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Under review as a conference paper at ICLR 2027

Phase Dependence Is a Task Property: Measuring Classification Accuracy Beyond the Fourier Magnitude in Time-Series Classification

Abstract

Complex-valued and other phase-aware architectures are regularly proposed for time-series tasks, yet their reported benefits are inconsistent. We argue the question "are phase-aware models better?" is underdetermined: phase sensitivity is first a measurable property of tasks. Because x -> |Fx| is not injective (its fibers contain all circular shifts, reflections and negations), any amplitude-spectrum classifier is blind to label structure varying within fibers, so the Bayes accuracy reachable from the global amplitude spectrum is a true ceiling for that class. We measure not that ceiling but how much of it classifiers reach: the phase-accessibility gap Delta_phi, the test-accuracy difference between the best model given the full signal and given only the amplitude spectrum, with model and representation selected by cross-validation on training data alone. It screens a model-agnostic target with a calibrated model family and is stable across disjoint estimator families. Against exact synthetic ground truth it gives no false positives in 30 amplitude-only tasks or 36 phase-uninformative nulls, but 11 of 12 on redundancy nulls (the label a function of |Fx| yet the phase encoding it), so what it identifies is a finite-family bound, not a Bayes gap. It decomposes, relative to an explicit shift-invariant repertoire and up to a measured estimator term, into a position component a fixed-window spectrogram largely recovers (81-86%) and a relative-phase component it recovers much less of (54-66%). Across 114 UCR datasets the estimated gap spans -0.20 to 0.53. Estimated from training data alone it predicts held-out gain across five model families with raw-signal access (1D CNN, MiniRocket, InceptionTime, a complex-valued CNN, 1-NN DTW; partial correlations 0.52-0.68 against untouched test performance, family-clustered intervals excluding zero) and is near zero where the gap is; an intervention randomizing phase while preserving amplitude drives the gap and an independent family's gain down together (r=+0.91). On the UEA multivariate archive, which took no part in its development, it again predicts held-out gain (r=+0.70, +0.62) and sorts it into the same semantic categories. Per dataset it is a screen: under train-selection uncertainty 33 of 114 datasets are confidently positive, 24 show no detected gap and 53 are inconclusive. As a case study, a real CNN given the analytic-signal input [x, Hx] matches or beats its complex counterpart on the trunk and budget we test, so what helped here was a phase-bearing input, not arithmetic. The literature's inconsistency is what a task property, interacting with input and readout, predicts.

Primary area:
learning on time series and dynamical systems
Keywords:
time series classification, phase information, dataset diagnostics, benchmark analysis, Fourier magnitude, complex-valued neural networks, evaluation methodology, representation learning

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_KEfDOpenReview ↗
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1
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Paper summary

I am unable to summarize the contributions of the paper because, despite my best attempts, i largely do not understand it. (see below)

Critical strengths

The authors have benchmarked five realistic deep learning models on a large benchmark comprising over one hundred tasks.

Critical weaknesses

(1) The problem statement and contribution of the paper are unclear. Quote:

The question is underdetermined as posed, because it locates phase sensitivity in the model

I do not see why the question is underdetermined as posed: all it takes is to check whether, for some model h and any two signals x and y with different phase spectra, h(x)≠h(y). Perhaps this is the wrong question to ask in an applied, but it is certainly not underdetermined. Then, the authors claim that there is a need to "reframe" the question by ascribing phase sensitivity to be a property of the task. I do not see how this is a kind of "reframing": rather, it is a whole other question. The authors are presenting the reader with a false dichotomy (either a property of the model or of the task) whereas it seems to me that both can coexist. The authors give an argument in Figure 1 that, i must confess, i have not understood after reading it multiple times:

Whether phase awareness can help is bounded by a logically prior quantity: how much of the task’s label information depends on phase at all—a property of the joint distribution of signals and labels, measurable without committing to an architecture. Once measured it varies so widely (zero to fifty-plus accuracy points) that averaging a model comparison over an arbitrary basket must produce unstable conclusions—the signature of a task property treated as a model property. I do not know what "varies so widely" nor over what domain. I do not know what "an arbitrary basket" or "unstable conclusions" are. It seems to me that the authors are trying to state a problem that does not really exist in the signal processing community, and then proceed to solve it in a way that is inadequate and inconclusive. The only theoretical result in the article, Proposition 1, is obvious and presented with excessive jargon. There are two many intermediate notations: what is the point of Z=amp(X) and eta_y(x)=P[X=x|Y=y]? What is sigma? But the bigger problem is that this Proposition has no practical utility since, by the authors' own admission, it concerns abstract quantities ("Bayes estimands"). The empirical version of \Delta\phi "has no guaranteed sign". Likewise, decomposition (3) is obvious and does not bring insight. It is purely a matter writing a difference of two terms as a sum of three differences of two terms by introducing telescoping.

(2) I have found the whole paper very hard to follow, and at parts inscrutable. As a specialist of machine learning for signal processing, i am puzzled by terms such as

"the empirical teeth"

"orbit-level disagreement is a sufficient witness"

"benchmark-level ordering is measured, per-task phase dependence only screened"

"the complex result binds one trunk"

"the readout matters more than the arithmetic"

"two points of a common fibre carry different labels with positive probability" (N.B. probability is defined over Borel sets, not points),

"Position” and “relative phase” are shorthand for these group- and repertoire-relative quantities, not identified information-theoretic ones; since the two sides also differ in candidates and budget, both are pipeline-specific performance difference"

and many more. The paper is poorly organized, with numerous repetitions of almost exactly the same claim: see for example "single-dataset use is a screen" or "input and readout, not arithmetic". Sections 3 through 7 are particularly challenging to read: more than once, i have felt like the paper might have been completed in a rush, with little attention to clarity.

Questions for authors
  • Are you able to explain, in simple terms, what i should be seeing in Figure 2 and Table 6? This figure is not directly referenced in the text.
  • Did this huge benchmark allow you to come up with practical recommendations for researchers and engineers working on neural network design? If so, how confident are you with your recommendations?
  • Your paper does not discuss architecture design at all. Most of the models you benchmark have already been published: InceptionTime, MiniRocket, etc. Are you able to explain your results, at least tentatively, by linking specific design choices (in terms of architecture, initialization, choice of nonlinearity, loss function, optimizer, etc.) to Delta Phi?
Reviewer_SfLvOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
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Soundness
1
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Paper summary

The paper argues that whether phase-aware models help is a property of the task rather than of the model. The argument is anchored in the non-injectivity of x -> |Fx|: a predictor that factors through the amplitude spectrum is constant on each fibre, so the Bayes accuracy reachable from the global amplitude spectrum is a ceiling for that class. The paper does not estimate that ceiling; it measures how much of it a fixed generic model family reaches, as the phase-accessibility gap Δφ = A_full − A_amp, with the model and representation selected by cross-validation on the training set only and the test split read once.

Δφ is estimated on all 114 fixed-length UCR datasets, and prospectively on 30 UEA datasets; decomposed into position (circular-shift-sensitive) and relative phase (shift-invariant) components; calibrated on synthetic tasks with known ground truth; and shown to predict the held-out gain of other model families. A case study finds that a real network given the analytic signal performs at least as well as a capacity-matched complex network.

Critical strengths
  1. The instrument is validated prospectively across model families, under controls built to break it. The paper keeps three things apart that this literature usually conflates — the Bayes-level estimand Δ*φ, the finite-family estimator Δφ, and the predictive claim — and states which conclusion attaches to which. Δφ is then estimated once with a fixed generic family, and it predicts the held-out gain of five architectures with different inductive biases, with family-clustered intervals and partial correlations controlling for length and class count. The obvious way to fake this result is available to the authors and they close it: because gap and gain share A_amp, Appendix I constructs the null for exactly that coupling (+0.10 to +0.32), shows the observed correlations exceed it, re-references every family to its own amplitude accuracy, and cross-fits the two axes on disjoint test halves. The prospective version in Section 4.1 touches no test label and is reported as the more conservative estimate rather than as confirmation, and UEA is a genuine out-of-sample archive, with the variable-length truncation disclosed and both counts given. This is what makes Δφ an empirical quantity rather than a notational device, and it is the main reason I did not rate the paper lower.

  2. The paper reports what its own instrument cannot do, and ships a conservative variant that lets the reading be checked. The redundancy nulls reach Δφ = +0.533 on a task with Δ*φ = 0; the lowbin held-out family fails at detection 0.35; one pre-registered prediction is reported as falsified; the Φ2-only repertoire is released as a floor variant so that the typology can be checked against a decomposition that was not selected on UCR; and three quantities are disclosed as not recomputable from the release. For an overall assessment this matters more than the positive results, because it means the paper's limits are known rather than unknown. It is also why I would still cite the instrument after criticising the claim built on top of it.

Critical weaknesses
  1. Δφ is not identified with the property the paper names, and the error is unbounded in both directions. The redundancy families in Section 6 have Δ*φ = 0 by construction — the label is an exact function of |Fx| and the phase is set from that label — and Δφ nevertheless reaches +0.533, which the paper itself notes is "numerically the archive's own maximum". The abstract concedes the consequence ("what it identifies is a finite-family bound, not a Bayes gap"); the title, contribution (1) and Section 10 do not. No bound is placed on how much of the 114-dataset map is contaminated, and the paper states in two appendices that both of its defences fail: the screen "bounds that one mechanism and no other ... so a wide margin above chance is not evidence against redundancy in general", and the learning curve, which is the instrument aimed at the mixture case, has a positive control that "slopes down only weakly ... so its demonstrated power is modest" and "no power against the parity family". The mixture mechanism — the realistic one — is covered by neither. On the 62 datasets with Δφ ≥ 0.03 the amplitude arm sits a median +0.359 above chance and only three are within 0.10 of it (Wine +0.037, Ham +0.091, SmoothSubspace +0.093), so the screen excludes the mechanism for nearly the whole stratum on the strength of a screen the authors say does not generalise. The error is unbounded in the other direction as well: Appendix M states that on signals whose label-bearing structure sits in low-magnitude bins the invariant "is biased toward the high-energy part of the spectrum", names a whitened representation as "the natural fix", and leaves it to future work, without estimating how many of the 114 datasets are affected. One case is conceded only in an appendix: SmoothSubspace, the archive's largest gap (Δφ = +0.533, Δrel = +0.340, CNN gain +0.498, the rightmost point in every panel of Figure 2) and a member of the "stable core of seven" that Section 3 offers as confirmation ("We did not select these datasets; the estimator did, and the semantics agree"), has an amplitude arm only 0.093 above chance, "which is exactly the regime in which our own null fires. We therefore do not claim that dataset as evidence of Bayes-level phase dependence." Sections 3 and 4 do not mention this. Finally, Section 10 converts a non-detection into sufficiency ("amplitude/power features are a sufficient baseline"), which is the inference Section 2.1 rules out ("states what was observed, not amplitude sufficiency, which no estimator can prove"), the set Section 4 calls "not a negative control", and the policy Appendix I measures and rejects: "On our data this policy loses to always-raw for the strong learners (MiniRocket 0.824 vs. 0.862; InceptionTime 0.792 vs. 0.803) ... Always-raw is the accuracy-safe default", with "The diagnostic's decision value is prognostic, not routing." The abstract carries two further overstatements of the same kind: "gain ... is near zero where the gap is" holds only under the shared A_amp definition (Table 1 gives InceptionTime +0.101 on its own baseline), and "is stable across disjoint estimator families" is true of the continuous gap only, with 25–37 of the 52 low-gap datasets remaining below 0.03. This is why the paper sits below the threshold: its headline deliverable is a landscape of what phase dependence tasks carry, and the semantic reading of that landscape rests on a quantity that is never estimated.

  2. The contribution is over-claimed relative to both its own evidence and the prior literature. Three evidential points. First, the claim that the five families "share nothing but the task" does not hold: Δφ and four of the five gains subtract the same A_amp, the paper's own null puts that coupling at +0.10 to +0.32 and describes it as "real and non-negligible", and the deep families fall from +0.513 to +0.237 (CNN) and from +0.645 to +0.450 (InceptionTime) once own-|Fx| baselines are used. Second, the only experiment with causal content is under-controlled in ways the authors identify and do not fix: the amplitude arm's input is identical across doses so its accuracy "should be identical, not merely close", the measured drift is median 0.032 and max 0.073, the remedy ("Fitting the amplitude arm once per dataset and reusing it across doses would make this control exact") is stated but not run, and the experiment covers six datasets with one randomization each ("we ran one randomization per dataset, not several ... not randomization variance"). Third, Section 6's own finding points at a baseline that is never run: a fixed-window spectrogram recovers 81–86% of the position component, i.e. that structure lives in localized magnitude, yet the model-family comparison contains no interval-spectral classifier. RISE (Lines, Taylor & Bagnall, 2018), which extracts spectral features over random intervals, is the natural comparator here; Section 9 does acknowledge that strong ensembles are absent, but no classifier of this kind is evaluated at all. Alongside these, two claims are unearned. The motivation — that the mixed published record for phase-aware models is explained by task heterogeneity — is asserted in Sections 1 and 8 and in the closing line of the abstract, and never tested: Section 5 trains its own networks under its own configuration, and no published per-dataset complex-versus-real result is checked against the map; comparing a few such published results with Δφ would turn the framing into evidence. And the novelty is positioned against generic feature libraries, whereas the classification-complexity / meta-learning line, surveyed by Lorena et al. (2019) and descending from Ho & Basu (2002), already extracts per-task measures from training data, uses them to predict which model family will succeed, and treats class ambiguity as non-zero Bayes error — the same theoretical object as Proposition 1, restricted to one representation. The phase-scrambling critique in Section 2 and Appendix C is likewise not new: Stojanoski & Cusack (2014) show that Fourier phase scrambling destroys local edges and contours and confounds local-receptive-field models, and Aru et al. (2015) show that phase-randomised surrogates are fully stationary after scrambling, so that the non-stationarities of interest and the unspecific ones are destroyed alike. Since the reframing is contribution (1), the paper's principal reason to exist, this bears directly on whether the contribution survives as claimed; what remains new is that the Bayes contrast is taken between representations rather than on the data as given, which is a smaller but still real claim.

Taken together, this is why I recommend weak rejection rather than weak acceptance: the parts that fail are the parts it leads with — the title, contribution (1), Section 10 — while the parts that hold are contributions (2) and (4). The wording defects are a red-pen fix and I do not count them; the missing quantity described above is not a wording problem, and it determines whether the landscape in Section 3 can be read as phase dependence at all. I would move to weak acceptance if the bound asked for in Question 1 is answered with a small number and the title, contribution list and Section 10 are made consistent with the abstract; to clear acceptance if, in addition, the intervention is re-run with the amplitude-arm fix the authors themselves identify; and to clear rejection if the revisions are confined to wording and the map's contamination is left unaddressed.

Sources cited above, in case the originals are not immediately at hand:

  • Lorena, A. C., Garcia, L. P. F., Lehmann, J., Souto, M. C. P., & Ho, T. K. (2019). How complex is your classification problem? A survey on measuring classification complexity. ACM Computing Surveys, 52(5), Article 107. doi:10.1145/3347711
  • Stojanoski, B., & Cusack, R. (2014). Time to wave good-bye to phase scrambling: Creating controlled scrambled images using diffeomorphic transformations. Journal of Vision, 14(12):6, 1–16. doi:10.1167/14.12.6
  • Aru, J., Aru, J., Priesemann, V., Wibral, M., Lana, L., Pipa, G., Singer, W., & Vicente, R. (2015). Untangling cross-frequency coupling in neuroscience. Current Opinion in Neurobiology, 31, 51–61. doi:10.1016/j.conb.2014.08.002
  • Lines, J., Taylor, S., & Bagnall, A. (2018). Time series classification with HIVE-COTE: The hierarchical vote collective of transformation-based ensembles. RISE, the interval-spectral ensemble referred to above, is introduced in Section 6, but the submission cites neither this paper nor RISE anywhere.
Questions for authors

Q1. The bound on redundancy contamination. This is the question that determines my rating. Your screen bounds one mechanism only, and your learning curve has modest power and none against the parity family, so the mixture mechanism is covered by neither. Can you quantify it? (i) mixed-mechanism synthetic families whose labels are amplitude-easy on some examples and phase-encoded on others, sweeping the amplitude arm's margin above chance; (ii) the largest false Δφ each margin can produce; (iii) the 62 UCR datasets with Δφ ≥ 0.03 placed against that boundary, with a count of those that cannot be distinguished from redundancy. If it cannot be produced, please state explicitly which part of the map in Section 3 is uninterpretable, and why the remainder is not.

Q2. Which A_full does the UEA study use? Section 7 says you apply "the prospective train-only diagnostic of Section 4.1", which Section 4.1 defines on the four-arm repertoire frozen before the UCR sweep. Appendix B says "the UEA studies, the magnitude-scope comparison and the intervention use the five-arm A_full that adds the bispectrum", and its final paragraph says the UCR-informed bispectrum enrichment "enters only the decomposition and the external runs, never the prospective diagnostic". These statements cannot all be correct. Which repertoire produced the numbers in Section 7, and should the UEA results be described as a transfer of the diagnostic in Section 4.1? Related: the UEA gains use own-|Fx| baselines throughout, whereas the headline UCR numbers use the shared A_amp (DTW excepted), so the external study changes the gain definition and the repertoire at the same time. Could you report the four combinations (four/five arms × shared/own baseline) on UEA?

Q3. The lowbin blind spot. How many of the 114 UCR datasets have label-bearing structure concentrated in low-magnitude bins? Would you run the magnitude-weighted or whitened variant that you call "the natural fix", and report how the typology and the gain correlations move? As it stands, the map is an unquantified mixture of a real landscape and a systematic blind spot.

Q4. Input dimensionality. |Fx| has ⌊L/2⌋+1 components, raw has L, and [|Fx|, cos∠Fx, sin∠Fx] has 3(⌊L/2⌋+1), so the two ends of Δφ differ about threefold in input dimension. Every control in the paper concerns dataset length or sample size; none concerns the arms' input dimensionality. Does Δφ survive a dimension-matched control, for example |Fx| interpolated or zero-padded to L, or raw passed through a dimension-matched random projection?

Q5. The learning-curve ladder. Could you define the 88-dataset / 22-rel-phase subset, and reconcile its endpoints with Table 3 (position 0.091 → 0.095 against Table 3's 0.123; rel-phase 0.151 → 0.201 against 0.209)? As written, the central argument of the appendix — that the gap does not shrink as the amplitude side receives more data — cannot be checked against the main table.

Q6. Reproduction coverage. You disclose three quantities outside the automatic recomputation: the 0/36 result, whose original script "was run locally and we were unable to recover it"; the two own-|Fx| rows, whose per-dataset file "was not preserved"; and the Appendix K table, which is "not bit-reproducible from a rerun". Could you add a table indicating which numbers in the paper reproduce automatically from the release and which do not, and what each of the latter is recomputed from?

Q7. The intervention. Since the amplitude arm's input is identical across doses, why not fit that arm once per dataset and reuse it, which you state would make the control exact? And would the dose-response slopes hold against that exact floor, with randomization variance estimated from repeated surrogates rather than one draw per dataset?

Q8. SmoothSubspace and the core seven. The appendix disclaims SmoothSubspace as "evidence of Bayes-level phase dependence", while Section 3 lists it among the "stable core of seven" and Figure 2 places it at the far right of every panel. Which is it? If the disclaimer stands, should it be removed from the core, and should the disclaimer appear in Section 3 and in the caption of Figure 2?

Q9. Several reported figures do not reconcile between the main text and the tables, and I would like to know which version is current.

  • Appendix C contains two stacked versions of the same relocated paragraph: the first gives 83% / 87% / 102 and a low-gap CNN mean of −0.008, the second gives 85% / 90% / 103; Table 1, Table 3, Table 4 and Section 4 all give −0.012.
  • "twelve estimates are negative" (Sections 2, 3 and 9) against Section 4's "103 with non-negative estimated gap"; Table 6 contains 11 negative values.
  • Section 6 attaches "(mean +0.503, max +0.533)" to both redundancy families; Appendix J gives +0.076 / +0.157 for redundant and +0.503 / +0.533 for parity.
  • The proximity-to-boundary count is 32/114 in Section 3 and 40/114 in Appendix M.
  • The rel-phase stratum's Δφ is 0.209 in Table 3 but 0.211 in Section 6; the aggregate gap is 0.084 in Section 6 against 0.080 implied by the stratum means in Table 3.
  • The UEA rel-phase share is given as "47% against 25%", where 25% corresponds to the pre-mask count of 28 rather than the reported 23 of 114.
  • Section 6's "the window-selected variant ... to −7% against 31%" cannot be mapped onto the fixed-window contrast of 81–86% / 54–66% that it refers to.

Q10. Four cross-reference and structural problems, and three further points on definitions and scope.

  • Section 9 cites Section 6 for a log-loss result that appears nowhere in the paper; Section 6 reports balanced accuracy only.
  • Section 4 attributes the A_amp residualization to Section 6; it is reported in Appendix I, with different numbers (+0.40 to +0.65 against +0.49 to +0.61).
  • Appendix B calls the shifted-raw arm one of "the shift-invariant arms", against Section 2.1.
  • One appendix, sitting between the material of Section 7 and Appendix K, carries no letter.
  • Gain definitions: Table 4 and Figure 2 use the shared A_amp (1-NN DTW excepted), Table 6 uses own-|Fx| for Rocket, InceptionTime and DTW, and Appendix E gives both; a reader recomputing Figure 2's MiniRocket coefficient (+0.720) from Table 6 will not recover it.
  • "no-detected-gap" denotes two different sets — the type (n = 52 in Table 3 and Figures 1c and 5) and the bootstrap verdict (n = 24 in Section 6 and Appendix I) — and Section 7 compares a UEA train-only count (10 of 30) with a UCR test-side type count (52 of 114).
  • Section 10's "a complex network with a magnitude readout gained nothing from it here" drops the scope set in Section 5 ("This is a case study, not a single-factor experiment"; "We do not call complex networks inferior in general"), and contradicts the sentence immediately before it in the same paragraph ("winning margin +0.017 with three of five heads losing").
Reviewer_HnXcOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
1
Soundness
2
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Paper summary

The paper performs a comprehensive analysis of the role the phase information could play when performing time-series classification tasks. The authors present theoretical justification, dataset-specific benchmarking, and evaluation across numerous datasets and model families.

Critical strengths

The paper presents comprehensive theoretical and empirical analysis.

Critical weaknesses
  • Standard time-series related learning has been heavily relying on patch-embeddings with Transformers/state space models to perform various tasks, such as classification, imputation, or forecasting. The evaluation covers several classification models but does not include the aforementioned models. It remains unclear whether how well the claim transfer to these model and tokenization architectures.
  • It is unclear how the proposed diagnostic benefits practical model selection. Using raw signals outperforms diagnostic-based input selection for the strong classifiers evaluated. Further clarification would help establish when the diagnostic provides actionable benefits.
  • Minor: The paper also benefits with additional structures and flows.
Questions for authors
  1. Can you clarify on what practical decisions are supported beside directly comparing the input representations (e.g., learning objectives)?
  2. Spectrogram inputs can already recover much information, what would be the additional values that are useful in such cases?
  3. Can it be extended to tasks with very different characteristics such as forecasting, imputation, or regression? Recent trends have been moving toward foundation models with task-agnostic learning, and some have proposed using phase information to guide representation learning. How can paper's interpretation transfer to those domains?
  4. How does the choice of patch-based models (and potentially the patch size and strides) affect this analysis?

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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