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Under review as a conference paper at ICLR 2027

RoPE at the End of Its Rope? Theory, Diagnosis, and Mitigation of Long-Context Failures

Abstract

Long-context failures of RoPE-based language models can arise from RoPE's intrinsic tradeoff between maintaining stable token preferences and distinguishing nearby positions. Determining which weakness to address, and how, requires a more precise characterization of RoPE's behavior in trained models across context lengths. We address a key limitation of prior theory by allowing unequal query–key scales across RoPE frequencies, which aligns well with practical empirical observations. Our theory makes both vulnerabilities measurable for individual heads and inputs, and quantifies how high-frequency components support positional sensitivity while potentially disrupting semantic stability. We also derive **a theoretical context-length bound** beyond which, under specified conditions, a fixed attention-score comparison cannot jointly avoid *semantic reversal* and *positional insensitivity*. Guided by our fresh theoretical insights, we introduce **RoPE Profiler**, a *lightweight, plug-and-play diagnostic toolkit* that augments existing evaluations with zero additional forward passes by reusing cached query and key activations. Reusing activations collected during evaluation, the toolkit incurs little overhead. It supplements standard benchmark scores with two diagnostic scores that reveal semantic and positional weaknesses and help users prioritize which aspect to address. Crucially, our evaluations across 49 long-context task settings reveal a distinct pattern where reasoning tasks predominantly suffer from semantic reversal, whereas retrieval tasks are primarily vulnerable to positional insensitivity. Guided by our theory and diagnostic profiles, targeted high-frequency rescaling achieves immediate gains without additional training, improving task accuracy by up to 20 percentage points on Qwen3-8B and 25 percentage points on Llama-3.1-8B-Instruct.

Primary area:
foundation or frontier models, including LLMs
Keywords:
Rotary position embeddings, Long-context language models, Attention mechanisms, Spectral analysis, Failure diagnosis

Reviews

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1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_MaJvOpenReview ↗
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2
Confidence
3
Informativeness
2
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2
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Paper summary

This paper studies long-context failures in RoPE-based language models through the tension between semantic stability and positional sensitivity. It develops finite-window bounds that accommodate nonuniform frequency coefficients and derives a conditional context-length bound on jointly maintaining these properties for a fixed attention-score margin. The authors introduce RoPE Profiler, which uses cached query/key activations to measure reference-ordering stability and local positional response, then guides training-free interventions on high-frequency components of selected attention heads. Experiments on Qwen3-8B and Llama-3.1-8B-Instruct cover 49 task/configuration settings from nine benchmark sources and identify best-observed gains of up to 20 and 25 percentage points, respectively.

Critical strengths
  1. Broad task coverage. The evaluation includes retrieval, multi-hop question answering, ordering, state tracking, and reasoning, rather than relying exclusively on synthetic needle retrieval. This breadth provides a useful basis for examining task-dependent failure profiles.

  2. Localized, training-free intervention. Modifications are restricted to selected heads and their high-frequency Q/K components, leaving low-frequency components and unselected heads unchanged. This is a restrained intervention design, although preservation of unrelated capabilities still requires empirical verification.

  3. A coherent connection between theory, diagnosis, and intervention. The theoretical tradeoff motivates opposing intervention directions: attenuating high-frequency contributions to stabilize key preferences, or amplifying them to strengthen positional response. Reusing cached activations also avoids additional model forward passes for the diagnostic calculation itself.

Critical weaknesses
  1. The practical explanatory value of the new theory needs stronger validation. The two failure modes and their conceptual tension build on prior work; the additional contribution lies primarily in more general finite-window analysis and a conditional joint-reliability bound. However, the formal result concerns fixed score-margin coefficients within a calibrated family of windows, rather than end-to-end model behavior. It remains unclear how much additional predictive power this result provides for actual task failures. Demonstrating that the theoretical quantities predict degradation across context lengths, beyond simpler spectral statistics, would make the contribution more convincing.

  2. “Semantic reversal” is not necessarily a task-level failure. The diagnostic treats the key ranking at zero relative distance as its reference and measures whether that ordering reverses at other virtual distances. This is a well-defined stability measure, but the reference ordering is not established as the task-correct preference. A reversal may therefore reflect position-dependent attention behavior without impairing the final prediction. The paper should more clearly distinguish reference-ordering instability from harmful semantic failure and provide evidence linking reversals involving relevant evidence and distractors to downstream errors. The authors themselves acknowledge that connecting local vulnerabilities to output errors requires downstream evidence.

  3. The diagnostic scores need more direct behavioral validation. Cross-model agreement in susceptibility rankings and successful interventions provide encouraging indirect evidence, but do not by themselves establish that lower diagnostic scores predict behavioral errors or that the recommended intervention direction is preferable to alternatives. I would like to see held-out analyses relating the scores to task accuracy and intervention gains, together with equal-budget comparisons against opposite-direction interventions, random head selection, and simple fixed-scaling baselines. Such controls would help separate the value of diagnosis from the benefits of searching over candidate configurations.

  4. Generalization of the calibration procedure is not established. The diagnostic activations and intervention evaluations come from the same reference examples, and the best intervention configurations are selected on the examples used to report their gains, without held-out validation. Consequently, the experiments do not establish whether a policy calibrated on a limited sample set can improve performance on unseen inputs without repeating diagnosis or configuration search. A clearer deployment-oriented evaluation would use a separate calibration set to compute the diagnostic profiles and select the heads, intervention direction, and strength, then freeze these choices and evaluate on a disjoint test set. Reporting sensitivity to calibration-set size and the associated computational cost would further clarify the method’s practical utility.

  5. Collateral effects on general capabilities are not established. The reported evaluation focuses on the long-context reference suite and does not establish whether the interventions preserve standard short-context or general-purpose capabilities. Restricting modifications to a small subset of heads does not itself guarantee the absence of collateral degradation. Since intervention direction and strength are task-dependent, it would also be useful to test whether a configuration selected for one task transfers to others. A modest general-capability evaluation would clarify whether this is best viewed as a task-specific adaptation procedure or a more broadly deployable modification.

Questions for authors

same as weakness

4 comments

We thank the reviewer for recognizing our broad task coverage, our training-free intervention, and the coherent connection between theory, diagnosis, and intervention. We address your concerns below.


W1a: The practical explanatory value of the new theory needs stronger validation. The two failure modes and their conceptual tension build on prior work; the additional contribution lies primarily in more general finite-window analysis and a conditional joint-reliability bound.

A1a: We appreciate the reviewer's summary, and would like to clarify the core distinction of our theoretical contribution. The two failure modes are inspired by [1] (semantic reversal) and [2] (positional insensitivity) separately, and our main theoretical contributions are as follows: 1) technically, we provide a more rigorous mathematical framework with an error-bounded frequency split, which allows us to 2) study the irreconcilable tradeoff between positional failure and semantic failure.


W1b: However, the formal result concerns fixed score-margin coefficients within a calibrated family of windows, rather than end-to-end model behavior.

W2: “Semantic reversal” is not necessarily a task-level failure.

A1b: Thank you for the comment. Our theoretical framework connects q/k-norm-level quantities to pre-softmax score behavior with bounded error, which is a standard analysis in theoretical work [1, 3, 4, 5, 6]. We acknowledge the gap between theory and model behavior, therefore, we provide an experiment connecting our attention-head-level failure modes to end-to-end model failure behavior. (Table R4, General Response)


W3: Held-out analyses on opposite-direction interventions, random head selection, and simple fixed-scaling baselines.

W4: Generalization of the calibration procedure is not established.

A3: Thank you for your suggestion. We ran the controls you suggested.

  • Opposite direction. We tested the opposite-direction intervention which improves only 19.4% of task settings, compared with 64.3**%** for the diagnosed direction.
  • Random heads. In Table R2 (general response), Profiler-selected heads beat the same number of random heads by at most 23.0 points at the same intervention strength.
  • Fixed scaling. We have reported accuracy under every fixed scaling coefficient in [Appendix H (H.1–H.4)].
  • Generalization of the calibration. Table R1 (general response) freezes the configuration selected on the calibration examples and evaluates it on 75–200 new examples. All four gains hold, and the method is better than YaRN in every setting.

We hope these experiments can address your concerns.


W5: Collateral effects on general capabilities are not established.

A5: We agree that restricting changes to a few heads does not by itself rule out degradation, so we measured it directly on the MATH dataset (General Response §2, Table R3). Intervening on the selected heads barely changes accuracy, whereas intervening on all heads causes a large drop. This shows that our head selection mechanism successfully avoids harming general capabilities.


Thank you again for the insightful comments. If you find our response satisfactory, we respectfully hope that you can re-evaluate our work. We are happy to address any further concerns.

References:

[1] RoPE Distinguishes Neither Positions Nor Tokens in Long Contexts, Provably, Du et al., 2026

[2] Beyond Semantics: Rediscovering Spatial Awareness in Vision-Language Models, Qi et al., 2026

[3] RoFormer: Enhanced Transformer with Rotary Position Embedding, Su et al., 2024

[4] Base of RoPE Bounds Context Length, Xu et al., 2024

[5] Round and Round We Go! What makes Rotary Positional Encodings useful?, Barbero et al., 2025

[6] Decoupling Positional and Symbolic Attention Behavior in Transformers, Urrutia et al., 2026

The author's response addresses some of my concerns. However, weakness 1 is still not fully solved. So I will keep my score.

AuthorsOpenReview ↗

Follow-up Clarification on Weakness 1

We sincerely apologize for not having fully addressed Weakness 1 earlier, as we overlooked the following point:

Demonstrating that the theoretical quantities predict degradation across context lengths, beyond simpler spectral statistics, would make the contribution more convincing.

Actually, we have already established the increasing reversal rate both theoretically (Lemma A.2, Corollary A.1) and experimentally (Table R5). Furthermore, in Table R4 of General Response 3, we can observe that as the task length increases, both the error rate and the reversal rate increase accordingly.

Table R5. Virtual reversal rate by window length.

Model8k16k32k64k128k
Qwen3-8B24.37%25.51%27.22%30.60%35.15%
Llama-3.1-8B-Instruct20.58%22.03%23.50%25.18%28.06%

If you find these clarifications meaningful, we respectfully hope you to consider re-evaluating our work. If not, could you please clarify which specific concerns from Weakness 1 still remain? As W1 covers several aspects, we want to make sure we address every remaining point thoroughly and accurately.

Reviewer_GEYEOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary
  • Analyzes RoPE attention scores and studies two failure modes:
    • semantic reversal: a position shift flips a query’s preference between two keys.
    • positional insensitivity: normalized score changes little between adjacent positions.
  • Theorem 1 states that a fixed score margin cannot meet both a reversal tolerance and an adjacent-response threshold.
  • RoPE profiler reuses cached query and key activations from evaluation to compute a Semantic Score and a Positional Score, without extra forward passes. It ranks tasks by their relative susceptibility to each failure (w_S) and uses that ranking to choose whether to attenuate or amplify high frequencies in selected heads.
Critical strengths
  • Overall very nice and elegant diagnostic analysis
Critical weaknesses
  • The connection between the theory and long-context failure is weak, IMO.

(1) The evaluated inputs <16k tokens. These are well inside both models trained windows. That says little about behavior “at the end of its rope.”

(2) Theorem 1 concerns single-head, pre-softmax score comparisons, and the paper reports no concrete M_max for either model.

(3) There is no comparison to existing training-free RoPE interventions under matched search.

Questions for authors

Previous box.

3 comments

We thank the reviewer for the encouraging comment for our nice and elegant diagnostic analysis. We address your concerns below.


W1: The connection between the theory and long-context failure is weak, IMO. (1) The evaluated inputs <16k tokens. These are well inside both models trained windows. That says little about behavior “at the end of its rope.”

A1: Thank you for raising this. We will clarify that “end of its rope” refers to the reversal rate increasing with context length (Lemma A.2, Corollary A.1, Table R5). In fact, models suffer from these failure modes even when the context is not very long. Table R4 (General Response) shows that a growing reversal rate degrades performance, and that samples with high reversal rates are more likely to be answered incorrectly.

Table R5. Virtual reversal rate by window length.

Model8k16k32k64k128k
Qwen3-8B24.37%25.51%27.22%30.60%35.15%
Llama-3.1-8B-Instruct20.58%22.03%23.50%25.18%28.06%

W2: Theorem 1 concerns single-head, pre-softmax score comparisons, and the paper reports no concrete M_max for either model.

A2: Single head: it is standard practice for theoretical works to analyze single-head (even linear) transformers, including analyses of RoPE [1, 2, 3], in-context learning as gradient descent [4, 5, 6], and chain-of-thought reasoning [7, 8]. Moreover, our single-head analysis drives us to select task-sensitive positional heads (Appendix F.2), which helps us understand the mechanism better and avoid harming general capabilities (Table R3, General Response).

Pre-softmax: softmax does not affect our conclusions, because we consider the relative ordering of different keys.

M_max depends on the reversal tolerance δ one is willing to accept. For δ = 1/4, M_max is around 16k for Qwen3-8B and 64k for Llama-3.1-8B-Instruct (Table R5).


W3: There is no comparison to existing training-free RoPE interventions under matched search.

A3: We provide experiments and a discussion of YaRN and p-RoPE in General Response §1 (Table R1). We hope this addresses your concerns.


Thank you again for the insightful comments. If you find our response satisfactory, we respectfully hope that you can re-evaluate our work. We are happy to address any further concerns.

References:

[1] Extending Context Window of Large Language Models via Positional Interpolation, Chen et al., 2023

[2] Round and Round We Go! What makes Rotary Positional Encodings useful?, Barbero et al., 2025

[3] RoPE Distinguishes Neither Positions Nor Tokens in Long Contexts, Provably, Du et al., 2026

[4] Transformers Learn In-Context by Gradient Descent, von Oswald et al., 2023

[5] What Learning Algorithm Is In-Context Learning? Investigations with Linear Models, Akyürek et al., 2023

[6] Trained Transformers Learn Linear Models In-Context, Zhang et al., 2024

[7] Towards Revealing the Mystery behind Chain of Thought: A Theoretical Perspective, Feng et al., 2023

[8] Chain of Thought Empowers Transformers to Solve Inherently Serial Problems, Li et al., 2024

I thank the authors for their response. I will maintain my score.

Thank you again for your constructive feedback. As mentioned earlier, your review has helped us significantly improve our work. Could you let us know if our previous responses have fully addressed your concerns? If any further issues remain, please point them out. We would be glad to address them!

Reviewer_N7BoOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper formalizes two RoPE failure modes. Semantic reversal is when a key preference flips as relative distance changes. Positional insensitivity is when a one-token shift barely changes the score. It proves finite-window moment bounds for the high-frequency score component with arbitrary fixed q/k, and derives a context-length bound M_max beyond which a margin cannot avoid both failures. It then introduces RoPE Profiler, which computes Semantic and Positional Scores from cached q/k, ranks 49 task settings to pick an intervention direction, and rescales or freezes high frequencies in selected heads. The authors report best-observed gains of up to +20% on Qwen3-8B and +25% on Llama-3.1-8B.

Critical strengths
  1. Clean formulation. The two failure modes are defined cleanly and are easy to compute. The complex-sum view makes the high- vs. low-frequency tradeoff intuitive, and Figures 1–2 communicate it well.
  2. The moment bounds drop the amplitude-regularity assumptions of prior work.
  3. The diagnostic is cheap, since it needs no extra forward passes.
Critical weaknesses
  1. Experiments: i. The gains are on tiny samples. Each reported number is the best of 4–9 candidates, chosen on the same 12–25 examples used for evaluation, with no held-out validation. The +20% result is 1/25 to 6/25, and the +25% result is 0/12 to 3/12. ii. The paper never tests the opposite direction, a global intervention, or random heads, so it is unclear whether w_S adds anything.

  2. The theory is weaker than claimed. Theorem 1 assumes an unverified Gaussian calibration bound τ_G, so the distributional assumption is moved into a hypothesis rather than avoided.

  3. No baselines like YaRN or p-RoPE are compared.

Questions for authors

Please provide more details about the above points.

1 comment

We thank the reviewer for the positive and encouraging assessment of our paper’s clarity, organization, theoretical contributions, and the cheap diagnostic. We address your concerns below.


W1: Experiments: i. The gains are on tiny samples.

A1: We agree that selecting and evaluating on the same 12–25 examples can overstate the gains. We therefore treated those examples as a calibration set, froze the selected direction, heads, and α, and evaluated on 75–200 new examples (General Response §1, Table R1). The results show that the positive gains still hold (up to 22.7%).


W2: ii. The paper never tests the opposite direction, a global intervention, or random heads, so it is unclear whether w_S adds anything.

A2: Thank you for your suggestions. We tested all three controls.

  • Opposite direction. With further experiments, the opposite-direction intervention improves only 19.4% of task settings, compared with 64.3% for the direction assigned by w_S.
  • Global intervention. Intervening on all heads seriously harms the model’s capabilities. On MATH, accuracy drops from 52% to 19% for Llama-3.1-8B-Instruct and from 83% to 62% for Qwen3-8B, whereas intervening on the selected heads leaves it nearly unchanged (General Response §2, Table R3).
  • Random heads. Table R2 (General Response) applies the same intervention to random heads. Selected heads win in all four settings, by up to 23%. Our first experiments in fact used random heads and gave only marginal gains, and the theory then led us to the task-sensitive heads [Appendix F.2]. We consider identifying these heads a contribution of the paper.

We hope these experiments can address your concerns.


W3: The theory is weaker than claimed. Theorem 1 assumes an unverified Gaussian calibration bound τ_G, so the distributional assumption is moved into a hypothesis rather than avoided.

A3: That is an insightful question. In fact, we also thought carefully about how to handle τ_G, because without this assumption, the zero mean and controlled variance in Proposition 1 and the semantic-positional tradeoff still hold. In the end, we keep it for three reasons:

  1. It holds empirically. On real heads and windows, the average gap between the measured reversal rate and its Gaussian approximation is only 0.0555% (Figure 3a; Appendix D.2.2).
  2. It is implied by the assumptions of prior work. Under the amplitude regularity assumed in prior work [1], the lacunary central limit theorem yields Gaussian behavior, as we note below Proposition 1. The calibration condition therefore covers that setting rather than adding a new restriction.
  3. It yields closed-form diagnostics. The Gaussian form turns the theoretical criteria into closed-form scores for RoPE Profiler, accelerating its calculation without enumerating reversals at every position.

In the revision, we describe Theorem 1 as conditional on a calibration bound that we verify empirically, while Proposition 1 stays assumption-free.


W4: No baselines like YaRN or p-RoPE are compared.

A4: We provide experiments and a discussion of YaRN and p-RoPE in General Response §1 (Table R1). We hope this addresses your concerns.


Thank you again for the insightful comments. If you find our response satisfactory, we respectfully hope that you can re-evaluate our work. We are happy to address any further concerns.

References:

[1] RoPE Distinguishes Neither Positions Nor Tokens in Long Contexts, Provably, Du et al., 2026

Comments on the paper

3 comments
AuthorsOpenReview ↗

General Response

We thank the reviewers for their positive feedback on our clear and elegant diagnosis analysis of RoPE’s failure modes and the coherent connection between theory, diagnosis, and intervention, which we also regard as the main contribution of this work. The reviewers also share concerns about the proposed intervention: lack of external baselines, ablation studies and further analysis. Therefore, we present experiments below in general response, which we hope can address your concerns. We thank the reviewers for these suggestions, which make our empirical study more convincing. We have added all results with their detailed settings from the rebuttal stage to the revised paper.

1. Expanded held-out evaluation and discussion with YaRN and p-RoPE

We agree that selecting an intervention on small examples used to report it can overstate the gain, and the intervention lacked an external baseline. We treated the original examples as a calibration set so that we can freeze the chosen scaling coefficient α for each tasks. We then evaluated on 75–200 new examples that were not used in the original search. Within the rebuttal period, we prioritized the two tasks with obvious accuracy gains in our original paper for each model.

Table R1. With the intervention frozen from the calibration examples, all four gains hold on the larger held-out sets, and the method outperforms YaRN [1] in every setting.

ModelTask SettingFrozen interventionHeld-out examplesNativeYaRNProfiler
Qwen3-8BBABILong QA7, 16kα = 0756.7%14.7% (+8.0)16.0% (+9.3)
Qwen3-8BFLenQA RuleTaker, 3kNo high-frequency rotation7582.7%86.7% (+4.0)89.3% (+6.7)
Llama-3.1-8B-InstructLIFBench, 3kα = 1.752002.5%3.5% (+1.0)7.5% (+5.0)
Llama-3.1-8B-InstructFLenQA PIR, 3kα = 27556.0%58.7% (+2.7)78.7% (+22.7)

How this differs from YaRN. YaRN extends a model beyond its training length with the same rescaling for every task, whereas our intervention adapts to each task to improve performance within the training length. Theorem 1 implies that, beyond M_max, no fixed setting avoids both semantic reversal and positional insensitivity, so the positional–semantic tradeoff should be tuned to each task rather than handled by a uniform context-window extension such as YaRN.

Relation to p-RoPE. p-RoPE [2] removes rotation from a fixed set of frequencies in every head, which is the same operation as our “no high-frequency rotation” intervention. Our variant removes rotation from a diagnosed band in selected heads rather than from a fixed band in all heads (Appendix B.4).

2. Task-sensitive heads improve long-context tasks without harming reasoning

(1) Task-Sensitive Heads Outperform Random Heads. Several reviewers also asked for an ablation for head selection. To test whether head selection matters, we compared the selected heads with the same number of randomly chosen heads. Result shows selected heads beat random heads in all four settings (Table R2).

Table R2. Selected heads beat random heads in all four settings.

ModelTaskInterventionProfiler-selected headsRandom heads
Qwen3-8BBABILong QA7, 75 ex.×0.534.7% (+3.1)31.6%
Llama-3.1-8B-InstructBABILong QA7, 75 ex.×0.545.3% (+4.9)40.4%
Qwen3-8BMK-hard, 100 ex.×1.567.0% (+11.0)56.0%
Llama-3.1-8B-InstructMK-hard, 100 ex.×1.553.0% (+23.0)30.0%

(2) Task-Sensitive Heads Preserve Reasoning Capabilities. We also test whether intervening on the task-sensitive heads (top 5%) harms general capabilities by evaluating 100 questions on the MATH reasoning benchmark [3]. MATH has short questions and long responses, unlike long-context tasks, which usually have long inputs and short responses. We use ×2 scaling for Qwen3-8B and ×1.5 for Llama-3.1-8B-Instruct, which is more fragile. The results show that (1) intervening on the selected heads has only a marginal effect, and (2) restricting the intervention to task-sensitive heads avoids harming reasoning capability, whereas intervening on all heads causes a large drop (Table R3).

Table R3. MATH accuracy before and after intervention.

ModelUnmodifiedTask sensitive heads(5%)All heads
Llama-3.1-8B-Instruct52%55% 19%
Qwen3-8B83%81% 62%

We consider the identification of task-sensitive heads a contribution that not only deepens our understanding of how attention heads operate in LLMs, but also serves as an integral part of our theory-guided, task-adaptive intervention.

3. Linking failure modes to real world task errors

We used LIFBench adjacent-element retrieval and evaluated native Qwen3-8B on 100 synthetic lists per length setting. For each question, we paired the correct item with a nearby incorrect item of the same format and kept both at their original positions. The results show that 1)tokens with higher reversal rates are more likely to be incorrect and 2) as the task length increases, both the error rate and the reversal rate increase.

Table R4. Correct responses show fewer reversals between the evidence and the distractor.

SettingCorrect / incorrect responsescorrect(Reversal rate)incorrect(Reversal rate)
3k32 / 6817.01%27.47% (+10.45)
6k29 / 71 23.31%28.46% (+5.16)
13k19 / 81 25.13%32.35% (+7.23)

References:

[1] YaRN: Efficient Context Window Extension of Large Language Models, Peng et al., 2024

[2] Round and Round We Go! What makes Rotary Positional Encodings useful?, Barbero et al., 2025

[3] Measuring Mathematical Problem Solving With the MATH Dataset, Hendrycks et al., 2021

We thank the reviewers again for their valuable suggestions on the experiments. Your feedbacks not only help us refine our intervention method (calibrating on a small set and generalizing to held-out samples) and make our evaluation more convincing (comparing against YaRN baseline, ablating task-sensitive heads, and verifying general capabilities), but also deepen our understanding of the correlation between theoretical failure modes and real task errors, which bridges the gap between theory and real LLM behavior. Since most of the concerns concentrated on the intervention method and this theory-to-practice gap, we respectfully hope you can re-evaluate our work. We are glad to address any further concerns.

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