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Paper summary
The paper studies the acceptance gate problem in recursive self-improvement (RSI) loops, and aims to design a reliable method to decide whether candidate agent‑harness updates should be kept. The paper proposes TRUST, an online multiple hypothesis testing procedure to control the rate of false evolution across sequential RSI rounds. TRUST defines False Evolution Rate (FER) to measure the expected fraction of accepted updates causing unacceptable performance degradation, and combines an e-value testing process with an overlap correction for reused validation examples, and an LLM-based context‑aware error‑budget allocator to adjust testing levels.
The paper provides a set theoretical guarantees, including FER control under an overlap-bias assumption, consistency for accepting truly beneficial candidates, and a lower bound on final population‑level performance gain. Experiments are performed on three benchmarks (HotpotQA, DROP, APPS) over two open‑source LLMs (DeepSeek‑V4‑Flash, Qwen‑3.8‑Flash). It results show that TRUST achieves the highest final gain, and reduces the mean FER and the mean maximum drawdown dramaticallly.
Critical strengths
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Well-motived, relatively underexplored problems: Not just proposing harness edits, but deciding whether an improved candidate should replace the existing one. The paper clearly describes the problems of existing approaches: greedy gates suffer high inferior‑update acceptance, and existing FWER‑based statistical gates are too conservative and produce zero improvement.
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Suitable formulation and theoretical treatment for closed‑loop adaptive RSI: The introduction of FER is a nice adaptation of false discovery reasoning to this setting, and it distinguishes unacceptable loss, tolerated loss, and strict improvement via the margin. Under certain assumptions, the paper proves FER control, TER consistency, and a lower bound on final deployment gain. The whole method is modular and interpretable.
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Meaningful and solid experimental results: Experiments run in a closed‑loop editable agent harness with four components, including reasoning, routing, memory, and workflow. Evaluation separates validation data (used for gate decisions) from held‑out test data (only for reporting metrics). Eexperiments are conducted with multiple seeds, clear baseline comparisons, comprehensive ablations, and illuminating case studies.
Critical weaknesses
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Guarantee depends on a very strong assumption about adaptation reuse: The guarantee in Theorem 1 and 2 depends on Assumption 1, which is an uncalibrated and potentially very strong assumption. There, \beta represents the strength of the correction for data reuse, but the paper does not provide a procedure for estimating a valid \beta. Because a small fraction of reused examples can still yield substantial adaptation bias if their outcomes are memorized, or used to modify a global harness. While the proof is a valid if Assumption 1 holds, the paper does not currently establish that the deployed procedure satisfies the premise needed for the advertised “trustworthy” protection.
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Tolerated losses accumulate across rounds: Each accepted update is compared only with the previous one. Tolerated losses up to \epsilon may accumulate over many accepted updates, and Theorem 4 does not provide conditions under which these terms are smaller than the positive-effect term P_T. Thus, while the result is a useful decomposition of "missed gain" cost and "accepted loss" cost, it does not establish the conclusion that TRUST yields a nonnegative final gain. The paper should address this issue, for example, by testing against the best incumbent using a cumulative margin budget.
Questions for authors
Small validation pool size and narrow experiment coverage: All experiments use a fixed validation pool consisting of only 200 examples. Real‑world agent systems may have access to much larger or streaming validation data. How do TRUST’s safety power tradeoffs behave as the number of validation samples increases? In addition, the scope of experiments have not established that the method transfers across agent architectures, richer tool-use environments, longer horizons, or settings where updates to harness are more complex.
2 comments
[Response to Weakness 2]
We appreciate the reviewer’s thoughtful analysis and discussion of our theoretical decomposition and the further insights they provide.
Thus, while the result is a useful decomposition of "missed gain" cost and "accepted loss" cost, it does not establish the conclusion that TRUST yields a nonnegative final gain.
We have added Corollary 2 in Appendix F.2. Under its stated conditions, the lower bound on the round sample size in Equation (28) ensures , as shown in Equation (29).
The paper should address this issue, for example, by testing against the best incumbent using a cumulative margin budget.
We thank the reviewer for suggesting this solution. We interpret the reviewer’s reference to “the best incumbent” in two ways.
In each round, our proposer generates three candidates. We use historical samples to select the best candidate and then test it against the currently deployed incumbent. The deployment question is whether this candidate can replace the system's running solver with controlled risk under our assumptions. The gate serves this decision and can complement methods for generating stronger candidates through feedback and reflection.
The true best historical incumbent is not directly observable during self-improvement: test results are reserved for reporting. To test against the best past version, we would have to keep a full copy of each past harness version. However, keeping and retesting all past harness versions would become costly as the run progresses.
[Response to Question 1]
All experiments use a fixed validation pool consisting of only 200 examples. Real‑world agent systems may have access to much larger or streaming validation data.
We report additional results for a larger validation pool in Figure 7(f) and for fresh validation in Figure 7(c) (p. 10). At , TRUST achieves the highest mean final gain. When each round uses fresh validation examples, TRUST's final gain is pp and its observed is .
How do TRUST’s safety power tradeoffs behave as the number of validation samples increases?
We then jointly increased the validation pool size and the round sample size on HotpotQA/DeepSeek in Appendix B.4. Table 8 (p. 19) compares gain, TER, and across these settings. As increases, TER rises from to and , which is consistent with the convergence result in Theorem 3 under Assumption 2, while also rises from to . These settings reveal a trade-off between accepting a larger fraction of improving candidates and a higher false acceptance rate. Figure 12 (Appendix B.4, p. 20) additionally compares four noninferiority margins under the two larger resource settings. This suggests that achieving a higher gain also requires an appropriate choice of .
In addition, the scope of experiments have not established that the method transfers across agent architectures, richer tool-use environments, longer horizons, or settings where updates to harness are more complex.
Whether agents solving problems in complex environments face risks during self-improvement is an important question. We have made efforts to evaluate the gates on ToolHop [1], a complex tool-use benchmark that requires agents to interact with the environment. Figure 14 (Appendix B.7, p. 22) shows that TRUST achieves a mean final gain of pp, close to Greedy's pp and above PACE's pp. TRUST and PACE both have an observed mean of , compared with for Greedy. SGM-B and SGM-H accept no updates, with zero gain. In this complex setting, we again observe a high risk of performance degradation with Greedy.
References
[1] Junjie Ye et al. ToolHop: A Query-Driven Benchmark for Evaluating Large Language Models in Multi-Hop Tool Use. ACL, 2025.
[Response to Weakness 1]
We appreciate that the reviewers raised questions about the choice of β and sample size, which led us to reconsider these settings. Drawing on the different perspectives offered by all three reviewers, we have developed a more detailed response.
We acknowledge that the choice of β is a limitation of this work. Our work aims to improve model safety through multiple hypothesis testing instead of adaptive data analysis. The parameters q, ε, and β each have an interpretable role and fit naturally into the framework. We use β=0.01 as a shared default hyperparameter. To explain this choice and our experimental setup, we provide the following three analyses.
Empirical reuse bias. We updated Assumption 1 (p. 6) to bound the conditional reuse bias directly. This bias is half the difference between the expected gain on reused validation samples and the true gain, consistent with the intuition that validation reuse can lead to overly optimistic gain estimates. For every draw with ζt,i>0, it requires 21E[Dt,i−Δt∣Ht,i−1,Qt,i=1]≤β. Lemma 1 (Appendix C, p. 25) derives the null mean bound we used in the former version.
Our data span different histories, with too few observations under any one history to estimate the conditional bias directly. We therefore report the average reuse bias in each setting as a rough indication of its scale.
b=∣S∣1∑(s,t)∈S2Δs,tvali−Δs,ttest,
Δs,tvali=∑i=1τs,tQs,t,i∑i=1τs,tQs,t,iDs,t,i,Δs,ttest=ntest∑j=1ntestDs,t,jtest,
Here, the validation mean averages the paired gains over reused samples (Qs,t,i=1) among the τs,t recorded draws. The set S contains all seed and round pairs (s,t) with at least one reused validation sample. The test mean uses the paired gains Ds,t,jtest on the ntest samples in the independent test set.
All six averages fall below β=0.01, giving magnitude support for using this value as default. Remark. This calculation uses test set information and was performed after the experiments, which was not used to select the parameters before the experiments.
Mechanistic studies of β. In Appendix B.2, we study how β relates to the size of the validation pool and the amount of historical feedback supplied to the proposer. Table 5 (p. 17) compares N=200 and 300. Mean FER0 falls from 23.33 to 20.00 at β=0 and from 10.00 to 0 at β=0.01. It stays zero at β=0.03,0.05. This indicates that the test becomes more conservative as N increases. In other words, as N decreases, sample reuse increases and the test becomes more aggressive. We also compare feedback from the most recent round with feedback from all completed rounds (Table 6, p. 18). Using the most recent round leads to one fewer accepted update across five seeds, suggesting slightly more conservative testing when less historical feedback is used. These patterns are consistent with the idea that reusing validation samples introduces optimistic bias, leading to more aggressive testing. So we need the overlap correction ζt,iβ. They provide support for the connection between overlap and β.
Performance and evaluation cost. Our choice of N, n, and T also reflects evaluation cost. The validation resource comparisons are now shown together in Figure 7(d–f) (p. 10). Across these additional settings, TRUST achieves higher mean final gains than all four baselines, while SGM-B/H make no updates. The final gains of all five methods change only slightly relative to the main experiment when we increase T, n, or N separately. Additional TRUST resource sensitivity trajectories remain in Figure 10 (Appendix B.4, p. 19). We therefore choose N=200,n=40,T=30 to balance performance and evaluation cost.