acceptodds
Under review as a conference paper at ICLR 2027

Where Self-Evolving Memory Systems Lose Their Gains: A Full-Loop Audit

Abstract

Self-evolving memory systems use large language model (LLM) agents to evaluate performance, diagnose failures, and revise shared memory components. These loops often improve early and then plateau. Their logic rests on three assumptions: evaluation identifies failures, edits repair them, and accepted repairs persist. We audit this chain in several self-evolution methods for memory systems on two conversational memory benchmarks, using question-level evidence independent of the agent. We find that evaluation provides unstable feedback for repair. Reevaluating an unchanged system changes which questions fail. At least half of the accepted single-step gains fall within this variation. Even edits that target the bottleneck stage do not prevent regressions. These edits raise scores much more often than other edits. Yet they break previously correct answers just as often, because the components they change are shared across queries. Across rounds, repairs do not accumulate reliably. Repairs decline toward the level of answer flips observed in an unchanged system. Regressions, however, persist. Addressing these weaknesses improves individual revisions but does not ensure sustained progress. We extend MemPro, one of the audited methods, with verified feedback, repair rounds, and paired acceptance. Development accuracy rises by up to 16.9 percentage points. Yet final held-out gains are at most 3.4 points, within the original loop's rerun variation. The remaining gains suggest that the bottleneck returns to feedback. They are below what a development set of the original size can resolve. Sustained self-evolution therefore requires repeated evaluation and question-level tracking of repairs and regressions. Selecting revisions also requires enough evidence to distinguish gains at the intended scale from evaluation variation.

Primary area:
foundation or frontier models, including LLMs
Keywords:
memory systems, LLM agents, self-evolving agents, self-improvement, failure attribution, causal intervention

Reviews

Among:
Shape:
1234this paper, Top 4%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.33 over 3 reviews, above 96% of the others.
Reviewer_PTC2OpenReview ↗
Rating
3(+2)
Confidence
3
Informativeness
2
Presentation
2(+1)
Soundness
2
Read review
Paper summary

This paper investigates why self-evolving memory systems often achieve substantial improvements in early iterations but struggle to make further progress. The authors analyze three stages of the evolution loop, and through experiments on EvolveMem, AutoResearchClaw, MemPro, and GEPA, and find that evaluation outcomes can be unstable, edits frequently introduce regressions, and previously repaired questions may fail again in later iterations.

Critical strengths

1: The paper studies an important and timely problem. Most existing work on self-evolving agents focuses on improving final performance, while paying relatively little attention to what happens during the evolution process. Understanding why performance improvements plateau is valuable for developing more reliable self-improving systems.

2: The experiments cover multiple evolution methods and include several useful diagnostic analyses. The repeated evaluations, model substitutions, and comparisons of aligned and misaligned edits provide valuable empirical evidence.

3: The question-level analysis provides useful insights beyond aggregate performance. Rather than reporting only the final accuracy, the authors examine which questions are repaired, which previously correct answers become incorrect, and whether repairs persist across iterations.

Critical weaknesses

1: Abstract is too abstract and hard to follow, as it lacks a clear logical flow. Also the paper is unnecessarily difficult to follow. Although the underlying motivation is relatively straightforward, the presentation introduces a large number of configurations, metrics, and terminology before clearly establishing the main research questions. The experiments often read as a collection of experiment logs rather than a coherent investigation, making it difficult to understand which findings are central and how they support the paper's main conclusions.

2: The paper identifies several failure patterns, but their causal contributions to the performance plateau remain unclear. The central claim is that performance gains are lost across three stages of the self-evolution loop. However, most experiments establish correlations between these failure patterns and performance changes, rather than isolating how much each factor contributes to the plateau.

3: Limited evaluation setting. Although the paper considers several evolution methods, the experiments are restricted to two conversational memory benchmarks. LoCoMo contains only ten conversations, and the Mem-Gallery experiments use caption-only scenarios. For an analysis paper, I'd like to see a comprehensive inclusion of different methods.

Questions for authors

1: Can the authors better distinguish the contributions of evaluation noise, edit-induced regressions, and bottleneck exhaustion to the observed plateau?

2: How do the authors distinguish false repairs from genuine improvements on questions with unstable baseline outcomes?

While AI-assisted research is becoming increasingly common, authors remain responsible for ensuring the scientific rigor and quality of their submissions. I encourage the authors to conduct a more thorough evaluation, carefully validate their claims and experiments, and ensure the presentation is sound and well-organized before submitting to a venue such as ICLR.

1 comment

Thank you for the detailed response and additional experiments, which address most of my concerns. I have updated my rating in support of the paper.

I sincerely encourage the authors to pay more attention to the clarity, coherence, and scientific rigor of the manuscript before future submissions. First impressions can be important in peer review, and a well-written paper makes it easier for reviewers to appreciate its contributions. I hope the authors will continue refining the manuscript to make it more coherent and easier to follow. Good luck!

Reviewer_R48uOpenReview ↗
Rating
4(+1)
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper is tackling a memory-related problem in LLMs. A memory system in general helps LLMs to be able to track the long conversations, by storing the extracted facts and retrieving them later. One mechanism for these systems is using another LLM agent for tuning the pipeline in terms of looking for the failures, trying to fix it by editing a shared component and if it helps to improve the results keeping this edit and continuing this cycle. However, the improvement seems to be saturated after few cycles, even though this editing loop is keep going. Authors' main claim is that this issue is caused by three main assumptions which are not always true. These assumptions are as follows: the evaluation can spot the issue correctly, the edit can fix the issue that it is targeting, and these fixes could stay useful over time. Authors claim that there are issues for all these assumptions, like identifying different failure points when they ran the same system multiple times, which contradicts the first assumption; or edits that help and add real fixes by targeting the right failure can still break previously correct answers, which contradicts the second assumption; or the gain from fixes decrease over multiple rounds of running the system, while damage stays, which contradicts the third assumption. Authors also proposed remedies for each of these issues. These remedies improved results on the development set, but on the held-out set the gain is not higher than what we can get from just running the original loop again. Authors' explanation for this observation is that remaining improvements are so small that a development set of this size can not differentiate them from random changes.

Critical strengths

I think the main strength of this paper is defining the problem in a clear way by identifying three assumptions which seem to be accepted widely without clear evidences or justifications, and examining those assumptions using well-defined and appropriate mechanisms that correctly target and test the issue in each assumption. Also, authors tried to fix the issues they identified, and when they observed the negative results, they reported them transparently, with an explanation for why the fixes did not help the held-out set.

Critical weaknesses

One issue I noticed is that the LLM agent which has been used as the judge may itself be a major source of the instability the paper reports. When the same unchanged system is evaluated again, the amount of answers that change is about three times higher under the LLM judge than under F1 scoring, and the paper also shows that switching to a different judge can turn a positive held-out gain into a negative one. However, as far as I was able to understand, authors haven't separated how much of the instability comes from the judge and how much from the system itself. I think this is important, because the paper’s main advice about more frequent evaluation and using a larger development set, only makes sense if the noise comes from the system itself.

Questions for authors
  • Following up on the point I mentioned in the weakness section, I would like to ask authors to elaborate more on the source of the instability they are reporting. Specifically, can you break down where the instability comes from? is it coming from randomness in the model itself, randomness in rebuilding the memory, or from the LLM judge? This clarification would help to identify how much each factor matters in terms of its contribution to the instability. If the judge is the main cause, then evaluating more often or using a larger development set might not be the best solution.

  • In Table 4, rerunning original unmodified loop gives a larger held-out improvement than any of the proposed fixes. How should this be interpreted? Does it mean the fixes don't make any real difference compared to the original loop? I think if authors can rerun the best fix several times with different random seeds this becomes more clear.

  • As far as I can understand, authors' explanation for why improvement saturates is that the remaining gains are too small to be detected for a development set with this size. However, I think this claim is based on calculation, not a direct experiment. The appendix mentions that a larger development set has been tried. I think if that experiment shows if a larger set allows gains to be accumulated or not, it should be in the main tex. Because this is the most clear and direct test of the paper’s conclusion.

Reviewer_yGX1OpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper studies why self-evolving memory systems often improve early and then plateau. It decomposes the evolution loop into three links: evaluation supplies failures and scores; diagnosis and editing attempt to repair them; and accepted revisions are expected to retain earlier repairs. The authors audit these links with repeated evaluation, intervention-based failure-stage labels, and question-level ledgers of repairs and regressions. Across EvolveMem, ARC variants, MemPro, and GEPA on LoCoMo and caption-only Mem-Gallery, the paper reports that unchanged systems produce substantial outcome flips, aligned edits repair more failures but still regress previously correct answers through shared components, and repair volume declines across rounds while regressions persist. A final set of MemPro interventions adds verified feedback, failure-stage information, repair rounds, and paired acceptance. These interventions change local behavior but do not produce a clear held-out advantage, motivating a development-set-resolution explanation.

Critical strengths
  1. The question-level, parent-paired audit reveals effects that aggregate scores hide. Pairing every revision with the version it actually modifies and counting both repairs and regressions is a well-motivated measurement choice (p. 4, Sec. 2, Eq. 3). It directly supports the paper’s most interesting result: bottleneck-aligned edits repair substantially more failures, yet aligned and misaligned edits can regress previously correct answers at similar rates (p. 6, Table 2 and Fig. 2). Tracking the same quantities along accepted trajectories further distinguishes residual improvement from turnover (pp. 7–8, Table 3; pp. 40–42, Tables 23–27). This is useful new knowledge for evaluating self-evolving systems, independent of whether the proposed interventions succeed.
  2. The central descriptive findings receive unusually broad triangulation. The paper examines fixed-version reevaluation and whole-loop reruns (pp. 4–5, Table 1), two datasets, several loop configurations, and both accepted and rejected edits. Appendices repeat the main measurements under GPT-4o/GPT-4o-mini substitutions (pp. 34–36, Tables 15–17), test judge sensitivity on fixed answers (pp. 38–39, Tables 18–19), and check probe-label reliability with repeated probes, a second solver, and a manual audit (pp. 20–21, Tables 11–12). Some effect sizes and exceptions vary, but the recurring combination of feedback flips, repair/regression asymmetry, and declining late repairs makes the core audit more convincing than a single-system case study.
  3. The paper is clear about measurement conventions and important limitations. The authors distinguish selection metrics from audit metrics, define repetition boundaries and ancestry, and provide the probe and acceptance algorithms and prompts (pp. 18–22, Appendices B.5 and C; pp. 23–31, Appendix D). They also explicitly note that stage labels cover only the attributable subset, held-out questions share conversations with development questions, retention is measured over adjacent steps, and repeated held-out inspection would require a fresh test set for confirmatory claims (p. 45, Appendix H). These qualifications improve interpretability and reproducibility.
Critical weaknesses
  • The intervention results do not support some of the section’s strongest causal wording. Section 6 states that “each change removes the loss it targets” and later suggests that the plateau “traces back to Link I” (p. 8). However, false-repair shares are higher under E2 and E3 than E0 in Table 4 (66% and 71% versus 52%), and E3+repair reduces stable regressions only from 3.0 to 2.7 per revision (p. 9, Table 4). The appendix reports that none of the nine E3+repair children is accepted, and only three of the eight within-round repair comparisons are significantly positive while one is significantly negative under the reported threshold (p. 43, Table 28). Moreover, each arm runs once on one split, and the repair arms use substantially more agent sessions and tokens; no original-loop control with the same repeated-evaluation budget is run (pp. 43–44, Table 30). These results are valuable as a bounded negative study, but they do not establish that every intervention reliably fixes its targeted link or that feedback resolution is the dominant remaining cause. This weakens the third contribution more than the descriptive audit.
  • The development-set-resolution argument is not yet matched to the acceptance rule whose plateau it is meant to explain. The main text compares late accepted steps of roughly 1 pp with a 5.8 pp single-evaluation root band (p. 8, Sec. 6), and Appendix F.4 derives a sample-size bound for a single comparison using flip rate ρ (p. 44, Table 31 and surrounding text). The repair arms, however, evaluate both incumbent and child twice and accept through stable-transition classes that exclude fragile questions (p. 22, Algorithm 2). The effective variance of that paired, filtered statistic need not equal the single-evaluation score band. The larger-split experiment is consistent with the resolution concern but examines one original-loop run rather than the paired gate (p. 39, Appendix E.6). Thus, limited development evidence is a plausible explanation, not yet a demonstrated diagnosis of the intervention plateau.
  • Uncertainty and selection effects in the pooled audit deserve more direct treatment. Tables 2–3 pool correlated edits and question outcomes from shared conversations and trajectories, but the main aligned/misaligned and early/late contrasts lack conversation- or run-level uncertainty summaries (pp. 6–8). The paper appropriately avoids independence-based significance claims for adjacent retention counts (pp. 41–42), but similar dependence concerns apply to other pooled comparisons. In addition, the bottleneck reference is computed only from attributable failures—about a third of observed failures in the stated MemPro analysis—and is not necessarily representative of all failures (pp. 4–5, Sec. 3; p. 45, Appendix H). The robustness checks mitigate these concerns, but per-conversation/run distributions or cluster-resampled intervals would clarify whether the headline effect sizes are driven by a small number of trajectories or by the selected attributable subset.
Questions for authors
  • Can you add a budget-matched original-loop control that receives the same repeated evaluation/replay budget as E2/E3, or explain why the existing E0 rerun is sufficient for attributing the intervention outcomes? If additional runs are not feasible, can you revise the causal wording in Section 6 to reflect the single-split, single-run evidence?
  • Can you derive or empirically estimate the noise band for the actual paired, stable-transition acceptance statistic in Algorithm 2, rather than using the single-evaluation score band to explain its late-round behavior?
  • Using the existing audit records, can you report per-conversation/per-run effects or cluster-resampled intervals for the principal aligned-versus-misaligned and early-versus-late contrasts, and show how sensitive the bottleneck conclusions are to the unattributable-failure subset?

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