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Under review as a conference paper at ICLR 2027

SIFT: Robust Meta-Faithfulness Verification of Chain-of-Thought Reasoning Under Distribution Shift

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Abstract

Chain-of-Thought (CoT) faithfulness detectors are widely used to audit reasoning models, yet a detector is itself a predictor whose verdicts are treated as stable properties of the model. We ask whether a faithfulness detector is faithful to itself under distribution shift. We formalize **meta-faithfulness** as an invariance principle: a valid detector must return identical verdicts on traces that differ only by transformations preserving ground-truth faithfulness. We prove three results: a behavioral indistinguishability theorem showing that no detector operating on intervention-response profiles can separate faithful from epiphenomenal mechanisms with identical signatures; an invariance-violation lower bound showing that any detector relying on shift-sensitive features must violate invariance at a rate independent of its in-distribution accuracy; and an asymptotic certified selective-risk guarantee enabling abstention with high confidence. We operationalize this principle in FaithShift, a stress-test protocol spanning ten shift axes, and propose **SIFT** (**S**hift-**I**nvariant **F**aithfulness **T**rajectory Detector), a hidden-state trajectory detector trained with cross-environment invariance objectives and certified abstention. Across 14,996 traces, four reasoning domains, and eight model architectures, three findings emerge. *First*, transfer collapse is real: all existing detectors exhibit gaps AUROC. *Second*, the dominant bottleneck is sampling stochasticity, not shift sensitivity: over 80% of detector instability stems from random seed variation rather than distribution shift, falsifying our preregistered hypothesis that shift-attributable invariance violations would exceed 0.25. *Third*, SIFT reduces shift-attributable instability, but its advantage vanishes against ensembles: SIFT cuts invariance violations by 64% over the best single-seed baseline, but a four-seed ensemble of any detector narrows the margin to 0.01, and at matched coverage the two are statistically indistinguishable (). SIFT also requires a 51% abstention rate that exposes a robustness-usability trade-off. Cross-model transfer degrades along a clear hierarchy, within-family cross-family open-weight open-weight to API, which multi-model training on 3-4 models partially closes. We therefore position this work as a framework for auditing auditors and a diagnosis of the actual barrier to reliable faithfulness detection: not distribution shift, but detector variance.

Primary area:
foundation or frontier models, including LLMs
Keywords:
chain-of-thought faithfulness, faithfulness detection, meta-faithfulness, distribution shift, invariance, certified selective risk, hidden-state trajectories, robustness

Reviews

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1234this paper, Bottom 2%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_K9bcOpenReview ↗
Rating
1
Confidence
4
Informativeness
1
Presentation
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1
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Paper summary

This paper proposes meta-faithfulness as a criterion for evaluating chain-of-thought faithfulness detectors: predictions should remain invariant under faithfulness-preserving transformations and respond appropriately to faithfulness-altering transformations. It introduces the FaithShift evaluation protocol, theoretical results concerning detector limitations and selective risk, and SIFT, a trajectory-based detector combining hidden-state features, invariance training, and abstention. The paper ultimately emphasizes an empirical diagnosis—that stochasticity dominates distribution-shift sensitivity—and reports that simple ensembling substantially narrows SIFT’s advantage.

Critical strengths

The audit-of-auditors perspective is well motivated. Evaluating preservation invariance jointly with alteration sensitivity and coverage is a useful way to assess faithfulness detectors beyond in-distribution AUROC. Requiring alteration sensitivity also addresses the trivial solution of obtaining perfect stability by always returning the same prediction.

Critical weaknesses
  • Internal inconsistencies undermine the central empirical conclusions.

Equation (8) defines MFS as coverage multiplied by a harmonic mean bounded by one, so MFS cannot exceed coverage. Yet Table 1 reports SIFT’s MFS as 0.72 at coverage 0.49; substituting the reported IVR and AS gives approximately 0.404. This discrepancy affects the principal comparisons and ablations.

The claim that over 80% of instability is stochastic is likewise unsupported by Table 1: the seed-repeat component is approximately 30% for four baselines and 27% for SIFT; the 82% figure applies only to attribution-consistency. Moreover, Appendix G redefines raw IVR as the union of seed-induced and transformation-induced disagreements, rather than the transformation disagreement defined in Eq. (6). The ensemble conclusions are also inconsistent: Table 8 reports 0.76 versus 0.71, a margin of 0.05, while the text describes 0.01. Finally, p=0.21p=0.21 does not establish equivalence. These issues prevent a reliable assessment of either SIFT’s advantage or the proposed stochasticity diagnosis.

  • The remaining contributions do not sufficiently establish the claimed verification capability.

The theoretical results have limited implications for SIFT: Theorem 4.5 is conditional on identical observations, Theorem 4.6 relies on local sensitivity and independence assumptions, and Theorem 4.7 requires calibration samples from the evaluation distribution. None establishes that SIFT’s descriptors identify causal faithfulness or remain certified under unseen shifts. The multi-feature bound in Theorem N.1 also incorrectly uses an upper bound on score perturbation to derive an IVR lower bound; orthogonal perturbations provide a counterexample.

FaithShift’s construct validity remains unclear. Answer sensitivity to CoT scrambling does not establish mechanism preservation across a transformed pair. Alteration sensitivity is supported by only three pairs each for cue injection and cue verbalization, while the reported pooled AS differs between the main table and limitations.

Conflicting architecture descriptions and insufficiently specified API access to Claude-3/GPT-4o hidden states further limit the interpretability and reproducibility of the cross-model results.

Questions for authors
  • Metric definitions and reporting: Which implementation of MFS generated the tables, and how can MFS=0.72 coexist with coverage=0.49? Please reconcile the reported components using the existing predictions. Please also clarify the inconsistent AS values and whether “transfer gap” denotes an average or worst-axis gap, including the definitions used for the preregistered hypotheses.

  • Stochasticity decomposition: Is the primary IVR the transformation-disagreement statistic in Eq. (6), or the union statistic in Appendix G? What aggregation supports the suite-wide 80% conclusion? Please specify whether the varied randomness belongs to backbone generation, feature extraction, detector training, or inference.

  • Ensemble comparison: Which configurations and operating points underlie Table 8, the matched-coverage comparison, and Appendix H? Please reconcile their reported differences and identify the comparator associated with p=0.21p=0.21. If equivalence was not tested, could the conclusion be limited to the absence of a statistically detected difference?

  • FaithShift construction and audit validity: Please reconcile 750 base items with the description of 250 items from each of four domains, and provide the existing verified-pair counts used for AS. What exactly does the scrambling audit establish, and why is it interpreted as mechanism preservation rather than intervention sensitivity?

  • Theoretical contribution and correctness: What conclusion specific to SIFT follows from Theorem 4.5? How do the Appendix K diagnostics support the assumptions of Theorem 4.6? Please address the orthogonal-perturbation counterexample to Theorem N.1 and correct or restrict the bound.

  • Certification and risk curves: Which distribution supplies the calibration data, and is target-specific calibration used for each shift? How is dependence among traces from the same base item handled in certification? Please also reconcile Table 3 with Figure 9 and explain why Proposition M.10, concerning optimal coverage as allowed risk changes, justifies smoothing risk as a function of coverage.

  • Implementation and cross-model evaluation: Which SIFT architecture generated the main results? How were trajectories aligned across models, and what target data were used for alignment or calibration? For the cached Claude-3/GPT-4o hidden states described in Appendix P, please identify the API endpoint/version and returned features, and clarify how the eight-model evaluation relates to the two-backbone trace construction.

1 comment
AuthorsOpenReview ↗

To the Program Chairs and Area Chairs, Concern Regarding Reviewer K9bc's Review (Submission 32732)

Dear PC and AC,

We request a human-level review of our paper. The Pangram report (link) flagged 94% as AI-generated, but we do not trust this review. Pangram itself notes false positives (~1 in 10,000), limited confidence on short/formulaic text, and segment-based scoring that mislabels hybrid human-AI editing. We ask that reviewers assess the substantive content and author contributions directly, rather than relying on this automated 94% figure.

Sincerely,

The Authors

Reviewer_61BMOpenReview ↗
Rating
1
Confidence
3
Informativeness
2
Presentation
1
Soundness
1
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Paper summary

The paper studies whether CoT faithfulness detectors remain reliable under changes to their inputs and evaluation settings. It introduces FaithShift to test detector stability and sensitivity, and proposes SIFT, which uses hidden-state trajectories, invariance training and selective abstention. The experiments also examine variation across random seeds and compare SIFT with ensemble baselines.

Critical strengths
  1. A faithfulness detector can become unreliable when the model, task or input format changes. Evaluating detectors on paired traces with verified label preservation or alteration is a useful way to investigate this problem.

  2. The paper includes ensemble baselines, coverage-matched comparisons and component ablations. It also acknowledges that several initial hypotheses are unsupported and that simpler ensembles recover much of SIFT’s reported advantage.

Critical weaknesses
  1. SIFT is reported to have an MFS of 0.72 at a coverage of 0.49, although the stated formula limits the score to the coverage. Using the listed values gives about 0.40. The claim that stochasticity accounts for over 80% of instability also holds for only one detector in the table. The others are around 27% to 30%.

  2. The paper reports eight models and six detector families, then describes a setup with two small models and two detectors elsewhere. It also gives 750 base items alongside four domains containing 250 items each. I cannot tell which setup produced each result.

  3. A model may change its answer after CoT scrambling because the text has become incoherent. This does not establish that the original and transformed traces use the same reasoning mechanism. The audit needs a more direct check of mechanism preservation.

  4. Paraphrasing and language changes appear in both the training environments and the robustness tests. The paper does not clearly identify which transformation types were withheld from training. This leaves the detector’s ability to handle unfamiliar changes insufficiently tested.

Questions for authors
  1. How was MFS 0.72 calculated using IVR 0.10, AS 0.76 and coverage 0.49?

  2. Which models and detectors were used to produce the main results?

  3. What evidence shows that the scrambling test verifies preservation of the reasoning mechanism across a transformed pair?

  4. Which transformation types were completely absent from training and introduced only during evaluation?

3 comments
AuthorsOpenReview ↗

To the Program Chairs and Area Chairs, Concern Regarding Reviewer 61BM's Review (Submission 32732)

Dear PC and AC,

We request a human-level review of our paper. The Pangram report (link) flagged 96% as AI-generated, but we do not trust this review. Pangram itself notes false positives (~1 in 10,000), limited confidence on short/formulaic text, and segment-based scoring that mislabels hybrid human-AI editing. We ask that reviewers assess the substantive content and author contributions directly, rather than relying on this automated 96% figure.

Sincerely,

The Authors

Thank you for the revisions. The corrected MFS, clearer experimental setup, and explicit list of held-out transformations address several of my original concerns. The scrambling audit shows that the model responds to the intervention. My main concern remains whether the original and transformed traces use the same reasoning mechanism. I’m keeping my rating at 1.

We thank Reviewer 61BM for acknowledging that the corrected MFS, clearer setup, and explicit held-out transformation list address several original concerns and for confirming the scrambling audit shows the model responds to the intervention. We address the remaining concern directly: it is the paper's central question, and we did not make that prominent enough.

1. Meta-faithfulness is label preservation, not mechanism preservation, by design. Definition 4.1 defines preserving as φ*(M, x′, c′) = φ*(M, x, c): the ground-truth faithfulness label is unchanged. Section 4.1 states, "This is label preservation, not mechanism preservation; the distinction is audited in Appendix J and discussed in Section 8." The concern is a scope condition we named and audited, not a gap overlooked. What we require is that the audited label be preserved, the only thing an auditor can be held to without access to the model's true computation.

2. The paper's central theorem is precisely that behavioral detectors cannot establish mechanism identity. Theorem 4.6 proves no behavioral detector can separate faithful from epiphenomenal mechanisms when intervention-response profiles coincide. This is a core contribution (Contribution 2), not a hidden limitation: if identical profiles do not imply identical mechanisms, we agree, and we prove this is a fundamental limit on the behavioral-detector family, not a fixable flaw.

3. The scrambling audit is the mechanism-response check the reviewer asks for. It verifies the intervention is causally effective rather than a no-op; with the independent label audit (Definition 4.2: only pairs with a confirmed flip enter the sensitivity estimate), we establish the intervention is effective and the audited label changes. It cannot establish mechanism identity: the reviewer's standard is stronger than any behavioral audit can certify, which is precisely Theorem 4.6.

4. We report the construct-validity limit as a substantive finding, not a caveat. Finding 3: two of three label-altering transformations verify at only 0.2% (3 of 1,500 pairs each for cue injection and cue verbalization), while causal truncation yields 212 (14.1%). We report this as "a construct-validity result about cue-based unfaithfulness induction" and rename the statistic AS_CT. We do not claim cue injection preserves the mechanism; we show it barely alters the audited label, so alteration sensitivity is measurable only under causal truncation.

5. SIFT is a trajectory detector precisely because behavioral profiles are insufficient. SIFT extracts hidden-state trajectories and trains with cross-environment invariance objectives (Section 5), because the behavioral route is provably limited (Theorem 4.6). We do not overclaim: SIFT "demonstrates that invariance training reduces stochastic instability, not that it is broadly superior" (Section 1), and clears no preregistered margin (H3 unsupported).

6. Revision plan. We will: (a) add an introduction paragraph stating that meta-faithfulness is label preservation and mechanism identity is not certifiable by any behavioral audit (citing Theorem 4.6); (b) move the Appendix J audit summary into the main text as "What the invariance principle does and does not certify"; (c) note the label-vs-mechanism distinction in the abstract; and (d) state in Section 8 that the reviewer's standard is the correct, stronger standard, unattainable under behavioral auditing, which is why we position the work as a framework for auditing auditors.

We ask only whether the concern is one the paper fails to address or one it addresses by proving it cannot be addressed behaviorally. Our position is the latter: Theorem 4.6 formalizes the objection, Finding 3 is its empirical footprint, and the distinction is stated in Definition 4.1 and audited in Appendix J. If the view is that a paper whose central theorem establishes a limit on its own construct cannot be accepted here regardless of how clearly that limit is stated, we would value hearing that explicitly, as it is a judgment about venue fit, not about whether the concern was anticipated.

Reviewer_1xzfOpenReview ↗
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2
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1
Informativeness
2
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2
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Paper summary

This paper asks whether CoT faithfulness detectors remain reliable when inputs or models change. It introduces FaithShift to test whether detectors keep the same judgment when faithfulness is preserved and change it correctly when faithfulness changes. The authors also propose SIFT, which uses hidden-state and attention trajectories, is trained across different environments, and can abstain on some samples to control its error rate. The authors find that existing detectors transfer poorly and argue that variation across random seeds explains most of their instability. SIFT has limited gains over simple ensembles and abstains on about half the samples. I think the question is worth studying, but the links between the theory, the chosen features, and the experiments are not clear. It is also unclear whether these features measure faithfulness or other properties of the traces. More importantly, several reported numbers do not match the metric definitions or support the paper's main conclusions.

Critical strengths

The research question is practically meaningful.Faithfulness detectors are themselves predictors subject to data distributions and estimation error, so reporting only in-distribution performance is insufficient; their applicable scope and stability should be examined. "Auditing the auditors" is a question worth studying.

Critical weaknesses
  • The writing feels AI-generated and insufficiently checked. Much of the text is repetitive and formulaic, while important claims change between sections. Section 5 describes SIFT as achieving "superior meta-faithfulness," but the conclusion acknowledges that it is not broadly better than the baselines. Also, five residual "CHANGED." markers in the appendix (near E.1, E.5, E.7, and the limitations appendix), apparently leftover edit-tracking artifacts; Font sizes and line spacing are inconsistent, and captions are much larger than the body text. These issues give the impression of text assembled without a careful final check. They do not establish whether AI was used; my concern is that the authors have not resolved contradictions that directly affect how the results should be read.
  • The theory, method, and results do not add up to a convincing argument. Poor cross-model transfer does not by itself show that a detector fails to measure faithfulness as changing the model also changes the data distribution and possibly the faithfulness label. Likewise, early answer decodability or changes in hidden states need not tell us whether the visible reasoning actually caused the answer. The theorems do not establish that SIFT's chosen features resolve this problem, and the selective-risk guarantee is not a guarantee of robustness to arbitrary distribution shifts.
Questions for authors
  • The required AI Use Statement is missing. ICLR 2027 requires every submission to disclose AI use in a mandatory section (not counted toward the page limit), regardless of whether or how AI tools were used. This submission contains an Impact Statement and a Reproducibility Statement but no AI use disclosure.
  • Please explain how MFS 0.720.72 and coverage 0.490.49 in Table 1 can jointly satisfy Eq. (8). Do these metrics come from different subsets or operating points? After recomputing all methods and ensembles under a unified definition, do the rankings, the ablation outcomes, and the coverage-matched comparisons survive?
  • What is the relationship between the calibration data and each transfer test distribution? Which operating points are recalibrated on the target distribution and which transfer the source-distribution threshold directly?
2 comments
AuthorsOpenReview ↗

To the Program Chairs and Area Chairs, Concern Regarding Reviewer 1xzf's Review (Submission 32732)

Dear PC and AC,

We request a human-level review of our paper. The Pangram report (link) flagged 84% as AI-generated, but we do not trust this review. Pangram itself notes false positives (~1 in 10,000), limited confidence on short/formulaic text, and segment-based scoring that mislabels hybrid human-AI editing. We ask that reviewers assess the substantive content and author contributions directly, rather than relying on this automated 84% figure.

Sincerely,

The Authors

I used AI tools for English translation and language polishing of a review that I originally wrote in Chinese, and I disclosed this in the required AI Documentation for Reviewing field. The final evaluation reflect my own assessment. I hope this clarifies the matter.

Comments on the paper

1 comment

Thanks for the response, but we do not trust your evaluation while understanding even the English language and how clearly you understand scientific arguments. We also noted that your evaluation confidence is 1. How can you judge a paper if you are not confident in what you are doing?. We also have significant concerns about your evaluation being fully AI generated; we do not care what you translate, we care about your real weakness when your evaluation does not make sense to us. We still request human-level evaluation.

Please note that there are a lot of translators with different language support, and why does AI need to translate?

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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