Appendix B — Appendix B — Methods Defense

The hard questions, answered before they’re asked

This appendix collects the strongest objections to the analysis and the program’s answers. The full technical treatment is in the repository’s PAPER_DRAFT.md (§6, Diagnostics, sensitivity, and limitations); this is the briefing-room version.

B.1 “Correlation isn’t causation — wells sit where the faults are.”

That is precisely the problem the estimator class is built for. Targeted learning adjusts for fault distance, fault-segment density, formation depth, well age, and neighborhood injection before comparing volumes. The residual question — unmeasured confounding — is addressed by negative controls and by the spatial signature: the effect concentrates at pore-pressure-diffusion distances (7–19 km) and vanishes in the far field, which is the physical fingerprint of a real mechanism, not of geographic confounding.

B.2 “Your headline number changed. Why should anyone rely on it?”

Because we publish the revision record and design the policy instruments around what didn’t change. Across every data vintage and estimator: the direction (positive), the mechanism (frequency-channel), and the spatial band (7–19 km) held. The pooled magnitude moved — and the Evidence Scoreboard documents each movement, including a cross-validation artifact we found and repaired ourselves. The model permit language (§A.4.5) makes a revision record an evidence requirement for exactly this reason.

B.3 “The per-radius estimates aren’t individually significant.”

Correct, and disclosed. Individual radii carry z ≈ 1; the basin-scale result is the inverse-variance pool of 13 correlated radii agreeing in direction. This is the appropriate inference for a mechanism that operates across a distance band, and it is why the policy artifacts use rankings and thresholds rather than single-radius point estimates.

B.4 “You don’t model operators reacting to earthquakes.”

True, and it is the program’s most important open limitation. If operators cut volumes after nearby events, a cross-sectional estimator can understate the true effect (the feedback loop biases toward null). Xiao et al. (2025, arXiv:2510.16360) demonstrate this longitudinal bias in the Fort Worth Basin with marginal structural models. Note the direction: correcting for the feedback loop would most plausibly strengthen the causal case for volume management, not weaken it. A longitudinal (LTMLE) extension is the program’s next methods milestone.

B.5 “Why should a 50,000-row subsample or a GPU solver be trusted?”

The two estimators cross-check each other. Estimator A (subsample, reference R implementation of HAL) and Estimator B (full panel, our GPU solver) agree on direction, mechanism, and spatial structure. The GPU solver was validated to 7-digit agreement against the reference implementation on synthetic problems before any production use, and its cross-validation selection rule carries a regression test born from the one artifact it produced.

B.6 “Near-field is where the public worries. Why no claim under 7 km?”

Because the data don’t support one. At 1–6 km, positive-event counts are small and the basis machinery is demonstrably unstable (sign flips under basis-degree changes, documented in PAPER_DRAFT.md §6.4). Reporting a fragile near-field number would be the fastest way to discredit the stable pressure-band result. The program reports what holds and labels what doesn’t.

B.7 “Who paid for this?”

No operator, regulator, or advocacy organization. See About the Author for the dual-role disclosure: an analyst who spent five years inside a Permian Basin operator, publishing evidence that supports injection limits, with the incentive structure that implies.