In the Red: Di Maggio, Ma & Williams (2025)

What this is. The paper’s core results, the identification strategy (class-action lawsuits banning high-to-low transaction reordering as a natural experiment), and the estimating specifications with exact table locators: enough to know what was found and how, without reading all 48 pages. To replicate or extend, read the full source at the original.

TL;DR

Banks’ practice of reordering transactions from high to low (HTLR) maximizes overdraft fees earned from low-income depositors. The paper exploits 37 class-action lawsuits that forced some banks to cease HTLR, comparing treated zip codes (with banned banks) to nearby control zip codes (also with sued banks but not banned) in a difference-in-differences design. After HTLR bans, low-income consumers reduce payday borrowing by $85 per borrower per quarter (11%), reduce installment borrowing by $358 per borrower per quarter (8%), improve credit scores, gain access to cheaper mainstream credit, and increase essential consumption. But HTLR bans also cause banks to close branches, especially in low-income areas, highlighting a tension between fee limits and financial access.

Core results

Magnitudes as reported; \*\*, \*\*\* = 5%, 1% significance. Standard errors clustered at the neighborhood level (consumer specs) or bank and zip-code level (branch specs). All consumer specifications use zip code x quarter observations in below-median income zip codes.

#	Result	Locator	Magnitude
R1	HTLR bans reduce payday loan borrowing per borrower	Table V col. (3), p. 1711	DiD coeff. = -$84.84*** (se 31.47); 11% reduction relative to mean
R2	HTLR bans reduce installment loan borrowing per low-income borrower	Table VI col. (3), p. 1714	DiD coeff. = -$358.3*** (se 135.8); 8% reduction relative to mean
R3	Alternative-credit declines persist for at least 3 years	Table VIII, p. 1717	Payday: -$84.84 (yr 1), -$72.02 (yr 2), -$50.47** (yr 3); Installment: -$358.3, -$293.2**, -$276.5**
R4	Consumers are more likely to experience a 50+ point credit score increase	Table IX Panel B col. (1), p. 1719	0.0288 pp*** (se 0.0111) at 1 year; 0.0315 pp*** at 3 years
R5	Credit card balances and limits rise, indicating improved access to mainstream credit	Table IX Panel A col. (1-2), p. 1719	Credit card balance: +$33.96** (yr 1); credit card limit: +$40.10** (yr 1) per low-income borrower
R6	Consumers increase essential consumption (durable and nondurable essential goods)	Table X col. (1)-(4), p. 1721	Durable spending: +$45.18** per household; nondurable essential: +$15.57**; nonessential nondurable: insignificant
R7	HTLR-banned banks are significantly more likely to close branches, concentrated in low-income areas	Table XI col. (1) and (5), p. 1724	Branch exit probability: +0.90 pp*** overall; interaction with Low-Income dummy: +0.33 pp** additional

Overall (paper’s conclusion). Aggressive overdraft pricing via HTLR creates demand for alternative credit, trapping low-income consumers in a cycle of high-cost borrowing. Ceasing HTLR reduces payday and installment borrowing, improves consumer credit health, and unlocks access to cheaper mainstream credit. However, HTLR bans also prompt banks to exit low-income neighborhoods, an unintended spillover that may offset some consumer gains and raise new concerns about financial access.

Theory / model

The paper has no formal model. It develops two competing hypotheses for the relationship between overdraft pricing and demand for alternative credit, and tests them empirically.

Hypothesis 1 (complements / debt-trap): Consumers improperly estimate overdraft costs (as in Bertrand and Morse (2011)) and turn to payday lenders to repay unaffordable overdraft balances and fees. Morgan, Strain, and Seblani (2012) and Melzer and Morgan (2015) document that overdraft providers and payday lenders compete and that consumers use both as substitutes; the paper’s findings challenge that view, showing they are better described as complements. A reduction in overdraft costs reduces payday demand.

Hypothesis 2 (substitutes / price-reduction supply shift): Overdraft credit and payday loans are substitutes for short-term liquidity. If HTLR bans reduce the supply of overdraft services (banks become less willing to provide the service at lower fee revenue), excess demand for short-term credit shifts to payday lenders. In this case, payday borrowing rises after HTLR bans.

Related literature: Melzer (2011) and Skiba and Tobacman (2019) provide evidence on the real costs of payday loan access. Dlugosz, Melzer, and Morgan (2021) study overdraft fee ceilings and the unbanked. Gabaix and Laibson (2006) formalize how shrouded attributes enable add-on pricing to persist in competitive markets, motivating why HTLR pricing is not competed away.

Identification logic. The key source of variation is the lawsuit outcome: within the same geographic neighborhood, some zip codes contain branches of banks required to cease HTLR, and neighboring zip codes contain branches of banks that were sued but not required to stop. The two groups operate in similar local economic conditions and share similar consumer demand dynamics. Within-neighborhood-quarter fixed effects additionally absorb any time-varying shocks (such as local unemployment changes) correlated with both HTLR bans and credit demand. The paper argues that lawsuit outcomes are quasi-exogenous because they depend on contract-level arbitration clauses and litigation strategy, not on bank or consumer characteristics, and tests this with a battery of balance checks (Table III Panel B, Internet Appendix Tables IV-V, pp. 1706, 1728-1729).

Method

The primary estimator is a zip-code-by-quarter-level difference-in-differences regression. The treatment group is zip codes containing branches of banks required to cease HTLR; the control group is zip codes within seven miles of a treated zip code that contain branches of sued banks not required to cease HTLR. This design restricts variation to local areas subject to similar lawsuit contexts.

The paper builds on the difference-in-differences and panel-regression primitives. The key structural feature is that the control group is not the general population of zip codes but rather nearby zip codes sharing the same lawsuit environment, selected to match on local consumer demand dynamics.

For colocation motivating evidence (Table IV, p. 1707), a conditional logit regression is estimated at the bank branch by year level:

$$\Pr(\text{AltFin within } d)_{bz} = F\left(\gamma \cdot \text{HTLR}_{b} + \eta_z\right) \tag{4-IV}$$

where $\text{HTLR}_b$ is an indicator for whether branch $b$ belongs to an HTLR bank, $\eta_z$ are zip code fixed effects, and $F(\cdot)$ is the logistic CDF. This within-zip-code test avoids comparing geographic areas with different demographic compositions.

For bank-level first-stage evidence (Table A.I, p. 1735), the estimating equation is a bank by quarter DiD:

$$\Delta \text{BankOutcome}_{bt} = \beta \cdot \text{HTLRBan}_b \cdot \text{Post}_t + \eta_b + \eta_t + \varepsilon_{bt} \tag{FS}$$

where bank and quarter fixed effects are included and standard errors are clustered at bank and quarter levels. This confirms HTLR bans reduced overdraft-related revenue by 6.44% (Table A.I col. 1, p. 1735).

Empirical specifications

All consumer-outcome specifications are estimated at the zip-code by quarter level, restricted to zip codes with below-median income.

Main DiD for payday and installment borrowing (R1, R2; equations 1 and 2 from the paper, p. 1712 and p. 1718):

$$\text{PaydayBorrowing}_{zt} = \beta \cdot \text{HTLRBan}_z \cdot \text{Post}_t + \eta_{nt} + \varepsilon_{zt} \tag{1}$$ $$\text{FinancialHealth}_{zt} = \beta \cdot \text{HTLRBan}_z \cdot \text{Post}_t + \eta_{nt} + \varepsilon_{zt} \tag{2}$$

where $\text{PaydayBorrowing}_{zt}$ is average dollars of payday loans disbursed per payday borrower in zip code $z$ in quarter $t$; $\text{HTLRBan}_z$ is a dummy for whether the zip code contains branches of a bank required to cease HTLR; $\text{Post}_t$ is a dummy for quarters after the HTLR ban; and $\eta_{nt}$ are neighborhood-by-quarter fixed effects (the most conservative specification, where neighborhood = all zip codes within seven miles). Standard errors are clustered at the neighborhood level. The window is two quarters before and four quarters after the HTLR ban.

The coefficient of interest $\beta$ measures the differential effect of the ban on consumer alternative borrowing in treated relative to control zip codes within the same neighborhood. Tables V (Clarity payday) and VI (Equifax installment) present six columns each, varying between neighborhood FE, quarter FE, and neighborhood-by-quarter FE.

Long-term horizon test (R3; Table VIII, p. 1717): The same DiD specification but extending the post window to one, two, or three years. The results show that the decline in both payday and installment borrowing persists without reverting to pre-ban levels, ruling out a temporary substitution explanation.

Credit health and consumption (R4, R5, R6; Tables IX and X, pp. 1719, 1721): The same zip-code-by-quarter DiD structure (equation 2) applied to credit card balances, credit card limits, probability of a 50+ point credit-score increase, total balance in good standing, and household expenditure (durable, essential nondurable, nonessential nondurable) from Earnest transaction data. Credit card variables come from Equifax; consumption variables are from Earnest Research’s transaction-level data for 6 million U.S. households. Consumption tests use an 8-quarter post window and 4-quarter pre window.

Branch exit spillovers (R7; Table XI, equation 4 from the paper, p. 1723):

$$\text{Exit}_{izt} = \beta \cdot \text{HTLRBan}_i \cdot \text{Post}_t + \eta_{zt} + \varepsilon_{izt} \tag{4}$$

where $\text{Exit}_{izt}$ is a dummy for bank $i$ exiting zip code $z$ in year $t$; the specification includes zip-code-by-year and bank-by-zip-code fixed effects; $\text{Post}_t$ covers up to three years after the HTLR ban. The interaction $\text{HTLRBan}_i \cdot \text{Post}_t \cdot \text{LowIncome}_{zt}$ shows that exits are concentrated in below-median income zip codes. Standard errors are clustered at the bank and zip-code level.

Datasets used

Dataset	Role in paper	Wiki page
Clarity Services (alternative credit bureau)	Primary outcome: payday and alternative installment loans disbursed 2013-2019; random sample of 171,445 alternative borrowers	No page yet
Equifax (traditional credit bureau)	Installment loan borrowing, credit card balances and limits, credit scores, total balances in good standing; representative 10% sample of 680,856 borrowers, 2005-2018	No page yet
Pew Charitable Trusts bank study (2012-2015)	HTLR practice indicator for the largest 50 US banks; four annual waves	No page yet
FDIC Summary of Deposits	Bank branch locations and deposit-level data for 50 largest banks	FDIC Summary of Deposits
FR Y-9C call report data (FFIEC 031/041)	Bank-level overdraft revenue, all-other-loans balances, and income statement items	No page yet
Earnest Research expenditure data	Household consumption: credit/debit card transaction-level data for 6 million US households; durable, essential nondurable, and nonessential nondurable spending	No page yet
Infogroup Historical Business Database	Payday lender and check-casher locations (SIC codes 609903 and 614113), 1997-2018	No page yet
Hand-collected lawsuit data set	37 class-action lawsuits against HTLR banks: event dates, settlement terms, behavior relief (HTLR ban or not), cash settlement amounts	No page yet
American Community Survey (Census)	Zip-code-level demographics: age, race, income, poverty, housing, employment, 2011-2018	No page yet
HMDA and SBA lending data	Bank branch exit spillovers to mortgage and small business lending (Table XII)	HMDA (no page yet)

Sample: Clarity data 2012-2019; Equifax data 2005-2018; bank lawsuit events concentrated 2008-2015. Analysis at the zip-code by quarter level; 6,975 zip-code-quarter observations for Clarity (main spec), 30,487 for Equifax.

When to read the full paper

Read the original if you are: studying the link between bank overdraft practices and the alternative lending market; estimating causal effects of fee policies on consumer financial health; interested in spillover effects of banking regulation (branch closures, financial deserts); or evaluating the “banked vs. underbanked” distinction as a policy target. The Appendix (Tables A.I-A.III, pp. 1735-1736) contains the first-stage bank-level DiD results. The Internet Appendix contains the full lawsuit data set (Table I), balance tests (Tables IV-V), and additional robustness tables (Tables VI-XIV).

Attribution and rights

Source: peer-reviewed, The Journal of Finance 80(3), June 2025. This distillation was extracted by an LLM on 2026-06-06 and is not human-verified or independently reproduced. The paper is paywalled; extract-only redistribution applies.

Di Maggio, Marco, Angela Ma, and Emily Williams. “In the Red: Overdrafts, Payday Lending, and the Underbanked.” The Journal of Finance 80, no. 3 (June 2025): 1691-1738. DOI: 10.1111/jofi.13447. © 2025 the American Finance Association.