# Week 8 lab: access, use, retention, and incidence

## Learning objectives

Distinguish randomized access from selected use; reconstruct a paired access ITT and its assignment-based uncertainty; separate the fixed-outcome sharp-null reference from the instructor truth audit; and propose an incidence ledger that follows initial workers through exit.

**Executed mode: original synthetic design reconstruction; not empirical replication.** All numbers and people are invented. The marker is `SYNTHETIC_TEACHING_CONSTRUCTION_NOT_PUBLISHED_REPLICATION`. The scientific anchor is Adhvaryu, Gade, Molina, and Nyshadham (2026), *Sotto Voce: The Impacts of Technology to Enhance Worker Voice*. Its low reported use and access effects motivate an option-value interpretation; the toy neither reproduces its findings nor identifies its effects on nonusers.

## Bridge: keeping workers and improving jobs

A channel can make recourse available before anyone uses it. Use also depends on grievance severity, expected remedies and perceived costs. A negative users-versus-nonusers association can coexist with beneficial access. Similarly, lower quits can reflect better conditions, fewer offers, inaccurate beliefs or costly exit. Keep retention, job conditions, earnings and employer savings separate.

This lab follows **Reproduce → Diagnose → Transfer**. Read the [README](README.md), then run:

```bash
ENV_NAME=research bash smoke.sh
```

For experimentation, use a new directory rather than this lab root:

```bash
conda run -n research python src/offline_lab.py --output /tmp/org8-week8-student-run --seed 88771
```

Existing populated targets are refused with exit code 2 and unchanged files. The README explains staged regeneration without erasing authored work.

## Field Core — Reproduce the access design

### 1. Draw a timeline before estimating

The generator freezes 20 workers' potential outcomes, then uses a separate random stream for treatment. Ten baseline pairs are independent assignment units. One member in each pair receives access, giving $2^{10}=1,024$ equally likely allocations. Matching on latent grievance category is part of this invented world, not a feasible claim about the source experiment.

Read `data/teaching/observed_workers.csv` and `teaching-schema.csv`. The key is `worker_id`; `pair_id` defines assignment. `access_assigned` is treatment. `recorded_use` follows assignment and is endogenous. Two distinct endpoints are `followup_condition_score` and `retained_at_horizon`. The score is observed for all initial workers, including leavers, by construction. The extra `score_if_only_stayers_observed` deliberately shows selected observation and is blank after exit. Do not replace its blanks by zero or use it as the main endpoint.

The core DGP assumes no interpersonal interference. A shared HR queue or remedy could violate that assumption in an actual intervention. Scores are arbitrary condition units, not clinical scores or monetized welfare. The main sample remains all 20 baseline workers; entrants would require a separate cohort ledger.

### 2. Reconstruct the paired estimate

For each pair, subtract the control worker's endpoint from the assigned worker's endpoint. With ten differences $d_p$, report

$$
\widehat\tau=\frac{1}{10}\sum_{p=1}^{10}d_p,\qquad
\widehat V=\frac{s_d^2}{10},\qquad
\widehat{SE}=\sqrt{\widehat V}.
$$

These are follow-up endpoint levels; the baseline score documents the population and is not silently subtracted. The usual pair variance estimator is conservative **in expectation** when pair-average effects vary. A realized estimate need not be an upper bound, and these standard errors do not define exact Fisher confidence intervals or identify individual treatment-effect heterogeneity.

Compare your calculations with `output/reproduced/access_itt.csv`:

| Endpoint | Default-seed observed ITT | Pair SE | Two-sided sharp-null p |
|---|---:|---:|---:|
| Condition score, all initial workers | 0.595608433 | 0.543138054 | 310/1,024 = 0.302734375 |
| Retention probability at fixed horizon | 0.100000000 | 0.276887462 | 1.000000000 |

The retention estimate is a 10-percentage-point difference. It is not a ten-percent relative change. Imprecision does not invalidate the synthetic run; significance is never an acceptance criterion.

### 3. Keep two enumerations separate

`output/reproduced/sharp_null_reference.csv` holds each observed endpoint fixed while assigning access in every legal way. Count statistics with absolute value at least as large as the realized statistic, including ties. This is the global sharp null of no access effect on that endpoint for any worker. It is not a weak null about the average, a use-effect test or an option-value test allowing arbitrary use effects. Enumeration supplies 1,024 assignments, not 1,024 independent experimental units.

Only after estimating from learner data should the instructor open `data/instructor/`. Its second enumeration recomputes outcomes from both potential schedules. The mean score estimate is .76; the mean retention estimate is .15. This checks unbiasedness over assignment. The oracle variance uses unavailable real-world counterfactuals and cannot be reported as an empirical standard error. No latent type or potential outcome belongs in a learner regression.

## Research Lab — Diagnose access, use, and incidence

### 4. Explain three different quantities

Four of 20 workers are possible users, concentrated in two matched pairs with worse baseline conditions. One-sided use means nobody uses without access. Exactly two of the ten access recipients use in every assignment, so the use first stage is .2. Every worker's access score receives .6 directly; use adds another .8 for possible users.

The known population access effect is $.6+.2\times.8=.76$. Its Wald ratio is $.76/.2=3.8=.8+.6/.2$. The .8 controlled-use effect is an instructor parameter, **not separately identified by the access randomization**. Exclusion fails even with one-sided compliance and a strong first stage. This is not a weak-instrument example.

Use `output/diagnose/access_use_diagnostic.csv` to distinguish the realized Wald ratio, about 2.978042167, from the population ratio 3.8. The observed users-minus-nonusers score difference is about −17.693979085: a selected association, not evidence that using the channel causes worse conditions. An effect among observed nonusers would also condition on post-treatment behavior. The toy's direct benefit for latent never-users is known only from its specified truth.

Read `access_option_curve.csv`. Holding .6 and .8 fixed while changing possible-user share makes the invalid Wald ratio explode at low take-up. This sensitivity curve is algebra from an invented model, not estimated mediation.

### 5. Audit the measurement arithmetic

| Diagnostic | Required result and interpretation |
|---|---|
| Hourly wage and hours | $20\times40=800$ versus $21\times35=735$: hourly pay +5%, earnings −8.125% |
| Amenity heterogeneity | WTP $(0,0,0,8)$: mean 2, median 0, acceptance share .25 at cost 1; mean WTP is not everyone's WTP |
| Exact compensation ratio | With log utility, $\exp(-.2)$ differs from the linear ratio approximation .8 |
| Equal quits | At wage 20, both offer environments have quit probability .02, but local wage elasticities are −1.8 and −1.0 |
| Posted-wage benchmark | With marginal product 30, supply elasticities 2 and 5 yield wages 20 and 25 only under the stated model |
| Stationary stock | Separation elasticity −1 with hiring elasticities .5 and 2 gives stock elasticities 1.5 and 3 |
| Own versus peer raise | An isolated 10% raise gives about −.00953; a common own/peer raise about −.00191, in quit-probability units |
| Composition | $(10,10,20,20)$ to $(20,20)$ raises the stayer mean 15→20 and lowers the bill 60→40 with no individual raise |
| Reporting | Incidents 100→80 and reporting .1→.5 create complaint records 10→40 |
| Compression | $(30,50)$ to $(30,40)$ halves the gap while lowering mean pay 40→35 |
| Transfer | Fixed output 100, wages 60→70 and profit 40→30 create no new joint resources |
| Survey response | Baseline $(10,20,30,40)$ with everyone's score +2 gives true gain 2; observing only the last two yields selected comparison 12 |

The CSVs in `output/diagnose/` and `analytical-examples.json` expose these calculations. The quit example assumes voluntary quits, fixed amenities, exogenous offer arrival and logistic offer values with scale 10. Equal quit levels do not identify a quit elasticity or employer power. Mapping a quit response into labor supply additionally requires hiring, separation, horizon, composition and equilibrium assumptions; do not mechanically negate or double it.

The relative-pay example is a local probability approximation with $b=.02,c=.08$, a 10% wage change measured as $\log(1.1)$, and a fixed outside environment. The posted-wage first-order condition requires an interior optimum, differentiable labor supply and constant marginal product, with other adjustment margins absent. None of these examples is a published estimate.

## Transfer: a two-page proposal and four-party ledger

Use the [transfer memo template](transfer-memo-template.md). Choose one pay rule, wage-information intervention or voice-service feature. Specify its treatment, counterfactual, announcement and implementation dates, eligibility, assignment/dependence unit, follow-up horizon and potential spillovers. Describe two competing explanations of retention and one outcome that could distinguish them.

Include firm outcomes, **all initial workers**, entrants, and destinations of workers who leave. Leavers are a post-treatment subset of the initial cohort, not a fourth group to add again to totals. Track pay, hours, earnings, conditions and resource costs separately. Mark observed, elicited, model-dependent and missing quantities; do not invent destination wages or treat missing total earnings as zero.

Include an independent conditions or worker-welfare endpoint, response/observation rates by assignment, outside-destination coverage and an uncertainty plan at the actual assignment unit. Separate access, awareness, use, response and remedy. A truly anonymous service may preclude person-level linkage; do not reconstruct identities or promise mediation from unavailable links. State what the proposed design cannot identify about use, welfare or employer power.

## Methods Box: evidence sufficient for a claim

Keep the baseline roster fixed for the main ITT. Selected stayer means and user associations do not inherit randomized assignment. A missingness model or bounding argument requires its own assumptions; monotone retention in this toy does not establish monotone survey response or general validity of selection bounds. Follow movers when feasible and report who remains unobserved.

A valid use-IV would require exclusion in addition to assignment and compliance assumptions. The deliberate direct-access channel violates it here. Exact Fisher testing uses the actual within-pair support and a global sharp null; asymptotic pair uncertainty and oracle truth answer different questions. Shared HR resources may require assigning and analyzing a higher-level unit.

## Reading ladder

Read the chapter's three required papers for different measurement objects: Mas–Pallais (2017), job-attribute valuations in recruitment; Jäger, Roth, Roussille, and Schoefer (2024), outside-pay beliefs, benchmarks and information; Adhvaryu, Gade, Molina, and Nyshadham (2026), voice access. Then use Dube–Giuliano–Leonard (2019) for own/peer pay comparisons. The chapter provides canonical linked references and data-access descriptions. These are intellectual anchors; no paper's empirical estimates are reproduced here.

## Exercises and submission

1. Reconstruct both paired ITTs, SEs and sharp-null p values using only learner outcomes and the permitted assignment rule.
2. Explain why the default realized ITT differs from .76, and why .76 differs from the .8 controlled-use parameter.
3. Compare all-cohort and stayer-only condition observation. State the missingness restriction you would need before generalizing from stayers.
4. Reproduce two measurement diagnostics and describe an alternative explanation a single outcome would miss.
5. Submit the two-page proposal and incidence ledger, the run log, one result table and a short source/mode statement.

## Reproducibility and slide companion

`src/offline_lab.py` freezes the population, enumerates assignment, estimates endpoints, runs the original 65 assertions and exports an explicit inventory. `src/install-generated.py` stages fresh outputs; `src/smoke-checks.py` compiles and reruns real code, independently checks saved results and verifies unchanged-file refusal. `validation.json` and `output/smoke-checks.json` record different checks. The full lab is offline; optional original empirical replication was not attempted.

The Week 8 chapter and slide deck provide the two original figures generated from `access_option_curve.csv` and `quit_curves.csv`. Compare their units and assumptions with the raw tables. Neither figure reproduces an article figure.