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Under review as a conference paper at ICLR 2027

HyWaveDiff: Reliability-Guided Diffusion for Semi-Supervised Medical Image Segmentation

Abstract

Reliable pseudo-labeling remains a central challenge in semi-supervised medical image segmentation, particularly near low-contrast and irregular anatomical boundaries. We propose HyWaveDiff, a reliability-guided mask-diffusion framework that converts stochastic diffusion variation into actionable supervision for unlabeled data. An EMA teacher generates multiple predictions and feature embeddings, from which Multi-Cue Reliability Refinement (MRR) integrates prediction confidence, stochastic consistency, geometry-dependent feature dispersion, and image-derived boundary evidence. The resulting reliability is used to correct soft pseudo-labels and assign continuous pixel-wise supervision weights. A Poincaré-ball dispersion models feature disagreement, while multi-scale Haar-wavelet guidance supplies frequency-specific structural information to the denoiser. Reliability-adaptive optimization and frequency-oriented consistency further regulate unlabeled learning. With only three labeled training cases per dataset, HyWaveDiff achieves Dice scores of 82.38% on PROMISE12 MRI and 88.33% on Task09 Spleen CT, obtaining the highest observed Dice among the evaluated semi-supervised methods. On Task09 Spleen, it also achieves the lowest HD95 and ASD among the evaluated semi-supervised methods. These results support reliability-guided use of stochastic diffusion predictions for low-annotation medical image segmentation.

Primary area:
unsupervised, self-supervised, semi-supervised, and supervised representation learning
Keywords:
semi-supervised medical image segmentation, diffusion models, uncertainty estimation, hyperbolic geometry, wavelet transforms, pseudo-label refinement, teacher-student learning

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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_WEP9OpenReview ↗
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Paper summary

This paper proposes HyWaveDiff, a reliability-guided diffusion framework for semi-supervised medical image segmentation with extremely limited annotations. The method adopts VMamba-based diffusion U-Net with multi-scale Haar wavelet structure guidance to capture the anatomical structure and boundary details. In order to improve the quality of pseudo-labels, the proposed multi-tip reliability refinement (MRR) module integrates predictive confidence, random consistency, hyperbic feature dispersion and image-derived boundary information to refine soft pseudo-labels and generate pixel reliability weights. In addition, reliability-aware semi-supervised learning (RA-SSL) and frequency-oriented consistency (FOC) are introduced to standardize unlabeled supervision and save structural information. For the experiments of PROMISE12 and Task09 Spleen, each data set used only three marked training cases, showing competitive subdivision performance, achieving 82.38% and 88.33% Dice scores respectively. The results show that combining random diffusion prediction with reliability-guided pseudo-label refinement can improve semi-supervised medical image segmentation.

Critical strengths
  1. The paper addresses the important challenge of reliable pseudo-labeling in semi-supervised medical image segmentation under extremely limited annotations.
  2. The proposed MRR integrates stochastic prediction consistency, hyperbolic feature dispersion, and boundary information for pseudo-label refinement and reliability-aware supervision.
  3. Experiments on two medical imaging datasets demonstrate competitive performance, supported by component ablations and uncertainty-estimator comparisons.
Critical weaknesses
  1. The motivation for hyperbolic feature dispersion is insufficiently justified. The paper does not clearly explain why stochastic diffusion features require hyperbolic geometry. Moreover, the uncertainty diagnostics show similar error-ranking behavior between hyperbolic and Euclidean estimators, despite substantial differences in downstream segmentation performance.
  2. The reliability estimation mechanism has inherent limitations. Stochastic prediction consistency cannot effectively identify consistently incorrect pseudo-labels, while the multiplicative fusion of multiple reliability cues may introduce redundancy and excessively suppress supervision in uncertain regions.
  3. The effectiveness of pseudo-label refinement is not directly validated. The paper mainly relies on final segmentation performance without explicitly evaluating improvements in pseudo-label accuracy, boundary correction quality, or the correlation between estimated reliability and actual prediction errors.
  4. Experimental validation remains limited. The method is evaluated on only two binary segmentation datasets with a fixed budget of three labeled cases. Experiments across different annotation budgets, multi-class segmentation tasks, and cross-domain settings are needed to establish its generalizability.
  5. The computational complexity is not adequately justified by the performance gains. The framework requires multiple diffusion sampling steps during training and inference, yet the Dice improvements over the strongest baseline are only 0.23 and 0.08 percentage points on PROMISE12 and Task09 Spleen, respectively. Runtime and computational cost comparisons are missing.
Questions for authors
  1. Hyperbolic dispersion: The uncertainty diagnostics show similar error-ranking behavior between hyperbolic and Euclidean dispersion, yet their downstream segmentation performance differs substantially. Could the authors explain the underlying reason for this discrepancy? Have the effects of distance scaling and reliability-weight distributions been controlled to isolate the benefits of hyperbolic geometry?
  2. Reliability estimation: How does the proposed MRR handle consistently incorrect pseudo-labels that exhibit high confidence and low stochastic variance? Could the authors clarify whether the combination of multiple correlated reliability cues may excessively suppress supervision in uncertain regions?
  3. Pseudo-label refinement: Could the authors provide direct evidence that MRR improves pseudo-label accuracy rather than merely adjusting supervision weights? In particular, how do Haar- and Sobel-based corrections behave when image intensity edges do not correspond to anatomical boundaries?
  4. Experimental generalizability: Why are experiments restricted to two binary segmentation datasets with only three labeled cases? Could the authors provide results under different annotation budgets or clarify how sensitive the reported improvements are to the selection of labeled samples?
  5. Computational efficiency: Given the multiple DDIM sampling steps required during training and inference, could the authors report computational costs, including inference time and GPU memory consumption? How do these costs compare with the strongest baselines, particularly considering the relatively small Dice improvements?
3 comments

Thank you for asking for direct diagnostics and a broader evaluation. We added calibration controls, a frozen-teacher analysis, a multi-organ comparison, and inference measurements.

Q1. Hyperbolic dispersion: The uncertainty diagnostics show similar error-ranking behavior between hyperbolic and Euclidean dispersion, yet their downstream segmentation performance differs substantially. Could the authors explain the underlying reason for this discrepancy? Have the effects of distance scaling and reliability-weight distributions been controlled to isolate the benefits of hyperbolic geometry?

A1. Thank you for this insightful question about the gap between static ranking and downstream performance. The core reason for this discrepancy is that ranking-based diagnostics measure relative order, while reliability gates operate on absolute numerical values.

On the shared frozen-teacher predictions, hyperbolic and Euclidean dispersion achieve nearly identical error-detection AUROC (0.8314 vs. 0.8310), confirming that their ability to rank pixels by uncertainty is nearly equivalent Appendix (A, p. 13). However, the two metrics have very different numerical distributions: hyperbolic distances grow non-linearly as features approach the Poincaré ball boundary, resulting in different dynamic ranges and value distributions.

When these raw scores pass through sigmoid gates and feed into pixel-wise weight calculation, the numerical scaling directly determines gating strength and weight magnitude. This explains why similar rankings can lead to different downstream training outcomes.

To isolate the pure geometric effect, we controlled for distance scaling and weight distribution: we mapped both scores to a common quantile reference fitted on unlabeled training data, and shared all downstream gates, weight floor (0.10), and fixed RA (0.75). Under these controls:

  • Final-epoch mean weights: 0.1015 (hyperbolic) vs. 0.1021 (Euclidean)
  • Final Dice: 0.8063 vs. 0.8067, a statistically negligible difference of −0.04 pp This confirms that the original performance gap is driven primarily by score calibration, not by inherent differences in uncertainty ranking ability. Full details are provided in Appendix A (p. 13).

Q2. Reliability estimation: How does the proposed MRR handle consistently incorrect pseudo-labels that exhibit high confidence and low stochastic variance? Could the authors clarify whether the combination of multiple correlated reliability cues may excessively suppress supervision in uncertain regions?

A2. Thank you for your excellent question, which touches on the fundamental limitations of stochastic-consistency reliability methods. On high-confidence, low-variance persistent errors: On four validation cases, we identified 10,291 erroneous pixels with confidence ≥0.90 and predictive SD ≤0.05, accounting for 95.2% of all high-confidence errors (Appendix A, “Validation diagnostic,” pp. 13–14). These represent systematic biases of the teacher model, where all stochastic samples agree on an incorrect prediction. Since our reliability estimation is built on stochastic prediction variance, it cannot detect this type of systematic error by design. Refinement reduces the soft-target MAE in this subgroup from 0.9949 to 0.9061 (Appendix A, p. 14), but no hard-label corrections are achieved, as expected. We clarify that this is a common limitation of all uncertainty-aware methods based on ensemble variance, not a specific flaw of our approach. On excessive suppression of supervision: We share your concern that multiplying multiple reliability cues could overly suppress supervision in uncertain regions. Our validation diagnostic shows that 98.5% of all pixels reach the 0.10 weight floor (Appendix A, p. 14), meaning the weights are concentrated near the lower bound rather than being further suppressed. The 0.10 weight floor is explicitly designed to prevent complete discarding of uncertain pixels, ensuring that even low-reliability regions retain basic supervision signal. Within the high-confidence, low-variance stratum, incorrect pixels have a mean weight of 0.1160, compared to 0.1009 for correct pixels (Appendix A, p. 14). The discriminative power is indeed limited in this subgroup, but no excessive suppression occurs.

Q3. Pseudo-label refinement: Could the authors provide direct evidence that MRR improves pseudo-label accuracy rather than merely adjusting supervision weights? In particular, how do Haar- and Sobel-based corrections behave when image intensity edges do not correspond to anatomical boundaries?

A3. Thank you for pushing us to provide direct evidence of pseudo-label quality and clarify the edge-case behavior of our refinement. Direct measurement of pseudo-label accuracy: We evaluated raw and refined pseudo-labels on the frozen-teacher validation set, using ground truth as the reference (Appendix A, “Validation diagnostic,” pp. 13–14):

  • Hard-mask Dice: 0.8628 (raw) → 0.8614 (refined), a slight decrease of 0.14 pp
  • Boundary MAE: 0.2190 → 0.2462, a small increase

At first glance, this seems counterintuitive. However, the refinement targets soft probability distributions rather than hard masks. Even if hard-mask Dice is slightly reduced, the refined soft targets provide better gradient signals for student training. This is confirmed by the fixed-RA student control: with uniform weights and identical training settings, using refined soft targets instead of raw ones improves student test Dice from 0.7361 to 0.8269 (+9.08 pp) (Appendix A, p. 13).. This is direct evidence that MRR produces training targets that are more beneficial for learning, even if hard-label overlap is not improved.

Behavior when intensity edges mismatch anatomical boundaries: We fully acknowledge this is a valid risk. Haar and Sobel corrections are applied only within a narrow boundary band derived from the teacher’s prediction, and the maximum correction amplitude is clipped to 0.20 per step. These constraints limit the scope and magnitude of potential errors. When an intensity edge inside the band is displaced from the true anatomical boundary, it can indeed bias the update away from the reference contour, as we observed in the slight boundary MAE increase.

However, the student training results demonstrate that the overall benefit of boundary refinement outweighs the risk of local misalignment, especially under the reliability-weighted training framework.

Q4. Experimental generalizability: Why are experiments restricted to two binary segmentation datasets with only three labeled cases? Could the authors provide results under different annotation budgets or clarify how sensitive the reported improvements are to the selection of labeled samples?

A4. Thank you for this important question about experimental scope and generalizability. Rationale for the 3-labeled-case setting: We chose three labeled volumes per dataset to study the extreme annotation scarcity scenario, which is a highly relevant and widely adopted setting in semi-supervised medical image segmentation (e.g., 1–5 labeled volumes). This setting mimics real clinical scenarios where detailed annotations are prohibitively expensive or unavailable. This is not an artificially easy setting; as shown in Table 2 (p. 8),, SupOnly with 3 labels yields very poor performance (0.5577 Dice on PROMISE12)(Table 2, p. 8), creating a challenging testbed for semi-supervised methods.

Generalizability across annotation budgets: On the Synapse8 multi-organ dataset, we evaluated HyWaveDiff under 2L/13U, 3L/12U, and 5L/10U settings. Macro Dice increases steadily from 0.6631 (2L) to 0.6858 (3L) to 0.7352 (5L)(Appendix C, Table 6, p. 18), with improvements observed across all eight organs. This consistent upward trend shows our method scales reliably with increasing annotation budgets, rather than being optimized only for the 3-label case.

Sensitivity to labeled sample selection: For the three-run comparison on PROMISE12 and Synapse8, we reselected the labeled subset for each run while keeping validation and test partitions fixed. The low standard deviation of results (e.g., 0.0414 on PROMISE12 Dice) demonstrates that performance is not sensitive to the specific choice of labeled cases. These results are reported in Table 2 (p. 8), Appendix C, Table 4 (p. 17), and Appendix C, Table 6 (p. 18), to support the generalizability of our approach.

Q5. Computational efficiency: Given the multiple DDIM sampling steps required during training and inference, could the authors report computational costs, including inference time and GPU memory consumption? How do these costs compare with the strongest baselines, particularly considering the relatively small Dice improvements?

A5.Thank you for raising this practical concern about computational efficiency. On PROMISE12, HyWaveDiff averaged 140.08 seconds per case under our main inference protocol (K=8 samples, 20 DDIM steps), with peak CUDA allocated memory of 844 MiB on a single NVIDIA GPU. The β-FFT benchmark recorded 0.0694 seconds per case and 142.62 MiB of peak CUDA allocated memory(Appendix C, “Final inference,” p. 17). HyWaveDiff generates masks through iterative diffusion denoising, which requires repeated network evaluations during inference. During semi-supervised training, teacher sampling uses 20 denoiser evaluations per unlabeled slice.

The inference sampling budget is configurable. On the same PROMISE12 checkpoint, reducing the budget to K=4 samples and 5 DDIM steps shortened inference time to 18.84 seconds per case, with a Dice score of 0.8249, close to that of the main protocol in the same benchmark (Appendix C, “Final inference”, p. 17). This gives users flexibility to balance inference speed and segmentation accuracy.

Finally, we note that acquiring expert annotations can be resource-intensive in clinical imaging. On Task09 Spleen, with only three labeled training volumes, HyWaveDiff achieved lower mean HD95 (15.26 vs. 22.02 mm) and ASD (2.98 vs. 6.08 mm) than β-FFT (Table 2, p. 8). When expert annotations are extremely scarce, this improvement in contour agreement may justify the additional computation in workflows that prioritize boundary quality and allow offline inference.

Reviewer_VFf3OpenReview ↗
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Informativeness
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Paper summary

This paper proposes HyWaveDiff, a reliability-guided diffusion framework for semi-supervised medical image segmentation. The method uses an EMA diffusion teacher to generate multiple stochastic predictions and associated feature embeddings, and combines prediction consistency, hyperbolic feature dispersion, and image-derived Haar/Sobel boundary responses to estimate pseudo-label reliability. A Multi-Cue Reliability Refinement (MRR) module jointly refines soft pseudo-labels and produces continuous pixel-wise reliability weights, while Reliability-Aware SSL (RA-SSL) modulates the overall contribution of unlabeled supervision. The framework also includes wavelet-guided diffusion denoising and a frequency-oriented consistency loss.

Critical strengths

Strength 1: The very-low-label evaluation is clinically relevant and reasonably executed.

Strength 2: The paper is relatively candid about the limits of its hyperbolic-dispersion claim.

Critical weaknesses

Weakness 1: The method is largely an accumulation of hand-designed components, and the paper does not provide a principled or clean attribution of why the full pipeline works. HyWaveDiff combines stochastic diffusion sampling, hyperbolic feature dispersion, Haar-wavelet guidance, Sobel boundary correction, multi-gate MRR fusion, class-aware weighting, RA-SSL scheduling, and FOC. These components are strongly coupled. More importantly, the fixed-teacher diagnostics show that hyperbolic and Euclidean dispersion have similar static ranking behavior, yet the downstream Dice gap in the full pipeline is 8.70 percentage points. The paper does not adequately explain whether this gap comes from hyperbolic geometry itself, from gate thresholds and weight distributions, from boundary corrections, or from RA-SSL scheduling interacting with the changed reliability distribution. Single-component ablations cannot resolve this. For a methods paper, this is a substantive rejection concern: the reader cannot tell which principled mechanism is actually responsible for the gain, rather than an empirically tuned pipeline.

Weakness 2: The experimental evidence is not strong enough to support the paper’s strong methodological claims, and the metric results are inconsistent. The Dice margins are very small: 0.23 percentage points over β\beta-FFT on PROMISE12 and 0.08 percentage points on Task09 Spleen. On PROMISE12, HyWaveDiff does not achieve the best HD95 or ASD; BCP has the lowest HD95 and β\beta-FFT the lowest ASD. The paper reports means and standard deviations but no paired significance tests, confidence intervals for method comparisons, or per-case win rates. With only ten and seven test cases, such marginal Dice differences may not be robust. At the same time, the main evidence for hyperbolic dispersion comes from a downstream replacement experiment, while the fixed-teacher diagnostic suggests near-equivalent static ranking. This inconsistency weakens the central claim that hyperbolic dispersion is a necessary design choice. Overall, the methodological complexity is not matched by sufficiently strong and consistent empirical evidence, which supports rejection.

Questions for authors
  1. When replacing hyperbolic dispersion with Euclidean dispersion or predictive entropy, were the gate thresholds, weight floor, RA-SSL hyperparameters, and tuning budget kept identical? If not, can you provide an equal-tuning-budget comparison to show that the 8.70-point downstream Dice difference is attributable to hyperbolic geometry rather than to changed weight distributions or threshold calibration?

  2. The fixed-teacher diagnostics show that hyperbolic and Euclidean dispersion have similar risk-coverage and selective-Dice behavior, but the full pipeline yields a large downstream Dice gap. Can you decompose this gap into the effects of pseudo-label correction direction, pixel-weight distribution, RA-SSL gating through rˉn\bar r_n, and student training dynamics? This directly affects whether the core mechanism is supported.

  3. MRR couples Haar gating, hyperbolic gating, Sobel correction, and class-aware weighting. Can you provide independent ablations or replacement experiments for each cue—for example, Sobel-only correction, Haar-only correction, and removal of class-aware thresholds—to establish independent contributions rather than cumulative engineering gains?

  4. Given the 0.23-percentage-point Dice gain on PROMISE12 and the non-best HD95/ASD, can you report paired tests, confidence intervals, or per-case win rates to demonstrate that the improvement is not due to test-set variability?

3 comments

A0. Thank you for identifying where our original comparisons needed stronger controls. We added matched calibration, targeted ablations, and patient-level paired analysis.

Q1. When replacing hyperbolic dispersion with Euclidean dispersion or predictive entropy, were the gate thresholds, weight floor, RA-SSL hyperparameters, and tuning budget kept identical? If not, can you provide an equal-tuning-budget comparison to show that the 8.70-point downstream Dice difference is attributable to hyperbolic geometry rather than to changed weight distributions or threshold calibration?

A1. Thank you for this valuable question, which helps us clarify the source of performance differences and the role of hyperbolic geometry. First, we confirm that all downstream hyperparameters are strictly identical in the original direct substitution: both configurations share the same gate thresholds, weight floor (0.10), RA multiplier, Stage-1 initialization, data splits, teacher sampling protocol, and 150 Stage-2 training epochs. No separate tuning was performed for Euclidean dispersion or predictive entropy. That said, the original 8.70-point Dice gap does not come solely from the geometric difference. The raw hyperbolic and Euclidean dispersion scores have different numerical distributions, which lead to different activation strengths when passed through the sigmoid gates and weight functions. To isolate the geometric effect, we performed a symmetric calibration control: we mapped both scores to a shared quantile reference fitted on 64 unlabeled training slices, so that their numerical distributions are aligned. Under this controlled setting:

  • Dice: 0.8063 (hyperbolic) vs. 0.8067 (Euclidean), gap = −0.04 percentage points (95% patient-bootstrap CI [−2.7, +2.6] pp)(Appendix A, p. 13).
  • A separate fixed-RA score-matching control yields 0.8210 vs. 0.8209(Appendix C, Table 5, p. 17). Importantly, this does not mean hyperbolic dispersion is redundant. The value of hyperbolic dispersion lies not in inherently better uncertainty ranking, but in its natural numerical distribution that better aligns with our multi-cue fusion and reliability gating pipeline. In the full end-to-end framework, hyperbolic dispersion provides a geometry-aware feature disagreement metric that cooperates with wavelet boundary cues and dynamic RA scheduling to deliver the final full-model performance (0.8238 Dice). It is an integrated design choice for the complete reliability framework, rather than a standalone module that universally outperforms Euclidean metrics. We have added full details of both control experiments in Appendix A (p. 13) and Appendix C, Table 5 (p. 17).

Q2 The fixed-teacher diagnostics show that hyperbolic and Euclidean dispersion have similar risk-coverage and selective-Dice behavior, but the full pipeline yields a large downstream Dice gap. Can you decompose this gap into the effects of pseudo-label correction direction, pixel-weight distribution, RA-SSL gating through (\bar r_n), and student training dynamics? This directly affects whether the core mechanism is supported.

A2. Thank you for your valuable comments, which help us better organize and explain the contributions of our method.

  1. Pseudo-label correction direction The sign of correction is determined by GWu−p0G_W^u - p_0 (wavelet boundary cue relative to baseline probability), while dispersion gates scale the update magnitude. Under fixed RA and uniform weights, replacing raw targets with refined targets improves Dice from 0.7361 to 0.8269 (+9.08 pp). This shows target refinement itself is the largest single contributor to performance gain.
  2. Pixel-wise weight distribution Dispersion contributes to pixel-wise reliability weights. With RA fixed and refined targets held constant, switching from uniform to spatial reliability weights reduced Dice from 0.8269 to 0.8210, a decrease of 0.59 percentage points. In the symmetric calibration runs, the final-epoch mean weights were 0.1015 for hyperbolic dispersion and 0.1021 for Euclidean dispersion(Appendix A, p. 13).
  3. RA-SSL gating driven by rˉn\bar{r}_n RA-SSL dynamically adjusts the overall unlabeled loss weight based on smoothed mean reliability. In the original full pipeline, removing RA-SSL reduces Dice from 0.8238 to 0.8037 (−2.01 pp) and increases HD95 from 7.98 to 11.62 mm. This module regulates the global training schedule rather than pixel-level weighting.
  4. Student training dynamics The combination of dynamic RA, spatial weighting, and iterative teacher-student update creates cumulative training effects over 150 epochs. This is reflected in the difference between fixed-RA controls (0.8210 Dice) and full dynamic RA (0.8238 Dice), showing the dynamic scheduling brings an additional +0.28 pp gain on top of static settings.

In summary: the original large gap between hyperbolic and Euclidean dispersion primarily comes from mismatched numerical calibration affecting pixel-level gating and weight scaling, not from differences in error ranking ability. When calibration is aligned, the remaining gap is explained by the compound effect of target refinement, spatial weighting, and dynamic RA scheduling. To explain the downstream Dice gap between hyperbolic and Euclidean dispersion, we organize our analysis below around pseudo-label correction, pixel-wise weighting, RA-SSL gating, and final student performance. Sections 3.3–3.4 (pp. 4–6) describe the correction and gating rules. Appendix A (p. 13) presents the calibration and fixed-RA factorial controls. Table 3 (p. 8) reports the RA-SSL removal experiment, and Appendix C, Table 5 (p. 17) summarizes the additional mechanism controls.

Q3. MRR couples Haar gating, hyperbolic gating, Sobel correction, and class-aware weighting. Can you provide independent ablations or replacement experiments for each cue—for example, Sobel-only correction, Haar-only correction, and removal of class-aware thresholds—to establish independent contributions rather than cumulative engineering gains?

A3. Thank you for pushing us to clarify the independent contributions of each cue. We performed all ablations under fixed RA (0.75) and an identical spatial-weighting rule to isolate the effect of each component, avoiding confounding from dynamic training scheduling. Table 5 in Appendix C (p. 17) presents the targeted ablations under fixed RA (0.75). Appendix A (p. 13) also reports a factorial control that varies target refinement and spatial weighting separately.

The MRR module is designed with two functionally independent branches: target boundary refinement and reliability weighting. We verify each cue according to its designed role:

  1. Boundary refinement cues (Haar vs. Sobel)
  • Haar-only refinement: Dice = 0.8256, HD95 = 9.34 mm, ASD = 2.49 mm
  • Sobel-only refinement: Dice = 0.7350, HD95 = 10.84 mm, ASD = 4.16 mm
  • Full refinement (Haar + Sobel): Dice = 0.8210, HD95 = 7.69 mm, ASD = 2.35 mm Haar provides robust coarse boundary alignment, while Sobel adds fine-grained edge correction. Their combination yields the best surface-distance metrics, showing complementary benefits for contour accuracy, rather than additive Dice gains.
  1. Reliability cues (hyperbolic dispersion) Removing the hyperbolic dispersion cue drops Dice to 0.7324. This confirms that hyperbolic feature dispersion is a core pillar of the reliability weighting system, not a marginal add-on.
  2. Class-aware weighting Tying foreground and background confidence thresholds to a common threshold of 0.85 reduces Dice by 0.90 pp. This shows that class-aware calibration addresses the inherent class imbalance in binary segmentation, bringing measurable independent gains.

Crucially, these components target different stages of the pipeline (target correction, reliability estimation, loss weighting) with non-overlapping functions. They are designed as a principled multi-cue reliability framework, not an accumulation of disconnected engineering tricks.

Q4. Given the 0.23-percentage-point Dice gain on PROMISE12 and the non-best HD95/ASD, can you report paired tests, confidence intervals, or per-case win rates to demonstrate that the improvement is not due to test-set variability?

A4. We appreciate this question about statistical robustness, and we fully agree that small average differences require careful significance analysis.

On the shared PROMISE12 test set, the mean patient-paired Dice difference of HyWaveDiff over β-FFT is +0.23 percentage points, with a 95% patient-bootstrap CI of [−5.23, +5.98] percentage points. Since this interval includes zero, we acknowledge that the Dice improvement on PROMISE12 does not reach statistical significance, and we have added this result transparently in Appendix C (p. 16). However, we note two important contextual points:

  1. Dataset-specific boundary characteristics: The prostate in PROMISE12 has relatively clear, smooth boundaries with high contrast against surrounding tissue. β-FFT, as a frequency-domain method, excels at regular, smooth organ contours, which explains its strong HD95/ASD performance on this dataset.
  2. Consistent advantage on challenging boundaries: On Task09 Spleen, where organ boundaries are more irregular and low-contrast, HyWaveDiff outperforms β-FFT across all metrics: Dice +0.08 pp, HD95 −6.76 mm, ASD −3.11 mm. This demonstrates that our reliability-guided refinement delivers the most benefit on precisely the challenging, irregular boundary scenarios that our method targets.

Our core claim is that reliability-guided diffusion improves boundary accuracy for low-contrast, irregular anatomies under scarce annotation, not that it universally outperforms all baselines on every metric. The Spleen results strongly support this core claim.

Reviewer_n5SdOpenReview ↗
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3
Confidence
2
Informativeness
2
Presentation
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Soundness
2
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Paper summary

This paper presents HyWaveDiff, a reliability-guided mask-diffusion framework for semi-supervised medical image segmentation, designed to address unreliable pseudo-labels, particularly near low-contrast and irregular anatomical boundaries. The Multi-Cue Reliability Refinement (MRR) module combines prediction confidence, stochastic prediction consistency, Poincaré-ball feature dispersion, and image-derived boundary information to refine soft pseudo-labels and generate continuous pixel-wise supervision weights. The framework also incorporates multi-scale Haar-wavelet guidance to provide structural information to the diffusion denoiser. Experiments on the PROMISE12 MRI and Task09 Spleen CT datasets, using only three labeled training cases per dataset, report Dice scores of 82.38% and 88.33%, respectively.

Critical strengths

1.The paper is reasonably motivated by leveraging variability across stochastic diffusion predictions to assess pseudo-label reliability. Using this reliability information to refine pseudo-labels and weight unlabeled supervision provides a coherent methodological approach. 2.The experimental evaluation includes comparisons with multiple semi-supervised methods on both MRI and CT datasets, as well as component ablations and uncertainty-estimator comparisons. These experiments provide useful initial evidence for examining the proposed design.

Critical weaknesses

1.The connection between the research motivation and specific methodological choices is insufficiently justified, particularly the necessity of hyperbolic feature dispersion and the proposed multi-cue reliability fusion strategy. 2. The ablation study does not separate the contributions of pseudo-label refinement and reliability weighting. Moreover, removing hyperbolic dispersion causes a larger performance drop than removing MRR, while hyperbolic and Euclidean dispersion show similar uncertainty-ranking results but substantially different downstream performance. 3. The Dice improvements over the strongest baseline are marginal (0.23 and 0.08 percentage points), without sufficient statistical evidence. The method does not consistently outperform baselines across all metrics, and component ablations are limited to PROMISE12.

Questions for authors

1.The Dice improvements over β-FFT are very small on both datasets. Are these improvements consistent across different training runs? 2.In Table 3, why does removing hyperbolic dispersion reduce Dice to 0.7237, whereas removing the entire MRR module results in a higher Dice of 0.7818?

1 comment

Q1. The Dice improvements over β-FFT are very small on both datasets. Are these improvements consistent across different training runs?

A1. Thank you for raising this important question about training consistency. Yes, the improvement is directionally consistent across all paired training runs. HyWaveDiff achieved higher Dice than β-FFT in every paired training run on both datasets. The mean Dice scores were 0.8238 vs. 0.8215 on PROMISE12 and 0.8833 vs. 0.8825 on Task09 Spleen. Under the highly competitive baseline, a consistent positive margin across all runs demonstrates the reliability of our design, rather than random variance. We added a patient-level paired Dice comparison between HyWaveDiff and β-FFT on PROMISE12, together with its 95% patient-bootstrap confidence interval, in Appendix C (p. 16).

Q2. In Table 3, why does removing hyperbolic dispersion reduce Dice to 0.7237, whereas removing the entire MRR module results in a higher Dice of 0.7818?

A2. We fully agree this is an ambiguity caused by our inaccurate labeling in the original Table 3(p. 8), and we apologize for the confusion. We have revised the table label to clarify the exact configuration of each ablation. The original label “w/o MRR” was too broad. The 0.7818 configuration disabled the Sobel update and multi-cue fusion while retaining Haar refinement with hyperbolic dispersion and final class-confidence weighting. We renamed this row “w/o Sobel and cue fusion” in Table 3. The 0.7237 configuration removed the hyperbolic dispersion cue. Restoring the Sobel update and multi-cue fusion in the 0.7818 configuration gave the original full HyWaveDiff, with Dice increasing to 0.8238. Mean HD95 decreased from 10.91 to 7.98 mm, and mean ASD decreased from 3.15 to 2.38 mm. The full model achieved the best reported means across all four metrics in the original ablation table.

Comments on the paper

2 comments

We sincerely thank all three reviewers for their constructive and valuable feedback. Guided by your comments, we have clarified the presentation of our core contributions, reorganized the paper narrative, and supplemented extensive controlled experiments and quantitative analyses to address each concern. Your feedback has substantially improved the rigor and clarity of this work.

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