Whether solar and geomagnetic activity perturbs tropical cyclone (TC) dynamics has a long and contested observational lineage. Elsner and Kavlakov (2001) reported correlations between geomagnetic indices and per-storm intensity changes; Elsner and Jagger (2008) linked US and Caribbean hurricane counts inversely to sunspot number; Pérez-Peraza et al. (2008), Mendoza and Pazos (2009), Hodges and Elsner (2011) and Hodges et al. (2014) reported solar-cycle dependences in various basins, and Li et al. (2023) and Nayak (2024) extend and review the picture. Proposed mechanisms range from the cosmic-ray–cloud pathway (Marsh and Svensmark, 2000; Svensmark, 2007; Kirkby et al., 2011; Yu and Luo, 2014; Svensmark et al., 2016) to downward wave–mean-flow coupling (Huth and Stryhal, 2024) and ionospheric gravity-wave forcing (Prikryl et al., 2019). Against this stands an equally substantial null literature: Forbush-decrease cloud analyses find no robust response (Kristjánsson et al., 2008; Calogovic et al., 2010; Laken et al., 2012), the ion-induced enhancement of cloud condensation nuclei appears too weak to matter climatically (Pierce, 2017), and IPCC AR6 WGI (2021, chap. 7) reflects the consensus that galactic cosmic rays contribute negligible radiative forcing. Across two decades effect sizes are modest, mechanisms vary, and null controls are unevenly applied. We treat the question as open, and use it here as the setting for a methodological one.

Existing observational studies almost universally operate at the per-storm scale. A more recently proposed scope treats all the cyclones active in one time window as a single cloud of points in (latitude, longitude, intensity) coordinates and asks about its shape. The tool for that is persistent homology (Carlsson, 2009; Ghrist, 2008; Edelsbrunner and Harer, 2010): one grows a ball of radius r around every point, records the radius at which each hole in the resulting union opens and the radius at which it closes, and summarises the cloud by the list of those (birth, death) pairs. A worked example makes the idea concrete. Six storms whose tracks happen to encircle a quiet region of ocean leave a ring of points with an empty middle; the balls around them meet each other before they fill the middle, so a hole opens at the radius where neighbours touch and closes at the radius where the middle is covered, and the width of that interval is the one number the method keeps about it. A perturbation shared across many storms, if present, might change how many such holes the ensemble has and how long they survive, in a way no single storm's trajectory reveals.

Related randomisation two-sample tests for collections of persistence diagrams were introduced by Robinson and Turner (2017), using losses built from within-group pairwise matching costs, and later extended by Islambekov and Pathirana (2024). Our resampling construction below differs in form, but shares the same dependence on the chosen diagram distance. Robinson and Turner are explicit about which guarantee their test carries and which it does not: under the null the p-value is uniform, but they know of no theory that it will be small when the distributions differ. The exponent of the matching cost is a parameter of the procedure, not a quantity the data fix.

Three further bodies of work bound what follows. Stability theory does reach across a change of metric: Chazal et al. (2014) bound the bottleneck distance between the Vietoris–Rips and Čech diagrams of two totally bounded spaces by the Gromov–Hausdorff distance between them. What that bounds is the distance between diagrams, not the verdict a test built on those diagrams returns, and it is the verdict that moves here. Substituting an intrinsic distance for an ambient one has been done before: Beshkov and Tiesinga (2022) exchange the Euclidean metric for a geodesic one in the persistent homology of neural activity and recover different features under the two. And reporting a result over the set of defensible analyses rather than one selected from it is established elsewhere as specification curve analysis (Simonsohn et al., 2020) and multiverse analysis (Steegen et al., 2016), with post-selection inference supplied by Girardi et al. (2024). What this paper adds to those three is a single dataset on which the representation is fixed on physical grounds, the residual dependence on the remaining unregistered choices is measured rather than argued, and the specification-averaged verdict is reported in a setting where the specifications are topological rather than regression choices.

Several steps of that comparison are chosen by the analyst, and the method does not fix them. Where to place the points: the longitude coordinate is periodic, and three principled treatments of that periodicity exist, each with defenders. How to charge for a mismatch between two lists of holes: one may add the mismatches as they are or add their squares, and nothing in the method says which. Which points enter the fixed-size subsample, and which control diagrams form the reference set against which the event is measured. A reader handed a p-value cannot tell how much of it came from the data and how much from those steps, and the author often cannot either, because each is made once, early, and never varied. If they can move a verdict across the conventional threshold, then every ensemble-topology result in the applied literature carries an unquantified term. Invariance under them is thus a precondition: a pipeline whose verdict depends on how the trajectories are represented, without converging, is not yet ready to test the substantive hypothesis.

We establish three things on one dataset. We show that the input geometry can be fixed on physical grounds: replacing the three coordinate encodings by a great-circle distance on the sphere the storms live on removes the ambiguity of which geometry to trust and returns a single verdict where the encodings returned three. We measure what that repair leaves untouched, and demonstrate that it is partial – the verdict the physical distance returns still moves with the exponent of the matching cost (resampling p from 0.003–0.087), with which 600 of the ensemble's fixes enter the diagram, and with which fifty control diagrams form the reference set, three quantities that had been fixed without being registered. We report, third, a test that selects no exponent and averages over the subsample realisation, and we give its specification-averaged p-value for three widths of family.

The central statement is therefore a qualified one. A physically interpretable input geometry removes one arbitrary choice; the event-level verdict still depends on the diagram metric and on the finite-sample realisation, and a test that selects neither leaves the effect below threshold.

The vehicle is a cyclone-trajectory dataset with a clean structure for the purpose. We construct three encodings of the (lat, lon, wind) point cloud – a linear modular normalization that ignores periodicity, a unit-sphere embedding and a cylinder embedding – and apply the same downstream pipeline to the same 25-storm event set and 1020-storm control pool. Persistence is computed by the Vietoris–Rips construction, whose object is the clique complex of the proximity graph, in which a simplex enters as soon as all its vertices are pairwise within r; that complex is closely related to but distinct from the Čech complex the nerve theorem ties to the union of balls. Two persistence lists are compared by matching their holes and summing the cost of the matching, and the null is built by resampling control storms. All storm sets are held fixed across representations, so across-representation differences cannot arise from event or control selection. This analysis is observational, not controlled: we manipulate the representation and the resampling while leaving the physical system untouched, and what we report is within-pipeline robustness, not causal isolation.

Persistent homology summarises the multi-scale structure of a point cloud (Edelsbrunner and Harer, 2010; Carlsson, 2009; Ghrist, 2008; Wasserman, 2018), with an environmental-science primer in Ver Hoef et al. (2023). Over the Vietoris–Rips filtration, connected components (H0) and loops (H1) are born and die at scales whose pairs form the persistence diagram, which Cohen-Steiner et al. (2007) proved stable under perturbations of the input in a fixed input metric. One H0 class never dies, and that essential class is dropped from every diagram, event and control alike, before any distance is computed (finite_pd), so all H0 figures below are over the finite classes. We restrict throughout to H0 and H1; higher-degree homology is not computed. Neither channel has a literal physical counterpart – H1 features are not closed storm tracks, H0 components are not storm clusters – and both aggregate across storms in a way mean-intensity statistics do not.

We quantify differences between diagrams with the degree-1 Wasserstein distance W1, a complete separable metric on diagram space (Mileyko et al., 2011) that sums the cost over all matched pairs. The exponent is not incidental to what follows, so we state the implementation precisely. W1 is computed with persim.wasserstein (persim 0.3.8; Saul and Tralie, 2019), whose signature carries no exponent argument and whose returned value is the plain sum of the matched costs under a Euclidean ground metric. Earlier versions of this manuscript described the same quantity as a Wasserstein-2 distance – the variant that adds the squares of the matched costs and takes a square root – a description that misnamed the implementation while leaving it correct; Sect. S1 records the correction. Because the exponent turns out to change the verdict, we recompute the load-bearing results under the true degree-2 distance and under the exact bottleneck distance W∞, the latter with gudhi 3.12 (The GUDHI Project, 2015). The three are different metrics, not three points on one continuum: W∞ replaces the Euclidean ground norm by the sup norm and the sum by a maximum, so it should not be read as the p→∞ limit of the same family.

Each fix is a vector in (latitude, longitude, wind) space. Latitude rescales linearly to [0,1]; wind is WMO_WIND/200, clipped. The intensity channel is largely imputed: WMO_WIND is missing for 268 335 of the 406 059 satellite-era fixes, or 66.1 %, and a missing value is replaced by the median wind of the subset being encoded. That rule is itself a choice, and the verdict is sensitive to it: replacing the per-subset median by a single global constant moves the great-circle event p-value from 0.012–0.034. Neither rule is a natural standard, so we report both and treat the difference as part of the specification dependence quantified in Sect. 4.7. Longitude is periodic; three encodings are tested.

Persistent homology has recognised atmospheric rivers in gridded water-vapour fields (Muszynski et al., 2019), a diurnal cycle in single-storm cloud imagery (Tymochko et al., 2020) and weather regimes via attractor topology (Strommen et al., 2022); Ghil and Sciamarella (2023) review its wider use in the climate sciences, and Inatsu et al. (2017) come closest in subject, identifying individual cyclones from a superlevel-set filtration with a merge-tree reconstruction. Our scope – the joint point cloud of many storms' fixes – differs from each, and we put the encoding-invariance question at that scope.

For each representation the event diagram is compared against a resampling distribution of control diagrams by mean W1 distance to a reference set of fifty control diagrams; the null is the same statistic with each control diagram substituted for the event diagram, jackknifing the reference; and the resampling p-value is the fraction of null draws whose distance is at least the event distance. This is a Monte-Carlo empirical null obtained by resampling the control pool, not a label-permutation test: no labels are exchanged, and the draws are without replacement.

That statistic is one-sided: the pre-specified alternative is that the event ensemble lies farther from the reference set than the controls do, and this convention was fixed in the discussion-paper version and is not changed here. Because sidedness is a convention rather than a result, Sect. S10 gives the two-sided companion of every value on which a threshold statement in this paper rests, under both of the conventions available, and where a statement below turns on which side of α a value lies we name the convention it rests on. Each iteration draws n storms matching the event count and concatenates their fixes, so the resampling unit is the storm and within-track autocorrelation is preserved. Placebo false-positive rates are compared to nominal with exact-binomial tests and per-proportion Wilson (1927) intervals. The finite-sample correction (1+#{null≥observed})/(1+B) sometimes recommended for resampling tests changes no qualitative verdict and no placebo classification here; its size stays below 0.001 for the B=1000 event runs, reaching 0.0099 at the B=100 used per placebo and 0.002 at the B=500 of Sect. 4.3 and 4.4.

A resampling p-value estimated from B draws carries its own sampling error, and near a decision threshold that error is not negligible. At B=1000 the Wilson 95 % interval on an estimate of 0.037 runs from 0.027–0.051 and on 0.044 from 0.033–0.059: both contain 0.05, so at that resolution the statement that either lies below α is not separable from Monte-Carlo noise. We therefore recomputed the five load-bearing results at B=10000, holding the reference set fixed so that the estimand does not move with B (Sect. 3.6). The intervals tighten by roughly a factor of three and none now contains 0.05: linear 0.0343 [0.0309, 0.0380], sphere 0.0120 [0.0100, 0.0143], cylinder 0.1516 [0.1447, 0.1588], the basin-matched subsample-averaged great-circle result 0.0427 [0.0389, 0.0468], and the same under index-minimum event dates 0.0329 [0.0296, 0.0366]. Where a statement below turns on which side of α an estimate lies, it rests on the B=10000 value; everything else stays at B=1000, being internal comparisons in which every entry shares one resolution.

Three further additions relative to a single-run analysis are motivated by the fragility we find. (i) A fixed ordering, with Monte-Carlo uncertainty reported. The control-draw order is a free implementation choice; we report the placebo false-positive count as a distribution over six auditable orderings, a deterministic sort and five seeded permutations of it. Its width is largely Monte-Carlo (Sect. 4.2), so reordering a uniformly resampled control pool selects a different realisation while the estimand does not move; the durable requirement is therefore the narrower one, to fix the ordering by an explicit sort key so the run is reproducible and to report the Monte-Carlo uncertainty of the resulting p-value alongside its point value. (ii) Matched null. In addition to uniform control draws we draw controls preserving the event ensemble's per-window (seasonal) storm counts (11/9/5), its genesis basin, its genesis era in 5 year bins, and the joint basin-by-era composition (Sect. 4.5). (iii) Subsample averaging. Where a statistic carries a conclusion, it is averaged over M=10 independent subsamples of the event ensemble and of every control draw alike (Sect. 4.7).

The event statistic is the mean distance from the event diagram to a reference set of fifty control diagrams, and which fifty is itself a choice that was never registered. The reference set is drawn from the pool of null draws, so enlarging that pool changes it: recomputing the linear encoding at B=10000 without pinning it moved the event distance from 0.352771–0.349897 and the p-value from 0.0370–0.0338 – a change in the estimand, not a gain in precision. Every B=10000 result reported here therefore pins the reference set to the one the archived B=1000 run used. Drawing five further reference sets of fifty from the same pool, and changing nothing else, moves the linear resampling p-value over 0.036–0.047 against 0.037 for the archived set: a spread of the same order as the Monte-Carlo interval at B=1000 and, unlike that interval, one that more null draws do not reduce. It flips no verdict here, and a study whose estimate sat closer to the threshold could be moved across it by this choice alone. We record the reference indices with the results and recommend that future work register the reference set alongside the exponent and the subsample.

D1 pool: 25 event against 1020 control storms, B=1000. The 49-placebo calibration uses the same calendar windows at random years 1985–2020 outside event years ±2, B=100 each. Stratified attribution covers two basin cells and three single-event cells at B=500, corrected by the procedure of Benjamini and Hochberg (1995). Subsample-size sensitivity covers Nsub∈{400,600,800,1000}. Python 3.11; numpy, scipy, pandas, matplotlib; ripser 0.6.14 (Bauer, 2021); persim 0.3.8; gudhi 3.12 (see Otter et al., 2017, for a survey of persistent-homology computation). The encodings and the great-circle distance are switchable variants of one pipeline module, so all representations share the same selection and resampling code, and the library version does not affect the verdict: numpy 1.26 and 2.4 give bit-identical resampling p-values once the control order is fixed.

Every specification reported here is defined in one place and every artefact carries its own configuration. A specification record fixes the encoding, the exponent and ground metric of the matching cost, the null design and stratum, the control-draw ordering, the subsample size and count, the number of null draws, the reference-set size, the random seed, the imputation rule and the stratum-sorting rule. Output file names are derived from that record and never typed, and each output header records the resolved encoder function actually called, the SHA-256 of the input archive, the library versions and the code revision – the resolved encoder in direct answer to the failure of Sect. 3.3.4, in which a label and the implementation behind it had come apart. A verification script re-derives all 87 registered specifications from the archived data and compares each with the value printed here; all 87 agree to the precision at which they are reported. That check covers the resampling p-value of every registered specification and, at p=1 under the Euclidean ground metric, the archived event distance as well. It does not cover every number in this paper: Sect. S10 sets out what falls outside it, including the five values recomputed at B=10000 and eighteen of the thirty-six cells of the matched-null comparison of Sect. 4.5, and says where each is anchored instead.

Table 1 gives the pooled event-versus-control comparison under the three encodings and, for reference, under the physical distance of Sect. 4.5.

Three representations of the same 25 storms give three verdicts. Under the archived longitude convention the linear and sphere encodings cross α=0.05 and the cylinder does not; under the single convention only the sphere does. A single-encoding readout would report a positive signal or a null on the same data depending on which encoding was chosen and, for the linear encoding, on where the circle was cut. The relative structure is the more stable part: under every one of the six event-subsample seeds the sphere p-value is the smallest of the three and the cylinder p-value the largest, while the position of any of them relative to 0.05 is not reproducible, and the particular combination printed in the first three rows occurs in one seed of six. Section S6 gives the six seeds in full, together with the ENSO and solar state of every event and placebo window. An earlier single run reported 0.130/0.009/0.214 for these rows; Sect. S1 records why those values are superseded.

The 49-placebo calibration runs the full pipeline on 49 fake event-date sets at the same calendar windows in random years. Table 2 reports the pooled false-positive count in each homology channel as a distribution over equally valid control-draw orderings.

Every H1 ordering is nominal-compatible. The H0 spread is the wider of the two in absolute terms and its upper ordering crosses the nominal rate, so what distinguishes the channels is not that H0 is stable and H1 is not: the H1 verdict sits near α at every ordering while the H0 verdict is far from it at most. The reproducible pipeline is H1-nominal with a mild ordering spread, and an earlier single run's H1 count of 16/147, read at the time as an inflation, cannot be placed among the auditable orderings (Sect. S1). Much of even the 9–12 spread is finite-resampling noise: a per-placebo decomposition attributes roughly half to two-thirds of the cross-ordering movement to the B=100 term alone, so raising B would compress it. Neither pooled count is a set of independent trials – the three encodings share the same 49 dates – so the exact-binomial p-values understate the sampling uncertainty and are used only to place the counts relative to the boundary, which the per-encoding Wilson intervals independently support: all contain 5 %, at H1 1/49, 4/49, 4/49 against H0 2/49, 1/49, 2/49 on the deterministic ordering.

The ordering sensitivity co-occurs with a measurable difference between the channels. On the reproducible cache the coefficient of variation of the event-to-null distance is 2.0–2.2 times larger for H1 than for H0 and that of the null mean itself 3.9–4.4 times larger. Both are measured across placebos, so neither establishes that the H1 null is narrower within any one placebo; what they establish is that the H1 summaries move more from placebo to placebo. Alongside them sits a population of threshold-straddling placebos: 17 of the 147 combinations, 11.6 %, have a resampling p between 0.02 and 0.10 under either the published implementation or the deterministic one. Across three orderings on a matched null, the H0 p in fact swings marginally more than H1 (mean range 0.158 against 0.135); the H1 swing straddles α because the event distance sits near the upper tail of the H1 null.

Two candidate explanations do not account for it. Against the exact bottleneck distance over three orderings on a matched null, W1 gives comparable H1 totals (11/15/11 against 12/10/12), and per placebo the bottleneck has the larger cross-ordering range (mean 0.214 against 0.135), a sign test on the paired ranges rejecting equality at p=1.5×10-6: the exact bottleneck is if anything the more order-sensitive of the two. It is a different-metric control, changing the aggregation from a sum to a maximum and the ground norm from Euclidean to sup, and it retains matching to the diagonal, which our implementation constructs explicitly. Ambient dimension is likewise excluded by the 4-D linear control of Sect. 3.3.5, and two statistic-level remedies also fail to change the picture, an L2-persistence-landscape statistic (Bubenik, 2015) giving 12/147 and a z-score normalization of the event distance 14/147, against 9/147 for the sorted W1 baseline. These placebo counts are the pipeline's empirical rejection frequency under realistic historical variability, folding methodological behaviour together with the climate, era and basin variability of the placebo years.

Table 3 breaks the pooled verdict into two basin cells and three single-event cells.

No cell survives correction in any encoding. The most extreme cell is D2_WP in all three, at 0.048–0.142 uncorrected, which is a weaker localization than an encoding-dependent extreme would be: the three representations agree on which cell is least consistent with its null, and none of them puts that cell past correction. Halloween 2003, the canonical extreme, is null in all three at 0.248–0.338. Cell-level H0 p-values are above 0.18 everywhere. The pooled D1 verdict is not localizable to a coherent single-cell source under any encoding.

In Table 4 the linear encoding is monotonic in Nsub and strengthens at N=1000; the sphere and cylinder encodings are not monotonic and weaken there. We read the table as ordinary sampling variability of the H1 channel; it is not a size dependence, since the same event realization tested at different subsample sizes draws different point subsets, so each entry is one seeded sample. The N=600 row and the corresponding column of Table 1 differ because the two are computed at different resolutions, B=500 here against B=1000 there, on independently drawn nulls; the differences (0.048 against 0.037, 0.018 against 0.021, 0.112 against 0.156) are of the size the Monte-Carlo intervals of Sect. 3.5 predict. Section 4.7 replaces the single realization by an average over ten.

We replace the three encodings by the single great-circle-plus-intensity distance of Eq. (1) and repeat the D1 test and the calibration. Under λ=1 the H1 resampling p-value stays within [0.006,0.017] across three control-draw orderings without crossing α, and the placebo calibration is nominal across seven such orderings, with per-ordering H1 false positives of 2–4 of 49. On the axis on which the three arbitrary encodings disagreed, the physically grounded distance gives a single value. That is stability across control-draw orderings, one of the pipeline's two random choices; Sect. 4.7 shows it does not extend to the other.

The verdict depends on the intensity weight. With pure track geometry (λ=0) the event H1 is not significant (resampling p=0.157), and significance appears as the intensity channel is weighted up (0.157→0.062→0.012 for λ=0→0.5→1), so under this single subsample the difference is located in the intensity channel; Sect. 4.7 shows that after averaging over subsample realisations the gradient across λ largely disappears, so this localization holds for one subsample only. A related sensitivity has the same character: the imputation rule for the 66.1 % of missing wind values moves the same p-value from 0.012–0.034 (Sect. 3.3).

Substituting a distance intrinsic to the space the data occupy for an ambient embedding is not a new action. Beshkov and Tiesinga (2022) replace the Euclidean metric by a geodesic one in the persistent homology of neural population activity and recover different features under the two. What differs here is that the intrinsic distance is fixed by the geometry the storms move on rather than estimated from the data, so the substitution removes a coordinate choice without introducing an estimated one.

A residual difference remains, of undetermined cause, and its survival is conditional on the metric. Table 5 gives it under four matched-null designs and three metrics.

Under W1 the difference survives all four matchings, non-monotonically and informatively so: matching basin alone sharpens it, matching era alone weakens it the most, and the joint match sits between, pointing to era over basin as the principal confounder. Those twelve verdicts are one-sided (Sect. 3.5), and the convention decides two of them, both era-matched, so that under the more conservative reading the difference survives three of the four designs and fails in the one already weakest; Sect. S10 gives the companion values under each convention. Under the true W2 and the exact W∞ none of the twelve cells reaches α, though the event lies between the 68th and the 87th percentile of the control distribution in every W∞ cell, and the era-matched design is the weakest of the four under both. The residual is therefore specification-conditional; it is not a metric-robust finding.

Three considerations preclude attributing that residual to solar activity even where it survives: it is confined to the intensity channel, being null for pure geometry; it is partly an era effect, the event storms' greater recency and the era dependence of recorded intensity accounting for a substantial share; and at three events, three specific periods can differ from same-calendar controls for reasons – era and instrumental intensity trends, ENSO phase, the idiosyncratic meteorology of those windows – that no resampling can separate from a solar cause. One covariate is uncontrolled by all four designs: the fraction of fixes carrying an observed wind value is 41.3 % for the event set against a control-draw mean of 38.0 %, the 81st percentile of 1000 draws, though aggregated to the storm the two distributions are indistinguishable (Mann–Whitney p=0.993). Because the draw randomises storms and not fixes, the axis was tested at that unit under the unmatched baseline draw and one of the four matched designs only (Sect. S8). We report the residual as a possibility motivating a larger-sample study.

Two quantities were held fixed throughout everything reported so far, and neither is addressed by the basin, era and ordering controls: the exponent of the matching cost, held at one, and the random subsample, drawn once for the event ensemble under a single seed while every control draw received its own. Section 4.6 and 4.7 vary both.

Having established a calibrated verdict under the physically interpretable distance, we next ask what that verdict is made of, and where in the persistence diagram the difference sits. That question turns out to have a definite answer, and the answer settles which exponent has power against the difference.

Because the exponent changes the verdict, quoting one exponent understates the uncerxtainty of the conclusion. What follows is an exploratory robustness analysis; it is not a pre-registered confirmatory test: the family was assembled after the sensitivity had been seen, and how wide to draw it is itself a judgement. Section S9 reproduces the two pre-registration records that were deposited before their runs, and the specification matrix that separates what was registered from what was not.

Reporting a result across the set of defensible analyses rather than one chosen from it is established practice in other fields. Specification curve analysis (Simonsohn et al., 2020) and multiverse analysis (Steegen et al., 2016) display the distribution of outcomes over the analytic choices, and PIMA (Girardi et al., 2024) supplies post-selection inference over that distribution, noting that the specification curve alone controls only the weak family-wise error rate. What follows carries that construction into ensemble topology, where the specifications are the matching exponent, the subsample realisation and the reference set.

The three encodings are each published, each physically motivated, and each, applied alone, would have produced a paper reporting a different verdict on the same data. Reporting one of them as “the answer” without the others, and without the caveat that the answer is encoding-conditional, is not defensible. The stability theorem of Cohen-Steiner et al. (2007) does not rescue this: it bounds output change under a fixed input metric and says nothing about the choice of metric on a periodic coordinate, which is itself a modelling choice. Škraba and Turner (2020) sharpen the stability picture in the Wasserstein setting, which is where our statistic lives, and their bounds too are stated for a fixed exponent. The spread we report is of the kind Silberzahn et al. (2018) documented across analysts working independently on one dataset; here all three verdicts come from a single pipeline in which one parameter was fixed without being recorded, so the spread is reproducible from the archive, with no differences of judgement between teams involved.

This bears on what an encoding-specific result could mean. Re-encoding a periodic coordinate changes the pairwise distance and hence the input metric to the filtration, and nothing forces two embeddings of the same data to give the same diagram. An effect that appears under one embedding and not others is therefore consistent with two readings – a genuine physical coupling legible only in one geometry, or a metric-induced amplification with no physical content – and the topology alone cannot separate them. This is why encoding invariance is a necessary but not a sufficient condition for attribution: a physically interpretable distance removes the ambiguity of which geometry to trust, and even a difference that survives it requires independent, non-topological evidence before it can be called a coupling.

The stability results usually invoked to licence persistence as a robust summary do cover a change of the underlying space. Chazal et al. (2014) establish q-tameness for the Vietoris–Rips and Čech complexes of a totally bounded space, and bound the bottleneck distance between the diagrams of two such spaces by the Gromov–Hausdorff distance between them; Cohen-Steiner et al. (2007) bound the effect of perturbing a function on a fixed space. What neither bounds is a resampling verdict. The spread measured in Sect. 4.1 is a spread of p-values, and a bound on the distance between two diagrams does not by itself bound the difference between tail probabilities computed from them against a resampled null.

The behaviour of Sect. 4.2 is a property of the sparse H1 channel: the metric is excluded, since the exact bottleneck is if anything more order-sensitive, and so is the ambient dimension, since a 4-D linear control stays calibrated. A related aggregation mechanism sharpens the point. Because a persistence diagram is a global summary of the whole cloud, pooling subgroups can open loops at scales neither subgroup supports alone (Fig. 1). We label this topological aggregation instability as a working descriptive term, not a formal result; the cell-level null pattern of Sect. 4.3 is consistent with it, and the variance measurements of Sect. 4.2 give it a measured footing.

Section 4.6 and 4.7 change what the repair of Sect. 4.5 can be said to have achieved. Fixing the input geometry on physical grounds removes one arbitrary choice, while leaving untouched three quantities downstream of it: how the mismatch between two lists of features is charged, which finite sample of points enters the diagram, and which reference diagrams the comparison is built against. On this dataset the first moves the event-level resampling p-value from 0.003–0.087, the second from 0.012–0.069, and the third, tested on the linear encoding alone, over 0.036–0.047 without crossing the threshold – sizes comparable to the effect being tested, which is the sense in which the repair is partial.

The reason the exponent matters here is legible in the diagram: the event–control difference sits at intermediate persistence, and squaring the matching cost spends the statistic's sensitivity on the part of the diagram where the event is least distinctive and the resampling noise is largest. That is a statement about this dataset and not a general rule – under the linear encoding the difference is present in the largest features as well, and squaring helps it. The same trade-off is documented elsewhere. Bendich et al. (2016) found that in populations of brain artery trees the highest-persistence features had far less distinguishing power with respect to age than features of intermediate rank, and Adams and Moy (2021) draw on that case to argue that persistence length alone should not decide what counts as signal; since the degree-p Wasserstein distance sums the pth powers of the matched costs (Cohen-Steiner et al., 2010), raising p concentrates the statistic on the largest of them. The parallel in high-dimensional testing is explicit: extreme-value statistics are the more powerful choice when a few components carry the effect, sums across components are used against effects that are individually weak and spread over many (Fan et al., 2015), and maximum-based procedures attain the optimal detection boundary only over part of the sparse range (Donoho and Jin, 2004). Which of the two situations obtains can be read off the diagrams before the exponent is committed to, and the effective count of Sect. 4.6.3 is one way of reading it: it envelopes the widening of the null in all sixty combinations examined, while as an estimate of the size of that widening it does not improve on a constant, and its sub-sampling scatter is wide enough that no ranking of representations follows. Its practical use is as a warning before the fact, never as a calibrated forecast.

Under the arbitrary encodings the pipeline does not give a single-valued verdict, so it cannot by itself support a positive or negative substantive claim at the ensemble-topology scope. Under the physically interpretable distance, the representation-level ambiguity is removed, and a residual event–control H1 difference survives all four matched nulls under W1, three of the four under the more conservative two-sided convention (Sect. S10) – but that residual is confined to the intensity channel, is attenuated by era matching, is absent under the true W2 and the exact bottleneck, and cannot be attributed to solar activity at three events. The cleanest defensible statement is therefore a cautious one: the ensemble-topology scope is not yet a tool that settles the solar–cyclone question, and the one representation that yields a calibrated difference surfaces a possibility that a larger-sample study should test. This non-detection at the ensemble-topology scope is consistent with both the older positive per-storm literature and the null microphysical literature; the three scopes interrogate different signatures, and a non-detection at one is not evidence either way at another. Causal isolation would require a design with many more events and an intensity- and era-controlled null – for example a synthetic-event injection with known perturbation strength – identified here as the priority follow-up and beyond the scope of the present study.

A second limitation is structural rather than statistical, and it bounds what this design can ever be used for. The three events were not selected on geomagnetic magnitude alone: the inclusion criteria of Sect. S5 also require sufficient cross-basin tropical-cyclone activity in the window, one benchmark per recent solar cycle, and ±2 year independence. Cyclone activity is part of the outcome under study, so event eligibility depends in part on the very quantity the test examines. For a methodological benchmark this is harmless and indeed convenient, since one wants windows with enough data to exercise the pipeline. For a test of solar or geomagnetic forcing it is not: a design in which exposure is defined partly by outcome cannot establish that direction of influence, however the statistics come out. Any physical test of the solar–cyclone question must therefore define its exposure from geomagnetic and solar-wind indices alone, before any cyclone data is consulted.

We propose five pre-registration requirements.

Representation. Report any positive H1 claim under at least two principled representations, preferring a physically interpretable distance wherever one exists. Where a periodic coordinate is unavoidable, reduce the source archive to a single convention and register the position of the branch cut.

Varying the ordering is a diagnostic check on requirement 5 rather than a reporting format, since reordering a uniformly resampled control pool selects a different realisation while the estimand does not move (Sect. 3.5). A template implementing these, with an operational agreement rule and a stratified-attribution requirement guarding against pooled-significant-but-stratified-null artefacts of the Simpson (1951) family, is shown in Sect. S3.

The present analysis does not fully meet its own protocol: the placebo set is n=49, below requirement 5's n≥200, and each placebo uses B=100 null draws, which inflates the ordering spread. Neither changes the qualitative conclusions, though the verdict is unstable across event-subsample realisations, as Sect. 4.7.1 and Table 1 show. The two statistic-level remedies a follow-up would try first do not help (Sect. 4.2); the productive move was the physically interpretable distance of Sect. 4.5, which removes the representational ambiguity that those remedies leave in place. Persistence images with kernel methods (Adams et al., 2017; Reininghaus et al., 2015), larger event samples, and non-Vietoris–Rips frameworks remain open directions.