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Under review as a conference paper at ICLR 2027

An Extreme-Value Perspective on Reasoning Failure in Transformers.

Abstract

We study extreme residual-stream changes as markers of reasoning failure in transformers. Under explicit assumptions on tail behavior, dependence, and coupling to logical validity, we derive conditional localization and overshoot laws, characterize a Kesten-type mechanism generating heavy tails, and analyze tail-index estimation accounting for within-trajectory dependence. On eligible failed Lean 4 proofs generated by DeepSeek-Prover-V2-7B, Goedel-Prover-V2-8B, and Kimina-Prover-Distill-8B, the largest whitened residual-stream increment identifies the first rejected step in 17.3–25.4% of cases on miniF2F and, for DeepSeek and Goedel, in 20.4–29.4% on ProofNet-Verified, compared with length-adjusted uniform baselines of 8.7–9.7% and 13.3–14.2%, respectively. In controlled deduction experiments with Qwen2.5-7B-Instruct, an exponential model of success probability as a function of reasoning length, fitted on calibration tasks, reduces the held-out Brier score by 9.2% relative to a constant-probability baseline at temperature 1.0.

Primary area:
interpretability and explainable AI
Keywords:
large language models, formal reasoning, extreme value theory, residual stream, failure localization, heavy tails, theorem proving

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_22KjOpenReview ↗
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2
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Paper summary

This paper studies whether large residual-state changes can help locate the first error in LLM-generated proofs. It develops a conditional extreme-value framework and evaluates residual-jump signals on three Lean provers across two benchmarks. The largest jump identifies the first rejected step more often than a uniform baseline, but its added value over simple features is small and model-dependent, with no significant improvement in online detection. The experiments suggest that jumps serve as relative within-proof signals rather than reliable fixed-threshold indicators of failure.

Critical strengths
  1. The paper provides a clear evaluation target. Lean verification can provide an objective label for the first proof step when LLM makes mistakes.
  2. It provides a broad empirical evaluation within formal proving. The paper also tests three provers across two benchmarks and multiple sampling temperatures.
  3. Positional baselines and prefix-restricted analysis help assess whether the jump signal goes beyond position effects and post-error text.
  4. Online detection and learned-localizer experiments test whether jumps add value beyond simple step features.
  5. The paper also clearly reports unsupported predictions and examines where the theoretical assumptions depart from observed behavior.
Critical weaknesses
  1. The connection between the theory and the empirical findings is limited. The theory provides conditional benchmarks and possible mechanisms for generating heavy tails, but does not explain the relative localization signal observed when fixed-threshold validity coupling fails. The diagnostics in Section 6, together with the lack of support for P1/P3/P4, leave the Kesten/EVT mechanism unvalidated as an explanation of the empirical findings. The paper could be strengthened by clarifying what the theory explains beyond the residual-jump heuristic and which of its predictions are supported by the empirical results.

  2. Concerns on practical value:

  • Could the authors clarify the intended use of the jump signal, given its exact localization rate of roughly 17–29%? Moreover, can the authors discuss when jump features might help online detection? Table 5 shows no significant gain, and exact detection even decreases for Goedel at the 20% target FPR.
  • Is there any reason why adding dump features helps DeepSeek (+2.66 pp) but does not improve Goedel in Table 6?
  • Is there any potential reason why jump should be preferred over surprisal? On ProofNet, surprisal has a higher exact-localization point estimate for DeepSeek.
  1. The comparisons include only uniform random selection, surprisal, and simple features. Could the authors clarify how the method compares with hidden-state probes, such as those cited from Azaria and Orgad, or process reward models?

  2. The connection of P5 to the main framework can be further justified. Could the authors clarify how the P5 experiment validates the proposed extreme-value framework? It uses a different model and synthetic tasks, without measuring residual jumps or testing the coupling assumption. Exponential decay in success could also follow from a simple constant per-step error model, and the improvement over the constant-probability baseline is not significant at temperature 0.6.

  3. Can the localization findings generalize beyond 7-8B Lean provers, particularly to informal reasoning where the first error is harder to identify?

Questions for authors

See weakness.

3 comments
AuthorsOpenReview ↗

sponse to Reviewer 22Kj (1/3)

We thank the reviewer for the detailed and constructive review. Below we list the changes in the revision and answer each point (W: weaknesses).

Changes in the revision related to this review

  • Sec. 3 states that the within-proof statements hold with a tolerance specific to each proof. This explains the relative signal (W1).
  • Sec. 4 states, for each section, which claim it tests; the Kesten mechanism is removed from the contributions (W1).
  • Secs. 7 and 11 add the intended use of the jump and the conditions under which jump features help online (W2).
  • Comparisons with hidden-state probes are in App. J (W3); results on informal solutions are in a new appendix (W5).
  • P5 is removed from the abstract and presented as a test of the predictive value of length, not of the framework (W4).

W1. The connection between the theory and the empirical findings is limited: the theory does not explain the relative signal observed when fixed-threshold coupling fails, and the Kesten/EVT mechanism is not validated.

The theory explains the following.

The relative signal. All within-proof statements — Theorem 3 (localization) and Proposition 5 (read-out noise) — hold with a tolerance τi\tau_i specific to each proof. A threshold common to all proofs is needed only by statements that compare proofs with each other: exceedance of a common level in failed versus verified proofs (Sec. 6) and online detection with a single threshold (Sec. 7). A theory with a proof-specific tolerance therefore predicts exactly the observed pattern: the relative signal within a proof persists, while a fixed threshold fails. An online detector does not know τi\tau_i before the proof ends; the retrospective argmax does not depend on it.

Which predictions are supported.

  • Localization (P2): yes. The jump argmax identifies the first rejected step 1.5–2.9 times as often as a uniform choice, including on new PutnamBench problems for DeepSeek.
  • The discriminating test gives an intermediate result. Under exact coupling the rejected step is the maximum of its prefix in 100% of failed proofs; without coupling, the share is at the level of a positional control (21–35%). We observe 35–43%: there is coupling, but not an exact threshold. Much of the gap comes from the norm as a read-out. Hypothesis 1 is stated for any deviation statistic; with a linear projection of the state learned out of fold instead of the norm, the share rises to 65% (DeepSeek) and 61% (Goedel) against controls of 28% and 26%, whereas the norm is dominated by directions that carry no information about the failure location (W3). Read-out noise lowers the share in the same way (Proposition 5).
  • Tail predictions P1, P3, P4: no.
  • P5 does not test the framework (W4).

The Kesten recurrence is a motivating model of how heavy tails could arise. It is not identified from observed states, and its tail predictions are not supported, so it is removed from the contributions.

In summary, the theory provides the conditions under which the largest step coincides with the failure and a test that discriminates between explanations. The data support coupling with a proof-specific tolerance, but not heavy tails.

AuthorsOpenReview ↗

Response to Reviewer 22Kj (2/3)

W2a. What is the intended use of the jump, given exact localization of 17–29%? When might jump features help online detection? Table 5 shows no gain, and for Goedel exact detection decreases at the 20% target FPR.

Intended use. In Lean the location of the first error is given by the verifier itself: here Lean is a source of exact labels, not the application. In future work we intend to use the largest jump as a likely error location where no step-level verifier exists. The jump requires no error labels: the whitening is estimated from verified proofs only. As a single rule it is weak (within one step: 43% and 48% on ProofNet). Its role is a feature that adds information to a learned localizer (W2b, W3) and a signal that narrows the search for the error within a proof.

Online. The scalar jump does not help online. This is expected for a relative signal: an online detector does not know the proof's own scale (W1). Direction helps. If the norm is replaced by a learned projection of the increment, online exact detection for Goedel on ProofNet increases by 12.2 pp [6.7, 18.1] at a 10% target FPR (Holm-adjusted p = 0.009). The realized FPR shifts by +1.9 pp [−6.4, 11.7], so this does not replace a strict comparison at equal FPR. In addition, from an accepted prefix the jump helps predict whether an error will occur before the end of the proof: on miniF2F, AUROC increases by 0.106 (DeepSeek) and 0.087 (Goedel) over a baseline of length, surprisal and its change. This is the setting of early stopping or restarting generation. On ProofNet there is no such gain.

Goedel at 20% FPR. The threshold is set on verified proofs of the inner folds, and the detector with the jump has a lower realized FPR on the test set: 12.3% vs 14.9%. Part of the decrease in exact detection reflects a stricter operating point.

W2b. Why do jump features help DeepSeek (+2.66 pp) but not Goedel?

The reason is Goedel's strong baseline, not the absence of a signal:

  • in Goedel's eligible population, tactic length predicts the failure location well: a localizer using only tactic length reaches 42.7% (DeepSeek 32.4%), the learned baseline 57.8% (DeepSeek 40.9%);
  • a likely reason is selection by the generation budget: 44% of Goedel's failed attempts (294 of 673) are truncated at 8192 tokens and do not enter the analysis, against 8% for DeepSeek;
  • over such a baseline, even the full 4096-dimensional state of the layer does not help Goedel: −7.0 pp (for DeepSeek +8.2 [2.2, 14.4]);
  • a single learned direction transfers for Goedel: the signed distance of the state to a hyperplane learned on ProofNet, as a single rule, identifies the failure in 38.5% on miniF2F and 39.5% on PutnamBench, against 21.5% and 6.7% for the norm; in the learned localizer on miniF2F it adds +6.8 pp [3.2, 10.6] (Holm-adjusted p = 0.034);
  • against simpler baselines Goedel does gain: over surprisal alone +2.84 pp [−3.27, 8.96] with better NLL; without the tactic-length feature, the jump's contribution is non-negative (+0.50 [−2.38, 3.70]).

W2c. Why should the jump be preferred over surprisal? On ProofNet surprisal has a higher point estimate for DeepSeek.

We do not claim that the jump is better than surprisal as a single rule. On ProofNet the difference "jump − surprisal" is −2.6 pp for DeepSeek and +5.2 for Goedel; both intervals include zero (Sec. 5). On miniF2F the jump exceeds surprisal in every cell, at temperature 1.0 by 4.4–7.0 pp; on PutnamBench DeepSeek reaches 19.8% vs 17.5%. The main point is that the two features are complementary. They hit different proofs: on ProofNet both hit together in only 8.0% (DeepSeek) and 12.5% (Goedel) of proofs. Over surprisal, the jump adds +7.45 pp [2.31, 12.65] for DeepSeek and +2.84 for Goedel. The comparison with the change in surprisal between steps is in our response to Reviewer wDaH (Q2).

AuthorsOpenReview ↗

Response to Reviewer 22Kj (3/3)

W3. How does the method compare with hidden-state probes (Azaria & Mitchell; Orgad et al.) and with process reward models?

Probes. In the spirit of these works we trained linear probes on the full 4096-dimensional state of the layer and on the increment, but to select a step rather than to assess an answer. They are added to the same baseline as the jump (App. J). For DeepSeek the state probe adds +8.2 pp [2.2, 14.4] on ProofNet and +16.0 [5.2, 26.9] on PutnamBench with frozen settings; the NLL improvement is significant after Holm correction. For Goedel: −7.0 pp (strong baseline, W2b). As a single rule, the jump along a learned direction (the signed projection of the increment) finds the failure in 40% (DeepSeek) and 44% (Goedel) of cases, against 19% and 25% for the norm on the same proofs, and the distance of the state to a learned hyperplane, transferred from ProofNet to miniF2F and PutnamBench, in 38–42% for both models. The part of the increment orthogonal to this direction carries no information about the failure location, yet it determines the norm: the argmax of the raw norm and of this part coincide (22.3% vs 22.1% for DeepSeek, 25.2% vs 25.2% for Goedel). The probe has access to all the information from which the jump is computed: it is trained on the same vector and, in addition, on labels of the first-error location. It should therefore be more accurate.

PRM. We did not use a PRM for Lean. A PRM is trained on step-level labels produced by humans or by an automatic procedure, while in Lean the validity of each step is already checked by the verifier. The jump needs no labels: the whitening is estimated from verified proofs only. The jump can therefore be applied where neither a verifier nor labels are available.

W4. How does the P5 experiment validate the framework?

The P5 experiment does not test the framework: it uses a different model and synthetic tasks, does not measure jumps and does not test the coupling. Exponential decay of success also follows from a constant per-step error model, and at temperature 0.6 the improvement is not significant. In the revision P5 is removed from the abstract, and Sec. 9 states that the experiment shows only the predictive value of length. App. G compares the exponential with more flexible curves, from which it is not distinguishable. It also shows that the hazard of the first invalid formula is not constant across steps: it is markedly higher at the last assigned step.

W5. Do the localization findings generalize beyond 7–8B Lean provers, particularly to informal reasoning?

  • New problems. On 76 new PutnamBench problems, with all settings frozen from ProofNet, the result replicates for DeepSeek: 19.8% vs 7.5%, and +9.3 pp [0.3, 18.4] over a positional predictor. For Goedel (48 attempts) it does not.
  • Informal reasoning. ProcessBench contains informal math solutions in which the first erroneous step is labeled by humans; the jump and projections are computed from the states of a model reading the completed solution. The jump norm is above the uniform level there (20.3% vs 15.8%) but below a positional rule (25.5%). A learned direction works here as well: the projection on a direction learned on ProcessBench out of fold finds the first error in 38–45% of solutions for 7–8B readers (Qwen2.5-7B-Instruct 38.4%, DeepSeek-Prover-V2-7B 40.7%, Goedel-Prover-V2-8B 44.7%) vs 20–23% for the norm; a PRM reaches 52.2%. In the learned localizer, replacing the norm by the projection gives Goedel-Prover-V2-8B +6.6 pp [3.9, 9.2] (Holm-corrected, p < 0.001). Directions learned on Lean do not transfer to ProcessBench (17.9% and 24.4%). Limitation: the reading model did not generate these solutions. New App. L.
  • Scale. This paper does not study models of other sizes.

We hope these changes address the reviewer's concerns and would be glad to clarify any point.

Reviewer_wDaHOpenReview ↗
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2
Informativeness
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Paper summary

This paper investigates residual jumps as markers of reasoning failure in theorem proving with Transformer and Lean. The authors derive conditional localization and overshoot laws, analyze the heavy-tail mechanism and tail-index estimation, and evaluate the relationship between the first Lean-rejected step and the largest residual jump in failed Lean proofs generated by three different models.

Critical strengths
  1. This paper explores an interesting perspective on reasoning failure by investigating the relationship between the first rejected step in Lean proofs and residual jumps in the latent space, which could be meaningful for understanding failure behavior in theorem-proving problems.
Critical weaknesses
  1. The paper titled as reasoning failure in Transformers, while the experiments mainly investigate the first rejected step in Lean proofs, although these two concepts are related, the first Lean-rejected step may not correspond to the first reasoning failure in transformers.
  2. The paper is not well organized, making the evaluation part difficult to follow. While the authors investigate several different aspects, the connections between these experiments and the main claims are not clear, some analyses could be moved to the appendix.
  3. The experiments do not provide sufficient evidence for the proposed extreme-value explanation. Section 5 shows that residual jumps outperform the random baseline, but the residual jump also shows no improvement in online error detection in Section 7, and their predictive value over other step-level features in Section 8 is limited.
Questions for authors
  1. Could the authors clarify how the results support the claim for extreme value? The fixed-threshold coupling assumption and several tail-related predictions are not supported by the experiments
  2. Could the authors clarify how this signal of residual jumps in the latent space is different from changes at the output level in practice? For example, the current surprisal baseline uses the average token surprisal within each step, and residual jumps measure changes between consecutive steps, could changes in step-level surprisal capture a similar signal?
4 comments
AuthorsOpenReview ↗

Response to Reviewer wDaH (1/3)

We thank the reviewer for the careful reading. Below we list the changes in the revision and answer each point (W: weaknesses, Q: questions).

Changes in the revision related to this review

  • The introduction and Sec. 2 state explicitly that we define the first reasoning failure as the first step rejected by Lean, and why (W1).
  • Sec. 3 is presented as a set of conditions that the experiments test. The Kesten recurrence is motivation (W3, Q1).
  • Sec. 8 adds a comparison with a baseline that contains the change in surprisal between adjacent steps; Table 2 adds the argmax of this change (Q2).

W1. The title refers to reasoning failure in Transformers, but the experiments measure the first step rejected by Lean.

We define the first reasoning failure as t∗t^\ast, the first step that Lean rejects when the completed proof is replayed step by step. This choice is deliberate. To study where reasoning breaks, one needs a definition of error that applies to every step and can be checked. A formal proof is reasoning written so that every step can be checked: Lean either accepts the step or rejects it. We do not see a more precise formalization of an error in reasoning: other notions of it have no criterion that can be applied to an individual step without manual annotation. The first rejected step is therefore the strictest available definition of where reasoning stops being valid, and this is why we study Lean proofs.

Revision: the introduction and Sec. 2, after the definition of t∗t^\ast, state that this is our definition of the first reasoning failure and why we chose it.

AuthorsOpenReview ↗

Response to Reviewer wDaH (2/3): W3 and Q1

W3 and Q1. How do the results support the extreme-value framework if the fixed-threshold coupling and the tail predictions are not supported?

The framework states conditions under which the largest step coincides with the first rejection (Theorem 3). The experiments test which of them hold in trained provers.

Localization (P2) holds. The jump argmax identifies t∗t^\ast in 17–25% of cases on miniF2F and 20–29% on ProofNet, 1.5–2.9 times as often as a uniform choice; at temperature 1.0, in 19.1–20.4% against 9.1–10.7%. On 76 new PutnamBench problems, with all settings frozen from ProofNet, DeepSeek reaches 19.8% against 7.5%, which is 9.3 pp [0.3, 18.4] above a positional predictor fitted out of fold.

Not supported: coupling to a common threshold (Sec. 6) and the tail predictions P1, P3, P4.

What discriminates the explanations. Under exact threshold coupling, the rejected step is the maximum of its prefix in 100% of failed proofs. If failure is unrelated to the residual stream, the share equals a positional control (accepted steps at the same positions): 21–35%. We observe 35–43%, 8–17 pp above the control in all five cells. Hence failure is coupled to the jump, but not through an exact threshold. One explanation of such an intermediate share is read-out noise: in the revision we prove (Proposition 5) that under it the share decreases monotonically from 100% to the uniform level. The position of the global maximum leads to the same conclusion: under exact coupling it cannot precede t∗t^\ast, yet it does in 29–51% of failed proofs.

Norm and directions. The jump norm sums over all 4096 directions of the layer. Splitting the increment along a direction learned out of fold shows why the norm is weak: the orthogonal remainder carries no information about the failure location, yet it dominates the norm — the argmax of the raw norm and of the remainder coincide (22.3% vs 22.1% for DeepSeek, 25.2% vs 25.2% for Goedel), while the argmax of the signed component along the direction reaches 39.9% and 43.6%. The estimation error of the whitening is small: a SIMEX correction based on two independent calibrations raises the share only to 37–45%. If the norm is replaced by a linear projection of the increment learned out of fold, the rejected step is the prefix maximum in 51% (DeepSeek) and 49% (Goedel) of proofs, against controls of 23% and 16%; the norm on the same attempts gives 41% and 38% against 33% and 26%. The information about the failure location is therefore concentrated in particular directions, and the norm captures it only partly. With a learned projection of the state, the prefix share reaches 65% and 61%. The directions are learned from the labels (out of fold), so this shows where the information lies, not a label-free rule.

In summary, the data support a weaker statement than the original framework: failure is coupled to the deviation of the trajectory, but not through a common threshold on the norm. The claims of the paper are revised accordingly. See also our response to Reviewer 1ooR (Q1b).

AuthorsOpenReview ↗

Response to Reviewer wDaH (3/3)

W3 (continued). Online detection (Sec. 7) and predictive value (Sec. 8).

Online. The absence of a gain is expected for a relative signal. The retrospective argmax compares steps within one proof, so the proof's own scale cancels. An online detector must decide at the current step without seeing the continuation. It can only use whether the step is a record of its prefix, and this feature is weak: a likelihood ratio of 1.2–1.7 per step. A common threshold does not help, because the scale shifts between benchmarks (Sec. 6).

Learned localizer. Sec. 8 does not test whether the jump is the best localizer, but whether it carries information beyond a strong baseline of position, tactic length and type, surprisal and its change. For DeepSeek it does: +2.8 pp [0.9, 5.0]. For Goedel it does not, but there even the full 4096-dimensional state of the layer does not help: −7.0 pp (for DeepSeek it adds +8.2 [2.2, 14.4]). Goedel's failure location is well predicted by tactic length: the longest-step rule alone reaches 42.7%. A likely reason is selection: 44% of Goedel's failed attempts are truncated at the 8192-token generation budget and do not enter the analysis. Against simpler baselines the gain is positive for both models. Over surprisal alone, the jump raises localization accuracy on ProofNet from 20.5% to 27.9% for DeepSeek (+7.45 pp [2.31, 12.65]) and from 24.1% to 26.9% for Goedel (+2.84 [−3.27, 8.96]); NLL improves for both. For error detection, the jump adds +0.016…+0.106 AUROC to the full baseline (length, surprisal and its change) on miniF2F, with intervals excluding zero in 11 of 12 settings (two models; an error in the completed proof, in the current prefix, in the next 1, 3 or 5 steps, or before the end). On ProofNet the AUROC gain is not significant. The abstract now describes the gain as small and model-dependent.

Q2. How does the residual jump differ in practice from output-level changes? Could the change in step-level surprisal capture a similar signal?

We tested exactly the change in surprisal between adjacent steps.

  1. Jump over surprisal. Over surprisal alone, the jump improves localization for both models (+7.45 and +2.84 pp, see W3). When the change in surprisal between steps is added to surprisal, the jump still improves NLL on ProofNet for both models: +0.042 [0.015, 0.069] (DeepSeek) and +0.083 [0.029, 0.135] (Goedel); accuracy changes by −1.4 and +2.8 pp, with intervals including zero. Over the change in surprisal alone, the jump adds +3.0 pp (DeepSeek) and +9.7 [3.4, 16.0] (Goedel), with NLL gains significant after Holm correction. When position, tactic length and type and the change in surprisal are added to the baseline, the gain persists for DeepSeek (+2.81 pp [0.90, 5.02]) and disappears for Goedel (−1.63 [−4.32, 0.63]), whose failure location is already well predicted by tactic length and position (see W3). On miniF2F the gain over this baseline is +0.2…+2.9 pp in five of six cells, with intervals including zero.
  2. As single rules they pick different steps. On ProofNet a localizer that uses only the change in surprisal (signed and absolute) hits t∗t^\ast in 21.1% (DeepSeek) and 17.7% (Goedel), the jump argmax in 18.5% and 26.6%, a uniform choice in 12.6% and 13.2%. Both rules hit together in only 8.0% and 10.0% of proofs; only the jump in 10.5% and 16.5%, only the surprisal-change localizer in 13.1% and 7.7%. Within a failed proof, the rank correlation of the jump with mean surprisal is 0.13–0.32 for DeepSeek and Goedel and 0.02 for Kimina. On the new PutnamBench problems, DeepSeek's jump hits 19.8%, the surprisal-change localizer 13.8%, a uniform choice 7.5%.
  3. The internal state carries more than the output level. A linear probe on the full state of the layer, added to the baseline with the change in surprisal, gives DeepSeek +8.2 pp [2.2, 14.4] on ProofNet and +16.0 [5.2, 26.9] on PutnamBench with frozen settings.
  4. Detecting a failed proof. When the task is to decide from the completed proof whether it contains a rejection, a detector based on surprisal and its change improves when the jump is added: AUROC +0.13 [0.09, 0.18] for DeepSeek and +0.11 [0.07, 0.16] for Goedel on miniF2F; on ProofNet +0.03 and +0.05, with intervals including zero.

Surprisal measures how unexpected the step's tokens are under the model's output distribution; the jump measures how far its internal state moves. The two are partly related but point to different steps. This is why the paper compares the jump not with surprisal alone, but with a baseline that already contains both surprisal and its change.

Revision: Table 2 adds a localizer that uses only the change in surprisal (signed and absolute). Sec. 8 adds the comparison with a baseline that contains the change in surprisal; comparisons with surprisal-based baselines and the full state are in App. J.

We hope these changes address the reviewer's concerns and would be glad to clarify any point.

Thank you for the detailed response and additional experiments, especially the surprisal change baseline, which helps address my concern about latent space jumps versus output level uncertainty. However, I remain unconvinced by the explanatory role of the extreme-value framework. The new projection experiments also suggest that failure-related information is concentrated in specific directions, while the residual norm is dominated by less informative components. This raises further questions about why the extreme values of the residual norm should be central to the theory. My main concern about the connection between the theory and empirical results remains, therefore I will maintain my original score.

Reviewer_1ooROpenReview ↗
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Paper summary

The paper investigates whether unusually large residual-stream changes indicate reasoning failures. It measures whitened residual increments at formal tactic boundaries and uses the largest increment to localize the first tactic rejected by Lean. A conditional extreme-value framework relates validity to threshold crossings, studies localization under extremal dependence, and gives a Kesten-type stochastic surrogate for heavy tails. Experiments use three provers on miniF2F, with two also evaluated on ProofNet and a frozen temperature replication on miniF2F. Residual maxima outperform a length-adjusted uniform reference, but their incremental value beyond position, tactic type, span length, and surprisal is small and inconsistent. Absolute thresholds transfer poorly, online jump features show no reliable gains, and the proposed heavy-tail diagnostics remain unconfirmed. A separate controlled deduction experiment finds predictive value in assigned reasoning length.

Critical strengths
  1. The formal-proof setting provides a useful and comparatively precise measurement target. Semantic replay identifies an actual rejected tactic, and the paper takes care to separate this from parsing failures, resource failures, and terminal unsolved goals. The evaluation also goes well beyond comparing a residual maximum with a random position. The prefix analysis removes post-rejection text and uses error-free prefixes of matched length to control for endpoint effects. The rejected step still has an 8.2–16.7 percentage-point advantage over that positional reference. This is meaningful evidence of an association between the statistic and local rejection.

  2. The strongest comparisons are thoughtfully designed, and the negative findings are valuable. The learned baseline includes position, relative position, tactic category, span length, and surprisal, with preprocessing and regularization fitted inside nested group cross-validation. Uncertainty resamples whole tasks or exercise groups, and the temperature replication freezes the analysis rules. The authors report weak incremental gains, failed online improvements, distribution shifts, and unconfirmed tail predictions directly. These checks substantially improve the credibility of the empirical study and make its limitations useful to researchers considering similar internal signals.

Critical weaknesses
  1. The connection between the extreme-value theory and the empirical finding remains loose. The validity-coupling hypothesis assumes that the first rejection coincides with crossing a fixed geometric tolerance. This supplies the crucial link from residual geometry to logical validity; the localization theorems then describe its consequences under additional dependence assumptions. At the evaluated thresholds, the diagnostics show substantial departures from both that coupling and extremal independence. The scalar Kesten recurrence is an illustrative model, with no fitted or independently measured correspondence to the provers' dynamics.

    The paper is explicit about these qualifications, and testing an unsuccessful hypothesis can be worthwhile. Still, the evidence does little to identify which part of the framework explains the observed association. Tail separation, rejection overshoots, and the grokking diagnostic provide no affirmative support for the proposed heavy-tail mechanism. The broader extreme-value framework also permits rapidly varying tails, so localization alone does not identify that mechanism. Likewise, an exponential success–length curve also follows from an ordinary constant per-step failure hazard; outperforming a length-independent probability establishes the predictive value of length without establishing a connection to residual extremes. I therefore find the theory more useful as a set of conditional possibilities than as an explanation of the observed failures. A discriminating prediction, or a fitted comparison against plausible alternative processes, would strengthen the central contribution.

  2. The useful information carried by the residual statistic is less convincing than the headline localization rates suggest. In the controlled ProofNet comparison, the cheap-feature baseline already reaches 40.85% and 57.82% exact localization. Adding the jump changes these to 43.51% and 57.13%, respectively. The DeepSeek gain of 2.66 percentage points has a positive interval, but the likelihood improvement is uncertain; Goedel shows no localization gain and worse held-out likelihood. The frozen temperature-1.0 test also does not confirm an incremental gain, and the online comparisons show no reliable benefit from adding jump features. Thus the relative association is more robust than its demonstrated predictive value.

    The evaluation population further limits the conclusion. The learned comparison covers 62% of non-verified DeepSeek attempts and 34% of Goedel attempts on ProofNet. The target is the first rejected tactic among reliably aligned failures, and the full-proof argmax uses text generated after that rejection. The prefix control addresses one concern about this retrospective statistic, but requires the rejection boundary to be known. Moreover, the paper evaluates one principal layer and one whitening configuration, while the archived tail analysis uses a different initial anchor. Some measurement sensitivity is needed before treating the finding as a stable property of reasoning failure rather than of this particular read-out and eligible population.

My assessment is weak rejection. The careful controls and transparent negative results are the strongest parts of the submission. I am less persuaded that the paper has established either an explanatory extreme-value account or a sufficiently robust new localization signal. A more focused demonstration of what the residual statistic contributes beyond the strong baselines would make the empirical finding more compelling.

Questions for authors
  1. Since the localization theorem also permits rapidly varying tails, which empirical result supports the Kesten heavy-tail surrogate specifically? More generally, what observable prediction would distinguish a model coupling validity to residual extremes from ordinary compounding per-step error? Could this distinction be tested on the existing traces?

  2. Could you summarize exclusions by failure type and compare the retained and excluded attempts in length and tactic composition? Table 9 notes that no eligible proof in the learned-comparison population first fails at its last step. What accounts for this pattern, and how does the eligibility mechanism affect the interpretation of the strong positional baseline?

  3. Could you use the archived alternative layers to assess the sensitivity of localization and incremental gains, and separately test the effects of whitening shrinkage and the initial anchor? In particular, do the tail diagnostics retain the same interpretation when recomputed with the formal-entry anchor used for the main localization analysis?

6 comments
AuthorsOpenReview ↗

Response to Reviewer 1ooR (2/5): discriminating prediction

Q1b. What prediction distinguishes coupling to residual extremes from ordinary compounding per-step error? Can it be tested on existing traces?

Yes, and we tested it. Two things do not discriminate between them:

  • the success–length law, since both give exponential decay (see P5 below);
  • the position distribution of the first error alone: in Lean proofs a constant per-step hazard (a truncated geometric law) fits it as well as an empirical positional model.

What discriminates is where the rejection occurs relative to the jumps. Consider the share of failed proofs in which the rejected step is the maximum of its own prefix (Table 3); steps after the rejection do not enter.

  • Exact coupling (Hypothesis 1) predicts 100%: all steps before the first rejection are below the tolerance and the rejected step is above it. Clustering, which lowers localization in Theorem 3, does not affect this share, because it concerns steps after the rejection.
  • Ordinary compounding error, whose per-step hazard does not depend on the model's state, predicts the positional control: the rejected step is a prefix maximum no more often than a step at the same position in proofs that fail later.
  • Coupling with read-out noise. Suppose the jump is a noisy read-out Wt=Zt+σηtW_t = Z_t + \sigma\eta_t of a coupled deviation ZtZ_t, with independent noise. Then the share is non-increasing in σ\sigma, equals 1 at σ=0\sigma = 0, and tends to the uniform level E[1/t∗]E[1/t^\ast] as σ→∞\sigma \to \infty (new Proposition 5, proof in App. A.5). Such noise does not change the limits of Theorem 3 as τ→∞\tau \to \infty; it matters at finite thresholds, as in our data.

The observed share is 35–43%:

  • far below 100%;
  • above the uniform level (16.5–24.8%);
  • 8–17 pp above the positional control (21–35%) in all five cells, including at two other layers, shrinkage 0.01 and 0.5, and a second calibration fold.

Consistently, the jump coefficient in the learned localizer is positive in every outer fold for both provers, given position, tactic length and type, and surprisal.

Exact threshold coupling and state-independent compounding error are therefore both rejected. A second check also excludes exact coupling: under it the global maximum cannot precede t∗t^\ast, yet it does in 29–51% of failed proofs. The data are consistent with a coupling between failure and trajectory deviation that is not an exact threshold on the norm, and much of the gap comes from the norm as a read-out:

  • the jump is a norm over all 4096 directions of one layer. Splitting the increment into its component along a direction learned out of fold and the orthogonal remainder shows that the remainder carries no information about the failure location (adding it to the localizer changes accuracy by at most 1.3 pp and NLL by at most 0.02), yet it dominates the norm: the argmax of the raw norm and of the remainder coincide (22.3% vs 22.1% for DeepSeek, 25.2% vs 25.2% for Goedel), while the argmax of the signed component along the direction reaches 39.9% and 43.6%;
  • with a learned linear projection instead of the norm, the rejected step is the prefix maximum in 51% (DeepSeek) and 49% (Goedel) of proofs for the increment and in 65% and 61% for the state, against controls of 16–28%; the norm on the same attempts gives 41% and 38% against 33% and 26%. Hypothesis 1 is stated for any deviation statistic, and with a better statistic the coupling comes much closer to exact.

The estimation error of the whitening, measured from two disjoint calibration sets, is small: correcting for it (SIMEX) raises the share only to 37–45%. The directions are learned from first-rejection labels (out of fold), so these results show where the information lies rather than a label-free rule. Under such noise a hard threshold and a graded coupling are observationally equivalent, and we do not claim that the mechanism is a threshold.

Revision: new paragraph "Discriminating explanations" in Sec. 6; a remark on read-out noise in Sec. 3 with Proposition 5.

AuthorsOpenReview ↗

Response to Reviewer 1ooR (3/5): Q2

Q2. Exclusions by failure type, the absent last-step failures, and the positional baseline.

Exclusions. A whole-proof re-audit of ProofNet (T = 0.6, 840 attempts per prover) found that some attempts previously counted as non-verified had completed a verified proof but were flagged as truncated. With this corrected, there are 685 (DeepSeek) and 673 (Goedel) non-verified attempts. The learned-comparison population and its labels are unchanged.

Non-verified attemptsDeepSeekGoedel
Included (reproducible first rejection)452259
Generation truncated at the token budget55294
Ambiguous localization5048
Resource limit / internal error5416
Parse error3832
All tactics accepted, goals remain2214
Context mismatch in replay97
Incomplete token boundaries43
sorry / invalid10
Total685673

Coverage is therefore 66.0% (DeepSeek) and 38.5% (Goedel), not 62.0% and 34.0% as stated in the paper (older denominator). Goedel writes long reasoning, and 294 of its 673 non-verified attempts (44%, vs 8% for DeepSeek) hit the 8192-token generation budget. For these attempts the first error is undefined, because the proof is incomplete. Included attempts have a median of 3848 (DeepSeek) and 3346 (Goedel) generated tokens and 14 steps. Excluded parse and resource failures are longer (median 4182–5637 tokens); ambiguous-localization attempts have similar token length but more steps (median 18 and 25). Tactic composition can be compared only where steps can be extracted (ambiguous localization, unsolved goals), and there it is close to the included attempts: exact is 19–25% of steps vs 23–29%, have 13–17% vs 14–15%. Truncated, parse and resource failures have no reliable step segmentation.

Last step. No rule in the pipeline excludes t∗=Lt^\ast = L; the pattern is a property of the eligible population. The error typically occurs while an auxiliary fact is being built (e.g., inside have h_main : … := by …). A closing step such as exact h_main is still generated afterwards and accepted, because Lean continues after an error. After the first rejection, 1–82 further steps remain for DeepSeek (median 7) and 1–161 for Goedel (median 6). In 442 of 452 (DeepSeek) and 252 of 259 (Goedel) eligible failures the last step is an exact tactic. The last-step rejections produced by an earlier, coarser replay all belong to excluded truncated or sorry answers.

Positional baseline. This structure makes position and span very informative:

  • the last step is never the target;
  • step 1 is the target in 22% (DeepSeek) and 32% (Goedel) of ProofNet failures;
  • tactic length predicts the rejected step well.
Single rule (exact, %, equal group weights)DeepSeekGoedel
Uniform12.613.2
Always step 119.828.7
Jump argmax18.526.6
Surprisal argmax21.421.3
Tactic length only (learned localizer)32.442.7

Selection likely acts most strongly on Goedel. Among its attempts that fit in the budget, position and tactic length predict the error better than for DeepSeek (table above; learned baseline 57.8% vs 40.9%). This plausibly explains why the jump adds little for Goedel. We cannot test it directly, because the first error is undefined for truncated attempts. We therefore measure the jump's added value against a learned baseline that already contains position, relative position, first/last-step indicators, tactic length and type, and surprisal (Table 2, Sec. 8).

Revision: Appendix B (exclusion table, retained vs excluded comparison); coverage corrected throughout; rows for the first-step rule and a tactic-length-only localizer added to Table 2.

AuthorsOpenReview ↗

Response to Reviewer 1ooR (4/5): Q3; P5

Q3. Layers, whitening shrinkage and anchor; tails with the formal-entry anchor.

We changed one factor at a time on the same populations:

  • the quarter and three-quarter layers (6/21 for DeepSeek, 8/26 for Goedel and Kimina);
  • shrinkage 0.01, 0.5 and 1 (isotropic) instead of 0.1;
  • a diagonal covariance, and no whitening;
  • a second calibration fold;
  • the prompt-end anchor, with the main transform and with one recalibrated for that anchor.

Results:

  • Full-proof argmax. On ProofNet every variant is above the uniform reference: 20.0–28.7% vs 13.3% (DeepSeek) and 25.6–31.3% vs 14.2% (Goedel). On miniF2F the variants with full whitening are within 3.5 pp of the main values; with a diagonal covariance or no whitening Goedel drops from 25.5% to about 5%.
  • Prefix contrast with the positional control. With full whitening it is positive in all five cells, and every interval excludes zero. Without whitening, or with the prompt-end anchor under the main transform, the first increment dominates the prefix maximum and the hit rate collapses (Goedel on ProofNet: 41.6% → 7.9%). On ProofNet the contrast is still positive; on miniF2F it is lost for Goedel (−1.4 pp without whitening). Whitening matters mainly because it rescales the first increment.
  • Added value of the jump (ProofNet; layers, shrinkage, no whitening, anchor). DeepSeek gains +1.3 to +3.4 pp, and the interval excludes zero in every variant except the prompt-end anchor under the main transform. Goedel changes by −1.6 to −0.2 pp, and every interval includes zero.

Tails. The threshold diagnostics (Tables 4 and 14 of the revision, Fig. 1) already used the formal-entry anchor. Only the archived tail-index table (Table 20 of the submission) used the prompt-end anchor, and we recomputed it with the main anchor and the current segmentation (miniF2F, T=0.6T = 0.6; Table 21 of the revision). Failed and verified proofs have similar signed estimates with wide intervals: the moment estimator for Goedel is 0.14 [−0.15, 0.21] vs 0.15 [−0.33, 0.24], and for failed DeepSeek proofs it is −0.30 [−3.31, 0.04]. At the rejected step the tail holds only 21–30 exceedances, too few for intervals. The held-out family comparison in Q1a uses the same anchor. The interpretation does not change: we find no evidence of a heavy upper tail tied to failure.

Revision: new Appendix I with all read-out variants; new Table 21.

On the success–length law (P5). This experiment shows only that assigned length predicts success; it does not test the framework. Revision: P5 is removed from the abstract, and Sec. 9 says this directly. The alternative curves and the first-error hazard analysis are in App. G.

Comments on the paper

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AuthorsOpenReview ↗

Response to Reviewer 1ooR (1/5): summary of changes and Q1a (Kesten surrogate)

We thank the reviewer for the careful review and the concrete questions. The main changes relevant to this review (highlighted in the revised PDF):

  • The extreme-value framework is presented as a set of conditions that the experiments test. The Kesten recurrence is presented as motivation, and P5 is removed from the abstract.
  • A new paragraph in Sec. 6 uses the existing prefix analysis as the discriminating test the reviewer asks for, together with a noisy read-out version of Hypothesis 1 (new Proposition 5).
  • Appendix B reports exclusions by failure type and corrects the coverage figures.
  • New Appendices I and J report all read-out variants and what hidden-state features add to the localizer.

Q1a. Which empirical result supports the Kesten surrogate specifically?

The Kesten recurrence is a motivating model: it shows how occasional expansive updates produce power-law tails. It gave three testable predictions:

  • tail separation between failed and verified proofs (P1);
  • a Pareto overshoot at the first rejection (P3);
  • a tail-index change at grokking (P4).

None was confirmed (Sec. 9).

We did not fit the recurrence directly, because the decomposition Xt=Xt⋆+EtX_t = X^\star_t + E_t is not identified from the observed states. The reference trajectory is not measured, so estimating the multipliers ata_t requires choosing a proxy for it, and both a good and a poor fit would mostly reflect that choice. We therefore tested its observable consequences; Sec. 3.3 already introduces the recurrence as illustrative.

The tails themselves do not single out this mechanism either:

  • Where shape estimates are positive (Goedel, about 0.17–0.26), they are the same for verified and failed proofs.
  • For DeepSeek and Kimina, the moment and GPD estimates are negative in several subsets (Table 21 of the revision).
  • In a new held-out comparison, Pareto has the worst held-out NLL among Pareto, exponential, lognormal and GPD: 3.502 vs 3.487–3.492 at q = 0.90 and 3.378 vs 3.367–3.370 at q = 0.95. The differences are small, so Pareto has no advantage, but no family is established as best. The moment and GPD shape estimates are negative in all five folds (−0.04 to −0.24). This cell (ProofNet, DeepSeek) is the only one that meets our preset minimum of 80 training exceedances in 20 groups.

Localization does not identify the mechanism: Theorem 3(ii) also holds under rapid variation.

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

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