# Pre-Analysis Plan: [Study title]

> Pre-analysis plan (PAP) for an economics or finance study: a field
> experiment, a lab or online experiment, a natural experiment, or an
> analysis of proprietary data that the team has not yet opened. It
> fixes the hypotheses, the sample, the outcomes, the estimating
> equations, the multiple-testing correction and the exclusion rules
> before anyone sees outcome data, and it keeps a log of every later
> deviation. The fields follow the registration form of the AEA RCT
> Registry (as checked 2026-10-25) and the OSF Registries workflow, and
> the plan can also serve as the Stage 1 protocol of a registered
> report. Replace every `[bracketed]` value and every row marked
> *Example*. This is a document format, not legal, ethics-review,
> financial or investment advice. Obtain the journal policy, registry
> rules and ethics regulations for the normative text.

<!--
Guidance: How to use this template
- Write the plan before outcome data exist or before the team can see
  them. Register it, or upload it to a registry entry, and record the
  timestamp in section 12. A plan written after looking at outcomes is
  not a pre-analysis plan.
- Be specific where it matters and brief where it does not. Fix the
  primary outcomes, the primary specification and the correction for
  multiple testing. Leave room for exploratory work, but label it.
- Every number in the power section must be reproducible from the
  stated inputs. Keep the power script in the replication package.
- When something changes, do not edit the registered plan. Add a row
  to the deviations log (section 13) and explain it in the paper.
- The worked example is a fictional household-finance field
  experiment run with "Fernhollow Bank", a fictional bank. It is not a
  real study and its numbers are illustrative only.
- Related documents: Preregistration (`science/preregistration`, the
  OSF psychology-style form), Empirical Finance Paper
  (`academic/empirical-finance-paper`), Event Study
  (`academic/event-study`), Replication Package README
  (`academic/replication-package-readme`), Data Management Plan
  (`science/data-management-plan`), DPIA (`compliance/dpia`) and
  Reproducibility Checklist (`science/reproducibility-checklist`).
-->

## Document control

<!-- Guidance: Identify the study, the registry entry and the people who sign off. Version 1.0 is the version registered before outcome data; anything later is an amendment and goes to the deviations log. -->

| Field | Value |
|---|---|
| Document ID | [PAP-001] |
| Study title | [Study title] |
| Registry and ID | [AEA RCT Registry AEARCTR-NNNNNNN / OSF DOI 10.17605/OSF.IO/XXXXX] |
| Registration timestamp | [YYYY-MM-DD HH:MM UTC] |
| Study type | [Field experiment / Lab experiment / Online experiment / Natural experiment / Proprietary-data analysis] |
| Principal investigators | [@pi-1], [@pi-2] |
| Implementing partner | [Partner organisation] |
| Ethics approval | [IRB or ethics committee name, approval number, date] |
| Version | [1.0] |
| Status | [Draft / Registered / Amended / Closed] |
| Owner | [@pi-1] |
| Approvers/reviewers | [@co-authors], [@partner-research-lead], [@data-protection-officer] |
| Last updated | YYYY-MM-DD |
| Classification | [Public after registration / Embargoed until YYYY-MM-DD] |
| Related documents | [Ethics protocol], [Data management plan], [Partner agreement], [Power script] |

### Approvals

| Role | Name | Decision | Date |
|---|---|---|---|
| Principal investigator | [@pi-1] | [Approved] | YYYY-MM-DD |
| Co-investigator | [@pi-2] | [Approved] | YYYY-MM-DD |
| Partner research lead | [@partner-research-lead] | [Approved] | YYYY-MM-DD |

### Revision history

| Version | Date | Author | Change |
|---|---|---|---|
| 0.1 | YYYY-MM-DD | [@pi-1] | First draft for co-author review |
| 1.0 | YYYY-MM-DD | [@pi-1] | Registered before randomisation and intervention start; baseline extract frozen, outcome data not yet collected |

## Contents

- [1. Study registration and identifiers](#1-study-registration-and-identifiers)
- [2. Background, research questions and hypotheses](#2-background-research-questions-and-hypotheses)
- [3. Study design and setting](#3-study-design-and-setting)
- [4. Sample, randomisation and power](#4-sample-randomisation-and-power)
- [5. Outcomes and measurement](#5-outcomes-and-measurement)
- [6. Estimation strategy](#6-estimation-strategy)
- [7. Multiple hypothesis testing](#7-multiple-hypothesis-testing)
- [8. Heterogeneity and mechanisms](#8-heterogeneity-and-mechanisms)
- [9. Data collection, cleaning and exclusions](#9-data-collection-cleaning-and-exclusions)
- [10. Threats to validity and contingency rules](#10-threats-to-validity-and-contingency-rules)
- [11. Ethics, data protection and disclosure](#11-ethics-data-protection-and-disclosure)
- [12. Timeline and registration record](#12-timeline-and-registration-record)
- [13. Deviations log and reporting commitments](#13-deviations-log-and-reporting-commitments)
- [14. Variant for natural experiments and proprietary data](#14-variant-for-natural-experiments-and-proprietary-data)
- [15. Glossary and references](#15-glossary-and-references)
- [Standard and licence note](#standard-and-licence-note)

## 1. Study registration and identifiers

<!-- Guidance: Choose the registry before writing. Field experiments submitted to AEA journals must be registered in the AEA RCT Registry before submission; check the journal policy for your target outlet. Pitfall: registering after the intervention starts, which removes the "pre-registered" status the registry shows. -->

Register the study in a public registry and attach this plan. The choice depends on the study type and on the journals you will target.

| Registry | Typical use | What it gives you | Notes |
|---|---|---|---|
| AEA RCT Registry (socialscienceregistry.org) | Randomised trials in economics and finance | Registry ID (AEARCTR-), public trial page, optional uploaded documents | AEA journal policy requires field experiments to be registered before submission; a trial registered before its intervention start date is flagged as pre-registered (checked 2026-10-25) |
| OSF Registries | Any design, including lab, online and observational studies | Frozen registration with a DOI once public; embargo up to four years | Registrations cannot be edited after submission; changes go through an update or a new registration (checked 2026-10-25) |
| EGAP Registry (hosted on OSF) | Governance and political economy experiments | OSF registration under the EGAP collection | Requires an OSF account |
| AsPredicted (also offered as an OSF form) | Short pre-registrations for lab and online studies | Short fixed questionnaire | Better as a supplement than as a full PAP |
| RIDIE (3ie) | Development impact evaluations | Registry record | Check that the registry is still accepting entries |

Fill the registry form from this plan, so the two never disagree.

| Registry field *(Example)* | Value |
|---|---|
| Trial title | Round-up savings defaults and payday reminders at Fernhollow Bank *(Example)* |
| Country | [Country] |
| Status | In development |
| Keywords | household finance; savings; defaults; reminders *(Example)* |
| Trial start / intervention start / intervention end / trial end | 2027-01-04 / 2027-02-01 / 2027-07-31 / 2027-12-31 *(Example)* |
| Primary outcomes | Emergency savings balance at month 6; any overdraft in months 1 to 6 *(Example)* |
| Clustered treatment | Yes, payroll-employer groups *(Example)* |
| Planned clusters / observations | 200 clusters / 4,000 customers *(Example)* |
| IRB | [Committee], [approval number], YYYY-MM-DD |

## 2. Background, research questions and hypotheses

<!-- Guidance: State the question in one sentence and say why the answer matters for theory or policy. Split hypotheses into primary (the claims the paper stands on) and secondary. Write the sign of the expected effect. Pitfall: listing twenty "primary" hypotheses, which makes the multiple-testing correction meaningless. -->

### 2.1 Motivation

[Two or three paragraphs: the economic question, what existing
evidence shows, the gap this study fills and why the setting is well suited. Cite the closest papers by author and year.]

### 2.2 Research questions

| ID | Research question |
|---|---|
| RQ-01 *(Example)* | Does an opt-out round-up savings feature raise liquid savings among salaried bank customers? |
| RQ-02 *(Example)* | Do payday reminders add to the effect of the default, or substitute for it? |

### 2.3 Hypotheses

| ID | Type | Hypothesis | Expected sign | Outcome family |
|---|---|---|---|---|
| H-01 *(Example)* | Primary | The round-up default raises the emergency savings balance at month 6 | Positive | F1 Savings |
| H-02 *(Example)* | Primary | The round-up default lowers the probability of any overdraft in months 1 to 6 | Negative | F2 Financial distress |
| H-03 *(Example)* | Secondary | Payday reminders raise savings without the default | Positive | F1 Savings |
| H-04 *(Example)* | Secondary | The two treatments are complements (interaction > 0) | Positive | F1 Savings |
| H-05 *(Example)* | Secondary | The default does not raise high-cost borrowing elsewhere (offsetting) | Null or negative | F2 Financial distress |

State which test is one-sided, if any, and why. Two-sided tests are the default in economics and finance journals; justify any exception here, before data exist.

### 2.4 Theory and predictions

[Explain the mechanism you expect (inertia, attention, mental
accounting, liquidity constraints) and the prediction each mechanism makes for the secondary outcomes. A table that maps mechanism to prediction makes later interpretation honest: if the data contradict a mechanism, you said so in advance.]

## 3. Study design and setting

<!-- Guidance: Describe the setting so a referee can judge external validity, and the treatment arms so a replicator could run them again. Pitfall: leaving the control condition vague; "business as usual" must be described too. -->

### 3.1 Setting and partner

[Describe the population, the partner institution, the product and the
period. Say what the partner already does for all customers, and what the partner may change during the study (pricing, marketing) that could interfere.]

### 3.2 Treatment arms

| Arm | Name | Description | Share of clusters |
|---|---|---|---|
| T0 *(Example)* | Control | Standard current account; savings feature available on request only | 25% |
| T1 *(Example)* | Default | Round-up to the nearest EUR 1 switched on by default; one-click opt-out | 25% |
| T2 *(Example)* | Reminder | Text message on payday suggesting a transfer to savings | 25% |
| T3 *(Example)* | Default plus reminder | T1 and T2 together | 25% |

The shares sum to 100%. The 2 x 2 factorial design lets you estimate each main effect and the interaction (H-04). State whether you will pool arms for the main effects; pooling raises power for H-01 but assumes no interaction.

### 3.3 Design diagram

The diagram shows the flow from the sampling frame to the endline data for the example design.

```mermaid
flowchart LR
  A[Eligible customers<br/>N = 4,000 in 200 clusters] --> B[Baseline data<br/>from bank records]
  B --> C{Stratified cluster<br/>randomisation}
  C --> T0[T0 Control<br/>50 clusters]
  C --> T1[T1 Default<br/>50 clusters]
  C --> T2[T2 Reminder<br/>50 clusters]
  C --> T3[T3 Default plus reminder<br/>50 clusters]
  T0 & T1 & T2 & T3 --> E[Months 1 to 6<br/>administrative data]
  E --> F[Endline survey<br/>month 7]
```

### 3.4 Unit of randomisation and spillovers

Randomise at the level at which spillovers would occur. In the example, colleagues at the same employer talk about the feature, so the unit is the payroll-employer group, not the customer. State the expected direction of any remaining spillover and how it would bias the estimate (usually towards zero).

## 4. Sample, randomisation and power

<!-- Guidance: Give eligibility rules, the randomisation procedure (with seed and code location), the balance checks and the power calculation. Report the minimum detectable effect (MDE) in outcome units and in standard deviations. Pitfall: computing power for individual randomisation when treatment is clustered. -->

### 4.1 Eligibility and sampling frame

| Rule ID | Criterion | Source | Example value |
|---|---|---|---|
| ELG-001 *(Example)* | Salaried customer with payroll credited to the account for 6 months | Bank records | Yes |
| ELG-002 *(Example)* | Age 18 or over | Bank records | Yes |
| ELG-003 *(Example)* | No existing automatic savings rule | Bank records | Yes |
| ELG-004 *(Example)* | Employer group with at least 10 eligible customers | Bank records | Yes |

### 4.2 Randomisation procedure

- **Method**: stratified cluster randomisation, implemented in
  [software and version] by [@pi-2], with the seed [seed] stored in
  [repository path].
- **Strata**: [region x baseline savings tercile], giving [N] strata.
- **Assignment within strata**: equal shares across the four arms;
  remainders allocated at random.
- **Timing**: after baseline data are frozen, before any outreach.
- **Balance checks**: compare arms on [list baseline covariates];
  report a joint F-test. Do not re-randomise on imbalance unless the
  rule is written here in advance (for example, re-draw when the joint
  p-value is below 0.05, with all draws logged).

### 4.3 Power and minimum detectable effect

For a two-arm comparison with share $P$ treated, $N$ units, outcome standard deviation $\sigma$, two-sided size $\alpha$ and power $1-\kappa$, the MDE under individual randomisation is

$$
MDE = \left(z_{1-\alpha/2} + z_{1-\kappa}\right)\sqrt{\frac{1}{P(1-P)}}\sqrt{\frac{\sigma^2}{N}}
$$

With clusters of size $m$ and intra-cluster correlation $\rho$, multiply by the square root of the design effect:

$$
DE = 1 + (m-1)\rho
$$

Controlling for a baseline covariate that explains a share $R^2$ of outcome variance multiplies the MDE by $\sqrt{1-R^2}$.

| Input *(Example)* | Value | Source |
|---|---|---|
| Comparison | Pooled default arms (T1+T3) vs pooled non-default arms (T0+T2) | Design |
| $N$ | 4,000 customers | Partner records |
| $P$ | 0.5 | Design |
| $\alpha$ (two-sided) | 0.05, so $z = 1.960$ | Convention |
| Power | 0.80, so $z = 0.842$ | Convention |
| Cluster size $m$ / clusters | 20 / 200 | Partner records |
| ICC $\rho$ | 0.05 | Pilot data |
| Outcome for H-02 | Any overdraft, baseline rate 30%, so $\sigma = \sqrt{0.3 \times 0.7} = 0.458$ | Bank records |
| $R^2$ from baseline overdraft | 0.30 | Pilot data |

| Step *(Example)* | Result |
|---|---|
| Multiplier $1.960 + 0.842$ | 2.802 |
| MDE in SD units, individual randomisation: $2.802 \times 2 \times \sqrt{1/4000}$ | 0.0886 SD |
| Design effect $1 + 19 \times 0.05$ | 1.95, square root 1.396 |
| MDE in SD units, clustered | 0.1237 SD |
| MDE for overdraft (x 0.458) | 5.7 percentage points |
| MDE with baseline control (x $\sqrt{0.70}$ = 0.837) | 4.7 percentage points |

Interaction tests (H-04) have much less power than main effects: in a balanced 2x2 design the standard error of the interaction coefficient is about twice that of a pooled main effect, so detecting an interaction of the same size needs roughly four times the sample. Report the MDE for $\beta_3$ separately (*Example:* about 2 x 0.1237 = 0.25 SD of OUT-001 before any baseline control, against 0.12 SD for the pooled main effect) and treat H-04 as secondary.

Judge whether the MDE is economically meaningful. If the smallest effect worth knowing about is 3 percentage points, the study is underpowered for H-02 and you should add clusters, not hope. Report power for each primary hypothesis separately and keep the script with the plan.

## 5. Outcomes and measurement

<!-- Guidance: Define every outcome so precisely that two people would code it the same way: source, timing, unit, transformation, winsorisation and treatment of zeros. Group outcomes into families and say which index you will build. Pitfall: deciding how to winsorise after seeing the tails. -->

### 5.1 Outcome definitions

| ID | Family | Outcome | Definition and timing | Source | Transformation |
|---|---|---|---|---|---|
| OUT-001 *(Example)* | F1 Savings | Emergency savings balance | Balance of linked savings account at end of month 6, EUR | Bank records | Inverse hyperbolic sine; winsorised at 99th percentile within arm-pooled sample |
| OUT-002 *(Example)* | F1 Savings | Net transfers to savings | Sum of transfers in less transfers out, months 1 to 6, EUR | Bank records | Winsorised at 1st and 99th percentiles |
| OUT-003 *(Example)* | F2 Distress | Any overdraft | 1 if the current account was overdrawn on any day in months 1 to 6 | Bank records | None |
| OUT-004 *(Example)* | F2 Distress | Overdraft days | Number of overdrawn days, months 1 to 6 | Bank records | None |
| OUT-005 *(Example)* | F2 Distress | Other high-cost credit | Self-reported use of payday or instant credit in the last 3 months | Endline survey | None |
| OUT-006 *(Example)* | F3 Wellbeing | Financial wellbeing score | Mean of [N] survey items on a 5-point scale | Endline survey | Standardised against control mean and SD |

### 5.2 Indices

For each family, build a summary index as the equally weighted mean of the standardised components (each standardised against the control group, signed so that higher is better), following Kling, Liebman and Katz (2007), or the inverse-covariance weighted index of Anderson (2008). Choose one now and name it here: [index method].

### 5.3 Covariates

List the baseline covariates used in the primary specification. Pick them now, on prediction grounds (strong predictors of the outcome), not on balance grounds after the fact.

| ID | Covariate | Source | Use |
|---|---|---|---|
| COV-001 *(Example)* | Baseline value of the outcome | Bank records | All specifications |
| COV-002 *(Example)* | Monthly net salary, EUR | Bank records | All specifications |
| COV-003 *(Example)* | Age band | Bank records | All specifications |
| COV-004 *(Example)* | Strata fixed effects | Design | All specifications |

## 6. Estimation strategy

<!-- Guidance: Write the primary estimating equation, the estimand (intention-to-treat or treatment-on-the-treated), the standard errors and the inference method. Pitfall: leaving the choice of controls, clustering level or sample open, which creates the forking paths the plan exists to close. -->

### 6.1 Estimand

The primary estimand is the intention-to-treat (ITT) effect: the effect of being assigned to an arm, whatever the customer did with it. Report the effect of actually using the feature (treatment on the treated) as secondary, using assignment as an instrument for take-up.

### 6.2 Primary specification

For customer $i$ in cluster $c$ and stratum $s$:

$$
Y_{ics} = \beta_0 + \beta_1 D_c + \beta_2 R_c + \beta_3 (D_c \times R_c) + \gamma Y^{0}_{ics} + X_{ics}'\delta + \mu_s + \varepsilon_{ics}
$$

where $D_c$ is the default assignment, $R_c$ the reminder assignment, $Y^0$ the baseline outcome, $X$ the covariates in section 5.3 and $\mu_s$ strata fixed effects. H-01 and H-02 are tests of $\beta_1 + \beta_3/2$ (the default effect averaged over reminder status), H-03 of $\beta_2$, and H-04 of $\beta_3$. State the exact linear combination for each hypothesis in a table so there is no doubt later.

| Hypothesis | Coefficient or combination | Test |
|---|---|---|
| H-01 *(Example)* | $\beta_1 + \beta_3/2$ on OUT-001 | Two-sided t-test, clustered SE |
| H-02 *(Example)* | $\beta_1 + \beta_3/2$ on OUT-003 | Two-sided t-test, clustered SE |
| H-03 *(Example)* | $\beta_2$ on OUT-001 | Two-sided t-test, clustered SE |
| H-04 *(Example)* | $\beta_3$ on OUT-001 | Two-sided t-test, clustered SE |

### 6.3 Standard errors and inference

- Cluster standard errors at the unit of randomisation (the employer
  group). With fewer than about 50 clusters per comparison, add
  randomisation inference or a wild cluster bootstrap and state which
  one is primary.
- Report point estimates, confidence intervals and the control mean
  for every outcome, not only p-values.
- Use linear probability models for binary outcomes in the primary
  specification; report logit or probit as robustness only.

### 6.4 Robustness specifications

List them now so they are not chosen for their results: no covariates; alternative winsorisation levels; levels instead of transformed outcomes; excluding the first month; dropping one region at a time.

## 7. Multiple hypothesis testing

<!-- Guidance: Decide which tests share a correction and which method you use. Economics practice is to correct within outcome families and to report both unadjusted and adjusted values. Pitfall: correcting across everything, which hides real effects, or across nothing, which overstates them. -->

### 7.1 Families and method

| Family | Hypotheses and outcomes | Method | Error rate controlled |
|---|---|---|---|
| Primary *(Example)* | H-01 on OUT-001, H-02 on OUT-003 | Romano and Wolf (2005) step-down | Family-wise error rate at 0.05 |
| F1 Savings secondary *(Example)* | All F1 outcomes across arms | Sharpened q-values (Anderson 2008) | False discovery rate at 0.05 |
| F2 Distress secondary *(Example)* | All F2 outcomes across arms | Sharpened q-values | False discovery rate at 0.05 |

### 7.2 Worked example of a false discovery rate correction

The Benjamini and Hochberg (1995) procedure orders the $m$ p-values from smallest to largest and rejects every hypothesis up to the largest rank $k$ for which $p_{(k)} \le \alpha k / m$. Sharpened q-values (Anderson 2008), the method chosen in 7.1, are a two-stage refinement of this procedure that first estimates how many null hypotheses are true; they reject at least as many hypotheses as the one-stage version.

The table below is an illustrative family of five outcomes chosen to show the arithmetic; it is not one of the families defined in 7.1, where OUT-001 sits in the primary family.

| Rank $k$ *(Example, illustrative family)* | Outcome | p-value | Threshold $0.05k/5$ | Reject? |
|---|---|---|---|---|
| 1 | OUT-002 | 0.004 | 0.010 | Yes |
| 2 | OUT-001 | 0.019 | 0.020 | Yes |
| 3 | OUT-006 | 0.031 | 0.030 | No |
| 4 | OUT-004 | 0.048 | 0.040 | No |
| 5 | OUT-005 | 0.220 | 0.050 | No |

The largest rank meeting the condition is 2, so the first two hypotheses are rejected. OUT-006 and OUT-004 would each pass at 0.05 on their own; report both the unadjusted and the adjusted result.

## 8. Heterogeneity and mechanisms

<!-- Guidance: Pre-specify the few subgroups you expect to matter, with a reason and a predicted sign. Everything else is exploratory. Pitfall: a long list of splits with no correction, which almost guarantees a "significant" subgroup by chance. -->

| ID | Dimension | Split | Reason and predicted direction |
|---|---|---|---|
| HET-001 *(Example)* | Baseline liquidity | Below vs above median baseline savings | Liquidity-constrained customers save less from the default, but gain more on overdraft |
| HET-002 *(Example)* | Income volatility | Top tercile vs rest of month-to-month salary variation | Reminders matter more when payday timing varies |
| HET-003 *(Example)* | Age | Under 35 vs 35 and over | No strong prior; reported for policy interest |

Estimate heterogeneity with an interaction term in the primary specification. If you also plan machine-learning methods for heterogeneous effects (for example generic machine learning or causal forests), name the method, the sample split and the tuning rule now, and label the results exploratory.

Mechanism tests: [list the outcomes that discriminate between the mechanisms in section 2.4, such as opt-out rates, timing of transfers relative to payday and survey measures of attention].

## 9. Data collection, cleaning and exclusions

<!-- Guidance: Write the rules for missing data, outliers, duplicates and attrition before you see outcomes. Pitfall: dropping "suspicious" observations case by case after looking at results. -->

### 9.1 Data sources and timing

| Source | Content | Frequency | Transfer and storage |
|---|---|---|---|
| Partner administrative data *(Example)* | Balances, transactions, overdraft flags | Monthly extract | Pseudonymised at the partner; secure transfer to [environment] |
| Endline survey *(Example)* | Wellbeing, other credit, attention | Once, month 7 | Survey platform [name]; linked by study ID |

### 9.2 Exclusion and cleaning rules

| Rule ID | Rule | Applied when | Reported where |
|---|---|---|---|
| EXC-001 *(Example)* | Exclude accounts closed by the bank for fraud before intervention start | Before randomisation | Sample flow table |
| EXC-002 *(Example)* | Keep accounts closed by the customer after randomisation; code outcomes as observed up to closure and as zero balance after | Always | Section 6 footnote |
| EXC-003 *(Example)* | Remove exact duplicate transactions (same ID, amount and timestamp) | Data cleaning | Cleaning log |
| EXC-004 *(Example)* | Winsorise continuous outcomes as defined per outcome in 5.1 (99th percentile, or 1st and 99th percentiles for flows that can be negative), using the arm-pooled sample | Analysis | Outcome table |

### 9.3 Attrition

Administrative outcomes should have little attrition; survey outcomes will not. Test whether response rates differ by arm. If the difference exceeds [5] percentage points or is statistically significant, report Lee (2009) bounds for survey outcomes alongside the main estimates.

## 10. Threats to validity and contingency rules

<!-- Guidance: List what could go wrong in implementation and decide now what you will do. Pitfall: a partner change of plan mid-study that nobody anticipated, forcing an unplanned design change. -->

| ID | Threat | Likelihood | Contingency rule decided in advance |
|---|---|---|---|
| THR-001 *(Example)* | Partner launches a bank-wide savings campaign during the study | Medium | Record the date; add a post-campaign indicator; report results with and without months after launch |
| THR-002 *(Example)* | Take-up of the default below 50% in T1 and T3 | Low | Keep ITT as primary; report first stage and TOT |
| THR-003 *(Example)* | Contamination: control customers learn of the feature from treated colleagues | Medium | Cluster design limits it; measure awareness in the survey |
| THR-004 *(Example)* | Survey response below 40% | Medium | Report survey outcomes as secondary with bounds |
| THR-005 *(Example)* | Data extract format changes | Low | Freeze the variable dictionary at baseline; log any mapping change |

## 11. Ethics, data protection and disclosure

<!-- Guidance: Record the ethics approval, the consent approach and the lawful basis for processing, and disclose funding and interests. Pitfall: assuming the partner's customer terms cover research use without checking with the ethics committee and the data protection officer. -->

- **Ethics review**: approved by [committee] on YYYY-MM-DD, reference
  [number]. For US federally funded human-subjects research, the
  Common Rule (45 CFR part 46) applies, including the criteria for IRB
  approval (46.111) and the informed consent requirements (46.116);
  check whether a waiver of consent was approved and on what grounds.
- **Personal data**: where the GDPR applies, document the lawful basis
  and the research safeguards under Article 89(1) (data minimisation
  and pseudonymisation where the purpose allows), and complete a DPIA
  if the processing is likely to be high risk. Use DPIA
  (`compliance/dpia`).
- **Harm review**: explain why no arm is expected to harm participants
  (for example, the default can be switched off in one click and no
  fees apply), and how a participant can opt out of the research.
- **Partner rights**: record what the partner may review before
  publication (factual accuracy and confidentiality only, not
  results), in writing.
- **Funding and interests**: list every funder and any financial or
  advisory relationship with the partner.

| Disclosure | Detail |
|---|---|
| Funding | [Funder, grant number] |
| Partner relationship | [Data-sharing agreement only / paid consulting / none] |
| Publication rights | [Researchers may publish regardless of results] |
| AI tools | [Which tools were used to draft code or text, and how outputs were checked] |

## 12. Timeline and registration record

<!-- Guidance: Show when the plan was registered relative to each data milestone. This table is what proves the plan was written blind. -->

```mermaid
gantt
  title Study timeline (Example)
  dateFormat YYYY-MM-DD
  section Plan
  PAP registered            :milestone, m1, 2027-01-15, 0d
  section Data
  Baseline extract frozen   :b1, 2027-01-04, 14d
  Randomisation             :milestone, m2, 2027-01-20, 0d
  Intervention              :i1, 2027-02-01, 2027-07-31
  Endline survey            :s1, 2027-08-01, 30d
  Outcome data released to team :milestone, m3, 2027-09-15, 0d
  section Analysis
  Primary analysis          :a1, 2027-09-15, 45d
```

| Milestone | Date | Who had access to outcome data |
|---|---|---|
| PAP version 1.0 registered | YYYY-MM-DD | Nobody |
| Baseline data frozen | YYYY-MM-DD | Nobody (baseline only) |
| Randomisation | YYYY-MM-DD | Nobody |
| First outcome extract | YYYY-MM-DD | [Data manager only] |
| Outcome data released to analysts | YYYY-MM-DD | [Analysts] |

## 13. Deviations log and reporting commitments

<!-- Guidance: Log every departure from the plan with date, reason and whether outcome data had been seen. In the paper, report the pre-specified analysis first and label everything else. Pitfall: silently replacing a pre-specified result that "did not work". -->

| ID | Date | Section | Deviation | Reason | Outcome data seen? | Effect on results |
|---|---|---|---|---|---|---|
| DEV-001 *(Example)* | 2027-03-02 | 4.1 | Dropped 6 clusters whose employer moved payroll to another bank | Partner data no longer available | No | Planned clusters 200 to 194; MDE recomputed |
| DEV-002 *(Example)* | 2027-07-20 | 5.1 | OUT-005 survey item reworded in the local-language version before fielding | Translation review | No | None expected |

Reporting commitments:

1. Report every primary hypothesis, whatever the result.
2. Present the pre-specified specification first; place deviations
   and exploratory analyses in clearly labelled sections.
3. Include a "populated PAP" appendix that shows each pre-specified
   test next to its result.
4. Publish the code and the data (or access instructions) with a
   Replication Package README (`academic/replication-package-readme`).

## 14. Variant for natural experiments and proprietary data

<!-- Guidance: Many finance studies are not experiments. A plan still helps when the outcome data are not yet available to you (a new data agreement, a future regulatory change, an upcoming data release). Say exactly what you have and have not seen. Pitfall: claiming a plan is blind when the team has already explored the same data for another paper. -->

When the identifying variation comes from a policy, a regulation or a data release rather than your own randomisation, replace sections 3 and 4 with the following.

| Item | What to write |
|---|---|
| Source of variation | The rule, date and population affected; why assignment is as good as random near the threshold or around the date |
| Data access statement | What data the team has seen, when, and who certified it (for example, the data provider's delivery log) |
| Design | Difference-in-differences, regression discontinuity, event study or instrumental variables; for event studies use Event Study (`academic/event-study`) |
| Identification checks | Pre-trends test, placebo dates, placebo outcomes, McCrary-type density test for discontinuities |
| Estimator choice | Name the estimator now, including staggered-adoption estimators if treatment timing varies |
| Sample period and filters | Exact start and end dates, filters (for example, exclude financials and utilities), minimum data requirements |
| Power or precision | Expected standard error from historical data, translated into an MDE |

## 15. Glossary and references

<!-- Guidance: Define terms once for co-authors and partners who are not economists. Cite method papers by author, year and journal. -->

### 15.1 Glossary

| Term | Meaning in this plan |
|---|---|
| Pre-analysis plan (PAP) | A dated document that fixes hypotheses, outcomes and analysis before outcome data are seen |
| Registered report | A journal track where the plan (Stage 1) is peer reviewed and accepted in principle before results exist |
| ITT | Intention-to-treat: the effect of assignment, regardless of take-up |
| TOT | Treatment-on-the-treated: the effect for those who took up, estimated with assignment as an instrument |
| MDE | Minimum detectable effect: the smallest true effect the design detects with the stated power and size |
| ICC | Intra-cluster correlation: the share of outcome variance that lies between clusters |
| FWER | Family-wise error rate: the probability of at least one false rejection in a family |
| FDR | False discovery rate: the expected share of false rejections among all rejections |
| Strata | Groups within which randomisation is balanced by design |

### 15.2 References

| Reference | Use |
|---|---|
| AEA RCT Registry, socialscienceregistry.org, registration instructions (checked 2026-10-25) | Registry fields and pre-registered flag |
| American Economic Association, RCT registry policy for AEA journals, aeaweb.org (checked 2026-10-25) | Registration before submission for field experiments |
| Center for Open Science, OSF Registries help: create a preregistration (checked 2026-10-25) | Templates, embargo up to four years, DOI on public registrations |
| Journal of Behavioral and Experimental Finance, Registered Reports guidelines (Elsevier PDF, checked 2026-10-25) | Stage 1 content for a finance registered report; confirm on the journal page |
| 45 CFR part 46 (Common Rule), sections 46.111 and 46.116 | Ethics review and consent (US) |
| Regulation (EU) 2016/679 (GDPR), Article 89 | Research safeguards (EU) |
| Bloom, H. S. (1995), Evaluation Review 19(5) | Minimum detectable effects |
| Duflo, E., Glennerster, R. and Kremer, M. (2007), "Using Randomization in Development Economics Research: A Toolkit", Handbook of Development Economics, vol. 4 | Power and design |
| McKenzie, D. (2012), Journal of Development Economics 99(2) | Baseline controls and multiple follow-ups |
| Kling, J., Liebman, J. and Katz, L. (2007), Econometrica 75(1) | Summary indices |
| Anderson, M. (2008), Journal of the American Statistical Association 103(484) | Inverse-covariance index, sharpened q-values |
| Benjamini, Y. and Hochberg, Y. (1995), Journal of the Royal Statistical Society Series B 57(1) | False discovery rate |
| Romano, J. and Wolf, M. (2005), Econometrica 73(4) | Step-down FWER control |
| Lee, D. (2009), Review of Economic Studies 76(3) | Bounds under attrition |
| Casey, K., Glennerster, R. and Miguel, E. (2012), Quarterly Journal of Economics 127(4) | Example of a pre-analysis plan in economics |
| Olken, B. (2015), Journal of Economic Perspectives 29(3) | Benefits and costs of pre-analysis plans |

## Standard and licence note

Based on the public registration fields of the AEA RCT Registry and the American Economic Association registry policy for its journals, the OSF Registries preregistration workflow, the published Registered Reports guidelines of the Journal of Behavioral and Experimental Finance, the US Common Rule (45 CFR part 46, a US federal work) and Regulation (EU) 2016/679, together with the methodological papers listed in section 15.2, which are cited and not reproduced. No registry form text, journal guideline wording or template from another organisation is copied; the OSF forms and the AsPredicted questions are referenced by name only. The study, partner and numbers in the examples are fictional. This template is original text written for this collection and is not affiliated with or endorsed by any registry or journal named. Check the current registry rules, journal policies and ethics regulations before use. Template licence: MIT.