A Small Lever

Abstract

In the Federal Reserve's 2025 Survey of Consumer Finances, the median Black family held $36,800 in net worth and the median White family $332,100, nine times as much. We ask how much decision tools that banks run at the moment money moves could narrow that gap. We grade the published evidence on overdraft alerts, gambling blocks, commitment, goal setting and automatic enrollment, and project effects with the household-wealth microsimulation of our earlier paper, Years and Dollars, started from the 2025 survey. Suppose the ten largest banks and the minority depository institutions deployed fee alerts and a gambling block together with a default saving program from 2027. Then the Black-to-White ratio of median wealth in 2050, 0.110 under current conditions, would be about 0.13 percentage points higher at central values, or $570 for the median Black household. Drawing every parameter over its range, nine runs in ten fall between −0.03 and +0.48 points; that band is a spread across simulated draws, not a confidence interval. About 88% of the effect comes from the saving program, a bank product; the alerts and the block add about 0.015 points, within sampling error of zero. Real-time alerts have the strongest causal evidence; no controlled study tests a bank gambling block. Our decision engine, measured on test sets we built, rarely errs but misses most sweepstakes casinos. Bank-side decision tools are a small lever; the larger levers lie outside the account. The authors own the company that sells the product modeled here.

1. Introduction

Black households in the United States hold far less wealth than White households. In the Federal Reserve's 2025 Survey of Consumer Finances (SCF), released on October 9, 2026, median net worth was $332,100 for White non-Hispanic families and $36,800 for Black non-Hispanic families, both in 2025 dollars [90]. The ratio of the two medians is 0.11, and the Federal Reserve calls the White-to-Black ratio of nine the largest since 2016 [90]. Measured per person, White Americans held about six times as much wealth as Black Americans in 2020, and the gap has widened since the 1980s as capital gains went mostly to White households [87]. The levers that could close the gap sit outside any single firm: earnings, mobility, returns, survival and transfers. Our earlier paper, Years and Dollars, found in a microsimulation of household wealth that no single lever closes the gap, that only combinations do, and that earnings is the largest [2]. Structural models reach the same ordering [88, 89]. A bank-side decision tool moves none of these levers. A bank does see money move, and at that moment it can warn before a fee, block a gambling transaction, or prompt and automate saving. How much could that be worth?

This paper answers that question with a projection. We grade the published evidence on interventions a bank could make at the account (Section 3). We estimate from public deposit and institution data how many Black households an adopting bank could reach, and feed the evidence into the Years and Dollars microsimulation, started from the households of the 2025 survey (Sections 4 and 5). The effect is small. If the ten largest banks and the minority depository institutions deployed fee alerts and a gambling block together with a default saving program from 2027, the model's 2050 Black-to-White ratio of median wealth would be about 0.13 percentage points higher than under current conditions, against a baseline of 0.110. Drawing every parameter of this paper over its range, the 5th to 95th percentiles of runs are −0.03 and +0.48 points. In the model's attribution, about 88% of the effect comes from the saving program, which is a product a bank runs, not a decision the tools make; the fee alerts and the gambling block together add about 0.015 points, within sampling error of zero. No bank has deployed the tools, so every effect here is a projection from studies in other settings, not a measured outcome; Appendix E sets out the pilot that would measure it.

Three contributions follow.

1. We grade the evidence on decision-time interventions at the account, correct four magnitudes that the published versions of the cited studies revised, and re-derive the saving-program parameter from steady-state flow evidence rather than balance stocks (Section 3; Appendix F).
2. We project the effect on the wealth gap with a model started from the 2025 survey, report a parameter Monte Carlo as the headline uncertainty, attribute the effect to levers with Shapley values, and rank what would move it with elasticities rather than one-at-a-time ranges (Sections 4 and 5).
3. We measure our own decision engine on test sets we built and publish its failures, and we date the product and regulatory facts the projection rests on (Appendices A to D).

Relative to Years and Dollars [2], which modeled a single consumer product with planning values, this paper models levers a bank could pull, ties each to a named study, and asks which institutions could reach Black households. Relative to Derenoncourt et al. [87] and Aliprantis et al. [88], which ask what closes the gap, it asks a narrower question, what a firm can do at the account, and finds the answer is little. Relative to the overdraft-economics literature [4, 83, 84, 85], it puts the alert evidence on the scale of household wealth rather than fees.

The scope is bounded in three ways. The model is a projection under assumptions drawn from other populations, products and countries; the Understanding API, the product that motivates the question, is in early access and has no bank or credit union deployments. The racial effect in the model rests on differences in incidence, not dollars, because no source gives fee or gambling dollars by race. And the model starts from a survey whose Black median fell 25% from 2022 in real terms, a change within the survey's sampling error; Section 2.1 reports the change with its standard error and Section 5.8 shows what the choice of starting survey does to the result.

Terms. The ratio is the Black-to-White ratio of median household wealth, a decimal; a change of 0.01 is one percentage point (pp). Active means a reached household that has taken up a lever and not dropped out. The saving program is a default saving product (goals, commitment or automatic transfers) that a bank would run; the decisions are the fee alerts and the gambling block. Dollars are real 2024 dollars unless stated. Core is the headline set of three levers; full adds the untested stress lever.

2. Background

2.1 The racial wealth gap in the 2025 survey

The 2025 SCF puts median family net worth at $332,100 for White non-Hispanic families and $36,800 for Black non-Hispanic families, and mean net worth at $1,694,700 and $242,400, in 2025 dollars [90]. In the 2022 survey the medians were $311,900 and $49,100 in the same dollars ($285,000 and $44,900 in 2022 dollars [1]). The White median rose 6% and the Black median fell 25%; the Black mean rose 5% [90]. The Federal Reserve's published standard errors are $12,240 on the 2022 Black median and $7,540 on the 2025 one [104], so the change of −$12,370 has a standard error of about $14,380 and cannot be distinguished from zero at conventional levels. The ratio of medians moved from 0.157 to 0.111. Black median family income fell 2% to $49,400 while White median income rose 7% to $95,300 [90]. The Bulletin attributes the fall in the median to the balance sheet of the typical Black family, in which real median values of vehicles, retirement accounts and bank balances each fell by about a quarter [90]; the Federal Reserve had already warned that the 2022 Black median was imprecisely estimated [103].

The projection model draws its households from the 2025 survey. Its starting ratio of medians is 0.110 in 2024 dollars, and the model's household counts are the survey's: 18.7 million Black and 82.0 million White households [91]. Household counts elsewhere in this paper come from the FDIC's 2023 survey, which weights to 17.25 million Black and 86.0 million White households, where each is the householder's single race and not Hispanic or Latino, the same groups as the model's [7].

Years and Dollars shows that under current conditions the gap does not close, and that no single change closes it [2]. This paper asks about a different set of levers: the small, repeated cash-flow leaks that a bank can see and sometimes stop.

2.2 Cash-flow leakage

By leakage we mean money that leaves a household's budget without buying something the household would, on reflection, have chosen. We cannot observe reflection. We observe fees, gambling deposits, returns and cancellations, and treat them as proxies. We take four channels, ordered by how much is known about how they differ by race.

Overdraft and nonsufficient-funds fees. The evidence on race is about incidence, and three surveys agree on direction.

• The Consumer Financial Protection Bureau (CFPB) reports that 37.4% of Black consumers lived in a household charged an overdraft or nonsufficient-funds fee in the past year, against 22.1% of White non-Hispanic consumers. In the frequent group (both fee types, or four or more of one type, in the year) the shares are 26.5% and 14.4%; the sample is consumers with a credit record [3].
• The Financial Health Network finds that 31% of Black, 24% of Latinx and 14% of White households with a checking account were charged an overdraft fee in 2023 [8].
• A Federal Reserve Bank of Boston study of 2021 payment diaries finds that 17.3% of Black and 10.0% of White consumers paid an overdraft fee [9].

Why the rates differ is less clear. In the Boston Fed regressions the Black–White difference in paying an overdraft fee is not statistically significant once income and balances are controlled; lower income stays a significant predictor, and Black consumers remain about 7 points more likely to pay some bank-account fee at equal income and balances [9]. We therefore present the raw gap as a burden and claim no race effect net of income.

The CFPB finds Black consumers 84% more likely to be in the frequent group [3]. The Financial Health Network finds no evidence that overdrafting households of color overdraft more often than overdrafting White households [8]. Both can hold, because more Black households overdraft at all. Fees are also concentrated: in an older large-bank sample, 8% of customers paid nearly 75% of overdraft and nonsufficient-funds fees [10], and in a later one 9% of accounts paid 79% [11].

In dollars, overdraft and nonsufficient-funds revenue was $11.8 billion in 2023 and $12.1 billion in 2024 on the Financial Health Network's revised series, which adds credit unions; its earlier series put 2023 at $7.9 billion [8, 12]. Overdraft and nonsufficient-funds revenue at banks over $1 billion in assets fell by nearly half from 2020 to 2023 on the CFPB's call-report series reproduced by the Congressional Research Service [13]. Large banks' fee eliminations of 2017 to 2022 relieved wealthier, liquid households more than financially vulnerable ones [83], and entry-level checking costs more in Black neighborhoods [97]. No source we found gives fee dollars by race.

Gambling. After online sports betting became legal, net brokerage investment in treated areas fell about 14% relative to control, and a dollar bet reduced net investment by just under a dollar. Bettors with below-median savings put 0.85% of quarterly income into betting, against 0.49% for those above the median, and constrained households raised card balances by about $368 relative to unconstrained ones, in the subsample with card data [5, draft read]. Legal betting also lowered credit scores, by about 0.7 points on average and about 12 points where online betting was added to retail betting, with more bankruptcies, collections and delinquencies [14]. A study of county spillovers finds a median credit score about one point lower and delinquency 0.3 points higher overall, which implies a rise of roughly 10 points among the bettors legalization induced [86]. In the records of one UK bank, Lloyds Banking Group, gambling as a share of spending is associated with financial distress and, at 30% of spending, with five-year mortality about a third higher (a factor of 1.37); a 10-point rise in the gambling share is associated with 51.5% higher payday-loan uptake. Those associations are descriptive [15].

On race, Pew finds that 27% of Black adults bet on sports in the year to July 2022, against 18% of White adults [16]. In two national telephone surveys, problem gambling was highest among Black and Hispanic respondents and fell with socioeconomic status [17]. Neither causal study observes race [5, 14]. No source we found gives gambling spend by race in dollars.

Stress, sleep and late-night spending. Years and Dollars concludes that device signals are plausible but unvalidated indicators of regretted spending [2]. Section 3.5 adds one study. We found nothing on how this channel differs by race.

Forgotten subscriptions and missed returns. The evidence is thin. In card-network data for ten subscription services, months in which a card is replaced show much higher cancellation, which implies that inertia roughly doubles seller revenue on average, with a range of 14% to more than 200% across the services under the authors' inattention model [18]. An online panel survey of 1,000 consumers in four generation quotas found that people guessed they spent $86 a month on subscriptions and itemized $219; its methods are sparse [19]. We found no study of how much households lose by missing return windows, and nothing by race. We include this channel in the model only as a labeled illustration.

2.3 What is known by race

Table 1. What is known about each channel, by race.

The case for a racial effect rests on incidence, not dollars. Black households are more likely to be charged fees and more likely to bet. We do not know whether they lose more per household, or how much of the difference in incidence would remain at equal income. The projection in Sections 4 and 5 inherits that limit.

3. Evidence on decision-time interventions

This section reviews what published studies show about interventions a bank could make at the account. We grade each study. A is a published randomized trial, a quasi-experiment with credible identification, or an official series read from the issuing agency. A− is such a paper read in working-paper form. B is a working paper, an abstract-only read of a non-randomized study, or a descriptive survey by a credible body. C is a press release, trade press, vendor data or a survey with unknown method. Every effect in this section was measured on something other than the Understanding API. Four magnitudes in version 1 of this paper came from superseded drafts; Section 3.3 and Section 3.4 give the published figures, and Appendix F converts each saving study to the model's unit.

3.1 Alerts and attention: overdraft

In randomized automatic-enrollment experiments at two large UK banks in 2017 and 2018, covering 1.1 million customers, just-in-time text alerts reduced unarranged-overdraft and unpaid-item charges by 17–19% and arranged-overdraft charges by 4–8%. That was worth £170–240 million a year across the market. Extra early-warning alerts had no statistically significant added effect, though the authors do not rule out economically significant ones. More than half of overdrafts could have been avoided using the customer's own savings or card liquidity, and the alerts captured less than half of that potential [4]. This is the strongest evidence in the paper.

The 2018 regulator version of the same work reported larger effects, 21–24% for unpaid-item alerts and 25% for unarranged-overdraft alerts, from automatic enrollment at two banks within a six-bank dataset of 1.5 million consumers [23]. We use the published numbers as central and the regulator's as a high end. The regulator version also shows who benefits: rare overdrafters could avoid up to half of their charges, while heavy users still paid most of theirs. Only 3–8% of customers had registered for alerts voluntarily before automatic enrollment, so opt-in reaches few people [23]. UK alerts came with a mandate: the Competition and Markets Authority's 2017 order required large banks to enroll customers in unarranged-overdraft and unpaid-item alerts by February 2018 [23]. US banks face none (Appendix C).

A US quasi-experiment from 2006 to 2008 points the same way. Among 7,448 checking-account holders in an online panel that is more educated and higher-income than the population, answering a survey about overdraft fees lowered the chance of paying a fee that month by 3.7 percentage points on a base of 30%. The effect was concentrated among lower-education, lower-literacy and lower-income panelists, ran through fewer debit and automatic transactions, and persisted for up to two years as a stock of attention [24].

Studies also warn of side effects. Card-payment reminders in Brazil cut late fees 14% but raised checking overdraft fees 9%, and users with an overdraft history paid 5% more in total fees [25]. Marketing messages in Turkey that mentioned overdraft availability without a price raised overdraft use [26]. In Iceland, an app that made balances easy to see was followed by a 38.4% fall in nonsufficient-funds fees after 24 months, with small rises in overdraft interest and late fees; that study was not randomized, and we read a summary, not the article [27, 102]. A decision that nudges one payment must see the balance it draws on.

The fee lever also depends on the bank's own fee schedule. A bank that has dropped overdraft fees has nothing to save, and Bank On certified accounts carry no overdraft or nonsufficient-funds fees under the Bank On National Account Standards [96]; more than 14 million such accounts were open at the end of 2024 [28]. Two findings cut the other way for the households the lever is meant to help. When fee ceilings were relaxed, banks raised fees but also expanded account supply, and more low-income households opened accounts [84]. And ending high-to-low transaction reordering reduced low-income customers' payday borrowing, which suggests that an avoided overdraft can be worth more to a liquidity-constrained household than the fee it saves; overdraft credit and payday loans are substitutes [85, 101].

3.2 Gambling, and the limits of evidence on blocks

The evidence that gambling harms households is strong (Section 2.2). The evidence that blocks prevent the harm is weak.

What exists. A University of Bristol study for GambleAware found that eight UK firms offered card blockers covering about 60% of personal current accounts, used by about 0.5 million customers. One firm's block stopped two to three gambling transactions per customer per month. Three of the eight blocks could be switched off instantly, users found workarounds through cash and e-wallets, and the report recommended a lock of at least 48 hours [20, 95]; we read the press release of the report. Trade press reported, quoting Monzo, that about 223,000 customers, about 5%, had enabled its block by July 2020 and that about 8% of those later turned it off [29]. UK cooling-off periods ranged from none to 48 hours, with no outcome data [30]. One transaction-data analysis speaks to selection: among Monzo customers who activated the block, average daily gambling spend tripled in the week before activation [82], so activators are not average bettors.

The closest thing to a payment-channel evaluation is the UK ban on gambling with credit cards. Card payments to gambling merchants fell as expected, with no spike in cash withdrawals or transfers and no visible displacement to unlicensed sites. The bank-data findings are directional; the Commission's consumer tracker adds that 15% of former credit-card gamblers moved to other borrowed money and 76% did not, in an evaluation window that overlapped the 2020–21 lockdowns [21].

What does not exist. We found no controlled evaluation of a bank gambling block or a cooling-off period. The only randomized trial of limits we found, with 4,328 analysed mainland-Finnish customers of an Åland operator who preferred online slots, prompted new customers to set a deposit limit. Limit-setting rose from 6.5% to between 22% and 45%. There was no effect on net loss, deposits or days gambled over 90 days; the Bayes factors favored the null strongly for the whole sample and moderately for the most active tenth. The limit was voluntary, one-off and easy to raise [22]. An observational study of heavy players found lower later spending among casino and lottery players who set limits, with no effect sizes in the abstract [31]. Self-exclusion programs are under-used and do not stop all gambling, though participants report benefits [32]. Prize-linked savings accounts, which substitute for gambling, are the one product that links the gambling and saving channels [100].

In short, blocks stop transactions at the card, users say they help, workarounds exist and soft limits do little. No study tests a hard block with a cooling-off period against a control. Any reduction we assume in Section 4 is a judgment.

3.3 Commitment, goals and reminders

Commitment devices also have a strong causal record, though not in this setting. In a Philippine trial, 710 of 1,777 clients of a rural bank were offered a savings account with withdrawal restrictions, and 28.4% of those offered took it up. After twelve months, average savings balances at the bank were 81% higher than their pre-intervention level in the offered group relative to the control group, an intent-to-treat effect of 411 pesos [33]. That is a stock effect on a bank balance, not a saving rate.

Goal setting in an app has a small causal effect and a larger descriptive one. In an Italian app with 47,643 users, goal setting raised saving in the app by €17–20 a month in intent-to-treat terms (€203–240 a year), estimated from 122 randomly chosen beta testers with 50 days of early access. Only 28.4% of them set goals, so the local effect for goal setters is about €60 a month. Among survey respondents, the median user's saving in the app was 1% of net income without goals and 2.4% with them; that difference is descriptive, from a self-selected subsample of 814 with a 16.3% response rate. Saving in the app did not displace saving outside it [34, working paper read].

Reminders work weakly. In three trials with banks in Bolivia, Peru and the Philippines, monthly reminders raised the amount saved at the partner bank by about 6% (p ≈ 0.07–0.08), and reminders that named the client's goal by more, in the 2010 working paper we read; we could not open the published text [35].

In a pre-registered experiment with 3.1 million customers of a Mexican bank, seven weeks of SMS nudges raised checking balances by 0.6% and cut spending by 0.8% across the sample; in the quartile predicted most responsive, balances rose 4.9% with card debt unchanged [36]. Peer-spending information moved users of a US app toward their peers' spending; we read only the abstract and use no magnitude [37]. We found no controlled study of cooling-off periods on spending.

3.4 Automatic enrollment, as a flow

Automatic enrollment raises retirement saving, and the published evidence on debt is reassuring. Among US Army civilian hires automatically enrolled at 3% of pay, cumulative contributions after four years were 4.1% of annual salary higher, about one point of pay a year, with no significant change in credit scores or in debt excluding auto loans and first mortgages (point estimate −0.6% of salary) [38]. In a randomized rollout to about 160,000 small UK employers, each month of automatic enrollment added £33–39 of pension saving and £7 of unsecured debt; the pension figure includes employer contributions and tax relief, which a bank saving program would not add [39]. A classic employer program, Save More Tomorrow, raised average contribution rates from 3.5% to 13.6% over 40 months, with 78% joining; it was not randomized and covered one firm [40]. Participation effects of automatic enrollment, which are larger, are not the right measure for wealth [41].

Two findings decide the parameter. First, once employee turnover, unvested matches, withdrawals at separation and opt-outs are counted, steady-state saving rates rise by 0.6% of income under automatic enrollment and by 0.3% under default auto-escalation, in nine US 401(k) plans; only 40% of employees escalate on their first escalation date [76]. Second, in over 100 US plans and a UK panel, automatic enrollment's effect on participation and contributions at 12 months is attenuated by 36 months; the average long-run increase is modest, though inequality in savings falls [77]. Defaults also work for liquid saving: automatic enrollment into payroll saving at UK employers raised participation by 48 points and balances by £114 at nine months and £193 at 18 months [78], and default enrollment in a salary-linked plan raised participation by 40 points in an Afghan firm [81]. Automatic contributions are largely new saving: 85% of Danish savers are passive, and each dollar of subsidy raises total saving by a cent [79]. Debit cards given to Mexican cash-transfer recipients built a savings stock of 2% of annual income in two years, financed by lower consumption [80].

We anchor the saving program on the flow evidence: 0.6% of income at the center, 0.3% at the low end, and 1.5% as a judgment at the upper envelope of the stock evidence (Appendix F).

3.5 Stress, sleep and spending

No study we found links measured sleep, heart-rate variability or stress to spending in dollars. The nearest result comes from one large Chinese online retailer, where purchases made between midnight and 5:59 a.m. were more likely to be returned and were returned sooner (hazard ratio 1.21) [42]. That measures returns, not spending, in one country. Years and Dollars reviews the experimental literature and concludes that these signals are plausible but unvalidated indicators of regretted spending [2]. None of the interventions in Sections 3.1 to 3.4 was timed by a stress, sleep or heart-rate signal, and none was tested on US Black households as such. A limit that lowers a per-purchase cap overnight rests on the mechanism, not on a measured effect. We label it untested and keep it out of the headline projection.

3.6 Effect sizes at a glance

Table 2. Effect sizes, designs and grades. No row measures the Understanding API. "A−" marks a published paper read in working-paper form.

4. Projection model

4.1 The engine and its starting point

We reuse the microsimulation of Years and Dollars (model version 2.1) [2]. A build script copies its engine unchanged from a snapshot of the committed code and adds this paper's levers. Simulated households start as the non-Hispanic Black and White households of the 2025 SCF, all five implicates, 15,218 records, converted from 2025 to 2024 dollars with the CPI-U (the October 2025 index was not published, so the 2025 average is the mean of eleven months) [91, 92]. Each year a household earns, saves, gives support to relatives, consumes out of wealth, earns the returns of its race-by-age-by-wealth portfolio and faces race-, sex- and age-specific mortality. At the last death its estate passes to children, and a successor household forms at 25. The model runs from 2025 to 2100 in wage-indexed dollars and reports real 2024 dollars.

The behavioral parameters are the ten that Years and Dollars calibrated to the 2022 survey under its one-saving-schedule ("equal") specification, unchanged. Version 2 therefore changes where households start, not how they behave; a refit of the same specification to the 2025 profiles is reported as a sensitivity (Section 5.7), as is the separate-saving-rate specification. Each run draws its own long-run returns, housing-distress gap, causal share of the wealth–mortality gradient, cost of debt and Trustees mortality alternative, as in Years and Dollars. The product lever of Years and Dollars is switched off, and so are its card-interest, housing-distress and return terms, because a bank-side tool does not set prices or choose a household's portfolio and because the fee and gambling channels would otherwise double count part of the card-interest term. This paper adds five explicit levers in their place.

4.2 Reach

A household is reached if its bank deploys the tools. Reach is a fixed trait of the household, drawn from a hash of its identifier, so the same household is reached in every scenario that shares a seed; successor households draw their own reach. The probability of reach is the FDIC banked share of the household's race (Black 89.4%, White 98.1%) [7] times the share of banked households at adopting institutions. Reach starts in 2027 and stays fixed; a linear rollout from 2027 to 2035 is a sensitivity.

Table 3. Reach scenarios. Every share is an assumption, not a measurement. "Black households reached" is the share of all Black households, banked or not.

The county-weighted reach proxy a referee asked for, deposits by county from the FDIC Summary of Deposits weighted by each county's Black household share, has not been computed; it is an open item (Section 6).

4.3 Levers, take-up and persistence

Within a reached household, each lever is a separate state: undecided, active or out. In the first year the household is eligible, it becomes active with the lever's take-up probability, and otherwise it is out; a reached household that is not yet eligible is tested again each year. Eligibility is the rule of Years and Dollars: under the full retirement age of 67, with wealth below the national median for its age band. We keep the rule because fee payers and bettors have thin balances and because it makes the comparison with Years and Dollars like for like, and we report a variant in which every reached household under 67 is eligible (Section 5.7). Each year an active household drops out for good with probability one minus the lever's retention. At the central retention of 90% a household is active for ten years on average, and 8.9% of 2027 adopters remain active in 2050 (0.9 to the power 23); at 80%, 0.6%; at 95%, 31%. The 2050 active stock is therefore mostly households that became eligible recently, and the headline is as much a statement about assumed persistence as about the tools. An active household bears the lever's effect while under 67.

• Fee alerts. The base annual fee times the fee reduction, added to wealth in real 2024 dollars. Active means enrolled and a fee payer, so take-up is enrollment times the race's fee incidence. Enrollment is opt-in at central values; default-on is a design variant (Section 5.7).
• Gambling block. The bettor's deposit share of income, times pass-through to lost saving, times the block's reduction, added to the saving rate. Active means a bettor who has turned the block on.
• Stress-spending limits. A share of income added to the saving rate. Untested; outside the headline.
• The saving program. A share of income, net of debt crowd-out, added to the saving rate. This lever is a default saving product that a bank would run, which decision calls could time or target. It is not one of the decisions the tools make.
• Other (missed returns, subscriptions). A placeholder in dollars, zero at low and central values, run only in a labeled sensitivity.

4.4 Parameters

Table 4. Parameters and sources. Values are derived from the sources cited as set out in the replication notes (research/parameters.md). Where a source does not report the quantity in these units, the value is marked J: a judgment, a midpoint, or a value borrowed from another product, bounded by the nearest evidence. Of the 60 ranged values, 36 are judgments. Low, central and high are the bounds of a sensitivity range ordered by effect size, not confidence intervals. Nothing was tuned to reach a target.

To limit double counting, the card-interest term of Years and Dollars is set to zero, because betting raises card balances [5] and reminders shift fees between products [25]. The fee and gambling levers act on different cash flows. The model includes no positive side effect and no response by banks. Two documented responses cut against the fee lever's transfer to the target population: fee ceilings reduced account supply to the unbanked [84], and large banks' 2017–22 fee eliminations relieved liquid households more than vulnerable ones [83].

4.5 Which levers are in the headline

• Core, the headline: fee alerts, the gambling block and the saving program. Alerts have randomized evidence on their effect, though not in the US or by race. The channel from betting to lower saving is quasi-experimentally identified, but the block's own effect has no controlled study, so its reduction is a judgment with a wide range. The saving program's flow effect is anchored on the steady-state automatic-enrollment literature; it is a bank product.
• Full: core plus stress-spending limits. No study links device-measured sleep or stress to dollars. The stress lever's sources are none; it is an assumption, and it is reported separately wherever it is run.
• Other: no evidence; run once as an illustration.

4.6 Runs and uncertainty

Each scenario uses 200 runs of 5,000 households, about one million simulated households, each scaled to the 2025 household population. The attribution, one-at-a-time and elasticity runs use 120. Every scenario replays the same seeds, which fix the inherited parameter draws and the household sample, so effects are run-by-run differences from the baseline; we report the mean of those differences with its Monte Carlo standard error, the median with a 90% bootstrap band, and the 5th to 95th percentiles across runs. Treat an effect within two standard errors of zero as not distinguishable from zero. Table 5 says what each band contains.

Table 5. Uncertainty types, and which bands contain them.

5. Results

Every number in this section is a projection from published effect sizes in other populations, run through the microsimulation of Years and Dollars from the households of the 2025 survey. None is a measured outcome of the Understanding API.

5.1 The baseline: a transition toward a steady state

Table 6. The baseline under current conditions, with none of this paper's levers. Median of runs; the 5th to 95th percentiles contain the inherited parameter draws and Monte Carlo noise. The model's starting ratio is 0.110 (2025, 2024 dollars); its balanced-growth steady state under current conditions is 0.200.

Under current conditions the ratio rises slightly to 2030, falls to 0.099 in 2040 and recovers to 0.110 in 2050, then climbs toward the model's steady state of 0.200 (0.213 by 2100). The dip is a transition, not a prediction about the 2040s: the 2025 Black cross-section has very low medians in the 25–44 age bands ($9,700 and $11,100 in 2024 dollars, against $67,300 and $198,300 for White households), and the model carries those cohorts forward with behavior calibrated to the 2022 profiles. Those medians are also imprecise; the 2025 Black sample has 698 families. Under the 2022 start of version 1 the 2050 baseline was 0.161. The median Black household holds $40,164 in 2050 in the baseline (median of runs), the median White household $355,251.

5.2 Headline: core levers at central values

Table 7. Change in the Black-to-White ratio of median wealth from the baseline, core levers at central values. Percentage points; mean across paired runs, with the 5th to 95th percentile of run-by-run changes (inherited draws and Monte Carlo noise). The 2100 column is reported for completeness; its standard error (0.04 points for S3) makes it a weak guide.

Table 8. Dollars added to the median Black household, core levers at central values. Real 2024 dollars; mean across paired runs (median of runs in brackets for 2050), with the 5th to 95th percentile for 2050.

In the headline case, S3 at central values, the 2050 ratio is 0.125 percentage points higher than the baseline (mean of paired runs; Monte Carlo standard error 0.009). The median of run-by-run changes is 0.112 points, with a 90% bootstrap band of 0.100 to 0.126, so the effect is distinguishable from zero but small. The median Black household's wealth is $566 higher on average across runs ($551 at the median run), about 1.4% of its projected 2050 wealth. That closes 0.14% of the 2025 gap in ratio terms and 0.20% in median-dollar terms. In 2075 the change is 0.113 points (standard error 0.026) and $731.

Deployment at MDIs and MDI credit unions alone (S2) moves the 2050 ratio by 0.02 points, because those institutions hold few households. The levers are race-neutral: they help any reached household that is eligible, so reached White households gain too, and because the saving levers add a share of income, a reached White household gains more dollars than a reached Black one. In S3 at central values, Black households gain about $14 billion in aggregate by 2050 and White households about $71 billion. The levers narrow the ratio only because Black households are more often eligible, more often pay fees and more often bet in the survey data used. In 2050, 9.9 million Black households are reached; 1.03 million are active in the saving program, 0.13 million in the gambling block and 0.03 million in the alerts.

5.3 The headline band: a parameter Monte Carlo

The corners of Table 4 are not quantiles of anything, so we draw every ranged parameter per run from a triangular distribution over its low–high range with mode at the central value, on the same seeds as the baseline, and read the band off the runs. This band adds the paper's own parameter uncertainty to the inherited draws and Monte Carlo noise; it still excludes calibration and survey-sampling uncertainty, and the ranges themselves are judgments.

Table 9. The parameter Monte Carlo, S3. Change in the ratio from the baseline, percentage points; 200 runs; every ranged parameter drawn per run.

The 2050 change is positive in 88% of runs and lies between −0.03 and +0.48 points in nine runs out of ten. The Monte Carlo mean (0.16) exceeds the central-value result (0.125) because several ranges are right-skewed: a triangular draw over a range whose high end is further from the center than its low end has a mean above the center. The draws that move the 2050 effect most are the saving program's retention (rank correlation 0.20 with the change), its size (0.18) and its take-up (0.15), and the reach of the ten largest banks (0.18). The block's retention also registers (0.19), because the block's effect accumulates over active years. Every other draw is within sampling noise of zero (Figure 2, panel B).

5.4 Corners of the range

Table 10. Core levers at low, central and high values. "Low" and "high" set every ranged parameter to that level together, so they are corners of the range, not likely cases. Change in the ratio in percentage points (mean; 5th to 95th percentile) and dollars added to the median Black household.

At low values the effect is close to zero. At high values it is 0.6 to 0.9 points in 2050, and the median Black household holds $3,000 to $4,000 more. Even that corner leaves the 2050 ratio within about one point of the baseline. With the untested stress lever added, S3 is 0.135 points at central values and 1.02 points at the high corner.

5.5 Attribution across the levers

We computed exact Shapley values over the lever blocks in S3 at central values, run by run, from all 16 combinations of the four levers on the same 120 seeds, so a run's values sum to that run's total effect. The core attribution uses the eight combinations without the stress lever.

Table 11. Shapley values, S3, central values, 120 runs. Percentage points of the ratio and dollars added to the median Black household; standard errors in parentheses. Shares are of the set's total and are unstable when the total is small.

The saving program accounts for about 88% of the 2050 effect in the headline set, and 82% when the stress lever is added. That lever is not one of the decisions the tools make. It stands for goals, commitment and automatic saving, which are products a bank runs; decision calls could time or target them, but most of the projected effect belongs to the saving product, not to the decision engine. The two decisions together, the fee alerts and the gambling block, add 0.015 points (standard error about 0.004) and $43 in 2050. The fee lever is not distinguishable from zero at opt-in enrollment. The gambling block's 12% share is larger than in version 1 (3%) because the saving program is smaller, not because the block grew.

5.6 What moves the result

One-at-a-time ranges of unequal width cannot rank the levers, so we scale each block's effect-size and take-up parameters by 0.9 and 1.1 together, everything else central, and report the change in the 2050 effect per 10% change in the block's dose, the product of the scaled parameters (for reach, the reached share). Figure 2 and Table 12 give the result; Appendix G keeps the range corners for reference.

Table 12. Elasticities of the 2050 effect to each block's dose, S3, 120 runs. The dose elasticity is the proportional change in the effect per proportional change in the dose; "per 10%" is the change in the 2050 effect for a 10% larger dose, with its paired standard error.

A 10% larger saving effect (size times take-up) adds 0.013 points to the 2050 effect; 10% more reach adds 0.011. Within the ranges we set, the saving block's high corner is far wider than reach's, which is why version 1's one-at-a-time table made reach look unimportant. On equal proportional terms the two matter about equally, and the gambling block matters an order of magnitude less. The elasticity of the saving program rises to 1.7 by 2075 because the flow compounds.

5.7 Sensitivities: persistence, eligibility, defaults, rollout, structure, calibration

Table 13. Structural and calibration sensitivities, S3 core at central values unless stated, 200 runs. Change in the 2050 and 2075 ratio in percentage points (standard error) and dollars added to the median Black household in 2050. The last two rows are measured against their own baselines.

Three things stand out. Persistence matters more than any single design choice: with no drop-out, the 2050 effect doubles to 0.26 points, and the retention-only rows bracket the headline between 0.08 and 0.26. Eligibility barely matters, because almost every reached Black household under 67 already falls below the national median wealth for its age, so the rule binds mostly on White households; the "all reached" row moves the ratio by 0.003 points and the dollars not at all. Defaults instead of opt-in matter at the margin the paper's policy advice (Section 7) depends on: default-on alerts add 0.016 points, a default-on block 0.041, and every lever on by default raises the headline to 0.25 points. A nine-year rollout costs 0.003 points. The calibration matters as much as any of these: the separate-saving-rate specification, which fits a lower Black saving rate, gives a lower baseline and a slightly larger effect, and the 2025 refit, which fits the new profiles worse (calibration loss 8.1 against 3.9 for the 2022 fit), gives 0.098 points. Across every reasonable re-parameterization the 2050 effect stays under about 0.3 points; the small lever stands.

5.8 What changed from version 1

Version 1 (October 12, 2026) reported +0.12 points for S3 at central values on a 2022 start. Two things changed: the parameters (Section 3.4; a saving effect of 0.6% instead of 1.0% of income, and opt-in alert enrollment of 5% instead of 28%), and the starting survey. Table 14 separates them on the same seeds and engine; the first cell reproduces version 1's published number exactly.

Table 14. Decomposition of the change from version 1, S3 core at central values, 200 runs. Mean change in the 2050 ratio in percentage points (standard error) and dollars added to the median Black household.

The re-derived parameters cut the effect by about a third. The 2025 start raises it by about two thirds, for two reasons: the same dollars are a larger share of a smaller Black median, and more reached Black households fall below the eligibility threshold. The two changes offset, which is why the headline ratio change is almost unchanged while the dollar figure fell from $863 to $566. That coincidence is not a sign of robustness; it is two corrections of opposite sign.

5.9 Comparison with Years and Dollars

The product lever of Years and Dollars, at a reach of 50% with every other condition unchanged, moved the 2050 ratio by 1.07 points and the median Black household by $5,937 on a 2022 start [2]. Our benchmark scenario S4, which reaches 50% of banked households, gives 0.12 points and $530 at central values, and 0.65 points and $3,018 at high values, on a 2025 start. The central case is about 11% of the earlier effect at the same reach, and the high case about 60%. The difference comes from the assumptions. The planning values in Years and Dollars were a 2-point saving increase, 0.5 points from stress, halved card interest, halved housing distress and 0.5 points of extra return. Our central saving effect is 0.6 points, we set the card-interest, housing and return terms to zero because a bank-side tool does not act on them, and we add fee and gambling flows that are small in dollars. The earlier numbers were planning targets. Ours are bounded by the evidence we found, and that evidence supports less.

5.10 Why the effect is small, and what would make it larger

Why it is small. In S3 at central values, 9.9 million Black households are reached in 2050. Eligibility, take-up and retention leave far fewer active: about 1.03 million in the saving program, 0.13 million in the gambling block and 0.03 million in the alerts. Each active household gains a modest flow. A 0.6% saving increase for a household earning $50,000 is $300 a year; ten active years of $300 at a 3% real return is about $3,400, and fewer than a tenth of 2027 adopters are still active in 2050. Fee savings average about $54 a year for an active fee-paying household at central values ($300 in fees cut by 18%), and at opt-in enrollment only 30,000 Black households are active. Against a median gap of about $295,000 in 2025 dollars, these flows add up to hundreds of dollars, not tens of thousands. The levers also do nothing for the 10.6% of Black households that are unbanked, who are among the poorest [7].

What would make it larger. The elasticities and the sensitivities point to four things, in order of size.

1. A larger, more durable saving effect. The saving block has the largest elasticity, and persistence doubles the effect. A bank that turned decision support into automatic saving with a default, and kept households enrolled, would act on the parameters that matter. The steady-state evidence [76, 77] says what a default delivers once attrition is counted, in other settings.
2. Reach. On equal proportional terms, 10% more reach is worth about as much as a 10% larger saving effect. Reach is bounded by which institutions Black households use, which no public source reports.
3. Defaults instead of opt-in. Opt-in reaches 3–8% for alerts [23] and about 5% for gambling blocks [29]. Every lever on by default doubles the headline (Table 13). Defaults raise autonomy questions that a pilot must settle.
4. Targeting. The levers are race-neutral, and White households gain most of the aggregate dollars. Tools aimed at households with the highest fee and betting incidence, or delivered through institutions that serve mostly Black households, would narrow the ratio more per dollar. The MDI-only variant raises the MDI effect by a third but stays small because MDIs are small.

Where the larger levers are. Years and Dollars finds that the gap closes only under combinations of equal earnings and mobility, equal returns and equal survival, with earnings the largest single contributor [2]; structural models agree that earnings equalization dominates and that transfers alone fade [88, 89], and the long-run record shows convergence stalled after 1950 [87]. A bank-side decision tool does none of these things. It can speed saving for the households it reaches and remove some leaks. It cannot substitute for the policies that change earnings, inheritance, homeownership and access to credit; even access to banking itself, which raised low-income and Black households' wealth in two quasi-experimental settings [98, 99], is a larger lever than any decision at the account. Median wealth in 2050 is also the wrong yardstick for the fee lever: an avoided overdraft can be worth more than the fee to a household that would otherwise borrow from a payday lender [85], and that value does not appear in a wealth ratio.

6. Threats to validity

Table 15 lists the main threats and the direction of bias where it is known. Five matter most: every effect is imported from another setting; the racial effect rests on incidence, not dollars; reach numbers are proxies; two levers, gambling blocks and stress timing, have no causal evidence; and the model's behavior is calibrated to a different survey wave from its starting population.

Table 15. Threats to validity.

Gaps we could not close. We looked for the following and did not find them. Silence should not be read as support.

• A causal evaluation of a bank gambling block or cooling-off period.
• A study linking measured sleep, heart-rate variability or stress to dollars.
• Overdraft or gambling dollars by race, and which institutions Black households use; a county-weighted reach proxy from the FDIC Summary of Deposits was not computed.
• Black-household banking rates for Michigan and Detroit.
• Outcome evaluations of round-ups, Bank On accounts and credit-union financial-health pilots.
• Money lost to missed return windows.
• The FDIC's current MDI list, a verified count of community development credit unions, and the text of the Section 1033 order.
• The published texts of the reminder study and the Iceland app study, which is why we use the 2010 draft's figures for the first and a summary's for the second [35, 27].

7. Discussion and policy

7.1 What the evidence and the projection say

Fee alerts have the best evidence. Gambling blocks address a clear harm with little evidence that they prevent it. Stress timing is a hypothesis. Saving defaults work, and reminders and goals work weakly; the default effect fades over a few years. Put through a model of household wealth started from the 2025 survey, these add about 0.13 points to the 2050 ratio at central values, between −0.03 and +0.48 points across the paper's parameter ranges, and under about 0.3 points under every structural variant we ran. Years and Dollars reached the same qualitative conclusion for a consumer product: it can narrow the gap but not close it [2]. This paper puts a number on that conclusion for a bank-side tool, and finds the effect smaller than the earlier planning targets.

The result also says where the effect sits. The uses that motivate the Understanding API, the fee alerts and the gambling check, carry about 12% of it, and the alerts alone none that the model can distinguish from zero at opt-in enrollment. The saving program carries the rest, and that is a bank product that decisions can support but do not replace.

That result does not make the tools worthless to the households that use them. Avoided fees and blocked bets are real money to a household with a thin balance, and an avoided overdraft can be worth more than the fee where the alternative is a payday loan [85]. But the result should set expectations. A bank that adopts decision tools to close the racial wealth gap will be disappointed. A bank that adopts them to cut avoidable fees, protect customers who ask for a gambling block and raise saving by default, and measures what happens, may do some good.

7.2 What banks could do

• Start in shadow mode and publish the comparison of any decision engine with the bank's own rules (Appendix B).
• Make alerts the default, with an easy exit. Opt-in reached 3–8%; automatic enrollment was what worked [4, 23]. In the model, default-on alerts add 0.016 points to the headline (Table 13).
• Offer a gambling block with a cooling-off period of at least 48 hours, as the Bristol researchers recommended [20, 95], and measure it. Do not describe it as proven. Check sweepstakes casinos by name, since the category code misses them (Appendix D).
• Put the most effort into saving defaults, and into keeping households enrolled. That is where the model finds the effect, and persistence is the parameter that doubles it.
• Report abstain rates, overrides and error rates by group, and route abstentions to people (Appendix A).
• Keep any decision API out of credit decisions (Appendix C).

7.3 What minority depository institutions and community lenders could do

MDIs and minority depository credit unions serve many households in the gap, though we cannot say what share [52, 55]. They are small, so their effect on national ratios is small, but their effect per household served could be the same or larger. Three steps would help: share a pilot across institutions so the sample is large enough; work through a shared core vendor; and ask supervisors how digital financial-health services will count under the Community Reinvestment Act (Appendix C). Michigan has six minority depository credit unions, so Detroit is a reasonable place to start [55].

7.4 What regulators could do

• Settle the CRA treatment of digital financial-health services, so banks know whether they earn credit (Appendix C).
• Say how unfair-practice authority applies to alerts and blocks. Regulation E does not require alerts [64].
• Publish overdraft and gambling-merchant data by race and income, where law allows. Dollars by race is the largest hole in this literature.
• Say how SR 26-2 applies to hosted decision models used at the account [93].

7.5 What researchers could do

• Test a hard gambling block with a cooling-off period against a control. No such trial exists [20, 22].
• Link measured sleep, heart rate or stress to transaction data, with consent (Section 3.5).
• Estimate fee and gambling dollars by race and income.
• Replicate the UK alert experiments at a US bank [4].
• Measure how a liquid-saving default's effect attenuates under continued enrollment, the parameter this projection is most sensitive to.

8. Conclusion

Decision tools at the bank account act at the right moment, and some of them have good evidence behind them. Real-time overdraft alerts cut charges in large field experiments. Saving defaults raise saving, with effects that fade over a few years. Gambling blocks stop transactions at the card, though no controlled study shows that they reduce losses.

Put through a model of household wealth started from the 2025 Survey of Consumer Finances, these tools are a small lever on the Black–White wealth gap. Deployed at the ten largest banks and at minority depository institutions together with a default saving program, they would raise the model's 2050 ratio of median wealth by about a tenth of a percentage point at central values. Across the paper's parameter ranges the band is roughly −0.03 to +0.5 points; with every lever on by default and no drop-out, the effect is about a quarter of a point. The saving program does most of the work. The alerts and the block, which motivate the product, add little to wealth in the model, though they may matter to the households they protect.

The main uncertainty is persistence, and its direction is known: the model lets a default's effect run for as long as a household stays enrolled, while the evidence shows the effect attenuating under continued enrollment, so the headline is more likely too high than too low. The second uncertainty is the starting survey, whose Black median fell by an amount within its sampling error; starting from 2022 instead gives a smaller dollar effect and a similar ratio effect.

The next question is empirical, and a bank can answer it: how much of a liquid-saving default's first-year effect survives three years at a deposit account, and for whom. The pilot in Appendix E is designed to measure that parameter, with take-up and retention as outcomes. The larger levers on the gap, in earnings, returns and survival, lie outside the account.

Appendix A. The Understanding API, as of October 18, 2026

This appendix describes the product that motivates the question. It is dated, because the product changed between version 1 and version 2 of this paper. Nothing in it enters the projection except the list of decisions a bank could call.

A.1 The contract

The Understanding API offers decisions at the account to banks, credit unions and health software. It is in early access, has no bank or credit union customers, and the examples on its page are labeled as illustrations, not measured results [6]. A caller asks one bounded question about one transaction, message or signal. There are three question types: a yes-or-no predicate, a choice from a list and a score on a scale [6]. Every response has four parts: the answer, a probability, machine-readable reason codes and an abstain flag that is true when the case should go to a person instead of the engine [6]. The API will not make credit underwriting or adverse-action decisions, medical diagnoses or treatment decisions, and it will not verify identity [6]; Appendix C explains the credit boundary.

A.2 What exists in code, and what changed on October 13, 2026

Version 1 of this paper described a decision layer of rules and hand-set weights, the code that runs Vueni, and said that no function returned a calibrated probability or an abstain flag. On October 13, 2026, after version 1's sources were closed, the company moved the API's decision layer to a hosted decision model, reached through a gateway, with the Understanding engine supplying facts to the model's state [105]. The design is facts first. The engine, which is deterministic, turns raw fields into facts: the network's description of the merchant category; gambling rule checks by category code and a brand list; and, for each candidate charge or refund, the amount gap, the time gap, the name similarity and the engine's own pick. It settles by rule the cases that are true by definition, such as no purchases to match. The hosted model then answers one typed question over those facts with a probability. The envelope is computed in the company's code: the probability is that of the answer given, and abstain is true when the probability falls under a threshold (0.8 by default, adjustable) or when the model declines [105]. We do not name the model here; the choice is provisional.

As of October 18, 2026, four banking decisions exist in code: restricted merchant (gambling), spend type (essential, discretionary or neutral), receipt matches transaction, and refund pairing. No health decision exists, and there is no standalone return-window decision or message routing. The endpoint is built and tested but not deployed, and it has processed no customer's data [105]. The benchmark in Appendix D measures the engine's facts layer on October 12, 2026; the hosted model's accuracy, calibration and latency have not been measured, because the gateway's free tier does not serve the model.

A.3 Comparison with general decision APIs

The Understanding API belongs to a family of interfaces in which a caller asks a typed question and gets a typed answer with a probability, instead of free text. OpenAI's endpoint, POST /v1/decisions, takes a question and returns a probability for a predicate, a probability per option for a choice, or a probability-weighted score, and supports one model, in public beta from October 6, 2026 [43, 46]. Its guide documents neither reasons nor abstention; a refusal answer is the nearest analogue [43, 45]. Microsoft's decision model is reported to return probabilities for the same three types, released on October 8 or 9, 2026 (secondary sources) [44, 47]; Cloudflare's model has a similar interface [48]. OpenAI says its endpoint is up to ten times faster than its Responses API; it publishes no absolute latency, and we found no independent benchmark [43, 46]; secondary coverage repeats the claim without figures [49, 50]. Our contract follows the same three question types, so a bank could compare engines behind one call shape. The vendors above offer general models; the Understanding API is limited to a short list of banking and, in the specification, health decisions, with reason codes and abstention specified as part of every response [6]. A narrow list is easier to specify, test and audit. We do not claim that narrower is better, and whether reason codes and abstention help in practice is untested.

A.4 Governance

A decision at the account affects a person's money. A bank that deploys any such engine will need to explain, audit and override it. The rest of this section is what we propose, not what exists.

• Reason codes. Each answer carries codes that a bank's system can log, show to the customer and audit [6]. A bank could count which codes fire, for whom, and how often a person reverses the outcome.
• Abstain and human review. When the engine abstains, the case goes to a person. We propose that deployers route abstentions to a named queue, set and publish an abstain threshold for each decision from its own reliability table, and sample confident answers for review so that confident errors are found.
• Audit trail. We propose logging every call with a hash of its input, the answer, the probability, the reason codes, the engine and model versions and any override, so an examiner could replay a decision.
• Model risk. On April 17, 2026 the Federal Reserve, OCC and FDIC replaced SR 11-7 with SR 26-2, which the agencies expect to be most relevant to banks over $30 billion in assets [93]. The engine's deterministic rules are probably outside its definition of a model; a hosted decision model is plausibly within it. A vendor should supply what a review needs: decision definitions, descriptions of development and test data, per-decision results, monitoring data such as abstain and override rates, and change notices.
• Fairness checks. Years and Dollars plans to check that interventions do not fire more often for some groups than for others at equal underlying risk [2]. The same applies here: a restricted-merchant decision that mislabels a grocery store as gambling blocks a legitimate purchase, and a bank needs the error rate by group. Such testing is good practice and a partner expectation; it is not a federal requirement for these decisions, and the CFPB's 2026 rule states that ECOA does not authorize disparate-impact liability [94].
• Data. The bank remains the data owner, and a vendor contract should bar the vendor from using bank data for any other purpose (Appendix C). The API page makes no claims about SOC 2 reports, data residency, a no-training commitment or business associate agreements, and this paper makes none [6].

Appendix B. Implementation at banks and credit unions

B.1 Integration points

A bank could call the API in three places. These are proposals; none has been deployed.

• Authorization. At card authorization, a restricted-merchant call can ask whether a merchant is gambling by category code plus descriptor, and the issuer can decline [6]. The call must return inside the authorization window, which the hosted model's round trip has not been measured against; until it is, the rule checks run inline and the model's answer is used for the next transaction or a hold. An abstain should default to the bank's existing rule, not to a decline.
• Alerts. Just-in-time alerts are the best-supported intervention (Section 3.1). A spend-type or score call could decide whether a message is worth sending. The UK trials found that early-warning alerts added nothing beyond just-in-time ones [4]; that fits a layer that suppresses low-value messages, but we have not tested it.
• App and statement. Receipt matching, return-window reminders and message routing sit in the app and the service queue. They have no outcome evidence (Table 2), and they are not in the projection.

All three can run on data the bank already holds, with the API seeing only the fields the bank sends.

B.2 Reach by institution type

Reach is the share of Black households that an adopting bank could serve. No public data say which institutions Black households use; the FDIC survey does not ask [7]. We use deposit shares and counts as proxies and treat every reach number as an assumption.

Table B1. Public data behind the reach assumptions. None of these is a count of Black households served.

Three points matter for the model. First, about 15.4 million of the 17.25 million Black households are banked (our computation from [7]); no bank deployment reaches the 10.6% who are unbanked, and at $50,000–75,000 of income the unbanked rate is still 3.5% for Black against 0.8% for White households [7]. Second, the largest banks hold most deposits: the four largest held 34.7% of domestic deposits on June 30, 2025 and the ten largest 48.7%, by our sums from FDIC call-report data across 4,494 records; on the FDIC's universe of 4,421 insured institutions for that date the shares are 34.9% and 49.1% [51]. Deposit dollars are not households. Third, minority institutions are many but small. The National Bankers Association Foundation counts 153 MDIs with $381 billion in assets, 16% of them Black-owned, or about 24 institutions by our computation, with a median of $201 million in assets among Black MDIs and $475 million among all MDIs [52]. The Federal Reserve counts 151 MDIs with $366 billion at the end of 2024 [53], against industry assets of $26.46 trillion in mid-2026 [54]. The NCUA lists 448 minority depository credit unions with 7.03 million members, who are individuals, not households [55]. We could not read the FDIC's current MDI list or verify a count of community development credit unions, so the model uses MDI credit unions in their place.

B.3 Detroit

TUC is in Detroit. The FDIC survey puts the Detroit–Warren–Dearborn area at 5.0% unbanked, 13.2% underbanked and 81.8% fully banked in 2023, across 1.94 million households. The interval on the unbanked rate is wide, 2.6% to 9.5%; the 2021-to-2023 change is not significant; and the 2023 underbanked rate is not comparable with 2021 because a question changed. Michigan overall was 3.2% unbanked [7]. No Black-household rate is published for Michigan or Detroit [7]. A 2024 Detroit City Council staff memo cites a 2005–06 survey of about a thousand low- and moderate-income Detroit-area families in which about 30% of adults were unbanked; neither the population nor the unit is comparable with the FDIC's household rate [56]. Six minority depository credit unions operate in Michigan, with about $816 million in assets and about 57,000 members (sums from the NCUA list) [55].

B.4 Adoption paths

A bank can adopt in steps that limit risk.

1. Shadow mode. The bank sends transactions to the API and compares the answers with its own rules, with no customer-facing change. This yields the evaluation data that Appendices D and E need.
2. Staff-facing. Abstentions and reason codes feed service queues.
3. Opt-in features. Customers choose alerts, a gambling block or an overnight spending limit. Opt-in take-up was only 3–8% for overdraft alerts [23] and about 5% for Monzo's block [29].
4. Default-on with a one-click exit. Default enrollment persists [38, 39], though its effect on saving attenuates over three years [77], so default-on alerts could reach far more people. A default gambling block raises autonomy questions (Appendix E).

The Community Reinvestment Act credits services as well as lending, which is a reason a bank might adopt (Appendix C).

Appendix C. Regulatory frame, as of October 17, 2026

This appendix states what is in force, proposed or enjoined. It is not legal advice. Items confirmed only in secondary sources are marked.

Table C1. Regulatory status on October 17, 2026.

C.1 Community Reinvestment Act

The CRA credits banks for services as well as lending. That is the opportunity for a bank that deploys decision tools in low- and moderate-income communities. The rules are unsettled. The October 2023 final rule set four tests for large banks and gave consideration to financial-literacy activities for low- or moderate-income people [58]; it was preliminarily enjoined on March 29, 2024, before its April 1, 2024 effective date, and the Federal Reserve states that it continues to apply the 1995 regulations [57]. On July 16, 2025 the three agencies proposed to rescind the 2023 rule [57]. The OCC and FDIC did not finalize that proposal: their August 12, 2026 proposed rule says so and replaces it for the banks they supervise, refocusing the regulations on credit needs, while the Federal Reserve's rule is untouched; comments were due October 13, 2026 [59]. Whether a digital financial-health tool earns credit under the 1995 rules is unsettled; we did not review the regulation text on that point and do not claim that it does. Activities with minority depository institutions, low-income credit unions and community development financial institutions qualified under the 2023 rule [58]; partnerships with them suit a pilot whatever the final rule says.

C.2 Unfair, deceptive or abusive acts or practices

Under 12 U.S.C. 5531 the CFPB can act against unfair, deceptive or abusive acts or practices [66]. On May 12, 2025, the CFPB withdrew 67 guidance documents, including its overdraft circulars, the 2023 abusiveness policy statement and the two circulars on adverse-action notices for complex models; the statute remains [65]. The exposure runs both ways. A decision that blocks a legitimate purchase, or an alert that misleads, could be challenged. A bank that keeps earning fees that a timely alert would have prevented was the target of the withdrawn circulars. A reason code on every answer, the abstain path and a one-click override are our design responses; they would reduce the risk, not remove it.

C.3 Regulation E and the repealed overdraft rule

Regulation E requires notice, affirmative consent and written confirmation before a bank charges a fee on an ATM or one-time debit-card overdraft; it does not apply to checks or ACH and does not require balance alerts [64]. Alerts are therefore voluntary in the United States, unlike the UK, where the Competition and Markets Authority's 2017 order required large banks to enroll customers by February 2018 [23]. Congress repealed the CFPB's 2024 overdraft rule on May 9, 2025, and the Congressional Review Act bars a new rule in substantially the same form [13]. A bank that adopts alert or decline-before-fee logic acts voluntarily, at a cost to fee revenue.

C.4 ECOA and Regulation B as a boundary

Regulation B defines its terms by reference to credit [67]. The API's decisions are not credit decisions, which is why the launch list excludes underwriting and adverse-action decisions [6]. If an API output ever fed a bank's decision on a credit line, an overdraft limit or an account closure, Regulation B could attach, with its duty to give specific reasons, and so could the Fair Credit Reporting Act where third-party data is used. A bank should bar that use by contract and by design. The CFPB's 2026 rule removes federal disparate-impact liability under ECOA; intentional-discrimination rules, state law and partners' own policies remain [94]. Lending is outside the scope of this paper.

C.5 Section 1033, Gramm-Leach-Bliley and HIPAA

A bank that uses the API on its own customers' data does not need the Personal Financial Data Rights rule, because it already holds the data; the rule matters for a consumer-permissioned path, and the projection does not rely on it [60, 62, 63]. Under Regulation P, a bank may share nonpublic personal information with a nonaffiliated service provider without offering an opt-out, with the initial notice and a written contract that bars the provider from using the data for any other purpose [68]; the API would run under that exception. When a health plan, a provider or one of their vendors calls the API with member data, TUC would be a business associate, and a business associate agreement would be needed first [69, 70]; the API page does not say that TUC signs such agreements, and we make no claim either way. When a consumer's own app sends health readings the consumer chose to share, HIPAA does not apply, and the FTC's Health Breach Notification Rule, as amended effective July 29, 2024, covers the vendor instead [71].

Appendix D. The engine, measured

D.1 What we measured and why

A decision layer at the account must be fast enough for card authorization, deterministic enough to audit and accurate enough not to block legitimate purchases. We built a harness that asks the same bounded questions of three arms on the same data and reports speed, accuracy, determinism and, where it applies, abstention, calibration and cost [105]. The arms are our engine's decision functions, run locally; the API's decision layer, which asks the hosted decision model with the engine's facts in its state (and the same model with raw fields only, to show what the facts add); and a general-purpose language model given the question in a prompt. Only the engine arm has been run, on October 12, 2026. The other two are pending paid gateway credits; both runners were checked end to end against a mock model, and those outputs were deleted. We will publish the results whichever way they go.

What this benchmark is not. It is not a measurement of the API as a service: no hosted call was timed, and the engine numbers are in-process function calls on one laptop. It is not accuracy on real transactions: every record is public-sourced, assumed or synthetic, and TUC, which sells the engine, built the datasets as a published, rerunnable test that deliberately includes cases the engine fails. It is not a result at any bank or customer.

D.2 Data and method

No label comes from the engine. Labels come from a public source, from a rule frozen before any engine run or from how a record was built. The restricted-merchant set has 210 records. Positives come from the ISO 18245 gambling category codes, the Ohio Casino Control Commission's list of active sports gaming licensees (each brand with and without a category code) and the 26 online sweepstakes casinos named in the New York Attorney General's June 2025 cease-and-desist letters, with assumed game or digital-goods codes. Negatives include ordinary merchants, game stores and arcades, and real and invented look-alike names. The spend-bucket set has 284 category codes labeled by a keyword rule frozen before the engine was run, so its result is agreement with our rule, not accuracy. Receipt matching (300 cases), refund pairing (175) and receipt extraction (130 emails) are synthetic, with ground truth known by construction and slices that vary what makes the task hard. Each task has one scorer, shared by all arms. Latency is timed around each single call in process: five warm-up passes are discarded, then 200 timed passes give 26,000 to 60,000 timed calls per task. Determinism is tested by hashing all predictions over five passes. The machine was an Apple A18 Pro, as reported by the operating system, with six cores and 8 GB of memory, running Node v24.20.0, on one thread.

D.3 Results

Table D1. Engine results, measured October 12, 2026, in process on one laptop, on test sets TUC built. These are not latencies of an API call and not accuracy on real transactions.

The engine almost never returns a wrong answer; it misses, and where it misses matters more than the totals. The gambling check caught every record coded with a gambling category (41 of 41) and raised no false alarm on 94 non-gambling records, including 34 look-alikes. It caught 61 of 116 gambling merchants. Of its 55 misses, 41 were sweepstakes casinos, which carry game or digital-goods codes and can be found only by name, and its merchant list is short and fixed; it also missed 10 of 17 licensed sportsbooks when the code was absent. Sweepstakes casinos are the gap a bank would most need to close, because the card network's category code does not flag them. The receipt matcher was right on every case in the slices it is built for and, when it named a charge, was right 179 of 183 times; it matched none of 30 receipts with a tip above 3%. The parser never returned a wrong total but missed every email that phrased the total as "You paid" or "Payment received". The refund finder was right whenever it answered and, by design, missed refunds of less than half the purchase and refunds after 45 days. On the 90 codes our rule calls discretionary, the spend bucket never chose essential; across all codes it assigned a class to 7 that the rule leaves neutral. Precision was 97.8–100% on the binary and pairing tasks; against our frozen rule the spend-bucket classes had precision of 80% and 91%.

Not benchmarked: the stress score, because the only labels that exist are the engine's own test expectations; the spend-type decision with a restricted class, the return-window decision, message routing and the health decisions, which have no decision function; and calibration, which belongs to the hosted model arm.

D.4 The two pending arms

The API arm asks the hosted decision model the four named decisions with the engine's facts in its state. It reports accuracy over all cases (an abstained answer counts as given), accuracy when not abstaining, the abstain rate, the Brier score and a reliability table; a raw-fields variant shows what the facts add. The language-model arm sends each task's fixed prompt with the same fields the engine receives, at temperature 0 with at most 64 output tokens, and scores replies with the same scorers. It times one HTTP round trip from the client machine, repeats the first 20 prompts of each task twice for determinism, and prices each call from the provider's usage field at a recorded price. The default models are the small, fast general models of two providers, priced from their published lists and a secondary source that will be checked before any cost is quoted [72, 75]. The model identifiers and request shapes have not been checked against a live service, and third-party latency figures are not comparable and are not used [73, 74]. Every number will carry its date, model, client location and price source. The engine and the models are not like for like: one is code on the same machine, the others are network calls to hosted models. A result in a model's favor is a result, and we will report it the same way.

D.5 Limits

The datasets were built by the company that sells the engine. The positive gambling brands come from two public lists, not a random sample of gambling merchants. Descriptors and most category codes are synthetic or assumed. Receipt and refund cases follow formats we wrote. The test may flatter the engine on the slices it was designed for and penalize it on slices we chose to include. Accuracy on these sets says nothing about whether a decision changes anyone's finances; that needs the pilot in Appendix E.

Appendix E. A pilot design, not yet registered

This is a plan, not a registered protocol. No registry has been chosen, no partner institution has agreed, no ethics board has reviewed the design and no start date is set. We will register the protocol at a public registry before any customer is enrolled. A pilot measures the parameters the projection is most sensitive to (the size of the saving effect, take-up and retention); it does not measure the wealth gap.

Phase 0, shadow mode. Before any customer sees a change, the partner sends transactions to the engine and compares its answers with the bank's own rules. This phase reports the engine's agreement, abstain rate and error rate by slice on the bank's own data, including the share of gambling-merchant spend that falls on sweepstakes casinos the engine would miss. It costs customers nothing and tells the bank whether to proceed.

Design. Individual customers at one or more partner institutions, randomized within strata defined by past fee incidence, past gambling-merchant spend and income band, with a holdout group that keeps the bank's current service. There are four arms, each compared with the holdout. The first is just-in-time balance alerts with decline-before-fee logic, default-on with a one-click exit. The second is an automatic transfer to savings at a default share of each deposit, with a one-click exit. The third is a card-level gambling block with a 48-hour lock on removal, checking sweepstakes casinos by name, offered to all and default-on only if the partner and the ethics review agree. The fourth is an overnight spending limit, exploratory and labeled so, offered only to customers who connect health data. Analysis is intention to treat with strata fixed effects, robust standard errors and a correction for multiple testing across the primary outcomes. The sample size will be set before enrollment from the partner's own baseline incidence and variance. As an illustration only, detecting a 15% relative reduction in annual fee incidence from a base of 34% (to 29%) with 80% power at the 5% level needs roughly 1,300 customers per arm; fee dollars are skewed and need more.

Table E1. Pre-specified outcomes.

Effects will be reported by income band, and by race and ethnicity where customers choose to share it, within the law that applies to the institution; how race and ethnicity may be collected for deposit-account analysis is a question for the partner's counsel, and the protocol will state the answer. The protocol will name harm thresholds before launch, such as a rate of false blocks or complaints, at which an arm is paused for review, and will track displacement to cash, other accounts and other borrowing, the displacement the UK credit-card ban evaluation watched for [21]. Consent language must tell holdout customers that they will not get interventions they might expect, and a default-on gambling block raises autonomy questions to settle before launch. We will publish the protocol, the results whether or not they favor the product, the distribution of interventions across groups and every change to the engine's thresholds during the pilot; we will seek an outside evaluator and share the data and code with them; none has been named.

Appendix F. Stock-to-flow conversions for the saving program

The model adds a share of income to an active household's saving rate every year it is active. The literature reports a mix of balance stocks, pension flows with employer money, and saving rates. Table F1 converts each to the model's unit; the central value is the steady-state flow.

Table F1. How each saving study converts to an annual saving rate.

Appendix G. One block at a time, for reference

Table G1. S3 with all four levers, every block at central except the one named, 120 runs. Within a block, take-up, persistence and effect size move together; the ranges are of unequal width, so these rows do not rank the blocks (Section 5.6 does).

Disclosures

Competing interest. The authors are the founders of The Understanding Company, which develops Vueni and sells early access to the Understanding API, the product whose decisions this paper models [6]. The company would benefit if banks adopted it. Readers should weigh our interpretation accordingly. Nothing here is financial, medical or legal advice.

Status of the product. The Understanding API is in early access. It has no bank or credit union deployments, and no outcome data exist. Vueni is waitlist only while it launches, with its card planned for 31 US states, and is not a bank; its accounts, cards and money movement run on Whop's financial infrastructure and its partners.

Funding. No external funding is reported for this work; the authors are employees and owners of TUC.

Role of AI tools. This paper was prepared with the assistance of AI tools, which searched for and read sources, built the model, the inputs and the benchmark harness, drafted text and checked citations; a referee-style audit by an AI tool on October 17, 2026 produced the list of fixes applied in this version. The authors are responsible for the content. Version 2's sources were opened on October 18, 2026 unless the source table says otherwise; where a source was read only as an abstract, a summary, a draft or a press release, Table 2 or the text says so. The check log is research/checks.md.

Data and code availability

• Public inputs. The 2025 Survey of Consumer Finances summary extract and full public data set [91], the CPI-U [92], the inputs of Years and Dollars for mortality and the literature parameters [2], the FDIC's 2023 household survey [7], FDIC call-report data [51], the NCUA's list of minority depository credit unions [55] and the sources in the References.
• Model. The projection model, its parameters with sources and judgment flags, and its results are in the study's replication folder (model/): Node 24 and Python 3, standard library only; seed base 1; Monte Carlo seed 20251018; 200 runs of 5,000 households per scenario and 120 for attribution, one-at-a-time and elasticity runs. The full run took about 59 minutes on six cores; the 2025 refit took 92 minutes on one core. Results do not depend on the number of threads. The engine of Years and Dollars and its 2022 data are vendored from the committed version 2.1 so that the results do not depend on later changes to that paper. Every number in Sections 4 and 5 and in Appendix G is read from model/results.json by the report and figure scripts.
• Benchmark. The harness, datasets, prompts, frozen label rule and results file are in bench/. Every dataset is rebuilt byte for byte by a script with fixed seeds, and each results file stores dataset hashes and the machine description.
• Engine. The Understanding engine's source code is proprietary, as stated in Years and Dollars [2]. The benchmark calls it unmodified. The hosted decision model is a third party's.
• Customer data. None is used.
• Public link. The replication folder has no public link or persistent identifier yet; it is available on request until one is minted.

Version note

Version 2 (October 18, 2026): re-baselined on the 2025 SCF; saving-program and alert-enrollment parameters re-derived; parameter Monte Carlo, Shapley attribution over the core set, elasticities, persistence, eligibility, default-on, rollout and calibration sensitivities added; figures added; the referee's fifteen fixes of October 17, 2026 applied; product and regulatory facts dated. Version 1: October 12, 2026 (+0.12 points on a 2022 start). The full change log is in the replication folder.

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