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Paper summary
This paper studies whether a learning signal's authority to change model parameters on the current update can be separated from its authority to write persistent optimizer state that influences future updates. The authors investigate this question in a strict replay-free Split CIFAR-100 class-incremental setting, using ten sequential tasks, a compact CNN with a fixed 100-class classifier, Adam, current-task-only training, and raw global 100-way inference. The central intervention is a 2 × 2 factorial design that independently controls present parameter action and persistent state writing. From the same arm-local pre-step state, the method constructs Adam candidates using a controller gradient and a source gradient; one intervention flag determines which candidate governs the current parameter update, while another determines which first- and second-moment state is retained.
The principal result is that the write-only condition, which denies the source direct influence over its same-update parameter transition while retaining its contribution to persistent Adam state, produces a mean current-acquisition increase of 0.00774 relative to the neither condition across five seeds. The corresponding mean differences are +0.00604 in forgetting and +0.00569 in the old-to-final endpoint. By contrast, the action-only condition changes current acquisition by only +0.00058. Follow-up interventions attribute the source-local effect predominantly to first-moment persistence, accumulated within-task history, and the current-relative orthogonal component of inherited history.
The paper also studies how acquisition-bearing history propagates after a task ceases to be current. In four independent paired seeds, with six origin tasks nested within each seed, the authors report source-dependent classifier weights and Adam moments at the current-to-old boundary, followed by source-dependent old-row displacement while the natural classifier gradient is exactly zero. A separate function-preserving reparameterization experiment shows that identical branch-time predictions do not uniquely determine the subsequent training trajectory in the tested stateful optimization setting. Importantly, the authors distinguish lifecycle provenance from behavioral mediation, do not propose a validated mitigation method, and explicitly limit their conclusions to the tested architecture, optimizer, benchmark, and source construction.
Critical strengths
- A clearly operationalized causal intervention rather than a correlational analysis.
The 2 × 2 action-by-write factorial is the strongest contribution. The authors independently assign present-action authority and persistent-write authority, define what each intervention changes, and construct the candidate Adam recurrences from the same arm-local pre-step state. This is considerably more informative than showing that resetting optimizer state changes performance or that optimizer moments correlate with earlier training signals. The five-seed results support the main observation: all five reported write-only contrasts for current acquisition are positive, ranging from 0.0053 to 0.0107, whereas the action-only acquisition contrast averages just 0.00058. The carrier-localization experiments then provide a structured investigation of which components of persistent history account for the observed effect. This causal organization is a substantive strength even though the experimental scope is narrow.
- Careful claim boundaries and attention to negative evidence.
The paper is appropriately cautious about what its experiments establish. It correctly distinguishes 24 nested lifecycle evaluations from four independent paired seeds, explicitly avoids treating those nested evaluations as independent replications, and does not claim that the measured boundary differences mediate behavioral forgetting. The negative and falsification experiments are also valuable. Rather than presenting every decomposition as a successful mitigation, the authors report failures of proposed static controls and acknowledge the acquisition–forgetting trade-off. These choices improve the credibility of the mechanistic interpretation.
Critical weaknesses
- The generality and incremental significance of the causal result remain uncertain.
All of the central experiments use one benchmark, one fixed class order, one compact CNN, one optimizer configuration, and one specially constructed source signal. Specifically, the source is the component of an auxiliary non-target-suppression gradient that is orthogonal to the contemporaneous controller gradient. The repeated experiments use new seeds and different interventions, but they do not establish whether the same action-versus-write pattern appears with an independently defined learning signal, a conventional learning objective, another architecture, or another optimizer. This matters because the paper's broader conceptual framing concerns causal rights in replay-free continual learning, while the direct empirical finding is source-local. The authors acknowledge this boundary, and I do not require state-of-the-art continual-learning baselines for a mechanistic study. The missing evidence is instead an independent replication of the mechanism under a meaningfully different source or training configuration. The related-work discussion already acknowledges Xu (2026), Stored in Optimizer State, Valued by Later Training: A Causal Account of Subliminal Trait Transfer. Given that prior work's focus on causal optimizer-state transport, the contribution here needs to rest clearly on the action-versus-write factorization and its consequences within the continual-learning task lifecycle—not on first-moment memory alone. A focused comparison against that prior work, ideally supplemented by one independent replication, would help establish the significance of the incremental contribution.
- Uncertainty reporting and the definition of the old-to-final endpoint are insufficient.
The principal action-by-write factorial contains only five independent seeds, and the lifecycle experiment contains four independent paired seeds. The paper provides useful seed-level contrasts, but does not report confidence intervals or comparable estimates of uncertainty. The prospectively specified materiality threshold is a legitimate decision convention, but it does not communicate how uncertain the estimated effect sizes are. For example, the five reported write-only old-to-final contrasts include one negative value, −0.005667, and four positive values. A simple small-sample, paired-contrast t interval reconstructed from the reported values is approximately [−0.0034, 0.0148]. This is only an illustrative uncertainty calculation, not a replacement for the authors' prospective decision procedure, but it shows why the mean old-to-final increase should be interpreted more cautiously than the consistently positive current-acquisition result. More importantly, the old-to-final recapture/capture endpoint is not given an exact mathematical definition in the manuscript. Appendix A explicitly says that the authors report the endpoint as implemented rather than reconstructing an unverified algebraic surrogate, but this does not remove the need to specify the metric itself. Because this endpoint appears in the abstract, results tables, and carrier-localization discussion, readers should be able to determine precisely what is measured, how it is aggregated, and what a positive or negative change means. This is a fixable but material reproducibility concern.
Questions for authors
- Exact definition of the old-to-final endpoint.
Could you provide the exact formula used to calculate the old-to-final recapture/capture endpoint, including the tasks included, the averaging or normalization procedure, and the sign interpretation? Please also identify where this computation is implemented in the supplementary materials, if code is provided. A precise definition and consistency check of the reported contrasts would resolve an important reproducibility concern.
- Uncertainty in the primary and secondary results.
Could you report confidence intervals or another justified uncertainty summary for the five-seed action-by-write contrasts, especially current acquisition, forgetting, and old-to-final recapture? Please clarify which endpoints the prospective materiality threshold of 0.005 governs and how the observed seed-level heterogeneity should affect the interpretation of the recapture result. I am not asking that the authors retroactively change their registered decision rule; I am asking for enough information to assess the precision of the reported effects.
- Specificity to the chosen source and training setting.
Is it feasible to demonstrate the main action-versus-write result with one meaningfully different source signal or training configuration—for example, a different controller component, an alternative task ordering, or another optimizer? If not, could the authors clarify why the proposed causal organization is expected to be scientifically informative beyond the particular orthogonalized source and Adam configuration studied here? Such evidence would materially affect my assessment of the paper's general significance.
Revised Manuscript — Clearer Contribution, Absolute Results and Broader Validation
Thank you again for your direct assessment of the manuscript's presentation, motivation and scientific value. We agree that the original version did not make its central contribution sufficiently accessible. We have now uploaded a substantially rewritten manuscript and anonymous supplement, with your criticisms directly informing the revision.
Page 1 explains this distinction using ordinary optimizer terminology, including why backpropagation and parameter updates continue in the write-only condition. Figure 1 (p. 3) presents the four interventions together. The original experiment is now clearly separated from subsequent mechanism tests and post-submission validation. We have reduced non-standard terminology and substantially reorganised the scientific narrative.
The write-only acquisition benefit is +0.774 percentage points (95% CI [+0.450, +1.098]), but forgetting worsens by +0.604 pp. Final overall accuracy improvement is not established. We now present this explicitly as an acquisition–forgetting trade-off, not a mitigation method.
Table 4 and Figure 3 additionally report controlled changes involving Tiny ImageNet, momentum SGD, ResNet-18 and a joint benchmark–optimizer setting. Negative and interaction-dependent results remain included. The original momentum-SGD executable source has also been recovered and independently hash-verified, with archived replay evidence described in §4.3 and Appendix F. Other task sequences remain untested.
The implication is methodological: comparisons of checkpoint restoration, optimizer-state interventions and continued training should account for retained optimizer history rather than treating model parameters alone as the complete continuing learner state. Section 8 now distinguishes this contribution from earlier optimizer-state work.
We appreciate your emphasis on clarity and scientific significance. We hope the revised paper now makes the primary result, its quantitative magnitude and its remaining limitations straightforward to evaluate, and we would welcome your reassessment.