Two corrections, before either pre-registration is filed

Both protocols are described as ready to file. Each has one defect that would waste the study. Neither is a design flaw — the designs are the strongest methodology in this corpus — and neither protocol is edited here. What follows is the arithmetic and the recommended replacement text; the registered values are the author's to set.

A note on trust. The D1 figure below is the third one produced for this defect tonight. An earlier review said "8.1 standard errors"; a first check said 2.77×; this says 3.92× and 11.4 standard errors. The first two were derived from a summary. This one is derived from the protocol's own sentence, and the derivation is shown line by line precisely so you can check it rather than take it. If it is wrong, the working is right there to be attacked.

---

D1 — prereg-01: the bar is an individual-level quantity, the test estimates a mean

What is registered

Two clauses, and they are on different scales.

The bar (§ Analysis Plan):

"The registered bar is that the active-minus-sham contrast must exceed a pre-registered drift ceiling, defined as 1.96 × the within-participant SD of the sham-only group's session-to-session ΔH."

The power calculation (§ Sample-size rationale):

"Alpha: 0.05 (two-tailed). Power: 0.80. Target effect: Cohen's d = 0.5 on the paired contrast → N ≈ 34."

The arithmetic

Both the sham-only ΔH and the active-minus-sham contrast are differences of two sessions, so both carry the same standard deviation. Call it S.

bar as an effect size    = 1.96·S / S            = 1.96
powered effect size                              = 0.50
ratio                                            = 3.92x

That understates it, though, because it compares two things that are not comparable. The bar is built from S, the spread of individual session-to-session drift. The test estimates a mean, whose precision is the standard error:

SE(mean) = S / sqrt(34) = 0.1715 S
bar      = 1.96 S       = 11.4 standard errors of the mean

The bar sits 11.4 standard errors from zero in a study powered to resolve 0.5.

What that does

from statistics import NormalDist
S_E = 1/34**0.5
print(1 - NormalDist().cdf((1.96 - 0.5)/S_E))    # 0.0

A true effect of exactly the size the study is designed to detect has, to floating-point precision, no chance of clearing the bar. The protocol would report it as "within measurement drift" and publish it as a refutation.

This is the reverse of conservative. It reads as caution — a high bar sounds rigorous — but a bar that a real effect cannot clear does not protect against false positives, it guarantees a false negative.

The defect is real, and it is a category error rather than a number

A 95% ceiling on individual drift is a perfectly sensible thing to want. It answers "could this participant's change be drift?" But the primary endpoint is a group mean, and the question there is "could this average change be drift?" — which is a bound on the mean, narrower by √N.

Three ways to fix it

Recommended: A. It preserves the protocol's stated intent — that significance alone is not enough, the effect must also be big enough to matter — while setting "big enough" at something the study can actually resolve. B is defensible but is close to the significance test it is meant to supplement, so it adds little.

C is not a bigger study — it is an unpowered one, and the earlier "N = 523" here was wrong. A ceiling fixed at 1.96 × the individual-drift SD does not shrink as N grows, while the mean it is compared against stays at the registered 0.50 S. Power against that ceiling is therefore decreasing in N, reaching at most 7.9% at N = 1, and the true effect required for 80% power falls only to 1.96 S in the limit — never toward 0.50 S. Option C is reachable only by re-designing the study around a target effect above 1.96 S, which is a different study rather than a larger one.

The withdrawn figure came from 34 × (1.96/0.50)² = 522.4576, ceiled to 523. That scaling answers a different question, and it multiplies the whole anchor when only one part of it may scale: 34 is a composite of 31.395519 (normal) + 1.971610 (Guenther z²/2) + 0.632871 (ceiling), so the spurious total is 38.0984 — exactly the gap between 522.4576 and the 484.3592 that the substituted question actually yields. If the intent was to report the cost of detecting a much smaller effect, the figure is 485 (exact one-sample t; the normal approximation gives 483) and it must carry the effect size it belongs to, d = 0.1276 — a quantity with no referent anywhere in the registered protocol.

Replacement text

The magnitude bar (noise floor), not just significance. Statistical significance of the paired contrast is necessary but not sufficient. The registered bar is that the mean active-minus-sham contrast must exceed 0.50 × the within-participant SD of the sham-only group's session-to-session ΔH — the effect size this study is powered to detect. A contrast that is "significant" but smaller than this is reported as within measurement drift and does not count as support for H1. This bar is fixed before unblinding.

Note on scale: the bar is a bound on the group mean, not on individual session-to-session drift. A 1.96 × SD ceiling would be the latter, and at N = 34 it sits 11.4 standard errors from zero — unreachable by any effect this design can detect.

---

E1 — prereg-02: the H1b null destroys the structure it should preserve

What is registered

H1b (§ Hypotheses):

"Day-to-day HRV of geographically co-exposed but socially unrelated participants correlates above the level expected under day-permutation."

The other confirmatory test, in the same document, registers something different:

"the storm-minus-quiet coherence contrast recomputed on ≥ 1000 circularly-shifted /phase-randomised Kp series"

So the correct null is already in the protocol. It is simply not applied to H1b.

Why day-permutation is the wrong null

HRV series are temporally autocorrelated — today resembles yesterday. Shuffling days independently destroys that autocorrelation, so the permuted series are less structured than real data. The resulting null distribution is too narrow, and the observed statistic — computed on data that does have autocorrelation — looks extreme by comparison.

A circular shift moves each series bodily in time. It destroys the alignment between participants, which is what H1b tests, while preserving each participant's own autocorrelation, which is not.

Measured

Simulated under H0 — twelve independent AR(1) participants, ninety days, φ = 0.6, no shared driver at all, so every rejection is a false positive. 300 simulations, 400 permutations each, α = 0.05, statistic = mean pairwise Spearman correlation.

The registered null rejects a true null more than twice as often as it claims to. On these parameters H1b is not a 5% test, it is a 13% test.

An honest caveat on the fix

The circular shift is a large improvement and it is not provably perfect. At 7.0% over 300 simulations the standard error is 1.26%, so the result is consistent with correct sizing but does not demonstrate it — a residual inflation of one or two points cannot be ruled out from this run. Two things would settle it: more simulations, and parameters taken from pilot data rather than assumed.

The parameters here are mine, not the protocol's. The exact false-positive rate depends on the true autocorrelation of daily HRV, which the protocol does not state. The direction and rough magnitude are robust — any positive autocorrelation makes day-permutation anti-conservative — but the specific 13.0% should not be quoted as a property of the study.

Replacement text

H1b (inter-participant synchronisation). Day-to-day HRV of geographically co-exposed but socially unrelated participants correlates above the level expected under a per-participant circular-shift null, computed as follows: for each of ≥ 1000 permutations, each participant's daily series is independently circularly shifted by an offset drawn uniformly from 1 … (n_days − 1); the test statistic (mean pairwise Spearman correlation across participants) is recomputed on the shifted set; the observed statistic's percentile within that distribution is the inferential quantity. The shift preserves each participant's own temporal autocorrelation while destroying inter-participant alignment, which is the structure under test. A day-permutation null is not used here: it destroys autocorrelation as well as alignment, yielding a null distribution narrower than the data and a test that over-rejects.

What it costs

A correctly-sized null is less likely to reject, so some power is given up. That is the point — the power the day-permutation null appeared to have was not real, it was the over-rejection. Quantifying the loss needs a specified alternative, which the protocol does not give for H1b; if you fix an expected synchronisation effect, this can be simulated the same way.

---

What neither review caught

In prereg-01, the bar and the power calculation are in different sections — the bar in the Analysis Plan, the power in the Sample-size rationale. Nothing in either points at the other. Whatever bar is chosen, a single sentence in the Analysis Plan stating its relationship to the powered effect size would make a recurrence impossible.

In prereg-02, the same document uses two different nulls for two confirmatory tests without saying why. Even after the fix, one line explaining that both now use circular shifts, and why that is the right choice for autocorrelated series, is worth adding — it is the kind of thing an OSF reviewer asks about.

---

Framework: Thomas Frumkin (@teslasolar), Konomi Systems. These corrections: V>>, with Claude Opus 5. Every figure reproduces from the code shown; the simulation seed is 20260822.