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Under review as a conference paper at ICLR 2027

Quality-Blind Detection of Settling in Agentic AI Loops

Abstract

In an agentic AI loop, a generator proposes a change, an evaluator accepts or rejects it, the accepted change is applied, and the cycle repeats. The loop usually cannot see the true quality of what it produces, so practitioners often give it a fixed budget of rounds, and the loop continues to run even after it has stopped improving. In this paper, we study what a quality-blind detector that sees only the artifact and the evaluator's accept or reject decision can conclude about whether a loop has settled, and propose a stopping algorithm that detects the settling. We first show that no such detector can tell whether the quality is rising or falling, and the most it can claim is a bound on how much the quality could still change, in terms of how much the artifact keeps changing. To measure that change, we hash any artifact into a sketch whose update across a round is the round's edit. On the path of those sketches, the coherence measures the share of the magnitude of the recent updates that carries the artifact a net distance. Once a loop has settled, its successive edits no longer change the artifact in a common direction, and we derive the value that the coherence takes at that point, as a closed-form function of the algorithm's decay setting. Our algorithm, named LoopStop, scores each change by how far its coherence falls below that value and accumulates the scores over the rounds that changed the artifact. A rejected round enters the sum as a change of magnitude zero, so a loop whose evaluator has stopped accepting is covered by the same accumulation. Our evaluation shows that LoopStop delivers higher quality than the next best adaptive baseline on average across multiple families of loops, at approximately fewer rounds.

Primary area:
foundation or frontier models, including LLMs
Keywords:
Agentic AI, large language models, control algorithm, statistical testing

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 3 reviews, above 85% of the others.
Reviewer_dAfpOpenReview ↗
Rating
3(+1)
Confidence
2
Informativeness
2
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Paper summary

In this paper the authors study a practical problem of determining when to stop an agentic loop system without access to its true quality of the repeated generated artifact. Overall, the authors demonstrate an important point that quality blind assessors cannot determine the true quality of the artifact generated. Now this is an important insight to the community specially in current times where lot of research and engineering work is being spent to come up with auto-research. This observation is also what motivates their approach of measuring coherence of updates to determine when to stop dynamically. Through experiments across different agentic loop baselines, they show that their method achieves 8% high quality while using almost 50% the iterations.

Critical strengths
  1. The proposed work by the authors are timely and solve and important problem. the observation that additional iterations do not always improve quality AND quality blind assessors cannot determine the true quality of the artifact generated are particularly interesting.

  2. The computation efficiency argument is supported through experiments. For e.g in table 2, loopstop achieves very similar accuracy but with much lower costs (faster latency) making the approach useful for practical applications.

  3. Expanded details on design ablations are provided in appendix I improving the transparency of the experimental methodology. For e.g. they discuss cross-fitted baseline comparisons, paired per-seed results, and scenario-level evaluations.

Critical weaknesses
  1. The theory analysis primarily measures changes in the artifacts rather than their quality. For e.g., in Theorem 1 assumes an quality function, allowing the construction of an adversarial evaluator using (1-q). While this analyses the limitation of quality-blind detection, it does not demonstrate that settling is a reliable indicator of when an agent should stop. For e.g., a loop can consistently degrade artifact quality while producing coherent updates, which would not necessarily trigger the proposed stopping condition.

  2. On some datasets like ARC-AGI, BigCodeBench-Hard, MLAgentBench-Kaggle, the improvements are relatively small and are often within the reported standard errors for the quality. Furthermore, BigCodeBench-Hard and MLAgentBench-Kaggle use only 3–5 seeds as the authors also acknowledge due to resource constraints, making it difficult to establish statistical significance. Interestingly, also as shown in Table I.4 with cross-fitted thresholds, PoU outperforms/at part with LoopStop on ARC-AGI and BigCodeBench-Hard. This still preserves the benefits of reduced loops though stopping criterion may not work as effectively for loops exhibiting slow but consistent improvements.

  3. Baseline's performance comparison are done using a single fixed hyparameteres as discussed in appendix I.7. The authors are encouraged to discuss more if this choice is optimum for other baselines for fair comparison. Also, given loopstop terminates early than other baselines, the authors are also encouraged to see how other baselines perform when terminated early at similar number of loops. This would be a useful baseline to understand if other baselines are able to reach similar quality but degrade further due to increased iterations.

Questions for authors
  1. Appendix I.7 mentions that the design choices were made using trajectories from the evaluated benchmarks. As an experiment, can the authors provide results where the algorithm is developed on one set of benchmark families and evaluated on entirely held-out families to better establish its generalizability?

  2. Refer to weakness-3.

6 comments
AuthorsOpenReview ↗

Response to Reviewer dAfp (1 of 2)

W1: Coherent Updates That Degrade Quality

A coherent decline can delay LoopStop's stop. On both controller families, whose quality decreases after its peak, LoopStop still delivers higher quality than every baseline (Table R1 in the General Response). PoR and PoU use more rounds there. By Theorem 1, a quality-blind rule observes the same updates whether they improve or degrade the quality. Such a rule thus cannot tell a coherent decline from a coherent improvement and can at most detect that the quality has stopped changing. Theorem D.1 shows that the bound on the remaining change is smallest once the updates share no direction, which is what LoopStop detects (see Section GR.3 in the General Response). LoopStop therefore continues a loop while its updates share a direction, and such a decline can cost quality under every quality-blind rule. In some controller loops, the changes after the best round still share a direction, so LoopStop does not stop them immediately. The new Table H.1 measures these loops on every controller scenario. The six scenarios whose changes after the peak keep the strongest direction have a mean yky_k of at least 1.45. On five of these six scenarios, LoopStop still avoids between 0.31 and 0.65 of the quality lost between the peak and the budget. The reason is that the direction fades within the budget, after which LoopStop stops the loop. In the revised paper, we have added the new Appendix H.1.2 on coherent decline.

W2: Small Improvements and Slowly Improving Loops

As mentioned in Section GR.1 in the General Response, we have run new experiments with both more benchmark families and more seeds in the revision. On most families other than the controllers, the quality increases and then holds or keeps increasing slowly, instead of decreasing after a peak. The quality that any stopping rule can gain over running to the budget is therefore small there, and LoopStop's benefit is to reach the same quality in fewer rounds. On these families, LoopStop delivers higher or comparable quality at fewer rounds than running to the budget (Table R1 in the General Response). LoopStop and running to the budget are within a standard error of each other on MLAgentBench-Kaggle. There, LoopStop delivers a quality of 48.0% at 24.8 rounds, and running to the budget delivers a quality of 47.2% at 60.0 rounds. To reduce the standard errors, we have increased the seeds to 20 on BigCodeBench-Hard and to 10 on MLAgentBench-Kaggle. On every family, LoopStop delivers higher quality than every baseline threshold that uses at most as many rounds as LoopStop (the new Figure H.3 in Appendix H.6.1). Section GR.2 in the General Response includes a summary.

The cross-fitted PoU of the original Table I.4 (Table G.4 in the revised paper) chooses the threshold of each scenario from the true quality of the family's other scenarios. A scenario is a combination of evaluator kind and model size. The cross-fitted PoU thus uses the true quality, which a quality-blind rule does not observe. On the mean, the cross-fitted PoU delivers a quality of 49.1% at 37.7 rounds, and LoopStop delivers a quality of 52.4% at 25.3 rounds (Table G.4). The cross-fitted PoU delivers slightly more than LoopStop on ARC-AGI, BigCodeBench-Hard, TravelPlanner and SciBench, at more rounds. On BigCodeBench-Hard and TravelPlanner, the cross-fitted PoU equals the best budget per scenario, which also uses the true quality, at fewer rounds. The cross-fitted PoU exceeds that reference on ARC-AGI, at more rounds. Exceeding the reference is possible because the reference stops every loop of a scenario at the same round, whereas a rule stops each loop at its own round. In the revised paper, we have extended the cross-fitted Table G.4 (previously I.4) to all families and increased seeds.

A loop that improves through frequent changes keeps their direction, so LoopStop continues it. In contrast, a loop that improves through sparse accepted changes among many rejected rounds can be stopped by those rounds before its best round. On cruise control, LoopStop stops 0.90 of the loops with the 4B model evaluator and 0.95 of the loops with the 9B model evaluator before their best round (Table H.1). With the 9B evaluator, LoopStop then delivers a quality of 60.9% at 23.4 rounds. The best budget per scenario, which uses the true quality, delivers a quality of 82.1% at 41.0 rounds (Table H.26). Over the scenarios of cruise control, LoopStop gives up at most 21.2 percentage points against the best budget per scenario. Every baseline gives up more in its worst scenario (Table 2). LoopStop can also give up quality if the improvement pauses for several rounds and then resumes, since it may stop during the pause. We mention this case as a limitation in the revised paper, with more details in Section GR.3 of the General Response.

AuthorsOpenReview ↗

Response to Reviewer dAfp (2 of 2)

W3 and Q2: Baseline Thresholds and Early Termination

In the main results, as in the original version, each baseline uses the threshold on its grid with the highest quality averaged over all families. Choosing a threshold for each family would require that family's true quality. PoR then uses a patience of 50 rounds, which is the largest of its grid. With this patience, PoR delivers a quality of 49.8% at 71.0 rounds, and LoopStop delivers a quality of 52.4% at 25.3 rounds (Table R1 in the General Response). A longer patience approaches running to the budget, which delivers a quality of 50.0% at 73.3 rounds. A single patience does not suit every scenario, since the best patience of a scenario ranges from 3 to 50 rounds within cart-pole alone. PoR also runs nearly every loop for most of the budget (Table H.15 and Section GR.2 in the General Response). On the scenarios that apply every change, PoR uses 73.2 rounds, and on those whose evaluator can reject, it uses 69.4 rounds.

Capped at LoopStop's rounds, every baseline delivers less than LoopStop on every family except TheoremQA, where PoR and PoU are level with LoopStop. We cap each baseline at LoopStop's mean rounds on the family, i.e., we stop the baseline no later than that round. As a reference, a fixed budget stops every loop at the cap. The fixed budget delivers a quality of 50.6% at 25.8 rounds, and LoopStop delivers a quality of 52.4% at 25.3 rounds. LoopStop delivers more because it chooses the stopping round of each loop, whereas the fixed budget stops every loop at the same round.

Baselines capped at LoopStop's rounds (new Table H.13 in Appendix H.6.1). The first table gives the true quality (%), and the second table gives the rounds used, with the standard error over seeds.

True quality (%)

FamilyFixed budget at the cap (reference)PoRPoURLFLoopStop
Cart-pole23.9 ± 1.323.9 ± 1.323.9 ± 1.320.8 ± 1.227.8 ± 1.7
Cruise control48.6 ± 1.448.6 ± 1.448.6 ± 1.440.7 ± 1.551.9 ± 1.6
Ship heading30.5 ± 1.430.5 ± 1.429.4 ± 1.418.8 ± 1.033.4 ± 1.5
Two-mass spring29.0 ± 0.929.0 ± 0.928.9 ± 0.924.3 ± 1.035.4 ± 1.0
ARC-AGI65.1 ± 0.165.1 ± 0.165.1 ± 0.165.2 ± 0.165.6 ± 0.1
BigCodeBench-Hard57.4 ± 0.257.4 ± 0.257.4 ± 0.254.1 ± 0.258.4 ± 0.2
MLAgentBench-Kaggle47.0 ± 1.447.0 ± 1.447.0 ± 1.444.6 ± 1.048.0 ± 0.9
TravelPlanner61.3 ± 0.161.3 ± 0.161.3 ± 0.159.6 ± 0.162.3 ± 0.1
GPQA Diamond66.2 ± 0.466.2 ± 0.466.2 ± 0.465.5 ± 0.467.6 ± 0.4
SuperGPQA41.7 ± 0.341.7 ± 0.341.7 ± 0.341.4 ± 0.242.2 ± 0.3
SciBench66.1 ± 0.166.1 ± 0.166.1 ± 0.165.3 ± 0.266.3 ± 0.1
TheoremQA70.2 ± 0.170.2 ± 0.170.2 ± 0.168.8 ± 0.270.2 ± 0.2
Mean50.6 ± 0.250.6 ± 0.250.5 ± 0.247.4 ± 0.252.4 ± 0.3

Rounds used

FamilyFixed budget at the cap (reference)PoRPoURLFLoopStop
Cart-pole27.0 ± 0.027.0 ± 0.027.0 ± 0.05.8 ± 0.126.1 ± 1.0
Cruise control17.0 ± 0.017.0 ± 0.017.0 ± 0.010.6 ± 0.316.2 ± 0.4
Ship heading48.0 ± 0.048.0 ± 0.045.5 ± 0.311.9 ± 0.847.7 ± 1.7
Two-mass spring40.0 ± 0.040.0 ± 0.039.7 ± 0.110.6 ± 0.739.5 ± 1.4
ARC-AGI23.0 ± 0.023.0 ± 0.023.0 ± 0.05.0 ± 0.022.9 ± 0.1
BigCodeBench-Hard29.0 ± 0.029.0 ± 0.029.0 ± 0.05.1 ± 0.028.4 ± 0.1
MLAgentBench-Kaggle25.0 ± 0.025.0 ± 0.025.0 ± 0.06.3 ± 0.124.8 ± 0.7
TravelPlanner20.0 ± 0.020.0 ± 0.020.0 ± 0.05.1 ± 0.019.5 ± 0.0
GPQA Diamond19.0 ± 0.019.0 ± 0.019.0 ± 0.05.0 ± 0.018.6 ± 0.1
SuperGPQA19.0 ± 0.019.0 ± 0.019.0 ± 0.05.0 ± 0.018.8 ± 0.0
SciBench21.0 ± 0.021.0 ± 0.021.0 ± 0.05.0 ± 0.020.2 ± 0.0
TheoremQA21.0 ± 0.021.0 ± 0.021.0 ± 0.05.0 ± 0.020.4 ± 0.0
Mean25.8 ± 0.025.8 ± 0.025.5 ± 0.06.7 ± 0.125.3 ± 0.2

Q1: Held-Out Benchmark Families

Yes, the seven families added in the revision played no part in LoopStop's design. These families are ship heading, two-mass spring, TravelPlanner, GPQA Diamond, SuperGPQA, SciBench and TheoremQA. On these families, LoopStop delivers the most quality or is within a standard error of the best rule (Table R1 in the General Response). PoR and PoU use more rounds there. In addition, if every method uses the setting with the highest mean quality over the other families, LoopStop delivers the most quality on every family left out. On the mean, LoopStop then uses more rounds than RLF and fewer than PoR and PoU (Table R5 in the General Response). In the revised paper, we have added this evaluation in the new Appendix H.7.3.

Reviewer_dAfpOpenReview ↗

response to rebuttal and followup

I thank the authors for their detailed response and rebuttal efforts. The expanded evaluation across benchmark, more seeds and qualit round comparisons help address some of my original concerns.

I have two followup questions:

for W1: I appreciate the additional analysis of coherent quality degradation in Table H.1. However, the table primarily examines coherence after the best-quality round. Could the authors provide a similar analysis of coherence before the quality peak (for only a subset of the tasks which could be feasible to run in the remaining time), comparing the statistics during improving, plateauing, and degrading phases? This would help further establish how reliably directional coherence distinguishes ongoing quality improvements from convergence.

for W3 : The leave 1 family out results are encouraging. though the avg rounds increase from 25.3 to 41.3, while mean quality improves only from 52.4% to 52.7%. Could the authors clarify which hyperparameters primarily drive this increase?

Also, as a suggestion, the authors are encouraged to explore the existing hyperparameter sweep and explore whether alternative settings provide a better quality–efficiency tradeoff, particularly for previously unseen tasks? This could be very useful for the community in general in this area of research.

Reviewer_HtjwOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This paper studies when to stop an iterative generator–evaluator loop without observing the artifact’s true quality. It first gives an indistinguishability argument: replacing the hidden quality function (q) with (1-q) preserves the observed trajectory while reversing the sign of quality changes. It then proposes LoopStop, which sketches artifact edits, measures the directional coherence of recent updates, and accumulates evidence for stopping when that coherence weakens. Separate scoring rules handle rounds that leave the artifact unchanged. The evaluation covers two controller-tuning families, ARC-AGI, BigCodeBench-Hard, and MLAgentBench-Kaggle, with several evaluator configurations. In Table 1, LoopStop achieves mean quality 0.508 versus 0.469 for the strongest adaptive baseline by average quality, while using 23.5 versus 48.0 rounds. The largest quality gains occur on the controller families; gains on coding and ML tasks are smaller.

Critical strengths
  1. In my opinion this paper is solving a very useful problem - an agent can keep making changes long after those changes are useful, and checking progress with another judge adds cost and another source of error. LoopStop uses information the harness already has. Looking at the relationship between successive edits is more informative than simply counting rejections or checking whether edits are small. This is useful for inspector-based loops, where every proposed change is applied.

  2. The experiments give reasonable evidence that the method can save computation without sacrificing much quality. They cover several artifact types and evaluator configurations, and the appendix includes useful comparisons with sentence embeddings, an ablation of unchanged-round scoring, and paired comparisons by seed. Even on tasks where the quality gains are small, the reduction in rounds is worth considering. I also think the presentation is very good.

Critical weaknesses
  1. The evaluation would be more convincing if it also reported task-success metrics. ARC-AGI is scored by the fraction of matching cells, and BigCodeBench-Hard by the fraction of tests passed. These measures capture partial progress, but they do not tell us how often the final grid is entirely correct or the program passes all tests. A stopping rule could preserve average partial credit while stopping before the last few changes needed to solve a task. I would like to see exact-match accuracy on ARC and all-tests-passed rates on coding, alongside the current metrics. This matters because the practical claim is that adaptive stopping saves rounds without losing useful outcomes, and preserving partial credit does not necessarily establish that.

  2. Another concern is the gap between detecting a loss of edit direction and detecting a quality plateau. A sequence of useful fixes to different parts of a program need not point in a common direction. Conversely, consistently directed edits need not improve quality. Theorem 1 establishes that the sign of quality change cannot be identified under the observation model, but it does not establish the proposed connection between coherence and settling. The Lipschitz argument does not close this gap either: the bound in Appendix D still grows with the future horizon even at zero drift. The stopping guarantees also need more careful qualification. Theorem 2 concerns a ratio of expectations, while the algorithm relies on the mean-ratio approximation. Theorem 3(i) assumes independent coherence statistics, although successive statistics reuse the same history. The paper acknowledges some of these limitations, but the discussion around the guarantees is broader than the results support.

Questions for authors
  1. How large is the mean-ratio approximation error in practice? Could you report this together with the serial dependence of the coherence statistics and explain what the observed dependence means for the false-stop guarantee?

  2. Have you examined cases where useful edits affect unrelated parts of an artifact, or where improvement resumes after several unproductive rounds? These seem relevant to whether coherence measures quality settling.

  3. How do the methods compare on exact-match accuracy for ARC-AGI and all-tests-passed rates for BigCodeBench-Hard? In particular, how often does LoopStop stop on an unsolved task that a later round would solve?

  4. Could you compare the methods across a common range of quality–round tradeoffs? Table 1 selects baseline thresholds for quality alone, while Table I.4 introduces a round cost. Using the same objective would make the efficiency comparison easier to interpret.

  5. For the reported setting (D=4), what delays are observed from a quality plateau to stopping? How often are the conditions of Theorem 3(ii) actually satisfied?

7 comments
AuthorsOpenReview ↗

Response to Reviewer Htjw (1 of 2)

W1 and Q3: Task-Success Metrics

We now report task success by each benchmark's own test, i.e., an exact grid with two attempts from two seeds on ARC-AGI and every test passed on BigCodeBench-Hard. At LoopStop's stop, the share of tasks solved is the highest of the quality-blind rules on ARC-AGI and BigCodeBench-Hard, at fewer rounds than PoR and PoU (table below). On ARC-AGI, the share solved is much lower than the true quality of Table R1 in the General Response, since a task is solved only if every cell matches. The true quality instead credits every cell that matches the hidden answer. An output grid shares most of its cells with the test input, so copying the input unchanged already scores 55.4% of the cells on average (new Table G.1). The Qwen3.5 models with thinking off produce an exact grid on few tasks. We keep the share of cells as the true quality, since it shows whether each round improved the grid. An exact match, in contrast, is 0 on almost every round.

Task success (new Table H.8). Solved is the share of tasks whose artifact at the stop passes the benchmark's test. Missed and kept are shares of loops, with standard errors. A missed loop is unsolved at the stop although a later round is solved, whereas a kept loop is solved at the stop although the budget's artifact is not.

FamilyMethodRounds usedQuality (%)Solved (%)Missed (%)Kept (%)
ARC-AGIRun to budget (reference)60.0 ± 0.065.0 ± 0.14.1 ± 0.00.0 ± 0.00.0 ± 0.0
ARC-AGIPoR59.7 ± 0.165.0 ± 0.14.2 ± 0.00.0 ± 0.00.0 ± 0.0
ARC-AGIPoU59.5 ± 0.065.1 ± 0.14.2 ± 0.00.1 ± 0.00.1 ± 0.0
ARC-AGIRLF5.0 ± 0.065.2 ± 0.14.2 ± 0.16.6 ± 0.11.2 ± 0.0
ARC-AGILoopStop22.9 ± 0.165.6 ± 0.14.4 ± 0.15.4 ± 0.11.1 ± 0.1
BigCodeBench-HardRun to budget (reference)60.0 ± 0.057.9 ± 0.133.4 ± 0.30.0 ± 0.00.0 ± 0.0
BigCodeBench-HardPoR57.6 ± 0.057.8 ± 0.133.2 ± 0.30.1 ± 0.00.0 ± 0.0
BigCodeBench-HardPoU55.6 ± 0.157.8 ± 0.133.2 ± 0.30.2 ± 0.00.1 ± 0.0
BigCodeBench-HardRLF5.1 ± 0.054.1 ± 0.229.5 ± 0.318.7 ± 0.36.1 ± 0.2
BigCodeBench-HardLoopStop28.4 ± 0.158.4 ± 0.234.2 ± 0.312.1 ± 0.26.1 ± 0.2

For Q3, LoopStop stops 5.4% of the ARC-AGI loops and 12.1% of the BigCodeBench-Hard loops before a later solution. LoopStop also keeps 1.1% and 6.1% of the loops at a solution that later rounds break. At LoopStop's stop, 4.4% of the ARC-AGI tasks and 34.2% of the BigCodeBench-Hard tasks are solved, at 22.9 rounds and 28.4 rounds. Running to the budget of 60 rounds solves 4.1% and 33.4%, since on ARC-AGI most exact grids reached after the stop are lost again at a later round. In the revised paper, we have added these metrics in the new Appendix H.4.

W2 and Q2: Edit Direction and Quality Plateaus

We have measured both cases of Q2. LoopStop's mean quality is the highest or within a standard error of it on most families (see Table R1 in the General Response). By Theorem 1, a quality-blind rule can at most detect that the quality has stopped changing. LoopStop detects this state as a loss of shared direction (Section GR.3 in the General Response). We measure the cost of the gap between this loss and a quality plateau against running to the budget, which runs every round. Edits that keep a direction can also lower the quality, which a quality-blind rule cannot tell from an improvement. We measure this coherent decline in the new Appendix H.1.2.

  • Useful edits to unrelated parts. This case is most frequent on TravelPlanner, where a plan improves through edits to unrelated entries, e.g., the meals of a single day. There, LoopStop is level with the best rule at fewer rounds (see Table R1 in the General Response).
  • Improvement that resumes after a pause. This is the case in which LoopStop can give up quality, since it may stop during the pause. The cost depends on what follows the pause. On the loops whose improvement resumes, the cost is largest on SciBench. Over all SciBench loops, LoopStop is within a standard error of running to the budget at fewer rounds (see Table R1 in the General Response).

The Lipschitz bound of Appendix D.1 on the remaining quality change grows with the horizon WW even without a shared direction. The reason is that undirected edits still change the artifact like a random walk. The bound grows as W\sqrt W for a settled loop and as WW for a directed loop, so it still separates settled loops from directed loops. For the mean-ratio approximation and the dependence in Theorem 3(i), please see Section GR.4 in the General Response. In the revised paper, we have added the new Appendix H.1.3 and the comparison of growth rates in Appendix D.1. We have also stated the scope of Theorems 2 and 3 next to each theorem.

AuthorsOpenReview ↗

Response to Reviewer Htjw (2 of 2)

Q1: Mean-Ratio Error and Serial Dependence

The approximation error is small, and the revised false-stop guarantee allows the serial dependence. Averaged over all families, Theorem 2's prediction differs from the measured mean of yky_k over the settled changes by 0.008 (see Table R4 in the General Response). This gap is small against the no-direction level of 1 in Theorem 2. Successive yky_k share most of their updates, and their lag-1 autocorrelation lies between 0.00 and 0.53 (new Table H.6). The revised Theorem 3(i) conditions on everything observed before each change, so it allows this correlation. The theorem instead requires that the mean of yky_k given that past exceed the reference level κ\kappa by a margin δ\delta (see Section GR.4 in the General Response). In the revised paper, we have added both measurements in the new Appendix H.2.

Q4: Common Quality-Round Tradeoffs

Yes, we now compare all methods at every threshold, so any objective can rank them (see Section GR.2 in the General Response). Averaged over all families, for every baseline threshold, some setting of LoopStop uses no more rounds and delivers more quality. We have also chosen every method's setting on the other families under the round cost of Table G.4, which charges 0.2 percentage points of quality per round. LoopStop then delivers the highest mean quality of 50.3% at 12.9 rounds. The best adaptive baseline, PoU, delivers a quality of 48.0% at 32.5 rounds. On ship heading, BigCodeBench-Hard, TravelPlanner and the four question-answering families, a baseline delivers more, at more rounds. In the revised paper, we have added Figure 3 to the main text and the selection under this round cost in the new Appendix H.7.3.

LoopStop delivers more quality at the same rounds because it adapts its stop to each loop, whereas a baseline stops every loop on the same event. PoR spends more rounds on loops that apply every change than on loops whose evaluator can reject, since the first kind rejects nothing (table below). LoopStop does the opposite, since the updates of a loop that applies every change soon share no direction. A rejected round, moreover, adds evidence only once the recent changes have lost their direction.

Every rule at its setting of Table R1 in the General Response, means over all families with standard errors (new Table H.15).

RuleRounds, every change appliedQuality (%)Rounds, evaluator can rejectQuality (%)
PoR (50)73.2 ± 0.138.7 ± 0.269.4 ± 0.258.4 ± 0.3
PoU (30)73.1 ± 0.038.8 ± 0.262.0 ± 0.358.0 ± 0.3
RLF (0.5)12.7 ± 0.542.1 ± 0.45.6 ± 0.150.8 ± 0.3
LoopStop16.2 ± 0.144.0 ± 0.433.5 ± 0.459.0 ± 0.3

Two scenarios (new Table H.16 in Appendix H.6.2). Each cell gives mean rounds and, in parentheses, mean quality (%), and the second column gives the peak of the scenario's mean quality curve.

ScenarioPeak of the meanPoRPoURLFLoopStop
Cruise control, no evaluator6 (49.3 ± 5.8)100 ± 0.0 (1.7 ± 1.7)100 ± 0.0 (1.7 ± 1.7)13.9 ± 3.7 (34.5 ± 7.4)11.8 ± 0.7 (42.0 ± 7.1)
Cart-pole, model evaluator 9B23 (48.9 ± 5.6)100 ± 0.0 (37.5 ± 5.7)96.5 ± 2.9 (38.0 ± 5.7)5.1 ± 0.1 (18.2 ± 2.6)31.9 ± 3.0 (48.3 ± 5.2)

Q5: Delay From Plateau to Stop

LoopStop stops a median of 0 to 8 rounds after a loop's best round, i.e., the round of highest true quality, on the controller families, ARC-AGI, MLAgentBench-Kaggle and TravelPlanner. On BigCodeBench-Hard and the four question-answering families, many loops hold their best artifact from round 0 or improve slowly until the budget, and the median is 13 to 17 rounds. Let the settling round be the round after which the quality improves by at most 5 percentage points over the next 20 rounds. Measured from the settling round, the median delay is 10 to 18 rounds on every family except cruise control (2.5 rounds) and ship heading (37 rounds). This delay is longer than D=4D=4, since Theorem 3(ii) counts DD from the fade of the statistic, and a loop with an evaluator changes only every few rounds. The conditions of Theorem 3(ii) hold at 0.01 to 0.20 of the stops in a family. On average in every family, LoopStop stops these loops within the bound of Theorem 3(ii), which exceeds DD at their peaks below the cap. The theorems describe the mechanism, and Table R1 in the General Response carries the performance claim.

Theorem 3(ii) bounds the delay for loops that showed a direction and then lost it. On most families other than the controllers, most loops settle without showing a direction, and LoopStop stops them once their yky_k stay below 1 or their evaluator stops accepting. Many stops on the controller families come while the running average of the recent yky_k is still above 1, which is earlier than Theorem 3(ii) assumes. In the revised paper, we have added these measurements in the new Appendix H.3.1.

Reviewer_HtjwOpenReview ↗

Rebuttal Comments

I appreciate the authors for the detailed responses, resolving my concerns and the new revisions made. The concern that I have is regarding if the method stops improving, does it really mean that any better solution does not exist? The additional failure analyses and missed solution rates help explain this but I feel that achieving same final success rate within the allowed budget does not prove that the method would not have found better solutions if it has continued. Hence I look forward to what the authors have to say about this.

Reviewer_28quOpenReview ↗
Rating
3(+1)
Confidence
2
Informativeness
2
Presentation
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Paper summary

The paper studies when to stop an iterative agent loop without observing true artifact quality. LOOPSTOP sketches artifact edits, measures the directional coherence of recent updates, and accumulates evidence for stopping. Experiments span five task families and report approximately 8.3% higher mean quality than the next-best adaptive baseline while using roughly half as many rounds. The problem is important, and the proposed method is computationally inexpensive. The appendices also provide substantial experimental detail and useful disclosures. Nevertheless, the theoretical development does not fully justify the interpretation assigned to the implemented statistic. In particular, the paper moves from a ratio of expectations to an expectation of a ratio, and from low directional coherence to quality-related settling, without sufficient guarantees.

Critical strengths

Practically important problem. Stopping without hidden-test or deployment-quality access is relevant to many agent systems.

Low implementation overhead. The sketch and online statistics avoid an additional expensive model call at every iteration.

Diverse evaluator mechanisms. The experiments include programmatic evaluators, accept/reject models, inspectors, and loops without evaluators.

Substantial supplementary analysis. Parameter sensitivity, representation substitutions, cross-fitted baseline configurations, and paired differences are documented.

Transparent disclosure of development choices. Appendix I acknowledges data-dependent choices in the algorithm’s design. This transparency is valuable, even though it requires the main-text claims to be qualified.

Critical weaknesses

Theorem 2 establishes a ratio of expectations, not the expected coherence used by the algorithm.The paper explicitly acknowledges a “mean-ratio approximation” on page 5, so this is not an undisclosed substitution. However, subsequent interpretations—including a normalized mean of one under no shared direction and comparability without calibration—depend on an approximation whose error is not controlled.

Theorem 3(i) assumes independence of the coherence statistics yky_k. These statistics share overlapping exponentially weighted histories; independence of the underlying updates does not generally imply independence of successive coherence values. The conclusion acknowledges this limitation, but the main interpretation of a theoretically controlled false-stop probability remains too broad. The result also concerns windows in which every round changes the artifact. It does not directly establish the same guarantee for the full process with interspersed unchanged rounds.

Theorem 1’s indistinguishability argument using qq and 1−q1-q is valid under its information assumptions. However, it does not establish that a loop with incoherent updates has little useful improvement remaining.

Questions for authors

How large is the mean-ratio approximation error on actual trajectories?

How does LOOPSTOP behave when quality improves through edits to independent artifact components?

What performance is obtained on task families entirely excluded from algorithm development?

Can the theoretical relationships among sketch distance, carried edits, normalized updates, and accumulated paths be clarified or corrected?

4 comments
AuthorsOpenReview ↗

Response to Reviewer 28qu (1 of 2)

W1 and Q1: Mean-Ratio Approximation Error

The approximation error is small on the actual trajectories, and the revised Theorem 2 now gives it exactly (see Section GR.4 in the General Response). The value predicted by the ratio of expectations is the first term of Theorem 2. Over the settled changes, the measured mean of yky_k differs from this value by 0.008 on average over all families and by at most 0.076 on BigCodeBench-Hard. Both gaps are small against the no-direction level of 1 in Theorem 2 (see Table R4 in the General Response). Over the improving changes, the gap reaches 0.200 on cruise control (new Table H.4), where an improving change then scores less than the first term predicts, which delays the stop.

The revised Theorem 2 shows that the expectation of the ratio, E[ct]\mathbb E[c_t], differs from the ratio of expectations by exactly Cov(ct,Vt)/E[Vt]\mathrm{Cov}(c_t,V_t)/\mathbb E[V_t]. This step of the proof does not need independence. Here ctc_t is the coherence and VtV_t is the mean squared magnitude of the recent updates. The reason is that the ratio of expectations weights the coherence of each window of updates by its VtV_t, whereas the expectation of the ratio weights every window equally. This covariance is in general nonzero, since ctc_t has VtV_t in its denominator and both quantities are built from the same updates. On the trajectories the covariance is small, because the coherence and VtV_t are nearly uncorrelated across the loops of a scenario, although both quantities vary widely. A scenario is a combination of evaluator kind and model size. You name two interpretations, namely a mean of 1 without a shared direction and comparability across loops without calibration. For updates that share no direction, both interpretations therefore hold for the mean of yky_k up to this small error. On the data, the level 1 bounds the mean yky_k of the settled changes from above instead of describing its typical value. This mean lies between 0.358 and 0.983 on every family (Table R4 in the General Response). Settled loops partly undo their changes, which lowers yky_k below 1 and brings the stop forward. In the revised paper, we have extended Theorem 2 in Section 3.2 and added a statement of its scope next to the definition of yky_k. We have also added the measurements in the new Appendix H.2.

W2: Dependent Statistics and Unchanged Rounds

The revised Theorem 3(i) conditions on the past, so it covers dependent successive yky_k and windows with unchanged rounds (see Section GR.4 in the General Response). Given everything observed before a change, the theorem requires the mean of yky_k over the possible changes of the loop to exceed the reference level κ\kappa by a margin δ\delta. A change whose yky_k lies below κ\kappa adds evidence for stopping. The observed past includes the recent updates that successive yky_k share, so the dependence between them is allowed. Unchanged rounds may occur in the window as long as the total evidence for stopping that they add stays within an allowance γ\gamma. If the running average yˉ\bar y of the recent yky_k stays at or above κ\kappa, an unchanged round adds no evidence, so γ\gamma is 0 in that case. At the setting used, Theorem 3(i) covers only windows of a few rounds and a stronger direction than the improving changes of these families show (Appendix H.3.1). The theorem thus describes the mechanism by bounding the false stops of loops whose mean yky_k stays above κ\kappa. The shares of loops stopped before a later gain in Tables H.1 and H.3 measure the false stops. In the revised paper, we have updated Theorem 3(i) in Section 3.3 and added its scope next to it.

W3: Incoherent Updates and Remaining Improvement

By Theorem 1, a quality-blind rule can at most detect that the quality has stopped changing. Theorem D.1 shows that the bound on the remaining change is smallest once the updates share no direction, which is what LoopStop detects (see Section GR.3 in the General Response). We therefore measure the improvement that remains after LoopStop's stop directly, against running to the budget, which runs every round. LoopStop delivers higher or comparable quality on every family at fewer rounds (see Table R1 in the General Response). Continuing the loops to the budget thus does not gain quality beyond a standard error on any family. Some improvement remains after the stop in loops whose improvement pauses and then resumes, e.g., on TravelPlanner and SciBench. In the revised paper, we have added the new Appendix H.1.3 on these pauses.

AuthorsOpenReview ↗

Response to Reviewer 28qu (2 of 2)

Q2: Independent Artifact Components

If the components improve in turn, consecutive edits to different components share no direction, so LoopStop may take the loop for settled and stop before a later improvement. TravelPlanner is such a family, since a plan improves through edits to unrelated entries, e.g., the meals or the accommodation of a single day. LoopStop stops before such an improving edit in 0.55 of the TravelPlanner loops that contain such an edit. These early stops give up 4.5 percentage points on average over those loops (new Table H.2). Over all loops of the family, this cost is absorbed, as LoopStop is level with PoR, PoU and running to the budget (see Table R1 in the General Response). LoopStop delivers a quality of 62.3% at 19.5 rounds. PoR and PoU deliver the same quality of 62.3% at 60.0 rounds and at 59.9 rounds. We state this case as a limitation in the conclusion. In the revised paper, we have added the measurement of these edits in the new Appendix H.1.3.

Q3: Families Excluded From Development

The seven families added in the revision played no part in LoopStop's design. These families are ship heading, two-mass spring, TravelPlanner, GPQA Diamond, SuperGPQA, SciBench and TheoremQA. On these families, LoopStop delivers the most quality or is within a standard error of the best rule (Table R1 in the General Response). PoR and PoU use more rounds there. In addition, if every method uses the setting with the highest mean quality over the other families, LoopStop delivers the most quality on every family left out. On the mean, LoopStop then uses more rounds than RLF and fewer than PoR and PoU (Table R5 in the General Response). In the revised paper, we have added this evaluation in the new Appendix H.7.3.

Q4: Sketch Distance and Accumulated Paths

Yes, the revision clarifies them. Assumption 2 links the quality to a distance between rounds. The revision defines that distance as the quantity that LoopStop measures, whereas the original version stated a distance between artifacts. This quantity is the magnitude of the sum of the updates between two rounds, d(s,t)=∣xt−xs∣d(s,t)=\\|x_t-x_s\\| with the path xt=∑r<turx_t=\sum_{r<t}u_r. A sketch is the hashed vector of an artifact's parts. To form each update, LoopStop takes the difference of the sketches across the round, together with the sketch of any text carried elsewhere within the artifact. LoopStop then divides this sum by a normalizing scalar of that round. The scalar is the square root of the mean number of parts for text and structured data, and it is 1 for numbers. On numeric artifacts, which carry no text, the sum of the updates telescopes. The distance d(s,t)d(s,t) then equals the magnitude of the difference S(ξt)−S(ξs)S(\xi_t)-S(\xi_s) of the sketches of the artifacts ξs\xi_s and ξt\xi_t of the two rounds. On text, d(s,t)d(s,t) equals that magnitude divided by the scalar if no text was carried and the scalar stayed the same. Carried text adds a term that shares no direction with that difference on average over the hash function. In the revised paper, we have updated the distance in Section 3.1 and Appendix E.1 (previously Appendix E) and added the new Theorem E.4.

I have read through the authors' rebuttal, and raised my score to weak accept.

Dear Reviewer 28qu,

Many thanks for the acknowledgment and for raising the score. We appreciate your efforts in reviewing our paper. Your comments have been very helpful for us to improve the quality of this work.

All the best,
Authors of Submission 24517

Comments on the paper

4 comments
AuthorsOpenReview ↗

General Response (1 of 4)

We thank the reviewers for their comments. We have run new experiments and analyses, and this general response includes answers to some shared concerns between reviewers. We have also revised the paper, with the edits in its body marked in blue. Some appendix sections have been regrouped for better clarity. Numbers of appendices, tables and theorems are those of the revised paper, unless otherwise specified.

GR.1 Results on New Benchmarks

(Reviewer dAfp)

We have run experiments with more benchmark families and more seeds. The results now cover 12 benchmark families, beyond the 5 families in the original paper. We have also increased the seeds from 5 to 20 on BigCodeBench-Hard and from 3 to 10 on MLAgentBench-Kaggle. We find that LoopStop's advantage holds on this larger set. As in the original version, each baseline keeps the single threshold on its grid with the highest quality averaged over all families.

LoopStop delivers the highest mean quality, namely a quality of 52.4% at 25.3 rounds. The best adaptive baseline, PoR, delivers a quality of 49.8% at 71.0 rounds. Running to the budget delivers a quality of 50.0% at 73.3 rounds (Table R1 below). Note: Each baseline uses the threshold on its grid with the highest quality averaged over all families (see also Section GR.5 in this General Response below), which is why the baseline performance has also changed for the pre-existing benchmark families, as the baseline threshold now maximizes the mean quality over all the 12 families.

Table R1 (new Table 1). Each baseline runs at its threshold with the highest mean quality, and LoopStop runs at τ=5\tau=5 and D=4D=4. Part (a) gives the true quality (%) at the stop, and part (b) gives the rounds used. Each value is a mean with the standard error over seeds.

Table R1(a). True quality (%)

FamilySeedsRun to budget (reference)PoRPoURLFLoopStop
Cart-pole2020.4 ± 1.620.4 ± 1.620.1 ± 1.520.7 ± 1.227.8 ± 1.7
Cruise control2039.3 ± 1.139.2 ± 1.139.5 ± 1.135.3 ± 1.651.9 ± 1.6
Ship heading2031.2 ± 0.929.8 ± 0.928.0 ± 0.918.6 ± 1.133.4 ± 1.5
Two-mass spring2031.6 ± 0.731.2 ± 0.729.7 ± 0.924.3 ± 1.035.4 ± 1.0
ARC-AGI2065.0 ± 0.165.0 ± 0.165.1 ± 0.165.2 ± 0.165.6 ± 0.1
BigCodeBench-Hard2057.9 ± 0.157.8 ± 0.157.8 ± 0.154.1 ± 0.258.4 ± 0.2
MLAgentBench-Kaggle1047.2 ± 0.847.1 ± 0.847.3 ± 0.844.5 ± 1.048.0 ± 0.9
TravelPlanner1062.3 ± 0.162.3 ± 0.162.3 ± 0.159.6 ± 0.162.3 ± 0.1
GPQA Diamond1067.0 ± 0.267.0 ± 0.267.1 ± 0.265.5 ± 0.467.6 ± 0.4
SuperGPQA1041.6 ± 0.341.6 ± 0.341.6 ± 0.341.4 ± 0.242.2 ± 0.3
SciBench1066.4 ± 0.266.4 ± 0.266.4 ± 0.265.3 ± 0.266.3 ± 0.1
TheoremQA1069.9 ± 0.169.9 ± 0.170.0 ± 0.168.8 ± 0.270.2 ± 0.2
Mean50.0 ± 0.249.8 ± 0.249.6 ± 0.246.9 ± 0.252.4 ± 0.3

Table R1(b). Rounds used

FamilyRun to budgetPoRPoURLFLoopStop
Cart-pole100.0 ± 0.098.2 ± 0.492.5 ± 0.96.2 ± 0.526.1 ± 1.0
Cruise control100.0 ± 0.093.8 ± 0.783.1 ± 1.021.1 ± 1.416.2 ± 0.4
Ship heading100.0 ± 0.089.2 ± 1.174.6 ± 1.017.0 ± 1.647.7 ± 1.7
Two-mass spring100.0 ± 0.093.7 ± 0.678.4 ± 1.115.4 ± 1.439.5 ± 1.4
ARC-AGI60.0 ± 0.059.7 ± 0.159.5 ± 0.05.0 ± 0.022.9 ± 0.1
BigCodeBench-Hard60.0 ± 0.057.6 ± 0.055.6 ± 0.15.1 ± 0.028.4 ± 0.1
MLAgentBench-Kaggle60.0 ± 0.059.7 ± 0.156.5 ± 0.46.8 ± 0.324.8 ± 0.7
TravelPlanner60.0 ± 0.060.0 ± 0.059.9 ± 0.05.1 ± 0.019.5 ± 0.0
GPQA Diamond60.0 ± 0.060.0 ± 0.059.7 ± 0.05.0 ± 0.018.6 ± 0.1
SuperGPQA60.0 ± 0.059.9 ± 0.059.7 ± 0.05.0 ± 0.018.8 ± 0.0
SciBench60.0 ± 0.059.9 ± 0.059.7 ± 0.05.0 ± 0.020.2 ± 0.0
TheoremQA60.0 ± 0.059.8 ± 0.059.5 ± 0.05.0 ± 0.020.4 ± 0.0
Mean73.3 ± 0.071.0 ± 0.166.5 ± 0.28.5 ± 0.225.3 ± 0.2

LoopStop is the best or within a standard error of it on every family.

AuthorsOpenReview ↗

General Response (2 of 4)

GR.2 Comparison at Every Threshold, Quality-Rounds Tradeoff

(Reviewers dAfp and Htjw)

We have compared all methods at every point of their grids (listed in Appendix H.6.1). Averaged over all families, the new Figure 3 shows that LoopStop gives a higher mean quality than the baselines at the same number of rounds. LoopStop also uses fewer rounds at the same mean quality.

Table R2 (new Table H.12 in Appendix H.6.1). The trade-off over the grid points of the new Figure 3. Each cell gives the highest mean quality (%) over all families, ± its standard error over seeds, among the method's grid points whose mean rounds stay within the limit. "Stops later" means that every point of the grid uses more rounds.

Round limitPoRPoURLFLoopStop
10stops laterstops later46.9 ± 0.249.6 ± 0.2
20stops laterstops later46.9 ± 0.251.5 ± 0.2
30stops laterstops later46.9 ± 0.252.6 ± 0.3
5048.3 ± 0.249.2 ± 0.246.9 ± 0.253.0 ± 0.2
7549.8 ± 0.249.6 ± 0.246.9 ± 0.253.0 ± 0.2

Why no single threshold suits every scenario. PoR's mean quality increases with its patience and stays below LoopStop at every patience (Figure 3). Each baseline stops every loop on the same event, e.g., PoR stops on a run of rejected rounds. A loop without an evaluator or with an inspector applies every change, so the event comes late or never and the loop runs past its peak. In contrast, a loop whose evaluator rejects most proposals produces the event within a few rounds, while its quality still increases. The best patience of a scenario thus ranges from 3 to 50 rounds within cart-pole (Table H.14). LoopStop instead stops once a loop's recent changes have lost their shared direction and counts a rejected round only after that direction has faded, so its stop follows the loop. Table R3 in the General Response gives the quality that each rule gives up against the best budget per scenario in its worst scenario of a family. LoopStop gives up the least on the mean and on most families, on some of which a baseline is within a standard error. A patience rule gives up less on TravelPlanner and, within a standard error, on GPQA Diamond. A rule can exceed the best budget per scenario, because this reference stops every loop of a scenario at the same round. That round is chosen in hindsight from the true quality, whereas a rule stops each loop at its own round.

Table R3. Quality (percentage points) given up against the best budget per scenario in each rule's worst scenario, at the settings of Table R1 in the General Response. Values are means over all families with standard errors over seeds (every family in the new Table 2).

PoRPoURLFLoopStop
Mean15.5 ± 0.915.4 ± 0.916.0 ± 0.98.0 ± 1.0

The new Figure H.3 in Appendix H.6.1 shows each family. On every family, LoopStop's setting of Table R1 in the General Response matches or exceeds the quality of every baseline threshold at no more rounds. See also Section GR.5 below, where every setting is chosen on the other families.

GR.3 What a Quality-Blind Rule Can Detect

(Reviewers dAfp, Htjw and 28qu)

By Theorem 1, a quality-blind rule cannot tell an improvement from a decline, so it can at most detect that the quality has stopped changing. Theorem D.1 shows that the bound on the remaining change is smallest once the updates share no direction, which is what LoopStop detects. Because the loop does not consult the true quality, the same loop scored by 1−q1-q instead of qq produces the same artifacts and accept decisions. Every quality increase, however, becomes a decrease. The evaluator makes a consistent direction an improvement through its accept decisions.

We therefore also compare LoopStop with running to the budget, which runs every round. LoopStop delivers higher or comparable quality on every family, at fewer rounds (Table R1 in the General Response).

Two cases are hardest for a rule that follows the direction of the changes. In the first case, quality improves through edits to unrelated parts of the artifact, whose updates share no direction. The second case is an improvement that resumes after several rounds without a quality change. In both cases, LoopStop may take the loop for settled and stop before the later gains. TravelPlanner shows both cases, since a plan keeps improving through edits to unrelated entries, e.g., the meals of a single day. The cost of the second case is largest on SciBench. Over all loops, LoopStop is level with the best rule on TravelPlanner and within a standard error of running to the budget on SciBench. Both results come at fewer rounds (Table R1 in the General Response). We state these cases as a limitation in the conclusion.

In the revision, we added this explanation after Theorem 1 and the measurements of both cases in the new Appendix H.1.

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General Response (3 of 4)

GR.4 Approximation Error and Dependent Statistics

(Reviewers Htjw and 28qu)

The revised paper states the approximation error formally and extends Theorem 3(i) to dependent statistics.

Mean-ratio approximation. The revised Theorem 2 gives the error exactly, and the measurements show that it is small. LoopStop treats a loop as settled once its recent edits no longer point in a common direction, which it measures by the coherence ctc_t of the recent updates. The coherence lies in [0,1][0,1] and is high if the updates point the same way. Updates without a common direction still give a coherence above 0, since the average of a few random updates is not 0. LoopStop divides the coherence by this noise level wtw_t, so that the result yky_k is about 1 without a common direction.

The revised Theorem 2 provides the mean coherence directly, for noisy updates drawn at random from a common distribution, which is how the paper defines the noise level. Theorem 2 obtains E[ct]=r+wtr+1−Cov(ct,Vt)E[Vt],\mathbb E[c_t]=\frac{r+w_t}{r+1}-\frac{\mathrm{Cov}(c_t,V_t)}{\mathbb E[V_t]}, where r≥0r\ge0 measures how strongly the updates share a direction and VtV_t is the mean squared magnitude of the recent updates. Without a common direction, r=0r=0, and the mean coherence is the noise level minus the covariance term. The submitted version stated only the first term. The covariance term appears because the first term weights the coherence of each window by VtV_t, while the mean coherence counts every window equally. The covariance term is nonzero only if the coherence of a window varies with VtV_t.

This covariance is small in practice. The coherence does not change if every update is scaled by the same factor. A loop with updates of larger magnitude thus has neither a higher nor a lower coherence for that reason. Across the loops of a scenario, ctc_t and VtV_t both vary widely and have a correlation between -0.15 and 0.11 (new Table H.5). Over the settled changes in Table R4 in the General Response, the mean of yky_k differs from the first term by at most 0.076. Averaged over all families, the gap is 0.008. Both the measured mean and the first term lie below the no-direction level of 1, since settled loops partly undo their changes. The partial undoing makes these changes score higher and brings the stop forward.

Table R4. The mean of yky_k over the changes after a loop's true quality last changed, the first term of Theorem 2, and their gap (± standard error over seeds).

FamilyMeasured mean of yky_kRatio of means (first term of Theorem 2)Gap
Cart-pole0.779 ± 0.0100.802 ± 0.006-0.023 ± 0.009
Cruise control0.956 ± 0.0380.990 ± 0.025-0.034 ± 0.019
Ship heading0.859 ± 0.0280.906 ± 0.010-0.048 ± 0.029
Two-mass spring0.983 ± 0.0230.993 ± 0.012-0.010 ± 0.027
ARC-AGI0.358 ± 0.0020.373 ± 0.001-0.015 ± 0.002
BigCodeBench-Hard0.506 ± 0.0020.430 ± 0.000+0.076 ± 0.002
MLAgentBench-Kaggle0.693 ± 0.0260.730 ± 0.015-0.037 ± 0.025
TravelPlanner0.546 ± 0.0030.538 ± 0.002+0.008 ± 0.003
GPQA Diamond0.420 ± 0.0010.360 ± 0.000+0.060 ± 0.001
SuperGPQA0.459 ± 0.0010.407 ± 0.000+0.052 ± 0.001
SciBench0.428 ± 0.0000.400 ± 0.000+0.028 ± 0.000
TheoremQA0.435 ± 0.0000.392 ± 0.000+0.043 ± 0.000
Mean0.619 ± 0.0050.610 ± 0.003+0.008 ± 0.004

Dependent statistics. LoopStop adds up evidence for stopping and stops once the sum reaches a threshold. A change adds evidence if its yky_k is below a reference level κ\kappa, and an unchanged round adds evidence once the recent changes have lost their common direction. Theorem 3(i) bounds the probability that LoopStop stops a loop whose changes keep a common direction. Successive yky_k are correlated, even for the independent updates of Theorem 2, since each value averages the last few updates and successive averages share most of their updates.

The revised Theorem 3(i) drops the independence assumption of the submitted version. The theorem requires only that at each change, given everything observed so far, the expected yky_k exceeds κ\kappa by a margin δ>0\delta>0. A change adds at most κ−yk\kappa-y_k to the sum, which is negative if yky_k exceeds κ\kappa. Under this condition, every change is expected to lower the sum by at least δ\delta, whatever the earlier changes, so the correlation between successive yky_k does not matter. The sum then reaches the threshold only if the actual yky_k lie below their expected values by a large total. The theorem bounds the probability of this event by a quantity that decreases exponentially in the threshold times δ\delta. At the setting used, Theorem 3(i) covers only windows of a few rounds and a stronger direction than the improving changes of these families show (Appendix H.3.1). The theorems thus describe the mechanism, and Tables H.1 and H.3 measure the false stops.

AuthorsOpenReview ↗

General Response (4 of 4)

GR.5 How Each Setting Was Chosen

(Reviewers dAfp and 28qu)

Every method uses the same setting on all families. Each baseline uses the threshold on its grid with the highest quality averaged over all families, as in the original version. LoopStop has two hyperparameters, namely a memory (τ\tau) of 5 changes and a tolerated delay (DD) of 4 rounds. The rule averages the recent updates over the memory and should stop a loop within the delay after it settles. In the early development of LoopStop, we also measured alternatives for two parts of the rule on the cruise control, cart-pole, and ARC-AGI families. These measurements compared a constant reference value with a reference value that grows with the direction that the loop has shown. We further compared two forms of the cap on that value. The memory was set to the smallest value at which the rule improved on its previous version, whereas the delay and the derived constants were not chosen on data.

Our revised paper reports results for 12 families under this setting (see Section GR.1 above). Two further results show that LoopStop's quality comes from the rule instead of from the choice of its setting:

  • Other settings rank higher. By mean quality over all families, the setting used in our experiments ranks 11th of the 35 grid settings. A search for the highest quality would thus have chosen another setting, which uses more rounds on every family (Table R1 above and Table R5 below).
  • Settings chosen on other families give the same result. If every method (including baselines) uses the setting with the highest mean quality over the other families, LoopStop delivers the most quality on every family left out. On the mean, LoopStop then uses more rounds than RLF and fewer than PoR and PoU (Table R5).

Table R5. Settings chosen on the other families, from the new Tables H.20 and H.21 in Appendix H.7.3. Part (a) gives the true quality (%), and part (b) gives the rounds used, with standard errors over seeds. The second column gives the (τ\tau, DD) chosen for LoopStop.

Table R5(a). True quality (%)

Family left outLoopStop's (τ\tau, DD)Run to budget (reference)PoRPoURLFLoopStop
Cart-pole(10, 4)20.4 ± 1.620.4 ± 1.620.1 ± 1.520.7 ± 1.224.0 ± 1.4
Cruise control(10, 4)39.3 ± 1.139.2 ± 1.139.5 ± 1.135.3 ± 1.655.1 ± 1.3
Ship heading(10, 3)31.2 ± 0.929.8 ± 0.926.0 ± 0.918.6 ± 1.134.9 ± 1.3
Two-mass spring(10, 4)31.6 ± 0.731.2 ± 0.727.9 ± 0.824.3 ± 1.035.4 ± 0.8
ARC-AGI(10, 4)65.0 ± 0.165.0 ± 0.165.1 ± 0.165.2 ± 0.165.6 ± 0.1
BigCodeBench-Hard(10, 4)57.9 ± 0.157.8 ± 0.157.8 ± 0.154.1 ± 0.259.4 ± 0.2
MLAgentBench-Kaggle(10, 4)47.2 ± 0.847.1 ± 0.847.3 ± 0.844.5 ± 1.048.0 ± 1.2
TravelPlanner(10, 4)62.3 ± 0.162.3 ± 0.162.3 ± 0.159.6 ± 0.163.3 ± 0.1
GPQA Diamond(7, 4)67.0 ± 0.267.0 ± 0.267.1 ± 0.265.5 ± 0.467.4 ± 0.2
SuperGPQA(10, 4)41.6 ± 0.341.6 ± 0.341.6 ± 0.341.4 ± 0.242.5 ± 0.2
SciBench(10, 4)66.4 ± 0.266.4 ± 0.266.4 ± 0.265.3 ± 0.266.5 ± 0.1
TheoremQA(10, 4)69.9 ± 0.169.9 ± 0.170.0 ± 0.168.8 ± 0.270.7 ± 0.1
Mean50.0 ± 0.249.8 ± 0.249.3 ± 0.246.9 ± 0.252.7 ± 0.2

Table R5(b). Rounds used

Family left outLoopStop's (τ\tau, DD)Run to budget (reference)PoRPoURLFLoopStop
Cart-pole(10, 4)100.0 ± 0.098.2 ± 0.492.5 ± 0.96.2 ± 0.551.6 ± 1.3
Cruise control(10, 4)100.0 ± 0.093.8 ± 0.783.1 ± 1.021.1 ± 1.441.2 ± 1.7
Ship heading(10, 3)100.0 ± 0.089.2 ± 1.159.5 ± 0.817.0 ± 1.661.2 ± 1.3
Two-mass spring(10, 4)100.0 ± 0.093.7 ± 0.660.1 ± 0.815.4 ± 1.466.4 ± 0.5
ARC-AGI(10, 4)60.0 ± 0.059.7 ± 0.159.5 ± 0.05.0 ± 0.035.5 ± 0.1
BigCodeBench-Hard(10, 4)60.0 ± 0.057.6 ± 0.055.6 ± 0.15.1 ± 0.042.8 ± 0.0
MLAgentBench-Kaggle(10, 4)60.0 ± 0.059.7 ± 0.156.5 ± 0.46.8 ± 0.340.7 ± 0.4
TravelPlanner(10, 4)60.0 ± 0.060.0 ± 0.059.9 ± 0.05.1 ± 0.032.3 ± 0.1
GPQA Diamond(7, 4)60.0 ± 0.060.0 ± 0.059.7 ± 0.05.0 ± 0.024.3 ± 0.1
SuperGPQA(10, 4)60.0 ± 0.059.9 ± 0.059.7 ± 0.05.0 ± 0.031.7 ± 0.0
SciBench(10, 4)60.0 ± 0.059.9 ± 0.059.7 ± 0.05.0 ± 0.033.9 ± 0.0
TheoremQA(10, 4)60.0 ± 0.059.8 ± 0.059.5 ± 0.05.0 ± 0.033.8 ± 0.0
Mean73.3 ± 0.071.0 ± 0.163.8 ± 0.28.5 ± 0.241.3 ± 0.2

In the revised paper, we have added the ranks in Appendix H.7.2 (previously I.7) and the leave-one-family-out results in the new Appendix H.7.3.

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