acceptodds
Under review as a conference paper at ICLR 2027

When Can A Trajectory Be Aligned? An Information Bound for Amplitude-Phase Separation

Abstract

Elastic functional data analysis separates trajectories into amplitude and phase by warping each one onto a common template and taking the warps as the phase, and recent work makes the warp a neural network that integrates a positive velocity field. Developed for densely sampled curves, it is now applied to trajectories with very few samples: contrast-enhanced MRI with three post-contrast frames, or ICU chemistry panels drawn three times in two days. We compute the Fisher information a set of measurement times carries about a warp parameter. Under the within-exam baseline normalisation these pipelines apply, it depends on the centred derivative of the response and the tangent direction of the warp family, neither of which involves the estimator, so the bound follows from acquisition metadata alone and holds for a network of arbitrary capacity. It implies that a warp pinning both ends of the time axis, the construction these differentiable pipelines are built from, cannot represent a rigid arrival delay at all; that a response with constant derivative carries no timing information once its onset precedes the window, at any sample size or SNR; and that fitting an unknown amplitude costs on a near-monotone response. Across six warp families and three encoders, in simulation and on real acquisitions, no configuration exceeds the bound, and the endpoint-pinned family recovers of the arrival variation against for free-endpoint ones: impaired on real scans rather than disabled as it is in simulation. On prostate DCE-MRI examinations across two protocols, thinning a dense acquisition degrades a measured arrival estimate from  s at forty samples to  s at three, and the bound tracks that degradation across a -fold range (). Sample count alone orders those schedules equally well; holding it at six and moving only where the six fall, the bound still orders the measured error. Applied to PhysioNet 2012 timestamps alone, the same calculation spans across ICU variables.

Primary area:
learning on time series and dynamical systems
Keywords:
identifiability, irregularly sampled time series, time warping, Fisher information, Cramer-Rao bound, elastic functional data analysis, amplitude-phase separation, experimental design, dynamic contrast-enhanced MRI

Reviews

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1234this paper, Bottom 2%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_1x5pOpenReview ↗
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Paper summary

The paper asks whether sparsely sampled trajectories contain sufficient information to identify phase variation, independent of alignment-algorithm capacity. The authors derive a Fisher information expression for a scalar warping parameter under baseline-normalized observations. Three observations follow: (i) rigid shifts on constant-derivative segments carry no timing information after baseline subtraction; (ii) endpoint-constrained warping families cannot exactly represent nonzero rigid shifts; (iii) unknown amplitude confounds phase, with an inflation factor set by the amplitude–phase score correlation. Validation uses six warping families, three encoders, prostate DCE-MRI examinations, MAMA-MIA breast MRI, and PhysioNet 2012.

Critical strengths

An estimator-independent perspective on the limits of neural trajectory alignment. The paper shifts focus from expressive alignment algorithms to whether observations support phase estimation at all, and separates model-family restrictions from information limitations; the amplitude–timing confounding analysis is practically informative. This yields useful diagnostics for interpreting learned warps and distinguishing architectural failures from intrinsic observational limits, relevant to functional data analysis, irregular time-series modeling, and neural alignment.

Critical weaknesses

(a) The theoretical guarantee relies on an idealized observation model, and the claimed estimator-independent limitation is broader than what is established. The bound assumes a scalar warping parameter, specified response shape, and Gaussian noise; as a Cramér–Rao bound it requires regularity conditions and applies to unbiased estimators. Yet the motivation concerns joint estimation of shape, amplitude, and warping. Two aspects are concerning: (i) the independent-noise model does not represent the covariance induced by subtracting an observed noisy baseline; (ii) the information quantity depends on response derivative, SNR, and parameter value, so it is not intrinsically computable from measurement times alone. It also does not characterize biased neural estimators or nonparametric warping identifiability. The abstract and conclusions sometimes communicate stronger universality than the mathematics establishes. This gap substantially limits the central claim.

(b) The real-data validation does not fully establish predictive usefulness for acquisition design. Reference values are dense-acquisition estimates, not independently observed ground truth, so reported errors measure agreement with a denser model-based estimate. Much of the strong correlation occurs across schedules with different sample counts, which the paper acknowledges rank equally well alone. The fixed-sample experiment exposes design-time fragility: Appendix I reports a predicted bound of approximately 0.90 s for the earliest-six-frame schedule but a median absolute arrival discrepancy of 54.40 s, because the calculation assumes the response begins at the first sample. Misspecification can also reverse design rankings. More convincing prospective validation is needed.

Questions for authors

(a) Noise covariance after baseline normalization. Equation (4) assumes independent noise after normalization, but subtracting the first noisy measurement induces correlations. What is the precise observation model under which Equation (4) holds? Can the authors derive the covariance-adjusted Fisher information for a noisy baseline and check whether the principal theoretical and empirical conclusions survive? An explicit treatment would substantially strengthen the contribution.

(b) Practical informativeness under uncertain response shape and arrival time. The bound depends on the assumed shape and the response location within the acquisition window, and misspecification can alter its relationship with actual error. How reliably can it rank schedules when shape and arrival time are unknown? Can rankings be evaluated under uncertainty sets or distributions over shapes and arrival times, rather than a single template at θ=0\theta=0?

(c) Validation against independently established timing information. Can the authors provide evidence that dense-acquisition references are sufficiently accurate, e.g., via independent timing information or an assessment of reference bias under heterogeneous response shapes? Agreement with a dense fitted reference does not by itself establish recovery of the physiological timing parameter.

3 comments
AuthorsOpenReview ↗

Response to Reviewer 1x5p (1/2): Thank You; the Covariance-Adjusted Bound Is Derived and the Principal Conclusions Survive

Thank you for a thoughtful review! We also appreciate your describing the work as "an estimator-independent perspective on the limits of neural trajectory alignment" and the amplitude–timing analysis as "practically informative."

In short: we derived the covariance-adjusted information you asked for, and the principal conclusions survive; we evaluated rankings under distributions over arrivals and shapes, as you suggested; and we scored the estimates against a model-free reference.

(a)(i) / Q(a). "Can the authors derive the covariance-adjusted Fisher information for a noisy baseline and check whether the principal theoretical and empirical conclusions survive?"

  1. Yes, and they survive. The covariance-adjusted information is (a/σ)² Σᵢ(gᵢ − ḡ)², the score centred on its mean, independent of which sample is subtracted. We also derived it under division by the baseline and under AR(1) noise, verified it by Monte Carlo and re-ran every experiment.
  2. Subsampling bounds rise 3–14% and placement bounds up to 2.3× (Table 4); the 108× span, the r = 0.96 tracking, the orderings and Props. 1–3 hold, with ρ in Prop. 3 now a Pearson correlation.

(a)(ii). "The information quantity depends on response derivative, SNR, and parameter value, so it is not intrinsically computable from measurement times alone... as a Cramér–Rao bound it requires regularity conditions and applies to unbiased estimators."

  1. Agreed; the claim is rescoped. The abstract, contributions and discussion say the bound needs an assumed response and noise level, and the CRB statements apply to unbiased estimators. Prop. 2 needs no estimator assumption, and the van Trees form in App. F covers biased estimators.
  2. App. H now states the regularity conditions. Gaussian noise fixes the support. The wash-in response's kink at onset breaks differentiability only at the finitely many θ that put a sample on the onset, and the gamma-variate with α > 1 has no kink.
  3. More nuisance parameters can only lower the information, so the scalar bound is a best case; it does not characterise nonparametric warps.

In the revised PDF (changes in blue): §3.1–3.2, App. H (centring, division, regularity, further nuisance parameters) and App. K (AR(1)), with every result recomputed; the abstract, contributions and §6 (rescoped claims).

AuthorsOpenReview ↗

Response to Reviewer 1x5p (2/2): Rankings Hold Under Uncertain Arrivals and Shapes and Against a Model-Free Reference

(b) / Q(b). "How reliably can it rank schedules when shape and arrival time are unknown? Can rankings be evaluated under uncertainty sets or distributions over shapes and arrival times, rather than a single template...?"

Thank you for this suggestion, which we followed directly.

  1. Averaged over the cohort's distribution of arrivals, the amplitude-profiled bound orders the thirteen placements at 0.89 and 0.92, against 0.687 and 0.676 at θ = 0. Over a wider set of response shapes it is 0.86 and 0.91 (App. F).
  2. At a single arrival the ordering depends on how exams are summarised; averaged over the prior it does not. At a single arrival it ranges from 0.53 to 0.86 between summaries; averaged over the prior it is 0.87–0.92 under either, and all twelve combinations are in the code release. Averaging the information is the summary the van Trees bound requires, and the one our prospective test pre-registered.
  3. Under shape misspecification the spread ordering holds at 0.71 while the total-error ranking inverts (§5.6).
  4. For choosing schedules an arrival-window heuristic did better. In the prospective test, a schedule chosen this way did not beat it (our reply to Reviewer 5HPY, Q2), and the design claim is narrowed to match.

(c) / Q(c). "Can the authors provide evidence that dense-acquisition references are sufficiently accurate, e.g., via independent timing information or an assessment of reference bias under heterogeneous response shapes?"

  1. Scored against a model-free arrival, the ordering holds at Spearman 1.000 and 0.821 on the two protocols. The model-free arrival is the time to 20% of peak on the dense curve and shares no response model with the bound (App. F). We concede that it is an independent reading of the same dense data rather than the physiological arrival, which no dataset here records.

In the revised PDF (changes in blue): §5.2 and App. F (bound averaged over arrivals and shapes, model-free reference).

Thank you again for the precise questions, which mapped directly onto the changes we made. We hope this answers your questions, and we look forward to your feedback. If it resolves your concerns, we would be grateful if you would consider raising your score.

I appreciate the authors' efforts on addressing my concerns. However, the current version is still quite difficult to follow, and the novelty is not clear. I maintain my original score.

Reviewer_si5gOpenReview ↗
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Paper summary

The paper investigates the identifiability of temporal alignment in sparsely sampled trajectories, focusing on separating amplitude and timing variations. The authors derive a Fisher-information-based bound on the accuracy of estimating temporal warps and analyze how sampling schedules, response shapes, and warp parameterizations affect identifiability. They evaluate their findings through simulations and experiments on clinical time-series data.

Critical strengths
  • The paper addresses a relevant problem concerning the reliability of temporal alignment, particularly when trajectories are sparsely sampled.
  • The theoretical analysis provides useful insights into the effects of sampling schedules, response shapes, and amplitude-timing confounding on alignment accuracy.
  • The experimental evaluation is relatively extensive, covering multiple warp families, encoder architectures, and both synthetic and real clinical data.
  • I appreciate that the authors investigate limitations of their own approach, particularly the effects of response-shape misspecification and unknown nuisance parameters.
Critical weaknesses
  • The manuscript is extremely difficult to follow. Relatively simple ideas are presented through unnecessarily complicated language, extensive formalism, and specialized terminology, often without sufficient intuitive explanation. The introduction is very short and provides little background or motivation for the problem and the proposed analysis. The authors frequently jump between concepts without properly connecting them, and repeatedly introduce unfamiliar concepts without explaining them. For instance, nonlinear ICA and its identifiability results are brought up in the introduction through a rather obscure analogy, concepts such as Fisher-Rao geometry, square-root velocity functions, and profile likelihood are mentioned with almost no explanation. I don't think these are necessarily familiar even to a general medical imaging audience, let alone the broader ML community. Section 3.5 introduces operators, tangent directions, and null spaces to describe what seems to be a relatively simple observation, with little explanation of why this formalism is needed. The paper also mixes different issues, such as whether a warp can represent a temporal shift, whether the measurements contain enough information to estimate it, and whether amplitude and timing can be distinguished, without clearly explaining how these relate to each other. Overall, I found the paper almost impossible to read, especially considering the relative simplicity of several of its main theoretical observations. I urge the authors to let an experienced reader go through the entire manuscript and get feedback on presentation before resubmitting (for camera ready or elsewhere).

  • I am not convinced that the theoretical contribution is substantial enough. Equation 4 follows directly from the standard Fisher information for Gaussian observations, Proposition 1 is a straightforward consequence of baseline subtraction, Proposition 2 follows immediately from the definition of endpoint-pinned warps, and Proposition 3 is a standard nuisance-parameter correction. These observations are useful in the context of trajectory alignment, but I think their novelty is rather limited.

  • The theoretical analysis is quite limited compared to the general amplitude-phase separation problem the authors aim to address. The main derivation assumes a fixed response shape, a scalar amplitude, and a single warp parameter, primarily representing a rigid temporal shift, but learned alignment methods generally involve unknown templates and more complex nonlinear warps. How much of the analysis actually carries over to such settings? Also, Table 2 shows that jointly learning the template substantially degrades recovery across all warp families. This raises additional concerns about the relevance of the theoretical analysis to the problem motivating the paper.

  • I have concerns about the noise assumptions underlying the main bound. Equation 2 assumes independent Gaussian noise after baseline subtraction, but subtracting the first noisy measurement from the remaining observations introduces correlated noise. This changes the Fisher information in Equation 4. The authors discuss noisy baselines in the appendix, but I don't see how these analyses resolve the discrepancy between the assumed observation model and the actual baseline-normalization procedure.

  • I find the claim that the proposed bound can be computed from acquisition timestamps alone somewhat misleading. The calculation also depends on assumptions about the response shape, arrival time, and noise level, which are generally unknown before acquisition. Figure 4 actually shows a case where the bound predicts that the earliest six frames are the most informative, although they recover almost nothing. Section 5.6 shows that response-shape misspecification can lead to substantial estimation biases and incorrect rankings of acquisition schedules. How useful is the proposed bound in practice if its predictions can be so sensitive to assumptions about the unknown response?

  • I don't think the experimental evaluation gives convincing evidence for some of the authors' broader claims. There are no ground-truth arrival times, so the authors evaluate sparse acquisitions against estimates obtained from the same densely sampled measurements, using the same response model. This does not necessarily tell us how accurately the actual arrival time is recovered. I am also not convinced by the repeated claim that no learned model exceeds the information bound. The Cramer-Rao bound applies to the variance of unbiased estimators, while the experiments use different error measures and learned models that may be biased.

  • In the main experiment, the number of samples predicts the error ordering just as well as the bound. The fixed-count experiment is more informative, but considers only thirteen sampling schedules and reports relatively moderate correlations. The practical advantage of the proposed bound over simpler sampling criteria is unclear. What would happen if the authors compared against simple criteria based on temporal coverage or sampling around the expected response onset? The PhysioNet experiment also provides limited evidence, as it only evaluates measurement timestamps without measuring actual timing recovery.

Questions for authors
  1. I would like the authors to clarify the novelty of their theoretical contribution compared to existing work on Fisher-information-based estimation and experimental design, particularly given that the main propositions appear to follow directly from standard results.
  2. Can the authors address my concerns regarding the assumptions underlying the proposed bound, particularly the baseline noise model and the dependence on the assumed response shape and arrival time? I think these issues are important for establishing the validity and practical usefulness of the proposed analysis.
  3. I would not consider a score raise unless the authors seriously commit to heavily revising the manuscript and presentation - I am familiar with medical imaging and MRI acqusition, and I still can't remember the last time I struggled so much with reading a paper.
3 comments
AuthorsOpenReview ↗

Response to Reviewer si5g (1/2): Thank You for the Frank Feedback on Presentation; We Rewrote the Paper and Corrected the Noise Model

Thank you for the detailed reading and the frank feedback on presentation. We also appreciate your noting that the analysis "provides useful insights into the effects of sampling schedules, response shapes, and amplitude-timing confounding on alignment accuracy," and that the authors "investigate limitations of their own approach."

In short: we rewrote the introduction and Section 3 and defined every specialised term; the noise model you flagged is corrected and the conclusions hold; and we ran the comparison with simple criteria you proposed. We also take your point that these changes are not enough on their own. We are rewriting the whole manuscript with feedback from experienced readers outside the project, as you suggested, and we commit to that rewrite regardless of the outcome here.

W1 / Q3. "The manuscript is extremely difficult to follow... The introduction is very short and provides little background or motivation... concepts such as Fisher-Rao geometry, square-root velocity functions, and profile likelihood are mentioned with almost no explanation... Section 3.5 introduces operators, tangent directions, and null spaces to describe what seems to be a relatively simple observation."

We accept this criticism, and the revision addresses each point:

  1. The introduction is rewritten with the clinical motivation, an example of an alignment that returns noise (a linear rise fits every delay equally well), and the three questions you identified, each answered by one proposition.
  2. Every specialised term is defined where it appears. Square-root velocity functions and the profile likelihood are defined; the nonlinear ICA analogy and Fisher–Rao are removed.
  3. The operator and null-space formalism moved to App. H. §3.5 keeps the amplitude–timing result and a pointer there.
  4. The prose is revised throughout for readability. The positioning table moved to App. G, so submitted Tables 2 and 3 are now Tables 1 and 2.

W2 / Q1. "Equation 4 follows directly from the standard Fisher information for Gaussian observations, Proposition 1 is a straightforward consequence of baseline subtraction, Proposition 2 follows immediately from the definition of endpoint-pinned warps, and Proposition 3 is a standard nuisance-parameter correction."

We agree the machinery is standard. Fisher-information design in MR (Alexander, 2008; Bouhrara et al., 2018) bounds tissue parameters of an un-normalised signal; ours bounds a warp parameter after within-exam normalisation (§2; App. G). What is new is what that yields for alignment pipelines: 5. A measured-baseline normalisation is information-equivalent to an unknown additive offset, and that is the quantity these pipelines estimate (your W4 found our error here). 6. Endpoint pinning and that centring compound: a random direction in a two-mode pinned family keeps a median 0.67 of its information (App. L). 7. The persistent-enhancement curve, a standard clinical kinetic type, is exactly degenerate once the amplitude is profiled (Prop. 3). 8. Prop. 2's failure is invisible to reconstruction error. It applies to the warp construction of a current differentiable aligner, which fits three-sample real curves at R² = 1.000 while recovering a simulated delay with the wrong sign (Table 1).

In the revised PDF (changes in blue): §1 (introduction), §2 (terms defined), §3.2 (the centring), §3.5 (formalism moved to App. H), App. L (pinned families) and the prose throughout.

AuthorsOpenReview ↗

Response to Reviewer si5g (2/2): The Bound's Assumptions Are Now Stated, Averaged Over and Tested Against Simple Rules

W3. "The main derivation assumes a fixed response shape, a scalar amplitude, and a single warp parameter... learned alignment methods generally involve unknown templates and more complex nonlinear warps. How much of the analysis actually carries over to such settings?"

  1. Extra nuisance parameters, such as an unknown template, can only lower the information about θ, so the fixed-template bound is a best case. Adding them replaces the information by a Schur complement (App. H); where the bound finds no timing information, a learned template supplies none. Table 1's learned-template arm shows the harder problem, and Prop. 2 holds for nonlinear warps of any capacity. The bound does not characterise nonparametric warp identifiability, and App. H says so.

W4 / Q2. "Equation 2 assumes independent Gaussian noise after baseline subtraction, but subtracting the first noisy measurement from the remaining observations introduces correlated noise. This changes the Fisher information in Equation 4."

  1. Thank you, you were right: the bound now follows from the covariance σ²(I + 11ᵀ) of the normalised data, the score is centred on its mean, and the conclusions hold. Every result is recomputed; our reply to Reviewer 5HPY (W1) gives the details.

W5. "I find the claim that the proposed bound can be computed from acquisition timestamps alone somewhat misleading... How useful is the proposed bound in practice if its predictions can be so sensitive to assumptions about the unknown response?"

  1. The claim is rescoped, and averaging over plausible arrivals and response shapes makes the ranking robust: 0.86 to 0.92 on the thirteen placements. At θ = 0 the bound credits frames that precede the arrival, which is why it rated the earliest six best.
  2. Under shape misspecification the spread ordering holds while the total-error ranking inverts (§5.6), and the paper states this as a limit.

W6. "There are no ground-truth arrival times... I am also not convinced by the repeated claim that no learned model exceeds the information bound."

  1. The ordering holds against a model-free reference (Spearman 1.000 and 0.821). We concede that no dataset here records the physiological arrival; the model-free reference is an independent reading of the same dense data.
  2. The "no model exceeds the bound" claim is now restricted to the simulated arm.

W7. "What would happen if the authors compared against simple criteria based on temporal coverage or sampling around the expected response onset?"

Thank you for this suggestion; we ran it (App. F). 7. A coverage rule beats the θ = 0 bound on the thirteen placements (0.84 against 0.69); averaged over the cohort's arrivals, the bound matches it (0.89) and adds the error's scale. 8. For choosing schedules the heuristic did better. In the pre-registered prospective test (our reply to Reviewer 5HPY, Q2), sampling around the expected arrival chose schedules better than the bound, and the paper now says so. PhysioNet is presented as an illustration.

In the revised PDF (changes in blue): §3.1–3.2, with every bound, table and figure recomputed; App. H (further nuisance parameters); the abstract, contributions and §6 (rescoped claims); App. F (averaged bound, model-free reference, simple rules); the caption of Table 1; App. N (prospective test).

Thank you again for the candid review; the paper is much clearer for it. We hope this answers your questions, and we look forward to your feedback. If it resolves your concerns, we would be grateful if you would consider raising your score.

I appreciate that the authors acknowledged and corrected several errors and conducted additional experiments addressing the reviewers' concerns. The presentation has also improved, although I still find parts of the manuscript unnecessarily dense and difficult to follow. I am still not convinced by the novelty and significance of the contribution - the theoretical results largely follow from standard estimation theory, and I am not convinced that their application to trajectory alignment is substantial enough for ICLR. The added prospective scheduling experiments also raise questions about the practical contribution, particularly as a simple arrival-window heuristic outperforms the proposed bound on both protocols. I therefore maintain my original recommendation.

Reviewer_5HPYOpenReview ↗
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3
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2
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Paper summary

The paper studies when sparsely sampled trajectories contain enough information to separate amplitude from temporal deformation. It derives a scalar Fisher-information bound under baseline centring, characterizes amplitude–timing confounding, and identifies the inability of endpoint-pinned warps to represent exact translations. Experiments combine simulations across six warp families and three encoders with 3,303 prostate DCE-MRI examinations, MAMA-MIA, and PhysioNet timestamps. The results support sampling-dependent limitations, but the claimed acquisition-only, estimator-independent guarantee exceeds what the derivation and validation establish.

Critical strengths
  1. The analysis distinguishes representation failure from insufficient information. Separating endpoint constraints from amplitude–timing confounding provides an actionable explanation for why low reconstruction error need not imply meaningful phase recovery.
  2. The fixed-count sampling experiment addresses an important confound. Moving six measurements across the same real acquisitions tests information placement independently of sample count, making it more informative than density-only comparisons.
Critical weaknesses
  1. The central likelihood does not follow from the stated normalization. Subtracting a noisy first measurement produces residuals (epsilon_i-epsilon_1), with covariance (sigma^2(I+\mathbf1 \mathbf1^\top)) over the remaining samples, rather than independent noise as assumed in Equation (4); division by the baseline produces a different likelihood again. The first-order autoregressive model extension does not explicitly propagate this normalization, so the main bound is not established for the preprocessing it claims to analyze.
  2. Equation (4) also requires the response derivative, amplitude-to-noise ratio, warp family, and evaluation point; Section 5.6 reports reversed accuracy rankings under misspecification, while Figure 4 ranks the uninformative earliest-six schedule best. These are failures of the proposed acquisition audit under plausible assumptions, not merely loose numerical calibration.
  3. A classical CRLB constrains the variance of unbiased estimators under the specified likelihood, not arbitrary learned estimators, median absolute error, or general amplitude–phase identifiability. Consequently, Table 2’s claim that efficiency above one would “violate the bound” requires bias and calibration conditions that are not established.
  4. Sparse estimates are compared against a fitted reference sharing their observations, using median absolute error and an assumed noise scale; Appendix F explicitly acknowledges that this cannot test bound attainment. The strongest fixed-count evidence is a moderate rank correlation across thirteen placements, while PhysioNet uses timestamps without testing timing recovery, leaving the headline universality insufficiently supported.
Questions for authors
  1. What is the exact likelihood after the preprocessing used in each experiment? Could the authors clarify how Equation (4) changes when the baseline is noisy, including the induced covariance and amplitude profiling?
  2. Can a schedule chosen before acquisition reliably improve timing accuracy when arrival, response shape, and SNR are uncertain? It would strengthen the paper if this were tested against uniform sampling and an arrival-window heuristic on held-out acquisitions.
  3. How is “calibrated error” in Table 2 defined, and are the compared estimators locally unbiased? Could the authors clarify which conclusions remain valid for biased neural estimators and which concern only the correctly specified scalar model?
3 comments
AuthorsOpenReview ↗

Response to Reviewer 5HPY (1/2): Thank You for Catching the Noise-Covariance Error; It Is Corrected and the Conclusions Hold

Thank you for a careful and constructive review! We also appreciate your recognising that the analysis "distinguishes representation failure from insufficient information" and that the fixed-count experiment "addresses an important confound."

In short, you were right about the likelihood after baseline subtraction: we corrected it, verified it by simulation and recomputed every result, and the conclusions hold. We also ran the prospective test you asked for.

W1 / Q1. "Subtracting a noisy first measurement produces residuals (epsilon_i-epsilon_1), with covariance ... over the remaining samples, rather than independent noise as assumed in Equation (4)." "What is the exact likelihood after the preprocessing used in each experiment?"

  1. Thank you for catching this! The corrected information is the score centred on its mean, (a/σ)² Σᵢ(gᵢ − ḡ)², whichever sample is subtracted. It follows from the inverse covariance σ⁻²(I − 11ᵀ/n); the submitted form overstated it by (Σᵢ(gᵢ − g₁))²/n.
  2. A Monte Carlo with a noisy baseline puts the estimator's spread at 0.944–1.009 times the corrected bound. The two ratios below 1 (0.980 at 80 frames, 0.944 at six samples) are the schedules with a sample within about one spread of the onset kink, where the likelihood is not locally quadratic (App. H). At six samples the estimator is also biased by −1.0 s, which an unbiased bound does not constrain.
  3. Each experiment's likelihood is now stated. Real acquisitions (§5.1–5.2) use the noisy-baseline, mean-centred form (Eq. 4); simulations with a fixed baseline use the known-baseline form, and the nuisance ladder (§5.5) switches at its noisy-baseline rung, a 1.75× cost. With the amplitude profiled, the cost is (1 − ρ²)^(−1/2), with ρ now the Pearson correlation of the two scores (Eq. 6). Division by the baseline gives |c|² − (r·c)²/(1 + |r|²), with r = S/S₁ (App. H), and AR(1) noise gives cᵀ(DRDᵀ)⁻¹c (Eq. 5), with the schedule ordering unchanged.
  4. Subsampling bounds rise 3–14% and placement bounds up to 2.3×. The 80-frame span is now 108× (was 119×) and the slope 0.851 (was 0.834), at r = 0.96. The placement windows start mid-curve, and their θ = 0 ordering improves from 0.654 and 0.621 to 0.687 and 0.676 (Table 4).

W2. "Equation (4) also requires the response derivative, amplitude-to-noise ratio, warp family, and evaluation point; Section 5.6 reports reversed accuracy rankings under misspecification, while Figure 4 ranks the uninformative earliest-six schedule best."

  1. We agree these are limits of the audit. The claim is rescoped, and averaging over the cohort's arrivals removes the earliest-six failure. At the cohort's arrival the earliest six frames carry no information in 99% and 82% of exams on the two protocols. Averaged over the arrival distribution with the amplitude profiled, the bound orders the thirteen placements at 0.89 and 0.92, against 0.687 and 0.676 at θ = 0.
  2. Under misspecification the spread ordering holds at 0.71 while the total-error ranking inverts (§5.6). The paper states this as the condition for calling one design more accurate.

In the revised PDF (changes in blue): §3.1–3.2 (Eqs. 2, 4 and 5), App. H (centring, division, Monte Carlo) and App. K (AR(1)), with every bound, table and figure recomputed; the abstract, contributions and §6 (rescoped claims); §5.2 and App. F (bound averaged over arrivals and shapes).

AuthorsOpenReview ↗

Response to Reviewer 5HPY (2/2): Biased Estimators, a Model-Free Reference and the Prospective Schedule Test You Asked For

W3 / Q3. "A classical CRLB constrains the variance of unbiased estimators under the specified likelihood, not arbitrary learned estimators, median absolute error, or general amplitude–phase identifiability." "How is "calibrated error" in Table 2 defined, and are the compared estimators locally unbiased?"

  1. "Would violate the bound" now applies only to the simulated arm, where truth and σ are known, and none of its 84 cells exceeds one. Calibrated error, defined in the caption of Table 1 (your Table 2), is the error after inverting the estimator's fitted linear shrinkage toward the mean. The real-data arms are now labelled a calibration diagnostic.
  2. For biased estimators the van Trees bound applies, and measured RMSE exceeds it in 13 of 14 real schedules. It constrains the mean-squared error of any estimator (App. F). Prop. 2 holds for biased estimators as well, since it concerns representation, at any capacity.

W4. "Sparse estimates are compared against a fitted reference sharing their observations... The strongest fixed-count evidence is a moderate rank correlation across thirteen placements, while PhysioNet uses timestamps without testing timing recovery."

  1. Against a model-free reference the ordering holds: Spearman 1.000 and 0.821 on the two protocols. That reference is the time to 20% of peak on the dense curve, which shares no response model with the bound. The shared data is why the slope is below one (App. E).
  2. On the thirteen placements the prior-averaged bound matches a one-bit coverage rule (0.84 and 0.82) and adds the error's scale.
  3. PhysioNet now uses all 4,000 stays, and the bound orders recovery of simulated events at 0.97 across 28 variables. It remains an illustration, since PhysioNet records no arrival time.

Q2. "Can a schedule chosen before acquisition reliably improve timing accuracy when arrival, response shape, and SNR are uncertain? It would strengthen the paper if this were tested against uniform sampling and an arrival-window heuristic on held-out acquisitions."

Thank you for this suggestion; we ran exactly this test (App. N). The protocol was fixed before the curves were rebuilt for it, on a cohort we had analysed earlier, and is in the code release. A six-frame schedule chosen on a design half of patients was compared on the held-out half with uniform sampling, the heuristic and the θ = 0 rule.

  1. On the 80-frame protocol (713 exams) the bound-chosen schedule beat uniform sampling, but the arrival-window heuristic did better. It beat uniform sampling by 0.62 s (95% CI 0.23–1.04) and the θ = 0 rule by 0.28 s (0.01–0.63), and lost to the heuristic by 0.81 s (0.63–1.10).
  2. On the 35-frame protocol (930 exams) it lost to all three, by 1.72–1.85 s. The criterion chose six consecutive frames (36–82 s), which leave 14% of exams with essentially no timing information.
  3. A first run omitted re-baselining late-starting schedules; the corrected rerun moved the margins against our schedule and changed no conclusion.
  4. We have narrowed the claim: the bound ranks and audits protocols, but for choosing one, sampling around the expected arrival did better.

In the revised PDF (changes in blue): the caption of Table 1 and App. F (calibrated error, van Trees bound, model-free reference, simple placement rules); §5.4 (PhysioNet); the new App. N and §6 (prospective test, narrowed design claim).

Thank you again for the careful review; it led directly to the corrected bound and the prospective test. We hope this answers your questions, and we look forward to your feedback. If it resolves your concerns, we would be grateful if you would consider raising your score.

I thank the authors for the additional experiments and their candid responses. Some of my concerns have been addressed, but the novelty of the current version is still not clear. I maintain the original score.

Comments on the paper

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AuthorsOpenReview ↗

General comment: Thank You to All Reviewers; the Shared Noise-Model Error Is Corrected and the Conclusions Hold

Thank you all for careful and detailed reviews. All three of you independently caught the same error in our noise model, and fixing it made the central result cleaner. The revised PDF is uploaded, with text added or changed since submission in blue.

The main changes:

  1. Noise covariance corrected. Subtracting a measured first sample correlates the noise. The corrected information centres the score on its mean. Every bound is recomputed (subsampling bounds rise 3–14%, placement bounds in Table 4 up to 2.3×), and the conclusions hold, with one exception in point 5.
  2. Claims rescoped. The bound needs an assumed response shape, SNR and evaluation point as well as the measurement times; the paper now says so.
  3. New analyses. A bound averaged over uncertain arrivals and shapes, comparisons with simple rules and a model-free reference, and a pre-registered prospective test, reported in full.
  4. Presentation. The introduction, terminology and Section 3 are rewritten (details in our reply to Reviewer si5g). A full rewrite of the manuscript, with feedback from readers outside the project, is under way, and we commit to it whatever the outcome.
  5. Other corrections. Weighting placements by the profiling cost no longer repairs the 35-frame ordering (0.676 to 0.670; the submission reported 0.599 to 0.775). PhysioNet now uses all 4,000 stays (20.2× across 28 variables; was 10.6× across 25 from 900). 165 patients appear in both prostate protocols; the submission called them disjoint. The attainment sweep (§5.5) is 12 settings with six rungs each; "72 settings" counted the rungs. The treatment-response appendix is removed: rerun with the current code, its fits failed in 99% of curves.

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

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