D18 | Macro Paper Warehouse

Automated credit limit increases and consumer welfare

Mon, 01 Jan 0001 00:00:00 +0000

Layer 1 — Overview

Research Question. Should regulators restrict banks from proactively raising credit card limits using machine-learning algorithms, and if so, how? The paper asks: to what extent are bank-initiated credit limit increases directed toward revolving borrowers (those who carry interest-accruing balances month-to-month), and what are the welfare consequences of policies that constrain such increases?

Data. The empirical analysis uses the Federal Reserve’s Capital Assessments and Stress Testing (Y-14M) regulatory data, January 2014 to December 2024, covering monthly account-level records for all credit cards issued by large stress-tested banks (assets > $100B). The 26 banks in the sample collectively represent more than 70% of U.S. credit card balances. A 0.5% sample yields more than 150 million observations across more than 3.6 million unique active credit cards. A key advantage of Y-14 over credit bureau data is that it identifies whether each limit change was bank-initiated or consumer-initiated — a distinction not available in other datasets.

Stylized Facts. Credit limit increases are an important and understudied source of consumer credit. During the post-pandemic period, limit increases generate more than $40 billion of additional available credit per quarter, roughly 60% of the approximately $70 billion coming from new card originations; prior to the pandemic the figure was about $30 billion, or roughly half of new issuance. The number of accounts undergoing a limit increase each quarter is on average 30% higher than the number of new cards issued. Consistent with “low-and-grow” lending strategies, limit increases are disproportionately important for lower credit-score borrowers: average subprime credit limits rise from $700 at origination to $2,700 by five years after origination (a 285% increase) and to nearly $5,000 by eight years, while average superprime limits rise only from approximately $12,000 to $15,000 (a 25% increase). About 30% of total revolving balances are made possible by limit increases, with the share reaching 60% for subprime borrowers but only 12% for superprime borrowers. Approximately 75–80% of all limit increases — both by dollar amount and by number of cards — are bank-initiated rather than consumer-initiated. Banks that more frequently reference “artificial intelligence” or “machine learning” in their 10-K filings support a larger share of revolving balances through limit increases. Bank-initiated increases are roughly 1.5–2 times more prevalent among accounts that have revolved in the prior three months, whereas consumer-initiated increases show essentially no differential by revolving status.

Empirical Analysis. Using a linear probability model with card-portfolio-group fixed effects, month fixed effects, and controls for credit score, income, prior limit changes, and other account characteristics, the authors show that the probability of a bank-initiated limit increase follows an inverse-U shape in revolving utilization: accounts with revolving utilization in the moderate range (roughly 0.2–0.7) are most likely to receive an increase, while those near zero or near 1.0 are not. An account with revolving utilization in the (0.2, 0.3] bin is approximately as likely to receive a limit increase as an account whose credit score just rose by 66 points. Transacting utilization, by contrast, follows a logistic growth pattern: the probability rises monotonically until about a utilization of 0.3 and is flat above that. An event study shows that after a bank-initiated limit increase, revolving utilization rebounds to its pre-increase level within approximately 8 months; on average, revolving balances increase by about 40% of the limit increase, with approximately 30% of the limit increase going toward revolving balances. This rebound occurs even for accounts with revolving utilization below the pre-increase mean of 0.28, indicating that the effect is not confined to liquidity-constrained borrowers.

Model. The authors develop a life-cycle consumption–saving model with credit card borrowing, uninsurable income and employment risk, potential default (Chapter 7 style), and heterogeneous preferences following Nakajima (2017) and Gul–Pesendorfer (2001, 2004). Two household types coexist: 60% with standard exponential-discounting preferences (calibrated β = 0.92) and 40% with temptation preferences (calibrated β = 0.96, temptation parameter λ = 0.28 from Kovacs et al., 2021). The credit limit increase function is calibrated using Y-14M data via a latent-variable formulation, replicating the empirical inverted-U relationship between revolving utilization and limit increase probability. The four internally calibrated targets are: share of households with revolving credit card debt (data: 45%, model: 41.8%); utilization rate conditional on debt (data: 35%, model: 28.9%); default probability (data: 0.94%, model: 0.94%); debt-to-income ratio (data: 8.6%, model: 6.8%).

Main Findings — Baseline. Through the model, tempted agents are disproportionately likely to receive credit limit increases because they are more likely to revolve. For customers with utilization above 50%, the majority of credit limit increases are detrimental from the borrower’s own perspective. Standard agents almost always benefit from higher credit limits.

Counterfactual 1 — UK-style (prohibit limit increases for revolving borrowers). This policy reduces the annual probability of limit increases from roughly 5.5% to approximately 1.0%. The default probability falls from about 0.9% to near zero. The debt-to-income ratio declines by roughly 2 percentage points. Aggregate welfare improves by 1.12% in consumption equivalent variation (CEV) when the social planner internalizes the psychological cost of temptation (0.98% without). Standard households incur a modest welfare loss of 0.21% from reduced consumption-smoothing flexibility, while tempted households gain approximately 3.12% in CEV.

Counterfactual 2 — Canada/EU-style (require consumer consent). This policy reduces the annual limit-increase probability from 5.5% to approximately 1.9%. Aggregate welfare improves by 1.16% in CEV (1.04% without psychological costs). Standard households lose 0.19%, while tempted households gain approximately 3.19%. Under the baseline assumption of sophisticated tempted households, results are nearly identical to the UK-style policy. However, when the fraction of naïve tempted households is large, the consent-based policy becomes ineffective (naïve consumers accept limit increases they will regret), whereas the UK-style revolving-borrower ban remains welfare-improving regardless of the naïve share.

Robustness. When the firm is allowed to re-optimize its credit limit increase policy, it endogenously reallocates more limit increases toward standard consumers. Welfare gains remain positive but are attenuated: the UK-style policy yields 0.21% CEV (vs. 1.12% in the baseline calibration) and the consent-based policy yields 0.27% CEV.

Policy Implications. The U.S. lacks regulation of bank-initiated proactive credit limit increases (existing rules under ECOA and ability-to-pay provisions are largely non-binding for this purpose). The authors conclude that banks’ revealed preference for targeting revolvers constitutes an implicit targeting of consumers with self-control issues, and that if a meaningful share of households have self-control issues, there are strong consumer protection grounds for regulating algorithmic credit limit increases.

In depth

Q1. Why do the authors use Y-14M data rather than credit bureau data, and what does this data uniquely enable?

A: The Y-14M dataset allows the authors to distinguish between bank-initiated and consumer-initiated credit limit changes — a distinction not observable in credit bureau data. It also contains actual payment information enabling identification of revolvers (those carrying interest-accruing balances) rather than just total balances. The sample covers more than 70% of U.S. credit card balances and more than 150 million monthly observations over the January 2014 to December 2024 period.

Q2. How large are credit limit increases relative to new card originations in the U.S. credit card market?

A: During the post-pandemic period, limit increases produce more than $40 billion of additional available credit per quarter, roughly 60% of the approximately $70 billion created by new card originations. Prior to the pandemic the figure was approximately $30 billion, or about half of new issuance. On a count basis, the number of cards undergoing a limit increase each quarter is on average 30% higher than the number of new cards issued.

Q3. What is the “low-and-grow” strategy, and how large is the subsequent credit expansion?

A: The low-and-grow strategy involves originating higher-risk borrowers at low initial credit limits and then expanding limits based on observed borrowing behavior. For the average subprime credit card, the initial limit of $700 grows to $2,700 by five years after origination (a 285% increase) and to nearly $5,000 by eight years. For superprime borrowers, the initial limit of approximately $12,000 grows only to $15,000 (a 25% increase) by five years and then is approximately unchanged.

Q4. How does a borrower’s revolving status affect the probability of receiving a bank-initiated limit increase?

A: Bank-initiated increases are approximately 1.5–2 times more prevalent among accounts that have revolved at least once in the prior three months, compared to non-revolving accounts. By contrast, consumer-initiated increases show essentially no differential between revolvers and non-revolvers. This reveals a bank-side revealed preference for targeting revolvers.

Q5. What is the shape of the relationship between revolving utilization and the probability of a bank-initiated limit increase, and how large is its economic magnitude?

A: The relationship follows an inverted-U shape. Accounts with revolving utilization in bins between approximately 0.2 and 0.7 have the highest probability of receiving an increase; accounts near zero or near full utilization are as unlikely to receive an increase as zero-utilization accounts. The effect of being in the (0.2, 0.3] revolving utilization bin has approximately the same positive effect on the probability of receiving a limit increase as a 66-point increase in credit score, making it economically large relative to standard risk signals.

Q6. How does transacting utilization relate to bank-initiated limit increases, and how does this differ from revolving utilization?

A: Transacting utilization follows a logistic growth pattern rather than an inverted-U. The probability of receiving a limit increase rises monotonically with transacting utilization until about a utilization of 0.3, above which the probability does not vary with utilization. This contrasts with revolving utilization, where very high utilization (above 0.9) is actually no more predictive than zero utilization.

Q7. What does the event study show about borrowing behavior following credit limit increases?

A: After a bank-initiated limit increase, revolving utilization (as a share of the credit limit) drops mechanically but then rebounds to pre-increase levels within approximately 8 months. On average, revolving balances increase by about 40% of the amount of the limit increase, with approximately 30% of each dollar of new credit limit going toward revolving balances. These magnitudes are somewhat larger than the 13% (Gross and Souleles, 2002) and 18% (Aydin, 2022) found in prior work, which the authors attribute to the non-causal nature of their event study, higher average utilization in their sample, and their focus on revolving rather than total utilization.

Q8. Is the post-increase borrowing rebound driven by liquidity-constrained borrowers?

A: No. The authors show that limiting the sample to accounts with revolving utilization below the pre-increase mean of 0.28 — accounts that are unlikely to be liquidity constrained — yields very similar results. This finding is consistent with the presence of self-control issues rather than binding credit constraints.

A: The model features two types: 60% with standard exponential-discounting preferences (estimated discount factor β = 0.92) and 40% with temptation preferences (β = 0.96, temptation parameter λ = 0.28 set from Kovacs et al., 2021). The 40% tempted share is internally estimated via the Method of Simulated Moments targeting four aggregate moments: share with revolving credit card debt (45% in data, 41.8% in model), utilization rate conditional on debt (35% vs. 28.9%), default probability (0.94% vs. 0.94%), and debt-to-income ratio (8.6% vs. 6.8%).

Q10. How do tempted and standard households differ in their credit card usage within the model?

A: In the model, 76% of tempted agents carry revolving credit card debt, with an average utilization rate of 73.6%, a debt-to-income ratio of 15.4%, and a default probability of 2.22%. Standard agents carry debt only 18.9% of the time, with average utilization of 4.1%, a debt-to-income ratio of 1.1%, and a default probability of 0.08%. Tempted agents also pay a substantially higher share of income on credit card interest.

Q11. How does the model capture the mechanism by which credit limit increases harm tempted households?

A: The Gul–Pesendorfer temptation utility function makes household welfare depend on both actual consumption and the most tempting consumption alternative available (the budget-set maximum). When credit limits rise, the most tempting alternative ˜c_t increases, which raises the utility cost of self-restraint even for households that do not succumb to temptation. This mechanism is distinct from hyperbolic discounting: temptation imposes a psychic cost even on those who ultimately choose not to over-borrow.

Q12. What are the quantitative welfare effects of the UK-style policy prohibiting limit increases for revolving borrowers?

A: The policy yields an overall welfare gain of 1.12% in consumption equivalent variation (CEV) when the social planner internalizes the psychological cost of temptation (0.98% without). Standard households suffer a modest welfare loss of 0.21% from reduced consumption-smoothing flexibility. Tempted households gain approximately 3.12% in CEV, because the benefit from reduced temptation and lower interest expenditure outweighs the cost of reduced credit access.

A: The consent-based policy yields an overall welfare gain of 1.16% in CEV (1.04% without psychological costs). Standard households lose 0.19%, and tempted households gain approximately 3.19%. Under the baseline assumption of fully sophisticated tempted households, results are nearly identical to the UK-style ban.

A: The UK-style ban on limit increases for revolving borrowers remains welfare-improving regardless of whether tempted households are sophisticated or naïve — the welfare impact is approximately flat as the naïve fraction rises from zero to one. The consent-based policy, by contrast, exhibits a negative linear relationship between the naïve fraction and welfare impact, with welfare gains disappearing as the naïve fraction approaches one. Naïve consumers accept limit increases they would regret, so the policy’s effectiveness depends on households accurately recognizing their own self-control issues.

Q15. What happens when the firm is allowed to re-optimize its credit limit increase policy in response to regulation?

A: With firm re-optimization, both counterfactual policies continue to improve welfare but the magnitudes are attenuated. The UK-style policy yields 0.21% CEV overall (tempted: 0.89%) and the consent-based policy yields 0.27% overall (tempted: 0.98%), compared to 1.12% and 1.16% without re-optimization. The re-optimizing firm reallocates more limit increases toward standard consumers, which reduces the number directed at tempted households but also limits the welfare gains from regulation.

Q16. What do lenders’ 10-K filings reveal about the role of AI/ML in targeting revolvers for limit increases?

A: Banks that mention “artificial intelligence” or “machine learning” above the median number of times in their 2024 10-K filings support a higher share of revolving balances through credit limit increases, for all credit score groups. This difference is not driven by differences in credit limits at origination between higher-AI and lower-AI lenders, suggesting that AI/ML adoption affects the targeting of limit increases toward revolvers rather than the initial credit allocation.

Key Concepts

Revolving utilization. In this paper, revolving utilization is defined as the portion of overall credit card utilization attributable to balances that the borrower carries from one month to the next without full repayment, thereby accruing interest. It is measured as revolving balances divided by credit limit, averaged over the prior three months. This is distinct from transacting utilization (new purchases as a share of limit) and is the primary signal banks use — implicitly, via their algorithms — to select accounts for proactive limit increases.

Bank-initiated vs. consumer-initiated credit limit increase. A bank-initiated limit increase is one in which the lender proactively raises a borrower’s credit limit without a request from the borrower. A consumer-initiated increase is one explicitly requested by the borrower. The Y-14M data uniquely identify the source of each change. The paper documents that approximately 75–80% of all limit increases are bank-initiated, and that bank-initiated increases are strongly correlated with revolving utilization whereas consumer-initiated increases are not.

Low-and-grow strategy. The practice of originating higher-risk borrowers at low initial credit limits and then expanding those limits over time based on observed borrowing behavior. In the paper this is a documented empirical pattern, not an assumption: subprime accounts start at an average $700 limit at origination and reach nearly $5,000 by eight years, a 285% increase versus only 25% for superprime accounts over the same horizon.

Temptation preferences (Gul–Pesendorfer). A utility framework in which household welfare depends not only on actual consumption but also on the most tempting consumption alternative within the budget set. The disutility from temptation arises even when the household does not succumb — it reflects the psychological cost of self-restraint. In the paper, λ (set to 0.28) parameterizes the weight of this temptation cost relative to standard utility. Temptation preferences are time-consistent, which facilitates welfare analysis, and are preferred to hyperbolic discounting in this setting because they predict that individuals may pay to have tempting options removed even without acting on them.

Revealed preference for targeting revolvers. The paper’s characterization of banks’ credit limit increase behavior as reflecting a systematic preference for giving increases to revolving borrowers, inferred from the empirical pattern in the Y-14M data (the inverted-U shape between revolving utilization and limit increase probability). Because banks’ algorithms are proprietary and unobserved, the paper interprets the observed allocation of limit increases as a revealed preference, consistent with banks’ profit motive since revolvers generate the majority of credit card interest income.

Consumption equivalent variation (CEV). The welfare metric used throughout the paper’s counterfactual analysis. CEV is defined as the percentage change in consumption in every period and state that would make households indifferent between the baseline policy regime and the counterfactual policy. A positive CEV indicates that the counterfactual policy improves welfare; a negative CEV indicates harm. The paper considers two versions: one in which the social planner internalizes the psychological cost of temptation (consistent with tempted households’ actual preferences), and one in which the planner ignores that cost (λ = 0 for the planner) but households still face temptation.

Persistent revolving debt (UK regulatory definition). In the UK Financial Conduct Authority’s framework, a borrower is considered in “persistent revolving debt” when the cumulative amount paid toward interest and fees exceeds the cumulative amount of principal repaid over a 12-month period. The UK rule prohibits lenders from increasing credit limits for borrowers meeting this definition. The paper models a stylized version: any account currently carrying a revolving balance is ineligible for a bank-initiated limit increase in the UK-style counterfactual.

Contract Terms, Employment Shocks, and Default in Credit Cards

Mon, 01 Jan 0001 00:00:00 +0000

Layer 1 — Overview

Research Question

This paper asks two related questions bearing on financial inclusion policy in developing countries: (1) How effective are credit card contract term changes — specifically interest rate reductions and minimum payment increases — in limiting default among new borrowers? (2) How large is the effect of formal-sector job loss on default relative to these contract term interventions, and can the difference in magnitudes be explained by differential cash flow impacts?

Setting and Data

The study is set in Mexico during 2007–2009 and exploits a large nationwide stratified randomized controlled trial implemented by a major commercial bank (“Bank A”) on its financial-inclusion credit card — a product that accounted for approximately 15% of all first-time formal-sector loans in Mexico as of 2010. The study card was targeted at borrowers with limited or no formal credit history (the bank’s “C, C- and D” customer segments); 47% of the experimental sample held it as their first formal loan product. A sample of 144,000 pre-existing cardholders was stratified into nine cells based on bank tenure (6–11 months, 12–23 months, 24+ months) and past repayment behavior, then randomly allocated to eight treatment arms combining two minimum payment levels (5% or 10% of the outstanding balance) and four annual interest rates (15%, 25%, 35%, 45%), for 26 months (March 2007 to May 2009). The study sample is representative of the bank’s national portfolio of approximately 1.3 million study card customers. Card-level data run through December 2014 — five years after the experiment ended — allowing examination of both short- and long-run effects. The experimental sample is matched to Mexico’s Social Security database (IMSS), providing monthly formal employment histories from January 2004 to December 2012 for 59% of the sample; and to credit bureau data, allowing observation of defaults across all formal financial institutions.

Main Findings with Quantitative Magnitudes

Result 1 — Interest rate effects are modest in aggregate. A 30 percentage point (pp) decrease in the annual interest rate (from 45% to 15%, a 67% reduction relative to the baseline rate) decreased cumulative default by 2.5 pp over the 26-month experiment, for a default elasticity of +0.20. Over the same 18-month horizon used for unemployment comparisons, the implied effect is 1.03 pp. These magnitudes are substantially smaller than predictions elicited from Mexican central bank regulators (mean predicted decrease: 8.6 pp) and from participants on the Social Science Prediction Platform (mean predicted decrease: 5 pp). Default continued to decline in the lower-rate arm for approximately three years after the experiment ended, reaching −1 pp by March 2012, after which effects became statistically indistinguishable from zero.

Result 2 — No effect on the newest borrowers. For the newest borrowers (those with 6–11 months of tenure when the experiment began — the group with a 36% cumulative default rate over 26 months versus 18% for those with 24+ months of tenure), the interest rate reduction has no effect on default over the 26-month period, with point estimates consistently small and statistically indistinguishable from zero. This is in contrast to older borrowers, who are meaningfully responsive.

Result 3 — Minimum payment increases increase short-run default but reduce long-run default. Doubling the minimum payment from 5% to 10% of outstanding balance increased cumulative default by 0.8 pp by the end of the experiment (26-month elasticity: +0.04; p = 0.016), driven primarily by defaults occurring within the first year. The short-run increase is concentrated among the most liquidity-constrained borrowers — those with the highest baseline debt utilization and those in the minimum-payer stratum (baseline debt utilization rate of 85%). After the experiment ended and all arms were returned to the same 4% minimum payment, the previously higher-minimum-payment arm exhibited persistently lower default, reaching a 1 pp decline by the end of the sample (p = 0.054 at end of study period), relative to a base default rate of 41% at that point.

Result 4 — Job displacement effects are seven times larger than contract term effects. Formal-sector job displacement (identified using mass layoff events at firms with 50+ employees, defined as year-on-year employment contractions exceeding 30% of prior-year average employment) increased cumulative default by 4.8 pp after 12 months and 7.6 pp after 18 months. This is seven times larger than the effect of a 30 pp interest rate decrease (1.03 pp over 18 months) and nine times larger than the effect of doubling minimum payments (0.8 pp). Formal job loss alone can explain approximately 14% of total study card default during the experiment (calculation: 19.8% of formally employed study card borrowers lose their job at least once in the first 18 months; multiplied by the 7.6 pp default increase per spell, this yields 1.5 pp of the 10.8% base default rate at 18 months). Results are corroborated using a nationally representative matched credit bureau–IMSS sample of 600,339 borrowers, which yields 8,723 mass layoff events and similar estimates.

Per-peso normalization. A back-of-the-envelope calculation normalizes all three shocks by their respective cash flow impacts. The interest rate decrease reduces cumulative required minimum payments due by 2,917 MXN pesos over 18 months; the minimum payment doubling increases them by 1,325 MXN pesos; formal job loss reduces total labor earnings by an estimated 21,328 MXN pesos (adjusting formal-sector earnings losses of 77,555 MXN pesos downward by 72.5% to reflect that 82% of workers who lose formal employment transition to informal employment in the following quarter, with total earnings falling only 27.5%). The per-peso default effects are: 0.36 pp per 1,000 MXN pesos for the interest rate intervention; 0.51 pp for the minimum payment intervention; and 0.36 pp for job displacement. The null hypothesis that all three per-peso effects are equal cannot be rejected (p = 0.78).

Interpretation

The authors present a simple two-period optimizing model emphasizing the role of previously accumulated debt and liquidity constraints. The model generates four testable predictions consistent with the data: (1) lower interest rates decrease default via reduced debt burden; (2) higher minimum payments increase short-run default by tightening liquidity constraints; (3) “surprise” minimum payment increases (where borrowers anticipated they would continue) reduce post-experiment default via debt reduction; (4) negative income shocks (modeled as first-order stochastic dominance deterioration in period-2 income) increase default. The per-peso normalization supports the interpretation that cash flow impacts — not differential per-peso susceptibility to shocks — drive the relative magnitudes of the three effects.

In depth

Q1. Why is the interest rate elasticity of default (0.20) so much lower than prior estimates in the literature?

A: The paper contrasts its 26-month elasticity of +0.20 with estimates from Karlan and Zinman (2019) (1.8) and Adams et al. (2009) (2.2), and notes it falls in the same range as Karlan and Zinman (2009) (0.27) and DeFusco et al. (2021) (0.01). The paper proposes that variation in borrower tenure may partly explain cross-study differences, as default elasticities appear to be increasing in bank tenure. The newest borrowers — the most policy-relevant subgroup — show zero elasticity, pulling the overall estimate down. The paper also argues that in this context, interest-rate-driven moral hazard (all channels: debt burden, concurrent, and dynamic) is collectively small.

Q2. What mechanism explains why newer borrowers are entirely unresponsive to interest rate changes?

A: The paper hypothesizes that newer borrowers place a higher continuation value on the card (captured by parameter v in the model) because they have fewer formal credit alternatives; at baseline, only 64% of the 6–11 month stratum held a card with another bank versus 78% of the 24+ month stratum. A higher continuation value implies more muted responses to interest rate changes (formally derived in Appendix E.3). Newer borrowers also respond more strongly to credit limit increases, consistent with tighter liquidity constraints. A regression controlling for age, gender, baseline card ownership, debt utilization, labor force attachment, and earnings cannot explain away the differential treatment effect between new and old borrowers (differential remains significant at p = 0.05), suggesting the tenure gradient in responsiveness is not simply a composition effect.

Q3. Why does increasing minimum payments raise short-run default but reduce long-run default?

A: In the short run, the doubling of minimum payments tightens liquidity constraints for already-constrained borrowers. The increase in default is concentrated among borrowers in the highest baseline debt-utilization tercile and among minimum-payers (baseline debt utilization of 85%), and is preceded by a sharp rise in delinquencies in months 3–5 (which trigger 350 MXN peso fees per occurrence, further worsening the repayment burden). In the long run, borrowers who anticipated continuing higher minimum payments (the experiment ended without advance notice, so borrowers expected the new terms to persist) chose lower debt levels during the experiment. Since all arms were returned to the same low minimum payment when the experiment ended, the lower-debt borrowers in the higher-minimum-payment arm were better positioned to weather subsequent shocks, producing the 1 pp post-experiment decline in default. The hypothesis that this is driven by habit formation in payment behavior is ruled out by the absence of any effect of past higher minimum payments on post-experimental payment levels.

Q4. How is the mass-layoff identification strategy designed and validated?

A: The paper uses the universe of IMSS formal employment records to define a mass layoff at a firm (50+ employees) as the first month in which year-on-year employment declines by more than 30% of average employment in the prior 12 months. An individual is “displaced” if they lost their job in the same quarter as their employer’s mass layoff event. The identification assumption is that, conditional on individual and time fixed effects, the exact timing of the mass layoff is uncorrelated with workers’ potential default outcomes. This is supported by: (1) mass layoffs occurring in every period, making coincidence with credit market shocks unlikely; (2) time fixed effects absorbing common trends; and (3) the absence of statistically distinguishable pre-trends in default between displaced and non-displaced workers. The paper implements both standard two-way fixed effects and the staggered DiD estimator of de Chaisemartin and D’Haultfoeuille (2024), which remains valid under heterogeneous and dynamic effects, and the results are similar across methods.

Q5. How does the paper account for informal employment when estimating the cash flow impact of job loss?

A: Formal-sector earnings losses over 18 months post-displacement are estimated at 77,555 MXN pesos using IMSS wage data in an event-study design paralleling the default equation. However, since more than 4/5 of workers who lose formal employment are informally employed in the following quarter (based on Mexico’s ENOE labor force survey panel), and total labor earnings fall by only an estimated 27.5% over the three post-displacement quarters, the paper scales the formal earnings loss down to 21,328 MXN pesos (≈ 0.275 × 77,555). This brings the estimated earnings loss closer to prior developed-country estimates of displacement costs and is treated as a lower bound relative to the raw formal-earnings loss figure.

Q6. Does the cost of default deter borrowers from defaulting, and what is the cost?

A: The paper argues that defaulters face substantial consequences. Using an instrumental variables strategy (treatment assignment as instrument for default on the study card), the probability of having a new loan one year after default is estimated to be 65 pp lower relative to the non-default counterfactual (p = 0.03). A selection-on-observables approach also shows that study card default is associated with the complete absence of any subsequent credit card for at least four years. These costs should provide strong incentives to remain current, making the high observed default rates primarily attributable to cash flow shocks rather than strategic default. The value of formal credit is further confirmed by the finding that a 100 MXN peso increase in the study card’s credit limit translates into 32 MXN pesos of additional debt (instrumental variable estimates are more than twice as large as OLS), and by the comparison of informal loan terms (annual rates averaging 291%, loan amounts of 3,658 MXN pesos, durations of 0.52 years) with formal loan terms (94 pp lower rates, 9,842 MXN peso average amounts, 1.07 year durations).

Q7. Are the default treatment effects different across the interest rate and minimum payment interventions, or do they interact?

A: The paper tests for and cannot reject separability between the two interventions at standard significance levels. At the end of the experiment (May 2009), the p-value for the null that the minimum payment effect is constant across interest rate arms is 0.44; five years later it is 0.65. The null that the interest rate effect is constant across both minimum payment arms yields p = 0.08 at end of experiment and p = 0.411 five years later. The fully saturated specification yields results indistinguishable from the parsimonious linear-separable specification.

Q8. Are there spillover effects from the contract term changes onto other loans held by study participants?

A: No spillover effects on default on other loans are found, either during the experiment or after it ended, based on credit bureau data covering all formal-sector loans held by the experimental sample. There is also no evidence of crowd-out or crowd-in from other lenders in terms of new loans or loan closures. The only minor exception is a small decrease in default (3%, or approximately 2 pp out of a 61 pp base) on other Bank A loans in the high minimum payment arm.

Q9. Why does the effect of unemployment on default exceed the model’s predictions from cash flow alone?

A: The paper’s back-of-the-envelope normalization finds that the per-peso effects of all three shocks on default are statistically indistinguishable (p = 0.78 for the null that all three λ estimates are equal), with point estimates of λ_IR = 0.36, λ_MP = 0.51, and λ_U = 0.36 pp per 1,000 MXN pesos. This implies that job loss does not have a larger per-peso effect on default than contract term changes; the larger absolute effect of displacement arises entirely from its larger cash flow impact. Additional consequences of job loss beyond cash flow (health, mental health) do not appear to generate additional default beyond what can be attributed to income loss.

Q10. How do the experimental results compare to what experts predicted?

A: Expert predictions were systematically too large. Mexican central bank regulators predicted a mean decrease of 8.6 pp from a 30 pp interest rate reduction at the 18-month horizon, versus the actual estimated effect of 1.03 pp. Social Science Prediction Platform respondents predicted a mean decrease of 5 pp. For minimum payments, regulators on average predicted a 0.4 pp decrease in default from doubling the minimum payment, whereas the actual effect was a 0.8 pp increase. Three-quarters of SSPP respondents correctly predicted the sign of the minimum payment effect (an increase in default), but the predicted mean increase was 6.4 pp, far larger than the estimated 0.8 pp.

Q11. Do the job displacement results generalize beyond the experimental sample?

A: Yes. The paper repeats the displacement event study on the intersection of the nationally representative credit bureau sample (approximately 600,339 individuals with both credit information and employment histories) with the universe of IMSS data for October 2011–March 2014, yielding 8,723 mass layoff events. This sample is representative of the population of Mexican borrowers with formal employment histories, and the estimated effects on default for any loan in the credit bureau are similar in magnitude to the experimental-sample results, providing a measure of external validity.

Q12. What do the debt dynamics during the experiment reveal about the mechanisms for interest rate effects on default?

A: The data show that purchases (net of payments) increase in response to interest rate decreases, consistent with downward-sloping demand for credit; yet total debt declines in lower-rate arms. This is consistent with the model’s prediction that the mechanical compounding effect (lower rate applied to previously accumulated debt) exceeds the behavioral new-purchase response. Confirmed empirically: the debt elasticity to the interest rate is estimated to be positive, with preferred estimates in the range [+0.18, +0.54]. The decline in default is further concentrated among borrowers with the highest baseline debt utilization rates, those for whom the debt compounding effect is strongest — consistent with the debt channel as the primary mechanism.

Key Concepts

Cumulative Default Measure: Default is defined as three consecutive monthly payments each below the required minimum payment due, at which point Bank A automatically revokes the card. The outcome variable is coded as Yit = 1 if borrower i has defaulted in any month s ≤ t and 0 otherwise, making it a cumulative (absorbing) measure. This allows estimation on an unchanging sample, avoiding attrition biases that would arise from conditioning on not having defaulted in the prior period.

Minimum Payment Due (mpd): The paper uses the required minimum payment due to avoid delinquency as its central cash-flow normalization variable. This is a comprehensive measure that incorporates not only the contractually specified fraction of outstanding balance but also interest charges, fees, and endogenous borrower responses (changes in debt and purchases). It serves as the common denominator for benchmarking the cash flow impacts of the two contract term interventions and formal job loss against one another.

Free Cash Flow / Per-Peso Normalization (λ): The paper defines per-peso default effects (λ^IR, λ^MP, λ^U) by dividing each intervention’s average treatment effect on cumulative default (in percentage points) by the cumulative change in the minimum payment due (or equivalent cash flow impact) induced by that intervention over 18 months. The resulting ratio is expressed as percentage points of default per 1,000 MXN pesos of cash flow change. This normalization is explicitly not treated as an instrumental variable estimate; it is a descriptive back-of-the-envelope calculation intended to equate the scale of the three shocks.

Mass Layoff / Displacement: A mass layoff at the firm level is defined as the first month in which year-on-year firm employment declines by more than 30% of average employment in the prior 12 months, restricted to firms with 50+ employees. An individual worker is classified as displaced if they lost formal-sector employment in the same calendar quarter as their employer’s mass layoff event. This definition follows Jacobson et al. (1993) and subsequent literature and is used to isolate plausibly involuntary (exogenous) separations from voluntary quits or individually driven terminations.

Continuation Value (v): In the paper’s two-period optimizing model, v is the reduced-form utility parameter capturing future flow of card benefits, warm glow from card ownership, or the option value of retaining access to formal credit, experienced only if the card is not in default. The paper uses v to rationalize the zero interest-rate response of newer borrowers: ceteris paribus, higher v implies that borrowers will remain current on the card even when interest rates are high, because they value continued access. Higher v thus implies more muted responses to interest rate changes.

Bank Tenure Strata: Borrowers are stratified into three groups based on length of relationship with the study card: “new customers” (6–11 months), medium-term (12–23 months), and long-term (24+ months). Tenure is used both as a stratification variable for the experiment and as a primary dimension of heterogeneity in treatment effects, reflecting differing default rates (36% vs. 18% at 26 months), labor market vulnerability (1.34× higher job loss probability for new vs. long-term), and interest rate responsiveness (zero for new, significantly positive for long-term borrowers).

Debt Burden Channel vs. Concurrent Moral Hazard: The paper distinguishes three channels through which interest rate changes can affect default: (a) the debt burden channel — higher rates mechanically increase the stock of interest-accruing debt, making repayment harder; (b) concurrent moral hazard — higher current interest rates alter the incentive to default on existing obligations, holding debt constant; and (c) dynamic moral hazard — higher future interest rates reduce the benefit of remaining current. The paper’s finding of a modest total effect (elasticity 0.20) implies that the sum of all three channels is small in this context, with the debt burden channel being the primary driver of what effect does exist.

D18 | Macro Paper Warehouse

Automated credit limit increases and consumer welfare

Layer 1 — Overview

In depth

Q1. Why do the authors use Y-14M data rather than credit bureau data, and what does this data uniquely enable?

Q2. How large are credit limit increases relative to new card originations in the U.S. credit card market?

Q3. What is the “low-and-grow” strategy, and how large is the subsequent credit expansion?

Q4. How does a borrower’s revolving status affect the probability of receiving a bank-initiated limit increase?

Q5. What is the shape of the relationship between revolving utilization and the probability of a bank-initiated limit increase, and how large is its economic magnitude?

Q6. How does transacting utilization relate to bank-initiated limit increases, and how does this differ from revolving utilization?

Q7. What does the event study show about borrowing behavior following credit limit increases?

Q8. Is the post-increase borrowing rebound driven by liquidity-constrained borrowers?

Q9. What are the key modeling assumptions about household types, and how were the share parameters calibrated?

Q10. How do tempted and standard households differ in their credit card usage within the model?

Q11. How does the model capture the mechanism by which credit limit increases harm tempted households?

Q12. What are the quantitative welfare effects of the UK-style policy prohibiting limit increases for revolving borrowers?

Q13. What are the quantitative welfare effects of the Canada/EU-style consent-required policy?

Q14. How sensitive are the two policy counterfactuals to the share of naïve (unaware of their self-control issues) tempted households?

Q15. What happens when the firm is allowed to re-optimize its credit limit increase policy in response to regulation?

Q16. What do lenders’ 10-K filings reveal about the role of AI/ML in targeting revolvers for limit increases?

Key Concepts

Contract Terms, Employment Shocks, and Default in Credit Cards

Layer 1 — Overview

In depth

Q1. Why is the interest rate elasticity of default (0.20) so much lower than prior estimates in the literature?

Q2. What mechanism explains why newer borrowers are entirely unresponsive to interest rate changes?

Q3. Why does increasing minimum payments raise short-run default but reduce long-run default?

Q4. How is the mass-layoff identification strategy designed and validated?

Q5. How does the paper account for informal employment when estimating the cash flow impact of job loss?

Q6. Does the cost of default deter borrowers from defaulting, and what is the cost?

Q7. Are the default treatment effects different across the interest rate and minimum payment interventions, or do they interact?

Q8. Are there spillover effects from the contract term changes onto other loans held by study participants?

Q9. Why does the effect of unemployment on default exceed the model’s predictions from cash flow alone?

Q10. How do the experimental results compare to what experts predicted?

Q11. Do the job displacement results generalize beyond the experimental sample?

Q12. What do the debt dynamics during the experiment reveal about the mechanisms for interest rate effects on default?

Key Concepts