Reliable Inference for Robust-Reference Profile Correlation

• Further refined the author draft after external AI feedback: clarified the abstract and calibration scope, made the local slope bound explicit, improved the qualitative comparison table, and moved software chronology to S3. Neither the alleged author-name typo nor a broken table row was found. No candidate result was promoted or simulation added.
• Subsequently incorporated the supported clarifications in a new outside-repository author revision, preserving six main sections and all numerical table bodies. Added an explicit random-index lemma and paired covariance details; clarified studentizer and numerical-certificate scope. The candidate fixed-tau CLT remains separate.
• Saved an internal proof dependency and boundary note separating current regular inference, a candidate fixed-tau shared-sign point-estimator limit, and frozen finite-sample evidence. Included an explicit random-index substitution lemma, its checked reference, and the separate role of empirical moving-window bounds.
• Re-read the existing n=80/640 pathway summaries to distinguish large finite-sample scale errors from eventual pointwise limits. No new rate, nonregular full-IF Wald validity, or independent mathematical certification is claimed. The initial note made no manuscript edits; the subsequent revision is linked above. Algorithms and frozen results remain unchanged; no new simulation cells or certificate replays were run.

• Connected the privately communicated Hoorn--Ho Pearson all-to-all profile definition to the robust-reference manuscript. Explicitly separate the profile construction from normalization and from the secondary C scale.
• Preserved all 21 numerical tables / 1,182 cells and the scientific proofs; 172 historical checks pass. No new design cells. The 42-page author PDF and verified Overleaf ZIP remain outside the repository. Broader supervisor feedback and independent mathematical review remain outstanding.

• Removed six tracked generated PDFs (three manuscript figures, an early integrated draft and two consultation documents) at the author's request. Verified copies remain outside the repository. Future PDFs are ignored. Figure checks retain the PNG assets and source-table reconciliation; PDF export is optional. Historical commits are unchanged.

• Narrower and more explicit contribution. Centered Frechet correlation already covers correlating distances from fitted centers. The new author revision acknowledges Fout--Fosdick alongside magnitude correlation and distinguishes the specific median--MAD--Huber inference chain from standard multistep theory. Segers is credited for estimated-center absolute-moment expansions. This is a bounded prior-work review, not a priority proof.
• Local proof repairs. State limiting Gaussian covariance separately from convergence of actual error covariance; control the entire weak-null unrestricted IF through Hhat + rhohat Khat; separate L2 component envelopes from L1 squared-class envelopes; align midpoint and KDE arguments with local density assumptions. These are internally reviewed repairs, not external mathematical certification.
• Targeted retained-evidence checks. Recalculate 34 conditioning indices from the symmetric bridge model. Replay 4,000 original severe samples at stored references, checking 16,000 marginal fits and the linear-location mechanism. Cross-check paired IF decomposition and 16 existing-seed orbit datasets. No new design cells or changed scientific outcomes.
• Author-source reconciliation. All 21 numerical tables / 1,182 cells are unchanged and source-reconciled; 172 historical checks pass. Clarify inactive population reference coefficients in all three older null models, finite-B permutation randomness and the scope of prospective Wilson intervals.
• Delivery and stopping point. The 41-page PDF and Overleaf source remain outside the repository, with the previous version preserved. The full suite passed 384 tests; another 18 version-specific checks passed with their matching sources (402 distinct repository tests). The independent-review handoff is updated with a blank response form. Hoorn's structure feedback, external mathematical review and author/venue decisions remain open.

• Closer antecedents and target comparison. Explicitly acknowledge existing magnitude correlation and compare the recent linear Lancaster target. A deterministic Gaussian formula/quadrature check separates targets without adding a simulation grid or claiming a generally superior coefficient.
• Proof and finite-sample qualifications. S1.3 now retains exact equality pieces in sign classes; S1.5 cites uniform-in-bandwidth theory with its assumptions distinguished. The odd-median <= convention explains a small finite-sample IF/SE reflection discrepancy; no default was changed.
• Environment correction. September 18--21 reports record source isolation and matching scientific-library versions, but not package isolation. Earlier prose overstated that latter claim. Historical reports remain unchanged; a fresh verified-environment replay records exact discrete fields and small floating differences under the existing tolerance, not bitwise equality.
• Audit strengthening. Exact scheduled method/solver joins, seed/truth checks and counterfactual corruptions close a row-identity gap. The original test plan is now explicitly historical; the active plan concerns manuscript and reproducibility obligations. Independent mathematical review remains open. See the review and correction record.
• Completed verification. The full suite passed 379 tests; all 18 version-specific manuscript tests also passed when given matching sources. The 40-page author revision preserves all 21 numerical tables / 1,182 cells. The verified environment replays 6,000 distinct original datasets; maximum scaled numerical difference is 6.67e-16 (rounded upward), with exact coverage decisions and no changed calibration conclusion. All 292 existing TSVs remain unchanged; zero new design cells were introduced.

• Integrated author draft. Local changes to the September 18 LaTeX add the focused target comparison, estimand-constant explanation, solver policy and S3.10 with the September 20 results. The Introduction, theorem, proof blocks and all 19 historical table bodies remain unchanged. The draft status now correctly records completed reproduction of the retained evidence.
• Additional-study reproduction. All six tables from the 6,000-dataset moderate-skew study reproduce exactly from an isolated source snapshot with recorded scientific-library versions, including 18,000 method and 6,000 solver rows. The earlier claim of package isolation is corrected in the September 25 entry. No new design cells or favorable-outcome search. Undercoverage remains.
• Checks. Twenty-one numerical tables / 1,182 cells reconcile; 21 focused tests pass. The 40-page PDF compiles without final warnings. LaTeX/PDF and the Overleaf package remain outside the research repository; the email is delivered in the conversation. External mathematical review remains open. See the integration and delivery record.

• One prespecified active-nuisance regular check. A moderate lognormal pair (log SD .3, latent correlation .4) was fixed before outcomes, with 2,000 replications at n=160/640/2560. Complete coverage is .9045/.9355/.9365; all Wilson intervals exclude .95. This did not deliver a calibrated positive benchmark, and no search for a favorable replacement was made.
• Full prospective solver comparison. On all 6,000 datasets, 12,000 checked marginal residuals pass; legacy and checked modes change no coverage decisions. Maximum estimate discrepancy is 6.15e-10 checked-SE units. Future analyses should explicitly request reference_solver="score_checked" and retain failures; the default stays legacy pending a deliberate versioned release decision. Neither this comparison nor successful return proves fixed-precision R5.
• Bounded completion materials. Two population-only clipping alternatives show that the reference-profile target changes. A corrected target table and verified literature connections are ready as short English LaTeX blocks. Fifteen focused tests and the full new-record audit pass. The September 18 working paper remains unchanged; actual external proof review remains open. See the decision and results record.

• Retained historical evidence reproduced. Six regular-null cells and all 34 retained S2 cells reproduce at their original settings, including bootstrap RNG consumption; quadrature, derivatives and post hoc diagnostics also match. The 12,800 dataset executions include 600 overlapping pilot samples. All 2,165 compared fields agree, and 286 original TSV hashes remain unchanged.
• Full-text literature interface closed. Pareto (2024) is a signed opposing-regression-line coefficient, not marginal radius correlation. Its worked example reproduces. A bounded Section 2 comparison and completed S3 reproduction record are integrated into the minimally edited author draft.
• Independent review package prepared. English questions, source map, blank response template and versioned proof/code evidence are ready for an external reviewer; independent review itself remains open. The 37-page PDF compiles cleanly; all 19 tables / 1,047 cells and 32 targeted tests pass. See the update record.

• Two core studies fully reproduced. Original skew and four-stage pathway studies reproduce all 14,000 existing datasets / 50,000 method-stage records, plus their listed summaries, paired contrasts and root checks. Eight tables contain 1,017,136 checked fields; maximum scaled discrepancy is 5.58e-16. Historical sources run in an isolated snapshot; frozen results remain intact.
• Review without forced manuscript changes. The September 15 working paper remains unchanged. Pareto's formula comparison still needs full text; Hoorn's Introduction, author placement decisions and independent proof review remain open. Seventeen targeted tests pass. This is not full historical-project reproduction and adds no new simulation cells. See the review and scope record.

• Proof clarifications integrated into S1. The author LaTeX adds explicit moving-boundary control, coefficient localization, weak-null empirical-norm reasoning and the residual-rule argument. Independent proof review remains open.
• Optional public solver mode. reference_solver="score_checked" checks the n-dependent score residual and recomputes the complete IF. Default arithmetic and return fields remain unchanged. All 41 existing datasets match the archived default exactly; all 82 optional marginal fits pass. No checked decision changes.
• Version-aware provenance and completed validation. The original source is archived under its unchanged manifest hash. All 327 tests pass; the actual manuscript's 19 tables / 1,047 cells pass audit. The local 36-page PDF compiles without warnings. No new simulation cells were added. See the integration report.

• Internal proof and root-condition review. The targeted review makes moving-boundary domination, random-coefficient localization and the weak-null empirical-norm argument explicit, with an analytic independent-t3 scope example. This is not independent mathematical peer review.
• A diagnostic residual-checked solver, not a new default. Under the internal protocol, a separate bisection prototype accepts only after an exact rational score check on represented inputs against 1/(10^8 n). All 82 margins of the same 41 existing datasets pass; full-IF recomputation changes no checked decision. Twenty-seven new deterministic tests and 14 existing API/pathway tests pass. The finite-machine failure guard is distinguished from the ideal-arithmetic R5 argument. Public algorithms, frozen results and manuscripts are unchanged; no new simulation cells were added. See the complete numerical audit.

• User-approved minimal LaTeX is the editing base. Literature distinctions, an elementary random-bandwidth KDE proof and a conditional numerical-root bound were added locally, preserving the original preamble, theorem and all 19 tables. Manuscript artifacts are delivered outside this repository.
• Final-LaTeX and bounded numerical checks now run in an isolated environment and source snapshot. The actual manuscript's 1,047 table cells match their sources; 41 existing datasets reproduce 137 method/stage rows and 193 decisions. Bracketed-root/full-IF comparisons change no checked decision. Seventeen targeted tests pass; no new simulation cells were added. See the interface report for scope, provenance, warnings and remaining independent-review obligations.

• Actual supplements are now connected to one author draft - The new integrated Markdown manuscript and combined PDF supply S1's paired Bahadur/Z proof and local class verification, S2's existing permutation figures and full bridge/family panels, and S3's designs, seeds, studentizers, result tables and diagnostics. Historical chapter drafts, frozen results, source manifests and the public estimator remain unchanged. Hoorn's Introduction is still awaited; the existing provisional text is retained.
• Previously missing interfaces are documented - The score vector and marginal/paired covariance, raw-MAD error coordinates, radius variances, exact DGMs, default Gaussian KDE, solver tolerances and stage-specific influences are explicit. The original preprint's planned normalization change is not represented as an already verified public revision.
• Supporting C uses the original replication values - One existing tau=.10,n=640 cell was deterministically replayed at stored references to recover both marginal CVs, without refitting. All 8,000 stage records from 2,000 stored seeds agree (maximum rho gap 1.56e-15; C gap zero). Mean C is not reconstructed by multiplying mean rho and mean CVs. There are no new Monte Carlo cells and no new reference fits.
• Provenance review qualifies the old family confirmation - The bridge pilot and larger matched-index confirmation share cell seeds and RNG consumption; the first 150 draws overlap. S2 now describes a larger-run confirmation rather than an entirely independent repetition. The old rates and hashes are retained, and this does not affect the September 9 pathway study.
• Validation remains scoped - The new audit checks 19 actual table/ledger blocks; the historical audit still passes 172 checks covering 95 displayed numbers. The full suite passes 280 tests. Independent mathematical review, a general solver-to-theorem guarantee, clean-environment reproduction and final author decisions remain open. The interface crosswalk distinguishes assembled proof material from independently certified results.

• Ready for a first integrated working draft, not yet certified for submission - Existing Sections 1--6, Discussion, Appendix A and the short shared-sign result now have an ordered reading entry and provisional English abstract. Hoorn's revised Introduction remains the author-integration input; no competing full rewrite or new simulation grid was added.
• Proof-to-text reconciliation corrected specific issues - The secondary C proof now uses its reduced three-moment vector under A5-C rather than borrowing the general-rho five-moment CLT. The paired six-dimensional score stack and its cross-margin covariance are explicit. Weak-null empirical-norm control is distinguished from population L2 with infinite fourth moments. A missing LaTeX command slash and stale re-pairing wording were corrected.
• Displayed numbers are checked against sources - A read-only audit compares 95 numeric entries in the actual Section 6 tables, recomputes pathway Wilson intervals and Monte Carlo SE, checks frozen display reconstruction and source hashes. No prior simulation records or estimator algorithms were changed. Audit output and exact check scope are in results/manuscript_completion_audit_20260910.json: 172 checks pass. The full regression suite passes 276 tests, including a deliberate optimistic-coverage edit that the new table audit correctly rejects.
• Supplement and application choices stay explicit - Detailed permutation Figures 2--3 and their supporting statements are proposed for Supplement S2, pending supervisor confirmation; no physical move or renumbering has been made. A real application is optional and must first pass a documented scientific-pairing/IID-design gate. No dataset has passed that gate yet.
• Remaining obligations are substantive but bounded - Independent proof review, numerical-root/software obligations, clean-environment reproduction, final bibliography and author review remain open. Historical external-source matching is not independent mathematical peer review. A universal cutoff, new resampling method or broad degeneracy theory is not a drafting prerequisite.

• Supervisor-directed scope now leads the manuscript - The working title is Robust-reference profile correlation: pointwise inference and finite-sample limits. The core is the fixed-regular-IID full-IF theorem and a worked failure example, not a general safe-use rule. Hoorn is rewriting the Introduction. A short genuine paired-IID application is optional; no clustered extension, broad family grid, new resampling method, or universal cutoff is added.
• Four stages distinguish two reference-error pathways - A protocol recorded before simulation uses four existing cells and 2,000 paired samples per cell (8,000 datasets; 32,000 stage records). At tau=.10,n=640, mean profile correlation is -.0006/.1117/.1117/.6306 when fixing the true reference, fixing true scale, fixing true median, and fitting everything. Fixed-scale reference errors already align; full median/MAD fitting adds substantial amplification. Corresponding stage-aware empirical null rejection is .0525/.0330/.0330/.5510; direct-only values are reported separately, so small rejection is not confused with small profile bias.
• Short model result makes the assumption failure precise - Population median and Huber location are zero, raw MAD is one, true profiles are independent, rho_P=0, and C=1. The sample median is not root-n regular although the population Huber slope is nonzero. The full standardized Jacobian is singular throughout the unbridged family, so I_n=0 cannot distinguish its severe and diffuse cells. The n^(-1/4) boundary is a conditional rate heuristic, not a new limit theorem.
• Inference labels and numerical caveats are explicit - Re-pairing leaves medians, MADs, and Huber references unchanged; only joint moments and the studentizer change. Permutation remains supporting empirical stress evidence. There were no invalid stage returns but two full-fit numerical root flags; bracketed recomputation changed neither rejection decision. The public fitting algorithm and original frozen results were not changed. The September 7--8 skew coverage study was not rerun or tuned.
• Reproducible reporting - Replication records, source hashes, Wilson intervals, reference RMSEs/correlations, and paired-comparison MCSE are linked from docs/reference_pathway_results_20260909.md. New regression checks cover the stage IFs, sample covariance algebra, root replay, permutation invariance, and stored-result accounting. The full suite passes 269 tests. A post-run protocol correction withdraws an overly strong empirical-root uniqueness assertion; population uniqueness is not an all-sample guarantee.

• A demanding referee review now distinguishes a substantial working paper from submission readiness - The central concerns are nonroutine novelty, practical undercoverage, independent mathematical review, the missing stochastic bridge behind the switching account, and the scientific purpose of an application. Passing source checks is not peer review. The active skeleton no longer says only typesetting remains; Section 7 and any stronger inferential promise remain supervisor decisions.
• Section 8 is drafted in English - Discussion now integrates pointwise theory, nonzero-effect undercoverage, nonregular reference fitting, the target-projection limitation of I_n, fair comparator interpretation, and design-respecting inference boundaries. No new distribution grid or practical correction was introduced. Appendix A explicitly records the negligible numerical score-residual condition needed for its empirical Huber root.
• Frozen-draw diagnosis separates the tails and studentization - At n=2560, complete-IF intervals miss below/above truth at .0595/.0135. An infeasible population-asymptotic-SE diagnostic has coverage .958, versus reported .927. It changes random scale and its association with the estimate simultaneously; it is post hoc evidence, not a recommended interval or proof that a simple SE correction works. Tail Wilson intervals, interval widths, paired MCSE and source hashes are saved. An exact studentization identity also accounts for the empirical mean shift without claiming a complete higher-order coverage-error theory.
• Root replay checks did not identify a numerical explanation - Eighteen already simulated regular fits agree with independently bracketed roots to within 2.35e-11 scale units. This is not a general solver guarantee. See docs/referee_readiness_review_20260908.md and results/referee_coverage_diagnostics_20260908.tsv. No original canonical evidence or September 7 replication records were overwritten.
• Regression validation - The full suite passes 259 tests, including six new checks for tail accounting, numerical identity, fixed-sample replay, source hashes, and manuscript/theorem boundaries. Passing these checks does not close the independent mathematical-review gate.

• The primary nonzero-effect nuisance path has now been tested directly - One existing correlated-lognormal law, three prespecified sample sizes, and 2,000 paired replications per size compare the public complete-IF procedure, a direct-only SE ablation, and an oracle fixed-reference benchmark. Complete 95% Wald coverage is .858/.9115/.927 at n=160/640/2560; all Wilson intervals exclude .95. Oracle intervals also under-cover. This supports a finite-sample convergence boundary, not a claim of adequate calibration or general superiority. No new distribution grid or interval tuning was run.
• Independent integration tightened the numerical benchmark - Analytic truncated moments and knot-split quadrature give population rho_P=.193475119, refining the old Gauss--Hermite approximation without replacing its frozen source. The full reference and indirect MAD paths are active; their variance and covariance contributions nearly cancel here. Replication-level values, fixed seeds, paired MCSE, Wilson intervals, and LF-normalized source hashes are retained in results/active_nuisance_*.
• Active manuscript claims are now more precise - The severe signed- lognormal example has a nonregular median, not a flat population Huber equation. The binary identity is conditional on imposed offsets, not a fitted-switching theorem. Family residuals are unexplained by I_n, not proved entirely higher order; score covariance and target projection also matter. The Forneron identification reference is correctly attributed. Sections 3--6, Appendix A, the claim ledger, and Figure 3 wording are aligned.
• Validation and next step - The test suite passes 253 tests, including eight new numerical, replay, provenance, and claim-boundary tests. The next safe step is Discussion/limitations integration and independent proof review, not an open-ended search for an interval that makes this table look favorable. See docs/active_nuisance_validation_20260907.md and its prespecified protocol. Application, local theory, and operational inference scope remain supervisor decisions.

• A supervisor-readiness audit now closes the reportable three-claim package - Twelve checks confirm that Sections 1--6, Appendix A, the primary rho_P API, fixed numerical evidence, source hashes, and inference tracks remain mutually consistent. Claim 1 is ready as a pointwise regular IID theorem, Claim 2 remains an exact limiting proposition plus triangulated finite-sample evidence, and Claim 3 remains a first-order explanatory diagnostic with an explicit family residual.
• Remaining work is now decision-driven - The meeting brief separates necessary manuscript tasks from expansions that require Professor Hoorn's direction: a real application, local-to-degeneracy theory, a weak-null permutation theorem, or an operational sample version of I_n. No further general distribution grid is recommended. See docs/supervisor_discussion_brief_20260906.md and results/supervisor_readiness_audit_20260906.tsv.

• Section 6 formal displays are now frozen and auditably separated by evidence role - Table 2 contains only six theorem-aligned regular-IID Wald cells. Figure 1 is separately labelled as empirical finite-sample switching interventions, not theorem calibration. Figures 2--3 contain only fully recomputed studentized-permutation evidence and retain the group-invariance / weak-null boundary in their captions.
• No new scenarios were generated - A deterministic reporting script reads fixed-source result tables, records source hashes and Monte Carlo uncertainty, and writes a display manifest. The Section 6 audit rebuilds all five display tables and verifies that the Wald and permutation tracks never share a main display. See a local-only author document and results/section6_display_manifest_20260905.tsv.

• Manuscript integration has replaced open-ended exploration - Sections 3--5 now form one continuous regularity--switching--conditioning argument. Section 3 states the compact regular IID theorem and complete paired influence function; Section 4 presents fixed-reference, exact-balance, and sign-coupling interventions as a causal mechanism sequence; Section 5 joins the first-order rationale for (I_n) to both its grouped predictive evidence and the prospective family residual.
• Every numerical manuscript statement now has a frozen source - A sixteen-row crosswalk maps Section 3--5 signposts to exact result tables and preserves their evidence types. The primary-(\rho_P) derivative audit now has an explicit Appendix A interface, and Sections 1--2 incorporate the Stavig and MAD/median-correlation priority boundaries. No new distribution grid was run. See a local-only author document and results/manuscript_claim_source_crosswalk_20260904.tsv.

• The three-part novelty package passed a claim-directed adjudication - A new distribution-level contamination calculation verifies the complete influence function for the primary (\rho_P), including active five-moment, fitted-location, and indirect MAD paths. Existing paired interventions were then recombined to verify that reference refitting, rather than the fixed radial target alone, can generate the studied severe distortion.
• The novelty boundary is now stricter and more defensible - Functional delta methods, generated-regressor corrections, MAD/median robust correlations, M-estimator uniqueness, and singular-Jacobian identification diagnostics all have established precedents. The paper's contribution is their problem-specific development for unsigned robust-reference profiles: complete regular IID inference, an isolated nonlocal switching mechanism, and a dimensionless first-order conditioning organizer. LOFO and prospective checks retain strong coarse ordering while the systematic fifth-family residual remains explicit. See docs/novelty_claim_adjudication_20260903.md.

• Stavig's absolute-deviation correlation was resolved at the estimand level - The ranked coefficient is a Spearman-footrule form, while the interval coefficient is a normalized L1 discrepancy between signed marginal z scores. Neither is the correlation of unsigned distances from fitted robust marginal references.
• A classical-alternatives positioning table is now frozen - Eleven rows place the primary (\rho_P) beside Hoorn's all-to-all (c_d), both Stavig coefficients, fixed-reference profile correlation, Pearson, rank, robust raw-data and MAD/median robust correlations, Gini, distance-correlation, and Mantel alternatives. Deterministic sign-reversal and sign-rewiring witnesses verify the target distinction without extending the general distribution grid. The resulting novelty claim is about generated-reference inference, switching failure, and its conditioning diagnostic--not the absolute-value transform or a broadly new correlation coefficient. See docs/novelty_and_classical_positioning_20260902.md.

• The primary (\rho_P) procedure now has a public API - huber_profile_correlation_inference exposes the validated robust-reference profile estimate, complete first-order influence values, plug-in standard error, Wald interval, and test. The historical simulation entry point now delegates to the same implementation.
• Validation stayed claim-directed - One fixed regular sample, rather than another distribution grid, checks implementation equivalence, direct estimand agreement, positive-affine invariance, influence centering, and the secondary (C=1+\rho_PCV_XCV_Y) identity. The API documentation explicitly retains the pointwise/nonuniform and robust-reference/not-globally-robust boundaries. See docs/public_rho_api_validation_20260901.md.

• Canonical evidence hashes are now checkout-stable - The four stale source hashes were refreshed after hashing tabular text with CRLF and lone CR normalized to LF. The 34 frozen evidence rows, fixed seeds, rejection counts, Monte Carlo uncertainty, and scientific conclusions are unchanged; a regression test now verifies LF/CRLF invariance. See docs/canonical_hash_repair_20260831.md.
• The archived predecessor was verified directly - Hoorn's original paper is arXiv:2510.16717, currently v2 (revised 2026-03-08). Visual inspection of Eq. 4 confirmed that the online v2 numerator is still a sum, not an empirical mean. The planned correction therefore belongs to a future arXiv version; active manuscript text no longer says the archived PDF is already corrected.
• Section 3 passed its blocking readiness audit - The primary (\rho_P) estimate and complete standard error were positively affine invariant to below 1e-14, empirical influence centering was below 2e-17, the full theorem/studentization chain remained present, and both frozen regular dependent Wald cells remained compatible with nominal size.
• The finite-sample boundary remains visible - Strong-skew Wald rejection decreased from .122 at n=640 to .082 at n=2560, supporting the pointwise theorem without suggesting uniform calibration.
• One nonblocking software gap was recorded - The validated primary profile-correlation inference routine still lives in a simulation script and should be promoted into src/cdelta.py before a software release. This does not block drafting Section 3. See docs/archive_and_section3_readiness_20260831.md.

• Formal manuscript drafting began - Sections 1--2 now provide a complete English Introduction and robust-reference estimand section. The draft leads with inference reliability rather than a new coefficient, fixes (\rho_P) as the primary effect, retains (C) as a secondary historical scale, and states the old/new construct boundary without claiming method superiority.
• Definitions are implementation- and theorem-aligned - The text records the midpoint median/MAD convention, (k=1.4826), default Huber (c=1.345), population and sample profiles, the (C=1+\rho_PCV_XCV_Y) identity, zero-profile handling, and the exact 1D L2 all-to-all closed form.
• Inference boundaries are explicit before the theorem section - The draft distinguishes a weak profile-covariance null from independence and label exchangeability, separates Wald theory from permutation evidence, and keeps (I_n) explanatory rather than presenting it as a universal cutoff. See a local-only author document.

• Supervisor scope decision incorporated - The original all-to-all (c_d) remains on arXiv with a normalization revision planned, while the robust-reference work becomes a separate Yao--Hoorn paper led by Yao. Its main question is when inference for paired robust-reference divergence profiles can be trusted or can be misleading, rather than how to define another broad general-purpose coefficient.
• (\rho_P) is formally frozen as the lead estimand - Profile correlation directly expresses similarity around the robust references. (C) remains a historical or secondary effect scale and should be accompanied by both profile CVs when used. The old/new construct map and manuscript consequences are recorded in docs/professor_scope_decision_20260829.md.
• The old/new relationship was audited without a new simulation grid - The implemented all-to-all L2 profile matched its exact mean-centred closed form to machine precision, while a fixed example confirmed that standardization does not turn it into the Huber-reference profile. Existing evidence again gave the (C)-(\rho_P)-CV identity error below 5e-16, zero fixed-margin permutation p-value difference, and a (C) range above 2.5 at fixed (\rho_P=.30).
• The three claims now answer one paper question - Claim 1 states when regular IID Wald inference is trustworthy; Claim 2 shows how unstable reference fitting can fool it in finite samples; Claim 3 supplies a principled but incomplete conditioning diagnostic. Higher-order family effects remain the explicit limitation.
• Manuscript assembly has started - A section-level skeleton now maps the introduction, estimands, regular theorem, constructive failure, conditioning diagnostic, simulations, discussion, and supplements to frozen evidence. The readiness audit identifies two material remaining decisions: whether a genuine applied illustration is required and whether (I_n) remains an explanatory warning quantity or is intended to become an operational rule. See docs/manuscript_skeleton_and_readiness_20260829.md.

• The paper-level claim ledger is now frozen - The primary estimand remains profile correlation (\rho_P), with (C) retained as the original scale. The three main claims are separated into theorem-level results, exact finite-dimensional propositions, and empirical observations, with an explicit list of claims that cannot currently be made. This establishes a stopping rule against open-ended anomaly search. See docs/manuscript_claim_ledger_20260826.md.
• Claim 1 gained an independence-orthogonality corollary - At global independence, the two marginal Huber-reference coefficients in the profile-correlation influence function cancel exactly. A deterministic product-law audit found errors below 6e-17. This explains why fixing population centres did not cure the independent strong-skew distortion, without extending the result to every dependent weak null.
• Claim 2's switching mechanism now has an exact limiting calculation - In the binary two-radius construction, common selected modes produce profile correlation +1, whereas opposite modes produce -1. This provides the algebraic core behind the coupling dose response, while the broad severity claim remains finite-sample evidence rather than a universal theorem.
• Claim 3 is now scale interpretable - The standardized nuisance Jacobian, its minimum singular value, and (I_n=\sqrt n,\sigma_{\min}(J)) are invariant to location shifts and positive changes of units. Numerical audits on hyperexponential-bridge and skew-lognormal laws matched transformed Jacobians within 3e-11. The index remains an organizer, not a universal cutoff.
• Appendix source protection was added - The source contains the correct single-numerator MAD derivative. Regression tests now reject duplicated numerator terms, control characters, or broken LaTeX escapes in the new corollary and proposition.

• Claim 1 separated from Claim 2 mechanistically - Fixing distribution-level population Huber centres in the independent strong-skew model left rejection and asymmetric tails essentially unchanged (.120/.125 at n=640, .092/.090 at n=2560, refitted/oracle). Strong- skew slow convergence is therefore a radius-correlation/studentization higher-order problem, not near-degenerate reference estimation.
• Claim 2 gained a coupling dose response - As shared-sign coupling rose from 0 to 1, mean refitted effects rose monotonically from -.006 to .806 at n=80 and .001 to .626 at n=640, while fixed-zero effects remained near zero. This demonstrates how coupled mode selection, rather than radial concordance, activates the centre-gap failure.
• Claim 3 received a prospective family test - A fifth hyperexponential bridge with exactly matched origin density preserved the coarse recovery ordering across conditioning levels. The old-family model improved MAE by 47.6% and log loss by 14.5% over its intercept baseline, but systematically overpredicted all six rejection levels. This simultaneously supports first-order ordering and the higher-order-family limitation. See docs/claim_external_validation_20260825.md.

• Claim 1 tail mechanism refined - In 800-repetition diagnostics, the regular dependent-normal model had reported-SE/empirical-SD ratios 1.007/1.014 and rejection .055/.051. Under strong skew, the ratio had recovered to .980 by n=2560, yet the studentized 2.5%/97.5% quantiles remained -2.741/1.705 and rejection .083. The residual problem is an asymmetric higher-order/self-normalization effect, not merely a constant SE underestimation that a scalar HC factor would necessarily repair.
• Claim 2 switching trigger isolated - In the severe centre-gap model, forcing exact sign balance reduced rejection from .766 to .058 at n=80 and from .535 to .060 at n=640; mean maximum absolute Huber centre displacement fell from .491/.239 to .013/.005. This is a mechanism intervention showing how IID sign-count noise triggers reference switching, not a proposed correction or a new IID theorem.
• Claim 3 passed stricter transport checks - Cross-sample-size prediction improved MAE by 77.6% and log loss by 23.7%; leaving an entire (n, epsilon) conditioning level out improved them by 72.2% and 18.0%. The index still organizes rather than fully explains the transition. See docs/claim_stress_validation_20260824.md.

• Three frozen claims tested directly with independent seeds - New 1,000-repetition Wald cells confirm calibration for the regular dependent weak null (.052/.044 at n=160/640) and near-calibration for independent t5 by n=640 (.059), while independently reproducing slow strong-skew convergence (.122 at n=640, .082 at n=2560).
• Reference fitting mechanism isolated by a paired counterfactual - With radial log-SD .10, refitting the robust reference rejected at .777/.541 for n=80/640; fixing the symmetry reference at zero on the same samples reduced this to .054/.050. At radial log-SD .40, the paired differences were only -.018/-.006. This directly strengthens Claim 2 without implying universal near-degenerate failure.
• Conditioning claim now has out-of-family validation - A logit model using only log(sqrt(n) sigma_min(J)) reduced pooled leave-one-family-out MAE from .158 to .040 (74.7%) and log loss by 13.9%. All four families improved, but residual MAE .030-.055 preserves the higher-order-family limitation. See docs/claim_directed_validation_20260823.md.

• End-to-end pipeline audit passed with one claim-boundary correction - The statistic, MAD/Huber influence path, nuisance Jacobian, appendix proof, stored result schemas, and canonical source hashes remain internally consistent. The 34 frozen rows are now regenerated in tests rather than checking only that their hash strings have the right length.
• Wald and permutation tracks are now separated - Appendix A proves iid full-IF Wald inference, while the four frozen panels use fully recomputed studentized permutation. The latter are empirical weak-null evidence and are exact only under a declared group-invariance null; they are not direct validation of the Wald theorem.
• One historical regularity label was too strong - The frozen shared-sign t5 model has a centre-density gap and is not regular under A2. A replacement dependent weak-null model with normal margins is properly regular and gave Wald rejection .052, .052, and .047 at n=160,320,640.
• Regular does not mean finite-sample automatic - With 600 repetitions, strong-skew Wald rejection declined from .147 at n=80 to .102 at n=640, but remained .082 at n=2560. This supports pointwise theory while requiring an explicit slow-convergence limitation. See docs/end_to_end_pipeline_audit_20260822.md.

• External source-level mathematical review completed - The principal MAD reference defines exactly the same midpoint sample median and midpoint MAD used by NumPy, so its weak Bahadur theorem applies directly under A2. The lower-quantile comparison is retained only as a software-sensitivity audit.
• Skew MAD sign independently protected - A distribution-level lognormal contamination check matched the implemented asymmetric endpoint-density term within 1.4e-6; reversing its sign missed by 0.46. The existing code and appendix formula are therefore retained.
• Entropy closure refined - The squared influence class now cites the continuous-transform Glivenko--Cantelli preservation theorem with an integrable envelope, rather than implying that an algebraic closure theorem alone controls unbounded tails. The four-piece sign-times-radius identity had zero discrepancy in 10,000 fixed-seed checks.
• Final appendix placement fixed - Main Appendix A keeps assumptions, nuisance/moment derivatives, a concise empirical-process verification, studentized Wald theory, and the nonuniform Jacobian boundary. Full entropy, convention, and truncation details move to Online Supplement S1; permutation equivalence and group invariance move to Supplement S2 or a short methods note. No weak-null conditional permutation CLT is added under the current paper scope. See docs/external_math_review_appendix_placement_20260821.md.

• A8 entropy claims matched class by class - Half-lines, intervals, signs, active Huber pieces, sign-times-radius terms, Lipschitz moment classes, influence closures, and squared influence classes now each have an explicit VC-subgraph, Euclidean, or truncation route. Random nuisance substitution is tied directly to van der Vaart--Wellner Theorem 2.1 rather than a generic appeal to stochastic equicontinuity.
• The exact sample MAD convention is frozen - Both production paths use NumPy's midpoint median for even samples and apply the same midpoint rule to deviations from that centre, followed by the separate 1.4826 scale factor. This differs finitely from the generalized-inverse lower median but only by central-spacing order under the regular theorem assumptions.
• Fixed-seed convention audit supports first-order equivalence - Across normal and lognormal sampling at n=40-640, 6,000 repetitions per cell, the root-n-scaled median absolute MAD gap declined by roughly a factor of four while its n-scaled version stayed near 0.80-0.83 and 1.08-1.10, respectively. The difference is therefore numerically consistent with O_P(1/n), not a root-n theorem term.
• Weak-null permutation CLT decision closed for this paper - It is not needed under the frozen three-claim scope. Use iid influence-function Wald inference for the regular weak null and claim exact permutation only under group invariance. Reopen the conditional CLT only if fully recomputed studentized permutation becomes a headline method or formal main claim. See docs/entropy_mad_permutation_decision_20260820.md.

• Independent appendix audit completed - The earlier moment assumption was sufficient for the C influence but not for profile correlation, whose general nonzero-effect variance terms require marginal fourth moments. The revision separates A5-C from the stronger general A5-rho, while proving a weaker-moment corollary specifically at the profile weak null.
• Empirical-process gaps repaired explicitly - A local VC/Euclidean-class condition and stochastic-equicontinuity lemma now control random nuisance substitution. Plug-in variance consistency is proved through population L2 convergence plus a Glivenko-Cantelli squared influence class, rather than pointwise convergence alone.
• At the 08/19 checkpoint, proof boundaries were recorded - The entropy citations and exact sample-MAD/Bahadur convention were resolved on 08/20--08/21. The conditional weak-null permutation CLT was deliberately left outside the frozen paper scope. See docs/appendix_proof_audit_20260819.md and the later dated updates above.
• Primary estimand recommendation resolved - Use Huber-profile correlation rho_P as the direct concordance estimand and retain historical C as a secondary CV-weighted scale. Existing checks give identity error below 4.5e-16 and exactly equal permutation p-values, while fixed rho_P=.30 allows population C to range from 1.019 to 3.546 as marginal CVs vary.
• Formal appendix proof drafted - The median, MAD, Huber, five joint moments, profile correlation, and c_delta derivatives are assembled into an iid asymptotic theorem and studentized Wald corollary. Exact randomization validity is separated from the still-incomplete conditional proof for studentized permutation under arbitrary weak nulls.
• Four canonical evidence panels frozen - Regular calibration, near-degenerate failure, 24-cell bridge recovery, and the confirmatory family residual are now selected from existing fixed-seed results. The 34-row canonical table records source hashes, seeds, counts, Monte Carlo SEs, and Wilson intervals.
• No anomaly expansion - Today's computation only audited and froze existing evidence. See docs/appendix_asymptotic_theory_20260819.md and docs/estimand_and_canonical_evidence_20260819.md.

• Project moved to paper-definition phase - The core narrative is now regular iid validity, severe finite-sample distortion under near-degenerate robust-reference fitting, and the first-order explanatory role of sqrt(n)*sigma_min(J). New simulations should serve one of these claims rather than open unrelated anomaly branches.
• Evidence boundaries frozen - Pointwise iid asymptotic normality is kept separate from exact permutation invariance; the Jacobian formula is analytic, while the predictive strength and lack of a universal cutoff for the conditioning index are empirical conclusions.
• Higher-order family effects retained as the main limitation - Matched first-order Jacobians do not remove the confirmed family residual. Curvature, influence-tail shape, and nonlocal median/MAD switching are future focused theory, not a reason for another broad simulation grid.
• Conceptual and claim audit added - The proposed paper structure, ten required conceptual explanations, evidence ledger, forbidden claims, and decisions for Professor Hoorn are in docs/paper_architecture_and_conceptual_guide_20260818.md.

• Complete nuisance Jacobian computed and numerically verified - The standardized median/MAD/Huber Jacobian includes centre density, both MAD endpoint densities, MAD asymmetry, Huber active-score curvature, and scale coupling. Central finite differences reproduced all entries within 5e-6.

• Smallest Jacobian singular value unifies the bridge scaling - Across 24 matched-family cells, smaller sqrt(n)*sigma_min(J) correlated .971 with rejection and gave logit R-squared=.932. The binding direction was d*f(m); nominal rows appeared only after the sample-scaled value was well above one, although no universal cutoff is claimed.

• Residual family effect is beyond first order - Adding MAD endpoint density and Huber curvature increased R-squared only to .938, while the matched-family Jacobians were nearly identical. The confirmed family difference is therefore a higher-order/nonlocal median-MAD selection effect, not a missing term in the functional delta derivative.

• Skew benchmark restored the full coupling - For lognormal log-SD 1.1, the standardized MAD density difference was -.294, Huber scale coupling was -.270, and the Jacobian condition number was 3.74, confirming the implemented indirect MAD-to-location path outside symmetry.

• Matched-density bridge families refined the identification claim - Four bridge laws with identical f(0)=epsilon/2 preserved the main n*epsilon^2 ordering (R-squared=.931). Family terms raised R-squared only to .949, but a targeted 500-dataset transition cell confirmed a modest residual family effect (p=.00013, Cramer's V .101). Centre density alone is therefore not a complete finite-sample condition.

• MAD collapse added to the diagnostic audit - Within the confirmed transition cell, small fixed-MAD-scale/IQR had risk-oriented Spearman correlations .726-.777 with rejection, stronger and more consistent than bootstrap location spread. Bootstrap MAD spread itself had the wrong directional interpretation and is not recommended as a risk score.

• External MAD-ratio check passed a conservative warning boundary - In 2,000-dataset external cells, MAD-scale/IQR < .40 never warned for t_5, affine near-constant, or the regular-behaving sign-link path, and warned .028/0 under strong skew at n=80/320. It remains descriptive, not a conditional-validity gate.

• Independent boundary calibration reproduced the failure transition - At n=80, studentized rejection fell from .847 to .053 as radial log-SD increased .10 to .30; at n=320 it fell from .753 to .033. Root-n bootstrap reference spread moved with this transition, whereas fixed spacing and density warnings remained too structural to determine validity.

• Positive centre density is not enough at finite n - Adding independent Uniform bridge radii makes f(0)=epsilon/2>0, yet epsilon=.05 still gave rejection .487/.313 at n=80/320. Recovery approximately followed n*epsilon^2, as predicted by the median error scale 1/(epsilon*sqrt(n)); the constrained collapse R-squared was .919.

• Bootstrap warning remains diagnostic, not a gate - The exploratory scaled-spread threshold 2 had zero warnings in eight external-null cells and tracked the broad recovery path, but samples passing the warning could still have strongly inflated conditional rejection. It must not be used to certify local p-values.

• Project audit - New boundary, bridge, collapse, and external validation artifacts are documented in docs/profile_bridge_calibration_20260817.md; after the nuisance-Jacobian extension, the full suite now passes 171 tests.

• Sample-size diagnostic comparison completed - Across n=40-640, the severe radial .10 profile null remained invalid (.887 to .553 rejection), while root-n scaled bootstrap Huber-reference spread increased from 2.53 to 5.22. The .20 path recovered to nominal rejection even though spacing and central density still warned, separating assumption diagnostics from operational estimator stability.

• Bootstrap reference stability is the leading operational warning - In 16 external null cells its scaled median stayed 1.03-1.39 and its largest 90th percentile was 1.69. A provisional value above 2 separates the severe path in this grid, but remains an exploratory warning rather than a formal gate. At least 199 bootstrap draws are recommended for reportable continuous scores.

• Fixed spacing gate not promoted - The .50 spacing rule over-warned small strongly skewed samples, whereas central valley density described the theoretical low-density boundary but also warned after finite-sample rejection recovered. Current reporting should retain two tiers rather than combine them automatically.

• Horizontal testing comparison completed - Pearson/CCC weak-null theory supports fully recomputed studentization; distance correlation/HSIC target independence and have different degenerate-null resampling theory; spatial Mantel work reinforces structure-preserving permutations rather than unrestricted room labels.

• Continuous regularity path located the recovery region - Under a true profile weak null with shared signs, ordinary profile permutation rejected .907/.903/.520/.157/.053 as radial log-SD increased .03/.10/.20/.40/.80; studentization reduced this to .947/.840/.203/.030/.017. It helps materially but cannot repair a nonregular Huber/MAD reference.

• Scale-free gap diagnostic piloted - Largest central spacing divided by IQR fell from median .945 at the severe boundary to .237 in the regular endpoint. A provisional .50 warning gate removed the failed .03-.20 path, retained .997 of t_5, .997 of the regular profile partial null, and .797 of strong-skew samples. It is a conservative diagnostic, not a universal cutoff.

• Small raw scale separated from nonregular geometry - Independent continuous margins scaled by 10^-12 passed the .50 gate in every replication and retained rejection .033, confirming that affine scale alone is not the failure mechanism.

• Project audit - The comparison is documented in docs/comparator_testing_and_regularity_gate_20260816.md with canonical result tables and reproducible code; after the diagnostic-scaling extension, the full suite now passes 152 tests.

• Iid stress test sharpened the promotion boundary - A new n=80, 300-dataset, 199-permutation pilot tested fully recomputed studentized permutation under t_5, t_3, strong skewness, and both partial-null directions. Regular-row Holm true-null error ranged from .0200 to .0533, strengthening its status as a pointwise iid candidate.
• Near-degenerate profile inference rejected - When population radii had SD only .03 inside separated sign mixtures, unstable median/MAD reference fitting dominated the genuine profile variation: mean estimated profile correlation was .9123 and true-null rejection was .9533. A stable Huber/MAD fit and profile variances bounded away from zero are now explicit reporting requirements; failure should yield weakly identified'' or undetermined'', not an ordinary local p-value.
• Technical reporting note - Added the focused interpretation in docs/studentized_permutation_stress_20260815.md; email and LaTeX drafts are delivered in conversation rather than stored in the project.
• Project audit - The full Anaconda test suite now passes 139 tests.

• Fully recomputed studentized permutation passed its first iid gate - On every permutation, the profile method recomputes all pairing-dependent complete-IF terms and Mantel recomputes its node-level Hájek variance. At n=80, Holm true-null FWER was .050/.030 under two global nulls and .0417/.0367 under the two partial nulls.
• Larger-iid extension remained conservative after Holm - At n=160, global/partial-null Holm FWER ranged from .0225 to .0350, while both- alternative Holm power was 1.000. One individual Mantel null row reached .070, so the evidence is pointwise rather than a uniform guarantee.
• Six-building room-iid inference rejected - Treating 120 rooms as iid produced family error .2450 under Gaussian clusters and .3685 under skew-scale clusters.
• Small-building corrections remain unresolved - Building-summed t_5 plus Holm reduced FWER to .0405 under Gaussian clusters but remained .0735 under skew scales. A linearized building sign-flip was severely invalid (.180/.236) and was rejected. Increasing to 12/24 buildings did not repair the skew-scale cluster-t row, indicating that the global Mantel cross-building U-structure needs a separate cluster-level derivation. See docs/studentized_permutation_and_small_building_20260814.md.
• Weak-null local tests derived - Added the complete functional-delta influence function for the Huber-radius profile correlation and the order-two Hájek-projection influence function for the Mantel distance correlation. Both test correlation = 0 without assuming label exchangeability.
• Proper Mantel sampling unit - The n(n-1)/2 edges are not treated as independent. The sandwich uses node-level U-statistic projections, and the alternative jackknife deletes one node and all incident edges.
• Iid partial-null confirmation - Replaced fixed templates with genuinely iid weak-null laws. At n=80/160, Mantel-null/profile-alternative jackknife rejection was .055/.047; profile-null/Mantel-alternative rejection was .053/.064.
• Finite-sample boundary remains - Full-refit/delete-node jackknife improved on the raw sandwich, but global-null local rejection still reached .075 for profile and .097 for Mantel. The local tests are theoretically motivated research implementations, not report-ready defaults.
• Multiplicity decision deferred - Holm equals closed Bonferroni for the two component nulls and does not require subset pivotality, but it does require valid local p-values. Confirmatory global-null Holm FWER remained as high as .080 at n=80 and .073 at n=160; neither Holm nor closed testing is promoted. See docs/weak_null_local_tests_and_multiplicity_20260814.md.

• Subset pivotality rejected for weak component nulls - Constructed independently calibrated profile-null/Mantel-alternative and Mantel-null/ profile-alternative laws at n=60. The true-null standardized component distribution changed materially when the other component was non-null.
• Partial-null behavior quantified - Under profile-null/Mantel-alternative data, raw/maxT profile rejection was .056/.038, close to the matched global-null .056/.044. Under the reverse path, the null Mantel score SD collapsed from 1.083 to .075 (KS .596) and rejected 0. No inflation appeared in these cleaned paths, but the distributional change disproves a general subset-pivotality claim.
• Interpretation boundary tightened - Standardized max remains valid for the joint random-pairing omnibus null. Adjusted component p-values and winner labels remain descriptive rather than strong partial-null discoveries. Closed testing cannot be used until valid local weak-null tests are derived. See docs/partial_null_subset_pivotality_20260813.md.
• Omnibus interpretation validated - Added permutation maxT-adjusted profile/Mantel evidence and a standardized winner. The omnibus p-value is exactly the minimum of the two adjusted component values.
• Focused attribution check - In two 600-dataset target-separation rows, profile was the standardized winner .735 under node salience and Mantel was winner .998 under shared dyadic geometry. Omnibus regret was only .013 and .007, respectively.
• Construct overlap made explicit - Most significant datasets supported both adjusted components because node salience and dyadic geometry are not orthogonal. Winner/evidence describe relative support; they do not identify a unique causal mechanism.
• Permutation resolution - Relative to 999 permutations, 499 achieved .984 decision, .988 winner, and .968 attribution agreement across 18 alternative cells; 499 is suitable for routine simulation and 999 remains preferable for final near-threshold attribution.
• Theoretical boundary - maxT controls the declared family under the joint random-pairing null. Strong component discovery still requires subset- pivotality or partial-null validation, so standardized max remains an interpretable omnibus sensitivity rather than the primary method. See docs/omnibus_interpretability_20260813.md.
• Project audit - The completed project passes 125 tests; all new omnibus result files and conditional attribution shares passed consistency checks.
• Unequal building sizes separated from informative size - Held total n=72 fixed across balanced, moderately unequal, and severely unequal allocations. Size imbalance alone did not cause systematic power loss; larger changes arose when building size co-varied with floor area, age, heteroscedasticity, prevalence, and signal strength.
• Temperature learning did not validate - Scanned temperatures 0,.1,.25,.5,1,2,4,8,16. Orbit-standardized CV power was flat near 0-.25 and then declined; temperature zero is a fixed 50/50 mixture. Learned weights also moved in the wrong radial-versus-dyadic direction.
• Aggregation is an estimand choice - Equal-building, square-root-room, and equal-room weights gave materially different adaptive results under severe imbalance; they cannot be selected as a technical afterthought.
• Standardized-max candidate - Permutation-standardized max stayed close to the better fixed method and averaged .422 over four alternatives, versus .402 profile and .418 Mantel. It is an omnibus test without a unified effect size, so it is retained as a promising sensitivity candidate, not promoted to primary method.
• Covariate-conditioned inference confirmed - In the severe-imbalance null, unrestricted rejection ranged from .001 to .314, while every within-building method calibrated at .043-.046.
• Earlier project audit - The project passed 121 tests at the end of the unequal-building stage. See docs/unequal_building_covariate_adaptive_20260813.md.

• Application mechanism model added - Separately controlled marginal positive-sign prevalence, directional sign agreement, shared radial heterogeneity, correlated building-centre offsets, and a declared dyadic component in a six-building generator.
• Node terminology refined - Across two 400-dataset seeds per factorial cell, sign agreement helped Mantel more (+.524 average power effect versus +.381 for Huber profile), whereas radial heterogeneity helped profile more (+.157 versus +.103). Positive prevalence and correlated block centres acted as power-reducing distribution/nuisance axes rather than equivalent measures of within-building node signal.
• Adaptive weighting calibrated conditionally - Four null designs with 2,000 datasets each placed fully retrained CV at .043-.045 and nested-max at .038-.049. The adaptive weight is a method-preference diagnostic, not a latent node/dyad mixture estimate.
• Within-building theorem completed - Stated the product-permutation-group orbit proof and verified all 3!^2=36 permutations in a small example. Data-driven weights require pre-specification, group invariance, independent training, or complete refitting under every permutation.
• Environment audit - The project passes 112 tests in the Anaconda scientific Python environment. The system Python lacks NumPy/SciPy, so its import failure is an environment issue rather than a project regression. See docs/application_node_decomposition_and_permutation_20260812.md.

• Project audit clean - All 103 pre-existing tests passed before the study; the completed project now passes 106 tests and compiles without errors.
• Skew attribution audited - Decomposed node positive-sign prevalence and dyadic lognormal margins in a 2x2 study with two population and two local- power seeds per cell.
• Sign structure, not skew magnitude, drove the early transition - Node sign prevalence shifted crossover by about -.277; dyadic lognormal skew shifted it only +.009 on average.
• Balanced magnitude-skew control - A node margin with skewness -.432 but unchanged sign agreement moved crossover only -.035 with Gaussian dyads and +.022 with lognormal dyads. The prevalence cell had skewness only .072 yet moved crossover by -.266 to -.288.
• Prior wording corrected - The .131/.043 configurations remain valid composite-generator results, but no longer support “greater skew implies an earlier crossover.” Huber/MAD derivative conclusions are unchanged. See docs/skew_mechanism_factorial_20260811.md.

• Skew-path nuisance theory - Derived transport derivatives for the median, MAD, and Huber location, including the nonzero MAD-to-Huber indirect term, then propagated them through profile correlation and c_delta_star.
• Population derivative confirmed - In the final eight-by-500,000 check, preferred-step complete-refit errors were at most .000217 and below their Monte Carlo SE; two seeds, three steps, three boundary bandwidths, and two sample sizes preserved the substantive directions.
• Huber movement matters more than MAD alone - MAD indirect profile terms were .0016-.0039, while total location terms were about .077-.082 and could reverse the profile slope under strong skewness.
• Composite skew-generator crossover replicated - Two independent local power runs placed the two composite configurations at .131 and .043. The 08/11 mechanism audit attributes the early values mainly to node sign prevalence, not marginal skewness alone. All profile-ratio/Pearson permutation p-values stayed identical. See docs/skew_mixed_path_huber_mad_derivatives_20260810.md.
• Prior logic independently reproduced - A new eight-million-dyad seed reproduced the growing pure-node profile-minus-Mantel gap within .00131 and the near-zero pure-dyad gap within .00150; all 95 pre-existing tests also passed before the new work.
• Mixed-path tangent derived - For the square-root variance mixture, derived the component tangent and propagated it through profile-radius and pair-distance correlations using the full covariance/variance derivative.
• Pathwise formula verified - Across four configurations and eight method rows, the analytic/pathwise effect slope agreed with a .001 central difference to maximum error .000166.
• Power slopes independently repeated - Two 800-dataset seeds showed that both methods' power generally falls near the crossover, but profile power falls faster. The combined profile-minus-Mantel slopes ranged from -.094 to -.538; only the weak-both path remained unresolved.
• Mechanism refined - Crossover is caused locally by faster loss of the node-specific profile advantage, not necessarily by Mantel power increasing. See docs/mixed_path_local_slopes_20260810.md.

• Pure-path theory - Derived closed forms for lognormal node salience and Gaussian dyadic signals. On the pure dyad path, profile and Mantel population correlations are exactly equal; on the sign-rewired node path, their Monte Carlo gap increased from .209 at node correlation .35 to .445 at .75.
• External row-and-column validation - Added intermediate node strength .65 and lower dyad strength .30, producing seven new cells with refined, independently repeated crossover estimates.
• Ratio conclusion revised - The original raw-ratio model predicted the seven new crossovers with RMSE .0247. Across all 16 cells it achieved R-squared=.803; separate strengths improved this to .903, with node and dyad coefficients +.785 and -.360.
• Qualified node dominance - Node strength remains the larger crossover direction, consistent with the pure-path mechanism, but lower dyad strength has a non-negligible monotone effect. See docs/pure_paths_and_external_strength_validation_20260809.md.
• Clean project baseline - All 85 pre-existing tests passed, all Python sources compiled, and the working tree was clean before the new study.
• Two-dimensional strength surface - Crossed node-radius correlations .35,.55,.75 with dyadic-value correlations .45,.65,.80, estimating a locally refined profile-versus-Mantel crossover for every cell.
• Initial nine-cell result - Raw and Fisher-z strength-ratio models explained only .686 and .644 of logit-crossover variation. Allowing node and dyad strengths to enter separately increased R-squared to .938 and reduced leave-one-cell-out RMSE from .202-.215 to .118; the new external grid above shows this was too small a basis for rejecting a ratio approximation.
• Node strength dominates the surface - Crossovers were .148-.170 for node strength .35, .211-.234 for .55, and .253-.304 for .75. Dyad strength produced a smaller, nonmonotone within-row adjustment.
• Interpretation boundary - The separate model is descriptive and does not support post-hoc method selection. Profile versus Mantel choice remains estimand-first. See docs/signal_strength_surface_20260809.md.

• Common-target building simulation - Compared original L2 c_delta, Huber c_delta_star, Huber-profile Pearson, cap 6, and Mantel in one four-building design with node-salience and dyadic-geometry alternatives.
• Construct-specific power - Across two independent 800-dataset runs, Huber c_delta_star exceeded Mantel for sign-rewired node salience (.823 versus .713 combined), while Mantel exceeded Huber for shared dyadic geometry (.959 versus .797). Neither method universally dominates.
• Building restriction replicated - Conditional-null rejection averaged about .222-.239 under unrestricted permutations and .041-.046 under within-building permutations.
• Pearson equivalence extended - Huber c_delta_star and Huber-profile Pearson had identical p-values in every unrestricted and block-restricted permutation test.
• CV weighting boundary - At fixed population Pearson concordance .30, theoretical c_delta_star ranged from 1.019 to 3.546 solely because the marginal CV product changed. The highest-CV row still had -3.5% relative bias and SD 1.46 at n=2000.
• Interpretation update - Report Pearson as the direct profile-concordance effect and report c_delta_star together with both CVs only when marginal heterogeneity weighting is scientifically intentional. See docs/building_target_separation_20260808.md.
• Continuous node--dyad mixture - Interpolated standardized node-salience and dyadic components over weights 0-1, then refined the crossover region with two independent 1,200-dataset runs per grid point.
• Transition region - Combined paired-power analysis estimates the Huber- versus-Mantel crossover at dyadic variance weight .216. Huber has a resolved advantage through .175, neither has a resolved advantage over .20-.25, and Mantel has a resolved advantage from .275 onward in this generator.
• Comparator distinction - Original L2 crosses earlier at .137; cap 6 and uncapped Huber both cross at .216, confirming that the cap is mostly inactive without a severe leverage event.
• Non-universality - The transition is conditional on the selected node and dyadic correlations, sample size, building design, and permutation scheme. It is not a data-driven rule for choosing a test. See docs/node_dyad_mixture_transition_20260808.md.

• Two estimands, not one replacement - Professor Hoorn's distinction is now explicit: original L2 c_delta describes concordance of overall divergence for every member of the exact observed set, whereas c_delta_star describes robust-centre salience-profile concordance for a typical or generalisable structure.
• Exact Pearson identity - For nondegenerate robust radius profiles, c_delta_star = 1 + corr(r_x,r_y) CV(r_x) CV(r_y). Consequently, Pearson profile correlation and c_delta_star have exactly the same one-sided permutation ordering and p-value; MAD scaling cancels from both.
• Mantel information boundary - Mantel compares the complete dyadic distance matrices. Original c_delta first compresses each matrix to one row-RMS divergence per labelled observation and therefore cannot establish equality of the complete pairwise geometry. Cross-building claims must be stated at the observation-salience level unless Mantel/QAP/MRQAP is used.
• Reference robustness is not bounded influence - The Huber centre protects ordinary observations from centre displacement, but an uncapped matched extreme can still dominate the final numerator. At planted magnitude 32 its median numerator share was .965 for uncapped c_delta_star, .474 for old L2, and .497 for cap 6.
• Design-respecting inference confirmed - Reanalysis of the existing 18,000-dataset conditional-null experiment gave unrestricted rejection .442-.520, versus .047-.048 after within-building permutation.

• Distribution-level validation - Replaced empirical contamination checks with analytic lognormal margins and Gaussian-Hermite joint quadrature. At regular points the full influence derivative matched finite differences to scaled error below 1.2e-5.
• Boundary clarification - A contaminating atom exactly at the median is a nondifferentiable quantile direction. This is probability-zero for continuous sampling but must be excluded or treated directionally in the theorem.
• Density diagnosis - Across 2,500 skew-lognormal datasets per row, ordinary KDE, five-fold cross-fitted KDE, and the known true density changed mean sandwich SE by at most 0.2%. KDE is not the main coverage bottleneck.
• HC-style corrections - HC1 and HC3-style scalar inflation improved coverage but remained inadequate; skew-model HC3-style coverage ranged only from .8544 to .8976 over n=40-160.
• Bootstrap-t result - In 600 outer datasets per condition, complete-refit bootstrap-t did not improve coverage and the skew log-pivot could produce very wide intervals.
• Formal theorem - Stated auditable regularity conditions, asymptotic linearity, paired asymptotic normality, sandwich consistency requirements, and the boundary of the studentized claim.
• Inference decision - Retain permutation inference as formal default; treat the complete-IF interval as asymptotic and exploratory. See docs/studentization_refinement_and_theorem_20260806.md.

• Full functional-delta derivation - Derived the Huber-centre influence, including median/MAD scale coupling, then propagated the numerator and both denominator moments through one complete paired influence function.
• Sandwich implementation - Added plug-in asymptotic variance, normal and log-normal studentized intervals, and one-/two-sided Wald tests for the uncapped continuous-margin primary statistic.
• Theory validation - A closed-form symmetric lognormal benchmark matched a 250,000-draw variance check; 300,000-pair contamination derivatives also confirmed the nonzero MAD/centre nuisance path under skewness.
• Finite-sample boundary - Across the 1,200-repetition coverage grid, the full log-sandwich interval improved mean coverage from .9198 for the fixed-profile approximation to .9415, but still covered only .9108-.9258 for rho=.5. It is not yet a formal replacement for permutation inference.
• New theory note - See docs/functional_delta_and_studentized_inference_20260805.md and the corresponding results/studentized_* and results/general_influence_validation_20260805.tsv files.
• Next-phase decision - Broad calibration grids are no longer the main bottleneck. Prioritise the primary statistic's full influence function, asymptotic variance, studentized interval, and a formal restricted- permutation theorem.
• Huber bootstrap implementation - Added paired profile-refitting percentile, basic, BCa, and bootstrap-SE normal intervals, including leave-one-pair-out BCa acceleration and affine-invariance tests.
• Analytic-truth coverage test - Against C=exp(.2025*rho), ordinary bootstrap intervals overcovered severely at n=20 but undercovered stronger effects at n=80-160; overall averages hid this pattern.
• Focused coverage replication - With 800 independent datasets per row at rho=.5, coverage was only .934-.939 at n=80 and .919-.933 at n=160. No tested bootstrap interval is ready as a formal 95% interval.
• Independent core replication - A new 3,000-repetition seed reproduced block correction (.6610 unrestricted versus .0453 within-block), binary conservatism (.0240), clean local power (.4350), and contaminated local masking (.0693).
• Theory roadmap - See docs/next_theory_and_interval_validation_20260805.md and the corresponding results/huber_bootstrap_* and results/inference_independent_replication_20260805.tsv files.
• Design-respecting inference - Added within-block profile permutation and an exact restricted-reference formula. Under a shared-scale conditional null, unrestricted rejection averaged .44-.52; within-block permutation restored .047-.048 calibration while retaining high matched-signal power.
• Restricted reference - The random-pairing reference is exactly 1 only for unrestricted permutations. With blocks, between-block salience is held fixed and the exact conditional reference can differ substantially from 1.
• Discrete and degenerate validation - Across Bernoulli, ordinal, Poisson, zero-inflated, quantized, and near-constant margins, null rejection was conservative-to-calibrated. An exactly constant margin is reported as undetermined; ties must not be confused with evidence of no raw association.
• Local weak-signal map - In a balanced lognormal diffuse family, Huber primary exceeded old L2 for weak-to-moderate latent salience correlations. This refines the diffuse limitation: performance depends on signal geometry, not merely whether the signal is sparse or distributed.
• Severe diffuse masking - Independent 5% magnitude-20 contamination left every method with low diffuse power even at n=320; cap 6 improved detection but did not solve the problem.
• Inference-boundary documentation - See docs/inference_boundaries_and_local_power_20260805.md and the corresponding results/design_respecting_*, results/discrete_degeneracy_*, and results/local_salience_power_* files.
• Comprehensive old-versus-new benchmark - Compared original L2/L1, Huber primary, and Huber cap 6 across 18 scenarios, four sample sizes, 108,000 datasets, and common permutations. Exchangeable-null mean rejection remained .0475-.0485 across methods.
• Scope decision - Continue development as a moderately broad test of positive paired salience under exchangeable or design-respecting pairing; do not market it as a general correlation, independence, causal, or full-distance-geometry statistic.
• Comparative performance - Huber-primary average core power exceeded old L2 from n=40 onward and was substantially stronger for balanced bimodality and moderate-to-large-sample t2 signals, while preserving sparse matched power. Old L2 retained a genuine clean-diffuse advantage.
• Expanded cap-6 cross-validation - Across 180 additional conditions, cap 6 kept worst clean-core loss at .024 and delivered .2319 mean masking gain over uncapped Huber. Cap 5.5 remained too close to the declared .03 loss boundary; cap 6.5 was safer but less resistant to masking.
• Expanded diffuse boundary - Across 80 conditions, clean diffuse power loss sometimes persisted beyond n=80, especially with sign imbalance. Independent 5% magnitude-20 contamination erased most diffuse power for all uncapped methods; cap 6 recovered only part of it.
• Final reporting structure - Use uncapped Huber as the formal primary, cap 6 as a pre-specified leverage-limited sensitivity, and old L2 as a pre-specified comparator when diffuse alignment is scientifically central; do not use an unadjusted reject-if-any rule.
• Comprehensive documentation - See docs/comprehensive_scope_and_cross_validation_20260805.md and results/comprehensive_scope_benchmark_20260805.tsv, results/cap6_expanded_cross_validation_20260805.tsv, and results/diffuse_boundary_expansion_20260805.tsv.
• Cap loss formalisation - Defined a constrained loss that maximises unmatched-masking gain subject to null calibration and at most .03 worst-case absolute power loss over matched, t2, diffuse, and bimodal core alternatives.
• Cap-6 selection - A fine 4.5-8 grid across three training seeds selected cap 6; independent 5,000-repetition evaluation kept the largest core loss at .0224 and greatly improved masking power.
• Tolerance map - Cap 6 corresponds to accepting roughly .02-.03 worst-core-power loss; stricter tolerances select 6.5-7, while looser ones select 4.5-5.5. It is a declared robustness policy, not a universal constant.
• Diffuse mechanism - Increasing the Huber centre constant recovers small-sample diffuse power but transfers substantial loss to bimodal salience. An exploratory tail-triggered rule did not resolve this conflict.
• Definition recommendation - Retain Huber centre constant 1.345 for the primary score-all profile, accept and disclose the small-sample diffuse limitation, and use cap 6 only as a pre-specified bounded sensitivity profile.
• Literature cross-validation - Connected the decision to Huber contamination/efficiency theory, adaptive robustification, robust distance covariance influence analysis, h-star, and the archived c_delta target.
• Documentation - See docs/cap_loss_and_diffuse_decision_20260805.md and the corresponding results/cap_loss_*, results/center_*, and results/joint_candidate_validation_20260805.tsv files.

• Robust-definition study - Formalised centre-radius, fit-without/score-all, bounded-influence, and h-star-inspired salience profiles after the 08/03 discussion.
• First validation - Across six 500-repetition scenarios, the provisional IQR-fit/all-score profile preserved matched-outlier, diffuse-profile, and heavy-tail paired-signal power, but did not bound final outlier leverage.
• Robustness tradeoff - A three-robust-scale cap improved power under huge unmatched masking (.272 versus original L2 .052) but reduced genuine matched-outlier power (.314 versus 1.000).
• h-star bridge - A leave-one-out h-star-style profile was effective for a single matched candidate but suffered multiple-outlier denominator masking.
• Recommendation - Treat robust-reference/all-observation scoring as the main redefinition candidate and bounded scoring as a separate sensitivity estimand; do not use ordinary k-means as a one-centre robustness device.
• Expanded robustness grid - Added trimmed-mean and Huber centres, independent contamination nulls, t2, skewed, bimodal, masking, sample-size, and parameter-sensitivity checks. Huber reference scoring was the strongest uncapped candidate in heavy-tail and bimodal settings.
• Bounded sensitivity - A prospective 6 x MAD cap preserved nearly all matched-signal power while substantially improving unmatched-masking power; it remains a separate estimand, not a post-hoc universal constant.
• Stage-1 initial pilot - Replayed the original six pilot scenarios at n=60; Huber robust-reference preserved aligned and contaminated-aligned power (1.000), gave zero upper-tail rejection for inverted salience, and kept heavy-tail/skew null rejection near .05.
• Stage-2 structural theory - Derived the population target, affine invariance, exact permutation reference, and the distinction between robust centre fitting and bounded final influence. Tested robust L2-like radial floors to separate centre robustness from the old variance-floor geometry.
• High-replication validation - Completed 864,000 datasets across four sample sizes and nine scenarios with 999 permutations per method. Huber radius null rejection stayed in .0462-.0509, preserved sparse matched power, and improved t2 and bimodal power for moderate-to-large n.
• Independent-seed audit - The 3,000- and 24,000-repetition runs differed by only .00323 on average across 180 matched rows and reproduced the same main directional conclusions.
• Definition refinement - L2-like radial floors added no consistent value; retain the pure Huber radius as the primary candidate and cap 6 as a separate masking-resistance sensitivity estimand.
• Cap pre-calibration pilot - A prospective training rule selected cap 5 rather than cap 6; independent evaluation preserved calibration and improved masking power but exposed a small-sample power cost. Treat the calibration protocol, not a universal cap constant, as the supported result.
• Multivariate feasibility - Spatial-median radius was rotation invariant and promising across dimensions 1, 2, 5, 10; coordinatewise Huber was not rotation invariant and should not be the general multivariate default.
• Diffuse tradeoff map - The robust-radius power loss was material in the constructed diffuse family for roughly n <= 40 and small by n = 60-80.
• Dual-reporting pilot - An unadjusted union of primary and bounded p-values lacked level-.05 protection, while Bonferroni was conservative. Retain one primary inferential rule and report the bounded profile as sensitivity.
• Documentation - See docs/robust_cdelta_redefinition_20260804.md and docs/robust_definition_stage2_summary_20260804.md, results/robust_cdelta_grid_20260804.tsv, results/robust_cdelta_null_high_rep_20260804.tsv, and results/robust_parameter_sensitivity_20260804.tsv, plus results/robust_definition_highrep_validation_20260804.tsv. Routine extension results are summarised in docs/robust_routine_extensions_summary_20260804.md.

• Teacher-claim overlap validation — Added a 27,000-dataset factorial simulation holding standout number and magnitude fixed while varying only paired-index overlap across L1/L2, three sample sizes, and three backgrounds.
• Overlap gradient — Average rejection rose from about .02 at disjoint standouts to .81-.84 at full overlap, directly supporting the paired- standout interpretation.
• High-replication null follow-up — A preliminary L1-normal flag disappeared at 5,000 repetitions (.0466, Wilson interval [.0411, .0528]).
• Binary-overlap theory bridge — Derived r = (n m - k^2) / (k (n - k)) for equal-size binary standout sets and compared it with continuous divergence across 24,000 additional datasets.
• Meeting preparation — Added docs/meeting_discussion_20260803.md with concise findings, qualifications, and questions for Professor Hoorn.
• High-replication overlap cross-validation — Repeated the magnitude-8 overlap gradient with 1,000 repetitions per condition; all L1/L2 and normal/t3/t2 curves remained monotone.
• Random-set null — Added 18,000 simulations in which both datasets contain four strong standouts with independently selected indices; rejection stayed between .0377 and .0493 while observed overlap followed its exact hypergeometric distribution.
• Next-step roadmap — Added docs/next_steps_before_and_after_meeting.md and implemented the exact chance-overlap PMF with unit tests.
• Independent accuracy audit — Recomputed all meeting-result tables, matched the fast and core permutation implementations in 120 checks, and clarified that strict p < .05 gives effective levels .045, .0475, and .048 for 199, 399, and 499 permutations.
• Audited meeting figures — Added a reproducible figure builder using the 1,000-repetition overlap results and the exact random-set overlap reference.

• Paired-salience reframing — Added the exact one-dimensional L2 identity showing that divergence ranks observations by absolute deviation from their sample mean, so the current statistic aligns observation-level salience profiles rather than general full internal structures.
• Salience validation — Added scripts/run_paired_salience_validation.py and results/paired_salience_*_20260731.tsv to compare diffuse alignment, sparse alignment, partial alignment, reverse alignment, and calibrated null scenarios under L1 and L2.
• Reframing summary — Added docs/paired_salience_reframing.md; diffuse salience alignment is detectable even without strong outliers, while full pairwise-distance correlation can remain near zero.
• Literature positioning — Distinguished the current row-summary target from distance correlation, HSIC, energy distance, MMD, and Mantel-type full-distance-matrix correlation.
• Exact information-loss example — Added a construction with identical L2 divergence vectors (r = 1) but almost unrelated full distance matrices (r = -0.0402), proving that row aggregation is many-to-one.
• Directional alternatives — Extended permutation_test() with greater, less, and two-sided alternatives and retained greater as the default. Focused null rejection rates remained between 0.0325 and 0.0475.
• Alternative validation — Added scripts/run_row_aggregation_and_alternatives.py, two result tables, and docs/row_aggregation_and_alternatives_summary.md.

The cumulative record of mathematical identities, stable simulation findings, representative numerical results, reporting cautions, and open questions is maintained in docs/key_findings.md. Update this file after each material simulation or theoretical revision.

• Cumulative findings record — Added docs/key_findings.md as the central retrieval document for stable conclusions, representative values, reporting rules, open questions, and the reverse-chronological research log.
• Direct background-masking diagnostics — Added scripts/run_background_masking_diagnostics.py to locate large background divergence scores, measure their cross-vector index overlap, and compare planted paired products with background and random-pairing products.
• Masking results — Added results/background_masking_diagnostics_20260730.tsv and results/background_masking_summary_20260730.tsv; heavy-tail background extremes usually occur at unmatched indices, and a background-product masking event is substantially more common when the permutation test does not reject.
• Mechanism summary — Added docs/background_masking_diagnostics_summary.md; common-MAD scaling restores part of the planted product advantage, but unmatched background leverage remains under the heaviest tails.
• Algebraic identity validation — Added the exact decomposition c_delta = 1 + corr(D_x, D_y) CV(D_x) CV(D_y) and tests confirming that corrected c_delta and divergence-vector Pearson correlation rank permutations identically.
• Teacher-feedback scale checks — Added scripts/run_teacher_feedback_validation.py to compare the earlier common scale-parameter tail design with common-MAD and common-variance designs.
• Distribution-level results — Retained 12,000 matched and independent-null statistic pairs and added separation, power, and identity summaries in results/teacher_feedback_*_20260730.tsv.
• Interpretation summary — Added docs/teacher_feedback_validation_summary.md; common-MAD scaling attenuates but does not remove heavy-tail power loss, while matched-null separation narrows as tails become heavier.

• Fixed-k versus fixed-proportion tail validation — Added scripts/run_fixed_fraction_tail_validation.py to compare fixed k = 2 with fixed k / n = .05 across l1/l2, seven tail settings, and n = 40, 80, 160.
• Sample-size design results — Added results/fixed_fraction_tail_validation_20260729.tsv and results/fixed_fraction_tail_contrasts_20260729.tsv; fixed-k power declines as the subgroup becomes sparser under heavy tails, while fixed-proportion power is generally preserved or increases.
• Interpretation update — Added docs/fixed_fraction_tail_validation_summary.md and updated the research tracker; larger n is not inherently harmful, and future sample-size studies should distinguish fixed subgroup size from fixed subgroup proportion.

• Broad signal/noise validation — Added scripts/run_signal_noise_broad_validation.py to test whether signal/noise diagnostics explain power across 486 matched settings covering l1/l2, tail settings, n = 40, 80, 160, k = 1, 2, 3, and magnitudes 4, 6, 8.
• Broad validation results — Added results/signal_noise_broad_validation_20260726.tsv and results/signal_noise_broad_correlations_20260726.tsv; the strongest metric, signal_over_topk_noise, has overall Spearman correlation 0.9399 with rejection rate and remains strongly positive across kinds, sample sizes, subgroup sizes, and magnitudes.
• Broad validation summary — Added docs/signal_noise_broad_validation_summary.md; background divergence noise is consistently negatively associated with power, supporting the mechanism that heavy tails reduce signal-to-background-divergence-noise contrast.
• Signal-to-noise diagnostics — Added scripts/run_signal_noise_diagnostics.py to quantify the proposed mechanism behind heavy-tail power loss using matched subgroup prominence and background-only divergence noise.
• Signal/noise results — Added results/signal_noise_diagnostics_20260726.tsv and results/signal_noise_metric_correlations_20260726.tsv; signal-over-noise metrics correlate strongly with matched rejection rates, while background max-to-mean divergence is negatively associated with power.
• Mechanism summary — Added docs/signal_noise_diagnostics_summary.md; the current interpretation is that heavy-tailed backgrounds reduce power by lowering the matched subgroup's signal-to-background-divergence-noise contrast.

• Tail cross-validation — Added scripts/run_tail_cross_validation.py with higher-replication checks for the central tail-power slice, independent-null tail-size validation, and a fixed-k versus fixed-proportion sample-size comparison.
• Confidence summary — Added docs/tail_cross_validation_confidence_summary.md; the heavy-tail power decline is now stable under independent seeds, while null rejection rates remain close to alpha .05.
• Cross-validation results — Added results/tail_power_cross_validation_20260719.tsv, results/tail_null_cross_validation_20260719.tsv, and results/fixed_k_vs_fixed_proportion_20260719.tsv.
• Tail-factor comparison — Added scripts/run_tail_factor_comparison.py to test a finer Student-t tail gradient across l1/l2, n = 40, 80, 160, k = 1, 2, 3, magnitudes 4, 6, 8, and matched versus independent-null settings.
• Tail-gradient results — Added results/tail_df_factor_grid_20260719.tsv, results/tail_df_background_noise_20260719.tsv, and results/tail_df_null_validation_20260719.tsv; matched power decreases gradually as tails become heavier, while higher-replication null validation remains close to alpha .05.
• Visual summaries — Added tail-gradient power, null-validation, and background-divergence-noise plots in figures/.
• Interpretation summary — Added docs/tail_factor_comparison_summary.md; the main interpretation is that heavy-tailed backgrounds reduce power by increasing background divergence noise, not by clearly inflating type-I error.

• Follow-up stable diagnostics — Added scripts/run_followup_stable_diagnostics.py to combine high-replication independent-null checks, normal-background power curves, and a heavy-tail gradient study under the corrected reporting scale.
• High-replication null checks — Added results/flagged_null_high_replication_20260718.tsv; previously flagged independent-null rows mostly return to the nominal .05 level with 1,200 repetitions, suggesting the earlier .08-.09 values were likely Monte Carlo fluctuations.
• Power and tail-gradient outputs — Added results/power_curve_stable_20260718.tsv, results/heavy_tail_gradient_20260718.tsv, and summary plots in figures/; power increases with subgroup size, while Student t2 remains the clearest hard background.
• Follow-up summary — Added docs/followup_stable_diagnostics_summary.md to summarize the null calibration, power-curve thresholds, and heavy-tail interpretation.

• Extended stable simulations — Added scripts/run_extended_stable_simulations.py to test calibrated matched and independent-null behavior across target correlations .25 and .35, l2 and l1, normal, t3, t2, and lognormal backgrounds, and n = 40, 80, 160.
• Extended simulation results — Added results/extended_stable_simulations_20260717.tsv and docs/extended_stable_simulation_summary.md; normal and lognormal backgrounds often saturate at larger n, while Student t2 remains the hardest background and several independent-null rows are marked for higher-replication follow-up.
• Stable reporting table — Added scripts/build_stable_reporting_tables.py to generate a report-friendly table that excludes old raw-scale columns and keeps permutation p-values, rejection rates, Wilson intervals, divergence-vector correlations, pairing-normalized values, and independent-null calibration summaries.
• Report-ready metrics — Added results/stable_reporting_metrics_20260717.tsv with 198 stable-metric rows combining lower-target calibration and sample-size sensitivity summaries.
• Reporting guidelines — Added docs/stable_reporting_guidelines.md to document which quantities should be emphasized after the 1 / n normalization correction and which older raw-scale columns should be avoided.

• Numerator normalization correction — Updated the raw c_delta implementation to include the missing 1 / n factor in the numerator, so raw values are now on the corrected scale and the permutation mean is 1 rather than n.
• Revision note — Added docs/normalization_revision_note.md to document the formula correction, expected effects on previous outputs, and the original-paper revision item.
• Corrected-scale verification — Added results/normalization_feedback_checks_20260716.tsv; exact enumeration now confirms the corrected permutation mean is 1.0, while p-values and rejection-rate conclusions are unchanged by the constant scale correction.
• Normalization follow-up checks — Added scripts/run_normalization_followup_checks.py, results/normalization_followup_checks_20260716.tsv, and docs/normalization_followup_summary.md; the previously flagged l1/lognormal/n=160/k=1 null setting returns to empirical size 0.053 with 1,000 replications.
• Sample-size sensitivity — Added scripts/run_sample_size_sensitivity.py to test lower-target calibrated behavior across n = 20, 40, 80, 160 for both l2 and l1.
• Large-n sensitivity results — Added results/sample_size_sensitivity_20260716.tsv and docs/sample_size_sensitivity_summary.md; matched power often saturates by n = 80 or n = 160, while independent-null behavior remains mostly close to alpha .05.
• Lower-target L1 calibration — Added scripts/run_lower_target_l1_calibration.py to repeat the non-ceiling target_corr = 0.35 subgroup calibration with the absolute-difference (l1) divergence definition.
• L1 calibration results — Added results/lower_target_l1_calibration_20260716.tsv and docs/lower_target_l1_calibration_summary.md; the subgroup-size pattern broadly persists under l1, while heavy-tailed backgrounds remain flatter across k.

• Calibrated subgroup simulation — Added calibrated_subgroup_simulation() and scripts/run_calibrated_subgroup_simulations.py to compare k = 1, 2, 3 after first matching approximate divergence-vector correlation.
• Calibrated subgroup results — Added results/calibrated_subgroup_simulation_20260715.tsv and docs/calibrated_subgroup_summary.md; normal backgrounds show a ceiling effect, while heavy-tailed backgrounds show that subgroup-size effects cannot be explained by permutation resolution alone.
• Research tracker update — Updated docs/research_questions.md to mark calibrated alternatives as started and to identify lower-target calibration as the next refinement.
• Lower-target calibration — Added scripts/run_lower_target_calibration.py, results/lower_target_calibration_20260715.tsv, and docs/lower_target_calibration_summary.md; target correlation 0.35 avoids the normal-background ceiling effect better than 0.55 or 0.65.

• L1/L2 variant comparison — Added variant_comparison_simulation() and scripts/run_variant_comparison.py to compare squared-divergence (l2) and absolute-divergence (l1) versions under matched, negative-control, and independent-null settings.
• Variant comparison results — Added results/variant_comparison_20260714.tsv and docs/variant_comparison_summary.md; the matched sparse co-divergence signal remains strong under both l2 and l1, while independent-null behavior stays close to alpha .05.
• Research question tracker — Added docs/research_questions.md to track Professor Hoorn's feedback items, including calibrated alternatives, overlap-layer interpretation, independent-null calibration, rank-based variants, and background-scale interpretation.

• High-replication validation — Added scripts/run_high_replication_checks.py for 1,000-replication independent-null size checks and 100,000-permutation overlap-layer diagnostics.
• Monte Carlo uncertainty reporting — Independent-null summaries now include rejection counts, Wilson intervals, and p-value quantiles.
• High-replication result summary — Added docs/high_replication_checks_summary.md and results/high_replication_checks_20260713.tsv.
• Feedback response checks — Added scripts/run_feedback_checks.py to test Professor Hoorn's latest points: the old unnormalized permutation mean issue, permutation statistics by extreme-index overlap layer, and independent-null calibration with chance overlap.
• Feedback check results — Added docs/feedback_checks_summary.md and results/feedback_checks_20260713.tsv; the historical check exposed the missing 1 / n normalization, and overlap-layer diagnostics support treating 1 / choose(n, k) as a layer size rather than a p-value.

• Large-scale simulation architecture — Optimized permutation_test() by computing divergence vectors once and permuting D_y directly, making larger sample-size simulations feasible.
• Large-scale simulation script — Added scripts/run_large_scale_simulations.py to test n = 100, 250, 500 under normal, heavy-tailed, and log-normal backgrounds.
• Large-scale result summary — Added docs/large_scale_simulation_summary.md and results/large_scale_simulation_20260712.tsv; fixed-magnitude matched extremes remain detectable at large n, but heavy-tailed backgrounds require stronger subgroup structure.
• Near-zero divergence boundary notation — Added docs/near_zero_divergence_notation.md to document the preferred notation \bar D_x \bar D_y \to 0^+ and the report wording "undetermined due to data limitations."
• Boundary behavior simulation — Added scripts/run_near_zero_boundary.py and near_zero_divergence_simulation() to show that c_delta remains stable for positive shrinking divergence scales and becomes undetermined only at the empirical zero-divergence boundary.
• Update log order — README updates are now listed newest first.

• Multi-extreme all-star subgroup simulations — Added scripts/run_multi_extreme_simulations.py to compare one, two, and three co-occurring extreme pairs across small and larger sample sizes.
• Finite-sample permutation resolution note — Added docs/finite_sample_permutation_resolution.md to summarize why a single dominant extreme pair can be limited by the permutation test's finite-sample resolution, especially when n is small.

• Follow-up power and size simulations — Added scripts/run_followup_simulations.py to map matched-extreme power curves across smaller sample sizes, test normal, heavy-tailed, and log-normal backgrounds, and check nominal size at alpha .05 and .01.
• Simulation results — Added results/followup_power_background_size_20260710.tsv with the first follow-up tables for Professor Hoorn's suggested next steps.
• Testing coverage — Added a power-curve sanity test; the current test suite runs 8 unit tests.

The first deliverable is a reproducible simulation baseline:

• implement c_delta and its divergence vectors;
• report raw c_delta, a sample-dependent pairing-normalized version, and the Pearson correlation between divergence vectors;
• run permutation tests for the null hypothesis that the pairing between x and y carries no divergence-structure signal;
• run paired bootstrap confidence intervals;
• compare behavior under normal, heavy-tailed, skewed, and contaminated data.

This keeps the first phase close to Professor Hoorn's suggestion that simulation studies are most urgent, while leaving room for later h-star screening, robust variants, weighting schemes, and machine-learning examples.

• src/cdelta.py: statistic, permutation test, bootstrap CI, and data generators.

• scripts/run_pilot.py: example simulation run.

• scripts/run_outlier_influence.py: matched/unmatched extreme-value pilot.

• scripts/run_outlier_repeated.py: repeated extreme-value alignment study.

• scripts/run_robust_center_validation.py: first centre/cap/h-star robust profile comparison.

• scripts/run_robust_cdelta_grid.py: contamination, tail, skew, bimodal, and sample-size validation for robust-reference profiles.

• scripts/run_robust_parameter_sensitivity.py: Huber, trimming, hard-cap, and soft-cap sensitivity grid.

• scripts/run_robust_initial_pilot.py: stage-1 replay of the original pilot scenarios for the new profile definitions.

• scripts/run_studentized_inference_validation.py: oracle, direct-profile, full-sandwich, and jackknife studentized coverage comparison.

• scripts/run_studentized_focused_replication.py: independent strong-effect studentized interval replication.

• scripts/run_general_influence_validation.py: point-contamination finite- difference validation of the complete influence function.

• scripts/run_population_skew_influence_validation.py: distribution-level quadrature validation under skew lognormal margins.

• scripts/run_density_hc_studentization_validation.py: KDE, cross-fit, true- density, and HC-style standard-error comparison.

• scripts/run_bootstrap_t_validation.py: focused complete-IF bootstrap-t coverage experiment.

• scripts/run_teacher_feedback_20260807.py: exact profile/Pearson checks, Mantel information-loss construction, exact-set versus typical-set outlier estimands, and cross-building reanalysis prompted by the August 7 feedback.

• scripts/run_building_target_separation_20260808.py: common building-style comparison of salience-profile and dyadic targets, plus fixed-correlation CV weighting and convergence diagnostics.

• scripts/run_node_dyad_mixture_20260808.py: coarse, refined, and replicated power curves over a continuous node-to-dyad variance mixture.

• scripts/summarize_node_dyad_mixture_20260808.py: combine paired rejection counts and estimate method crossover locations without rerunning simulation.

• scripts/run_signal_strength_surface_20260809.py: coarse and refined node-strength by dyad-strength crossover surface and ratio-model comparison.

• scripts/run_signal_strength_extension_20260809.py: targeted independent extension for the one cell whose refined grid missed its coarse bracket.

• scripts/summarize_signal_strength_surface_20260809.py: assemble the final complete surface and refit ratio and separate-strength models.

• scripts/run_followup_simulations.py: power curves, non-normal backgrounds, and nominal size checks.

• scripts/run_multi_extreme_simulations.py: one-vs-subgroup extreme-value simulations for finite-sample permutation resolution.

• scripts/run_near_zero_boundary.py: near-zero divergence boundary behavior.

• scripts/run_large_scale_simulations.py: larger-n multi-extreme simulations using the optimized permutation test.

• scripts/run_feedback_checks.py: algebraic and null-calibration checks from Professor Hoorn's feedback.

• scripts/run_high_replication_checks.py: higher-replication validation with Wilson intervals and p-value quantiles.

• scripts/run_variant_comparison.py: L1/L2 divergence variant comparison.

• scripts/run_calibrated_subgroup_simulations.py: calibrated subgroup-size comparison.

• scripts/run_lower_target_calibration.py: lower-target calibrated subgroup comparison.

• scripts/run_lower_target_l1_calibration.py: lower-target L1 calibrated subgroup comparison.

• scripts/run_sample_size_sensitivity.py: sample-size sensitivity comparison for lower-target calibrated simulations.

• scripts/run_normalization_followup_checks.py: corrected-scale verification and flagged large-n null recheck.

• scripts/build_stable_reporting_tables.py: generate report-friendly stable metrics without raw-scale columns.

• docs/finite_sample_permutation_resolution.md: summary note on the small-sample permutation issue.

• docs/near_zero_divergence_notation.md: notation and reporting note for vanishing empirical divergence.

• docs/large_scale_simulation_summary.md: larger-n result interpretation.

• docs/feedback_checks_summary.md: results of the July 13 feedback checks.

• docs/high_replication_checks_summary.md: higher-replication validation summary with Wilson intervals.

• docs/variant_comparison_summary.md: L1/L2 variant comparison summary.

• docs/calibrated_subgroup_summary.md: calibrated subgroup-size simulation summary.

• docs/lower_target_calibration_summary.md: lower-target calibrated subgroup summary.

• docs/lower_target_l1_calibration_summary.md: lower-target L1 calibrated subgroup summary.

• docs/sample_size_sensitivity_summary.md: sample-size sensitivity summary.

• docs/normalization_revision_note.md: formula correction note for the missing 1 / n numerator factor.

• docs/normalization_followup_summary.md: corrected-scale follow-up summary.

• docs/stable_reporting_guidelines.md: guidance for report-stable quantities after the normalization correction.

• docs/functional_delta_and_studentized_inference_20260805.md: full Huber functional-delta derivation, sandwich variance, and interval validation.

• docs/studentization_refinement_and_theorem_20260806.md: distribution-level validation, studentization refinements, and formal first-order theorem.

• docs/building_target_separation_20260808.md: two-seed target-separation, building-permutation, and CV-weighting findings.

• docs/node_dyad_mixture_transition_20260808.md: current framework, mixture construction, paired transition estimates, and interpretation limits.

• docs/signal_strength_surface_20260809.md: two-dimensional crossover surface, ratio-hypothesis test, validation, and limitations.

• docs/application_node_decomposition_and_permutation_20260812.md: application-oriented mechanism decomposition, adaptive weighting, and the finite-sample within-building permutation theorem.

• docs/unequal_building_covariate_adaptive_20260813.md: unequal-size versus informative-size validation, temperature sensitivity, covariate-conditioned inference, and the adaptive-omnibus decision assessment.

• docs/omnibus_interpretability_20260813.md: maxT component evidence, construct attribution, power regret, permutation stability, and the global-null/partial-null interpretation boundary.

• docs/studentized_permutation_stress_20260815.md: heavy-tail, skewness, partial-null, and near-degenerate stress-test interpretation.

• docs/comparator_testing_and_regularity_gate_20260816.md: horizontal parameter-test comparison, continuous recovery path, and provisional profile-regularity warning gate.

• docs/profile_diagnostic_scaling_20260816.md: sample-size scaling, spacing-versus-density-versus-bootstrap comparison, external validation, and bootstrap Monte Carlo precision.

• docs/profile_bridge_calibration_20260817.md: independent fine-grid replication, positive-density bridge scaling, and diagnostic-gate audit.

• docs/profile_bridge_family_validation_20260817.md: matched-centre-density bridge families, targeted family confirmation, MAD nuisance audit, and external scale-ratio validation.

• docs/nuisance_jacobian_20260817.md: complete nuisance estimating system, finite-difference verification, singular-value identification scale, and skew benchmark.

• docs/appendix_asymptotic_theory_20260819.md: formal iid functional-delta, influence-function, plug-in variance, and studentized Wald appendix.

• docs/appendix_proof_audit_20260819.md: independent audit of moment, stochastic-equicontinuity, and in-sample L2 arguments.

• docs/entropy_mad_permutation_decision_20260820.md: exact class-by-class entropy mapping, NumPy sample-MAD convention audit, and decision boundary for a conditional weak-null permutation CLT.

• docs/external_math_review_appendix_placement_20260821.md: external source-level proof cross-check, numerical safeguards, claim boundary, and final main-appendix versus online-supplement placement.

• docs/research_questions.md: active research questions and next checks.

• tests/test_cdelta.py: minimal unit tests using Python's built-in unittest.

For the complete test suite on this machine, use the Anaconda scientific environment; the default system Python does not contain NumPy/SciPy:

/opt/anaconda3/bin/python -m pytest -q

From an environment with the scientific dependencies installed:

python3 -m unittest discover -s tests
python3 scripts/run_pilot.py
python3 scripts/run_outlier_influence.py
python3 scripts/run_outlier_repeated.py
python3 scripts/run_robust_center_validation.py
python3 scripts/run_robust_cdelta_grid.py
python3 scripts/run_robust_parameter_sensitivity.py
python3 scripts/run_robust_initial_pilot.py
python3 scripts/run_studentized_inference_validation.py
python3 scripts/run_general_influence_validation.py
python3 scripts/run_population_skew_influence_validation.py
python3 scripts/run_density_hc_studentization_validation.py
python3 scripts/run_bootstrap_t_validation.py
python3 scripts/run_teacher_feedback_20260807.py
python3 scripts/run_building_target_separation_20260808.py
python3 scripts/run_node_dyad_mixture_20260808.py
python3 scripts/summarize_node_dyad_mixture_20260808.py
python3 scripts/run_signal_strength_surface_20260809.py
python3 scripts/run_signal_strength_extension_20260809.py
python3 scripts/summarize_signal_strength_surface_20260809.py
python3 scripts/run_application_node_decomposition_20260812.py
python3 scripts/summarize_application_node_decomposition_20260812.py
python3 scripts/run_unequal_building_adaptive_validation_20260813.py
python3 scripts/summarize_unequal_building_adaptive_20260813.py
python3 scripts/run_omnibus_interpretability_20260813.py
python3 scripts/summarize_omnibus_interpretability_20260813.py
python3 scripts/run_partial_null_subset_pivotality_20260813.py --phase confirmatory
python3 scripts/run_weak_null_local_tests_20260814.py --phase confirmatory
python3 scripts/run_studentized_permutation_weak_null_20260814.py --phase confirmatory
python3 scripts/run_small_building_weak_null_20260814.py --phase confirmatory
python3 scripts/run_studentized_permutation_stress_20260814.py --phase pilot
python3 scripts/run_profile_regularity_comparison_20260816.py --phase pilot
python3 scripts/run_profile_regularity_comparison_20260816.py --phase pilot --design gate_cv
python3 scripts/run_profile_diagnostic_scaling_20260816.py --phase pilot --design path --n 80 --radial-log-sd 0.2
python3 scripts/run_profile_diagnostic_scaling_20260816.py --phase pilot --design external --n 80 --scenario independent_t5
python3 scripts/run_bootstrap_reference_precision_20260816.py --phase pilot --n 80 --scenario radial_0p1
python3 scripts/run_profile_bridge_calibration_20260817.py --phase pilot --design bridge --n 80 --bridge-probability 0.1
python3 scripts/summarize_profile_bridge_calibration_20260817.py
python3 scripts/run_profile_bridge_family_validation_20260817.py --phase pilot --n 80 --bridge-probability 0.1 --bridge-family half_normal
python3 scripts/summarize_profile_bridge_family_validation_20260817.py
python3 scripts/run_profile_bridge_family_nuisance_20260817.py --phase confirmatory --bridge-family uniform
python3 scripts/run_mad_ratio_crossvalidation_20260817.py --design external --n 80 --scenario independent_t5
python3 scripts/run_nuisance_jacobian_20260817.py
python3 scripts/summarize_nuisance_jacobian_20260817.py
python3 scripts/audit_mad_convention_20260820.py
python3 scripts/audit_external_math_review_20260821.py
python3 scripts/run_followup_simulations.py
python3 scripts/run_multi_extreme_simulations.py
python3 scripts/run_near_zero_boundary.py
python3 scripts/run_large_scale_simulations.py
python3 scripts/run_feedback_checks.py
python3 scripts/run_high_replication_checks.py
python3 scripts/run_variant_comparison.py
python3 scripts/run_calibrated_subgroup_simulations.py
python3 scripts/run_lower_target_calibration.py
python3 scripts/run_lower_target_l1_calibration.py
python3 scripts/run_sample_size_sensitivity.py
python3 scripts/build_stable_reporting_tables.py

If using the Codex bundled runtime on this machine:

/Users/jialiangyao/.cache/codex-runtimes/codex-primary-runtime/dependencies/python/bin/python3 -m unittest discover -s tests
/Users/jialiangyao/.cache/codex-runtimes/codex-primary-runtime/dependencies/python/bin/python3 scripts/run_pilot.py
/Users/jialiangyao/.cache/codex-runtimes/codex-primary-runtime/dependencies/python/bin/python3 scripts/run_outlier_influence.py
/Users/jialiangyao/.cache/codex-runtimes/codex-primary-runtime/dependencies/python/bin/python3 scripts/run_outlier_repeated.py
/Users/jialiangyao/.cache/codex-runtimes/codex-primary-runtime/dependencies/python/bin/python3 scripts/run_followup_simulations.py
/Users/jialiangyao/.cache/codex-runtimes/codex-primary-runtime/dependencies/python/bin/python3 scripts/run_multi_extreme_simulations.py
/Users/jialiangyao/.cache/codex-runtimes/codex-primary-runtime/dependencies/python/bin/python3 scripts/run_near_zero_boundary.py
/Users/jialiangyao/.cache/codex-runtimes/codex-primary-runtime/dependencies/python/bin/python3 scripts/run_large_scale_simulations.py
/Users/jialiangyao/.cache/codex-runtimes/codex-primary-runtime/dependencies/python/bin/python3 scripts/run_feedback_checks.py
/Users/jialiangyao/.cache/codex-runtimes/codex-primary-runtime/dependencies/python/bin/python3 scripts/run_high_replication_checks.py
/Users/jialiangyao/.cache/codex-runtimes/codex-primary-runtime/dependencies/python/bin/python3 scripts/run_variant_comparison.py
/Users/jialiangyao/.cache/codex-runtimes/codex-primary-runtime/dependencies/python/bin/python3 scripts/run_calibrated_subgroup_simulations.py
/Users/jialiangyao/.cache/codex-runtimes/codex-primary-runtime/dependencies/python/bin/python3 scripts/run_lower_target_calibration.py
/Users/jialiangyao/.cache/codex-runtimes/codex-primary-runtime/dependencies/python/bin/python3 scripts/run_lower_target_l1_calibration.py
/Users/jialiangyao/.cache/codex-runtimes/codex-primary-runtime/dependencies/python/bin/python3 scripts/run_sample_size_sensitivity.py
/Users/jialiangyao/.cache/codex-runtimes/codex-primary-runtime/dependencies/python/bin/python3 scripts/build_stable_reporting_tables.py

1. How stable is raw c_delta as a function of sample size?
2. Does pairing-normalization reduce sample-specific scale effects?
3. How often does the permutation test reject under null, aligned, inverted, nonlinear, heavy-tailed, skewed, and contaminated settings?
4. How wide are bootstrap intervals across these settings?
5. Which scenarios separate c_delta from Pearson/Spearman-style association?
6. When does a single extreme value define a shared divergence structure rather than merely destabilizing the statistic?

• Add h-star based outlier assessment before robustifying c_delta.
• Treat zero-divergence cases as "undetermined due to data limitations" in reports rather than as computational errors.
• Compare matched, mismatched, and one-sided extreme observations to study when a single observation defines shared divergence structure.
• Map power curves across smaller sample sizes and test heavy-tailed or skewed background distributions.
• Study whether multiple co-occurring extreme observations reduce the small-sample permutation resolution problem observed for a single dominant matched pair.
• Add L1/Gini and rank-based variants.
• Add weighted pairwise distances after defining a principled weight function.
• Add comparisons with energy distance and MMD.
• Add machine-learning examples, such as comparing dispersion structures in embedding dimensions, model residuals, or representation clusters.