Agent evolution follows a simple loop: a proposer writes candidate artifacts (prompts, skills, memories) and selection accepts those that score higher. This loop has shown promise, yet practitioners face a puzzle: methods trade wins across papers, and evolution often fails to bootstrap on certain tasks. We trace this puzzle to the Resolution Hypothesis: agent evolution stalls not because methods fail to propose better artifacts, but because noisy evaluations cannot reliably identify them. Across seven evolution methods and six models (over 10M LLM calls), we find support for the hypothesis at both levels where evaluation scores are used. At the candidate level (choosing artifacts), helpful candidate artifacts exist, but selection is no better than random at telling them from harmful ones, so errors accumulate across rounds. At the method level (ranking methods), typical margins of a few percentage points are smaller than the difference between two independent runs of the same method, so published rankings often rest on luck. Together, these findings indicate that agent evolution is often bottlenecked by reliably identifying improvements. This calls for a shift in how we develop and evaluate self-improving agents, from designing ever more candidate improvement systems to making true improvements detectable and accumulable.
Figures & tables
Figure 1: (a) Four candidate moves on the same landscape, scored under high and low evaluation noise (thought bubble: score relative to the current artifact). Under high noise, a worse candidate artifact scores highest. (b) Agent evolution as a loop: a proposer writes candidate artifacts, and a selector accepts the artifacts with the highest noisy score. P1–P3 are the predictions we test in Section 5 .
Figure 2: (a) Gap between all-run means of same-benchmark configuration pairs vs. the standard deviation of a single-run comparison; shaded: gap below one standard deviation. (b) Runs per method to identify the median literature margin (3.4 pp) at 80% power; gray bar: interquartile range 1.2–6.6 pp. Per-method values: Table 6 . Typical method differences are within single-run resolution.
Figure 3: (a) Unevolved baseline plus one rule. (b) Same artifacts under the repaired evaluation (per-pair values: Appendix E.2 ). The largest reported gains are reproduced by one sentence and vanish after repair.
Figure 4: Candidate quality in the Proposal Pool (a) and what selectors recover on the Selection Pool (b). (a) Quality@ K (solid) vs. matched equal-quality null (dashed) across the 10 disjoint Terminal-Bench v2.1 test tasks of the Proposal Pool ( n=100 skills, 16 rollouts each), contrasting the 2-hour budget (blue) against the original per-task timeout (charcoal) under the κmax=100 empirical-Bayes estimator; shading shows pointwise 95% posterior credible intervals (observed) and 95% null simulation ranges. (b) Selected-artifact gain over baseline vs. candidate budget K across the 11 tasks of the Selection Pool (Appendix F.1 ; held-out quality reference in Appendix F.3 ); random draws an artifact rather than the baseline, and the oracle is clipped to the selector range.
Selection
Pairwise acc. (%)
False accept. (%)
Random
50.0 ± 0.0
30.5 ± 14.0
Execution (1 rollout)
49.7 ± 1.9
62.1 ± 42.9
SkillOpt-Lite †
48.6 ± 2.6
59.4 ± 46.2
GEPA †
48.6 ± 2.6
31.6 ± 14.5
LLM judge (pointwise)
45.4 ± 4.5
39.9 ± 17.5
LLM judge (pairwise)
49.0 ± 2.2
57.6 ± 23.3
Table 1: Selection mechanisms evaluated at K=n on the fixed candidate pool. Pairwise acc. : probability that the selector picks the higher-quality artifact in a head-to-head comparison; 50% is chance. False accept. : among artifacts accepted as baseline replacements, the fraction that are actually worse. Values are posterior means ± half-width of 95% credible intervals. † Uses two visible rollouts per artifact; all others use one. Neither execution-based selection nor LLM judges can reliably identify helpful artifacts among regressions.
Figure 5: In-loop vs. independently re-evaluated validation gains across rounds (relative to initialization; shading: 95% bootstrap intervals over eight runs). In-loop gains reflect noise exploitation, not true improvement.
Figure 6: Run-to-run variance τ^t2 over rounds ( τ02=0 ; dashed: raw; solid: noise-corrected; shading: 95% bootstrap intervals over eight runs). Run-to-run variance grows over rounds.
Appendix figures & tables10 assets
Supplementary material from the paper’s appendix.
Appendix
Method
Evolves
Proposer writes
Selection
SkillOpt-Lite
skill document
1 edit per round, ≤ 10 rounds
accept if the validation score is ≥ 2 points above the current skill
GEPA
skill prompt
full rewrite, 1 per iteration
3-task training gate; parent sampled from the Pareto frontier on validation
Trace2Skill
skill document
1 patch per trajectory, merged
none (all patches kept)
ReasoningBank
memory bank
≤ 3 memories per task
none (all memories kept)
HarnessLens
instructions, skills, tool descriptions
1 edit per cycle
paired check on training tasks; best confirmed candidate on validation
Meta-Harness
harness code
new program, 1 per round
best training score of 5 candidates
Appendix
Table 2: What each method evolves, what its LLM proposer writes, and how it decides what to accept, as run on ALFWorld, SpreadsheetBench, and OfficeQA. Every validation score is one rollout per task.
Figure 7: Distribution of the score a single run would report, one evolution evaluated once, for the unevolved baseline (Base) and the four text-artifact methods (SOL: SkillOpt-Lite, GEPA: GEPA, RB: ReasoningBank, T2S: Trace2Skill) on all four benchmarks (Terminal-Bench for DeepSeek-V4-Flash, GPT-5.6 Luna, and GPT-5.6 Terra only), obtained by resampling the observed artifacts and their repeated evaluations ( 105 draws). The dotted line marks the mean over all runs and evaluations. Each ridge is scaled to the same height, and the horizontal range differs between panels.
Benchmark
Shortcut in the released evaluation
Repair
SpreadsheetBench
Formula cells are read without recalculation, so every formula scores as empty
Recalculate with LibreOffice before comparison, as the official evaluation does
AIME 2025
The parser accepts only a bare integer
Equivalence check after removing L a T e X wrappers
LiveMathematicianBench
A “stronger result” option is correct whenever it appears
Score only questions without that option
DocVQA
Near-exact string match (ANLS ≥0.999 )
Semantic grading
HotpotQA
Exact match rejects correct answers written differently
Semantic grading
OfficeQA
The version released with SkillOpt-Lite drops the official instruction to answer with a bare value
Restore the official instruction and reward
Appendix
Table 9: Shortcuts in the released evaluations and their repairs.
Benchmark
Rule appended to the baseline
SpreadsheetBench
Write computed literal values into the answer cells, never Excel formula strings: compute the result in Python and write the resulting number or text.
AIME 2025
Provide final answers exactly in the requested format: single integer, fraction in lowest terms, or exact closed-form expressions without additional commentary or formatting.
LiveMathematicianBench
If one option states that one of the remaining options is correct but a stronger result can be proven, choose that option.
DocVQA
Inside <answer> , output only the minimal span exactly as printed in the document, with no full sentence, field label, unit, qualifier, or trailing period.
HotpotQA
The answer is scored by exact match against a short reference answer. Output only the minimal answer span, with no full sentence, explanation or qualifiers.
OfficeQA
Put only the bare value inside <answer> : no units, currency signs, %, or explanatory words, unless the question explicitly asks for them. Keep the requested decimal places.
Appendix
Table 10: Rules used in the one-rule test, abridged; the full text is released with our code. The ALFWorld rule is a short search procedure rather than a statement about evaluation. LiveBench-Math and IFBench have no rule (Appendix E.2 ).
Figure 8: Per-benchmark gain audit. Gray: gain reported under the released evaluation. Black tick: unevolved baseline plus one rule. Green: the same artifacts under the repaired evaluation. Light bar with dotted end: headroom after repair (100 minus the repaired baseline). SpreadsheetBench gains and the rule use the released grader; its repaired values use LibreOffice recalculation.
Figure 9: Effect of agent timeout cutoff on Quality@ K vs. the matched equal-quality null on the Proposal Pool (10 disjoint Terminal-Bench v2.1 test tasks, n=100 skills, κmax=100 empirical-Bayes estimator). Panels (a)–(e) evaluate the same 16,000 trajectories under progressively relaxed cutoffs: original per-task timeout ( 900–1800 s), 2× , 3× , 4× , and the full 2-hour budget. Panel (f) overlays the net excess above the matched null across all five cutoffs.
Figure 10: Per-task Quality@ K (solid) and matched equal-quality null (dashed) across all 10 disjoint Terminal-Bench v2.1 test tasks of the Proposal Pool under the 2-hour budget (blue) and original per-task timeout (charcoal), using κmax=100 empirical Bayes; each panel uses its own vertical scale.
Figure 11: Sensitivity of macro-averaged Quality@ K vs. matched equal-quality null under the 2-hour budget to the upper concentration cap κmax∈{30,100,300,∞} of the empirical-Bayes Beta prior. A tight cap ( κmax=30 ) inflates dispersion in homogeneous null pools, whereas κmax=100 (primary) through unbounded ( κmax=∞ ) behave consistently and cleanly separate observed from null.
Figure 12: Per-task selection curves underlying Figure 4 b across the 11 tasks of the Selection Pool. Each panel shows selected-artifact success probability under the held-out quality reference (Appendix F.3 ); the oracle and its credible band are clipped to the selector range.
Method
σreward2
σbehavior2
Ratio
Baseline
0.073
0.0013
57 ×
GEPA [ 2 ]
0.074
0.0026
28 ×
HarnessLens [ 36 ]
0.056
0.0044
13 ×
Meta-Harness [ 15 ]
0.084
0.0015
57 ×
ReasoningBank [ 27 ]
0.075
0.0021
35 ×
AHE [ 18 ]
0.095
0.0022
44 ×
Appendix
Table 13: Variance of the evaluation noise: terminal pass/fail vs. a process metric (fraction of check commands without masked failure diagnostics), DeepSeek-V4-Flash.
Agent harness evolution enables recursive self-improvement (RSI) without updating model weights. We examine whether higher benchmark scores yield reliable, efficient, and transferable improvement. We evaluate four methods across harnesses, general and coding tasks. Repeated evaluations, controlled agent expansion, component interventions, and admission replays reveal recurring patterns. All sixteen evolved agents gain previously uncovered tasks while losing previously covered ones. In one general-task case, reliability rises by 5.2 points despite losing ten previously covered tasks. Most reliability gains also increase deployment cost. Specific changes usually outperform generic reminders, but their benefits can change when combined. The highest-scoring agent does not yield the largest mean improvement in any of our four pools, and stricter admission can discard useful alternatives. Transfer selectively preserves gains: coverage usually falls on the general-task target across both harness types and paradigms, but rises on the coding target with the outer-layer-only harness. These findings motivate preservation-aware evaluation, tested decision rules, and explicit applicability conditions. As a constructive follow-up, EvoAudit turns these diagnostics into revisions of select, analyze, mutate, and gate, achieving the best performance.
Xiaobo Wang, Zimu Wang, Siyu Ye +13
University of Science and Technology of China · Beijing Institute for General Artificial Intelligence · University of California, Berkeley +2
Self-evolving agents improve through repeated cycles of modification and evaluation. However, existing methods receive feedback on modifications only after costly evaluations, and aggregate scores may obscure distinctions between failures that require different repairs. We introduce predictive self-evolution through an editable Improvement Dynamics Model (IDM). Before evaluation, the IDM predicts task-level outcomes of a proposed modification and guides an optional revision. After evaluation, past modifications and their observed outcomes are used to improve the IDM, allowing predictive knowledge to accumulate across generations. The system can thus improve how it solves tasks, proposes modifications, and predicts their effects. Building on HyperAgents, we evaluate this approach across multilingual coding, paper review, robotics reward design, and Olympiad-level mathematical grading. Our approach outperforms HyperAgents across all four domains, with up to 46% higher average performance over generations. Gains also persist under matched token budgets that include both agent evolution and task evaluation, and extend to held-out tasks. Forecast accuracy improves as the IDM evolves, and the learned predictive knowledge transfers to improve evolution in a new domain.
Zixuan Xie, Chang Xu, Yuhua Jiang +1
University of Virginia · Microsoft Research · Tsinghua University
2026 has brought an explosion of interest in LLM-guided evolution of agentic artifacts, with systems like GEPA and Autoresearch demonstrating that LLMs can iteratively improve prompts, code, and agent architectures across diverse domains. As adoption accelerates, a central question emerges: given the same information, the same seed agent, and the same objective, which optimization algorithm yields the best results under the same evaluation budget? This question becomes critical when evaluations are expensive, such as when they require human judgment or multiple LLM calls. We present the first systematic comparison of three optimization paradigms -- Elo tournament selection (RoboPhD), Pareto-based selection (GEPA), and greedy hill-climbing (Autoresearch) -- across four benchmarks spanning abstract reasoning, cloud scheduling, SQL generation, and financial QA, all under a fixed budget of 1,500 evaluations. RoboPhD introduces validation-free evolution: instead of splitting the budget between training and validation, it uses Elo competition on training data to simultaneously evaluate agents and drive evolution. All three systems receive seed agents with diagnostic print() statements that evolution can grow, enabling self-instrumenting agents that develop increasingly informative diagnostics for the benefit of their evolutionary successors. Using a single default configuration, RoboPhD outperforms both GEPA and Autoresearch on three of four benchmarks, losing only on the simplest task, where the winning solution (from our Autoresearch adaptation) required under 90 lines of code. On ARC-AGI, RoboPhD evolves a 22-line seed agent into a 1,013-line multi-strategy system, improving accuracy from 27.8% to 65.8% using Gemini 3.1 Flash Lite as the solver. We release RoboPhD as a versatile toolkit under the MIT license with a simple optimize_anything() API for evolving diverse complex agents.