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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
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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.
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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.
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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
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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.
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“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.
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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.
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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.
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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
The author's response addresses some of my concerns. However, weakness 1 is still not fully solved. So I will keep my score.
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.
| Model | 8k | 16k | 32k | 64k | 128k |
|---|---|---|---|---|---|
| Qwen3-8B | 24.37% | 25.51% | 27.22% | 30.60% | 35.15% |
| Llama-3.1-8B-Instruct | 20.58% | 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.
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.
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