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- Informativeness
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Paper summary
HCT-Net trains a SegMamba branch and a Swin UNETR branch for semi-supervised 3D segmentation. An exponential moving average of labeled-training-batch foreground Dice chooses the temporary teacher. A relative-performance gate activates cross-branch training, while a ramp-up schedule and the teacher's confidence coverage weight each unlabeled sample's pseudo-label loss. A detached feature-alignment objective follows the same direction. Both branches continue receiving supervised losses. At inference, a branch or a validation-selected probability fusion is used. Evaluation on ACDC and LA covers 10% and 15% labeling. At 15%, HCT-Net improves Dice over symmetric CPS with the same heterogeneous pair by 1.09 and 2.20 percentage points, respectively. Homogeneous controls and descriptive disagreement/error trajectories provide further analysis of the complete configuration.
Critical strengths
S1 The mathematical specification makes the training policy inspectable
Secs. 3.3-3.6 specify a score EMA rather than a parameter EMA, detached teacher targets, full-domain pseudo-label cross-entropy, and a separate feature-alignment loss. The text explicitly states that coverage weights a whole sample rather than filtering individual voxels. These details make it possible to identify what supervision is actually applied, and they are more useful than describing the method simply as reliability-aware co-training.
S2 The matched backbone control is more informative than an unmatched architecture comparison
Table 3 holds the Mamba-Transformer pair fixed and improves Dice from 0.8192 to 0.8301 on ACDC and from 0.8280 to 0.8500 on LA, with corresponding surface-metric improvements. The homogeneous controls also expose a negative result: HCT reduces ACDC Dice for the homogeneous Mamba pair from 0.8219 to 0.7871. Reporting that dependence is helpful and argues against treating the controller as universally beneficial. The parameter-count analysis further shows that the best heterogeneous result is not simply the result of having the most parameters. [Secs. 4.4-4.6; Table 3, p. 8.]
Critical weaknesses
W1 The reported comparison does not identify the benefit of coordination
Table 3 holds the backbone pair fixed, which is a useful control, but it changes the full training strategy. HCT replaces two-way supervision with one-way supervision, changes its effective weight, and adds directed feature matching. The gain can therefore reflect reduced pseudo-label pressure or feature regularization without establishing that coordinating the three decisions is beneficial. This matters because the paper itself identifies performance-based dynamic teaching in DiCo (Xu et al., CVPR 2025) as prior work; the new claim is the value of the coordination. The current contrast establishes a package-level improvement over symmetric CPS, not the proposed explanation for that improvement.
The inference protocol introduces another unresolved source of benefit. Sec. 3.7 allows a selected branch or validation-chosen probability fusion, together with optional TTA and connected-component processing. The actual choices for the CPS and HCT rows are not reported. A heterogeneous pair may improve through complementary inference errors, even if its training-time reliability policy adds little. Figure 3's larger disagreement is compatible with that alternative. The homogeneous Mamba degradation on ACDC, from 0.8219 to 0.7871, is also informative: lower performance under the controller cannot be explained solely by insufficient parameter count. The paper acknowledges this result, but does not connect it to routing behavior or supervision exposure. [Table 3; Secs. 3.7 and 4.4-4.6.]
W2 The reliability diagnostics do not measure the reliability claim on a common population
Eq. 8 compares the selected teacher's current labeled-training Dice with a fraction of its own smoothed score. A branch with persistently poor but stable predictions can pass this gate: once its current and smoothed positive scores agree, the inequality holds for either reported alpha. The gate detects a relative drop in training fit, not absolute pseudo-label quality. Coverage in Eq. 11 averages over all voxels, so confident background can give a sample a high weight even when its foreground predictions are unreliable. The full-domain loss still teaches low-confidence foreground voxels. Meanwhile, feature alignment bypasses the ramp and coverage factors entirely. Thus the mechanisms do not uniformly suppress unreliable cross-branch information, even when pseudo-label weighting is small.
Figure 3 does not resolve these limitations. For LA, disagreement is measured on validation volumes, whereas pseudo-label error is measured only on active pseudo-supervision mini-batches. Because each configuration has its own teacher ranking and gate, the error curves can condition on different crops and training stages. A lower curve can reflect easier selected examples rather than more accurate pseudo-labels on the same examples. For ACDC, shared error overlap is an intersection-over-union restricted to ground-truth foreground: it omits false-positive regions and changes when the sizes of either branch's error set change. Neither statistic establishes that the selected teacher is better than its peer on the routed unlabeled batch. The curves are useful descriptions, as the text calls them, but they cannot carry the causal explanation attributed to reliable heterogeneous coordination. [Sec. 4.5; Figure 3.]
Figure 1 also raises a provenance and accuracy concern. I would like clarification about possible generative-AI assistance in constructing this illustration; appearance alone cannot establish its provenance. The verifiable issue is that panel (b) draws a sequence from hard pseudo-label to confidence map to coverage mask to safety gate. Confidence requires the probability map, and Eq. 8's gate depends on labeled Dice and warm-up, not coverage. The caption partly acknowledges the schematic nature but leaves these arrows misleading. The AI Use Statement mentions ideation, literature retrieval, drafting, and polishing, but does not say whether figures were generated or edited. The authors should clarify this and make the figure agree with the actual computation; this concern is about faithful scientific communication, not proof that experimental data were fabricated.
Questions for authors
Q1 What changed between the matched CPS and HCT results
For the two heterogeneous rows in Table 3, were the supervised Hausdorff term, training budget, checkpoint criterion, and inference rule identical? Please identify the branch or fusion coefficient, TTA, and connected-component settings actually used for each. Which reported observation distinguishes improved training-time coordination from a change in regularization strength or inference-time ensembling?
Q2 What is the population behind Figure 3
For each LA configuration, which samples and epochs enter the active-batch error curve, and what fraction of candidate batches is excluded by its gate? Does the plotted error average first over crops, batches, or voxels? Please explain how the curves can be compared when their inclusion rule is method-dependent. For ACDC, what happens to the shared-error ratio when one branch improves while the other does not? These definitions are necessary to interpret the existing diagnostics.
Q3 What does the gate protect against in the observed runs
Do the available routing records show that the labeled-training-score winner provides better unlabeled targets than its peer, or only that it fits the labeled crops better? How do those records explain the homogeneous Mamba failure? Please also explain what limits unreliable feature transfer immediately after warm-up, since Eq. 15 lacks the ramp and coverage factors used in Eq. 12. A mechanistic explanation tied to the reported runs would be more informative than a general claim that the controller is adaptive.
Q4 Were generative tools used to produce the figures
Was Figure 1 generated or substantially edited using generative AI, and if so, which elements and how were their computational dependencies checked? Please reconcile the confidence-to-gate arrows with Eqs. 8 and 11. For clarity, distinguish any illustrative assets from Figures 2 and 3, which are presented as experimental evidence, and state whether those panels were rendered directly from segmentation outputs and recorded training diagnostics. This requests provenance and an accurate depiction; it does not presume that those experimental panels were generated.
3 comments
Q3. Do the available routing records show that the labeled-training-score winner provides better unlabeled targets than its peer, or only that it fits the labeled crops better? How do those records explain the homogeneous Mamba failure? Please also explain what limits unreliable feature transfer immediately after warm-up, since Eq. 15 lacks the ramp and coverage factors used in Eq. 12. A mechanistic explanation tied to the reported runs would be more informative than a general claim that the controller is adaptive.
A3. The gate controls when cross-branch transfer is active. After warm-up, Eq. (8) checks whether the selected teacher’s current labeled-batch Dice exceeds a fraction of its own EMA. A low but stable positive Dice can satisfy this relative criterion. The score thus has a specific role: it ranks the branches by their smoothed labeled-batch performance. Figure 3 characterizes the corresponding training behavior at the configuration level.
The shared gate disables feature alignment on iterations that fail this check. On active iterations, the feature loss uses its own coefficient and the detached teacher feature directs the update to the student side. The ramp-up and coverage factors instead scale the pseudo-label cross-entropy. The revised Figure 1 (p. 4) depicts these separate controls, which are defined in Eqs. (12)–(16).
Table 3 (p. 8) also shows why the backbone pairing matters empirically. On ACDC, Dice moves from 82.19% to 78.71% for homogeneous Mamba and from 81.92% to 83.01% for the heterogeneous pair when switching from CPS to HCT. The two outcomes support evaluating the training policy together with the backbone pairing. This is the distinction we emphasize in Sec. 4.7 (p. 8).
Q4. Was Figure 1 generated or substantially edited using generative AI, and if so, which elements and how were their computational dependencies checked? Please reconcile the confidence-to-gate arrows with Eqs. 8 and 11. For clarity, distinguish any illustrative assets from Figures 2 and 3, which are presented as experimental evidence, and state whether those panels were rendered directly from segmentation outputs and recorded training diagnostics. This requests provenance and an accurate depiction; it does not presume that those experimental panels were generated.
A4. We used generative AI to produce reference artwork for the original Figure 1 and redrew the framework in Draw.io. Some illustrative icons in the submitted figure came from the reference artwork. The revised figure uses editable vector elements drafted with AI assistance. Its volume icons are vector traces of example 2D slices with schematic depth. We added this disclosure to the AI Use Statement (p. 9).
Your comment identified a specific mismatch between the original diagram and Eq. (8). In revised Figure 1(b) (p. 4), the gate receives warm-up status and the teacher’s current labeled-batch Dice relative to its EMA-based threshold. The teacher’s probability map now branches separately into hard pseudo-labels and voxel-wise confidence, following Eqs. (10)–(11). Coverage and ramp-up enter the crop-level weight in Eq. (12), which scales cross-entropy in Eq. (13). Feature alignment shares the gate in Eq. (15) and uses its own coefficient in Eq. (16). We also updated Figure 1(a) to show labeled inputs reaching both branches and supervised loss entering the total objective. The revised caption and Sec. 3.4 (pp. 4–5) now follow the same computational paths.
Figure 2 was rendered directly from segmentation outputs and reference masks. Figure 3 was plotted directly from the training diagnostics described in Sec. 4.5. The AI-generated reference artwork was used for the framework illustration in Figure 1.
Thank you for the detailed response. The authors have partially addressed my concerns. However, the contribution of the proposed coordination mechanism and the reliability of teacher selection remain insufficiently demonstrated. Accordingly, I have updated my score from 1 (Clear Rejection) to 2 (Weak Rejection).
A0. Thank you for identifying the incorrect dependency in the original schematic and for asking us to clarify the training diagnostics. We corrected Figure 1 and its caption (p. 4), aligned the description in Sec. 3.4 (pp. 4–5) with the revised paths, clarified the LA curves in Sec. 4.5 (p. 7), and expanded the AI Use Statement (p. 9).
Q1. For the two heterogeneous rows in Table 3, were the supervised Hausdorff term, training budget, checkpoint criterion, and inference rule identical? Please identify the branch or fusion coefficient, TTA, and connected-component settings actually used for each. Which reported observation distinguishes improved training-time coordination from a change in regularization strength or inference-time ensembling?
A1. The shared control in Table 3 is the SegMamba–Swin UNETR backbone pair. At 15% labeling, the complete HCT configuration improves mean Dice over symmetric CPS from 81.92% to 83.01% on ACDC and from 82.80% to 85.00% on LA. HD95 and ASD are also lower on both datasets. The gain therefore extends across both overlap and surface-distance metrics at this labeling level.
For HCT-Net, Sec. 4.1 (p. 6) specifies a supervised Hausdorff coefficient of 0.1 and a schedule of 200 supervised warm-up epochs followed by 250 semi-supervised epochs. Sec. 3.7 (p. 5) describes the validation-based selection of the branch or fixed probability fusion and any test-time augmentation or post-processing. The quantitative claim in Table 3 (p. 8) is a comparison of the evaluated HCT and CPS configurations with the backbone pair held fixed. Its central result is the improvement of the complete HCT configuration on both benchmarks at 15% labeling.
Q2. For each LA configuration, which samples and epochs enter the active-batch error curve, and what fraction of candidate batches is excluded by its gate? Does the plotted error average first over crops, batches, or voxels? Please explain how the curves can be compared when their inclusion rule is method-dependent. For ACDC, what happens to the shared-error ratio when one branch improves while the other does not? These definitions are necessary to interpret the existing diagnostics.
A2. For LA, the two panels describe different populations. Foreground prediction disagreement is evaluated on validation volumes. Pseudo-label error is computed as one minus Dice against reference masks on training mini-batches with active pseudo-supervision. The reference masks are used only for the diagnostic. We added a clarification in Sec. 4.5 (p. 7) that each error curve summarizes the active batches of its own configuration. The relative heights of the curves therefore reflect pseudo-label accuracy together with the composition of the selected batches. We interpret the LA error curves as descriptive training trajectories conditional on each configuration’s active batches.
For ACDC, shared-error overlap measures the intersection-over-union of the two error sets within reference foreground. With one branch fixed, correcting a shared error shrinks the intersection while leaving the union unchanged. Correcting an error unique to the improving branch shrinks the union while leaving the intersection unchanged, which can increase the ratio. This explains why the metric depends on which errors are corrected as well as how many.