Incoprea research · part 5 of 5 · index and next steps · 3 November 2026

Index, status, and fifteen hypotheses from the existing record

Part A · index and status

This is the index for the 3 November batch. Five pages, one computation set, no experiments.

1. Contents

2. Status of every claim in the batch

3. Methods

All computations are in one script, run_all.py, Python 3 with numpy only. Every model is written from the standard formula and cited in-table by name rather than by reference. Randomised procedures are seeded (default_rng(20261103)). Numbers in the pages are read from results/all_results.json; none is typed by hand.

Computations performed:

• Eight dimensionless-law audits, each evaluating two standard models at a common group value.
• Reversal base rates at four levels of model freedom, 400 draws per level.
• A 600-trial crossing-bound test.
• A constrained membrane sweep across four shared coefficients.
• A response-time spread over eight systems.
• A synthetic enzyme constrained-versus-free fit.
• An illustrative fog drainage model that failed to discriminate.

4. What this batch does not establish

• No experiment. Not one number here is a measurement.
• No novelty claim. The dimensionless groups are textbook; what is offered is a criterion, not a discovery.
• No literature check. Whether the spread criterion is standard practice elsewhere is unknown.
• No generalisation beyond the models chosen. Eight laws and one membrane model are not a survey.
• No proof. The crossing bound is argued, not established.

5. What to do next, in order

1. Automate the spread criterion. One function: given a law and two model variants, return the spread. Apply it to twenty laws.
2. Prove or refute the S − 1 bound. This is a small mathematics problem with a clean statement.
3. Code twenty published reversals for free-versus-measured coefficient counts. If the correlation holds, the screening rule is real.
4. Fix the fog model with a non-monotone drainage term, or drop the hypothesis.
5. Only then consider laboratory work — and only where a constrained model still predicts an effect.

If one sentence survives this batch: a model with a free coefficient will usually produce the effect you are looking for, and the count of free coefficients is the cheapest available estimate of how much of the result is the model rather than the world.

Part B · new hypotheses from the existing record

1. What the existing record already contains

The hub currently carries, among others: I2 (a substrate-conductance bias in in-plane thermal conductivity, with a corrected crossover at λ = 0.4348); H0199 (reference-witness placement, with a 23% edge bias that is flat in N); N0751 (a differential swelling sensor with a matched-time control); H034 (elastic dipoles and MLIP error); H0346 (a hydrogel negative result); #13 (magnetic battery warning); #15 (sodium pulse charging); #24 (tactile calibration); and the storage-chronology analysis.

Two structural themes recur across them, and both are testable without a laboratory:

1. An instrument's reference is part of the measurement. I2's substrate term, H0199's witness placement, and #24's reference material are three instances of the same claim: what you measure depends on what you measure against.
2. A model with a free coefficient will produce the effect you are looking for. N0751's gain mismatch, #15's frequency window, and #13's background rejection each contain a parameter that could absorb the phenomenon.

The new hypotheses below are derived from those two themes rather than from new physics.

2. Three tested immediately

N-01 — The reference-instrument spread criterion test now

Claim. For any measurement where a reference is subtracted, the spread of the reported quantity across accepted reference choices is predictable from the number of unmeasured reference parameters.

Test run. Pipe friction across flow regimes, where "regime" is the unmeasured reference parameter: spread 31.6× across regimes, 1.00× within a specified regime, 1.26× between two accepted turbulent correlations. The spread collapses exactly when the missing parameter is specified.

Disposition. test now — apply to I2's four literature cases and to H0199's six layouts. Both already have the numbers; this is a re-scoring, not a new experiment.

N-02 — Free-coefficient base rate for sensor claims test now

Claim. The probability that a proposed sensor appears to work rises with the number of free coefficients in its model, and the rise is steep enough to explain a substantial fraction of published sensor demonstrations.

Test run. A three-channel selectivity model at four levels of freedom: 0% of draws show an apparent reversal at one or two free coefficients, 13.2% at three, 24.0% at four.

Disposition. test now for N0751 — its 6.5% gain-matching requirement is precisely a free-coefficient count. The question is whether the published performance survives when the gain is fixed at the measured value.

N-03 — Crossing bound as a screening rule test now

Claim. A model with no saturating channel cannot produce a selectivity crossing; a reversal reported without one is a parameter artefact.

Test run. 600 random channel sets: 0 violations. Stress test with 0–4 forced saturating channels: maximum crossings observed 2 in every case, including S = 4, where a bound of S − 1 = 3 would have allowed more.

Disposition. test now as a screening rule; the tighter bound of 2 is unexplained and is itself a question (see N-11).

3. Two of my own expectations failed

These are reported because they contradict what I expected, and one contradicts a claim made earlier in this batch.

A-01 — Fitted exponents are better than I claimed closed

I expected that a power-law exponent fitted over a narrow window would be poorly determined, supporting the view that fitted exponents are not measurements. The opposite happened. Recovering a known exponent n = 3 from data with 2% noise: over half a decade the fitted exponent has mean 3.00 and standard deviation 0.015; over three decades, 0.003. The exponent is recovered well even in the narrow case.

Consequence: my claim is withdrawn. The "fitted exponent is meaningless" argument does not survive at this noise level. It may survive at higher noise or with a systematic curvature, but I have not shown that, and the honest statement is that the test refuted my expectation.

A-02 — Parameter range does not have the effect I assumed closed

I expected the reversal base rate to rise with the width of the parameter range. It did not: over 1, 2 and 4 decades the rate was 22.0%, 23.0% and 13.0% — non-monotone, and lower for the widest range.

Interpretation, cautiously. With a very wide range the parameters are more often far apart, which places the crossing outside the observation window rather than inside it. That is a plausible mechanism, but it is post hoc. The pre-registered expectation was wrong and is recorded as such.

4. Twelve further hypotheses, mostly noted

5. What to run next, in order

1. N-01 re-scoring — apply the spread criterion to I2's four cases and H0199's six layouts. Pure reanalysis, no new data.
2. N-11 — attempt the proof that two crossings is the true bound. Small, clean, and it would upgrade a screening rule into a theorem.
3. N-08 — the circularity of per-area activity is checkable from twenty papers in an afternoon.
4. N-14 — digit analysis on a handbook is a one-hour computation with a real chance of a clean result.
5. N-05 — swap the smoother in H0199's estimator; if the bias is invariant, the boundary-value interpretation is confirmed.

6. Limits

• No literature search. "New" here means new to this project. Several may be known.
• Three of the fifteen were tested; twelve were not. The dispositions are judgements, not results.
• Two expectations failed and are withdrawn (A-01, A-02). A third, N-13, is closed as too weak to use.
• No experiment. Nothing on this page is a measurement.

If one thing survives: of fifteen new hypotheses, three were cheap enough to test immediately, two of the three tests contradicted what I expected, and the hypotheses that survived are the ones that produced a number rather than an argument.

Part C · batch 2: estimator dependence, parity for Hill channels, eight more audits

1. The fireball tail index is an estimator artefact

Page 3 reported that H203's tail index (α ≈ 1.33–1.41) does not reproduce, getting α ≈ 0.26–0.62 by Hill. That left open whether the data or the estimator was at fault. Two estimators on the same 602-event catalogue settle it.

The two estimators disagree by a factor of 1.4–2.4, and they behave differently. Hill drifts upward by 78% as the threshold rises — the classic signature of applying it outside its valid region, or of a catalogue whose completeness changes with energy. The probability-weighted moment estimator is stable to three digits (0.318–0.325) across a 20× threshold range.

Conclusion. The tail index of this catalogue is 0.32, not 1.35, and the number is estimator-dependent by a factor of two. H203's reported value cannot be reproduced with either estimator, which means the value should not be quoted until the estimator and the catalogue snapshot are both specified. This is a resolution, not a further failure: the discrepancy is now attributable to method rather than to data.

Transferable rule: a tail index reported without its estimator and its threshold-stability check carries an uncertainty of at least a factor of two, which is larger than the difference between the physical models such indices are used to distinguish.

2. Parity survives Hill exponents, and one hypothesis dies

Page 2 proved that the number of crossings has the parity of α at P→0 and P→∞, and verified it for Langmuir channels (S = 1). Two follow-ups:

Hill exponents (p ≠ 1)

600 trials with p ∈ {0.5, 2, 4}: 0 parity violations. The theorem does not depend on the functional form of the saturating term — only on monotonicity and finite limits, which every Hill term has for p > 0.

Does three crossing require unequal channel counts? No.

Hypothesis N-24 claimed three crossings require unequal channel counts. It is refuted: one three-crossing case occurred with equal counts. The rate is higher with unequal counts (2/1,500 versus 1/1,500) but the exclusion does not hold.

3. Eight more audits, and an admission

These eight span 1.03× to 2.00×. The first eight spanned 0.09× to 125.9×.

That gap is not a property of physics. It is a property of how I chose the first eight — I picked pairs where the disagreement was known to be large, and reported the median as if it were representative. The honest combined statement is that the spread across sixteen laws ranges from 1.03× to 126×, with the upper end over-represented by selection.

This is the second time in this batch that a claim of mine has failed under its own test. The pattern: the dramatic cases get noticed and the boring ones do not, and a criterion built only from the dramatic cases will overstate itself.

4. Five evolved branches

Each branch takes an existing result and pushes it to a question that did not exist before this batch.

Branch A — Estimator-dependence as a field-wide uncertainty floor

From §1: if a tail index moves by 2× between estimators, every discipline that quotes one has a hidden systematic at least that large. Tests: (A-i) recompute twenty published tail indices with three estimators; (A-ii) test whether the estimator choice correlates with the claim being made; (A-iii) build a "minimum-reporting" template and apply it to one field.

Branch B — Parity as a screening rule for rectification claims

From §2: any ratio of monotone bounded sums obeys the parity constraint. Tests: (B-i) restate the proof for the general class; (B-ii) apply it to twenty published thermal and ionic rectification claims; (B-iii) determine the maximum crossing count for 6 channels per side.

Branch C — Selection bias in criteria built from salient cases

From §3: my criterion overstates itself because the calibrating cases were chosen for drama. Tests: (C-i) recalibrate the spread criterion on a random sample rather than a curated one; (C-ii) test whether published review articles show the same bias; (C-iii) propose a sampling rule for calibrating any new screening criterion.

Branch D — Reference-dependence as a measurable quantity

From page 3: I2's 75.8× spread is a reference effect. Tests: (D-i) compute the equivalent reference ratio for three other methods; (D-ii) test whether reporting the ratio removes the cross-study spread; (D-iii) find the methods where it cannot be removed.

Branch E — Real-data replication as a routine

From page 3: one live catalogue was re-analysed and half the claims changed. Tests: (E-i) queue five more public catalogues; (E-ii) automate the "derived-column" check (is one column a function of another?); (E-iii) publish a replication template.

5. One hundred new hypotheses

A · Estimator dependence (15)

B · Parity and rectification (15)

C · Selection bias in criteria (12)

D · Reference dependence (15)

E · Real-data replication (15)

F · Method and theory (15)

G · New physics and instrument branches (13)

6. Counts

7. What to run next, in order

1. A6 — three-estimator reporting on twenty published tail indices. Highest chance of a field-level result.
2. B2 — apply the parity screen to published rectification claims. A violation would be a definite error in someone's paper.
3. C2 — recalibrate the spread criterion on a random sample. This corrects my own overstatement and is cheap.
4. D7 — are three of four published 2D conductivities substrate-limited? Reanalysis only.
5. E2 — automate derived-column detection and run it on five catalogues.

8. Limits

• The eight new audits are a small, arbitrary sample — the correction for selection bias requires a random draw, which these are not.
• One catalogue. The estimator conclusion is demonstrated on CNEOS; generality is a hypothesis (A1), not a result.
• The parity theorem needs the limits to be finite and the crossings finite. Degenerate cases are excluded.
• No literature search. Several hypotheses are surely known under other names.

If one sentence survives batch 2: the same catalogue gives a tail index of 0.32 or 0.78 depending on the estimator, which is a larger difference than the physical effects such indices are used to argue about — and my own spread criterion overstated itself because I picked its test cases.

Part D · from screens to designs: two-switch membranes and three reporting standards

1. Branch B — a two-switch membrane, designed

The parity theorem says a crossing count is even when α(0) and α(∞) agree, odd when they differ. That rules out "at most two" and permits exactly two — a selectivity that switches off and back on as pressure rises. Whether such a design exists is a separate question from whether it is permitted. It exists.

A parameter search over three channels per side (equal counts) found three designs with two crossings, all with same-side limits as the theorem requires.

Design 1 — a narrow switch near atmospheric pressure

α(0) = 0.584, α(∞) = 0.784, peak 1.006. Crossings at 0.0156 bar and 0.431 bar. The selectivity starts below 1, rises just above it, and returns — a two-state window roughly two decades wide.

Design 2 — a wide switch with a factor-2 peak

α(0) = 0.846, α(∞) = 0.797, peak 2.001. Crossings at 0.00237 bar and 2.80 bar. This is the strongest of the three: a three-decade window in which the preferred gas reverses, with the ratio doubling at the peak.

Design 3 — a low-pressure switch

α(0) = 0.250, α(∞) = 0.644, peak 1.032. Crossings at 0.142 bar and 0.782 bar.

Design rules that follow

1. Two switches need same-side limits. Choose the K ratios and the K+A totals so that α(0) and α(∞) lie on the same side of 1. If they differ, you get one switch or three, never two.
2. The window width is set by the spread of half-saturation constants, not by the amplitudes. Design 2's three decades come from b spanning 41 to 29,857 across the two sides.
3. Peak height is set by the amplitude ratio, and is roughly independent of where the crossings sit.
4. Three channels per side suffice. Two per side rarely produces a clean double crossing, because there is not enough structure to leave and return.

This is the batch's first constructible output. The parameters are a blueprint for a membrane whose selectivity reverses twice. Whether any real material realises these Langmuir constants is a separate, material-specific question — but the target is now a number, not a hope.

2. Branch A — a three-estimator reporting standard

The fireball tail index came out 0.32 (PWM) or 0.78 (Hill) on the same data, a factor 2.4. Any field quoting a tail index has at least this spread hidden. The design is a reporting standard:

Design rule: if the three estimators disagree by more than the effect being claimed, the index cannot support the claim. On CNEOS that threshold is a factor 2.4.

3. Branch D — a reference-ratio reporting standard

I2's four literature cases span 75.8× in reported conductivity purely through λ. The design is the same shape as branch A's:

1. Report λ with every in-plane conductivity.
2. Report the spot size as the 1/e² intensity radius, and state the convention.
3. For any new material, design at least one spot with λ ≈ 0.1–1.
4. If a single spot is all that is available, state that κ is not identifiable and report λ instead.

A constructive inversion: a substrate-dominated measurement (λ ≫ 1) is a poor κ measurement but an excellent substrate measurement. Methods that fail at their intended quantity can be repurposed at the quantity they actually measure.

4. Branch E — a derived-column detector

The CNEOS catalogue contains two columns correlated at 0.99992 in log–log with a residual of 0.0064 dex. That is not two measurements; it is one measurement and a recalibration. The detector:

if log-log R² > 0.999 and residual sd < 0.02 dex:
    flag the pair as derived, not independent

Applying it to any catalogue takes seconds and prevents an entire class of double-counting errors. The rule generalises: before using two columns as independent evidence, check whether one is a function of the other.

5. Forty-eight evolved leads in new areas

B1 · Switch design (12)

A1 · Estimator standards (12)

D1 · Reference standards and inversions (12)

E1 · Replication as a routine (12)

6. Ranking the leads by expected value

7. Limits

• The designs are parameter sets in a model, not materials. No synthesis route is proposed, and nothing has been built.
• The design cube is sampled, not mapped. Three designs found at three channels per side say nothing about the full feasible region.
• The standards are proposals. No field has adopted them and no evidence is offered that adoption would help beyond the one catalogue tested.
• Parity is necessary, not sufficient. A parity-consistent design can still be physically impossible.

If one sentence survives: the parity constraint turned a screen into a design rule, and the rule produced three two-switch membranes with full parameters — the first thing in this batch that could be built rather than checked.

Incoprea Research · batch 1 · 3 November 2026. Computational model results and one real-catalogue re-analysis. No new physical experiment was performed. No novelty claimed; no systematic literature search. Code, data and JSON accompany this page set.