Robustness & Inference (expecon-robustness)

When to trigger

• A referee asks "is the study adequately powered?" and there is no sample-size justification
• You ran several treatments / outcomes and report many p-values without correction
• Inference treats individual decisions as independent when subjects interact in groups
• Results move when you change the exclusion rule, the outcome measure, or pool/unpool sessions

The ExpEcon inference stack

Experimental control buys clean identification; it does not buy clean inference. Five things separate a robust ExpEcon paper from a fragile one.

1. Power / sample-size justification (do this before data, defend it after)

• Pre-specify the minimum detectable effect (MDE) that is economically meaningful and the power to detect it, at the correct unit (session or matching group, not individual decision). A study powered on individual n but analyzed at the group level is overstated.
• Use pilot or prior-literature variances; for interactive games, simulate at the group level. Report the realized power for the primary comparison, not just a post-hoc "we found p<0.05."
• A clean, well-powered null is publishable here — especially as a Registered Report. Do not p-hack a null into significance; defend it with power.

2. The unit-of-observation problem

• Within a matching group, decisions are correlated; the independent unit is the group/session, often giving far fewer effective observations than the raw decision count suggests.
• Use group-level summaries, cluster-robust SEs at the session/matching-group level, mixed models with group random effects, or non-parametric tests on group means (Mann–Whitney / permutation). With few clusters, prefer randomization-inference / permutation tests over asymptotic clustering.

3. Multiple treatments & multiple hypotheses

• If you test several outcomes or several pairwise treatment contrasts, correct for multiplicity (Holm, Romano–Wolf, List–Shaikh–Xu for experiments, or pre-registered families). Distinguish the primary pre-registered comparison (no correction needed if it is the single confirmatory test) from secondary/exploratory ones (correct, and label exploratory).
• Report the pre-registered analysis first, exactly as specified; report deviations and additional analyses separately and labeled.

4. Non-parametric vs. parametric

• Experimental outcomes are often bounded, censored (contributions in [0,20]), or non-normal. Lead with non-parametric tests on the primary comparison; use regression for covariate adjustment and heterogeneity, not to rescue a fragile mean difference.

5. Robustness to design and analysis choices

• Show the effect survives: alternative exclusion rules (comprehension failers in/out), first-half vs. second-half rounds (learning), partner vs. stranger if both run, and a permutation test of the treatment label.
• Report attrition and, in field/online studies, differential attrition (Lee bounds if it threatens balance).

Execution bridge (StatsPAI / Stata MCP)

Run the battery, don't just enumerate it. Full map: execution-with-mcp. Experimental Economics is lab/field experiments; randomization inference, romano_wolf for many treatments/outcomes, and power are decisive — observational tools secondary.

• Many outcomes / specifications: romano_wolf (step-down FWER) or benjamini_hochberg.
• OVB sensitivity: oster_delta / sensemakr.
• Inference: wild_cluster_bootstrap (few clusters), twoway_cluster / conley.
• Re-fit off one handle: audit_result(result_id) lists missing checks + the exact suggest_function for each.
• Exhibits: etable / did_summary_to_latex from the handle — no retyped numbers.

Decisive checks in the body, exhaustive battery in the appendix. JF execution walkthrough.

Checklist

• Sample size justified via MDE + power at the group/session unit; realized power reported
• Inference uses the correct independent unit (cluster-robust / group-means / RI), not raw decision n
• Few-cluster inference handled (permutation / randomization inference) when sessions are few
• Multiplicity corrected across outcomes/contrasts; primary vs. exploratory clearly separated
• Primary analysis matches the pre-analysis plan exactly; deviations flagged
• Non-parametric test leads for the bounded/non-normal primary outcome
• Robustness to exclusions, learning (round halves), and order shown; attrition reported

Anti-patterns

• "We found a significant effect" with no power analysis and a tiny number of independent groups
• Per-decision n inflating significance when subjects are in repeated, interacting groups
• A cherry-picked significant contrast among many, uncorrected and unlabeled as exploratory
• Switching the primary outcome or exclusion rule after seeing results, without disclosure
• Parametric t-tests on heavily censored contribution data as the only evidence
• Declaring a null "no effect" when the design never had power to detect a meaningful effect

Worked vignette (illustrative)

A public-goods paper runs 4 treatments × 3 outcomes and reports 7 significant tests. The fix: declare the single pre-registered primary contrast (cooperation under punishment vs. no-punishment) tested at the matching-group level via a permutation test on group means (say 12 groups/arm), then apply Romano–Wolf across the remaining family and label the rest exploratory. The headline survives correction (illustrative p=0.004); two secondary "effects" do not and are reported honestly as exploratory.

Referee pushback mapped to the fix

• "How many independent observations do you actually have?" → Count groups/sessions, not decisions; report inference at that unit and the realized power for it.
• "You ran a fishing expedition." → Declare the single pre-registered primary test; correct the rest (Romano–Wolf/Holm) and label them exploratory.
• "Few clusters — your SEs are unreliable." → Use randomization inference / permutation tests on group means rather than asymptotic clustering.
• "The null is uninformative." → Report the MDE; show the design had power to detect a meaningful effect, so the null is evidence of absence, not absence of evidence.
• "Results depend on dropping subjects." → Show the effect with and without comprehension failers and state the pre-specified rule.

A minimal robustness panel to pre-build

1. Primary test at the group/session unit (non-parametric lead).
2. Same test with comprehension failers included vs. excluded.
3. First-half vs. second-half rounds (learning).
4. Permutation/randomization-inference p-value on the treatment label.
5. Multiplicity-corrected family of secondary contrasts, labeled exploratory.
6. Attrition table (and differential attrition / Lee bounds in field-online designs).

If all six point the same way, the result is robust in the sense ExpEcon referees mean; if (3) or (4) flips it, the headline is fragile and you learned that before a referee did.

Output format

【Journal】Experimental Economics (ESA method flagship)
【Skill】expecon-robustness
【Verdict】robust / fragile / underpowered
【Power】MDE + power at group/session unit; realized power
【Inference unit】group-means / cluster-robust / randomization inference
【Multiplicity】correction used; primary vs. exploratory split
【Design robustness】exclusions / learning halves / order / attrition
【Next skill】expecon-tables-figures