4 November 2026 · late · the fifteen near-proof dossiers

Thirteen of fifteen checked; two corollaries are wrong

The Nov3 release archive carries all fifteen dossiers. Thirteen reduce to arithmetic or simulation; two do not (NP-05 cites Kesten–Stigum, NP-08 is labelled a conjecture and says so). All thirteen core claims hold. Two derived corollaries do not.

Error 1 — NP-04 squares the wrong quantity

The dossier derives D ≥ σ²N^(−2/d), takes square roots to get an RMS error of σN^(−1/d), and then states that halving the RMS error costs 2^(d/2) more antibodies, citing 32-fold in d = 10.

Halving the RMS error costs 2^d. In d = 10 that is 1024-fold, not 32. The 32 figure is what halves the *squared* error — the exponent got divided by two when it should have been doubled. The substitution step immediately above it is correct, which is what makes the slip easy to miss.

Error 2 — NP-10 states the asymptotic backwards

The dossier gives C(τ) = c/τ + 2d·Φ(−a/(σ√τ)), derives the optimum correctly, and then says “for small c/d, τ* ≈ (cσ/(da))²”.

The asymptotic holds for large c/d, not small — the opposite regime, off by nine orders of magnitude at the small end of the stated range. The reason is internal: the approximation assumes the tolerance argument z = a/(σ√τ) is small at the optimum, and that is only self-consistent when the calibration cost is large relative to the out-of-tolerance cost. So the scaling τ ∝ c² is right and the coefficient should be 2π (the dossier omits it, harmless); the domain of validity is inverted.

One correction to this entry while writing it: three of the four failures in the first run were bugs in the checking code (a Voronoi boundary filter, an unconstrained least-squares fit, an inconsistent test value), not in the dossiers. They were fixed before anything was reported. NP-09’s CV of 0.526 is from twelve simulated tessellations of 3 000 points with boundary cells excluded.

4 November 2026 · late · the audit’s own record

Three corrections to this audit

An outside check that reports only the errors it finds in its host is not reporting. This entry lists every claim this audit has had to withdraw, and what replaced it.

Three withdrawals against roughly forty checks. Two of the three share a signature that is worth naming, because it will recur in any audit of this kind: the auditor reads the summary layer and not the source layer. The I2 case came from a table of numbers rather than the defining expression; the Nov3 case came from an index rather than the archive. Both are cases where the correct object was one link away.

The countermeasure that actually worked was arithmetic. In two further cases this session — a magnetic field that looked 1000× too small, and a ranging bound that disagreed with its own Monte Carlo — the discrepancy was traced by recomputing from first principles rather than by re-reading, and both times the archive was right. A check that cannot be reduced to arithmetic is a comment, not a check.

4 November 2026 · evening · Blind Spots R02 and R03

One real error, one accusation withdrawn

Two arithmetic claims in the blind-spots collection were flagged by the earlier audit pass. Checking them properly splits them: one is wrong, and one is right and the audit was wrong about it.

R03 — the crossover is at λ = 0.43, not 1

The page states the standard fit returns κ_app = κ/[e^λE₁(λ)], “which crosses unity at λ = 1”, and then, four lines later, “at λ = 1 the bias is +68 %”. Both cannot hold, and the second one is right:

So the ratio crosses unity at λ = 0.4348, and at λ = 1 it is already 68 % above it. The error propagates into the one number the claim turns on: the spot radius at the sign change is √(2κd/G) × √0.4348 = 0.381 µm, not the quoted 0.58 µm. The physical conclusion survives — 0.38 µm is still inside the operating range of a Raman thermometer — but the stated crossover and the stated radius are both off, and the page contradicts itself within four lines.

R02 — no error; the earlier flag was mine

The page says the charge-transfer resistance falls to 0.644 of its low-amplitude value at x = 1.95, and that the Bessel result G_app/G_true = 2I₁(x)/x is exact. An earlier audit pass reported these as inconsistent, on the grounds that 2I₁(1.9455)/1.9455 = 1.554, not 0.644.

They are consistent. 1.554 is the conductance ratio; the resistance ratio is its reciprocal, 1/1.554 = 0.6435. The page tabulates the resistance. The accusation is withdrawn — the only fault is that the page does not say which of the two quantities 0.644 refers to, which is what made it look wrong.

4 November 2026 · evening · E4-H160 delay precision

The √2 is right, and the open question has a number

The 1 November correction says the complex-noise Fisher information needs a factor of two, so the delay bound falls by √2, and it says correctly that single-target precision is a different question from two-target resolution. Both parts checked.

1 · The factor of two

Monte Carlo over 600 trials per point against the closed-form bound, for a 32-line burst with 16 Hz of bandwidth:

The simulation sits on the complex-convention bound to within 9 % at every SNR, and the real-convention bound is 41 % higher — exactly √2. The correction is right.

Worth recording: the first version of this check used a bound missing a factor of 2π, and the Monte Carlo disagreed with it by exactly that factor. The simulation caught the error, not the algebra — which is the argument for having both.

2 · Two targets, which the correction explicitly leaves open

Computed the six-parameter Fisher matrix — two delays, two unknown complex amplitudes — and compared the delay bound against the single-target one, as a function of separation measured in units of the record’s resolution 1/bandwidth:

The inflation is independent of SNR, because both bounds scale as 1/SNR — so the cost of resolving a close pair is a pure SNR multiplier, the square of the inflation. Two targets a tenth of a resolution apart cost about a hundred thousand times the single-target signal-to-noise. That is not a correction to the single-target result; it is a different regime, and it is why the scope note was right to separate them.

For any dataset quoted as “single-target delay precision”, the two-target number is therefore not a refinement — it is unavailable at any realistic power. The honest phrasing is the one already on the page: the precision result holds for one target, and says nothing about a scene.

4 November 2026 · evening · #24 tactile calibration

The arithmetic is right; one unmeasured number sets every headline

The dossier’s headline figures reproduce exactly: U(k=2) = 2.9 % of operating force on a matched bench, 9.5 % as-shipped, stiffness 13.9–16.5 %, bill of materials €3 751. The uncertainty budget is internally consistent — every expanded uncertainty is twice the root-sum-square of its listed terms, and the variance shares sum to 100 %.

The 9.5 % figure is one assumption wearing a measurement’s clothes. Hysteresis is modelled as a 3 % of full-scale play operator. That number is not measured for any sensor in the dossier — it is a plausible value. Across the dossier’s own parameter grid the answer spans 3.2 % to 31.1 %.

The contrast floor is exactly linear in that same assumption

Contrast floor = 6.4 × the hysteresis in % FS, to two decimals, with no offset. So “hysteresis destroys contrast below 19 %” is exactly “hysteresis = 3 % FS” restated. If the real sensor is at 1 %, the floor is 6.4 % and the statement is three times less alarming; if it is at 10 %, the floor is 64 % and the sensor cannot resolve the clinically interesting pairs at all.

The measurement that would settle it: one hysteresis loop on one sensor, at the intended loading rate. It is an afternoon on the dossier’s own €3 751 bench and it moves the headline by a factor of three either way.

4 November 2026 · evening · H203 impact-loss tail

Reproduces, and needs error bars

The 3 November round fits a power law to the CNEOS fireball catalogue and derives an impactor size exponent from it. Re-pulled the live catalogue today (1 074 events) and reproduced the fit from the impact-e column, which is the one in kt and the one the round used — bin counts match to within catalogue drift since 3 November.

The result holds. The tail is consistent with a single power law at every threshold (KS p from 0.19 to 0.79), and there is no significant drift of the exponent with threshold, so the choice of cut is not manufacturing the shape. The size exponent that follows, 3 × 0.96 ≈ 2.9, matches the canonical impactor size distribution.

On the second catalogue: still absent. The velocity column allows an internal check of the mass–energy scaling instead — the correlation between log velocity and log energy is −0.007, i.e. velocity carries no information about energy in this catalogue, which justifies the pure mass-scaling used to turn the energy exponent into a size exponent. That is a consistency check within one catalogue, not an independent replication, and the difference matters.

I could not establish from the round’s text what the third derived column represents, so I make no claim about it. Everything above concerns the energy-tail exponent and the size exponent only.

4 November 2026 · evening · H0199 and N0751

Two loose ends, closed

H0199 — the design-optimisation thread is retired

An earlier optimisation found that carefully placed boundary-only witness designs perform almost as well as freely placed ones (0.130 against 0.083 in predictive error). That looks like a contradiction of the 22.9 % boundary-witness failure, and it is not.

The optimisation assumes the field is a draw from a Gaussian process with a known covariance. Under that assumption boundary samples necessarily carry information about the interior — that is what the covariance means — so the calculation cannot exhibit a boundary blind spot for any field. Putting three designs and six field families in one table makes the point: the gap between boundary and free designs does not track the boundary contrast C at all, and the boundary-null case that the rule was built on comes out at a ratio of 1.03.

So the optimisation result should be cited as neither a contradiction nor support. The design rule stands on the estimator-level factorial, which used the dossier’s own estimator against actual field families — and that result is unchanged. This entry exists so the optimisation number is not read as evidence against the rule by the next person who finds it.

The random-field normalisation does not need repairing

The site records that the supplied random-field generator “needs repair” because it normalises by the realised maximum. Tested over eight draws, the opposite is true of the proposed fix:

Normalising by the standard deviation makes the fields stronger and leaves them equally variable in relative terms. What needs fixing is reporting, not the generator: quote C beside every RMSE so the reader knows how hard that draw was. No normalisation can equalise difficulty, because difficulty is the boundary contrast, not the variance.

N0751 — drive the sensor with a square wave at f*, and never with a ramp

The dossier specifies the instrument and the validation protocol but not the stimulus. With τ = (20, 60) s, a 480 s record and drift profiled out, the Cramér–Rao bound on Δτ:

A single step — the natural calibration choice — costs a factor of three, because half the record is spent on an already-decayed response. A slow ramp carries almost no differential signal at all and tests nothing; if it appears in the held-out set it should be treated as a null test rather than a signal test. The square wave is also what the matched-time control already needs, so adopting it costs nothing.

Absolute precisions here are optimistic because drift is profiled out exactly; the earlier drift analysis showed real drift must stay below 0.7 % of the gain. The ranking is the result, not the magnitudes.

4 November 2026 · afternoon · #13 magnetic warning

Checked, and it holds

The forward model is correct and every budget formula checks out. A 10 mA through-plane filament gives 0.48 nT at 3 mm; an independent Biot–Savart recomputation at the reported peak gives 0.59 nT. The required-rejection, balance and warning-time formulas all reproduce from the dossier’s own tables.

One reframing. The dossier describes itself as “held hostage by one geometric unknown”. It is not: sensitivities enter logarithmically, so the full 400× spread in return-path geometry moves the required growth constant only from 86 s to about 50 s. The binding unknown is whether a developing soft short has a growth time constant of tens of seconds at all — a cell-level measurement, not a magnetometry one. The next experiment is a controlled soft-short test, not a sensor bench.