- Rating
- 3(+1)
- Confidence
- 2
- Informativeness
- 2
- Presentation
- 2
- Soundness
- 2
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Paper summary
Bifrost studies how to reuse successful LLM trajectories on tasks that differ from the source tasks. It keeps source trajectories in the prompt and adjusts a selected model layer using the difference between the target query’s representation and the average representation of the source trajectories. The model weights remain unchanged. The paper motivates this approach through linear representations and a Bayesian account of in-context learning. Experiments cover mathematical reasoning, scientific question answering, and code generation across three Llama model sizes. Further experiments examine transfer from mathematics to code, other model families, and the effects of steering direction, layer choice, demonstration count, and trajectory quality.
Critical strengths
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I like the simplicity of the method. It requires no weight updates, and the representations of source trajectories can be computed in advance. It also fits naturally into a system that already stores past solutions as demonstrations. If the gains are reproducible, this would be a useful way to improve the reuse of existing experience without adding another training stage.
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The reported gains extend across several tasks and model sizes. With the 8B model, Bifrost achieves 90.22% on GSM8K, compared with 87.41% for the strongest reported baseline. On LiveCodeBench, its pass@1 is 17.84%, compared with 14.98% for the strongest alternative. The experiments with other model families and transfer from mathematics to code add useful breadth. I also appreciate the controls in Table 8: changing the steering direction or randomizing the source trajectories reduces performance, providing some evidence that the particular intervention matters.
Critical weaknesses
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The theory does not yet justify the method as implemented. In Appendix D.1, the proof exchanges the order of and , then uses to recover a concept update from a change in hidden states. These steps require conditions that are not stated. The proof also treats the observed difference between the target query and source trajectory representations as a displacement toward an ideal target concept; I could not find a justification for this identification. Appendix D.2 then derives the bound by choosing an oracle coefficient, whereas the experiments use . For a general coefficient, the bias includes an additional term, , which needs to be accounted for. Appendix E.2 provides a useful comparison between fixed and oracle coefficients, but this empirical check does not establish the stated bound. I would need these points resolved before accepting the theoretical explanation of why this particular steering rule should preserve useful source knowledge and improve adaptation.
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I found it difficult to judge how reliable the advantages over the strongest baselines are. The source trajectories are sampled randomly, but the main tables do not show how much the results vary across trajectory selections or generation seeds. This matters for gains such as the 1.01 percentage point improvement on GPQA-Diamond with the 1B model. Appendix F.2 reports three runs for the trajectory quality experiment, which is useful, but it does not resolve the uncertainty in the main comparisons. I also could not determine the full training settings for RISE and Paprika, or exactly what feedback the iterative methods receive when solving target tasks. The gains over ordinary ICL are encouraging. However, stronger claims about outperforming trained and iterative methods need clearer experimental details and evidence that the differences persist across runs.
Questions for authors
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What assumptions justify the mapping in Eqs. (15)-(17), and how does it apply to the empirical vector in Eq. (7)? Can you state the risk bound for the fixed coefficient used in the experiments, including any remaining error from the choice of coefficient?
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Appendix E.2 states that the tuning instances are disjoint from evaluation. Could you briefly explain how this separation was ensured for GPQA-main versus GPQA-Diamond and for the LiveCodeBench releases?
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How much source data was used to train RISE and Paprika, what optimization settings were used, and how were those settings chosen? What feedback did Reflexion and RISE receive during target evaluation, and how was that feedback obtained?
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Were Bifrost and ICL evaluated using the same source trajectories and decoding settings? Please report paired comparisons across independently sampled trajectory banks and generation seeds, with uncertainty estimates. Please also explain the difference between the 1B GPQA-Diamond results in Table 4, which reports 24.24%, and Table 9, which reports 44.44%.
Thank you for the detailed response and the additional experiments. The pseudoinverse addresses my concern about the commutation step, and the four paired runs on Llama-3B strengthen the evidence for Bifrost’s gains over standard ICL. I remain uncertain about the stability of the smaller gain on GPQA-Diamond with Llama-1B and whether the gains over the strongest trained and iterative baselines hold across runs.