Artificial Intelligence · arXiv:2610.08215 v2 · submitted 6 Oct 2026
Learn2Play Bench: How Well Do LLM Agents Learn from Experience in Unfamiliar Environments?
The paper says
“Learning from experience is essential for LLM agents to adapt to unfamiliar and dynmaic environments. Evaluating this ability is therefore important for understanding how effectively agents acquire and use new knowledge.”
more of the abstract
Existing benchmarks have sought to evaluate this ability, but they primarily evaluate tasks whose rules are provided in the instructions or already familiar to pretrained models, making it difficult to distinguish learning from interactions from reasoning with existing knowledge. To address this, we introduce Learn2Play Bench, a benchmark of newly designed text-based games, whose rules are novel or counterintuitive, requiring agents to acquire knowledge through interaction rather than rely solely on pretrained knowledge. These games provide reproducible feedback and automatic scoring, enabling controlled evaluation of learning across repeated attempts. We also vary game instances to test whether agents can apply what they have learned to new situations. Therefore, we evaluate how backbone models, self-evolving methods, and agent harnesses affect agents' learning ability, revealing three findings: (1) Experience retention: Retaining complete records of actions and feedback can support more effective learning than summarizing these experiences into rules or strategies. (2) Human agent gap: Top-performing human players achieve higher peak scores than the evaluated agents. Human explore more varied strategies, and repeat actions less. (3) Harness matters: With the backbone fixed, changing the harness can improve performance while reducing estimated inference cost. Together, these findings provide insights into how LLM agents learn from experience and suggest directions for future work to improve their learning ability. Project website: https://liushiliushi.github.io/learn2play-bench-website/
from the abstract
Pith says
Machine review · deepseek-v4-flash · 7 Oct 2026 · of version 1 of the paper; version 2 is newer · what was read was not recorded · not checked by a person
It can be wrong. Challenge this review or reply to it.
Holds up, with conditions. A genuinely useful, unusually transparent benchmark for measuring agent test-time learning, but the central claim that its rules cannot come from pretraining is asserted, not tested; fixable with a zero-play baseline and significance tests, and worth sending to review either way. This line is wrong
4 major objections · 4 minor
How often objections from reviews like this one are right: not yet measured
Not checked: figures, code, what the references say.
The paper says, at Section 3 and Abstract; Tables 1, 62, 35
The review did not quote this passage.
Pith says: Objection 1 of 4 · major
The benchmark's load-bearing premise — that the games have 'novel hidden rules not found in existing games,' so that agents 'must discover them by acting, observing textual feedback' — is asserted but never tested. No contamination check and no zero-shot or no-feedback baseline are reported.
more of objection 1
The NAIVE ablation (Table 1) is not a control for pretraining recall: it still receives within-episode feedback, so it cannot separate recalled structure from learned structure on rule templates like hidden-preference inference or delayed-effect planning. Moreover, the paper itself publishes complete per-seed solutions for the pinned instances in Appendix D (e.g., Table 62, T2 gives the exact five-feature conjunction for Poisoner seed 2; Table 35, T7 gives the unique 339 stocking vector), so the released materials are a genuine shortcut surface. Whatever the knowledge cutoffs of the evaluated models, the paper should add a no-feedback or blind-probe condition (goal plus initial state, no interaction, score the terminal state) and/or a documented leakage analysis; without it, the abstract's central 'learning from experience rather than pretrained knowledge' distinction is not established.
The paper says, at Tables 1, 2, 13–15; Sections 4.2.2, 4.3
The review did not quote this passage.
A classifier read this sentence of the paper as acknowledging the concern (probability 0.76):
“The small number of trials limits the precision of the SD estimates.”
Pith says: Objection 2 of 4 · major
Several headline claims rest on differences within the reported trial SDs, and no significance testing is provided. Example: the claim that MEMORY 'leads all four metrics with Kimi K3' (Section 4.2.2) — Max 63.3±4.0 vs EvoTest 62.4±3.5 vs Reflexion 61.6±3.2, and LG +16.9±4.0 vs Reflexion +14.8±4.7 is within about one-third of a combined SD; only the MEMORY-vs-EvoTest LG gap (+15.1, ~2.6 combined SD) is suggestive.
more of objection 2
Similarly, the harness claim (Section 4.3, Table 2) compares Claude Code Max 81.8±4.4 with OpenCode 74.5±2.6 (~1.4 SD) and LG +27.1±5.2 with +21.3±3.1 (~1.0 SD). The paper acknowledges SD precision limits (Appendix C) but still states findings 1 and 3 as established facts. A paired test over the 20 game-level values (e.g., Wilcoxon signed-rank on game-level Max/LG) would be cheap and would let the paper either support or appropriately hedge these claims.
The paper says, at Table 6 and Appendix A.2.4
The review did not quote this passage.
Pith says: Objection 3 of 4 · major
Four of twenty reference scores are labeled 'estimated' — CATNIP 320, DREAMGARDEN 6300, MOLA TEA 1000, PATCH REALITY 960 — and CATNIP and DREAMGARDEN are challenge games carrying weight 3 (Appendix A.2.3). Since every metric is computed as z = 100·x/C_g (Appendix A.2.2), any error in these caps enters every aggregate Max, Mean, LG, and LS linearly and could reorder configurations.
more of objection 3
The paper discloses the estimation and its evidence levels (A.2.4), which I credit, but it provides no sensitivity analysis. A focused perturbation (e.g., ±20% shift of the four estimated caps, holding exact/partial caps fixed) would establish whether the headline rankings survive.
The paper says, at Section 4.4, Table 1, Appendices B.3.1 and B.3.2
The review did not quote this passage.
Pith says: Objection 4 of 4 · major
The human-agent gap (finding 2) compares the single best of 21–30 participants per game against the mean of three agent trials. This mechanically favors the human side: the per-game 'Human Top-1' is a max-of-many statistic while each agent cell is a mean-of-few, and the paper itself reports Human Mean Max = 43.6 (B.3.2), far below the best agent (74.5).
more of objection 4
The 84.3 vs 81.8 Max gap is also within roughly one agent SD (81.8±4.4). The Top-k selection rule is disclosed in B.3.1, but the selection asymmetry that inflates the headline claim is not discussed. The paper should report a fairer comparison — e.g., per-game best human record vs per-game best agent trial, or how many of the 20 games Human Top-1 actually wins — and temper the claim accordingly.
4 minor objections
The paper says, at Abstract and Section 4.4
Pith says: minor objection 1 of 4
Typos: 'dynmaic' in the abstract; 'requiresss' in Section 4.4 ('succeeds requiresss executing').
The paper says, at Section 4.1, LG definition
Pith says: minor objection 2 of 4
The Learning Gain window k_g = min(3, ⌊T_g/2⌋) reduces to a two-episode window for normal games (T=5), so LG for fifteen of twenty games compares only episodes 1–2 against 4–5 and is quite noisy; consider also reporting a larger-window variant.
show 2 more
The paper says, at Footnote 1 and Appendix A.2.3
Pith says: minor objection 3 of 4
The choice of the five challenge games (weight 3, ten episodes) is based on pilot difficulty estimation. This is disclosed, but the paper should state whether the headline ordering is robust to equal-weight aggregation.
The paper says, at Table 3, Section 4.5
Pith says: minor objection 4 of 4
Two rows report negative LS drops (Qwen −0.41, Codex −0.19), meaning those agents learn faster under re-shuffling; the 'LS drop' framing and the Section 4.5 generalization ('changes can reduce learning slopes') would benefit from the same paired-test treatment suggested for the other comparisons.
What would settle it
Blind-play control: run four backbones (Claude Opus 5, Kimi K3, Qwen 3.8 Max, GPT-5 Mini) under the same OpenCode harness on all 20 pinned instances with the same seeds and 3 trials, but replace every environment feedback string with a fixed non-informative message (e.g., 'You performed an action.') while keeping action enumerations, episode endings, and terminal scores intact. Compare Max and LG against the Table 1 rows for these backbones, and also compare first-episode scores against a uniform-random-action control. If blind-play LG is near zero and first-episode scores are at chance, the novelty premise holds and the reported gains are attributable to feedback; if blind-play LG stays positive or first-episode scores exceed chance by more than the trial SDs in Appendix C, gains are at least partly pretraining recall and the benchmark's core claim needs re-scoping.
from the skeptic's reading
How the review went
4 readings by deepseek-v4-flash · 7 Oct 2026
- Reader holds up, with conditions
- Skeptic agrees
- Editor wrote the verdict above
- Referee major revision: 4 major objections, 4 minor
Not run on this paper: the simulated authors' defence.
Pith did not check this review's objections against the paper.
The review in full
The review in brief, machine-written
Two things to know. First, this is a serious benchmark paper, unusually transparent, with findings that look real in direction: raw interaction histories beat summarization methods, harness choice moves scores about as much as backbone choice, and weaker backbones transfer worse when instances are re-shuffled. Second, the paper's load-bearing premise — that its hidden rules are absent from pretraining and must be discovered by acting — is asserted (Section 3) but never tested. No contamination check, no zero-shot probe, no no-feedback baseline. The counterintuitive rule design (lunch theft leads to promotion) argues in the authors' favor, since models would predict the opposite, but that is a design argument, not a measurement. A zero-play baseline would settle it: give the goal and initial state, no interaction, and ask for the rules or the best action. The NAIVE ablation does not do this, because NAIVE still receives within-episode feedback.
Credit where it is earned. The 20-game suite is the contribution: deterministic feedback, automatic scoring, fixed versus re-shuffled instances, and a systematic comparison across nine backbones, six methods, three harnesses, and humans. Metric formulas, normalization, reference-score evidence levels, trial SDs, and per-game rule-discovery tables are all specified in the appendices. The paper is honest about its limits: the human behavioral statistics are explicitly descriptive, the small trial count is acknowledged, and the paper itself says one compression anecdote does not establish the aggregate effect. The self-cited methods (EvoTest, and Meta-TTL by way of attribution) mostly lose in its own comparisons, which is healthy.
Soft spots, in order of softness. The rule-novelty gap is the one that matters. If models merely recall structural templates we already know exist in agent benchmarks — hidden-preference inference, trap-and-decoy chains, delayed-effect planning — Learning Gain conflates retrieval with parameter discovery. This is fixable and not fatal: the specific parameters still require interaction, so the benchmark retains value. But the central distinction in the paper's title is currently a hypothesis, and the stress-test note lands. Second: trial SDs are wide (three trials per cell), and headline comparisons like Opus 5 LG +21.3 ± 3.1 versus Qwen +25.2 ± 4.5 are presented without significance testing. The paper reports the SDs, which is more than most, but then draws strong comparative conclusions from noise-level gaps. Add tests or downgrade those claims to descriptive. Third, minor: four reference caps are labeled estimated, and three of the five challenge games ride on them, concentrating a third of the total weight in uncertain denominators. The paper labels this clearly; a sensitivity note would finish the job. Fourth, minor: Human Top-1 Max (84.3) beats every agent, but Top-1 humans are selected per game on the outcome being compared; Human Mean (43.6) loses badly. The abstract's 'top-performing' qualifier keeps it honest, but the main text should state the asymmetry in one sentence.
Who this is for: anyone building or evaluating test-time learning agents, and anyone who wants a careful template for how a benchmark should report its variability. It deserves a serious referee. Send it to review; revisions should add the contamination or zero-play baseline, significance testing or softer comparative claims, and released code, data, and logs.
The strongest objection
The central claim, stated in the abstract and §3, is that Learn2Play's games have 'novel hidden rules not found in existing games', so that agents 'must discover them by acting, observing textual feedback, and carrying useful experience into later episodes'. Nothing in the paper tests this premise. No contamination check, no zero-shot probe, and no no-feedback ablation is reported. If any rule, or its structural template (hidden-preference inference, trap-and-decoy chains, delayed-effect planning, nontransitive orderings), is recallable from pretraining—or from the public project website, whose Appendix A and Tables 4–5 spell out per game what 'the player needs to learn' (e.g., 'infer taste constraints... apply them to new menus')—then positive Learning Gain trajectories partly reflect known structure, and the paper's whole distinction between learning from interaction and reasoning with pretrained knowledge collapses. The paper's own NAIVE ablation (Table 1: Kimi K3 LG +0.3, Opus 5 LG −5.1) is consistent with feedback-driven learning, but NAIVE still receives within-episode feedback, so it cannot separate recalled structure from learned structure. The question of whether Opus 5 or Qwen 3.8 Max, given only the goal and initial state, would spontaneously produce the counterintuitive rules (e.g., that stealing a colleague's lunch drives promotion) is never asked, let alone answered.
The reader's weakest_assumption is exactly this novel-rules premise, and I agree it is the load-bearing one. Of the reader's four conditions, the other three are method-level: code/log release and significance testing affect confidence but not the benchmark's purpose, and the human-gap framing asymmetry weakens a secondary finding. The estimated reference scores (Table 6: CATNIP 320, DREAMGARDEN 6300, MOLA TEA 1000, PATCH REALITY 960; combined weight 10 of 30) are a genuine correctness risk, but errors there rescale scores nonlinearly and can compress ceiling effects without destroying the learning-vs-recall separation; a violated novelty premise, by contrast, invalidates all three headline findings at once. I credit the paper's transparency: Appendix C reports trial SDs and acknowledges the small n=3 precision limit; Appendix A.2.4 labels reference-score evidence levels honestly; Appendix B.3.3 explicitly flags human behavioral statistics as descriptive and non-independent; and the per-game rule-discovery tables in Appendix D show what was actually observed, including honest '–' entries. The NAIVE ablation is genuinely informative—near-zero LG without cross-episode memory supports the interaction-driven story—and the paper does not hide the multiple-trial SDs. But the novelty of the rules, the reason this benchmark claims to measure learning rather than recall, has no direct evidence anywhere in the manuscript and is directly testable with a no-feedback control. Because the paper is otherwise honest and internally consistent, and the gap is a missing condition rather than a demonstrated error, the reader's CONDITIONAL verdict stands unchanged.
The referee's report
If the findings hold, they are informative for the test-time learning literature: the MEMORY-over-distillation result, the harness effect, and the human-agent behavioral contrast are all directly actionable, and the benchmark itself (20 games, pinned seeds, deterministic scoring, re-shuffled variants) is a reusable resource. The paper is unusually transparent: metric formulas are explicit (Appendix A.2), trial SDs are tabulated for every configuration-game cell (Tables 13–15), reference scores carry evidence labels (exact/partial/estimated), and several limitations are stated candidly (B.1.3 concedes the compression finding is not causal; B.3.3 calls the behavioral statistics descriptive; C acknowledges SD precision limits). The primary risk is to the benchmark's core premise: rule novelty is asserted (Section 3) but never tested, so measured Learning Gain is not cleanly separated from pretrained recall.
Pith's reading of the paper (a machine's summary, not the authors')
The paper tries to establish whether LLM agents can genuinely learn from experience, as opposed to recovering knowledge their pretrained weights already contain. To do that it introduces Learn2Play Bench, a set of 20 newly designed text-based games with hidden or deliberately counterintuitive rules that are not stated in the instructions. Agents must discover the rules by acting, reading textual feedback, and carrying experience into later episodes, all without updating model weights. The paper's three main findings are that retaining complete action-feedback histories can support stronger learning than summarizing those histories into rules, that top-performing humans still reach higher peak scores than the best agents, and that changing the agent harness while fixing the backbone can improve both performance and estimated inference cost. If these claims hold, they reframe how benchmark designers should isolate learning ability from world knowledge and give concrete engineering guidance about how to store an agent's experience.
What carries the argument. The carry the argument is the benchmark itself alongside its scoring scheme: 20 manually designed text-based game templates, half fixed and half re-shuffled each episode, with deterministic feedback and automatic scoring. Each episode returns a terminal score normalized against a per-game reference score, and four metrics are computed from the normalized trajectories: Max and Mean measure achieved performance, while Learning Gain (LG) and Learning Slope (LS) measure improvement across episodes. The fixed-versus-re-shuffled split is what tests transfer: re-shuffled games keep the underlying rule fixed but change the visible instance, so a rising score there indicates the agent applied a learned rule rather than memorizing a menu position or layout. The self-evolving methods being compared (Reflexion, EvoTest, ReasoningBank, Agent Workflow Memory) are the mechanisms whose behavior the benchmark is designed to adjudicate.
Core claim. The central claim is that learning from interaction and reasoning from pretrained knowledge can be separated by building games whose rules are novel, and that on such games three patterns emerge. First, the MEMORY method, which retains complete unmodified interaction histories across episodes, outperforms methods that distill experience into reflections, reasoning banks, or workflows: with Kimi K3 it leads all four metrics (Max 63.3, Mean 48.0, LG +16.9, LS +4.69), and the paper argues raw histories keep the original evidence available when earlier conclusions need revision, whereas distillation can turn incomplete evidence into a definitive rule based on a single failed attempt. Second, Human Top-1 achieves Max 84.3, higher than every evaluated agent configuration, with humans showing lower consecutive-action similarity (0.54 vs 0.66) and more recovery after setbacks (33% vs 22%). Third, with the backbone fixed, upgrading the harness from OpenCode to Claude Code raises Opus 5 from Max 74.5 to 81.8, and Codex similarly lifts GPT-5.6-SOL from 57.0 to 74.3, while reducing estimated inference cost through fewer model calls and less repeated context.
The premise it rests on. The claim that the benchmark's rules are truly novel, in the sense that no pretrained model can solve or shortcut a game without playing it, is asserted but not verified by any contamination check or zero-interaction baseline, and if any rule or its structural analogue is recallable from pretraining, the score gains attributed to learning would partly reflect existing knowledge.
If the paper is right (Pith's inferences, not the authors')
Benchmark design should favor hidden, counterintuitive rules with a zero-interaction check, so that score gains can be attributed to learning rather than to pretrained recall.
Experience-storage strategy is a first-order design choice: keeping complete action-feedback histories can support stronger learning than summarizing them into rules or workflows, because raw evidence preserves the option to revise earlier conclusions.
Harness engineering can matter as much as model choice: with the backbone fixed, a better-suited harness improved peak scores while lowering estimated per-episode cost.
Re-shuffled instances expose a transfer gap: weaker backbones show much larger drops in learning slope when the visible situation changes even though the rule is unchanged.
Exploration behavior, measured by action-sequence similarity and recovery after setbacks, distinguishes humans from agents and offers a target for future agent designs.
The novelty premise is the load-bearing assumption; the paper asserts the rules are not in existing games but reports no contamination check or zero-interaction baseline, so the central distinction between learning and recall would need an explicit pretraining-shortcut probe to be airtight.
The finding that raw histories beat distilled rules on these 20 games is a claim about this benchmark, and would be more convincing if tested on other novel-rule environments where context budgets press harder against full-history retention.
The human-agent gap, though reported only for top-selected players, suggests concrete agent-side levers: force periodic strategy switches and add recovery behavior after low-scoring episodes, mirroring the human statistics the paper reports.
Four of the twenty reference scores are labeled estimated rather than exact, and any error in those caps would shift every normalized aggregate metric; readers should treat the aggregate numbers as provisional until those references are proven or replaced.
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The paper
Abstract
Learning from experience is essential for LLM agents to adapt to unfamiliar and dynmaic environments. Evaluating this ability is therefore important for understanding how effectively agents acquire and use new knowledge. Existing benchmarks have sought to evaluate this ability, but they primarily evaluate tasks whose rules are provided in the instructions or already familiar to pretrained models, making it difficult to distinguish learning from interactions from reasoning with existing knowledge. To address this, we introduce Learn2Play Bench, a benchmark of newly designed text-based games, whose rules are novel or counterintuitive, requiring agents to acquire knowledge through interaction rather than rely solely on pretrained knowledge. These games provide reproducible feedback and automatic scoring, enabling controlled evaluation of learning across repeated attempts. We also vary game instances to test whether agents can apply what they have learned to new situations. Therefore, we evaluate how backbone models, self-evolving methods, and agent harnesses affect agents' learning ability, revealing three findings: (1) Experience retention: Retaining complete records of actions and feedback can support more effective learning than summarizing these experiences into rules or strategies. (2) Human agent gap: Top-performing human players achieve higher peak scores than the evaluated agents. Human explore more varied strategies, and repeat actions less. (3) Harness matters: With the backbone fixed, changing the harness can improve performance while reducing estimated inference cost. Together, these findings provide insights into how LLM agents learn from experience and suggest directions for future work to improve their learning ability. Project website: https://liushiliushi.github.io/learn2play-bench-website/
The paper's own sentences, arranged, kept beside the review and separate from it. Each label is drawn from a closed vocabulary; the number beside it is the probability the classifier gave that label. No sentence in this record was written by a model.
abstract compiled · 2026-10-07
The authors' main claim, as the classifier picked it out 0.69
“Together, these findings provide insights into how LLM agents learn from experience and suggest directions for future work to improve their learning ability.”
How the main claim is stated: hedged possibility 0.51
What the abstract itself states, as probabilities: claims first 0.10 · states limitation 0.49 · human participants 0.34 · controlled comparison 0.49 · randomized assignment 0.02 · states quantitative result 0.08 · compares with prior results 0.82 · mentions code or data availability 0.60
The abstract, sentence by sentence
This table labels the abstract only (arXiv listing abstract v1). The number is the probability the classifier gave the label.
| Sentence | Role | The authors' own work | States the main conclusion | Strength |
|---|---|---|---|---|
| Learning from experience is essential for LLM agents to adapt to unfamiliar and dynmaic environments. | background 1.00 | 0.05 | 0.02 | asserted 1.00 |
| Evaluating this ability is therefore important for understanding how effectively agents acquire and use new knowledge. | background 1.00 | 0.06 | 0.02 | asserted 0.99 |
| Existing benchmarks have sought to evaluate this ability, but they primarily evaluate tasks whose rules are provided in the instructions or already familiar to pretrained models, making it difficult to distinguish learning from interactions from reasoning with existing knowledge. | gap 0.98 | 0.06 | 0.02 | asserted 1.00 |
| To address this, we introduce Learn2Play Bench, a benchmark of newly designed text-based games, whose rules are novel or counterintuitive, requiring agents to acquire knowledge through interaction rather than rely solely on pretrained knowledge. | contribution 0.96 | 0.89 | 0.04 | asserted 1.00 |
| These games provide reproducible feedback and automatic scoring, enabling controlled evaluation of learning across repeated attempts. | method 0.88 | 0.78 | 0.02 | asserted 0.99 |
| We also vary game instances to test whether agents can apply what they have learned to new situations. | method 0.91 | 0.88 | 0.02 | asserted 0.96 |
| Therefore, we evaluate how backbone models, self-evolving methods, and agent harnesses affect agents' learning ability, revealing three findings: (1) Experience retention: Retaining complete records of actions and feedback can support more effective learning than summarizing these experiences into rules or strategies. | result 0.91 | 0.96 | 0.28 | asserted 0.97 |
| (2) Human agent gap: Top-performing human players achieve higher peak scores than the evaluated agents. | result 1.00 | 0.93 | 0.11 | asserted 1.00 |
| Human explore more varied strategies, and repeat actions less. | result 0.83 | 0.86 | 0.05 | asserted 1.00 |
| (3) Harness matters: With the backbone fixed, changing the harness can improve performance while reducing estimated inference cost. | result 1.00 | 0.94 | 0.12 | asserted 0.96 |
| Together, these findings provide insights into how LLM agents learn from experience and suggest directions for future work to improve their learning ability. | interpretation 0.76 | 0.57 | 0.29 | hedged possibility 0.51 |
| Project website: https://liushiliushi.github.io/learn2play-bench-website/ | contribution 0.57 | 0.15 | 0.02 | unclear 0.89 |
What kind of paper the classifier reports this is: dataset or benchmark 1.00 · evidence from observation or experiment 0.98
What was examined, and what was not
Sources read
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Cited by 2 Pith papers
Reviewed papers on Pith that cite this one. The full citation record
- PlayCraft: Designing Engaging Games from Agent Play Experience cs.AI · Nov 2026
- The World Won't Wait: Evaluating and Teaching Agents Under a Live Clock cs.AI · Oct 2026
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