acceptodds
Withdrawn from ICLR 2027

SymBreak: Breaking the Implanted False Belief to Identify Subvisual Ischemic Changes

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

Stroke is a leading cause of death and disability, and rapid diagnosis is critical to improving patient outcomes. Although non-contrast CT (NCCT) is the first-line imaging modality for suspected stroke, hyperacute ischemic changes, particularly within 4.5 hours, remain difficult to detect because of their subtle imaging manifestations. When pathological signals are extremely weak, lesion-related responses can be difficult to distinguish from the model's own background hallucinations—weak, spatially irregular lesion-like responses elicited even by negative scans. Here, we propose SymBreak, a new training and inference paradigm based on false-belief implantation that organizes these otherwise unstructured background responses into a predictable pattern, thereby improving the detectability of subtle ischemic changes. During training, generative models transform unilateral ischemic samples into bilaterally symmetric counterfactual cases, implanting the false belief that ischemic changes MUST BE symmetric between hemispheres. During inference, background responses in non-stroke cases tend to follow this implanted symmetry, whereas genuine unilateral ischemic changes break it. We quantify this violation using the Symmetry-Breaking Index (SBI), which converts hemispheric imbalance in predicted lesion evidence into a patient-level diagnostic signal. Across five public NCCT datasets, SymBreak consistently improves patient-level discrimination over existing intensity- and lesion-size-based methods across four held-out AIS cohorts and multiple segmentation architectures. Response analyses further show that false-belief implantation substantially reduces hemispheric imbalance in non-stroke cases while preserving pronounced symmetry breaking in unilateral AIS. Together, these findings establish SymBreak as an accurate and robust approach for detecting hyperacute ischemic changes and suggest a broader weak-signal learning paradigm: deliberately structuring model background responses enables pathology to be detected through violations of the resulting structure.

Primary area:
applications to computer vision, audio, language, and other modalities
Keywords:
Model Priors, Imaging Biomarkers, Weak Signal Detection, Medical Image Analysis, Non-Contrast CT, Ischemic Stroke

Reviews

Among:
Shape:
1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_qf1EOpenReview ↗
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2
Confidence
2
Informativeness
1
Presentation
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Soundness
1
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Paper summary

The paper proposes SymBreak, a framework for detection of acute ischemic stroke (AIS) on non-contrast CT (NCCT). The motivation of the paper is to address Background Hallucination they define as "responses to imaging noise or normal anatomy whose magnitudes can resemble subtle lesion signals, making them difficult to distinguish." The paper hypothesize that we can detect genuine pathology through symmetry breaking with an implanted symmetry generative model. Their framework relies on 3 mechanisms: First, they generate new symmetric synthetic data using a a 2D DDPM inpainter then a LesionGen diffusion model. These new data are used to train a 3D segmentation network and its inference is analyez following a new metric Symmetry-Breaking Index (SBI) that the paper claims can be used as a patient-level AIS score.

The framework is evaluated with 4 datasets (with leave-one strategy): SinoCT (non-stroke controls and NormalGen training) and AISD, APIS, ISLES’24 and CPAISD.

Critical strengths

The paper covers an important problem.

The paper proposes an original idea: training on symmetric positives so that unilateral evidence becomes an out-of-distribution deviation, which is a creative form of anomaly detection built from a supervised segmentation model.

The paper provides sufficient details for reproducibility.

Critical weaknesses
  • The evaluation is completely confounded! AIS versus controls (all from SinoCT) come from different sources, so actually the approach may not be really learning anything mleaningful and only learning to distinguish SinoCT samples from any other AIS dataset.

  • I still cannot understand the “false-belief” mechanism. There is no demonstration that we are actually facing hallucinations or beliefs as popularied by LLM litterature. These concepts are not supported by any evidence. At best we have "correlations" that far from perfect: the paper claims soundness because the SBI metric they propose goes to 0 on control, but we can also get lower SBI if we have a lower total evidence (R_L, R_R => small). With ϵ\epsilon in the log, low total evidence gives SBI ≈≈ 0 regardless of symmetry.

  • The claims in abstract and intro emphasise hyperacute (<4.5 h) and subvisual changes, but no result is stratified by time from onset. The datasets used can contain up to 24h scans!

  • Some results opposing the main claims are hidden! Table 1 shows SBI without false belief at 0.93 on CPAISD versus 0.92 with it, so false belief does not help on one of four held-out sets. With only four datasets, one of which has 54 or 96 studies, the macro average is not strong evidence. No confidence intervals, no seeds, and no significance tests are given for Table 1 or Table 2.

  • Missing critical ablations: (i) flip-equivariance and pair-consistency losses alone on real data; (ii) symmetrized data without the extra losses; (iii) training on real + symmetrized data; (iv) the generative pipeline versus simple mirror-and-paste of the real lesion; (v) severity-matched versus random-severity contralateral lesions. Each tests a different component.

  • Unfair baselines: The 2 baselines (NWU and predicted volume) are weak. They are not the state of the art for AIS detection

Questions for authors

1- Discuss and fix the cofounding effects with appropriate studies: Can you report results with same-site negatives (e.g., DWI-negative suspected stroke patients in AISD, APIS or ISLES’24), and with a dataset-source classifier as a control?

2- Add missing ablations

3- Significance of results: Give 95% CIs (DeLong/bootstrap) for every AUROC in Tables 1–3, paired tests of SBI versus Volume/NWU, and variance across training seeds (including the generators). Why is CPAISD the only dataset used for Tables 2–3 and the analysis, and does the pattern hold on the other three?

4- Compare with actual SoTA, like some work you actually cited: Sahoo et al., 2022; Lu et al., 2022

Reviewer_5q8AOpenReview ↗
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2
Confidence
3
Informativeness
2
Presentation
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Paper summary

This is a well-scoped and thoughtfully motivated paper: the authors correctly identify the spatial unpredictability of background hallucinations as the core obstacle, and their decision to structure false beliefs into a known symmetric pattern rather than merely suppressing them is a genuinely interesting idea, supported by a carefully specified generator pipeline and an evaluation design that matches the diagnostic claims. The reference handling is clean, the arithmetic in the reported metrics checks out, and the limitations section is admirably honest about the method’s vulnerability to bilateral, multifocal, or symmetric infarctions. However, the main themes needing work are mathematical rigor and reproducibility: several derivations and definitions should be tightened so that the symmetry-breaking signal is unambiguously defined and its behavior under registration error and asymmetric artifacts is formally characterized, and the experimental setup needs more complete implementation details, hyperparameter disclosure, and code/data availability to allow independent verification. The writing itself is largely clear, but a few acronyms and transitions could be smoothed. Overall, the core idea is promising and the empirical evidence is directionally convincing, but the current presentation would benefit from a more rigorous formal foundation and a more complete reproducibility package before it is ready for review.

Critical strengths
  • Structurally sound reference list. All 29 bibliography entries are cited in the text, with no broken [?] markers, no orphan references, and no detectable self-citation cluster (References, pp. 10–12). This is a careful, professional level of bibliographic hygiene that reviewers and readers appreciate.

  • Clear problem framing. The paper identifies the spatial unpredictability of background hallucinations as the core bottleneck and motivates a constructive alternative: “rather than attempting to eliminate background hallucinations, can we deliberately constrain them into a known pattern” (p. 2). This framing is both honest and actionable, and it sets up the proposed method as a principled design choice rather than a heuristic patch.

  • Well-specified generator pipeline. NormalGen and LesionGen are described in detail (Table 5, App. B.1, pp. 13–15), with strong internal consistency: Eq. (14) matches Table 5’s weights 4/1, and Eq. (13) matches the Normal-anchor probability 0.5. This level of specification makes the method reproducible and the design rationale transparent.

  • Evaluation structure well matched to the diagnostic claims. The leave-one-dataset-out external evaluation (Table 1), backbone transfer (Table 2), and lesion-size stratification (Table 3) directly probe the paper’s central claims. The NWU and SBI macro-averages verify arithmetically, which strengthens confidence in the reported results (Tables 1–3, pp. 6–8).

  • Honest limitations section. The paper explicitly acknowledges that bilateral, multifocal, or approximately symmetric infarctions may produce weak symmetry-breaking signals, and that asymmetric abnormalities, registration errors, or artifacts may produce false positives (§5, p. 9). This candor is a genuine strength and gives future work a clear roadmap.

  • Response analyses support the mechanism. Non-stroke mean SBI decreases from 0.5090.509 to 0.06280.0628 (a factor of 8.18.1, arithmetically correct), and SBI has the highest point estimate in every lesion-size stratum of Table 3 (§4.3, p. 7; Table 3, p. 8). These quantitative checks substantiate the proposed mechanism rather than relying on qualitative impressions.

  • References largely verified. The Von Kummer 2001 “sensitivity of only 64%” figure, the dataset descriptions (SinoCT, CPAISD, ISLES’24), and the future-dated references (Prabhakaran 2026, Chu 2026, Shah & Sundaresan 2026) were all externally verified as accurate (References, pp. 10–12; external verification, Rounds 3 and 5). This is a strong indicator of scholarly rigor and reliability.

Critical weaknesses

We appreciate the ambition of the paper and the careful experimental design. The following suggestions are intended to strengthen the claims and make the contributions even more reproducible and generalizable.

  • Qualify the “consistently improves” claim. The statement that “SymBreak consistently improves patient-level discrimination over existing intensity- and lesion-size-based methods” (Abstract, p.1; Intro, p.3) is stronger than what Table 1 (p.6) supports. In particular, on ISLES’24 the Volume baseline achieves 0.90870.9087 AUROC versus 0.87830.8783 for SBI, and on CPAISD the SBI variant without false-belief implantation reaches 0.93570.9357 versus 0.92260.9226 with false belief. The macro-average improvement is real, but it is driven by APIS and AISD. We suggest rephrasing to something like “improves the macro-average AUROC” or “improves patient-level discrimination on APIS and AISD,” and adding a brief discussion of why the method does not help on ISLES’24 and CPAISD with false belief.

  • Isolate the effect of the implanted prior. The ablation “SBI without false belief” removes the counterfactual data DsymD_{\mathrm{sym}} and the explicit regularizers Lflip/LpairL_{\mathrm{flip}}/L_{\mathrm{pair}} simultaneously. As a result, the “central role of the implanted symmetry prior” (p.3; Table 1, p.6; §4.3, p.7) is confounded with the flip-equivariance loss. We recommend adding two additional ablations: one with DsymD_{\mathrm{sym}} but without Lflip/LpairL_{\mathrm{flip}}/L_{\mathrm{pair}}, and one without DsymD_{\mathrm{sym}} but with the regularizers. This would cleanly attribute the observed gains to the data augmentation versus the explicit regularization, and would make the mechanistic claim much more convincing.

  • Add a generator fidelity evaluation. The entire method depends on NormalGen/LesionGen producing plausible bilateral counterfactuals, yet no fidelity metric is reported in App. B.1 (pp.13–15). We suggest including a quantitative measure such as FID or a human evaluation of the synthetic images, or at least showing a few representative examples of generated counterfactuals alongside the real inputs. Without this, it is difficult to assess whether the benefit comes from realistic counterfactuals or from some other property of the generated data.

  • Operationalize or reframe “false belief.” The term “belief” is never formally defined for the segmentation model SθS_\theta, and no technique from the cited LLM papers is actually used. The mechanism is inferred only from the SBI distribution shift described in §4.3 (p.7). As implemented, the method is data augmentation plus explicit regularization. We suggest either (a) providing a precise operational definition of “belief” in the context of SθS_\theta and showing how the false-belief implantation changes it, or (b) reframing the contribution as “counterfactual data augmentation with symmetry priors,” which would avoid overloading the term and make the connection to the LLM literature more explicit.

  • Scope the “broader weak-signal learning paradigm” claim. The Abstract (p.1) and Conclusion (p.9) frame the method as a general paradigm, but the Discussion explicitly states that “An important next step is to extend the idea beyond left-right brain symmetry” (§5, p.9). To avoid overclaiming, we suggest either scoping the claim to the single application domain (e.g., “in left-right symmetric medical imaging”) or adding a small cross-domain experiment (e.g., on a non-brain dataset with known symmetry) to demonstrate the generality. If the latter is not feasible, a more cautious phrasing would be more appropriate.

We believe these changes will make the paper’s contributions clearer and its claims more defensible, and we look forward to seeing the revised version.

  1. Literature & Related Work

We thank the authors for a thoughtful and well-written manuscript. The central idea of SymBreak — implanting a counterfactual bilateral symmetry prior and then detecting violations of that prior — is clinically motivated and clearly presented. The related-work section correctly identifies the gap between conventional asymmetry-based features and modern generative models, and the authors’ decision to frame the problem as one of belief violation rather than simple feature comparison is conceptually appealing. The following suggestions are intended to strengthen the framing, situate the work more precisely within the existing literature, and ensure that all claims are supported by appropriate citations and baselines.

  • Title and framing. The title “Breaking the Implanted False Belief” may be misread as implying that the method removes or erases a prior belief, whereas the method actually detects violations of an implanted prior. Consider a title that more explicitly conveys detection, e.g., “Detecting Violations of an Implanted Symmetry Prior for Subvisual Ischemic Changes,” or add a clarifying subtitle. This would prevent potential misinterpretation by readers who expect a belief-editing or unlearning method.

  • Dataset scope. The abstract states “Across five public NCCT datasets,” but the diagnostic evaluation rests on four held-out AIS cohorts plus SinoCT controls. SinoCT is used only for controls and generator training, not for diagnostic evaluation. Please clarify in the abstract and §4.1 that the diagnostic claim covers four AIS cohorts, with SinoCT serving as a control/generator-training resource. This will make the scope precise and avoid overstating the evaluation.

  • Missing diagnostic baselines. Tables 1–3 currently compare only NWU, Volume, and SBI readouts derived from SymBreak’s own segmentation predictions. To establish the clinical value of the approach, we strongly recommend adding at least one prior deep-learning AIS detector as a diagnostic baseline. Two particularly relevant works are:

  • Lu et al., “Identification of early invisible acute ischemic stroke in non-contrast computed tomography using two-stage deep-learning model,” Theranostics, 2022, doi:10.7150/thno.74125 — the closest prior work to the stated clinical problem of early invisible AIS.

  • PAPL (2024), a same-task, same-modality symmetry-based method that is directly comparable to SymBreak.

Reporting AUROC for these baselines on the same held-out cohorts would substantially strengthen the claim that SymBreak improves upon the state of the art.

  • ISLES’24 challenge evaluation. The paper uses only the ISLES’24 training split (149 suspected patients) and reports no leaderboard-comparable numbers. We suggest reporting performance on the ISLES’24 challenge test set (100 cases, public leaderboard, arXiv:2408.10966) and comparing against the CPAISD dataset’s own baseline model. This would provide an external, standardized benchmark and allow readers to situate SymBreak relative to the challenge’s official results.

  • Systematic review context. To contextualize the AUROC claims, please cite and discuss the recent systematic review and meta-analysis by Gete & Ayele, “Deep-learning-based non-contrast CT for detecting acute ischemic stroke: a systematic review and HSROC meta-analysis of patient-level diagnostic accuracy,” BMC Neurology, 2025, doi:10.1186/s12883-025-04528-3. Their summary sensitivity of 0.91 and specificity of 0.90 across patient-level AIS detection studies provides a useful reference point for the reported AUROC values.

  • Diffusion-based anomaly detection. The motivation of “background hallucination” is directly relevant to a large body of work on diffusion-based anomaly detection, where a central problem is distinguishing genuine anomalies from model hallucinations. We recommend adding a brief subsection or paragraph in §2 covering this literature (e.g., anomaly detection with diffusion models, reconstruction-based and score-based approaches). This will help readers understand how SymBreak’s counterfactual generation relates to — and differs from — existing generative anomaly-detection frameworks.

  • Hallucination-belief citations. The claim that “a model’s hallucinations are closely related to its internal beliefs” (p.2) is currently supported by Li et al. 2023 (Inference-Time Intervention) and Marks & Tegmark 2023 (Geometry of Truth). Both are LLM-truthfulness papers that study activation steering and linear structure of true/false representations; neither addresses perceptual hallucinations in vision segmentation models. We suggest either replacing these citations with work on visual hallucinations in generative or segmentation models, or softening the claim to indicate that the analogy is drawn from the LLM literature and remains to be validated for vision models.

  • Standard technique citations. Several standard techniques are used without citation. We recommend adding references for:

  • Cosine noise schedule (Nichol & Dhariwal, 2021),

  • Classifier-free guidance (Ho & Salimans, 2022),

  • Soft Dice loss (Milletari et al., 2016).

These are widely used and should be cited in App. B.1 and the methods section for reproducibility and scholarly completeness.

  • NWU baseline provenance. The NWU comparator is attributed to Minnerup et al. 2016, but that paper is an onset-time classifier (within vs. beyond 4.5 h), not an AIS-vs-control diagnostic. The Table 1 NWU macro-average of 0.7056 appears to be a new evaluation of an adapted readout whose formula is unspecified. Please clarify that this is an adapted NWU-based readout, provide the exact formula used (e.g., the intensity reduction relative to a contralateral reference), and state that it is not directly comparable to the original paper’s numbers.

  • Synthetic-anomaly mechanism. The implant-a-prior-then-detect-violation mechanism is essentially the same mechanism used in synthetic-anomaly learning (CutPaste, DRAEM — both cited by the paper), re-targeted to bilateral symmetry. We recommend acknowledging this explicitly in §2 and framing the novelty as the application of this mechanism to symmetry-based AIS detection, rather than the mechanism itself. This will position the contribution more accurately and help readers appreciate the engineering and clinical value.

  • Symmetry-based AIS prior work. Symmetry-based AIS detection is not new: EIS-Net (2021), SEAN (2021), ADN (2022), PAPL (2024), and Cl-SegNet (2024) all exploit inter-hemispheric asymmetry. The claimed novelty is implanting symmetry as a training prior rather than using asymmetry as a feature. We suggest adding a sentence in §2 that explicitly contrasts SymBreak with these methods, emphasizing the distinction between learning from asymmetry features and learning to detect violations of an implanted symmetry prior. This is an incremental but meaningful distinction that should be stated clearly.

  • SBI context. The Symmetry-Based Index (SBI) defined in Eq. (7) is a standard hemispheric log-ratio asymmetry index, and contralateral-ratio statistics are standard in stroke imaging (NWU itself is one). No citation is strictly needed, but we recommend adding a brief note in §3.2 acknowledging that SBI belongs to this well-established family of asymmetry measures. This will help readers who are not familiar with the stroke-imaging literature understand the index’s provenance and rationale.

We believe these revisions will significantly improve the clarity, completeness, and impact of the related-work section and the overall paper. The core idea is strong, and with these additions the manuscript will be even more compelling to both the AIS-imaging and generative-modeling communities.

  1. Mathematical Correctness

The mathematical core of the paper is sound: the invariance claims are correct, and the dimension checks are consistent. The following suggestions will improve reproducibility and precision.

Parameter values and reproducibility

  • Please state the value of ϵ\epsilon in Eq. (7) and report the sensitivity of SBI values to it; every reported SBI number (0.509, 0.0628, 4.27, 7.896) and the 'factor of approximately 8.1' claim are ϵ\epsilon-dependent and currently unreproducible.
  • Please assign a value to λdice\lambda_{\mathrm{dice}} in Eqs. (2) and (16); λflip=0.1\lambda_{\mathrm{flip}} = 0.1 and λpair=0.05\lambda_{\mathrm{pair}} = 0.05 are given but λdice\lambda_{\mathrm{dice}} never is.
  • Please give the values of λflip\lambda_{\mathrm{flip}} and λpair\lambda_{\mathrm{pair}} at their first use in Eq. (4); they appear only in App. B.2 (p16).

Notation and symbol disambiguation

  • Please disambiguate ϵ\epsilon: it denotes Gaussian noise ϵ∼N(0,I)\epsilon \sim \mathcal{N}(0, I) in Eq. (9) (and Eqs. 11, 14) but a stability constant ϵ>0\epsilon > 0 in Eq. (7); use a different symbol for one of them.
  • Please disambiguate Ω\Omega: it denotes the full slice domain (Eq. 11), the voxel domain of the current training volume (App. B.2), and hemispheric regions ΩL/ΩR\Omega_L/\Omega_R (Eq. 6); use distinct symbols.
  • Please fix the silent notation change: xx and mm denote slices in §3.1/App. B.1 but volumes in App. B.2; state the convention once and keep it consistent.
  • Please state that F−1=FF^{-1} = F for a left-right reflection in Eqs. (3) and (17), or avoid F−1F^{-1} entirely.
  • Please declare the implied symbols in the generator equations: εϕN\varepsilon_\phi^N (Eq. 11), εφL\varepsilon_\varphi^L (Eq. 14), and x~(d)\tilde{x}^{(d)} (Eq. 15) are used but never defined, and the expectation EE in Eq. (14) lacks a subscript over its random variables.

Definitions and forward references

  • Please define dd before its first use: Eq. (1) uses severity dd, but d∈[0,1]d \in [0,1] is first defined only in App. B.1 (p14).
  • Please define LCEL_{\mathrm{CE}} and LDiceL_{\mathrm{Dice}} before their first use in Eq. (2); they are defined only in App. B.2 (p15).
  • Please define the behavior of μ(p,m)=∑upumu/∑umu\mu(p, m) = \sum_u p_u m_u / \sum_u m_u in Eq. (18) when ∑umu=0\sum_u m_u = 0; the 'regularizer set to zero' clause handles missing minibatch samples, not empty masks within a sample.
  • Please specify which robust estimator is used in the severity computation ('robust mean' — median? trimmed mean? Huber?).
  • Please define 'derived mask volume': 3,161 mask volumes from 538 cases (398 AISD + 140 ISLES'24) is ~5.9 per case, and the term is never explained.
  • Please fix the wrong cross-reference: 'by equation 11' (p14) points to the training loss; the intended reference is the RePaint inference procedure described in the following sentences.

Claims needing qualification or correction

  • Please correct the regularizer count: the text says 'three complementary regularizers' but only LflipL_{\mathrm{flip}} and LpairL_{\mathrm{pair}} exist in Eqs. (3)–(4) and (17)–(19); change 'three' to 'two' in §3.1 and App. B.2.
  • Please recompute and reconcile the Table 1 Volume row: the four per-dataset values (0.8922, 0.6353, 0.8184, 0.9087) have mean 0.8137, not the reported macro 0.8373; the text's '0.8184 for predicted lesion volume' matches neither the macro cell nor Table 2's CPAISD Volume 0.8922 for the identical model/test/readout.
  • Please discuss or fix the scale-dependence of SBI: for fixed ratio r=RL/RRr = R_L/R_R and scale BB, SBI=∣log⁡((rB+ϵ)/(B+ϵ))∣→∣log⁡r∣\mathrm{SBI} = |\log((rB+\epsilon)/(B+\epsilon))| \to |\log r| as B→∞B \to \infty but →0\to 0 as B→0B \to 0; in the weak-signal regime SBI≈s/ϵ\mathrm{SBI} \approx s/\epsilon, i.e., a scaled absolute evidence, not an imbalance ratio.
  • Please qualify the background-cancellation claim: for stroke evidence ss and balanced background bb, SBI=log⁡((s+b+ϵ)/(b+ϵ))\mathrm{SBI} = \log((s+b+\epsilon)/(b+\epsilon)) cancels background only when s≫bs \gg b; when s≈bs \approx b (the subvisual case) SBI ≤log⁡2≈0.69\le \log 2 \approx 0.69 regardless of the true imbalance.
  • Please state the assumption ∣ΩL∣=∣ΩR∣|\Omega_L| = |\Omega_R| or normalize the sums in Eq. (6); the unnormalized sums make SBI biased if the registered hemispheres differ in size, since a symmetric probability map would then yield RL≠RRR_L \neq R_R.
  • Please justify the absolute value in the severity computation: ∣xN−x∣|x_N - x| also assigns high severity to hyperdense differences, yet the text claims 'This maps lesion hypodensity onto a common [0, 1] scale'; for hypodense lesions the signed difference is already positive.
  • Please specify how per-slice severities are aggregated into the single dd used by Tsym(d)T_{\mathrm{sym}}^{(d)} (Eq. 1); severity is computed per slice but the transformation uses one dd per sample.
  • Please reconcile the 'severity-matched lesion' claim (p3) with the implementation: App. B.1 says DsymD_{\mathrm{sym}} is built 'at selected severity levels' (p15); the matching procedure is never described.
  • Please address the NormalGen conditioning train/test mismatch: cNc_N is trained on healthy slices (x0∼Dhealthyx_0 \sim \mathcal{D}_{\mathrm{healthy}}, Eq. 10) but applied to AIS slices at inference ('conditioned on cN(x,mU)c_N(x, m_U)', p14) — a domain shift in the conditioning variable.
  • Please reconcile 'strictly symmetric counterfactual cases' (p3) with the implementation: mc=F(m)m^c = F(m) is 'restricted to the brain and excluding overlap with mm' (p14), so the counterfactual is not strictly bilateral for midline-crossing lesions.
  • Please remove or implement the statistical-testing framework implied by Figure 2's 'Empirical Null Distribution' and 'Independent Healthy Reference' panels; no null distribution is constructed and no pp-values are computed anywhere in the method.
  • Please validate the severity conditioning: the claim 'Varying dd controls the appearance of the added lesion' (p15) is never supported by an analysis showing that dd actually controls synthesized lesion severity.
  • Please describe how slice-level counterfactuals DsymD_{\mathrm{sym}} are composed into the 3D training volumes consumed by SθS_\theta; DsymD_{\mathrm{sym}} is defined at slice level but SθS_\theta is a 3D model, and this bridge is never specified.

Consistency checks and strengths

  • Type/dimension checks pass: xctx=(1−m)⊙x−m∈[−1,1]x_{\mathrm{ctx}} = (1-m) \odot x - m \in [-1,1] is consistent with the stated rescaling; the 4-channel utu_t matches Table 5's 'U-Net input channels 4'; (1+3mu)∈{1,4}(1+3m_u) \in \{1,4\} matches 'weights 4/1'.
  • The paper contains no theorems, lemmas, or propositions; the only formal statement (Eq. 8, hemisphere-exchange invariance) is trivially correct, as are the claims that balanced evidence gives SBI near zero and that SBI is invariant to hemisphere exchange.
  1. Reproducibility

Thank you for the detailed reproducibility statement, the thorough Appendix A, and the transparent reporting of dataset inventories and ethical considerations. The following suggestions are intended to make the already strong reproducibility package fully verifiable and to close a few remaining gaps between the claims and the available artifacts.

  • Reconcile dataset counts and move the local-inventory caveat earlier. The prose in §4.1 and Table 4 currently disagree for several datasets: SinoCT 9,776 vs. 4,381, AISD 397 vs. 398, APIS 96 vs. 54, and ISLES'24 149 vs. 140. Please harmonize these numbers and state explicitly which figure refers to the local inventory versus the official release. In addition, the caveat “Available counts refer to the local data inventory, not official dataset release sizes” appears only in the Table 4 caption (p.13); please also include it at the first use of “5,085 volumes” in the abstract/introduction so readers are not misled before reaching the table.

  • Add an explicit code-release and data-availability statement. The reproducibility statement (p.10) promises “training settings, model hyperparameters, and implementation details,” but no code or data commitment appears anywhere in the paper. Please add a dedicated statement indicating whether code, trained weights, and preprocessed data will be released, under what license, and at which repository/DOI. Even a clear “available upon request” is more actionable than silence.

  • Strengthen the ethics statement with governance details. The current statement (“We considered the potential ethical implications of this work and identified no specific concerns,” p.10) asserts an outcome without documenting the process. Please add: IRB approval or exemption status, informed-consent arrangements for the clinical datasets, data-usage agreements with each of the five public sources, and dataset-license information. This will make the ethical review auditable rather than merely declarative.

  • Specify the fixed segmentation threshold used for the Volume comparator. §4.1 (p.7) mentions “a fixed segmentation threshold yields a predicted mask,” but the threshold value is not given. Please report the exact threshold (e.g., 0.50.5 or a calibrated value) and state explicitly whether it was chosen on the test set or fixed a priori. If it was tuned, describe the tuning procedure and the data split used.

  • Report the full training hyperparameters for SθS_\theta. The claim “All backbones follow the same training protocol; implementation details are provided in Appendix A” (p.7) is inaccurate because Appendix A (pp.13–14) contains only generator settings (Table 5). Please add a companion table for SθS_\theta listing the learning rate, number of epochs/steps, optimizer and its parameters, batch size, the Dice loss weight λdice\lambda_{\mathrm{dice}}, and the random seeds used. This is essential for reproducing the main results.

  • Specify the training protocol of the “SBI without false belief” ablation. This central ablation (Table 1, p.6; §4.3, p.7) is currently unverifiable: the data, losses, and hyperparameters used to train this variant are not described. Please provide the exact protocol, or explicitly state that it uses the same settings as the full SBI model with only the false-belief component removed. If the ablation was trained with different data or a different loss, those differences must be documented.

  • Add uncertainty quantification to the AUROC results. The paper reports single AUROC point estimates throughout, with only one confidence interval, and no DeLong tests or multi-seed variance. The Discussion itself concedes that “paired comparisons are needed to assess the uncertainty of the differences” (§4.4, p.9). Please report confidence intervals for all AUROC values, perform DeLong tests for the key pairwise comparisons (e.g., SymBreak vs. each backbone),, if feasible, run multiple seeds to report mean ±\pm standard deviation. This will substantiate the claim that “symmetry breaking provides a more stable diagnostic signal under cross-domain shifts” (§4.2, p.7).

  • Clarify the role of the archived generator test splits. Appendix A (p.13) mentions “The archived generator test splits contain 50 SinoCT volumes for NormalGen” and 116 non-CPAISD AIS volumes for LesionGen, but these splits are never referenced in the main text. Please explain whether these splits were used for generator evaluation only, for early stopping, or for any downstream analysis. If they are not used in the main experiments, state that explicitly to avoid confusion.

  • Acknowledge the small positive count in the smallest stratum and report CIs for all strata. The headline result “0.958 [0.880, 1.000]” for lesions ≤20\leq 20 mL (Table 3, p.8) rests on only 12 AIS cases versus 200 controls. Please add a sentence noting this imbalance and its implications for the precision of the estimate. In addition, report confidence intervals for the other strata (e.g., 2020–5050 mL, >50>50 mL) so readers can assess the stability of the pattern across lesion sizes.

  • Report compute and software details. The paper currently omits hardware, library versions, and runtime/cost. Appendix A (p.13) states “batch settings are those specified by the launch scripts,” but no scripts are provided. Please add: GPU model(s) and count, PyTorch (or other framework) version, CUDA version, key library versions (e.g., MONAI, SimpleITK), total training time per model, and approximate total compute (e.g., GPU-hours). If launch scripts exist, include them in the code release or as supplementary material.

  • Specify the registration algorithm and target. The preprocessing description (App. A, p.13) mentions “spatial registration, denoising and spatial normalization to the MNI space” but does not name the registration method. Please specify the algorithm (e.g., affine vs. nonlinear, SyN, ANTs, FSL FLIRT/FNIRT), the target template (e.g., MNI152 1mm or 2mm), and the interpolation method. This is critical for reproducing the exact input geometry.

  • Support or soften the “accurate and robust approach” claim. The abstract (p.1) states “these findings establish SymBreak as an accurate and robust approach for detecting hyperacute ischemic changes,” but the paper reports no sensitivity/specificity, no comparison to prior deep-learning detectors, and the Discussion itself lists caveats (bilateral infarcts, registration errors, artifacts) that directly limit this claim. Please either add sensitivity/specificity at the operating point used for the Volume comparator, include a comparison to at least one prior AIS detector, or temper the wording to “promising” or “effective in our evaluation cohort.” The current phrasing overreaches relative to the evidence presented.

  • Discuss the interaction between the implanted prior and the native symmetry mechanisms of the backbones. The three backbones include Cl-SegNet and AsymFeX, which are themselves symmetry-based AIS methods (§4.2, p.7). The paper never addresses whether their intrinsic symmetry handling reinforces, conflicts, or is redundant to the implanted false-belief prior. Please add a short discussion of this interaction, including any empirical observations (e.g., whether SymBreak’s gain is smaller for these backbones than for non-symmetric ones). This will strengthen the conceptual contribution and help readers understand when the prior is most beneficial.

These changes will make the reproducibility section fully actionable and will further increase confidence in the reported results.

  1. Spelling, Grammar, Acronyms
  • Cross-references (strength): All figure, table, and section cross-references resolve correctly throughout the manuscript. We found no instances of “Figure ??” or “Table ??” — this is a clear sign of careful final proofreading, and it makes the paper much easier to navigate.

  • Dataset name (minor): In §4.1 (p6), please correct the dataset name: “The Core-Penumbra Acute Ischemic Stroke Dataset (CPAISD)” should be “Core-Penumbra Hyperacute Ischemic Stroke Dataset” to match the official dataset title (Sci Data 2025). The acronym “CPAISD” can remain unchanged, but the full name should be accurate for consistency with the cited source and to avoid confusion for readers who look up the dataset.

Minor editorial findings (typos and wording)

3 minor points, listed here rather than in the sections above so they do not obscure the substantive feedback. None of these affects the scientific content.

  • Fix the typos: 'AsymFex' → 'AsymFeX' (Table 2 caption vs text/reference); 'with baseline without false belief setting' → 'with the baseline (without false belief)';
  • Expand or define the acronyms never defined: ADC (p6), EMA (Table 5), MNI (p13), NIfTI (p13), PACS (p6), Δsym\Delta_{\mathrm{sym}} (p8), APIS (p6), SinoCT (p6). [p1 (AIS, DWI); pp6–14; p8, Figure 3/4 area]
  • Fix the grammar/clarity issues: 'with the gains remaining consistent across held-out external evaluations' (p3) is awkward; 'We evaluate our framework against baseline methods using five NCCT datasets' (p6) is imprecise because the comparators are readouts derived from the same predictions, not independent methods. — "with the gains remaining consistent across held-out external evaluations" [p3; p6]
Questions for authors
  1. Could you report AUROC (and, if possible, sensitivity/specificity) for at least one state‑of‑the‑art deep‑learning AIS detector (e.g., Lu et al., 2022 or the PAPL method) on the same four held‑out AIS cohorts, so that the clinical value of SymBreak can be directly compared to existing baselines?

  2. Please evaluate your model on the ISLES’24 challenge test set (100 cases) and provide the corresponding leaderboard‑compatible metrics, together with a comparison to the official ISLES’24 baseline, to demonstrate performance on an external standardized benchmark.

  3. The paper omits several key hyper‑parameter values (e.g., the stability constant ε in Eq. 7, the Dice loss weight λ₍dice₎, and the exact values of λ₍flip₎ and λ₍pair₎ at first use). Could you disclose these values and include a brief sensitivity analysis showing how variations affect the reported SBI and AUROC results?

  4. Several symbols are overloaded or undefined (ε used both for Gaussian noise and a stability constant, Ω used for different domains, and symbols such as ε_φⁿ, ε_ϕᴸ, \tilde{x}^{(d)}). Please provide a clear notation table that assigns distinct symbols to each concept and defines all previously undefined symbols used in the equations.

  5. The generator component is central to the method, yet no fidelity assessment is presented and the process of assembling slice‑level counterfactuals into 3D volumes is unclear. Could you (a) report a quantitative fidelity metric (e.g., FID or a human rating) for the NormalGen/LesionGen outputs, and (b) describe how the generated slices are combined into full‑volume inputs for the segmentation model S_θ?

Reviewer_8AnMOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
1
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Paper summary

This paper proposes SymBreak for detecting subtle ischemic changes in non-contrast CT. It trains a segmentation model on synthetic bilateral lesions to encourage balanced background responses, then uses hemispheric imbalance in predicted lesion probabilities for diagnosis. Experiments evaluate the approach across datasets and segmentation backbones.

Critical strengths
  1. I find the idea of making residual background responses more predictable interesting for weak-signal detection. The method connects bilateral counterfactual training with a simple patient-level diagnostic score based on hemispheric imbalance.

  2. SBI outperforms NWU and predicted lesion volume with all three tested segmentation backbones, supporting the usefulness of this diagnostic readout across the evaluated architectures. The cross-dataset results provide additional preliminary evidence, although their interpretation is limited by the source-confounding concern in W1. (Tables 1–2.)

Critical weaknesses
  1. The evaluation does not sufficiently establish the intended clinical diagnostic claims. Each AIS test cohort is compared with SinoCT controls, leaving disease status associated with data source. Standardized preprocessing does not rule out source effects, so an evaluation of AIS and symptomatic non-AIS patients from the same clinical source would materially strengthen the evidence. Furthermore, although CPAISD is described as hyperacute, the paper does not report performance within an explicitly defined onset-to-CT window or among cases independently judged to have no visible ischemic changes on NCCT. Lesion-volume stratification does not directly validate these target groups. These limitations weaken the claims about clinical generalization and hyperacute, subvisual ischemia. (Sections 4.1 and 4.4, Table 1.)

  2. The contribution of the implanted prior and the interpretation of its effects remain insufficiently established. The no-prior baseline is not described clearly enough to determine which training conditions are held constant, and matched component ablations are missing to separate bilateral synthesis from the additional consistency losses. Moreover, CPAISD AUROC decreases numerically from 0.9357 to 0.9226, despite the improved-separation description in Section 4.3. Lower SBI values in non-stroke controls alone do not establish better diagnostic discrimination. The main prior-versus-no-prior comparisons also lack paired confidence intervals for the AUROC differences and results from repeated training runs, leaving the stability of the reported gains uncertain. (Sections 3.1 and 4.3, Table 1.)

Questions for authors

Do the available data support an evaluation of AIS and symptomatic non-AIS patients from the same clinical source, or an analysis controlling for differences in data source?

How many test cases were scanned within 4.5 hours of onset, and how many were independently judged to have no visible ischemic changes on NCCT? Please report subgroup performance where the annotations permit. If these annotations are unavailable, please clarify which hyperacute and subvisual claims the existing evidence can support.

What training data, losses, training budget, and model-selection procedures are used for the no-prior baseline? Which are held constant relative to SymBreak, and are matched ablations available to separate the contributions of bilateral synthesis and consistency losses?

How do you reconcile the numerical decrease in CPAISD AUROC with the statement in Section 4.3 that separation improves? Are paired confidence intervals for the prior-versus-no-prior AUROC differences or results from repeated training runs available?

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