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Under review as a conference paper at ICLR 2027

Present Action Is Not Persistent Write: Causal Rights of Optimizer History in Replay-Free Continual Learning

Abstract

Stateful optimizers normally grant a learning signal two permissions at once: it may change parameters on the present update, and it may write persistent state that conditions future updates. We ask whether these permissions are experimentally separable in replay-free continual learning. We study a strict replay-free Split CIFAR-100 learner with one fixed 100-class head, current-task-only training, raw global inference, and no task routing, model growth, or post-hoc calibration. In a five-seed action-by-write factorial, a write-only intervention, denying the source its same-update parameter action while retaining its persistent Adam write, increases current acquisition by 0.00774 relative to the comparator, while increasing forgetting by 0.00604 and old-to-final recapture by 0.00569; the action-only cell increases acquisition by only 0.00058. Successive interventions localise this durable pathway predominantly to first-moment state, accumulated within-task history, and the current-relative orthogonal action of inherited history. We then follow acquisition-bearing history across the task lifecycle: in four independent paired seeds, with six origin tasks nested within each seed, all 24 provenance units show source-distinct classifier weights and Adam moments at the current-to-old boundary followed by source-distinct row-relative old-row displacement under exactly zero natural classifier gradient. This provides direct cross-lifecycle provenance evidence, not behavioural mediation. Finally, a function-preserving reparameterisation with transported Adam state leaves final features, all 100 logits, predictions, and the classifier head exactly unchanged at the branch, yet all four fresh pairs diverge on the first lawful subsequent update and develop different continual-learning trajectories. Within this tested Adam setting, present parameter action and persistent-history ownership are distinct causal rights, and persistent optimizer history contributes to the causal state governing future learning.

Primary area:
transfer learning, meta learning, and lifelong learning
Keywords:
continual learning, catastrophic forgetting, replay-free continual learning, optimizer state, stateful optimization, causal interventions

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.25 over 4 reviews, above 2% of the others.
Reviewer_97qUOpenReview ↗
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2
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3
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2
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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
  1. 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.

  1. 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
  1. 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.

  1. 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
  1. 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.

  1. 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.

  1. 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.

Reviewer_ah7cOpenReview ↗
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Paper summary

The authors investigate the effects of using the Adam optimizer in a replay-free continual learning setting when the architecture uses a shared head for classification of different tasks. Their findings suggest the behavior of the different mechanisms of Adam during learning.

Critical strengths
  1. Examining the effects of a stateful optimizer in replay-free continual learning is a timely and important problem.
Critical weaknesses
  1. The experiments are very limited, with only one benchmark evaluated and lacking robustness checks and clear findings.
  2. The writing quality is very low, being very hard for the reader to understand the details of the methodology or the takeaways from the findings.
Questions for authors
  1. The authors propose a new split for the CIFAR-100 dataset separating into 10 tasks. More discussion is needed why this split is done, and why the authors do not use the CIFAR-10 benchmark directly that is already split into 10 tasks.
  2. Additional benchmarks, expanding the study to continual reinforcement learning benchmarks is needed to evaluate the effects suggested in the manuscript.
  3. The magnitude of the changes discussed in the results are very low and do not have any discussion on what they mean in continual learning settings.
  4. The quality of the writing and the figures is very low. The manuscript needs re-editing to improve the overall writing, figure quality, and avoid the use of jargon.
  5. What are the main takeaways for continual learning practitioners? What changes do the results suggest for choosing different optimizers in these settings?
Reviewer_cZRXOpenReview ↗
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Paper summary

This paper investigates a replay-free incremental learning method. The paper defines the component of the auxiliary gradient (excluding the target suppression component) that is orthogonal to the controller gradient (see Equation 1 and Appendix B). During each parameter update, the system computes two Adam candidate results based on the same preceding state, which are used to perform the current parameter update and persistent write. Experiments are conducted on the Split CIFAR-100 dataset (containing 10 tasks; the model is a two-layer convolutional neural network with 121,892 parameters and a fixed 100-class output layer; the optimizer is Adam; each task is trained for 3 epochs). In 5 random-seed experiments, the configuration that only performs the "write" operation shows improvements in relative accuracy, forgetting level, and old-to-final recapture compared to the baseline.

Critical strengths
  1. The paper reports seed-level results (Tables 5–8), keeps cohorts separate, treats the 24 lifecycle units correctly as nested within four seeds, and reports negative and falsifying results (Table 12).

  2. The experimental results are subject to strict limitations, as they are explicitly stated to hold true only under specific conditions.

Critical weaknesses
  1. The motivation remains unclear. I only understand the inherent limitations of stateful optimizers and the shortcomings of continuous learning without replay. These shortcomings lie in the findings that previous experimental approaches failed to separate the individual components. However, the paper relies heavily on non-standard terminology (“causal rights”, “authority”, “lawful update”, “afterlife”, “phenotype”, “recapture”), lacking of elegant word choice in reader-oriented academic papers. Under the case, the manuscript is more like an experimental report than a systematic and academic paper. Unlike any article I've seen before, this seems too much like an autoresearch product.

  2. The metrics used in this paper are derived from the CIFAR-100 dataset. However, no absolute accuracy figures are provided, so readers and I cannot determine whether a change of 0.77 percentage points is significant relative to the baseline. And it is therefore unclear whether the findings bear on continual learning practice, and the paper proposes no downstream method that uses them.

Questions for authors
  1. For standard cross-entropy sources, other architectures or datasets, other task sequences, or other stateful optimizers (such as those driving SGD), do the main results still hold?

  2. What are the absolute current accuracy, forgetting rate, and final old task accuracy for the comparator and the completely correct case?

I am unable to distinguish between primary and secondary experiments, most of the experimental results are in the appendix, and the value of this work cannot be assessed due to the lack of clear statements and explicit downstream applications. Therefore, I recommend rejection.

2 comments
AuthorsOpenReview ↗

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.

  1. A clearer scientific question and presentation. The revised Introduction now asks one question: can a newly computed learning signal's contribution to today's parameter update be separated experimentally from its contribution to retained optimizer state that influences later learning?

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.

  1. Absolute results and practical significance. Table 1 (p. 4) now reports absolute current acquisition for all four original arms: neither 40.944%, action-only 41.002%, write-only 41.718%, and both 41.862%. The corresponding forgetting values for neither and both are 27.253% and 27.949%, and final old-task accuracies are 14.562% and 14.762%. Table 2 provides paired uncertainty.

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.

  1. Generality beyond the original source and setting. A separate post-review experiment implements the complete four-arm factorial using a conventional global-cross-entropy-derived backbone source. Across five fresh paired seeds, write-only acquisition improves by +0.874 pp (95% CI [+0.422, +1.327]; Table 3). The source overlaps the controller, so we do not claim fully independent-objective generality.

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.

  1. Scientific contribution and practitioner takeaway. We do not propose a new continual-learning algorithm, forgetting remedy or preferred optimizer. The contribution is a controlled experimental separation of two consequences ordinarily changed together by source-on/off ablations.

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.

After carefully reviewing the revised manuscript and the authors' responses, I appreciate the improvements made. I find that my main concern regarding the presentation. I would encourage the authors to place greater emphasis on independent scientific reasoning and critical analysis, rather than relying excessively on AI-assisted tools in the research and writing process. Overall, my assessment remains unchanged.

Reviewer_fWkYOpenReview ↗
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Informativeness
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1
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Paper summary

The paper studies Adam optimizer where a gradient term's effect on the current weight update can be separated from its effect on later updates through Adam's running averages, and which of the two matters for forgetting in continual learning. The authors train a small CNN on a standard class-incremental benchmark and, for one extra gradient term, choose at every step whether the term moves the weights and, separately, whether it is saved into Adam's running averages. They find that saving the term without using it for the step produces most of its effect on learning and forgetting, while using it for the step without saving it has almost no effect. They attribute this to Adam's running average of gradients built up over each task, and add experiments showing that this saved state keeps moving a task's classifier weights after the task ends, and that two networks with identical outputs but differently scaled weights train differently. They do not propose a method; they conclude that Adam's saved state is part of what a continual learner carries forward, so the weights alone do not determine how training will continue.

Critical strengths
  1. The experimental design separates the two effects directly: at every step, two Adam updates are computed from the same optimizer state, one with and one without the extra term, and the run chooses independently which one moves the weights and which one is saved; the supplied code checks that each variant does this.

  2. The reporting shows clearly with per-seed values are shown, including a seed whose sign goes against the mean (Table 5); negative results are kept (Table 12); seeds from different experiments are not pooled and the 4 seeds over 6 tasks in Section 6 are not counted as 24 independent samples.

Critical weaknesses
  1. Most of the main results follow from Adam's update rule and from how the extra term was built, and the paper neither tests nor discusses this. With beta1 = 0.9 (Adam's decay rate for the gradient average), a gradient enters the average with weight 0.1 at the current step and with weight 0.1 x 0.9^k from k steps earlier. Using the term only for the current step keeps the 0.1 share, saving it without using it keeps all the earlier shares, which add up to about 0.9. If the term changes little over about ten consecutive steps, the expected split is roughly 10% and 90% of the full effect; the paper reports 6% and 84%. The follow-up results are expected in the same way:
  • Build-up within a task: a gradient's weight in the average falls to about 4% of its starting value after 30 steps (0.9^30 = 0.04), while a task lasts 237 steps, so clearing the saved history at each task boundary should only affect the start of each task. Table 7 shows that keeping it across tasks adds 0.08 points.

  • Gradients versus squared gradients: the squared term enters Adam's second average with weight 0.001 (1 - beta2) rather than 0.1, so a much smaller effect is expected there, and Table 6 shows -0.04 points.

  • Direction: the term is built to be perpendicular to the main training gradient, so its saved history also stays mostly perpendicular to it. The part along the main gradient is under a quarter the size of the perpendicular part, and the steps it produces are under a fifth the size (0.000224 vs 0.001219, Appendix G). The comparison therefore mixes direction with size, and it supports no claim about direction until the along-gradient part is rescaled to the same size.

  • Classifier weights of finished tasks: these get exactly zero gradient by design, because in the code no loss term sends gradient to them. With zero gradient, Adam still moves a weight by an amount set by its saved averages, shrinking by a factor of about 0.9 per step, so if the saved averages differ between runs at the end of a task, the later movement must differ too. In addition, the code (in src/lifecycle.py) counts two tensors as different whenever their SHA-256 hashes differ, so a one-bit difference counts, and 24 out of 24 would follow from almost any change to training.

  • Rescaling: when a channel is multiplied by s, the code divides the gradient average by s and the squared-gradient average by s^2 (supplementary code: src/predictor_identity.py), which leaves Adam's step for each weight unchanged. A step of the same size in rescaled weights is a different change to the network's outputs, so the two runs must diverge at the first step; this follows from Adam's per-weight normalisation and needs no seeds to establish.

  1. The evidence and controls are too narrow for the general claim in the title, abstract and conclusion, namely that a gradient term's effect on the current step and its effect through Adam's saved state are distinct. Everything uses one benchmark, one task order, one two-layer CNN, one Adam setting (learning rate 1e-3, betas 0.9 and 0.999) and one extra term with loss weight 0.04. Three further gaps:
  • No absolute numbers. Only differences between runs are reported, never the accuracy or forgetting of any run, including the run without the extra term, so one cannot tell whether the main result, a gain of 0.77 percentage points in accuracy from saving the term without using it, is a large or small change relative to that run's accuracy.

  • No null controls. The code runs with cuDNN benchmark mode on (set_seed in src/data.py), so two runs with the same seed are not bit-identical, and any small change to Adam's state makes runs drift apart. Two controls are missing: the spread between two runs without the extra term that use the same seed, and runs that save a random vector, or the negated term, of the same size in place of the term. Without them, one cannot tell whether the effect depends on what the term contains or only on perturbing the gradient average by that amount.

  • No uncertainty estimates. The authors judge effects against a cutoff of 0.5 points fixed in advance, not against variation between seeds. From the per-seed values in Table 5, saving the term without using it gives paired t-statistics (4 degrees of freedom) of 6.6 for accuracy (p = 0.003), 3.3 for forgetting (p = 0.03), and 1.7 (p = 0.16) for the third metric, the share of old-task test images that the final model assigns to the last task's classes, where one of the five seeds has the opposite sign. The abstract reports all three as effects, but the third cannot be distinguished from zero at the 5% level.

As it stands, the paper supports a statement about one term in one small setup, measured as differences of under one point whose size relative to the baseline accuracy and to run-to-run noise is unknown.

** The figures in the paper are also disproportionate and needs to be properly formatted.

Questions for authors
  1. If you repeat the main comparison with beta1 = 0.5 and 0.99, and with SGD with momentum, does the share of the effect that comes from saving the term without using it follow beta1? If it does, what does the paper show beyond the weights of the gradient average?

  2. How far apart are two runs without the extra term that use the same seed, under the same GPU settings? What happens if a random vector, or the negated term, of the same size is saved into the gradient average instead of the term?

  3. Please report absolute values for the run without the extra term: accuracy on each task right after it is learned, forgetting, final accuracy on old tasks, and final accuracy on the last task. Please also report the differences in final old-task accuracy and final last-task accuracy, which the supplied code already computes. Does saving the term without using it change final average accuracy at all?

  4. Are the loss on only the current task's outputs and the restoring of other tasks' classifier weights used in all experiments in Sections 4-5? Why is the restoring turned off in Section 6, and do the Section 4 results hold without it?

  5. Since the classifier weights of finished tasks have zero gradient by design, is their later movement anything more than a fixed function of their weights and Adam state at the end of the task? How are the percentages in Table 10 normalised, and what range do you get for two runs that differ only by a negligible perturbation?

  6. In Appendix G, what happens if the part of the saved history along the main gradient is rescaled to the size of the perpendicular part before it is applied?

  7. Do any of the results hold with a different extra term (for example the auxiliary loss on the correct-class score, Eq. 11), a larger network or a second benchmark?

1 comment
AuthorsOpenReview ↗

Revised Evidence — Adam Recurrence, Source Controls and Numerical Repeatability

Thank you again for your detailed examination of the optimizer recurrence, implementation and experimental limitations. Following our earlier response, we have uploaded a substantially revised manuscript and anonymous supplement, including new experiments directly motivated by your concerns.

  1. Adam recurrence and novelty. We agree that Adam's moment recurrence, history decay, zero-gradient parameter motion and parameterisation sensitivity are established mathematics. Section 4.2 explicitly acknowledges this. The approximate 10/90 first-moment weighting is not, by itself, a quantitative prediction of the observed action/write accuracy decomposition: second moments, evolving gradients and subsequent trajectories also change. Our contribution is the experimentally controlled, repeated same-step counterfactual that independently assigns a newly computed source's immediate parameter action and retained optimizer-state write.

  2. Absolute outcomes and uncertainty. Tables 1–2 now report all four original arms and paired uncertainty. The comparator achieves 40.944% current acquisition, versus 41.718% for write-only. The paired difference is +0.774 pp (95% CI [+0.450, +1.098]). Forgetting worsens by +0.604 pp, and final overall accuracy improvement is not established.

  3. Matched source-content controls. A separate post-review five-seed experiment (§7.2, Table 5) finds that the original focal write exceeds a globally norm-matched, controller-orthogonal random write by +0.870 pp (CI [+0.538, +1.202]) and a sign-negated write by +1.924 pp (CI [+1.223, +2.625]). These results constrain a generic matched-perturbation explanation, without matching every Adam coordinate or subsequent gradient trajectory.

  4. Numerical repeatability. We measured non-negligible Z-only same-seed variation, including maximum differences of 0.80 and 0.84 pp under a contemporary, nonidentical CUDA environment. We retain this adverse result explicitly (Appendix K). A redesigned matched Z/write-only repeat found +0.958 pp across five historical seed clusters (95% CI [+0.674, +1.242]), with all ten process-pair contrasts positive. This supports bounded matched-effect repeatability under an extracted two-arm execution graph, not historical bitwise determinism or complete original-graph reproduction.

  5. Further factorial validation and history sensitivity. A new conventional-source complete four-arm experiment finds a +0.874-pp write-only acquisition effect across five fresh seeds (Table 3). A separate eight-seed β₁-policy experiment finds a prespecified +1.420-pp interaction between β₁ = .99 and .50, directionally compatible with Adam's recurrence but not identifying a unique mediator.

The equal-magnitude controller-parallel directional control and lifecycle numerical-null baseline remain unperformed. We preserve these limitations rather than claiming that all mechanistic alternatives have been excluded.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Revised Manuscript and Anonymous Supplement — Summary of Changes

We thank the reviewers for their detailed and constructive feedback. We have now uploaded a substantially revised manuscript and an updated anonymous supplement.

The original five-seed action/write factorial remains the paper's central contribution. The revision retains that experiment while substantially improving the explanation, reporting and evaluation of its scientific significance.

The principal changes are:

  1. Clarity and reproducibility: A clearer introduction and intervention diagram, absolute four-arm results, paired confidence intervals, the exact old-to-final metric, and a more focused discussion of novelty and limitations.
  2. Independent experimental validation: A separate post-review conventional-source complete four-arm factorial (five fresh paired seeds) finds a +0.874 percentage-point write-only acquisition contrast, 95% CI [+0.422, +1.327].
  3. Additional controls: Random and sign-negated source comparisons, Adam β₁ sensitivity, and numerical-repeatability tests. Importantly, the revision reports non-negligible CUDA variability rather than concealing it.
  4. Broader training settings: Evidence across benchmarks, architectures and optimizers, including recovered and hash-verified momentum-SGD executable source and an archived forensic replay.

The new results are explicitly distinguished from the original submission. Negative findings remain: forgetting can worsen, final overall accuracy improvement is not established, and neither universal causal topology nor exclusive first-moment mediation is identified.

The anonymous supplement includes evaluation records and a CPU statistical verifier. We have also provided targeted responses to the individual reviews.

We appreciate the opportunity to have the revised work assessed on its clarified scientific claims and evidence.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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