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Under review as a conference paper at ICLR 2027

Beyond Answer Consistency: Evaluating the Stability of Explicit Clinical Reasoning Across Repeated LLM Generations

Abstract

Final-answer consistency does not necessarily imply stability in the explicit reasoning produced by a large language model (LLM). This distinction is particularly important in clinical diagnosis, where repeated generations may reach the same conclusion while relying on substantially different evidence and interpretations. We study clinical reasoning stability by representing generated diagnostic reasoning as Clinical Reasoning Graphs (CRGs) and comparing their explicit support structures using a symmetric structural distance, CA-CRED. To distinguish prompt-associated changes from ordinary generation variability, we introduce a leave-one-case-out calibration procedure and a case-level calibrated Structural Reasoning Divergence score (cSiRD). Using 120 clinical cases and 720 formal generations from Qwen3-8B, we find substantial structural variability even under repeated generation of the same case. Importantly, the apparent increase in structural dispersion under Structured Reflection largely disappears after masking diagnostic conclusion identity: the Baseline–Structured within-condition gap decreases from 0.0661 to approximately 0.0020. Likewise, the strong association between conclusion-aware cSiRD and answer changes (AUC = 0.888) is markedly reduced under support-only calibration (AUC = 0.599), indicating that final diagnosis identity accounts for a substantial portion of the original separation. Nevertheless, semantically consistent diagnostic answers can still coexist with highly divergent support structures. Finally, in an exploratory multi-level analysis, support-only similarity follows a consistent hierarchy across cases, with same-case similarity (0.7280) exceeding same-diagnosis similarity (0.7005), which in turn exceeds different-diagnosis similarity (0.6952). Together, these results suggest that answer consistency, conclusion variation, and support-structure stability capture distinct aspects of observable clinical reasoning behavior.

Primary area:
foundation or frontier models, including LLMs
Keywords:
large language models, clinical reasoning, reasoning stability, clinical reasoning graphs, diagnostic reasoning, medical AI

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.75 over 4 reviews, above 25% of the others.
Reviewer_aX5xOpenReview ↗
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Paper summary

This paper studies whether agreement in a large language model’s final clinical diagnosis implies stability of the explicitly expressed reasoning that supports it. The authors generate three responses per condition for 120 MedCaseReasoning cases using Qwen3-8B under a baseline prompt and a structured-reflection prompt. They convert each response into a deterministic Clinical Reasoning Graph containing FACT, INTERPRETATION, and CONCLUSION nodes connected in a star-shaped support structure. They then compare graphs with the CA-CRED distance and calibrate cross-prompt differences against repeated-generation variability using a leave-one-case-out cSiRD score. A conclusion-aware analysis finds greater dispersion under Structured Reflection, whereas masking conclusion text reduces the Baseline–Structured gap from 0.0661 to approximately 0.0020. Answer-status discrimination also falls from AUC 0.888 to 0.599 after masking. An exploratory support-only analysis reports higher similarity for repeated generations of the same case than for cases sharing or not sharing a diagnosis. The paper argues that answer consistency, conclusion variation, and observable support-structure stability should be evaluated as distinct properties.

Critical strengths

1. Meaningful evaluation perspective with a transparent experimental protocol. The paper highlights an important distinction between final-answer consistency and the stability of explicitly expressed supporting evidence. The comparison between conclusion-aware and support-only analyses illustrates how diagnostic conclusion identity can influence measured structural divergence, with the Structured–Baseline within-condition gap decreasing from 0.0661 to approximately 0.0020 after conclusion masking. The repeated-generation design, fixed experimental configuration, and clearly documented evaluation procedures further strengthen the analysis. Although the interpretation depends on the validity of the proposed graph representation and masking procedure, the paper offers a useful perspective for evaluating clinical LLM reasoning beyond final-answer agreement.

Critical weaknesses

1. Insufficient validation of the proposed reasoning-structure metric. The proposed CRGs use a fixed star-shaped topology, while CA-CRED primarily relies on lexical token overlap rather than explicitly modeling clinical reasoning relationships. Important aspects such as negation, semantic equivalence, and dependencies between clinical evidence are not adequately captured. Without expert validation or comparisons with alternative semantic metrics, it remains unclear whether the measured differences reflect meaningful changes in clinical reasoning structure rather than surface-level textual variation.

2. Limited experimental scope and lack of cross-model validation. All formal experiments are conducted using only Qwen3-8B, a relatively small 8B-parameter model, on 120 clinical cases from MedCaseReasoning. The study lacks evaluations on larger-scale LLMs, models from different families, and additional clinical datasets. Given that reasoning stability may vary with model scale and architecture, it remains unclear whether the reported findings generalize to larger and more capable models. This limited experimental scope weakens the broader applicability of the proposed evaluation framework.

Questions for authors
  1. How do the authors validate that CA-CRED captures clinically meaningful differences in reasoning structure rather than primarily lexical overlap? Could the authors provide human expert evaluations or comparisons with alternative semantic similarity metrics?

  2. Could the authors extend the evaluation to larger-scale LLMs and models from different families to examine whether the observed reasoning stability patterns generalize beyond Qwen3-8B?

  3. Since the support-only analysis masks only the CONCLUSION node, could the authors investigate whether diagnosis-related information remaining in FACT and INTERPRETATION nodes affects the results? Do the main findings remain consistent under more comprehensive diagnosis masking?

Reviewer_2mQHOpenReview ↗
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Paper summary

Paper Summary

Beyond Answer Consistency: Evaluating the Stability of Explicit Clinical Reasoning Across Repeated LLM Generations argues that evaluating clinical LLMs solely on final-answer accuracy or consistency misses whether the supporting reasoning text remains stable across repeated generations. The authors state three contributions, which this review translates into plain language:

  1. They introduce a deterministic, rule-based pipeline that extracts lexically cued spans from an LLM's output into a star-shaped "Clinical Reasoning Graph" (CRG), compares graphs using a primarily token-overlap path distance with a role-consistency term (CA-CRED), and scores prompt-induced shifts against repeated-generation variance via a leave-one-case-out percentile (cSiRD).

  2. They compare "conclusion-aware" graph distance (which includes the final diagnosis string in every path) against "support-only" graph distance (which masks the final diagnosis string with a constant placeholder token), showing that the apparent increase in structural dispersion under Structured Reflection prompting (0.0661) nearly vanishes once the diagnosis string is masked (0.0020), and that discrimination between answer-consistent and answer-changing cases drops from AUC = 0.888 to AUC = 0.599.

  3. They run an exploratory cross-case comparison of support-only similarity across three levels, reporting that repeated generations of the same case are slightly more similar (0.7280) than traces from different cases sharing a diagnosis (0.7005), which in turn are slightly more similar than traces from different diagnosis groups (0.6952).

For validation, the authors evaluate a single model (Qwen3-8B, with native thinking disabled) across 120 cases from the MedCaseReasoning dataset under two prompt templates (Baseline and Structured Reflection, with three stochastic generations per condition, totaling 720 outputs).

Critical strengths

Critical Strengths

The paper addresses an important distinction between consistency of final answers and consistency of expressed supporting reasoning. Repeated generation of the same case is a sensible design, and attempting to separate diagnostic-conclusion identity from the remaining support text is well motivated. The deterministic extraction procedure also favors reproducibility, and the authors are appropriately candid about several limitations and about the exploratory status of parts of the analysis.

Critical weaknesses

Critical Weaknesses

Overall: The paper's claim that Structured Reflection increases structural dispersion appears to be largely an artifact of its own metric. Because this masking decomposition was introduced post hoc during the Qwen3-8B analysis and the surviving support-only and multi-level results are explicitly exploratory, the net solid contribution reduces to a methodological caveat (conclusion identity dominates graph distance) that Patel (2026) had already demonstrated for graph-similarity metrics.

In addition to this major concern, there are two main recurring weaknesses which manifest in multiple ways throughout the paper.

Weakness #1: The central measurement instrument is insufficiently validated and key experimental details are under-specified.

The proposed Clinical Reasoning Graph is a highly constrained representation: lexically selected statements are retained under fixed caps and connected directly to a single conclusion node (the authors themselves describe it as "a constrained star-shaped representation of explicitly expressed support organization rather than a reconstruction of latent multi-step causal reasoning," Sec. 3.2, and concede that it "intentionally favors reproducibility over expressive graph complexity," Sec. 5). The authors do not establish that this representation faithfully captures clinically relevant reasoning, or that it meaningfully examines how deployed LLM-driven systems perform reasoning in practice.

The experiment compares two externally scaffolded output formats in one particular inference configuration. The paper does not provide an examination of ordinary/default behavior versus structured reflection, externally prompted reflection versus native thinking, or reasoning-enabled versus reasoning-disabled behavior. Consequently, the authors cannot tell whether Structured Reflection merely reorganizes reasoning the model would produce anyway or induces something additional. They cannot isolate how Structured Reflection interacts with the model when thinking is enabled, and they cannot show that the masking and stability results persist when native deliberation is active. The authors' "Baseline" is itself a multi-part structured template (requesting a ranked top-five differential, a leading diagnosis with probability estimates, and step-by-step supporting and opposing reasoning). While the paper acknowledges that it compares two prompted conditions, omitting an un-scaffolded default or native-thinking baseline leaves the intervention unanchored to how Qwen3-8B behaves out of the box.

Unlike the cited work by Patel (2026), the authors perform no clinical validation of extraction precision or recall, provide no shuffled-pair noise floor for their masked metric, and never test whether CA-CRED captures anything beyond basic sentence-level word overlap (Patel reports 98.4% edge precision and 94.8% clinically salient recall under physician review of sampled graphs, and a shuffled-label noise floor of 0.466). Comparing the proposed distance with simpler lexical or embedding-based alternatives would have been a low-effort way to demonstrate that their graph formalism contributes something distinct.

Troublingly, the authors never report the model's diagnostic accuracy against the ground-truth case diagnoses, even though the gold labels were in hand and were used structurally (Sec. 2 describes MedCaseReasoning as providing reasoning statements "alongside diagnostic labels," and Sec. 4.1 groups the 120 cases into "12 frozen diagnosis groups"). Answers are only labeled across repetitions as SAME, DIFFERENT, or UNCERTAIN (using an under-specified "model-assisted semantic adjudication" whose judge model and prompt are never named; the authors themselves concede the labels come from "blinded model-assisted adjudication rather than independent expert clinical annotation" and should be treated as "supporting analysis rather than a clinical gold standard," Sec. 5). As written, a reader cannot tell whether the reasoning whose "support structure" is being measured is clinically sound or is a small model's plausible-sounding boilerplate. The paper measures stability of structure with no anchor to whether that structure is clinically accurate or worth stabilizing.

The authors had everything they needed to evaluate this, and doing so would have been straightforward. MedCaseReasoning (Wu et al., 2025) includes both gold diagnostic labels and ground-truth clinical reasoning statements derived from published case reports and validated with board-certified physicians for faithfulness and clinical relevance (validated on a 100-case sample reviewed by four board-certified physicians).

The support-only analysis is also difficult to interpret. Masking the conclusion leaves a shared placeholder in every support path, while diagnosis-related language can remain in the retained support statements; indeed, the authors concede that "the support-only metric reduces rather than eliminates diagnosis-related influence" for exactly this reason (Sec. 5). Without an empirical shuffled-pair floor or other calibration of what similarity unrelated traces receive, the high absolute similarities and the very small same-diagnosis advantage cannot confidently be interpreted as clinically meaningful structure.

This concern is heightened by comparison to Patel (2026), which demonstrated how easily graph-similarity measures can be dominated by shared form and scoring conventions. The present paper needed to show that its new instrument avoids those failure modes, rather than relying primarily on deterministic construction.

There are also significant gaps in reproducibility. In addition to providing no supplementary code or data archive, the authors omit the verbatim Baseline and Structured Reflection prompts from Appendix A.1, which is titled "Frozen Prompting Protocol" yet supplies only prose descriptions (the Reproducibility Statement enumerates the Appendix contents as the CA-CRED equations, frozen CRG construction rules, threshold-sensitivity results, and multi-level aggregation and inference procedures — not the prompts). The manuscript also fails to specify how Qwen3-8B's native thinking was disabled. In Qwen3, disabling thinking via a chat-template parameter versus appending a /no_think control token alters the rendered prompt context. Since the study treats the prompt as the primary intervention, readers cannot verify the exact context given to the model.

Similarly, the authors omit critical serving details. While they provide a model revision hash and sampling parameters, they never state the inference engine/framework, numerical precision or quantization, batching setup, or hardware used. Setting a random seed in Python and NumPy only produces "three reproducible, seed-controlled stochastic draws" (Sec. 4.1) if the exact inference stack, precision, and kernel configuration are held fixed, as serving choices routinely perturb token-level sampling trajectories. In a single-model study with no supplementary dataset release, omitting the serving specification makes exact replication unnecessarily difficult.

Furthermore, while the authors report an 8,192-token cap and note in Table A1 that during conclusion extraction "empty cleaned matches are skipped without introducing new patterns or synonyms," they never report the rate of truncation or failed/empty conclusion extraction per condition. If multi-phase Structured Reflection outputs fail the fixed answer-anchor regex patterns (or truncate) more often than Baseline outputs, that would asymmetrically degrade CRG construction in Structured Reflection. This would amount to a straightforward formatting artifact that could explain why within-condition distance rose in Structured Reflection and collapsed after conclusion masking.

Finally, MedCaseReasoning (Wu et al., 2025) contains 14,489 clinical cases, but the authors evaluate on only 120 cases (about 0.8% of the benchmark, grouped into "12 frozen diagnosis groups with 10 cases per group") without justifying the tiny sample size, explaining the selection criteria, or even naming the 12 diagnosis groups or 120 case IDs anywhere in the manuscript or Appendix. Without knowing which 120 cases were selected, an independent reproduction of this paper would truly be gestural at best.

Weakness #2: The empirical evidence is too narrow and exploratory for the paper's general claims.

All formal results come from Qwen3-8B with native thinking disabled, using one dataset, two prompting conditions, and three generations per case-condition. There is no independent model family, extraction method, dataset, or prompting framework establishing robustness. This scope is insufficient to support broad conclusions about clinical reasoning in LLMs.

There is no justification in the paper for selecting Qwen3-8B as the sole model, nor any argument that an 8B model with thinking disabled is sufficient to carry the paper's claims. Every mention of Qwen3-8B is a setup description, a table/figure label, or a limitation note. There is no compute argument, capability-threshold check, or evidence that this configuration represents models used in clinical research. A single non-thinking 8B configuration cannot support field-wide recommendations in the Discussion such as: "evaluations of clinical prompting strategies should avoid treating a stable final answer as sufficient evidence of stable reasoning behavior."

Patel (2026) used GPT-5.4, GPT-5.2, Claude Opus 4.5, Claude Sonnet 4.5, and Gemini 3 Pro. While evaluating these frontier models (or similar) would have brought this paper in line with the closest prior work, the authors neglected to include a single model that would speak to the impact of scale. They also missed a natural opportunity to justify and strengthen an 8B-focused design. Wu et al. (2025) demonstrate that supervised fine-tuning on MedCaseReasoning substantially improves small open-source models (Table 3: MedReason-8B 10-shot accuracy 0.382→0.501; LLaMA-3.1-8B 0.332→0.479; Qwen-2.5-7B 0.287→0.425) and release the dataset and SFT recipe to reproduce this, so a domain-adapted small model is readily obtainable; comparing base Qwen3-8B against such a counterpart (or again, comparing thinking-disabled against thinking-enabled Qwen3-8B) would have provided a meaningful test of the proposed framework.

Beyond this, Table A1 reveals that Qwen3-8B's outputs contain frequent echoes of the prompt instructions that must be manually stripped via a hardcoded "Dropped phrases" list ("supporting findings; ranking reasoning; estimated probability; high/moderate/low probability; leading diagnosis; top 5"). Because the verbatim prompts are not provided, a reader cannot determine how much of the remaining retained text reflects genuine diagnostic reasoning versus surface compliance with the prompt's formatting cues. While the authors aim to study "how consistently the same clinical case gives rise to explicit reasoning structures," the pipeline risks largely measuring how consistently a single 8B model fills out a requested form.

Finally, the principal Structured Reflection effect nearly disappears once diagnostic-conclusion identity is masked, and the association with answer changes is substantially attenuated, with the remaining support-only mean difference no longer statistically significant. Both the support-only decomposition and the multi-level analysis are explicitly described as exploratory additions introduced after inspecting the Qwen3-8B data. Consequently, the remaining results amount to descriptive observations of sampling variability and a small exploratory cross-case effect on a single model, rather than confirmatory evidence for the paper's broader framing.

Questions for authors

1 Appendix A.1 describes the Baseline and Structured Reflection prompts in prose but does not quote them verbatim. Please provide the exact prompt text (system and user messages) used for both conditions.

2 How exactly was Qwen3-8B's native thinking disabled?

3 Please specify the inference engine/framework, numerical precision or quantization, batching setup, and hardware.

4 Can you report, separately per condition, the rate of truncation at the 8,192-token cap and the rate of failed or empty conclusion extraction under the fixed answer-anchor patterns in Table A1?

5 Please provide the identifiers of the 120 selected cases and the 12 diagnosis groups, along with the selection criteria used to draw them from MedCaseReasoning.

6 MedCaseReasoning provides gold diagnostic labels and clinician-authored reasoning statements. Can you please report diagnostic accuracy against the gold labels on the 120 cases?

7 Did you consider running the protocol with Qwen3-8B reasoning enabled, and with an unscaffolded (no structured template) baseline?

8 The Discussion draws field-wide recommendations from a single non-reasoning 8B model. Would the authors be willing to evaluate additional models (including reasoning-enabled Qwen3-8B and models previously evaluated on MedCaseReasoning) in a revision?

Reviewer_khpPOpenReview ↗
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Paper summary

This paper investigates whether consistency in final clinical diagnoses reflects the stability of LLMs' explicit reasoning. To examine this, the authors convert medical diagnostic responses into Clinical Reasoning Graphs (CRGs), comprising fact, interpretation, and conclusion nodes, and introduce CA-CRED to measure structural differences between graphs. They further propose a leave-one-case-out calibration procedure and a case-level calibrated Structural Reasoning Divergence score (cSiRD) to assess whether divergence between prompting conditions exceeds ordinary generation variability.

Experiments on 120 clinical cases with 720 generations from Qwen3-8B reveal substantial structural variation across repeated generations. In particular, the distance gap between Baseline and Structured Reflection decreases from 0.0661 to 0.0020 when conclusions are masked, suggesting that most of the observed divergence between the two prompting conditions stems from differences at the conclusion level. Similarly, the metric’s ability to distinguish between same and different answer statuses decreases substantially, with the AUC falling from 0.888 (conclusion-aware) to 0.599 (support-only). An exploratory analysis further shows that support-only similarity is highest for generations of the same case (0.7280), followed by different cases with the same diagnosis (0.7005), and cases with different diagnoses (0.6952). Overall, the findings suggest that answer consistency alone is insufficient to establish the stability of explicitly expressed clinical reasoning.

Critical strengths

The paper provides empirical evidence that consistent final clinical diagnoses do not imply consistent reasoning. Specifically, among 23 cases with semantically consistent diagnoses, there are 5 cases still exhibit high structural diversion in the support-only analysis. This finding motivates reconsidering the conventional evaluation of clinical LLM stability, solely on relying on the final answer consistency is insufficient.

Critical weaknesses
  1. The proposed CA-CRED metric has not demonstrated that it can capture the structure of clinical reasoning. Node matching relies on Jaccard similarity over lowercased token sets, which fails to capture semantic meaning. For example, “evidence of consolidation” and “no evidence of consolidation” have high lexical similarity despite expressing opposite clinical meanings. Conversely, paraphrases with similar meanings may have zero lexical overlap. The paper also lacks comparisons with existing semantic similarity metrics (e.g., embedding cosine, BERT score). Furthermore, the reported support-only similarity is 0.7280 for the same case versus 0.6952 for different diagnoses, suggesting limited discriminative ability.

  2. The experimental scale is too small, with only a single dataset (120 cases), one model (Qwen3-8B), and three generations per condition. This limits the reliability of the findings and does not establish that the framework generalizes.

Questions for authors
  1. How does Jaccard over token sets handle paraphrase and negation?
  2. Could the authors compare CA-CRED with other semantic similarity metrics on the headline results?
Reviewer_ZJfqOpenReview ↗
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Paper summary

This paper examines whether an LLM provides consistent diagnostic explanations when it is asked to answer the same clinical case multiple times. The authors convert the written explanations into graphs and compare them with and without the final diagnosis.

Critical strengths

Repeating each case under both prompts gives the study a reference for how much explanations vary under the same prompt.

Masking the final diagnosis is an informative check. The difference in within-prompt variation drops from 0.0661 to 0.0020, showing how strongly the conclusion contributes to the original result.

Critical weaknesses

The case selection is unclear. The paper reports 10 cases per diagnosis group but provides little detail on which diagnoses were included, which MedCaseReasoning split the cases came from, or how cases were selected within each group. This makes the sample difficult to reproduce and the cross-case results hard to interpret.

The paper does not validate whether the graph distance captures clinically important changes in the evidence. A paraphrase can increase the distance, while adding “no” to a finding can reverse its meaning with little effect on token overlap. The reference reasoning in MedCaseReasoning offers a way to check whether the metric detects omitted or misinterpreted evidence.

Questions for authors

Could you list the 12 diagnosis groups and describe how the 10 cases in each group were selected?

Among pairs with the same final diagnosis, do higher distances correspond to more clinically important omissions or misinterpretations when assessed by clinicians?

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