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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
- The paper addresses the important challenge of reliable pseudo-labeling in semi-supervised medical image segmentation under extremely limited annotations.
- The proposed MRR integrates stochastic prediction consistency, hyperbolic feature dispersion, and boundary information for pseudo-label refinement and reliability-aware supervision.
- Experiments on two medical imaging datasets demonstrate competitive performance, supported by component ablations and uncertainty-estimator comparisons.
Critical weaknesses
- 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.
- 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.
- 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.
- 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.
- 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
- 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?
- 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?
- 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?
- 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?
- 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
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.
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:
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.