- Rating
- 4
- Confidence
- 3
- Informativeness
- 3
- Presentation
- 3
- Soundness
- 3
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Paper summary
The paper proposes a benchmark dataset, called ExplorationBench, to evaluate if AI systems can get real new knowledge by actively exploring, rather than only relying on recalling and reasoning over existing knowledge. Specifically, it introduces AlienCode and AlienLogic, which are two executable sandboxes with deliberately conflicting rules against those of familiar priors. The system learns by exploring and interacting with the environment for 4 rounds, and after that it is asked to solve questions in the held-out set without the help of tools. Three distinct milestones, including probe design, rule discovery, and rule application, are reported and evaluated verifiably without the help of an LLM judge.
Critical strengths
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All the questions in this benchmark are rigorously verifiable via an interpreter or proof checker, and no LLM judge is involved. The benchmark is designed in such a way that the pretraining priors actively conflict with the hidden rules, so the model is also not gonna be able to hack it by recalling. All this makes the work a trustworthy benchmark to probe LLM systems' ability to explore new knowledge and is resistant to data contamination.
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The work provides two different sandboxes that comprehensively measure LLMs' capability across different cognitive operations, including both program synthesis and formal proof. The detailed case study provided by the authors also provides insight into the underlying mechanisms of LLMs for exploring new knowledge.
Critical weaknesses
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The benchmark datasets are still of a synthetic nature. Without the presence of other natural science domains, it remains unclear how the capabilities benchmarked against this work would translate into performance on real-world scientific exploration.
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Only 3 trajectories per system per sandbox are sampled, which are not sufficient for estimating the trajectory distribution at any level of precision. The 73.3 points variance shown in finding 7 is very extreme, confirming this lack of precision. Also, the Best@3 metric itself can be misleading, since this metric only answers "if a system can ever succeed" rather than "if this system can reliably succeed", which may, in turn, favor unreliable systems with just one lucky trajectory.
Questions for authors
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Your Finding 2 (designing probes beats receiving identical evidence) is one of the most intriguing results in the paper. Can you provide a more detailed analysis of the mechanism behind this finding, or do a case study of the high-performing trajectories to characterize their behavior?
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Can you report rankings at higher ns, say n=5-10? You claimed in the paper that the choice of aggregate changes the ranking, but I am still not fully convinced, since more trajectories might, in turn, stabilize the ranking.
6 comments
Response to Reviewer 9jG5 (2/3)
Why the main ranking uses three attempts (W2, continued). This is part of the evaluation design, not only a matter of cost. We measure how well a system explores with limited opportunities: at most 12 tool calls in each of four rounds, and likewise only three independent attempts. Best@3 therefore asks not whether a system can succeed at all, but whether it succeeds within three attempts. A system that needs many attempts to produce one good trajectory explores less efficiently, and once attempts are unlimited, the score increasingly rewards retrying, as the Seed2.1 Pro example shows. Keeping n small is precisely what limits the effect of "one lucky trajectory" that you are concerned about.
For reliability, the revision reports Mean@n and Worst@n beside Best@3, with bootstrap confidence intervals for Mean@n (Table 6); where the Mean@n intervals of two systems overlap, we do not claim that their reliability differs. The paper's main conclusions rest on controlled comparisons between conditions, not on fine-grained rankings between systems. These results are in Appendix G.3 (Table 6), and the discussion of Best@n is in Appendix C.1.
Question 1: Your Finding 2 (designing probes beats receiving identical evidence) is one of the most intriguing results in the paper. Can you provide a more detailed analysis of the mechanism behind this finding, or do a case study of the high-performing trajectories to characterize their behavior?
Response: To analyze the mechanism, we ran a paired hindsight experiment: each of the first five autonomous trajectories of every system is replayed with its own probes, and each trajectory is compared with its own replay, so that neither side is selected by its score. The results led us to revise the argument for this finding, and revealed a new one.
(1) The original gap came mainly from selecting the best trajectory. Given identical evidence, designing the experiments autonomously brings no detectable extra benefit. Over 49 pairs in AlienCode, the mean difference is −2.2 points (95% CI −9.8 to +5.3, p = 0.40). Over 50 pairs in AlienLogic, it is 0.0 points (95% CI −2.1 to +1.9), statistically equivalent within ±2 points (see our response to Reviewer VuUJ).
(2) Yet designing one's own experiments still matters. At three repetitions each, fixed-probe exploration falls below autonomous exploration for 10/10 systems in both sandboxes, by a median of 31.7 points in AlienCode and 16.0 in AlienLogic (p = 0.002). The revised Finding 2 is therefore: the gain of exploration comes from the evidence carried by the experiments a system designs itself; handing the same evidence back to the same system recovers the gain, whereas generic probes do not.
(3) Mechanism: the bottleneck lies at a different step in each sandbox.
| Sandbox | Mean absolute difference, trajectory vs. its replay | Correlation | Share of between-trajectory spread explained by the probes |
|---|---|---|---|
| AlienCode | 14.5 points | 0.73 | 43% |
| AlienLogic | 3.4 points | 0.88 | 89% |
- AlienLogic: the evidence almost determines the outcome; which proofs were tried sets the accuracy reached.
- AlienCode: more than half of the spread remains once the evidence is fixed. For example, Claude Opus 5's second trajectory reaches 49.0% autonomously but 83.3% when its probes are replayed; Gemini 3.8 Flash's fourth trajectory reaches 76.2% autonomously but only 8.1% on replay.
This gives controlled support for Finding 4 of the paper: AlienLogic is limited by discovering the rules, and AlienCode by using them.
(4) What high-scoring trajectories do: the key evidence comes early and quickly becomes a rule. We compare the 25 autonomous AlienCode trajectories that end at or above 75% (mean 83.1%) with the 27 that end below 25% (mean 12.7%), focusing on the two keystone rules R14 (the PLUCK index shifts left by one) and R15 (both CARVE bounds shift left by one):
- High-scoring trajectories: all 25 ran an experiment exposing R14 within the first two rounds and state R14 correctly at M4; 23 stated it in the round of exposure or the next, 15 in the same round. R15 is similar: 24 exposed it within two rounds, all 25 state it at M4, and 24 stated it within one round of exposure.
- Low-scoring trajectories meet such experiments later. Of the 24 that exposed R14, only 1 did so in round 1, most in rounds 2 and 3; none of the 22 that exposed R15 did so in round 1. Most also never state the rule: 20 of the 24 for R14 and 19 of the 22 for R15.
The next comment traces two such trajectories.
Response to Reviewer 9jG5 (3/3)
Two high-scoring trajectories (Q1, continued). The rules involved are all introduced in the paper's case studies; lists and indices below are actual values after the rewrite.
- Integer literals are rewritten (R01, R01+). At the top level an integer is XOR-ed with 27, so 0 is written 27 and 1 is written 26. Inside a function (
CRAFT) body it is XOR-ed with 53 instead, so 0 is written 53 and 1 is written 52. - R14:
PLUCK(seq, i)actually takes element i−1, so index 0 returns the last element. - R15: both bounds of the slice
CARVEshift left by one. - R16:
STRANDbuilds a list in reversed order.
Case 1: misread at first, then corrected by an experiment that tells two readings apart (Claude Opus 5, trajectory 1, M4 82.4%).
- Round 1: the experiment cannot tell two readings apart. The system takes index 0 of the list [24, 25, 26] and gets 26. Two readings explain this: under the true rule the index shifts left, 0 becomes −1, and the last element, 26, is returned; under "reverse the list, then index", element 0 of [26, 25, 24] is also 26. Since
STRANDalready reverses, the system chose reversal: its M1 report states R14 as(get (reverse seq) i)and R15 with swapped bounds as(slice seq (+ hi 1) (+ lo 1)), and accuracy is 16.2%. - Round 2: an experiment that tells them apart. The system takes index 1 of the four-element list [31, 24, 25, 26]: shifting left predicts 31, reversing predicts 25, and the sandbox returns 31. The system then writes "PLUCK is 1-based". In the same round, a slice on four elements returns [31, 24], where the swapped bounds predict an empty list.
- Result: the M2 report states R14 and R15 correctly, and accuracy rises from 16.2% to 83.8%, and from 12.4% to 81.0% on the 51 tasks that use R14 or R15. When all of this trajectory's probes are replayed to the same model, the jump occurs at the same milestone (M1 16.7%, M2 82.9%).
Case 2: rules stated correctly but not used, until the system chased an anomaly it had recorded (Claude Opus 5, trajectory 5, M4 90.0%).
- Stated, but not used. From M0 on, this trajectory states R01+ correctly from the worked examples (69 of the 70 tasks need it). At M3 its report states 26 rules correctly, including R14 and R15, yet accuracy is only 14.3%, because its answers still encode numbers inside function bodies with the top-level key 27. For example, task A46 asks for a function that returns the last element of a list. The answer
DELIVER PLUCK(lst, 27)means index 0, but inside a function body 27 becomes 46, the index is out of range, and every test fails. Of the 70 answers at M3 (the first per task), 59 write top-level values such as 27 and 26 inside function bodies, and only 3 write 53 or 52. - An anomaly it recorded. The last experiment of round 3 is a recursive factorial. The system meant "return 1 when n ≤ 1" and wrote
UPON BENEATH(n, 26): DELIVER 26, but inside the body 26 becomes 47, so fact(5) returns 47. Its round summary says: "Unsolved: the recursive factorial fact(5) returns 47 (should be 120). … the next round must locate the true semantics of recursion and nested calls." - Round 4 chases it. The system reproduces the effect with several functions and writes "Breakthrough! Literals inside function bodies seem to use a different key." It then writes 0, 1 and 100 inside a function body, gets 53, 52 and 81, and concludes "Key inside function bodies = 53 (top level = 27), fully verified." Rewritten with key 53, the factorial returns the correct 120.
- Result: the report states the same 26 rules at M4 as at M3, yet accuracy rises from 14.3% to 90.0%, and from 9.8% to 88.2% on the 51 tasks that use R14 or R15. 66 of the 70 answers now use the function-body key, and A46 passes every test.
The two cases show three things:
- High-scoring trajectories run targeted experiments. Each one either separates two of the system's own hypotheses (Case 1) or chases an anomaly it met (Case 2), designed from its hypotheses at the time. Fixed generic probes cannot do this, which can explain why fixed-probe exploration falls far below autonomous exploration.
- Once the experiment is run, the evidence suffices. Replayed with the same probes, the same model learns at the same point (Case 1). This is the revised Finding 2.
- Stating a rule is not using it. In Case 2 the rule report does not change at all, yet accuracy rises by 75.7 points, consistent with Finding 6.
In summary, the revision rewrites Finding 2 according to these results. The paired experiment is in Appendix G.1 (Table 4), the statistics on high- and low-scoring trajectories in Appendix G.4, and the two cases are Cases 5 and 6 in Appendix H.
Thank you again for your careful review and valuable suggestions. All new experiments and changes are in the revised paper; please let us know if you have any further questions.
Response to Reviewer 9jG5 (1/3)
We sincerely thank you for your recognition of our work and your valuable suggestions! To answer your questions, we ran 140 new autonomous trajectories so that every system now has ten per sandbox, replayed the probes of each system's first five trajectories to study the mechanism behind Finding 2, and traced two high-scoring trajectories probe by probe. All new experiments and changes are included in the revised paper.
Response: We agree that this is a boundary of our work. The design choice rests on three considerations:
(1) Artificial worlds make exploration exactly measurable. Measuring exploration requires two things at once. First, answers must be exactly verifiable, whereas testing a new hypothesis in real science is often costly and slow, and observations are noisy. Second, answers must not be recallable, whereas the laws of known domains are present in pretraining corpora. The rules of the Alien Worlds are executable and conflict with what models know, so the complete loop of proposing hypotheses, designing experiments, reading feedback and applying new knowledge can be measured in isolation.
(2) The two worlds cover different cognitive operations. AlienCode tests program semantics and AlienLogic formal reasoning. The rankings of the ten systems in the two worlds have a Spearman correlation of only 0.35: a system that explores well in one world does not necessarily do so in the other, so the benchmark does not measure a single narrow skill.
(3) The framework extends. The procedure for constructing a world is general, and the same method can generate new worlds; the supplementary material already provides two demo worlds and the complete evaluation code.
Appendix D states this boundary: our results concern executable rules and deterministic feedback, not real research with physical experiments and noisy observations. The revision adds there that noisy feedback, experiment costs and open-ended hypothesis spaces are our next step.
Response: You are right that more trajectories estimate the distribution more precisely. We therefore extended all ten systems to ten autonomous trajectories in both sandboxes, all under the paper's protocol.
Agreement with the ranking at ten trajectories (Spearman correlation):
Results with ten trajectories (M4, %):
*DeepSeek-V4.1-Flash has been retired; DeepSeek-Flash 1017 stands in for it. Best@3 uses the first three trajectories, which for the other nine systems are the three in the paper.
We draw the following conclusions:
(1) Rankings are largely stable with more trajectories (first table). In AlienLogic, where scores lie closer together, the correlations are lower at three trajectories but already about 0.9 at five.
(2) Systems with close scores need more trajectories or confidence intervals to separate. In AlienLogic, all ten systems lie between 60.4 and 77.0 by Mean@10. If each system keeps three of its ten trajectories at random, Best@3 orders 84% of system pairs the same way as Best@10 in AlienCode, but only 77% in AlienLogic. The revision accordingly limits our statement about the choice of aggregate to systems with close scores and adds confidence intervals.
(3) The Best@n bias you point out is real, and it grows with n. From three to ten trajectories, Best@n rises by up to 27.1 points in AlienCode and 20.5 in AlienLogic. For example, Seed2.1 Pro's Best@n in AlienCode rises from 40.0 at n = 3 to 67.1 at n = 10, while its Mean@10 is only 25.2. The next comment explains why the main ranking still uses three attempts.