acceptodds
Under review as a conference paper at ICLR 2027

Learning from Uncertain Agreement and Informative Disagreement for Semi-Supervised 3D Medical Image Segmentation

Abstract

Teacher–student learning is widely used for semi-supervised 3D medical image segmentation, yet effectively exploiting uncertain and conflicting teacher predictions remains challenging. Directly enforcing agreement may preserve ambiguity, whereas suppressing difficult regions can discard useful supervisory cues. To address this dilemma, we propose a reflective teacher–student framework that interprets teacher guidance according to predictive state and disagreement behavior. Specifically, Consensus Sharpening and Disagreement Reconciliation (CSDR) distinguishes uncertain agreement from informative disagreement and applies state-adaptive supervision to refine tentative consensus and reconcile meaningful conflicts. Teacher-Perturbation Disagreement Probing (TPDP) further characterizes disagreement through its responses to controlled teacher-probability perturbations and uses these responses to modulate teacher-guided learning. Experiments on BraTS2019, LA, and Pancreas-NIH demonstrate consistent improvements under limited-label settings, achieving the highest Dice score across all six evaluated labeling settings. The code will be publicly released upon acceptance.

Primary area:
unsupervised, self-supervised, semi-supervised, and supervised representation learning
Keywords:
Semi-supervised learning;Uncertainty-aware consistency learning;3D medical image segmentation;Disagreement learning

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 3 reviews, above 85% of the others.
Reviewer_H7YROpenReview ↗
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3
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Paper summary

The paper proposes a teacher–student framework for semi-supervised 3D medical image segmentation. Consensus Sharpening and Disagreement Reconciliation (CSDR) distinguishes uncertain agreement from informative disagreement using prediction agreement and entropy. It sharpens shared targets for uncertain agreement and progressively combines entropy minimization with confidence-weighted alignment for disagreement. Teacher-Perturbation Disagreement Probing (TPDP) perturbs teacher probabilities and uses the mean and variance of disagreement responses to weight supervision from the original teacher. The framework incorporates labeled-data pretraining and 3D CutMix. Experiments on LA, BraTS2019, and Pancreas-NIH cover two annotation budgets per dataset. The method reports the highest Dice among the listed methods in all six settings, with particularly notable improvements on Pancreas-NIH. Component ablations and sensitivity analyses provide additional evaluation.

Critical strengths
  1. Pancreas-NIH provides the strongest empirical result. At 10% labels, the reported Dice increases from the strongest listed comparator’s 78.53 to 82.92, and from the framework baseline’s 77.86 to 82.92. These gains suggest practical value for limited-label segmentation.
  2. The framework explicitly assigns different supervision strategies to different predictive states. CSDR and TPDP each improve the baseline across all three datasets, and their combination performs best in the module ablation. This supports the practical usefulness of integrating the two components.
Critical weaknesses
  1. TPDP uses perturbations to construct weights while retaining the original teacher as the supervision target. With zero perturbation, its score reduces to a function of the original teacher–student KL divergence. The current experiments do not clearly distinguish the benefit of probing from that of simply emphasizing larger discrepancies. The TP-only objective is also insufficiently defined. This matters because perturbation-response analysis is a central claimed contribution.
  2. The reported CML Dice/Jaccard pair of 77.26/56.21 requires clarification under standard binary metric definitions and matching averaging conventions. Several algorithm-defining settings are also omitted, making the comparison protocol difficult to reconstruct fully. In addition, the overlap gains do not consistently extend to boundary metrics, particularly on BraTS2019. These issues call for a targeted audit and a more precise account of the method’s benefits.
Questions for authors
  1. What exact objective is used for the TP-only configuration? When disagreement weighting is removed, how do the perturbations influence student optimization?
  2. Does TPDP outperform direct original-KL weighting when the effective loss scale is matched? If this comparison is already represented by the DW-only variant, please specify its exact formula and configuration.
  3. Can you verify the CML Dice/Jaccard values of 77.26/56.21 and explain their aggregation conventions? Under standard binary definitions and matching case weights, the reported mean Dice implies a mean Jaccard of at least approximately 62.95%.
5 comments

Critical Weaknesses:1.TPDP uses perturbations to construct weights while retaining the original teacher as the supervision target. With zero perturbation, its score reduces to a function of the original teacher–student KL divergence. The current experiments do not clearly distinguish the benefit of probing from that of simply emphasizing larger discrepancies. The TP-only objective is also insufficiently defined. This matters because perturbation-response analysis is a central claimed contribution.

Response: We thank the reviewer for this important comment. We agree that the original manuscript did not sufficiently clarify the TP-only objective or distinguish the contribution of perturbation-response analysis from direct KL-based disagreement weighting. We have therefore revised the ablation study in Section 4.3 to explicitly define these configurations and introduce additional uniform-scaling baselines.

Specifically, TP-only uses the K perturbed teacher predictions as direct supervisory targets for the student, following the same perturbation procedure and settings as full TPDP. Its loss averages the KL divergence between each perturbed teacher prediction and the student prediction, without disagreement-based weighting. By contrast, DW-only removes teacher perturbations and weights the KL divergence between the original teacher and student predictions according to its instantaneous magnitude. It uses the same λμ\lambda_\mu as full TPDP.

In particular, DW-only corresponds to the zero-perturbation limit of TPDP. When the perturbation magnitude \delta=0, all perturbed teacher predictions reduce to the original teacher prediction, yielding μR(v)=D(v)\mu_R(v)=D(v) and σR2(v)=0\sigma_R^2(v)=0, where D(v)=KL(pt(v)∥ps(v))D(v)=\mathrm{KL}(p^t(v)\parallel p^s(v)). Consequently, the TPDP weighting score reduces to S(v)=λμD(v)S(v)=\lambda_\mu D(v), which gives exactly the DW-only formulation. This comparison therefore isolates the additional contribution of perturbation-response information beyond instantaneous KL-based weighting.

We have also introduced two uniform-scaling baselines to examine whether the improvements arise merely from increasing the overall consistency-loss magnitude. Uniform-Mean preserves the average TPDP weighting factor while removing its voxel-wise variation, whereas Uniform-2× applies a simple fixed global scaling factor of two.

As shown in Table 6, both TP-only and DW-only improve upon the baseline. Full TPDP achieves the best results across all four metrics on all three datasets and outperforms both individual variants and the two uniform-scaling baselines. These results support the additional benefit of perturbation-response-guided voxel-wise weighting beyond direct KL-based disagreement weighting and global consistency-loss scaling.

The corresponding loss formulations, experimental configurations, and ablation results have been incorporated into the revised Section 4.3 and Table 6.

2.The reported CML Dice/Jaccard pair of 77.26/56.21 requires clarification under standard binary metric definitions and matching averaging conventions. Several algorithm-defining settings are also omitted, making the comparison protocol difficult to reconstruct fully. In addition, the overlap gains do not consistently extend to boundary metrics, particularly on BraTS2019. These issues call for a targeted audit and a more precise account of the method’s benefits.

Response: We sincerely thank you for the careful examination of our experimental results and for raising these important concerns regarding metric consistency, experimental reproducibility, and boundary performance. We agree that these aspects require careful verification and clearer presentation. We have therefore revised the experimental results and supplemented the implementation details and sensitivity analyses, as described below.

(1) Verification and correction of the CML results.

We thank you for identifying the inconsistency in the reported CML Dice/Jaccard pair (77.26/56.21). After tracing its source, we confirmed that these values, reported in Table 3 for the Pancreas-NIH dataset, were taken from the comparative results in Dycon (Assefa M, Naseer M, Ganapathi I, et al. Dycon: Dynamic uncertainty-aware consistency and contrastive learning for semi-supervised medical image segmentation. CVPR, 2025), rather than independently calculated using our evaluation pipeline. In the original submission, the quantitative results of the compared methods were primarily collected from their original publications or other relevant comparative studies, rather than obtained by rerunning all methods under a unified evaluation protocol. Consequently, we had not independently verified whether the reported CML Dice and Jaccard values were calculated using matching binary segmentation definitions and aggregation conventions. We acknowledge that this practice was not sufficiently rigorous and sincerely apologize for this oversight.

To improve the reliability and consistency of the quantitative comparisons, we reran all compared semi-supervised methods on the three datasets. In the original submission, their results were primarily collected from the original publications or relevant comparative studies. In the revised manuscript, all methods are evaluated using a unified pipeline, with Dice, Jaccard, ASD, and HD95 computed independently for each test case and reported as mean ± standard deviation. Accordingly, Tables 1-3 have been updated based on the reproduced results, and some quantitative values differ from those in the original submission. In particular, the CML results in Table 3 are now based on our reproduced experiments, with Dice/Jaccard values of 69.50 ± 12.49/53.40 ± 14.53 under the 10% labeled-data setting and 77.60 ± 7.91/63.60 ± 10.33 under the 20% setting.

(2) Completeness of implementation details and reproducibility.

We agree that the original manuscript did not sufficiently document several algorithm-defining hyperparameters, which could make the proposed framework difficult to reproduce. We have therefore expanded the Datasets and Experimental Setup section to explicitly specify the key parameter settings. These include the dynamic scheduling of the low- and high-entropy thresholds in CSDR, the temperature parameter and power-sharpening exponent in consensus construction, the perturbation magnitude, mean and variance weighting coefficients, and the number of perturbation samples in TPDP, as well as the loss weighting coefficients of the two proposed mechanisms.

Furthermore, we have substantially expanded the sensitivity analyses in the appendix to examine the effects of these key design choices. Specifically, we investigate the effects of temperature scaling and power-sharpening exponents within the +CS configuration, the sensitivity of CSDR to different entropy-threshold configurations, the influence of TPDP perturbation magnitude, the relative loss weights of CSDR and TPDP, and the balance between Consensus Sharpening and Disagreement Reconciliation. We also visualize the spatial distributions of the UA and ID masks under different threshold configurations to illustrate how threshold choices affect the regions selected by CSDR.

These additional descriptions and experiments provide a more complete account of the implementation settings and their influence on segmentation performance, thereby improving the reproducibility and transparency of the proposed framework.

(3) Discrepancy between overlap and boundary metrics.

We acknowledge your observation that improvements in region-overlap metrics do not consistently translate into better boundary-distance metrics, particularly on BraTS2019. A closer examination of the results confirms this observation. Our method achieves the highest Dice and Jaccard scores under both annotation settings. However, UnCo achieves lower ASD under both settings (1.96 vs. 3.07 at 10% and 1.68 vs. 2.45 at 20%). At the 10% setting, UnCo also achieves a lower HD95 (8.75 vs. 11.33), whereas our method obtains the best HD95 at the 20% setting (7.83).

This difference reflects the distinct optimization objectives of the proposed framework. CSDR and TPDP primarily improve semi-supervised learning by providing state-adaptive and perturbation-response-guided voxel-wise supervision, rather than explicitly optimizing surface-distance metrics. Consequently, improvements in regional overlap do not necessarily lead to uniformly improved boundary localization, particularly in anatomically complex structures with irregular boundaries. To address this point, we have refined the quantitative results discussion in the revised manuscript to explicitly distinguish improvements in regional overlap from those in boundary-distance metrics. In particular, we now explicitly acknowledge that the improvements in Dice and Jaccard on BraTS2019 are not consistently accompanied by improvements in ASD and HD95. We believe this provides a more balanced and accurate assessment of the proposed method across different evaluation criteria.

We sincerely appreciate your constructive comments, which have helped us identify inconsistencies in the original comparisons, improve the completeness of our experimental descriptions, and present the strengths and limitations of the proposed framework more accurately.

Reviewer_5MipOpenReview ↗
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3
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4
Informativeness
2
Presentation
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2
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Paper summary

This paper proposes Consensus Sharpening and Disagreement Reconciliation and Teacher-Perturbation Disagreement Probing losses to address the dilemma of enforcing agreement or suppressing difficult regions. The authors evaluate their proposed method on three public 3D medical image segmentation datasets: BraTS2019, LA, and Pancreas-NIH. It achieves good results on the LA and Pancreas-NIH datasets (best scores on most metrics), and fair results on BraTS2019 (two best, and three 2nd-best out of 8 metrics). The ablation study also shows that each component has a positive contribution to the overall method.

Critical strengths
  • The distinction between uncertain agreement and informative disagreement offers an intuitive taxonomy for semi-supervised segmentation.
Critical weaknesses

-Currently, the gains of the method compared to previous work, ie. CMFN seem to be limited and unlikely to be statistically significant. The paper would be strengthened if the results were accompanied by error bars, confidence intervals, or statistical significance tests. Also the comparsions on pancreas-NIH dataset doesn't provide results from CMFN. Therefore, it is uncertain whether this works exceeds sota. -Some of the architectural components are outdated. The backbones used in the comparison, which are 3D U-Net (Cicek et al., 2016) for BraTS2019 and V-Net (Milletari et al., 2016) for LA and Pancreas-NIH, are a bit old. It would be interesting if the authors could compare it on a more recent backbone. -To ensure that this work in semi-supervised learning is meaningful it should be also compared with medical image foundational models: e.g Vista3D, MedSAM 2 -The paper could benefit from further ablations. Currently, it is difficult to tell whether gains come from the spatial distribution of sensitive disagreement or simply from scaling up the unsupervised loss. It would be useful to ablate against a uniform scaling.

Questions for authors

-How does the proposed method perform on the modern segmentation backbones? -How does the proposed model compare to medical image foundation models?

4 comments

Critical Weaknesses: -Currently, the gains of the method compared to previous work, i.e. CMFN seem to be limited and unlikely to be statistically significant. The paper would be strengthened if the results were accompanied by error bars, confidence intervals, or statistical significance tests. Also the comparisons on pancreas-NIH dataset doesn't provide results from CMFN.

Response:

(1) Statistical reliability of the performance improvements. We agree that the performance differences between our method and strong existing approaches, particularly CMFN, should be supported by statistical evidence rather than mean performance alone. To address this concern, we now report the mean and standard deviation of all evaluation metrics across test patients in Tables 1-3. Furthermore, we perform two-sided paired t-tests to compare our method with the corresponding second-best method for each metric on which our method achieves the highest mean performance. Statistically significant improvements (p < 0.05) are marked with “†” in the revised tables. These analyses provide a more comprehensive assessment of both the variability and statistical significance of the observed performance improvements.

(2) CMFN results and unified re-evaluation of comparison methods.We thank you for pointing out the absence of CMFN results on the Pancreas-NIH dataset. In the original submission, the quantitative results of the compared methods were primarily collected from their original publications or relevant comparative studies, rather than obtained by rerunning all methods under a unified evaluation protocol. Since the original CMFN paper did not report experiments on Pancreas-NIH and its source code was not publicly available, we did not have an independently verified CMFN result for this dataset to include in the original comparison.

To address this limitation and improve the reliability and consistency of the experimental comparisons, we have now rerun all compared methods on LA, BraTS2019, and Pancreas-NIH and reevaluated their predictions using a unified evaluation pipeline. For CMFN, we independently implemented the method based on its published methodological description and evaluated it on Pancreas-NIH under the same experimental protocol and backbone configuration as the other compared methods. Specifically, Dice, Jaccard, ASD, and HD95 are calculated independently for each test case and then summarized across the test set as mean and standard deviation.

Accordingly, we have updated the quantitative results in all three dataset-wise comparison tables based on our reproduced experiments. We have also added the results obtained from our independent implementation of CMFN on Pancreas-NIH to Table 3. Consequently, some quantitative results in the revised manuscript differ from those in the original submission.

-Some of the architectural components are outdated. The backbones used in the comparison, which are 3D U-Net (Cicek et al., 2016) for BraTS2019 and V-Net (Milletari et al., 2016) for LA and Pancreas-NIH, are a bit old. It would be interesting if the authors could compare it on a more recent backbone.

Response: We thank you for this valuable suggestion. We agree that evaluating our method with a more recent segmentation backbone would provide additional evidence of its applicability beyond conventional architectures.

In the main comparisons, we use the same segmentation backbone for our method and all compared semi-supervised methods within each dataset: 3D U-Net for BraTS2019 and V-Net for LA and Pancreas-NIH. This controlled setting minimizes the influence of architectural differences and allows a more direct comparison of the underlying semi-supervised learning strategies.

To further investigate the compatibility of our framework with recent segmentation architectures, we have conducted additional experiments using SegMambaV2 (Xing Z, Ye T, Yang Y, et al. Segmamba-v2: Long-range sequential modeling mamba for general 3d medical image segmentation. IEEE Transactions on Medical Imaging, 2025). Specifically, we replace V-Net with SegMambaV2 and evaluate our framework on the LA dataset under both 10% and 20% labeled-data settings, while retaining the CSDR and TPDP mechanisms unchanged.

As shown in Table 9 in Section A.4 of the Appendix, our method achieves slightly better overall segmentation performance with SegMambaV2 than with the original V-Net backbone under both labeling settings. These results provide preliminary evidence that the proposed supervision strategy can be applied to more recent segmentation architectures and is not restricted to conventional backbones.

-To ensure that this work in semi-supervised learning is meaningful it should be also compared with medical image foundational models: e.g Vista3D, MedSAM 2.

Response: We sincerely thank you for this valuable suggestion. We agree that including medical image foundation models as additional references would provide a broader perspective for evaluating the proposed semi-supervised segmentation framework. We have therefore incorporated MedSAM2 (Ma J, Yang Z, Kim S, et al. Medsam2: Segment anything in 3d medical images and videos. arXiv preprint arXiv:2504.03600, 2025) as a supplementary foundation-model baseline and evaluated it on LA, BraTS2019, and Pancreas-NIH.

Specifically, we use the publicly available pretrained MedSAM2 weights without additional fine-tuning. For each test volume, a bounding-box prompt is generated from the ground-truth segmentation mask of its middle slice and used to initialize MedSAM2, which then propagates the segmentation to the remaining slices to obtain a volumetric prediction.

The corresponding results have been included in the quantitative comparisons in Tables 1-3. With 10% labeled training data, our method achieves higher Dice scores than pretrained MedSAM2 on all three datasets. Given its prompt-based inference setting, MedSAM2 serves as a supplementary foundation-model reference rather than a directly comparable semi-supervised baseline.

-The paper could benefit from further ablations. Currently, it is difficult to tell whether gains come from the spatial distribution of sensitive disagreement or simply from scaling up the unsupervised loss. It would be useful to ablate against a uniform scaling.

Response: Thank you for this insightful suggestion. We agree that it is important to distinguish the benefits of spatially adaptive supervision from those of indiscriminately applying the unsupervised losses or simply increasing their overall magnitude. To address this concern, we have expanded the ablation study in Section 4.3 with additional control experiments for both CSDR and TPDP, as reported in Tables 5 and 6.

For CSDR, we introduce +CS (All Voxels) and +DR (All Voxels), which apply the corresponding losses to all voxels rather than restricting them to their respective prediction-state regions. Both variants perform worse than their region-selective counterparts. This result indicates that CSDR benefits from selecting supervision regions according to predictive states, rather than applying the corresponding losses indiscriminately to all voxels.

For TPDP, we introduce four additional configurations: +TP, +DW, +Uniform-Mean, and +Uniform-2×. These configurations respectively examine the effects of perturbed teacher predictions without disagreement weighting, direct original teacher-student KL-based weighting without perturbations, and two forms of uniform loss scaling. The uniform controls preserve either the average TPDP weighting magnitude or apply a fixed global scaling factor of two, while removing voxel-wise weighting variations. As shown in Table 6, full TPDP achieves the best performance across all four metrics on all three datasets and outperforms both the individual variants and the uniform-scaling baselines.

Taken together, the CSDR and TPDP ablations suggest that the observed performance gains are not merely attributable to applying supervision more broadly or increasing the overall unsupervised-loss magnitude. Instead, they support the contributions of prediction-state-aware region selection in CSDR and perturbation-response-guided spatially adaptive weighting in TPDP. The corresponding formulations and experimental results have been incorporated into Section 4.3 of the revised manuscript.

Questions For Authors:

-How does the proposed method perform on the modern segmentation backbones?

Response: Thank you for this question. As detailed in our response to Critical Weaknesses 2, we have evaluated the proposed framework using SegMambaV2 (Xing Z, Ye T, Yang Y, et al. Segmamba-v2: Long-range sequential modeling mamba for general 3d medical image segmentation. IEEE Transactions on Medical Imaging, 2025), a more recent segmentation backbone. Specifically, we replaced V-Net with SegMambaV2 and conducted experiments on the LA dataset under both 10% and 20% labeled-data settings, while keeping CSDR and TPDP unchanged.

As reported in Table 9 of the Appendix, our method achieves slightly better overall segmentation performance with SegMambaV2 than with the original V-Net backbone under both labeling settings. These results provide preliminary evidence that the proposed supervision strategy is compatible with more recent segmentation architectures and is not restricted to conventional backbones.

-How does the proposed model compare to medical image foundation models?

Response: Thank you for this question. As detailed in our response to Critical Weaknesses 3, we have incorporated pretrained MedSAM2 as a supplementary foundation-model baseline and evaluated it on all three datasets.

Under the 10% labeled-data setting, our method achieves Dice scores of 90.81%, 86.07%, and 82.92% on LA, BraTS2019, and Pancreas-NIH, respectively, compared with 89.65%, 82.15%, and 59.12% obtained by MedSAM2. These results show that our method achieves higher Dice scores across all three datasets, with improvements of 1.16, 3.92, and 23.80 percentage points, respectively.

The corresponding results for Dice, Jaccard, ASD, and HD95 are reported in Tables 1-3. As discussed in our response to Critical Weaknesses 3, MedSAM2 serves as a supplementary foundation-model reference because its prompt-based inference setting differs from the semi-supervised learning paradigm considered in this work.

Reviewer_kbw9OpenReview ↗
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3(+1)
Confidence
4
Informativeness
2
Presentation
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Soundness
2
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Paper summary

This paper proposes a teacher–student framework for semi-supervised 3D medical image segmentation that differentiates supervision according to student–teacher agreement, confidence, and response to perturbations. Its two core design, CSDR and TPDP. CSDR sharpens tentative consensus and progressively reconciles disagreement, while TPDP probes disagreement responses to teacher-probability perturbations to modulate teacher-guided learning.

Critical strengths

Experimental results are reported on multiple public benchmarks, which strengthens the empirical validity of the approach.

Critical weaknesses
  1. while the proposed two main modules are interesing, they lack more explanaiton. for example, CSDR is propsoed" to adapt teacher–student supervision to different predictive states". it seems CSDR will gate the teacher supervision, but Dice and CE loss still use teacher predictions throughout the unlabeled CutMix region, regardless of the CSDR masks. CSDR adds losses on selected voxels, while TPDP's Equ. (24) applies a positively weighted KL loss to every voxel. Thus, the framework does not remove unreliable teacher guidance from the main objective.

  2. sharpenning is widely adpoted in semi/self supervised learning, and the paper designs a complicted method, squares and renormalizes the averaged probabilities, why we need "squares", how it can be better than standard power-sharpening?

  3. Key hyper-parameters, the threshold choices, are not investigated. The entropy thresholds determine which voxels enter CSDR, but the appendix does not vary them or report how mask coverage changes.

  4. while the paper only focuses on modification of the teacher supervions, the proposed methods are very complicated with many hyper-paremeters. but at the same time, the improvements on BraTS2019/LA are sort of marginal.

Questions for authors

equ.25 retains teacher targets throughout the unlabeled CutMix region, how do CSDR and TPDP prevent unreliable teacher pseudo-labels from being reinforced by the main Dice/CE loss?

6 comments

Critical Weaknesses1.While the proposed two main modules are interesting, they lack more explanation. For example, CSDR is proposed “to adapt teacher–student supervision to different predictive states”. It seems CSDR will gate the teacher supervision, but Dice and CE loss still use teacher predictions throughout the unlabeled CutMix region, regardless of the CSDR masks. CSDR adds losses on selected voxels, while TPDP's Equ. (24) applies a positively weighted KL loss to every voxel. Thus, the framework does not remove unreliable teacher guidance from the main objective.

Response: We sincerely thank the reviewer for identifying this important issue. We agree that the original description did not clearly distinguish the global teacher-guided objective from the additional supervision introduced by CSDR and TPDP, which may have led to the impression that the UA and ID masks filter teacher predictions in the main objective. We apologize for this lack of clarity.

In the current formulation, the teacher-supervised Dice and CE terms in L_mix remain active throughout the unlabeled CutMix region. These region-wide losses provide the student with global teacher guidance and support overall semantic and structural consistency across the unlabeled region. The UA and ID masks are not used to gate these main Dice and CE terms. Instead, they select the uncertain-agreement and informative-disagreement voxels on which the respective CS and DR terms in CSDR are applied. Similarly, TPDP applies positive voxel-wise weights to the KL divergence across the unlabeled region, adaptively adjusting the relative contribution of teacher–student consistency according to perturbation responses rather than excluding any voxels. Thus, CSDR and TPDP refine the global teacher-guided supervision through two complementary mechanisms: state-adaptive supervision and perturbation-aware consistency weighting.

To further examine whether explicitly excluding uncertain teacher predictions would improve supervision, we conducted an additional experiment under the 10% labeled-data setting. Specifically, high-entropy unlabeled voxels are excluded from the teacher-supervised Dice and CE terms in L_mix and the TPDP KL loss, while all other training settings remain unchanged. Compared with this hard-exclusion variant, our full method improves Dice by 0.76, 0.92, and 1.57 percentage points on LA, BraTS2019, and Pancreas-NIH, respectively, and Jaccard by 1.25, 1.23, and 1.91 percentage points. It also reduces ASD by 0.10, 0.28, and 0.19, and HD95 by 0.23, 0.77, and 0.58, respectively. The full method outperforms the hard-exclusion variant on all 12 dataset-metric comparisons under this setting, supporting the effectiveness of retaining global teacher supervision while applying the proposed state-adaptive and perturbation-aware supervision mechanisms. Since this experiment evaluates an alternative supervision strategy rather than an additional component or hyperparameter configuration of the proposed framework, we report its results here as a supplementary analysis rather than incorporating it into the revised manuscript.

More broadly, we believe that predictive entropy provides a useful indication of uncertainty but is not a definitive indicator of pseudo-label correctness. High-entropy voxels may include unreliable predictions, but they may also contain informative boundary and anatomical cues. A hard-exclusion strategy based solely on entropy cannot distinguish between these cases and may therefore discard potentially useful supervision signals. This provides a rationale for retaining region-wide teacher guidance while refining supervision according to predictive states and perturbation responses, rather than removing all high-entropy voxels from the global objective.

To clarify these relationships, we have revised the Introduction to explain the role of teacher predictions throughout the unlabeled region in supporting overall semantic and structural consistency. The Method section now specifies that these predictions supervise the mixed Dice and CE losses throughout the unlabeled CutMix region, whereas the UA and ID masks select the voxels for the corresponding CS and DR terms. These clarifications make explicit how the global teacher-guided objective works together with CSDR's state-adaptive supervision and TPDP's perturbation-aware consistency weighting.

3.Key hyper-parameters, the threshold choices, are not investigated. The entropy thresholds determine which voxels enter CSDR, but the appendix does not vary them or report how mask coverage changes.

Response: Thank you for pointing out the insufficient investigation of hyperparameter sensitivity in the original manuscript. We agree that a more systematic evaluation of the key hyperparameters across the proposed framework is necessary, particularly the entropy thresholds that directly determine the selection of uncertain-agreement (UA) and informative-disagreement (ID) voxels in CSDR. To address this concern, we have substantially expanded the sensitivity analyses in the Appendix to examine the effects of key parameter choices on both the individual mechanisms and the overall framework.

Specifically, we have included five complementary analyses: (1) loss weight sensitivity, examining the relative contributions of CSDR and TPDP; (2) perturbation strength sensitivity, evaluating different perturbation magnitudes in TPDP; (3) CS-DR ratio sensitivity, investigating the balance between the two CSDR strategies; (4) temperature scaling and power-sharpening exponent sensitivity, examining their effects on consensus construction; and (5) entropy threshold sensitivity, investigating how different threshold configurations affect CSDR.

Regarding the entropy thresholds, we evaluate five configurations covering fixed thresholds, individual dynamic schedules, reversed schedules, and jointly dynamic schedules. The results are reported in Table 8 of the Appendix. Specifically, the jointly dynamic configuration, with τ_L(e) = 0.3 + 0.2e/E and τ_H(e) = 0.6 − 0.1e/E, achieves the highest Dice and Jaccard scores across all three datasets while maintaining competitive surface-distance performance. These results support the selected dynamic schedules as a balanced configuration for CSDR.

To further illustrate how threshold choices affect the regions selected by CSDR, we have added Fig. 4, which visualizes the UA and ID masks under all five configurations. The UA masks remain predominantly concentrated around the target structure and its boundary regions, while their spatial coverage varies across threshold configurations. In contrast, the ID masks generally exhibit more limited coverage and greater spatial variation across configurations, ranging from a few isolated responses to more extended boundary-adjacent regions. These changes in mask coverage follow from the threshold-based selection rules of CSDR. For fixed predictions, increasing the low-entropy threshold expands the jointly low-entropy agreement regions excluded from UA, whereas decreasing the high-entropy threshold expands the jointly high-entropy disagreement regions excluded from ID. Consequently, the number of voxels eligible for the corresponding auxiliary supervision decreases. The stage-wise visualization in Fig. 5 further shows that the selected regions evolve during training, with UA remaining focused on the target structure while ID becomes more spatially restricted at the later stage.

These additional analyses provide a more comprehensive assessment of hyperparameter sensitivity and clarify how entropy-threshold configurations influence both segmentation performance and the spatial selection of supervision regions in CSDR.

4.While the paper only focuses on modification of the teacher supervions, the proposed methods are very complicated with many hyper-paremeters. but at the same time, the improvements on BraTS2019/LA are sort of marginal.

Response: We thank the reviewer for raising this important concern regarding the trade-off between methodological complexity and performance improvement. We acknowledge that the gains on LA and BraTS2019 are relatively modest and that the proposed framework introduces additional complexity during training. We have therefore further examined the contributions of the individual mechanisms, the sensitivity to key hyperparameters, and the computational implications of the proposed design.

Our objective is to improve the allocation and weighting of teacher-student supervision under different predictive states and perturbation responses, rather than to introduce additional segmentation architecture components. Specifically, CSDR distinguishes uncertain agreement from informative disagreement and provides state-adaptive supervision for the corresponding voxel regions, whereas TPDP exploits perturbation-response information to adaptively weight voxel-wise teacher-student KL consistency. These mechanisms address complementary aspects of teacher-student supervision.

The ablation results provide further evidence for the necessity of these designs. As shown in Table 5, the full CSDR outperforms its individual components and the corresponding all-voxel variants, demonstrating the benefit of selecting supervision regions according to predictive states rather than indiscriminately applying auxiliary supervision. Similarly, Table 6 shows that full TPDP achieves the best results across all four metrics on all three datasets, outperforming TP-only, DW-only, and the two uniform-scaling baselines. These comparisons indicate that the improvements are attributable to the respective region-selection and perturbation-response-guided weighting strategies, rather than simply to broader supervision or an increased overall consistency-loss magnitude.

Regarding computational complexity, we acknowledge that CSDR and TPDP introduce additional operations and hyperparameters during training. However, these mechanisms do not modify the underlying segmentation architecture or introduce additional inference modules. After training, only the student segmentation network is retained for inference, without requiring the EMA teacher, perturbation sampling, or auxiliary supervision mechanisms. Therefore, the proposed framework introduces no additional architectural or computational overhead during inference compared with the underlying segmentation backbone.

Regarding hyperparameter selection, all datasets are evaluated using the same hyperparameter configuration rather than independently optimized dataset-specific settings. Furthermore, we have substantially expanded the sensitivity analyses in the Appendix, covering the loss weights, perturbation magnitude, CS-DR balance, entropy thresholds, temperature scaling, and power-sharpening exponent. These experiments provide a more systematic assessment of the key parameter choices and their effects on segmentation performance across the three datasets.

Regarding the reliability of the quantitative comparisons, results in the original submission were primarily collected from the original publications or related comparative studies. In the revision, we reran all compared semi-supervised methods on the three datasets using the same experimental protocols and backbone configurations as our method. We used publicly available implementations except for CMFN, whose source code is unavailable; CMFN was independently implemented based on its published methodology. All methods were evaluated using a unified pipeline, with Dice, Jaccard, ASD, and HD95 computed per test case and summarized as mean ± standard deviation. Accordingly, Tables 1–3 have been updated with the reproduced results, and some quantitative values differ from those in the original submission.

Based on these reproduced results, our method achieves the highest mean Dice across all six dataset-labeling settings, with gains of 0.58/0.60 percentage points on LA, 0.81/0.31 on BraTS2019, and 3.66/1.86 on Pancreas-NIH, relative to the best competing method under the 10%/20% labeled-data settings, respectively. We acknowledge that the improvements on LA and BraTS2019 are modest. To provide a more rigorous assessment, the revised Tables 1-3 report mean ± standard deviation, with † indicating statistically significant improvements (p < 0.05) based on two-sided paired t-tests.

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