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Under review as a conference paper at ICLR 2027

Adaptive Nested-Path Conformal Prediction for Medical Image Segmentation

Abstract

Reliable uncertainty quantification is essential for medical image segmentation, where missed object regions can affect downstream clinical decisions. We present Conformal Prediction Adaptive Segmentation (CPAS), a conformal prediction framework for image segmentation that constructs compact prediction sets with finite-sample coverage guarantees. Unlike confidence-thresholding methods that treat pixels independently, and morphological dilation methods, which expand masks uniformly, CPAS defines a nested expansion path that jointly exploits model confidence and spatial structure. Starting from the predicted mask, CPAS iteratively adds boundary pixels through a confidence-guided exploitation step combined with a spatial exploration mechanism, and calibrates a threshold on the accumulated uncertainty along this path. The resulting sets adapt to both the model’s soft predictions and the object geometry while preserving conformal validity. More generally, we formalize conformal calibration over input-dependent nested prediction paths. Experiments on multiple medical imaging benchmarks show that CPAS achieves the target object coverage while producing substantially more compact prediction sets than conformal segmentation baselines. On average, CPAS reduces stretch by approximately 20% compared to previous methods. These results demonstrate that confidence-guided spatial expansion is an effective approach for producing compact, statistically valid segmentation uncertainty sets.

Primary area:
interpretability and explainable AI
Keywords:
conformal prediction, segmentation, nested path

Reviews

Among:
Shape:
1234this paper, Top 32%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.50 over 4 reviews, above 68% of the others.
Reviewer_tnNjOpenReview ↗
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2
Confidence
3
Informativeness
3
Presentation
2
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2
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Paper summary

This work introduces an image-adaptive nested boundary expansion path for calibrating conformal segmentation.

Critical strengths

The key novelty is constructing the segmentation prediction set as an image-adaptive nested expansion path, separating two aspects: the expansion mechanism and its extent. Expansion is guided by confidence and spatial-structure heuristics, and conformal calibration provides finite-sample coverage guarantees on how far expansion can proceed.

Critical weaknesses

The proposed method is simple and easy to understand. However, I doubt whether its performance can meet the bar for ICLR. Since the visualizations are not striking enough, I remain skeptical about the reported performance gains. Could the authors report key metrics including FNR and FPR (or Dice and IoU)? The current set of results is insufficient to convince me.

Questions for authors

Beyond the aforementioned weaknesses, I note that the paper is missing citations and comparisons with several closely related approaches:

  • Conformal Risk Training: End-to-End Optimization of Conformal Risk Control
  • Enhancing image-conditional coverage in segmentation: adaptive thresholding via differentiable miscoverage loss
  • Automatically adaptive conformal risk control
Reviewer_ThqfOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

The paper proposes Conformal Prediction Adaptive Segmentation (CPAS), a method that constructs segmentation uncertainty regions by expanding an initial predicted mask along an image-dependent nested path. Different from classical confidence thresholding or uniform dilation, CPAS incorporates spatial adjacency into the model confidence to determine which boundary voxels should be considered. The conformal calibration step then translates this adjusted approach to attain a prescribed object-coverage set. I see the approach as very intuitive and, from a theoretical perspective, it is only a direct application of split conformal prediction to nested sets. So, I do not see any major theoretical contributions in this paper. I also have several concerns, specifically in ignoring some very closely related and recent proposals as well as the calibration algorithm's adequacy in handling edge cases, the novelty of the conformal formulation, and the adequacy of the experimental baselines.

Critical strengths

The problem that the paper addresses is a genuine limitation of segmentation uncertainty quantification. The existing prediction regions can become spatially fragmented when defined through voxel-level confidence thresholding, or unnecessarily large when obtained by uniform morphological dilation. So the method addresses a valid problem.

The exploitation–exploration construction is relatively straightforward and can be applied to pretrained segmentation networks without retraining.

Although I do not regard Theorem 1 as a fundamentally new conformal result, the explicit separation of an image-dependent expansion path from a conformal stopping threshold is conceptually useful.

Critical weaknesses

1 My main concern is on Theorem 1. I think it requires additional assumptions for its coverage guarantee. The Theorem is based on a standard conformal argument, i.e. construct a nested sequence of prediction regions, identify the first region achieving the required object coverage, define its path score as the nonconformity score, and calibrate the resulting scores. The basic argument is sound if the prediction path is label-independent, the required coverage is eventually attainable, and the full path is available under a consistent construction. But I do not see that the theorem explicitly impose all these conditions. Specifically, in the oracle stopping index as defined in Eq. 3, the minimum exists only if at least one candidate set covers the required fraction of the ground-truth object. Consider an image with two disconnected lesions, where the initial predicted mask covers only the first lesion. Boundary expansion may eventually reach the second lesion if the process continues sufficiently long, but the authors do not establish that the method always does so. The problem becomes more serious if the initial mask is empty or the algorithm cannot select additional boundary voxels.

  1. I also see discrepancies between the theory and the implementation pseudo code. Theorem 1 assumes that the candidate expansion path is constructed without accessing the ground-truth mask. However, Algorithm 1 says that for each calibration image, the procedure should expand the mask until the desired coverage fraction is reached, and then stop. That stopping condition depends directly on the calibration ground truth. This is not necessarily a violation of conformal validity. Ground-truth labels are, of course, used to calculate calibration nonconformity scores. The issue is whether the algorithm constructs a common, label-independent path and merely evaluates its first successful index, or whether the path construction itself is modified by the label-dependent stopping rule.

  2. The manuscript does not well cover the edge cases, and I think there are undefined operations and discrete expansion of edge cases. Eq. 5 requires both |\Delta_t|<>0 and |C_0(I)|<>0, but neither condition is guaranteed. An empty initial mask is entirely plausible in lesion segmentation when the model fails to detect a small or low-contrast lesion. In that case, \ and both boundary expansion and the normalization are problematic. The authors need to provide explicit conventions for empty masks, empty boundary sets, selection rounding, and ties in cumulative scores, and explain how these preserve a well-defined nested path.

  3. In my opinion, the theorem is essentially a standard split-conformal argument, and the novelty should be positioned accordingly. the authors acknowledge that Theorem 1 does not introduce a new conformal proof technique. This is an appropriate concession. For any fixed input-dependent nested path, one can define an oracle stopping index and use its associated score for split conformal calibration. The finite-sample guarantee then follows from exchangeability and nesting. So, the main technical novelty is not the existence of conformal calibration for nested paths, but the particular method of constructing an adaptive path using confidence-guided and spatially guided expansion. This leads me to the final point, i.e. the paper's weakness in covering existing methods.

  4. The authors cite several recent conformal segmentation methods but only compare directly against CRC and CPS. Although these two baselines are relevant and important, they do not sufficiently establish superiority over the broader sota in spatially adaptive conformal segmentation. Two particularly recent relevant works are:

  • Anatomically-aware Conformal Prediction for Medical Image Segmentation with Random Walks (Gaillochet et al., 2026).
  • SACP: Spatially-Adaptive Conformal Prediction in Uncertainty Quantification of Medical Image Segmentation (Bereska et al., MIDL 2025).

There are other cited but missing comparisons. I do not buy the author's statement that these methods are not directly comparable because they use different objectives or additional model components. This does not fully justify excluding methods addressing the same broad goal of spatially coherent segmentation uncertainty quantification.

Please see my questions regaridng your experimental evaluations.

Questions for authors
  1. The ablation study does not adequately isolate the two components of the expansion policy The reported ablations mainly study parameter sensitivity and modifications of the cumulative path score. They do not cleanly distinguish gains due to the path ordering from gains due to the choice of nonconformity score.

  2. The scoring ablations do not consistently support all the conclusions. The manuscript claims that the complete uncertainty-weighted path score consistently produces more compact prediction regions. But the full scoring method does not outperform every ablation across all settings.

3.The chosen efficiency metric can hide clinically important errors. The primary efficiency metric is stretch. I think, for images with very small predicted masks, this ratio can be extremely large and for images with relatively large initial predictions, the same absolute expansion can appear modest. Therefore, stretch is useful but insufficient.

  1. The distribution-shift motivation (as claimed in intro) is not tested directly.
Reviewer_apriOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

The paper proposes CPAS (Conformal Prediction Adaptive Segmentation), a split-conformal method for binary and multi-class medical image segmentation. It targets a tolerance-style guarantee: Pr⁡(∣Y∩C(I)∣/∣Y∣≥ρ)≥1−α\Pr(|Y\cap C(I)|/|Y| \ge \rho) \ge 1-\alpha.

Starting from the thresholded prediction Y^\hat Y, CPAS builds a nested sequence of sets. At each step it adds a fraction kk of the outer boundary pixels. A fraction rr of those are chosen by model confidence f(x)f(x) ("exploitation"). The rest are chosen by an adjacency score that favors pixels next to regions added early ("exploration"). Each step increases a path score λt\lambda_t by the mean uncertainty 1−f(x)1-f(x) of the added pixels, normalized by ∣Y^∣|\hat Y|. The nonconformity score is λ\lambda at the first step where coverage ρ\rho is reached. At test time the path is grown until λt>q\lambda_t > q.

Theorem 1 states the general principle: any label-independent, input-dependent nested path with a nondecreasing score can be conformally calibrated. A joint multi-class extension works in pixel–class space and controls aggregate coverage.

Experiments cover four binary datasets (Polyps, WBC, OASIS, Kvasir) and the M&Ms cardiac dataset. CPAS matches the coverage of CRC and CPS (morphological dilation) with lower stretch: about 20% lower than CPS and 40% lower than CRC on average.

Critical strengths
  1. Clean, correct validity argument. Theorem 1 and its proof are correct. Separating "how the path is built" from "how far to go along it" is a useful design principle, and the paper is candid that Theorem 1 is not a new proof technique.
  2. Well-motivated idea. Combining confidence with spatial contiguity addresses known weaknesses of both baselines: CRC's fragmented, pixel-independent sets and CPS's direction-agnostic dilation. Figures 1 and 2 illustrate this well.
  3. Simple, model-agnostic, post-hoc. It needs only a soft probability map. There is no retraining, no ensembles, and no foundation-model features, and the runtime (~125 ms per image on CPU) is practical for 2D images.
  4. Multi-class extension. It is handled carefully. The authors correctly state that the guarantee is on aggregate coverage, not per class.
  5. Broad evaluation. Five datasets, several backbones (UniverSeg, U-Net, PraNet), two (ρ,1−α)(\rho, 1-\alpha) settings each, and 36 random splits. Hyperparameters are fixed across datasets.
Critical weaknesses

W1. Limited novelty in both theory and algorithm.

  • Theorem 1 is essentially nested conformal prediction (Gupta, Kuchibhotla & Ramdas, 2022) applied to the coverage functional GG. The (ρ,α)(\rho,\alpha) criterion is a standard tolerance-region / PAC-type guarantee (see also Learn-then-Test, Angelopoulos et al., 2021). Neither is cited.
  • The expansion procedure is a batched form of priority-based seeded region growing (e.g., Adams & Bischof, 1994), which is also not discussed.
  • The contribution therefore rests mainly on the specific heuristic path and score, and the evidence for these is mixed (see W3 and W4).

W2. The test-time rule is unnecessarily conservative.

  • If S(I,Y)=λTρ≤qS(I,Y)=\lambda_{T_\rho}\le q, then Tρ≤t∗:=max⁡{t:λt≤q}=Tq−1T_\rho \le t^* := \max\{t:\lambda_t\le q\} = T_q - 1. So returning Ct∗C_{t^*} already satisfies the guarantee.
  • The proposed rule returns CTqC_{T_q}, which adds one extra expansion step (about 15% of the boundary) to every test image for free.
  • This also suggests the conditions in Theorem 1 have not been examined closely.

W3. Fairness and adequacy of the baselines.

  • (a) CRC controls expected risk E[1−G]≤α\mathbb{E}[1-G]\le\alpha, not the tail probability Pr⁡(G≥ρ)≥1−α\Pr(G\ge\rho)\ge 1-\alpha. The paper never explains how CRC was adapted to the (ρ,α)(\rho,\alpha) target. If it is a split-conformal threshold on ff, it should not be called CRC.
  • (b) CRC and CPS often over-cover substantially, for example 1.00 (0.00) on OASIS and Kvasir at ρ=0.99\rho=0.99, and CPS at 0.96 for a 0.90 target. Comparing stretch at different realized coverage is not apples-to-apples. This also suggests ties or discretization in the baseline scores that should be explained.
  • (c) A simple baseline is missing: threshold a single combined score such as f(x)−β⋅dist(x,Y^)f(x) - \beta\cdot \mathrm{dist}(x,\hat Y), or a smoothed or geodesically restricted ff. This also yields a nested, contiguous, confidence-aware family with one parameter. Without it, the gain cannot be attributed to the iterative path.
  • (d) Davenport (ICLR 2025) and RW-CP (2026) are dismissed as "not directly comparable", but both produce outer confidence sets from the same kind of soft output. At least Davenport's outer set (which gives a stronger guarantee) could be evaluated.
  • (e) In the multi-class setting, CRC with a single global threshold across all channels (stretch up to 168) and CPS with an identical dilation count for every class look like strawmen. Natural alternatives are per-class thresholds or dilation counts combined through a max-type score.

W4. The empirical claims are stronger than the evidence.

  • The headline "20% / 40%" figures are an arithmetic mean of stretch across cells, dominated by a few high-stretch cells (CRC on Polyps at ρ=0.99\rho=0.99: 10.78 and 15.41).
  • Without Polyps, CPAS improves on CRC by about 15%. On OASIS the gain is about 2%.
  • In several cells CPAS is no better or worse than a baseline: WBC (0.9, 0.95) 1.13 vs 1.11; Kvasir (0.9, 0.95) 6.01 vs 5.29 (CRC). Many differences on WBC and OASIS are within one standard deviation.
  • The 36 splits come from the same pool, so their standard deviations understate uncertainty. A per-cell relative reduction or geometric mean, plus paired tests, would be more appropriate.

W5. The ablation undercuts the claimed role of the score.

  • In Table 3, CPAS_iter (the CPAS path with a plain iteration-count score) averages 5.40 vs 5.22 for full CPAS. Compared with CPS on Kvasir (average ≈ 6.71), almost all of the gain comes from the path, not from the uncertainty-weighted score.
  • In the (0.9, 0.95) setting, full CPAS (6.01) is worse than CPAS_iter (5.62) and CPAS_−C0 (5.56). This contradicts "the full score formulation consistently yielded more compact prediction sets."
  • Removing the ∣C0∣|C_0| normalization makes little difference, which is expected: it is a per-image constant rescaling of λ\lambda.
  • The claim that averaging over ∣Δt∣|\Delta_t| "removes dependence on the expansion rate" is not accurate. A smaller kk means more steps and hence a larger λ\lambda.

W6. Hyperparameters and protocol.

  • kk and rr were tuned on OASIS, which is also an evaluation dataset. It is unclear whether tuning used data overlapping the calibration and test pool. This does not invalidate coverage empirically, but it affects the efficiency claims on OASIS and formally requires the path to be independent of the calibration and test data.
  • The sensitivity study (Table 4) uses only OASIS, where all variants differ by less than 0.1. Kvasir or Polyps, where differences are larger, would be more informative.
  • The extreme settings r=0r=0 (pure spatial) and r=1r=1 (pure confidence) are missing. They would directly test the "exploration vs. exploitation" narrative.

W7. Edge cases and scope.

  • If Y^=∅\hat Y=\emptyset (e.g., a missed small lesion), the score in Eq. 5 divides by zero, the boundary is empty so the path cannot grow, and the stretch metric is undefined. Theorem 1 also implicitly requires G(Y,CT)≥ρG(Y, C_T)\ge\rho for every (I,Y)(I,Y), i.e., the path must eventually be able to reach Ω\Omega.
  • Because growth happens only along the boundary, objects disconnected from Y^\hat Y can be reached only through many low-confidence steps. The paper should state how these cases are handled and how often they occur.
  • "Exploration" is a misnomer. Since 1/(1+d(h))1/(1+d(h)) weighs pixels in C0C_0 most heavily, s(x)s(x) favors compact growth around the original mask. It acts as a smoothness prior, not exploration in any meaningful sense.

W8. Missing conditional and clinical analysis.

  • The method is pitched as "adaptive", but only marginal coverage is reported. Coverage and stretch stratified by object size, and per-domain results for M&Ms, are needed. The 1/∣C0∣1/|C_0| normalization may systematically affect small objects.
  • In multi-class, the aggregate guarantee may hide under-coverage of smaller structures such as RV. Per-class empirical coverage should be reported.
  • Distribution shift is motivated in the introduction, and M&Ms is a natural testbed for it (calibrate on one vendor, test on another), but it is not evaluated.

W9. Presentation issues.

  • Table 1 is captioned "Calibration results" but reports test-split results.
  • Footnote 3, meant for UniverSeg, links to an unrelated Springer AI-ethics article.
  • The Kvasir polyp segmentation set should be Kvasir-SEG (Jha et al., 2020), not the Kvasir classification dataset (Pogorelov et al., 2017). Also, Polyps contains Kvasir, so the two benchmarks overlap.
  • The M&Ms sample unit is unclear. With 100–252 volumes per domain and even splits, calibration sizes of 65–190 are impossible at the volume level, so slices were presumably used. In that case slices from the same patient may appear in both calibration and test, and the reported coverage is per slice, not per patient.
  • How ∣Δt∣=k∣Bt∣|\Delta_t| = k|B_t| is rounded, and how ties are broken, are not specified.
  • Runtime is reported only on small OASIS 2D images. There is no discussion of 3D volumes, where the iterative process may be much slower.
Questions for authors
  1. How exactly is CRC adapted to the (ρ,α)(\rho,\alpha) tail-probability guarantee? Please give the calibration score used for CRC and CPS, and explain why they reach 1.00 coverage on OASIS and Kvasir at ρ=0.99\rho=0.99.
  2. Can you return CTq−1C_{T_q-1} instead of CTqC_{T_q} (see W2)? How much does stretch decrease?
  3. How does CPAS compare with a single-threshold baseline on a combined confidence–distance score (W3c), and with Davenport's outer confidence sets?
  4. What happens when Y^=∅\hat Y=\emptyset, or when ⌊k∣Bt∣⌋=0\lfloor k|B_t|\rfloor = 0? How many images in each dataset hit these cases?
  5. Please report r∈{0,1}r\in\{0,1\} and the ablations on Polyps and Kvasir, ideally with paired significance tests.
  6. Was hyperparameter tuning on OASIS done on data disjoint from the calibration and test pool?
  7. For M&Ms, is the unit a 2D slice or a 3D volume? Are calibration and test split by patient? Please also report per-class (LV, RV, MYO) empirical coverage and per-domain results.
  8. Can you provide size-stratified coverage and stretch to support the "adaptive" claim?
  9. How does runtime scale with image size and in 3D?
3 comments

We thank the reviewer for their feedback.

W1: Core Contribution Our primary contribution bridges conformal risk control with spatial boundary geometry, providing a principled mechanism to systematically control stretch and eliminate baseline over-coverage in multi-class segmentation.

W2 & Q2: Test-Time Rule You are entirely correct. The stopping rule (min⁡{t:λt>q}\min\{t: \lambda_t > q\}) mathematically added a redundant step. We updated Theorem 1, its proof, and Algorithm 1 to use your exact optimal rule: Tq=max⁡{t:λt≤q}T_q = \max\{t: \lambda_t \le q\} (setting Tq=0T_q=0 if λ0>q\lambda_0 > q). Crucially, our Python code and all reported empirical results already utilized this optimal rule; the discrepancy was solely a notational error in the manuscript, now corrected. W3 & Q1, Q3: Baselines: (a) CRC Adaptation: We apply CRC using an indicator loss L=1{G(Y,C)<ρ}L = \mathbf{1}\{G(Y, C) < \rho\}, where G(Y,C)=∣Y∩C∣/∣Y∣G(Y,C) = \vert{}Y \cap C\vert{} / \vert{}Y\vert{} represents the object coverage fraction. This indicator checks whether the coverage falls below the target ρ\rho, and its expected value corresponds to the tail probability, aligning the risk bound directly with our target.
(b) Over-Coverage: The meaningful over-coverage observed in our experiments stems from its discretization. CPS relies on integer morphological dilations that add large, indivisible blocks of pixels at each step. In contrast, CPAS uses a highly granular path, halting much closer to the target. (c) Static Baseline: We implemented your suggested baseline f(x)−β⋅dist(x,Y^)f(x) - \beta \cdot \mathrm{dist}(x, \hat{Y}) and evaluated it on WBC and OASIS (β∈{0.01,0.05,0.1}\beta \in \{0.01, 0.05, 0.1\}). CPAS outperformed this static baseline, achieving strictly smaller mean stretch for the same coverages. (d) RW-CP/Davenport: RW-CP requires foundation models not assumed here. Davenport's outer prediction sets reduce to CRC (identity transformation) and CPS (distance transformation). (e) Multi-Class: Assigning a per-class threshold reduces the problem to KK independent binary tasks, destroying the joint multi-class framework we aimed to achieve with a single global threshold. The catastrophic stretch (up to 168) of global CRC highlights why CPAS is effective: it manages varying class difficulties globally without splitting into binary problems. W4: Empirical Claims While averages can be influenced by outlier cells, CPAS's primary strength is consistency: across virtually all datasets and coverages, it matches or outperforms baselines without catastrophic failures. Significant improvements on complex structures (Polyps, Kvasir) highlight its effectiveness in high spatial ambiguity. We also included geometric mean of median Dice, Stretch and IoU scores.

W5: Ablation and Score Role

We agree that the structural path provides the performance gain; however, our ablation studies (Table 3) confirm that incorporating the full uncertainty-weighted score provides the optimal overall results. ∣C0∣\vert{}C_0\vert{}: While constant per image, CP computes a single global threshold qq. Normalizing aligns images with vastly different initial object sizes on a comparable scale before computing this quantile. ∣Δt∣\vert{}\Delta_t\vert{}: we did not mean the step-size hyperparameter kk. Dividing by ∣Δt∣\vert{}\Delta_t\vert{} computes average per-pixel uncertainty, normalizing scores between images with large vs. small boundaries. We clarified this in the text.

W6 & Q5, Q6: Protocol Tuning used a data partition strictly disjoint from the final evaluation/calibration splits. We evaluated on extreme settings (manuscript updated): setting r=0r=0 turns off confidence exploitation entirely, relying purely on spatial adjacency. Conversely, pure confidence (r=1r=1) results in noisy, fragmented growth and significantly higher stretch.

W7 & Q4: Edge Cases Empty Masks:

We can ensure the initial set is never empty. If a mask is empty, we initialize C0C_0 using the single highest-confidence pixel. The ceiling function ensures at least one boundary pixel is added per iteration (∣Δt∣≥1\vert{}\Delta_t\vert{} \ge 1), strictly preventing division by zero. Zero images hit these edge cases in our experiments. Reachability: Because CPAS uses morphological dilation, a single starting pixel guarantees eventual coverage of the entire image. Exploration: Refers to probability space: the score allows the path to step into low-probability regions to cross uncertain gaps.

W8 & Q7, Q8: Analysis & Scope "Adaptive" meant selecting a targeted subset of boundary pixels. To avoid confusion with conditional coverage, we removed it from the headings.M&Ms sample unit is 2D slices, split by patient (manuscript updated).Our guarantee is marginal and does not imply equal coverage per size subgroup.Distribution shifts are outside this foundational paper's scope.

W9: Presentation All presentation issues will be fixed.

Q9: 3D Volumes We did not evaluate 3D volumes (our focus is 2D slices). Extending to 3D is an exciting future direction.

Thank you for the detailed rebuttal and additional experiments. I appreciate the clarification of the stopping rule, the handling of edge cases, and the new ablations with extreme values of (r), which address several of my technical concerns.

However, my main concerns regarding novelty and empirical validation remain.

  1. the proposed confidence–distance baseline was only evaluated on WBC and OASIS, whereas Polyps and Kvasir are where CPAS demonstrates its most substantial gains. Evaluating this simpler alternative on these datasets would better establish the necessity of the proposed iterative expansion.
  2. I am not fully convinced by the argument that class-dependent thresholds necessarily destroy joint multi-class guarantees, since a shared calibration score (e.g., a max-type score) could preserve joint validity.
  3. While I understand that the theoretical guarantee is marginal rather than conditional, empirical per-class and object-size-stratified coverage analysis remains important, particularly in medical segmentation.

Overall, the rebuttal improves the paper's technical clarity, but I believe the evidence is still insufficient to fully establish the novelty and empirical advantages of CPAS over simpler, carefully calibrated alternatives. I therefore maintain my current assessment.

Thank you for your follow-up feedback.

  1. We evaluated the suggested baseline f(x)−β⋅dist(x,Y^)f(x) - \beta \cdot \text{dist}(x, \hat{Y}) baseline using the β∈{0.01,0.05,0.1}\beta \in \{0.01, 0.05, 0.1\} across all four binary datasets over all 36 splits. Even when selecting the best β\beta independently for each dataset (while keeping CPAS parameters fixed), CPAS achieves lower geometric-mean stretch across all benchmarks at the target coverage: Kvasir: 5.04 vs. 6.49 (−22.3%) Polyps: 1.81 vs. 1.92 (−5.6%) WBC: 1.50 vs. 1.62 (−7.5%) OASIS: 1.76 vs. 1.84 (−4.4%)

  2. We agree that a shared max-type score (S=max⁡cScS = \max_c S_c) preserves joint validity by enforcing simultaneous per-class coverage (∀c,G(Yc,Cc)≥ρ\forall c, G(Y_c, C_c) \ge \rho). However,it still applies the single-class CRC/CPS operator to each class (where CPAS already outperforms both across four binary datasets) and forces all classes to expand to the worst-case class quantile, inflating total stretch. Our goal on M&Ms was specifically to test unified global calibration across coupled classes, where CPAS avoids worst-case class spillover.

  3. We agree that conditional guarantees across object sizes and individual classes are valuable in clinical settings. However, enforcing coverage per subgroup requires Mondrian or class-wise calibration, which is an orthogonal step outside our global split-conformal scope. Within our global framework, CPAS accounts for scale and structural imbalance by normalizing path increments by initial mask volume (∣C0(I)∣\vert{}C_0(I)\vert{} in Eq. 5; ∑c∣C0,c(I)∣\sum_c \vert{}C_{0,c}(I)\vert{} in Eq. 6) and ranking boundary pixels jointly across classes by confidence and adjacency, prioritizing expansion into plausible, high-confidence regions.

Reviewer_8AKNOpenReview ↗
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3
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

The paper proposes CPAS, a conformal prediction method for medical image segmentation. Starting from the predicted mask, it grows the set step by step. At each step it adds a fraction of boundary pixels, chosen partly by model confidence and partly by adjacency to regions added early. A nonconformity score accumulates the average uncertainty of the added pixels, normalized by initial mask size. The authors provide a theorem that any input-dependent nested path with a nondecreasing score can be calibrated this way, which gives finite-sample coverage. On several datasets, CPAS meets the coverage targets and reduces “stretch” with respect to baselines.

Critical strengths
  1. The study provides a a theorem (Theorem 1) with a clean framing, stating the sufficient conditions (nested, label-independent path plus monotone score) explicitly. Conformal prediction for segmentation (CPS) is shown to be a special case, and the multi-class extension is derived as an instance via the augmented pixel-class space.

  2. Results show this theory holds in practice, with consistent efficiency gains with valid coverage. Coverage lands near target across settings, with their stretch lowest in most rows. The gains are large in the harder regimes.

  3. The method extends beyond the binary setting to multi-class targets. The method beats baselines (CRC, CPS) on multi-class domains in terms of stretch.

  4. The results includes an ablation of the score components and a hyperparameter sensitivity study.

Critical weaknesses
  1. The paper only compares against CRC and CPS. It dismisses recent methods as "not directly comparable," but I'm not sure that holds for Kandinsky CP or SACP, which also give pixel-level conformal sets from a standard model.

  2. Stretch is the only efficiency metric in the main text, and it's a mean of ratios, so a few images with small predicted masks can dominate it. I'd like to see medians or distributions, plus something like Dice or precision of the set against the ground truth. Also, the Hausdorff results in the appendix are mixed.

  3. The method relies on hand-picked pieces (expansion rate k, exploitation/exploration split r, the geometric exploration score), tuned and analyzed on OASIS only. The r sweep never tests no exploration or pure exploration, so it's unclear how much the exploration term matters.

Questions for authors
  1. Why were Kandinsky CP and SACP left out of the comparison? They both produce pixel-level conformal sets from a standard model, so it's not clear to me why they count as "not directly comparable." Could you add at least one of them?

  2. Could you report median stretch (or the full distribution) along with Dice or precision of the prediction set against the ground truth? Mean stretch seems easy to skew with small masks, and it doesn't show whether the added pixels are the right ones.

  3. What does the exploration part of the expansion actually contribute? Could you add a run with no exploration (r = 1), ideally on more than just OASIS, to show the gain isn't coming from confidence-based selection alone?

Comments on the paper

1 comment

Thank you for your thoughtful follow-up and positive feedback on our revisions. Below, we address your three remaining points:

  1. Conformal Quantile Edge Case (⌈(n+1)(1−α)⌉>n\lceil (n+1)(1-\alpha) \rceil > n)

You are right to point out the finite-sample edge case when α\alpha is small relative to the calibration set size nn. We have updated Theorem 1 and Algorithm 1 to explicitly adopt the standard split-conformal convention: when ⌈(n+1)(1−α)⌉>n\lceil (n+1)(1-\alpha) \rceil > n, we define S(n+1)=+∞S_{(n+1)} = +\infty (so q=+∞q = +\infty), which returns the full image domain Cq(I)=ΩC^q(I) = \Omega and trivially satisfies G(Y,Cq(I))≥ρG(Y, C^q(I)) \ge \rho with probability 11.

  1. Stronger Baselines Combining Probabilities and Geometry

To evaluate CPAS against stronger baselines using the exact same base-model probabilities f(x)f(x) and spatial geometry without external dependencies, we conducted additional experiments and report two direct comparisons:

  • Static Confidence–Distance Baseline: We evaluated f(x)−β⋅dist(x,Y^)f(x) - \beta \cdot \text{dist}(x, \hat{Y}) for β∈{0.01,0.05,0.1}\beta \in \{0.01, 0.05, 0.1\} across all four binary datasets and 36 splits. Even against the best-performing β\beta chosen independently per dataset (while keeping CPAS hyperparameters fixed), CPAS consistently achieves lower geometric-mean stretch at the target coverage: Kvasir: 5.04 vs. 6.49 (−22.3%), Polyps: 1.81 vs. 1.92 (−5.6%), WBC: 1.50 vs. 1.62 (−7.5%), and OASIS: 1.76 vs. 1.84 (−4.4%).

  • Iterative Single-Mechanism Baselines (r=0r=0 and r=1r=1): Our extreme ablations also serve as direct single-source path baselines under the exact same calibration rule: r=0r = 0 is pure spatial boundary growth and r=1r = 1 is pure probability-ordered boundary growth. Combining both (r=0.6r = 0.6) outperforms either extreme.

  1. Stretch Metric Limitations and Multi-Class Scope
  • Stretch Limitations: Because stretch (∣C(I)∣/∣Y^∣\vert{}\mathcal{C}(I)\vert{} / \vert{}\hat{Y}\vert{}) is a ratio, it can appear inflated when initial masks ∣Y^∣\vert{}\hat{Y}\vert{} are very small. To ensure transparent evaluation across object scales, we complement stretch with scale-bounded overlap metrics (Dice and IoU in Appendix A.4, Table 7) and boundary distance (Hausdorff distance dHd_H in Appendix A.2, Table 6), where CPAS also achieves the best overall performance.

  • Multi-Class Scope: We agree that per-class guarantees are valuable for clinical reliability. However, enforcing coverage per individual class requires Mondrian or class-wise calibration, which is an orthogonal step outside our global split-conformal scope (Eq. 6). Furthermore, calibrating each class independently effectively reduces the problem to separate single-target binary tasks—a regime where we have already demonstrated across four diverse benchmarks that CPAS consistently outperforms baselines. Within our joint multi-class framework, CPAS accounts for scale and structural imbalance by normalizing path increments by initial mask volume (∣C0(I)∣\vert{}C_0(I)\vert{} in Eq. 5; ∑c∣C0,c(I)∣\sum_c \vert{}C_{0,c}(I)\vert{} in Eq. 6) and ranking boundary pixels jointly across classes by confidence and adjacency, prioritizing expansion into plausible, high-confidence regions.

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