- Rating
- 2
- Confidence
- 2
- Informativeness
- 2
- Presentation
- 2
- Soundness
- 2
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Paper summary
The paper connects data attribution, forgetting, and plasticity loss through first-order interactions between language-model updates. It separates a readout channel (CH1) from a backbone channel (CH2), using explicit approximations to obtain scores from forward quantities. Experiments examine attribution, cross-lingual retrieval, multilingual memory, and data selection. The authors distinguish interference from extreme updates ('collision') from accumulated weak interference ('erosion'). During prolonged PubMed training, a task-conditioned readout transmission score declines alongside downstream adaptability; restoring the readout partially recovers performance. The theory establishes local interactions and conditional directional attenuation, while the broader learning-trajectory account is supported empirically.
Critical strengths
The paper connects data selection, forgetting, and future learnability through a common update-behavior interaction. Its progression from local geometry to these three applications, supported by the overview and channel diagrams, helps readers follow the central motivation. This broad perspective also yields testable distinctions: on Qwen, adding CH2 improves cross-lingual MMLU retrieval from 0.488 to 0.625 when direct token overlap is limited. The combination of a coherent organizing framework and concrete predictions is useful for relating problems that are often evaluated separately.
The empirical study is substantial, combining controlled attribution, multilingual retrieval, data selection, interference interventions, and long-horizon adaptation across multiple models. These experiments test different aspects of the framework. This breadth makes the paper informative beyond a single benchmark result and gives readers several ways to assess the framework's practical utility and explanatory value.
Critical weaknesses
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The presentation does not consistently distinguish evidence from interpretation in the plasticity account. Section 5 uses 'formally prove' for the feedback loop, whereas Appendix A.3 describes the trajectory account as an extrapolation and Appendix B.3 proves attenuation under fixed forces and contraction. The empirical attribution also leaves three issues unresolved: Equation (7) varies with both readout geometry and task-force directions; the effect of retaining the final RMSNorm Jacobian is untested; and Figure 7(b) does not isolate whether the restoration benefit requires backbone updates. The scope of the plasticity argument is difficult to follow because its qualifications are distributed across Section 5 and Appendices A.3 and B.3. Stating the proof’s assumptions and limits alongside the main claim would help readers distinguish established results from the proposed feedback mechanism.
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The numerical results and comparative wording need separate corrections. Section 3 reports LESS as 0.587 for Qwen at 5%, whereas Table 5 gives 0.6171 versus 0.6356 for CH1+2: an advantage of 1.85, not approximately 4.9, percentage points. Separately, Table 1's broad superiority claim conflicts with HyperINF's higher MMLU retrieval score (0.694 versus 0.625). The first issue changes the reported gain; the second overstates where the method outperforms its competitors.
Questions for authors
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Please reconcile Section 5's 'formally prove' statement with Appendices A.3 and B.3. If the proof establishes conditional attenuation only, state that scope in the main text and present the feedback loop as a hypothesis. If a stronger result is intended, identify where the evolving feedback loop is established.
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On fixed held-out examples, compare , , and with baseline , using Equation (7). Here 0 denotes the checkpoint before PubMed training. Does attenuation persist when probe forces are fixed? One task and a few saved checkpoints would distinguish contributions from readout changes and changing force directions.
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For the same task and checkpoints, evaluate , retaining the final RMSNorm Jacobian as specified in Appendix B.1. Does its change relative to the pre-PubMed baseline agree with the decline in raw ? This tests whether the diagnostic tracks transmission into the pre-normalization backbone.
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At one late PubMed checkpoint, compare reset versus no reset under both head-only and full-network adaptation, using matched data and update budgets. How much does the reset benefit differ between these two settings? Figure 7(b) already establishes the full-network benefit; the additional control would clarify whether that benefit requires backbone updates.
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For Qwen2.5-1.5B at the 5% selection budget, do Section 3's 0.587 and Table 5's refer to the same configuration? Please identify the correct comparable LESS result and the corresponding CH1+2 gain. If the values come from different configurations, specify the difference and align the main-text comparison accordingly.
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Please revise Table 1's 'markedly outperforming gradient-based baselines' wording to reflect both retrieval columns. CH1+2 exceeds HyperINF on GSM8K (0.600 versus 0.370) but trails it on MMLU (0.625 versus 0.694); the caption should state the setting-specific advantage without implying superiority in both.
4 comments
Response (2/2)
W2 (same with Q5 and Q6). The numerical results and comparative wording need separate corrections.
We thank the reviewer for pointing out these issues, and we apologize for the numerical errors. The numbers in the main text were copied from an earlier version, while those in Table 5 are correct. We also agree that the caption of Table 1 was imprecise. We will correct these issues in the revised version. Please also refer to our overall response. We have also clarified that Table 5 used a different evaluation protocol, and we provide a new table in Appendix G, Table 16, comparing different evaluations.
Questions.
Please refer to our responses to the corresponding weaknesses above, where we discuss each of these questions.
Thank you for the detailed response. The LESS correction, the clarification of the GSM8K evaluation protocols, and the revised Table 1 caption address my concerns about the numerical comparisons. The revised Section 5 also gives a more defensible account of what Appendix B.3 establishes. In particular, the new ablations show that a readout reset can improve adaptation even when subsequent updates are restricted to the backbone.
My remaining concern is the link between this reset benefit and the proposed mechanism. Figure 29 shows a modest decline in readout transmission on out-of-distribution tasks with probe forces held fixed. How much this contributes to the loss of plasticity remains unclear. In particular, the spectral analysis and reset experiments leave open whether the learning signal entering the backbone weakens in the way described in the abstract, since the transmission analysis omits the final RMSNorm Jacobian. This link matters to the paper’s unified account of long-horizon learning, so I am keeping my overall rating at 2.
Thank you for the follow-up and for confirming that the numerical and evaluation concerns are resolved.
On the remaining point, we agree that our results do not quantify how much the measured transmission decline contributes to plasticity loss. We have revised the abstract and introduction accordingly: readout-mediated attenuation is now stated as a hypothesis consistent with the evidence rather than an established mechanism. More broadly, the revised Section 5 is intended as an empirical analysis of how the readout evolves under long-horizon training and how this relates to plasticity loss, rather than a formal account of the mechanism. We hope this clarified scope addresses your remaining concern.
Regarding the RMSNorm Jacobian: in the backbone-only ablation (Fig. 7c), the reset and no-reset runs start from the same backbone and the same final-norm parameters, so the normalization Jacobian is identical across the two conditions at the point of reset. The reset benefit under backbone-only updates therefore cannot come from the normalization layer and must be attributed to the change in the readout. What this intervention does not separate is whether the readout acts through its transmission geometry or through the forces it induces; we now state this limitation explicitly in Section 5. Because this comparison holds the normalization fixed by construction, we believe it isolates the readout’s contribution more directly than incorporating the Jacobian into the transmission diagnostic would.
Response (1/2)
We thank the reviewer for the careful and constructive assessment, particularly the insightful questions regarding the plasticity analysis. The main concerns center around the evidence supporting Section 5 and some imprecise claims about the experimental results in Section 3. We have revised these claims and restructured Section 5 to directly analyze the evolution of the readout geometry. We have also narrowed the scope of the "formally prove" statements and now present Section 5 as an empirical analysis with a discussion of possible mechanisms. The experiments suggested by the reviewer are also included in the appendix. Please refer to our overall response and the revised PDF for more details. Below, we respond point by point.
Thanks very much for raising these insightful comments on Section 5. We agree that the "formally prove" statement was too strong, and the evidence chain in the original Section 5 was not sufficiently supported: R_D depends on both readout geometry and task-force directions, and our theoretical results only hold for one or a few steps. Therefore, in the revised version, we have reorganized Section 5 to directly analyze the spectrum of w, rather than relying on the indirect scalar R_D, to better understand how the degeneration occurs. This is similar to what we did for the sequential SFT experiments in Appendix F, but with a more systematic analysis of the PubMed experiment. We believe that directly analyzing the spectrum allows us to make more precise claims and observations about how the readout degenerates.
We summarize this concern into the following four points and respond to them one by one.
Yes, that is correct. As also mentioned by reviewer JaP8, R_D requires samples from downstream tasks, which makes it less practical to use. Therefore, in the revised version, we directly analyze how the spectrum of w (and some submatrices of w) changes. This provides a more solid evidence chain, and the spectral diagnostics are also easier to compute in practice.
Regarding the R(Wt, g0) suggested in Q2, we believe the revised Section 5 no longer requires this analysis. However, since the observations are indeed interesting, we still provide them in Appendix G, Figure 29. In short, our results suggest that readout degeneration is more closely related to spectral redistribution than to an overall decrease in norm.
We agree that the RMSNorm Jacobian affects the gradient magnitude entering the backbone. However, even when accounting for this Jacobian, the gradients in CH2 are still mediated by the shared readout w. The readout geometry therefore remains a common component of the gradient propagation pathway, motivating our direct spectral analysis of wwT without modeling the additional Jacobian effects. In the revised Section 5, we no longer use R_D to predict plasticity loss, but instead focus on empirical spectral evolution and readout-reset interventions. We therefore believe that the proposed RMSNorm-specific experiment is no longer essential for the revised analysis, but we would be happy to include it in a subsequent revision if the reviewer considers it necessary.
Thanks very much for raising this concern. We agree that Figure 7(b) needs further ablations to understand where the recovery comes from. In addition to the experiment you suggested, we have conducted a full ablation under three settings. Specifically, after resetting w, we compare: (1) fine-tuning all parameters; (2) fine-tuning w only; and (3) fine-tuning the backbone only. Before resetting, we also try the three ablations above. The ablations show that resetting the readout improves both backbone-only and readout-only fine-tuning compared with their no-reset counterparts, while full-model fine-tuning achieves substantially lower losses than either restricted setting. This suggests that backbone updates remain important for recovering downstream plasticity. Please also refer to the new Figure7-c and Appendix G, Figure 28 for more details.
We agree that the "formally prove" statement was too strong. The result in Appendix B.3 is conditional on specific assumptions and does not establish the full feedback loop. We have therefore removed this claim and now present the feedback loop as a possible explanation rather than a proven mechanism. The theoretical result in Appendix B.3 remains valid under its stated assumptions, and we have clarified its scope in the revised version.