issuers who offered more generous debt modifications during the randomized experiment. In this scenario, estimates of equation (4) would be biased upwards because we would attribute the larger treatment effect solely to the more generous debt modification, not the greater sensitivity of the individuals who chose that bank. Conversely, our estimates would be biased downwards if these individuals with greater sensitivities are less likely to borrow from the issuers who offered more generous debt modifications. These concerns are particularly salient given the substantial across-borrower dispersion in credit card characteristics documented in prior work (e.g. Stango and Zinman forthcoming). 16 To partially test the validity of our identifying assumption, Appendix Table 6 examines whether our potential treatment intensity variables capture all of the relevant variation in issuer specific treatment effects. Our identifying assumption would be violated if borrowers from a particular issuer systematically experience smaller or larger treatment effects than would be predicted from the potential treatment intensity variable. Appendix Table 6 reports coefficients of indicators for holding debt with each of the eleven credit card issuers participating in the experiment interacted with treatment eligibility. We also control for treatment eligibility interacted with potential treatment 15 Equation (4) implicitly assumes that there are no direct effects of treatment eligibility, and that the impact of lower interest rates and longer repayment periods are linear and additively separable. Consistent with the first assumption, our reduced form results are unchanged when we add an indicator for treatment eligibility, and the coefficient on the indicator for treatment eligibility is small and not statistically different from zero. To partially test the second assumption, Appendix Table 4 presents non-parametric results using bins of treatment intensity that do not rely on these functional form assumptions. The results are broadly consistent with linear and additively separable treatment effects, although large standard errors makes a precise test of these assumptions impossible. 16 Appendix Table 5 describes the correlates of potential treatment intensities. Borrowers with larger potential interest rate changes are less likely to be black, more likely to be homeowners, and have higher baseline earnings. Borrowers with larger potential monthly payment changes are also less likely to be black, are at lower risk of default as measured by MMI s standardized risk score, and have lower baseline earnings. Not surprisingly, borrowers with more debt with issuers participating in the experiment and less debt with issuers not participating in the experiment have larger potential treatment intensities. 18

20 intensity, potential treatment intensity, the individual controls listed in Table 2, strata fixed effects, and non-interacted indicators for holding debt with each of the eleven credit card issuers. None of the credit card issuers have systematically larger or smaller treatment effects once we control for the direct effect of lower interest rates and lower minimum payments, and the p-values from F-tests of the joint significance of the issuer interactions range from to None of the results suggest that our identifying assumption is invalid in our setting. 17 We will also show below that our estimates are remarkably similar across gender, race, and homeownership status, suggesting that our LATEs are similar across observably different borrowers. In results available upon request, we further examine this issue by using the baseline characteristics available from Table 2 to calculate predicted treatment intensity for all borrowers in our sample. We then estimate results interacting our treatment effect with an indicator for having an above or below median predicted treatment intensity. There are modestly larger effects of interest rate changes for borrowers with low predicted treatment intensity, although only the point estimate on starting repayment is statistically significant. There are also smaller effects of monthly payment changes for borrowers with low predicted treatment intensity, but again only the earnings result is statistically significant. None of the estimates suggest that our specification given by equation (4) is invalid or that our LATEs systematically differ across borrowers. Subsample Estimates: We are interested in how the effects of the experiment vary across a number of characteristics, such as gender, race, and homeownership. However, we are likely to find a number of statistically significant estimates purely by chance when performing multiple hypothesis tests. We were also unable to file a pre-analysis plan as the experiment was conducted by MMI and the credit card issuers, not the research team. In our main analysis, we therefore restrict ourselves to the single subgroup analysis suggested by the experimental design: high and low levels of financial distress just prior to contacting MMI. MMI originally requested that the pilot program only be tested on individuals with a higher likelihood of default, and many of the credit card issuers that participated in the experiment subsequently offered more borrower-friendly loan terms to all financially distressed borrowers after the experiment. To test how the effects of the experiment differ across this dimension, we estimate effects separately for borrowers with below and above median debt-to-income ratios. Results are similar if we split borrowers by debt alone or split borrowers using the predicted probability of default A second potential test of our identifying assumption would be to compare the effects of treatment eligibility for borrowers with different creditors but identical treatment intensities (i.e. borrowers with all debts held by one of the three issuers that reduced interest rates by 9.9 percentage points and reduced monthly payments by 0.4 percentage points). Unfortunately, there are too few borrowers meeting these criteria to provide empirically informative tests of our identifying assumption. 18 Unfortunately we do not have the required data to construct the measure of financial distress used by credit card issuers following the experiment. The median unsecured debt-to-annual income ratio in our sample is just over 0.5. Appendix Figure 2 plots debt repayment outcomes by debt-to-income ratio. Debt repayment through the repayment program is increasing in debt-to-income ratio until approximately 0.75, perhaps because relatively more indebted borrowers have more to gain from the repayment program over this range. Debt repayment then decreases monotonically after a debt-to-income ratio of approximately

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