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Under review as a conference paper at ICLR 2027

Spike-Triggered Adaptive Reasoning Steering to Mitigate Cognitive Inertia in Large Reasoning Model

Abstract

While Large Reasoning Models (LRMs) have achieved remarkable performance by scaling test-time compute, they frequently suffer from cognitive inertia, a failure pattern manifesting in two distinct modes: 1) overthinking, where models spiral into redundant verification loops long after a solution is reached, and 2) reasoning rigidity, where models stubbornly adhere to incorrect parametric priors even when they contradict explicit task constraints. Previous inference-time methods designed to mitigate these reasoning failures primarily focus on overthinking via suppressive early-exit strategies. However, by relying on surface-level textual heuristics that serve as unreliable proxies for reasoning quality, these methods often prematurely terminate potentially recoverable reasoning paths. Furthermore, they remain fundamentally blind to reasoning rigidity, as they lack any mechanism to redirect a model that has confidently committed to an incorrect trajectory. To address these limitations, we propose STARS (Spike-Triggered Adaptive Reasoning Steering), a training-free framework designed to actively correct reasoning trajectories by monitoring internal latent dynamics. STARS identifies cognitive pivots—critical moments of reasoning transition—by detecting distinct distance spikes in the hidden states. Upon detection, the framework employs geometric trajectory analysis to diagnose the structural nature of the transition and injects state-aware language cues to steer the model on-the-fly. Our experiments across diverse benchmarks show that STARS consistently improves accuracy—by up to 6.6% on AIME25 and 6.5% on ConditionedMath—while consistently lowering end-to-end latency relative to existing baselines. By resolving internal conflicts rather than merely truncating output, STARS ensures a superior accuracy-compute trade-off, effectively rescuing failed reasoning paths.

Primary area:
foundation or frontier models, including LLMs
Keywords:
cognitive inertia, large reasoning model, adaptive reasoning steering

Reviews

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1234this paper, Bottom 10%
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_L7AQOpenReview ↗
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Paper summary

The paper presents STARS, a training-free method for steering large reasoning models during decoding. The authors group overthinking and rigid adherence to prior assumptions under the term cognitive inertia. STARS monitors the size of the hidden-state change between consecutive tokens at a selected layer. When a spike occurs, it checks whether the update direction reverses and whether the current state resembles states recorded at earlier reversals, and on that basis appends one of two short sentences to the generation, either prompting the model to verify its new direction or telling it that its reasoning is looping. On DeepSeek-R1-Distill-Qwen 1.5B and 7B and Qwen3-4B-Thinking, across several mathematics benchmarks, PuzzleTrivial and GPQA-Diamond, STARS improves average accuracy by roughly two to three points over standard decoding and runs faster than the DEER and ConCISE baselines.

Critical strengths
  1. The timing experiments are well conceived. The same sentence is inserted at occurrences of the token wait, at fixed positions, or whenever an LLM judge flags a problem, and spike-triggered insertion performs best in most configurations. This is precisely the control needed to show that the benefit does not come from the wording of the suffix alone.
  2. The method is inexpensive and straightforward to deploy. The trigger relies on hidden states that are already computed, requires no additional forward pass, and yields lower latency than DEER, which makes it easy to adopt for open-weight models.
Critical weaknesses
  1. The evidence is modest relative to the strength of the claims. After filtering, ConditionedMath contains 52 problems, PuzzleTrivial 33 and each AIME year 30. The 6.5-point gain on ConditionedMath therefore corresponds to three or four problems and the 6.7-point gain on AIME25 to two, and many differences fall within one standard deviation, with essentially no change on GPQA-Diamond. Although the thresholds are described as calibrated on held-out data, Appendix E.4 selects the final values by inspecting accuracy on ConditionedMath and AIME24, both of which are evaluation sets, and the chosen pair happens to be optimal on both. The calibration pool, moreover, consists of the filtered-out portion of the same benchmarks, including near-duplicates of test items. The prefix-continuation analysis in Table 4 raises a further concern. From the intervention points, the base model without any suffix solves most of the problems on average, which suggests that much of the recovery comes from resampling at that point rather than from the suffix, and treating the remaining nine to sixteen percent as causal evidence overstates what the analysis shows.
  2. Important comparisons are missing, and the mechanistic interpretation is not fully convincing. The prompt-hinting baseline in Appendix I reaches 67.7 on ConditionedMath with Qwen3-4B, well above the 58.9 obtained by STARS, yet it is absent from the main results. Closely related latent-steering methods such as SEAL and manifold steering, as well as NoWait, are discussed but not evaluated, and the two baselines that are included are early-exit methods designed for efficiency rather than accuracy. All models have at most seven billion parameters, so it remains unclear whether cognitive inertia, and the corresponding gains, persist in larger reasoning models. As for the mechanism, the layer selected for Qwen3-4B is layer 2, which is very shallow and largely lexical, and the examples in Figure 3 place spikes directly on discourse tokens such as Wait and Oh, nice. The detector may therefore be tracking particular tokens rather than internal reasoning transitions. The notion of cognitive inertia itself adds little beyond a new label for overthinking and rigidity.
Questions for authors
  1. Could the thresholds be selected without reference to any evaluation benchmark, and could the results be accompanied by a paired significance test over problems? I would like to know which gains survive both changes.
  2. On the problems in Table 4, how does STARS compare with suffix-free continuation from the same intervention points? A small difference would indicate that the suffix contributes little.
  3. How often do spikes coincide with specific tokens such as Wait or line breaks? A control that triggers on those tokens at the same frequency as STARS would help separate the two explanations.
  4. Why is prompt hinting excluded from the main table, and how does STARS compare with SEAL and NoWait?
  5. Do the gains hold for a reasoning model in the 30B range?
2 comments

We thank the reviewer for the thoughtful feedback and for recognizing the value of our timing controls and deployment efficiency. The revised PDF reflects all changes below.

W1-1 & Q1. Problem-level significance

Five-run standard deviations measure seed variability rather than uncertainty over problems. We therefore compute paired per-problem accuracy differences averaged over trials, with problem-level bootstrap CIs and paired permutation tests across five target benchmarks.

ModelModel–problem pairsGain (pp)95% CIppWins / losses
DeepSeek-1.5B222+3.60[+0.45, +6.76]0.0368 / 46
DeepSeek-7B222+3.69[+1.26, +6.13]0.00457 / 31
Qwen3-4B222+1.26[−0.90, +3.42]0.3032 / 21
All models666+2.85[+1.35, +4.38]<0.001< 0.001157 / 98

Table A: Problem-level paired comparison with vanilla across MathPerturb, ConditionedMath, PuzzleTrivial, AIME24, and AIME25.

The pooled gain and the gains for both DeepSeek models are statistically significant. Qwen3-4B also shows a positive gain (+1.26 pp), although it does not reach statistical significance, with identical outcomes on 76% of problems. MATH500 and GPQA-Diamond assess generalization rather than targeted improvements (Section 4.2).

W1-2 & Q1. Threshold selection and calibration pool

The default thresholds were frozen before the results in Table 10 of the original submission were examined. Table 10 (now Table 14 in the revised manuscript) was a subsequent sensitivity analysis, not a selection step (clarified in Appendix E.4). Although the calibration pool includes near-duplicates, threshold selection relies exclusively on label-free statistics (SPR, spike density, and cosine and recurrence distributions), never ground-truth answers or evaluation accuracy.

Calibration uses only excluded ConditionedMath and MathPerturb instances. The frozen configuration transfers unchanged to AIME24/25, PuzzleTrivial, and GPQA-Diamond, none of which appears in calibration, with some of the largest gains on AIME25 and PuzzleTrivial. Table A establishes the pooled significance of the gains without accuracy-based threshold selection.

W1-3 & Q2. Outcome-independent effect of the suffix

Table 4 in the original submission examined whether reaching the intervention point alone accounts for STARS's recoveries. To directly quantify the suffix effect, we conducted an outcome-independent paired comparison. Since STARS follows vanilla until its first intervention, we compare STARS and suffix-free continuations from every first-intervention prefix, regardless of final outcome, with identical prefixes and budgets.

CM 1.5BCM 7BCM 4BAIME25 1.5BAIME25 7BAIME25 4B
Prefixes229192226137128146
Suffix-free38.4340.6253.1018.9831.2573.29
STARS51.5351.0457.5223.3637.5073.29

Table B: Paired continuation accuracy (%). CM denotes ConditionedMath.

Across 1,058 prefixes, STARS improves accuracy by 6.99 pp (95% problem-level bootstrap CI [+4.58, +9.46]), with 69 wins versus 23 losses (sign test, p<10−5p < 10^{-5}). STARS improves five settings and ties in one.

Restricting to STARS successes as in Table 4 of the original submission yields suffix-free accuracies of 63.6%, 69.4%, and 86.9% on ConditionedMath, consistent with the original results. Including all eligible prefixes demonstrates the benefit of suffix-based steering beyond resampling. We have replaced Table 4 in the revised manuscript with this analysis.

W2-1 & Q4. Prompt hinting

Prompt hinting outperforms STARS in only one of the nine settings in Table 13 of the original submission (now Table 23 in the revised manuscript), underperforming in the other eight and on average. It also falls below vanilla on AIME24 for all three models. The hint explicitly signals an unusual condition, a defining property of ConditionedMath, thereby providing benchmark-specific information at the input, whereas STARS responds dynamically as reasoning unfolds. We therefore report prompt hinting separately in Appendix I.

W2-2 & Q4. Reflection suppression

SEAL and Manifold Steering suppress reflection through direct hidden-state modification, whereas STARS monitors hidden states and redirects reasoning via language cues. As a representative reflection-suppression baseline, we added NoWait (Appendix J).

MethodCM 1.5BCM 7BCM 4BAIME24 1.5BAIME24 7BAIME24 4BAIME25 1.5BAIME25 7BAIME25 4BAvg
Vanilla46.54 ± 4.2848.08 ± 5.0156.54 ± 1.5428.00 ± 4.5253.33 ± 2.1176.00 ± 3.8922.67 ± 3.2739.33 ± 1.3370.67 ± 5.3349.02
NoWait43.08 ± 5.7846.54 ± 4.2856.15 ± 0.7726.00 ± 2.4944.00 ± 6.4670.00 ± 2.1118.67 ± 5.4229.33 ± 4.4272.67 ± 2.4945.16
STARS53.08 ± 2.6154.62 ± 1.9658.85 ± 3.1228.00 ± 4.0055.33 ± 3.4076.67 ± 2.9827.33 ± 3.8943.33 ± 2.9877.33 ± 3.8952.73

Table C: Accuracy (%, mean ± std over five trials). NoWait suppresses the reflection keywords of Wang et al. (2025) by setting their logits to −∞-\infty.

NoWait shortens generation to 8,958 tokens (vanilla: 14,987; STARS: 14,104) but falls below vanilla in eight of nine settings. STARS is best or tied in all nine settings, supporting selective redirection over uniform reflection suppression.

W2-3 & Q5. Model scale

Evaluating a 30B-scale model with 32K-token generation and per-token hidden-state access exceeds our single 48GB GPU capacity without quantization, which would alter the monitored states. Reasoning rigidity has been documented in Qwen3-32B (Jang et al., 2025), and our gains persist across 1.5B–7B models. STARS requires only hidden-state access, making it applicable in principle to larger open-weight models.

W2-4 & Q3. Token tracking

Across the main experiments, only 0.73%, 2.04%, and 0.00% of spikes coincide with discourse tokens (e.g., Wait, Oh, Hmm, But, Alternatively) for DeepSeek-1.5B, DeepSeek-7B, and Qwen3-4B, respectively, below their prevalence in generated text (2.6–2.8%). At most 0.10% of paragraph line-break positions coincide with a spike. In Figure 3, the highlighted tokens are "style" and "numer"; "Wait" and "Oh, nice" occur in the preceding context.

Table 6 already provides the suggested Token-Triggered control, which injects the same suffix at "wait" tokens, with its intervention limit matched to the average flip frequency. STARS outperforms this control in all six settings, supporting latent detection beyond these surface cues. We have included the token overlap analysis in Appendix F.2 of the revised manuscript.

W2-5. Cognitive inertia

The unification is operational: both failure modes involve self-reinforcing trajectories, enabling a common detector but requiring different corrective actions. Flip-only and STARS share the same intervention trigger, differing only in the suffix applied at recurrent flips. STARS consistently outperforms Flip-only (Tables 5 and 12 in the original submission, now Tables 5 and 20 in the revised manuscript), supporting the value of this distinction.

Reviewer_FxMaOpenReview ↗
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2
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3
Informativeness
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Paper summary

STARS is a training-free inference controller that uses hidden-state dynamics to decide when and how to steer a reasoning model. It detects unusually large normalized displacements, diagnoses directional flips and recurrence, and appends either a shifting cue or a loop-breaking cue through the ordinary decoding context. The model weights remain fixed. Experiments on three backbones and seven benchmarks, using five runs, report average accuracy improvements and lower inference cost in the tested configuration. Ablations examine diagnostic components, intervention content, timing, and static prompting, while additional analyses relate the detected events to failure and recovery.

Critical strengths
  1. The method uses sparse hidden-state events to choose both the timing and type of intervention. Separating spike detection from diagnosis is sensible, and suffix insertion preserves cached decoding without training or external verification.

  2. The empirical coverage is meaningful: three backbones, seven benchmarks, five runs, component and content ablations, fixed-position and capped-token controls, static prompting, and latency distributions. The mean gains of about 3.33, 2.86, and 1.81 points warrant attention.

Critical weaknesses
  1. The calibration/test separation is unclear. Section 4.1 says thresholds are chosen on disjoint held-out data, but page 20 selects the default configuration by its observed balance on ConditionedMath and AIME24; the calibration filtering and near-duplicate rules also lack separation details. The selection chronology, sample IDs, and deduplication rules are needed to interpret the cross-task results.

  2. The mechanism analyses are outcome-selected. Table 4 selects STARS-successful cases and samples continuations, so the 9–16% never-solved controls do not establish causal recovery; even a zero-effect intervention can produce such controls. Failure-type recovery comparisons and flip-count correlations also need controls for difficulty, trajectory length, and repeated seeds. An outcome-independent paired branching comparison with matched budgets, or narrower causal claims, is needed.

Questions for authors
  1. Were the default thresholds frozen before the evaluation grid in Table 10 was examined? Please provide the development and evaluation IDs, filtering and near-duplicate rules, and the order of configuration selection and sensitivity analysis.

  2. What is the paired benefit of the suffixes and their timing when eligible prefixes are selected independently of STARS's final success, with matched budgets and problem-clustered uncertainty? If such evidence is not part of the current study, can the causal and specificity claims be narrowed?

3 comments

We thank the reviewer for the constructive feedback. The revised PDF reflects all changes below.

W1 & Q1. Threshold selection and calibration set

The default thresholds were frozen before the results in Table 10 of the original submission were examined. We selected the layer and kk by SPR on held-out data (Appendix E.1), then fixed τflip=0.2\tau_{\mathrm{flip}}=0.2 and τrecur=0.9\tau_{\mathrm{recur}}=0.9 from the held-out cosine and recurrence distributions (Appendix E.4). Table 10 (now Table 14 in the revised manuscript) was a subsequent sensitivity analysis on ConditionedMath and AIME24, not a selection step.

Appendix D.1 now specifies our exclusions: near-duplicates (same structure, different numerical values) and undefined-answer problems in ConditionedMath; MATH training-split derivatives and undefined or non-unique answers in MathPerturb.

Calibration uses these excluded instances and only label-free statistics, never answers or accuracy. The frozen configuration transfers unchanged to AIME24/25, PuzzleTrivial, and GPQA-Diamond, none of which appears in calibration. We will release the development and evaluation IDs with the code.

W2-1 & Q2. Outcome-independent effect of the suffix (Table 4)

Table 4 in the original submission examined whether reaching the intervention point alone accounts for STARS's recoveries, rather than estimating the average suffix effect. We now assess this effect using the suggested outcome-independent paired comparison.

For every run with an intervention, regardless of outcome, we compare the actual STARS continuation with one suffix-free continuation from the same first-intervention prefix with equal budgets. STARS follows vanilla until this point, making prefix selection independent of the outcome.

CM 1.5BCM 7BCM 4BAIME25 1.5BAIME25 7BAIME25 4B
Prefixes229192226137128146
Suffix-free38.4340.6253.1018.9831.2573.29
STARS51.5351.0457.5223.3637.5073.29

Table A: Paired continuation accuracy (%). CM denotes ConditionedMath.

Across 1,058 prefixes, STARS improves accuracy by 6.99 pp (95% problem-level bootstrap CI [+4.58, +9.46]), with 69 wins versus 23 losses (sign test, p<10−5p < 10^{-5}). STARS improves five settings and ties in one, demonstrating benefits beyond resampling. We have replaced Table 4 in the revised manuscript with this analysis.

W2-2 & Q2. Inertia failures beyond resampling (Table 3)

To account for inherent recoverability, we compare STARS with resampling: the rate at which the other four vanilla trials solve the same failed problem.

Failure typeFailures (problems)STARS fix (%)Resampling fix (%)Difference (pp)Mean tokens
Inertia298 (162)37.931.0+6.9 [+1.6, +12.0]13,351
Plain579 (209)24.218.9+5.3 [+1.6, +8.9]13,517

Table B: Recovery across ConditionedMath, MathPerturb, PuzzleTrivial, and all three models. Brackets indicate 95% problem-level bootstrap CIs.

STARS exceeds resampling for both failure types, whose mean trace lengths are nearly identical. We have revised the interpretation of Table 3 accordingly. Gains concentrate on inertia-prone benchmarks, with comparable performance on GPQA-Diamond (Section 4.2).

W2-3 & Q2. Flip counts (Appendix G)

We control for length using flips per 1k tokens and for difficulty and repeated seeds through within-problem comparisons with problem-level Wilcoxon tests. Length-normalized flip counts are higher in incorrect runs for DeepSeek-7B, lower for Qwen3-4B, and similar for DeepSeek-1.5B. Within problems, incorrect runs exhibit more flips for all three models, significantly so only for Qwen3-4B. We now present Appendix G as a descriptive observation and have revised Appendix E.4 accordingly.

W2-4 & Q2. Random-timing control

Beyond the intervention timing controls in Table 6 of the original submission, each random-timing run matches the STARS problem, trial, suffix sequence, and target intervention count, sampling positions from empirical STARS position and gap distributions.

MethodCM 1.5BCM 7BCM 4BAIME25 1.5BAIME25 7BAIME25 4BAvg
Vanilla46.54 ± 4.2848.08 ± 5.0156.54 ± 1.5422.67 ± 3.2739.33 ± 1.3370.67 ± 5.3347.30
Random timing49.62 ± 2.2444.62 ± 4.4555.38 ± 2.2420.00 ± 2.9842.00 ± 7.7772.67 ± 2.4947.38
STARS53.08 ± 2.6154.62 ± 1.9658.85 ± 3.1227.33 ± 3.8943.33 ± 2.9877.33 ± 3.8952.42

Table C: Timing control (accuracy %, mean ± std over five trials).

STARS beats random timing in all six settings; random timing yields inconsistent gains over vanilla. Random timing averages 1.60 vs. STARS's 1.83 injections, as some runs end before sampled positions. Tables A and C support suffix use and spike-aligned timing.

Reviewer_FxMaOpenReview ↗

Follow-up on the Authors' Response

Thank you for your response!

Regarding Q1, we acknowledge your clarification that the default thresholds were frozen before the evaluation experiments.

Regarding Q2, we appreciate the extensive paired continuation experiments across 1,058 prefixes, which address our concerns about the effectiveness of the suffix interventions. We sincerely appreciate the authors' efforts to provide this additional evidence.

However, we believe the paper still falls somewhat short of a score of 3. Our main concern is that all three models evaluated in the paper are based on Qwen backbones, which raises questions about whether the proposed method is model-specific and whether it can generalize to models from different model families.

We would therefore be inclined to raise our score from 2 to 2.5, if such a rating were available. However, ICLR does not offer a 2.5 rating.

We also apologize that our response came relatively late, potentially leaving the authors insufficient time to conduct additional experiments with models beyond the Qwen family. We sincerely regret this.

We thank the reviewer for their thoughtful follow-up and for acknowledging that our calibration clarification and outcome-independent paired comparisons address the earlier concerns. We also appreciate the concern about backbone diversity.

Additional cross-family evaluation

To directly address this concern, we conducted additional experiments with DeepSeek-R1-Distill-Llama-8B, which uses a Llama backbone rather than the Qwen backbones of our three original models. We evaluated ConditionedMath (52 problems), AIME24 (30), and AIME25 (30) over five independent trials, comparing STARS with vanilla decoding, DEER, and ConCISE.

MethodConditionedMathAIME24AIME25
Vanilla39.62 ± 3.5740.00 ± 4.7127.33 ± 5.33
DEER38.46 ± 6.8838.67 ± 4.5224.00 ± 4.90
ConCISE53.46 ± 1.4446.67 ± 2.9829.33 ± 5.33
STARS56.15 ± 3.0853.33 ± 3.6538.67 ± 4.99

Table D: Accuracy (%) on DeepSeek-R1-Distill-Llama-8B, mean ± std over five trials.

STARS improves over vanilla on all three benchmarks, with statistically significant paired problem-level gains: +16.54 pp on ConditionedMath (95% CI [+9.23, +24.23], p<0.001p < 0.001), +13.33 pp on AIME24 ([+3.33, +24.00], p=0.022p = 0.022), and +11.33 pp on AIME25 ([+6.00, +18.00], p<0.001p < 0.001).

Pooling the 112 problems, we obtain:

ComparisonSTARS gain (pp)95% CIpp
vs Vanilla+14.29[+9.82, +18.93]<0.001< 0.001
vs DEER+16.07[+11.25, +21.07]<0.001< 0.001
vs ConCISE+5.54[+1.43, +9.64]0.010

Table E: Paired gains pooled across ConditionedMath, AIME24, and AIME25 (112 problems).

The improvement over ConCISE is also significant on AIME25 (+9.33 pp, 95% CI [+4.00, +14.67], p=0.004p = 0.004). These results provide direct evidence that STARS's benefits are not limited to Qwen backbones. While a single additional family does not establish universal generalization, the consistently positive gains on a Llama-based reasoning model substantially strengthen the cross-family evidence.

We appreciate the reviewer highlighting this limitation and hope that this additional evaluation addresses the remaining concern. We would be grateful if the reviewer could take these new results into account when reassessing the paper.

Reviewer_kfYGOpenReview ↗
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Informativeness
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Paper summary

STARS is a training-free inference controller that monitors normalized hidden-state displacement at a calibrated layer. Spikes nominate intervention points; directional reversals and recurrence against a memory bank choose between shifting and loop-breaking natural-language suffixes. Tests on three reasoning models and seven benchmarks report improved average accuracy and lower mean latency. The paper also studies intervention timing, component removal, threshold robustness, and qualitative interpretations of latent spikes.

Critical strengths
  1. The controller is concrete and the ablations support more than a generic prompting effect. Tables 5–6 compare diagnostic components and alternate intervention timing; Appendix E.3 studies suffix components and swapping. The paper also tests a text verifier and static prompt hinting. These controls make a substantive case that trigger and cue selection matter, rather than merely inserting any instruction.
  2. The evaluation balances accuracy with actual decoding costs. Table 1 reports five-run variability across multiple models and tasks. Table 2 and Appendix J distinguish output tokens from internally generated tokens and report latency, including tails. Gains on ConditionedMath and AIME25, alongside largely preserved performance elsewhere, make the method potentially useful without retraining.
Critical weaknesses
  1. The causal and diagnostic claims exceed what the analyses identify. Section 4.3/Table 4 conditions its continuation analysis on STARS success cases and compares three no-suffix continuations. This post-treatment selection cannot estimate the average causal benefit of the suffix at intervention points. A model with nonzero chance of solving a problem can also fail all three continuations. Further, “inertia failures” in Table 3 are defined by having reached and abandoned the correct answer, which already selects comparatively recoverable failures; higher repair rates do not alone establish an inertia-specific mechanism. The main accuracy and ablation results remain valid evidence of an effective heuristic, but claims of causal diagnosis or guaranteed high-plasticity windows need stronger controls (p. 8).
  2. The mechanism and effect uncertainty need validation beyond the selected annotation and run averages. Appendix F.1 starts with the highest-spike-density samples; the scaled LLM annotation reuses the manual examples as exemplars and is explicitly descriptive. It does not establish population-level diagnostic sensitivity/specificity of the geometric rule. Moreover, the prominent AIME gains are measured on small question sets, and five-run standard deviations do not directly quantify uncertainty over distinct problems. The appendix's near-matched fixed/token injection counts are useful, but a prospective prefix-matched random-timing control would more cleanly isolate the claimed importance of spike alignment (Table 1; Appendices F.1 and H.2).
  3. With the suffix held fixed, the latent trigger is not consistently better than the surface-text verifier, so the timing comparison does not isolate latent detection. App. D.3 describes the verifier as "designed to isolate the trigger while holding the intervention fixed" (L. 842), but the verifier always appends the shifting suffix (L. 848), whereas STARS chooses between two suffixes. The like-for-like comparator is therefore Flip-only, which "injects the shifting suffix at every detected directional flip" (L. 1240). Against Flip-only, the N = 512 verifier scores higher in 4 of the 6 model–benchmark cells of Table 6: Qwen3-4B ConditionedMath (59.62 vs. 55.77) and all three AIME25 cells (27.33 vs. 23.33, 40.00 vs. 38.67, 72.67 vs. 71.33). It scores lower only on the two DeepSeek ConditionedMath cells. The N = 1024 verifier is higher in 2 cells and ties in 1. STARS's advantage over the verifier thus coincides with the recurrence/loop-breaker branch, which the verifier lacks, rather than with latent timing alone. Sec. 4.4 also says the verifier fires "far more often than STARS does" (L. 458–459), whereas App. D.3 only says it inspects the trajectory more often (L. 851–852). The number of verifier interventions is not reported. Finally, the problem set behind the verifier's 518.01 s latency is not stated (L. 853–854), while STARS's 251.34 s is the Table 15 average over a 100-problem mixed subset (L. 1359–1360). The "more than twice" comparison may therefore not be like-for-like. Since "when to intervene matters more than what to inject" is one of the paper's two headline findings (L. 484–485), this comparison needs matched suffix logic and matched intervention counts.
  4. The state-aware cue selection behind the two-mode framing has little direct support, and the evidence on what to inject points in different directions.

Others:

  • L. 31, 97, 349, 358: the gains "by up to 6.6% on AIME25 and 6.5% on ConditionedMath" and "6.54%" are absolute percentage-point differences, not relative improvements; please write "pp". The AIME25 gain is 77.33 − 70.67 = 6.67 pp, which rounds to 6.7.
  • Table 1 (L. 342): the Qwen3-4B STARS average (77.64) does not equal the mean of its seven entries (77.74). The reported average would be consistent with an AIME24 entry of 76.67, and the row's AIME24 and AIME25 entries are identical (77.33±3.89, repeated in Table 13, L. 1313). Other entries also need checking. DeepSeek-7B STARS on PuzzleTrivial (44.23, L. 337) is not attainable as a five-run mean on 33 problems (43.64 or 44.24). Table 10's 54.48 and 54.32 (L. 1060, 1063) are not attainable with 52 problems × 5 runs (54.23 or 54.62). Token-Triggered and Fixed Injection have identical Qwen3-4B entries on both benchmarks (53.85±2.11 and 71.33±2.67; L. 444–445).
  • Table 6 (L. 443–449): several second-best underlines are misplaced. Vanilla is underlined in the Qwen3-4B ConditionedMath and DeepSeek-7B AIME25 columns. In the Qwen3-4B AIME25 column, the three 71.33 entries are underlined, while 72.67 (Verifier, N = 512) is not.
  • Notation: k denotes both the MAD multiplier (Eq. 3) and the memory-bank index (h_k, Eq. 7). Sec. 3.2 drops the layer superscript from v_t, h_t, and c_t, although the layer matters. δ_t (Eq. 1) is used only to describe Fig. 2 (L. 153), but the figure's y-axis is the normalized displacement of Eq. 2. P is defined twice (L. 209–210 and 213–215). Fig. 4 uses an unsubscripted τ for the flip test and the term "Hidden State Momentum Flip", which appears nowhere else.
  • L. 27, 115, 482: "L2 distance spikes", "Latent L2 spikes", and "hidden-state L2 spikes" describe the trigger as a raw L2 distance, whereas the detector uses the normalized ratio of Eq. 2.
  • Table 7 (L. 918–927): "Vote" is undefined. For DeepSeek-7B and Qwen3-4B, both rows use the same layer and their votes sum to more than 1 (0.80 + 0.60; 0.89 + 1.00), so the column cannot be the share of trials in which each configuration ranked first. The selected k is not listed.
  • App. E.4: Table 9 and Fig. 7 do not state the model or data. The flip and non-flip groups are defined by thresholding the same cosine, so d′ grows mechanically with τ_flip, and its growth (L. 1030–1032) cannot by itself justify τ_flip = 0.2. The bimodal recurrence-score distribution that motivates τ_recur = 0.9 (L. 1038–1042) is described but not shown.
  • Fig. 2 (L. 108–117): tick labels and the legend are illegible at print size, and the caption does not say how spikes were labeled Critical or Functional.
  • Fig. 3 (L. 165–169): the functional-pivot window reads "(2 + 8 + 1)/4 = 1025/4, correct.", which is arithmetically false as printed (perhaps an extraction artifact). The highlighted spike tokens are "style" and "numer" (a word fragment), and the critical-pivot window ends at "in the style", so the windows give little context for the claimed pivots.
  • Fig. 8 (L. 1155–1157): the caption says flips are shown as "solid bars", but they are hatched, and the legend encodes only the models. Spike counts also depend on per-model layers and thresholds (Table 7), so the cross-model comparison at L. 1159–1162 is not like-for-like.
Questions for authors
  1. Can you sample intervention prefixes before knowing the STARS outcome, then compare suffix/no-suffix continuations with equal sample budgets? Please include successes and failures and report paired, problem-level uncertainty.
  2. How well does the actual flip/recurrence decision distinguish harmful from benign pivots on randomly sampled held-out traces? Please distinguish this from the descriptive label distribution among selected spikes.
  3. Can you report paired problem-level confidence intervals for the principal accuracy gains and the latency cost of monitoring at a fixed generation length? A random-timing control matched by intervention count, prefix length, and suffix type would help separate timing from intervention frequency.
  4. With the suffix logic held fixed, does latent timing still beat the text verifier? Please report the number of verifier interventions per sequence and compare the verifier with Flip-only at matched intervention counts. Please also evaluate a verifier variant that uses STARS's recurrence-based choice between the two suffixes. If the verifier matches latent timing once suffix selection is matched, the "when to intervene" conclusion would need revision.
  5. How often does each suffix fire for each model and benchmark, and what are the per-suffix fix and break rates? How does injecting only "Wait." (or a neutral sentence of the same length) at the same flip positions compare with the full suffixes? Because the gap between STARS and Flip-only is largest on AIME25, please also report Suffix-swap and the State-/Action-only variants there for all three models.
  6. Was Table 10 computed on the evaluation sets, and did it play any role in choosing (τ_flip, τ_recur) = (0.2, 0.9)? Please report the threshold grid for all three models, on held-out data or on both AIME sets. Please also report sensitivity to k and to the monitored layer (e.g., L21 instead of L27 for DeepSeek-1.5B).
  7. What fraction of traces reaches the 32K-token cap for each method, model, and benchmark? How much of the accuracy and latency gains comes from traces that vanilla leaves truncated? Please also report per-model latency on the full benchmarks and define throughput.
4 comments

We thank the reviewer for the detailed and constructive feedback, and for recognizing the effectiveness of STARS through its ablations and cost-aware evaluation.

W1-1 & Q1. Outcome-independent effect of the suffix

Table 4 in the original submission was designed to examine whether reaching the intervention point alone accounts for STARS's recoveries. While it showed that suffix-free continuations do not recover every case, it did not quantify the average effect of the suffix. To directly assess this effect, we conducted the outcome-independent paired comparison suggested by the reviewer.

For every STARS run with an intervention, regardless of its final outcome, we compare the STARS continuation with a suffix-free continuation from the identical first-intervention prefix under the same generation budget. Since STARS follows vanilla decoding until its first intervention, prefix selection is independent of the intervention outcome.

CM 1.5BCM 7BCM 4BAIME25 1.5BAIME25 7BAIME25 4B
Prefixes229192226137128146
Suffix-free38.4340.6253.1018.9831.2573.29
STARS51.5351.0457.5223.3637.5073.29

Table A: Paired continuation accuracy (%). CM denotes ConditionedMath.

Across 1,058 prefixes, STARS improves accuracy by 6.99 pp (95% problem-level bootstrap CI [+4.58, +9.46]), with 69 wins versus 23 losses (sign test, p<10−5p < 10^{-5}). STARS improves five of six settings and ties in the remaining one. This demonstrates the benefit of suffix-based steering beyond resampling from the same intervention point. We have replaced Table 4 in the revised manuscript with this analysis.

W1-2. Inertia failures beyond resampling

To distinguish the effect of STARS from the inherent recoverability of inertia failures, we compare its fix rates with those of resampling, measured by how often the other four vanilla trials solve the same failed problem.

Failure typeFailures (problems)STARS fix (%)Resampling fix (%)Difference (pp)
Inertia298 (162)37.931.0+6.9 [+1.6, +12.0]
Plain579 (209)24.218.9+5.3 [+1.6, +8.9]

Table B: Recovery beyond resampling across ConditionedMath, MathPerturb, and PuzzleTrivial. Brackets indicate 95% problem-level bootstrap CIs.

STARS significantly exceeds resampling for both failure types, including the more inherently recoverable inertia failures. We have refined the interpretation of Table 3 accordingly. The concentration of gains on inertia-prone benchmarks (Section 4.2) further supports the intended scope of STARS.

We have also clarified that spikes tend to mark unconverged transitions rather than guaranteeing high-plasticity windows.

W2-1 & Q2. Validating the diagnostic rule

Appendix F.1 characterizes the semantic diversity of spikes rather than measuring diagnostic sensitivity or specificity. The geometric rule is designed to identify actionable intervention points, which we evaluate through intervention outcomes.

Fixes are at least as frequent as breaks across every evaluated model, benchmark, and suffix (Table F), while rule-selected intervention points outperform random timing across all six settings (Table D). These results support the operational effectiveness of the diagnostic rule beyond the descriptive annotation.

W2-2 & Q3. Problem-level uncertainty

We computed paired per-problem accuracy differences averaged over five trials, using 10,000-sample problem bootstrap CIs and paired permutation tests across the five benchmarks targeted for improvement.

ModelModel–problem pairsGain (pp)95% CIppWins / losses
DeepSeek-1.5B222+3.60[+0.45, +6.76]0.0368 / 46
DeepSeek-7B222+3.69[+1.26, +6.13]0.00457 / 31
Qwen3-4B222+1.26[−0.90, +3.42]0.3032 / 21
All models666+2.85[+1.35, +4.38]<0.001< 0.001157 / 98

Table C: Problem-level paired comparison with vanilla across MathPerturb, ConditionedMath, PuzzleTrivial, AIME24, and AIME25.

The pooled improvement and the gains for both DeepSeek models are statistically significant. Qwen3-4B also shows a positive gain (+1.26 pp), although it does not reach statistical significance, with identical outcomes on 76% of problems. This analysis is now included in Appendix H.1.

W2-3 & Q3. Random-timing control and monitoring overhead

Each random-timing run matches the STARS problem, trial, suffix sequence, and target intervention count, with positions sampled from empirical STARS position and gap distributions.

MethodCM 1.5BCM 7BCM 4BAIME25 1.5BAIME25 7BAIME25 4BAvg
Vanilla46.54 ± 4.2848.08 ± 5.0156.54 ± 1.5422.67 ± 3.2739.33 ± 1.3370.67 ± 5.3347.30
Random timing49.62 ± 2.2444.62 ± 4.4555.38 ± 2.2420.00 ± 2.9842.00 ± 7.7772.67 ± 2.4947.38
Wait-only45.00 ± 2.6145.77 ± 2.5554.23 ± 4.2818.67 ± 4.0032.00 ± 1.6374.00 ± 4.4244.94
Flip-only51.54 ± 3.9253.46 ± 4.6255.77 ± 3.6523.33 ± 2.1138.67 ± 5.8171.33 ± 3.4049.02
V-flip (512)42.31 ± 3.2248.85 ± 4.6557.69 ± 2.1124.67 ± 3.4039.33 ± 8.5472.00 ± 4.9947.47
V-flip (1024)42.31 ± 7.0949.23 ± 4.3257.69 ± 3.6523.33 ± 3.6538.00 ± 3.4071.33 ± 5.8146.98
V-recur (512)45.38 ± 6.2746.54 ± 4.1157.69 ± 3.2224.00 ± 4.4241.33 ± 2.6771.33 ± 6.8647.71
V-recur (1024)47.31 ± 3.7748.08 ± 3.2258.08 ± 2.2425.33 ± 2.6740.00 ± 2.1174.00 ± 5.7348.80
STARS53.08 ± 2.6154.62 ± 1.9658.85 ± 3.1227.33 ± 3.8943.33 ± 2.9877.33 ± 3.8952.42

Table D: Timing and content controls (accuracy %, mean ± std over five trials).

STARS outperforms random timing across all six settings, while random timing yields inconsistent improvements over vanilla. The realized intervention counts are comparable (1.60 vs. 1.83), as generation may end before a sampled position.

At a fixed generation length, monitoring adds only 0.13–1.94% per-token latency, since STARS reuses already-computed hidden states (Appendix K.3).

W3-1 & Q4. Verifier with matched suffix logic and budgets

The original verifier uses only the shifting suffix, making Flip-only its direct counterpart. To further isolate the trigger, we implemented V-flip and V-recur, following the suffix logic of Flip-only and STARS, respectively, with intervention budgets capped at their counterparts' mean counts. V-recur stores hidden states at verifier-triggered interventions for recurrence diagnosis.

With matched suffix logic and comparable intervention budgets, STARS outperforms both V-recur variants in all six settings (Table D). Flip-only also exceeds both V-flip variants on average, without requiring an external LLM call at every check.

W3-2 & Q4. Intervention counts and latency

Without intervention caps, the verifier intervenes 8.9×8.9\times (N=512N=512) and 3.8×3.8\times (N=1024N=1024) as often as STARS. The reported latencies (518.01 s vs. 251.34 s) were measured on the same 100-problem subset of AIME, MathPerturb, and ReasoningTrap using the same GPU. We have clarified both points in Appendix D.3.

W4-1 & Q5. State-aware cue selection

Flip-only and STARS share the same intervention trigger, differing only in the suffix applied at recurrent flips. STARS consistently improves upon Flip-only (Tables 5 and 12 in the original submission, now Tables 5 and 20 in the revised manuscript), supporting state-aware cue selection.

Replacing both suffixes with \n\nWait. consistently reduces accuracy compared to STARS (Table D), highlighting the importance of suffix content. We further extend the suffix ablation to AIME25:

Suffix variantDeepSeek-1.5BDeepSeek-7BQwen3-4BAvg
STARS (full)27.33 ± 3.8943.33 ± 2.9877.33 ± 3.8949.33
State-only19.33 ± 3.8930.00 ± 7.6072.00 ± 4.9940.44
Action-only18.67 ± 4.5230.67 ± 3.8970.67 ± 3.8940.00
Suffix-swap20.67 ± 1.3335.33 ± 2.6772.00 ± 2.6742.67

Table E: Suffix ablation on AIME25 (accuracy %, mean ± std over five trials).

The full state-aware suffixes outperform all ablated variants across all three models, supporting both suffix structure and adaptive selection (Appendix E.3).

W4-2 & Q5. Suffix firing frequency and fix/break rates

Across seven benchmarks, shifting/loop-breaker suffixes fire 1.57/0.29, 0.89/0.45, and 1.19/0.73 times per question for DeepSeek-1.5B, DeepSeek-7B, and Qwen3-4B, respectively.

We compare STARS and suffix-free continuations from the first occurrence of each suffix, as in Table A.

SuffixPrefixesFix (%)Break (%)Net (pp)
Shifting1,05811.534.54+6.99
Loop breaker6906.814.20+2.61

Table F: Fix/break rates across ConditionedMath, AIME25, and all three models.

Both suffixes yield positive net recovery, with pooled break rates below 5%. Fixes are at least as frequent as breaks in every individual setting (Appendix H.3).

Collectively, these controls demonstrate that both latent intervention timing and state-aware cue selection contribute to STARS's effectiveness.

Q6. Threshold calibration and sensitivity

The default thresholds were frozen before examining Table 10 of the original submission (now Table 14 in the revised manuscript). The phrase "We therefore select ..." misleadingly framed sensitivity analysis as threshold selection. Thresholds were fixed exclusively from held-out calibration distributions, without ground-truth answers or evaluation accuracy, and applied unchanged across benchmarks. We clarified this chronology in Appendix E.4.

We extend this analysis to all three models on AIME24/25, neither used for calibration.

(τflip,τrecur)(\tau_{\mathrm{flip}}, \tau_{\mathrm{recur}})DeepSeek-1.5BDeepSeek-7BQwen3-4BAvg
(0.2, 0.9) default27.67 ± 3.4349.33 ± 2.0077.00 ± 1.9451.33
(0.1, 0.9)21.00 ± 2.9141.00 ± 4.5575.67 ± 3.0945.89
(0.3, 0.9)20.33 ± 3.4042.33 ± 3.2774.67 ± 1.9445.78
(0.2, 0.5)18.67 ± 1.2538.33 ± 4.8374.33 ± 4.0343.78
(0.2, 0.7)19.67 ± 3.2342.00 ± 3.8674.00 ± 2.4945.22

Table G: Threshold sensitivity on AIME24 and AIME25 combined (accuracy %, mean ± std over five trials).

The calibration-derived default performs best across all three models.

On ConditionedMath, reducing kk from 7, 9, and 13 to 5 at the selected layers leaves average accuracy unchanged. Using the second-ranked layers (L21, L14, L4) reduces it by 4.23 pp, supporting robustness to kk and the importance of SPR-based layer selection (Appendix E.2).

Appendix E.2 now specifies the selected kk values and defines Vote as the fraction of calibration runs in which the listed layer ranks first by SPR at the given kk.

Table 11 (Table 9 in the original submission) and Figure 7 in the revised manuscript pool all three models on held-out calibration data. The flip threshold of 0.2 separates strong reversals from weak changes near zero; d′d' is no longer its justification. The new bimodal recurrence histogram places 0.9 at the onset of the high-similarity cluster near 1.

Q7. Token cap and inference efficiency

MethodDeepSeek-1.5BDeepSeek-7BQwen3-4B
Vanilla9.975.976.64
DEER14.6611.634.58
ConCISE9.757.043.29
STARS0.970.725.41

Table H: Percentage of traces reaching the 32K-token cap, averaged across seven benchmarks. ConCISE counts internally generated tokens. Per-benchmark results are in Appendix K.4.

STARS nearly eliminates cap-reaching traces for both DeepSeek models without an explicit termination rule.

Grouping problems by whether vanilla hits the cap in at least one trial, approximately 56% of the accuracy gain comes from cap-reaching problems and 44% from the rest. For DeepSeek-7B, 72% comes from non-cap-reaching problems, including its entire ConditionedMath gain. Thus, avoiding truncation alone cannot explain the gains. On Qwen3-4B, ConCISE hits the cap less often than STARS but has lower average accuracy. The savings of 915 output tokens per question come almost entirely from cap-reaching problems.

On the 100-problem latency subset, STARS achieves the lowest latency for both DeepSeek models (172.81 s and 183.02 s). ConCISE is slightly faster on Qwen3-4B (393.73 s vs. 398.18 s), but STARS achieves the lowest latency averaged across models and the highest throughput for each model.

Throughput counts final output tokens per second, while Compute Token includes internally regenerated tokens. Full-benchmark timing would require approximately 940 GPU hours per trial; we therefore use the controlled 100-problem subset and report per-model latency in Appendix K.2.

Other comments

We verified the following corrections against our result files:

  • Table 1: DeepSeek-7B STARS on PuzzleTrivial is 44.24; Qwen3-4B DEER on AIME25 has a std of 4.99; Qwen3-4B STARS on AIME24 is 76.67 ± 2.98, consistent with the reported average and corrected in Table 23 of the revised manuscript (Table 13 in the original submission). MATH500 standard deviations now follow the same convention as the other columns.

  • Table 10 in the original submission (now Table 14 in the revised manuscript): The two ConditionedMath entries are 54.62 and 54.23.

  • The identical Qwen3-4B Token-Triggered and Fixed Injection entries are genuine: their generations differ, but their per-problem correct counts coincide.

None of these corrections changes the experimental conclusions. The revised manuscript also addresses the remaining presentation issues, including pp units, Table 6 underlines, notation, normalized-displacement terminology, and Figures 2, 3, and 9 (Figure 8 in the original submission).

We appreciate the reviewer's suggestions, which have helped us strengthen the empirical evidence and clarify our findings.

Thanks for the improvement. Considering the novelty I will keep my score.

Comments on the paper

1 comment
Area_Chair_xNjaOpenReview ↗

Reminder: Author–Reviewer Discussion Deadline

Dear Reviewers,

This is a friendly reminder that the author–reviewer discussion period for ICLR 2027 will end on November 18, 2026 (AOE).

As the deadline approaches, I encourage you to actively engage in discussions with the authors and carefully consider their rebuttal responses. Please address any remaining concerns, seek further clarification where necessary, and update your assessments if appropriate.

Your timely and constructive participation is essential to ensuring a fair and well-informed evaluation.

Thank you very much for your time and effort!

Best regards,

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