Skip to content

DAAF-Contribution-Community/daaf / .claude/skills/creative-verification

creative-verification

Verified

Researcher-facing analytic triangulation ("creative verification") for stress-testing provisional findings and designing pre-specified challenges before an analysis runs. Turns a researcher's concern or focal claim into competing explanations, bounded discriminating tests, audited diagnostic artifacts, and evidence-calibrated interpretations in a hypothesis/evidence ledger — behavioral, output-level verification replacing line-by-line code review. Covers 12 challenge families organized by Shadish-Cook-Campbell validity type, named sensitivity statistics, pre-committed interpretation rules, anti-fishing guardrails, and interactive diagnostic-artifact QA. Use in Ad Hoc Collaboration to verify, challenge, or stress-test a result, or to design discriminating tests before an analysis runs. Not code-change verification (verify skill / code review) and not final adjudication or re-execution (data-verifier, Reproducibility Verification) — prospective, hypothesis-driven challenge design of analytic claims.

references/sensitivity-statistics.md

View on GitHub
# Sensitivity Statistics

The catalog of **named, computable sensitivity statistics** that turn "challenge the
identification assumption" (challenge Family 11) and "challenge external validity"
(Family 12) into an auditable number with a threshold, rather than prose. Each entry
states what the statistic quantifies, the formula where it is verified (with an
honest confidence label on that verification), an **executable** closed-form Python
recipe where the container supports one, or a **flag-and-describe** treatment where
no installed route exists, and the misuse caveats that most often invalidate the
number.

**Container reality (OBSERVED, `uv pip list` / `Rscript installed.packages()` snapshot,
2026-08-06).** DAAF prohibits runtime installs, so this catalog is split by what the
container can actually run. Installed and usable: `statsmodels` 0.14.6, `pyfixest`
0.60.0, `linearmodels` 7.0, `rdrobust` 1.3.0, `scipy`, `numpy`, `polars`, `plotnine`,
`marginaleffects`. **Not installed on either lane:** `sensemakr`/`PySensemakr`,
`evalue`/`EValue`, `specr`/`specification_curve`, `HonestDiD`/`diff-diff`, `rddensity`,
`rbounds`, `doubleml`, `econml`, `dowhy`. The R lane is equally unequipped for these
specific packages — a flag-and-describe method cannot be rescued by switching to R.
For any flag-and-describe method the remediation is a **Dockerfile addition** (user
additions block, fast rebuild) proposed to the maintainer, not a runtime install and
not a speculative reimplementation.

**Evidence-grading of the formulas below.** Per DAAF's evidence-graded reporting: a
formula labeled **primary-source-verified** was read in full text and quoted; one
labeled **secondary-corroborated** is a widely-reproduced result confirmed across
independent secondary sources but not quoted from the paywalled primary; one labeled
**inference / verify-before-relying** was not verified against primary text and must
be cross-checked before a result depends on it. These labels are load-bearing — carry
them into any report that uses the statistic.

---

## Quick Catalog

| Statistic | Challenges | Container status | Formula confidence |
|-----------|-----------|------------------|--------------------|
| E-value | Unobserved confounding (RR scale) | Executable (RR closed-form) | RR form primary-source-verified (primary-author letter, Mathur et al. 2018); common-outcome OR/HR and continuous verify-before-relying |
| Cinelli–Hazlett robustness value (RV_q) | Unobserved confounding (regression) | Executable (closed-form from t, df) | Primary-source-verified |
| Rosenbaum Γ | Hidden bias in matched designs | Flag-and-describe | N/A (no installed route) |
| Oster δ | Proportional selection on unobservables | Executable (needs 3 regressions + R²_max) | Approximation primary-source-verified (Oster 2016 WP, p. 12); exact δ* = Prop. 3; δ=1 benchmark caveat |
| DiD pre-trends / honest-DiD | Parallel trends | Event-study executable; honest-DiD flag-and-describe | Event-study standard; honest bounds flag |
| McCrary / Cattaneo density | No manipulation (RD) | Flag-and-describe (`rddensity` absent); `rdrobust` estimate executable | N/A |
| IV falsification | Exclusion restriction (untestable) | Executable (overid / placebo) | N/A — exclusion is never "tested" |
| Transportability checks | External validity | Executable (reweighting) | Method standard |

---

## E-value

**What it quantifies.** The minimum strength of association — on the risk-ratio scale —
that an unmeasured confounder would need with *both* the treatment and the outcome to
fully explain away an observed association (VanderWeele & Ding 2017 —
https://doi.org/10.7326/M16-2607 ; Stata `evalue` — Linden, Mathur & VanderWeele
(2020), https://doi.org/10.1177/1536867X20909696 ; R `EValue` — Mathur et al. (2018),
https://doi.org/10.1097/EDE.0000000000000864). A large E-value means only
a strong confounder could overturn the result; an E-value near 1 means a weak one
could.

**Formula.** For a risk ratio RR ≥ 1:

```
E = RR + sqrt(RR * (RR - 1))
```

For RR < 1, invert first (RR' = 1/RR) and apply the same form. Apply it to the point
estimate and, separately, to the confidence limit closest to the null to get the
E-value for the CI. If the CI already includes 1, the CI E-value is 1: it is the
confounding strength "capable of attenuating the confidence interval such that it
includes the null" (Mathur et al. 2018), and no confounding is needed for that.

> **Confidence: primary-source-verified (primary-author letter).** The RR closed form
> above and the invert-below-1 rule are read from the primary authors' open-access
> letter (Mathur, Ding, Riddell & VanderWeele 2018, *Epidemiology* 29(5):e45): "If the
> original risk ratio is below 1, then one first takes the inverse before applying the
> E-value formula." The Annals of Internal Medicine paper itself was not read (the
> publisher returned HTTP 403). The same letter says the formula "can also be used for
> hazard ratios or odds ratios with outcomes that are rare at the end of follow-up".
> The common-outcome OR / HR and continuous-outcome conversions (VanderWeele & Ding
> 2017 Table 2) are **inference / verify-before-relying** — confirm each conversion
> constant against VanderWeele & Ding 2017 Table 2 before a result depends on it.

**Executable recipe (RR scale only).**

```python
# INTENT: compute the E-value for a risk-ratio estimate and its near-null CI bound
# REASONING: quantifies how strong an unmeasured confounder must be to nullify the finding
# ASSUMES: rr and rr_bound are risk ratios on the original scale; rr_bound is the CI limit closest to the null (the helper inverts RR<1 itself)
# CONFIDENCE: RR closed form primary-source-verified (primary-author letter, Mathur et al. 2018)
import numpy as np
def _evalue(rr):
    rr = 1.0 / rr if rr < 1 else rr
    return rr + np.sqrt(rr * (rr - 1.0))
rr, rr_bound = 1.8, 1.3
evalue_bound = 1.0 if (rr >= 1 and rr_bound <= 1) or (rr < 1 and rr_bound >= 1) else _evalue(rr_bound)  # rr_bound = CI limit closest to the null; CI E-value is 1 when the CI includes the null
print({"evalue_point": _evalue(rr), "evalue_bound": evalue_bound})
# INTENT: interpret against a benchmark — is a confounder this strong plausible here?
```

(The one helper `def` above is illustrative for the formula only; in a real DAAF
script inline the two lines of arithmetic rather than defining a function, per the
flat-script code style.)

**Misuse caveats.** The E-value is a *threshold*, not a probability the result is
confounded — it says nothing about whether such a confounder exists, only how strong
it would have to be; always pair it with a substantive benchmark. Do **not** apply the
RR formula directly to an odds ratio or hazard ratio for a common outcome without the
documented conversion — direct use is licensed only when the outcome is rare at the
end of follow-up, and treating a common-outcome OR as an RR overstates the E-value.

---

## Cinelli–Hazlett Robustness Value (RV_q)

**What it quantifies.** In an omitted-variable-bias framework based on partial R², the
robustness value RV_q is the strength of confounding — as a share of residual
variance it would need to explain in *both* treatment and outcome — required to reduce
the estimated effect by 100·q percent (Cinelli & Hazlett 2020, *Making Sense of
Sensitivity* — https://carloscinelli.com/files/Cinelli%20and%20Hazlett%20(2020)%20-%20Making%20Sense%20of%20Sensitivity.pdf).
Like the E-value it needs no assumption on the confounder's distribution (and none on
the treatment-assignment functional form); unlike it, it is exact for linear regression
and is parameterized in partial R² rather than risk ratios (Cinelli & Hazlett 2020,
§6). It is computable from a standard regression table.

**Formula (primary-source-verified — full-text read and quoted, Eq. 18).**

```
RV_q = (1/2) * ( sqrt(f_q**4 + 4 * f_q**2) - f_q**2 )
where f_q = q * |f_{Y~D|X}|  and  f_{Y~D|X} = |t| / sqrt(df)
```

Here `t` is the treatment coefficient's t-statistic and `df` its residual degrees of
freedom — nothing else is needed. The α-adjusted variant defines
`f_{q,α} = f_q − |t*_{α,df−1}|/sqrt(df−1)` (Eq. 19) and substitutes it for `f_q` in the
same form to give RV_{q,α} (Eq. 20); if `f_{q,α} < 0`, the robustness value is zero.

**Executable recipe (closed-form from any statsmodels/pyfixest fit).**

```python
# INTENT: compute the Cinelli-Hazlett robustness value from a regression t-stat and df
# REASONING: RV_q says how strong confounding must be to shrink the effect by q*100%
# ASSUMES: model is a fitted OLS with a treatment coefficient; q=1 -> effect to zero
# CONFIDENCE: formula primary-source-verified (Cinelli & Hazlett 2020, Eq. 18, quoted)
import numpy as np, statsmodels.formula.api as smf
m = smf.ols("y ~ treat + x1 + x2", data=df.to_pandas()).fit()
t = m.tvalues["treat"]
dof = int(m.df_resid)
q = 1.0
f_q = q * abs(t) / np.sqrt(dof)
rv_q = 0.5 * (np.sqrt(f_q**4 + 4 * f_q**2) - f_q**2)
print({"t": t, "df": dof, "RV_q": rv_q})
# INTENT: RV_q near 1 => only near-total confounding overturns it (robust);
#         RV_q near 0 => trivial confounding suffices (fragile)
```

**Misuse caveats.** RV_q assumes the *same* partial-R² strength on treatment and
outcome (the "equal confounding" benchmark); a confounder much stronger on one side
can overturn the result at a lower RV — report benchmark bounds against observed
covariates (the paper's formal bounds benchmarked on observed covariates, §4.4) rather
than RV_q alone. It bounds bias
from omitted *confounders*, not from measurement error or selection.

---

## Rosenbaum Γ (gamma)

**What it quantifies.** In a matched observational design, the magnitude of departure
from random assignment — expressed as Γ, the maximum odds-ratio by which two matched
units could differ in treatment odds due to an unobserved covariate — at which the
result's significance is lost (Rosenbaum 1987 — https://doi.org/10.1093/biomet/74.1.13;
definition not re-checked against Rosenbaum's text).
Γ = 1 is random assignment; the reported number is the smallest Γ that breaks
significance.

**Container status: flag-and-describe.** No `rbounds` (R) or Python equivalent is
installed, and implementing the Γ-sensitivity search over the Wilcoxon signed-rank
null distribution from scratch in `scipy` is algorithmically non-trivial and high-
authoring-risk. **Do not reimplement speculatively.** Describe the method, cite it,
report the matched design's vulnerability qualitatively, and recommend a Dockerfile
addition (`rbounds` via the R lane, or a vetted Python port) to the maintainer as a
follow-up.

> Absence note: the Python-package absence is inference from web search, not a PyPI-
> index probe; the in-container absence of `rbounds` on the R lane is OBSERVED via
> `installed.packages()`.

**Misuse caveats.** Γ is defined for *matched* designs — it is not a general-purpose
confounding bound for arbitrary regressions. A design significant only to Γ ≈ 1.1 is
extremely fragile to hidden bias; report the number, not just "significant."

---

## Oster δ (delta)

**What it quantifies.** Under proportional selection — the assumption that selection on
unobservables is proportional to selection on observables — δ is the degree of that
proportionality required to drive the treatment effect to zero, given an assumption
about the R² a hypothetical regression on *all* confounders would reach (R²_max).
δ > 1 means unobservables would have to matter *more* than observables to nullify the
effect (Oster 2019; Diegert, Masten & Poirier, arXiv:2504.21106 —
https://arxiv.org/html/2504.21106).

**Container status: executable** (three OLS fits + arithmetic; no special package).
Requires the uncontrolled and controlled coefficients/R² and a chosen R²_max
(Oster suggests R²_max = min(1.3·R²_controlled, 1) as one convention).

```python
# INTENT: compute Oster's delta for proportional selection
# REASONING: delta is how much stronger selection on unobservables must be to zero the effect
# ASSUMES: short = treatment-only model, full = treatment + controls; Rmax chosen explicitly
# CONFIDENCE: restricted approximation primary-source-verified (Oster 2016 WP, p. 12); the delta=1 BENCHMARK is NOT automatic
import statsmodels.formula.api as smf
short = smf.ols("y ~ treat", data=df.to_pandas()).fit()
full = smf.ols("y ~ treat + x1 + x2", data=df.to_pandas()).fit()
b0, r0 = short.params["treat"], short.rsquared
b1, r1 = full.params["treat"], full.rsquared
r_max = min(1.3 * r1, 1.0)
# Oster (2019) restricted approximation (β* ≈ β̃ − δ(β̊−β̃)(Rmax−R̃)/(R̃−R̊)), solved for β*=0; for reported results use the exact δ* of Oster's Proposition 3 (needs τ̂x from a treatment-on-controls regression)
delta = (b1 * (r1 - r0)) / ((b0 - b1) * (r_max - r1))
print({"beta_full": b1, "R2_full": r1, "R2_max": r_max, "delta_for_zero_effect": delta})
```

**Misuse caveats — the central trap.** δ = 1 is **not** an automatic "equal selection"
benchmark: absent an exogeneity assumption δ can converge to any real number, so
reporting "δ > 1, therefore robust" without justifying R²_max and the proportionality
premise is misuse (Diegert, Masten & Poirier, arXiv:2504.21106 —
https://arxiv.org/html/2504.21106). Always report the R²_max used
and its rationale; show sensitivity of δ to R²_max. δ is a coefficient-stability
heuristic, not a proof of unconfoundedness.

---

## DiD Pre-Trends and Honest-DiD

**What it quantifies.** For difference-in-differences, the credibility of the parallel-
trends assumption. Two tools: an **event-study** plot of pre-period lead coefficients
(should be near zero), and **honest-DiD** (Rambachan & Roth 2023) sensitivity bounds that
ask how large a post-period parallel-trends violation could be, disciplined by the
observed pre-trend, before the effect loses significance.

**Container status.** Event-study is **executable** via `pyfixest`
(`pf.event_study(..., estimator="saturated")` for Sun–Abraham under staggered adoption,
or interacted leads-and-lags; pyfixest has no `sunab()` — see the `pyfixest` skill,
`references/difference-in-differences.md`). Honest-DiD is
**flag-and-describe**: `HonestDiD` (R) and `diff-diff` (Python) are both absent, and
the underlying optimization over convex restriction sets is non-trivial — do not
reimplement.

```python
# INTENT: estimate an event-study to inspect pre-trend leads before any DiD claim
# REASONING: near-zero, non-trending leads are necessary (not sufficient) for parallel trends
# ASSUMES: `cohort` = each unit's first treated period (gname); Sun-Abraham handles staggered timing
# ASSUMES: argument names as in the pyfixest skill (references/difference-in-differences.md)
import pyfixest as pf
m = pf.event_study(data=df.to_pandas(), yname="y", idname="unit", tname="period",
                   gname="cohort", estimator="saturated", att=False, cluster="unit")
m.iplot()  # INTENT: visual inspection of leads/lags; save the figure to the workspace
# FLAG-AND-DESCRIBE: for formal honest-DiD bounds (Rambachan-Roth), no installed route;
#   describe the pre-trend magnitude qualitatively, cite the method, recommend a Dockerfile add.
```

**Misuse caveats.** Naive pre-trend significance tests are **low-powered, biased, and
under-cover** — a non-significant pre-trend is *not* proof of parallel trends, and
conditioning the analysis on passing a pre-test induces its own distortions
(Roth 2022 — https://doi.org/10.1257/aeri.20210236). Report the pre-trend as an
event-study picture plus honest-DiD-style reasoning, never as a conventional pass/fail
pre-test (conditionally valid pre-tests exist — Mikhaeil & Harshaw, arXiv 2510.26470 —
but are flag-and-describe here).

---

## McCrary / Cattaneo Density (RD manipulation)

**What it quantifies.** For regression discontinuity, whether units *manipulated* their
position around the cutoff — tested as a discontinuity in the density of the running
variable at the threshold (a placebo test on the running-variable density), followed
by covariate-as-placebo-outcome falsification.

**Container status.** The formal density/manipulation test (`rddensity`; Cattaneo,
Jansson & Ma 2020, *JASA* 115(531):1449–1455,
https://doi.org/10.1080/01621459.2019.1635480) is **not installed** (OBSERVED). `rdrobust` 1.3.0 **is**
installed but implements RD *point estimation*, not the density test. Two options: (a)
flag as missing tooling and recommend a `rddensity` Dockerfile addition; (b) a manual
local-polynomial density comparison in `scipy`/`statsmodels`, which is a materially
less rigorous approximation than Cattaneo's estimator — if used, label it as an
approximation, not the McCrary/Cattaneo test.

```python
# INTENT: RD point estimate is executable; the manipulation DENSITY test is not
# REASONING: separate what the container can do rigorously from what it cannot
from rdrobust import rdrobust
res = rdrobust(y=df["outcome"].to_numpy(), x=df["running"].to_numpy(), c=cutoff)
print(res)  # point estimation only
# FLAG-AND-DESCRIBE: density/manipulation test needs `rddensity` (absent). Recommend Dockerfile add;
#   optionally report a coarse histogram-density comparison as a labeled approximation, not the test.
```

**Misuse caveats.** A passed density test does not prove no manipulation: researchers
often misread a statistically insignificant density discontinuity as evidence of
negligible manipulation, and equivalence testing is needed to bound it (Fitzgerald 2025 —
https://jack-fitzgerald.github.io/files/RDD_Equivalence.pdf). Pair it with
covariate-placebo falsification. `rdrobust`'s `rdplot()` is reported to fail in 1.3.0 (read-only
array bug) — this claim is unverified in this container, so probe it before relying on
it, or plot RD binned means manually. Reporting a home-rolled density comparison
as "the McCrary test" overstates rigor.

---

## IV Falsification

**What it quantifies.** For instrumental variables, indirect evidence on the exclusion
restriction — which is **fundamentally untestable**; placebo-outcome falsification is
the leverage the cited source names
(https://mike-data-analysis.share.connect.posit.cloud/sec-quasi-experimental.html).
Available falsifications: placebo-outcome checks (the instrument should not affect an
outcome it can only reach through the treatment), overidentification tests (with more
instruments than endogenous regressors), and balance of the instrument across
pre-determined covariates — the last two are DAAF inference, not from the cited source.

**Container status: executable** via `linearmodels` (`IV2SLS`, Sargan/Wooldridge overid
where overidentified).

```python
# INTENT: run falsification checks around an IV design (never a "test" of exclusion)
# REASONING: exclusion is untestable; overid + placebo outcomes are the only leverage
from linearmodels.iv import IV2SLS
m = IV2SLS.from_formula("y ~ 1 + [treat ~ z1 + z2] + x1", data=df.to_pandas()).fit()
print(m.sargan)  # overidentification test (only informative if overidentified AND instruments valid jointly)
# INTENT: placebo — instrument should NOT predict an outcome outside the causal channel
```

**Misuse caveats.** Never describe the exclusion restriction as "tested" — overid tests
assume at least one instrument is valid and can pass while all are invalid (DAAF
inference, not from the cited source; check an IV text before relying on it). A placebo
that runs through the treatment channel gives false comfort.

---

## Transportability Checks

**What it quantifies.** How far an estimate generalizes to a target population, framed
as a selection-into-sample / trial-participation problem: compare effect-modifier
distributions between sample and target, then reweight the sample to the target and
re-estimate (Degtiar & Rose 2023 — https://doi.org/10.1146/annurev-statistics-042522-103837 ;
preprint 2021 — https://arxiv.org/pdf/2102.11904 ; Pearl &
Bareinboim 2014 selection-diagram transport —
https://doi.org/10.1214/14-STS486).

**Container status: executable** (participation-propensity reweighting via
`statsmodels` + `polars`). Recipes 12a–12c in `challenge-families.md` implement the
sample-vs-target comparison, reweighting, and leave-one-group-out.

**Misuse caveats.** Reweighting corrects only for *observed* effect-modifiers;
unobserved modifiers remain a transport threat and must be stated. Extrapolation beyond
the sample's covariate support is unsupported regardless of reweighting.

---

## Reporting Sensitivity Statistics

Every sensitivity statistic reported must carry: (1) the number; (2) the **benchmark**
it is compared against (an observed covariate's strength, a plausible confounder, the
target population) — a bare statistic is not evidence; (3) its **formula-confidence
label** from this file (primary-source-verified / secondary-corroborated /
verify-before-relying); and (4) for flag-and-describe methods, an explicit statement
that the container could not compute it and the Dockerfile-addition path. Per DAAF's
evidence-graded reporting, a sensitivity result is *observed* only when the generating
script and its output are quoted or linked (`interpretation-and-evidence.md`).

## References

- VanderWeele, T. J., & Ding, P. (2017). Sensitivity Analysis in Observational Research: Introducing the E-Value. *Annals of Internal Medicine*, 167(4), 268–274. https://doi.org/10.7326/M16-2607
- Stata `evalue` — Linden, Mathur & VanderWeele (2020), *Stata Journal* 20(1):162–175, https://doi.org/10.1177/1536867X20909696; R `EValue` — Mathur et al. (2018), *Epidemiology* 29(5):e45, https://doi.org/10.1097/EDE.0000000000000864
- Cinelli & Hazlett (2020), *Making Sense of Sensitivity* (robustness value) — https://carloscinelli.com/files/Cinelli%20and%20Hazlett%20(2020)%20-%20Making%20Sense%20of%20Sensitivity.pdf
- Rosenbaum, P. R. (1987). Sensitivity analysis for certain permutation inferences in matched observational studies. *Biometrika*, 74(1), 13–26. https://doi.org/10.1093/biomet/74.1.13
- Oster, E. (2019). Unobservable Selection and Coefficient Stability: Theory and Evidence. *Journal of Business & Economic Statistics*, 37(2), 187–204. https://doi.org/10.1080/07350015.2016.1227711
- Oster, E. (2016). Unobservable Selection and Coefficient Stability: Theory and Evidence (working paper, August 9, 2016; source of the "Oster 2016 WP, p. 12" approximation). Archived copy: https://web.archive.org/web/20250401072627id_/https://emilyoster.net/wp-content/uploads/UnobservableSelectionandCoefficientStabilityTheoryandEvidence.pdf
- Oster δ, benchmark caveat — Diegert, Masten & Poirier, *An Axiomatic Approach to Comparing Sensitivity Parameters*, arXiv:2504.21106 — https://arxiv.org/html/2504.21106
- Rambachan, A., & Roth, J. (2023). A More Credible Approach to Parallel Trends. *Review of Economic Studies*, 90(5), 2555–2591. https://doi.org/10.1093/restud/rdad018
- Roth, J. (2022). Pretest with Caution: Event-Study Estimates after Testing for Parallel Trends. *AER: Insights*, 4(3), 305–322. https://doi.org/10.1257/aeri.20210236 ; conditionally valid pre-tests — Mikhaeil & Harshaw, arXiv:2510.26470 — https://arxiv.org/pdf/2510.26470
- `rddensity` — Cattaneo, Jansson & Ma (2020), *JASA* 115(531):1449–1455, https://doi.org/10.1080/01621459.2019.1635480
- RD manipulation: a passed density test does not prove no manipulation (equivalence testing) — Fitzgerald (2025), *Manipulation Tests in Regression Discontinuity Design: The Need for Equivalence Testing* — https://jack-fitzgerald.github.io/files/RDD_Equivalence.pdf
- IV exclusion untestable; placebo-outcome falsification (the overid and instrument-balance points are DAAF inference) — https://mike-data-analysis.share.connect.posit.cloud/sec-quasi-experimental.html
- Degtiar & Rose (2023), A Review of Generalizability and Transportability, *Annual Review of Statistics and Its Application* 10:501–524 — https://doi.org/10.1146/annurev-statistics-042522-103837 (preprint 2021: https://arxiv.org/pdf/2102.11904) ; Pearl, J., & Bareinboim, E. (2014). External Validity: From Do-Calculus to Transportability Across Populations. *Statistical Science*, 29(4), 579–595. https://doi.org/10.1214/14-STS486
rea-analysis-optimizationmorluto/reaOptimize REA providers and shared analysis workflows for agent context, latency, CPU, and memory while preserving correctness and Evidence. Use for analysis bottlenecks and cache or query design; CI/test-suite optimization belongs to rea-ci-tests-audit.Stars: 470kUpdated Claude CodeCodexVerifiedInstall
rea-ci-tests-auditmorluto/reaAudit REA CI and test suites for correctness, fixture drift, false passes, and measured performance; use for suite or workflow investigations and efficiency changes, rather than ordinary feature testing or a single test failure.Stars: 470kUpdated Claude CodeCodexVerifiedInstall
rea-tool-designmorluto/reaAudit, investigate, design, or change REA investigation tools, CLI/MCP contracts, provider capabilities, and Evidence semantics.Stars: 470kUpdated Claude CodeCodexVerifiedInstall
ponytail-auditDietrichGebert/ponytailQuality audit of the whole repo: bugs, security, real load, missing tests, speed, and what to delete. Most important first.Stars: 194kUpdated Claude CodeCodexVerifiedInstall