Digital Credit and Financial Behavior

Participants are interviewed once, in person, at their stall or place of business in a Maputo market. Every participant watches a video on the enumerator's tablet, at the same point in the interview, immediately after prior beliefs are collected.

The treatment has three components, delivered at two points in the interview. The video and the eligibility check come together, immediately after prior beliefs are collected. The card comes at the very end, after the questionnaire is complete. Because the video and the check both precede outcome measurement, the survey outcomes reflect those two components jointly. The card is handed over after every survey outcome is recorded, so it can only affect the administrative outcomes measured 30, 90, and 180 days later.

The treatment group watches a video on the terms of Txuna, the digital credit product offered through M-Pesa. It covers three things a borrower cannot readily infer from the handset menu: what the product costs, how much a given person can borrow, and what follows from late repayment. The price is given for each of the three repayment terms with worked examples, and it is the same for every user rather than something earned through a good repayment record. Borrowing capacity is explained as an individual limit within a stated range, set automatically and available to check free of charge. On late repayment, the video covers what happens to the balance once the term has passed, how money entering the wallet is used to repay, the potential legal consequences of non-repayment, and how reporting affects future access to formal credit. Each of these corresponds to a belief measured before the video.

Treated participants are then offered an optional check of their own eligibility and borrowing limit, which each completes on their own handset. The check addresses a barrier the video cannot reach. A person may understand the terms perfectly and still not borrow because they do not know whether the product is open to them, or how to find out. Because the limit is set automatically from a person's transaction history, no general message can convey it. Only checking the participant's own account can reveal it.

Treated participants also receive a wallet-sized card at the end of the interview, once the questionnaire is complete. It restates the same terms in print: the minimum and maximum loan amounts, the fee at each repayment term with a worked example, and the two steps needed to check eligibility. The card stays with the participant, so the information remains available whenever they want to check it while considering a loan.

The control group watches a placebo video on the everyday role of mobile money in Mozambique. It names no product, gives no price, and never mentions credit or Txuna. It states in general terms that different operators and services carry different menus, costs, and conditions, which is the only reference to cost anywhere in it. The placebo holds constant the interruption of the working day, the presence of a video, the tablet, the enumerator's silence during playback, and the video's position in the interview, so the comparison turns on the message content rather than on having been given attention.

The control group receives no check, no card, and no product information during the interview or afterward while borrowing behavior is measured. Once the administrative outcome window has closed, they receive the correct terms and the same card.

2026-08-17

2026-09-30

Beliefs about the terms of Txuna, measured in the same visit immediately after the intervention. Accuracy of posterior beliefs relative to the true contract terms, reported separately for the items asked identically before and after the intervention at the amounts used in the video, and for the transfer item asked at a loan amount never shown in the video.

Txuna take-up. Any Txuna loan taken within 30 days and within 90 days of the interview, measured in M-Pesa administrative records for participants who consent to data linkage.

Belief questions take one of two forms, according to what they ask.

For each quantitative term (e.g., service fees), we record an open numeric estimate, in meticais or in days as the item requires, with no response options read out. Monetary items are in meticais. For items where a respondent could plausibly guess, we also record certainty by asking them to place ten beans on a 0-10 scale so we can distinguish a confident wrong answer from an admitted guess.

Items about the likelihood of alternative scenarios (e.g., consequences of not repaying on time) use a trained 0-10 scale, practiced with the respondent before the belief modules begin, and we store the comprehension flags.

In both forms, we record "does not know" and "does not want to answer" as separate indicators, never as scale midpoints.
Accuracy is how close the reported estimate lies to the true contract term. We compare accuracy in two ways. The first covers the items asked identically before and after the video, at the amounts the video uses, and assesses whether the respondent updated toward the signal. The second covers the item asked at 2,000 MT at the seven-day term, a combination the video never shows, and speaks to whether the respondent learned the pricing rule rather than a number. The pre-analysis plan sets out whether we report them item by item, as summary indices, or both, and the standardization and weighting behind any index, before we look at the outcome data. We report the bean measure alongside accuracy rather than folding it into a single number.
Take-up is a binary indicator of at least one Txuna loan in the administrative records within the stated window. Both administrative primary outcomes depend on M-Pesa transferring records under the data processing agreement, which is being finalized at the time of filing. If the transfer does not take place, or takes place only in part, we will report the survey primary outcome and state plainly that we could not construct the administrative primary outcome. We will not substitute a self-reported measure of borrowing for the administrative one.

We do not predict the direction of the effect on take-up. Correcting a belief that overstates the cost of borrowing or that wrongly rules out eligibility should raise take-up, and correcting a belief that understates the cost or omits the automatic deduction and the Credit Registry consequence should lower it. Both directions are informative, and we pre-specify the test of a difference in either direction rather than a one-sided prediction.

Measured in the interview, immediately after the video.
- Open-ended recall of what happens to the debt after the deadline, of what happens to money entering the wallet while a debt is unpaid, and of the consequences of non-payment.
- Description of the steps needed to check one's own eligibility or limit, and the reported chance of completing that check alone.
- Recognition of the consequences of non-payment from a closed list read after all open-ended items.
- Stated chance of checking one's own eligibility or limit within 7 days.
- Stated chance of trying to take a Txuna loan within 30 days, the intended amount, the intended repayment term, the stated chance of repaying by the chosen deadline, the expected source of repayment, and the purpose of the loan.
- Identifying the cheaper of two credit offers, and the choice between an informal moneylender and a hypothetical digital credit product across three scenarios.
- Reported reasons for not taking a Txuna loan now, and the stated chance of receiving money on another account while holding an unpaid Txuna debt.
- For the treatment group only, acceptance of the assisted eligibility check and its outcome as reported by the participant. This is a descriptive measure of offer take-up within the treatment arm, not a comparison across arms.

Measured in M-Pesa administrative records for consenting participants.
- Whether the participant checks their Txuna eligibility or limit, if the provider records this action.
- Repayment behavior conditional on borrowing, the chosen repayment term, arrears, and time spent in unpaid-debt status.
- Incoming transfers, wallet activity, and shifts of inflows away from the M-Pesa account while indebted, which is the avoidance response implied by the automatic deduction.

We measure all interview outcomes in the same visit as the intervention. We do not conduct a follow-up survey, so we do not measure belief persistence directly and infer it only from behavior in the administrative records. The enumerator codes open-ended items against closed lists they never read aloud, coding each true consequence and each false belief separately: that the debt keeps growing and that non-payment leads to arrest. Items about likelihood use the same trained 0-10 scale as the primary belief items, and quantitative items use the same open numeric format. We summarize scenario choices as the share of scenarios in which the respondent chooses the digital credit product, overall and by scenario, and we randomize the reading order of the two options at the respondent level. We construct administrative outcomes from M-Pesa transaction and digital credit records, linked with participant consent, over 30, 90, and 180-day windows after the interview date. The administrative secondary outcomes share the same dependency as the administrative primary outcomes, so if M-Pesa does not transfer the records, we report the interview outcomes and note it.

One-visit survey experiment with micro-entrepreneurs trading in Maputo markets. We sample markets first, then respondents within markets, and randomize treatment at the respondent level.

We drew fourteen markets from the official municipal register of Maputo markets, Resolution number 94/AM/2008 of the Maputo Municipal Assembly approving the Markets and Fairs By-law. Markets serve as sampling units only. Both arms are present in every market, so markets are sampling clusters and not treatment units, and all specifications include market fixed effects. We allocate interviews across markets in proportion to market size rather than equally.

Within each market, enumerators approach respondents by a fixed protocol with office-drawn starting points that leaves no selection to the enumerator, and they substitute neither refusals nor ineligible respondents. Eligibility requires being 21 years of age or older, owning or being self-employed in a business operating in the market, and holding an active M-Pesa account registered in the respondent's own name with the handset present at the interview.

After consent, and after we collect all baseline covariates and prior beliefs, the survey software assigns treatment at the individual level with probability one-half. The respondent then watches the video assigned to their arm. We measure all survey outcomes in the same visit, with no follow-up survey. For participants who consent to data linkage, we add M-Pesa administrative records from 30, 90, and 180 days after the interview date.

Not available

Market selection. Done by computer in the office, in Stata, before fieldwork began, with fourteen markets as a pre-specified target rather than a number derived from the frame. We drew the fourteen from a frame of 27 units, built from the official municipal register of Maputo markets, as set out in Resolution number 94/AM/2008 of the Maputo Municipal Assembly approving the Markets and Fairs By-law.
The frame is cross-classified on two dimensions. The first is the municipal district, namely KaMpfumo, Nlhamankulu, KaMaxakeni, KaMavota, and KaMubukwana, the five mainland districts of Maputo City. The second is the market category in the by-law, namely Class A, Class B, and Class C for formal markets, and a fourth category for informal markets. Together the two dimensions define 13 non-empty cells across the 27 units.

District is the explicit stratum. We allocated the fourteen markets across districts in proportion to the number of frame units in each, by largest remainders with a floor of one market per district, giving three to KaMpfumo, three to Nlhamankulu, two to KaMaxakeni, two to KaMavota, and four to KaMubukwana. Category is the implicit stratum. We sorted each district's units by category before a systematic selection with a random start, so the draw spreads across categories within district in proportion to their frequency in that district. Each unit has a known, non-zero inclusion probability equal to its district allocation divided by its district frame size, and carries the corresponding design weight. We fixed the seeds before running the draw, with a master seed and one derived seed per district, so the draw is reproducible from the do-file.

Respondent selection within market. No list of traders exists from which to draw a sample, so selection is systematic rather than a lottery. Enumerators follow a fixed traversal route from a pre-defined starting position, taking every fifth stall, which removes enumerator discretion, with a birthday rule to choose among eligible people at the same stall.

Treatment assignment. Done by the survey software, SurveyCTO, on the enumerator's tablet during the interview. A stored once(random()) call draws a uniform number once per respondent, only after consent and after every pre-treatment module is complete, and maps it to treatment with probability 0.5. The form retains the assignment timestamp. Enumerators cannot anticipate the arm while selecting, screening, or consenting a respondent, and they cannot redraw it. Treatment assignment is not stratified.

Individual respondent, single-level randomization. The survey form assigns treatment to each respondent separately, so both arms are present in every market and in every enumerator's caseload. Markets are sampling units, not treatment assignments, and the same holds for stalls and enumerator-days.

No

Treatment is randomized at the individual level, so there are no randomization clusters. The sample is drawn in 14 market clusters, with both arms present in each.

1,400 individuals aged 21 or older, owning or self-employed in a business in the market, and holding an active M-Pesa account registered in their own name. Interviews are allocated across the 14 markets in proportion to measured market size rather than equally.

700 individuals in the control group and 700 individuals in the treatment group. Assignment is an independent draw with probability one-half per respondent, so realized arm sizes will deviate slightly from equality.

With 1,400 individuals split equally, 80 percent power, and a 5 percent two-sided test, the minimum detectable effect for standardized survey outcomes is 0.15 standard deviations without covariates, and about 0.12 standard deviations for posterior beliefs controlling for the prior of the same item, assuming the prior explains 35 percent of posterior variance. For administrative take-up, assuming a 10 percent control group take-up rate over 90 days, the minimum detectable effect is 4.5 percentage points. At a 20 percent control rate, it is 6.0 percentage points. Because treatment is randomized within market, clustering at the market level does not inflate the standard error of the treatment coefficient once market fixed effects are included, so these calculations require no design effect correction for the treatment contrast. The 14-market design does limit precision for descriptive and weighted population statements, which use the market design weights and are reported with market-clustered standard errors. Market fixed effects are not credited in the calculations above. Detailed power calculations are reported in the pre-analysis plan. The administrative minimum detectable effects apply to the subsample consenting to data linkage. If consent falls materially below the full sample, the realized detectable effect rises in proportion, and we will report the achieved figure rather than the planned one.