acceptodds
Withdrawn from ICLR 2027

AlienBody: Diagnosing How LLM Agents Acquire and Use Action Models

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

Agent benchmarks typically expose meaningful action names, conflating name retrieval with action understanding. We introduce AlienBody, a 900-instance benchmark that randomizes action mappings across six action families to separate exploration, interpretation, and planning. Controlled naming interventions reveal a model-specific prior: misleading labels lower GPT-4o's success below anonymous controls on two families while truthful labels raise it directionally, so named success need not reflect identification from interaction. Even when the mapping reaches the agent as effect names, the tested in-context agents achieve only 0–10% success on Relational environments, while symbolic breadth-first search that computes with the mapping achieves 100%. Direct probes on the two tested models show why: defining the operators behind the names lifts per-step predictions from near-blind-guess accuracy to at most 52.6%, so a description of the actions does not by itself substitute for computing with them. A frozen interface study under one matched protocol isolates how that knowledge is used: on Relational grids, a programmable interface improves success over a conversational transition oracle by 49.75 points for DeepSeek V4 Flash and 35.75 for Qwen3.5-35B-A3B. Boolean workflows reverse that ranking for one model, and inspecting successful programs separates plans computed in code from fixed plans merely submitted through code. When the mapping is unknown, schema induction with verified search and active identification provides a constructive route from observations to control. These interventions make acquisition and use separately measurable, exposing the central shortfall: action information, whether a familiar label, a correct description, or a supplied mapping, can be available without being usable for control.

Primary area:
foundation or frontier models, including LLMs
Keywords:
LLM agents, vision-language models, action understanding, agent evaluation, in-context learning

Reviews

Among:
Shape:
1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 6 reviews, above 10% of the others.
Reviewer_D1KmOpenReview ↗
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Paper summary

AlienBody studies whether LLM agents can learn unfamiliar action effects through interaction and use that knowledge to complete a task. The benchmark contains 900 instances across six action families. The authors vary action names, provide different levels of rule information, and compare conversational and programmable interfaces. They also investigate action-model identification through verification and active exploration. The results show that receiving action information does not ensure that an agent can use it effectively, and that the execution interface can substantially affect task success.

Critical strengths
  1. The paper asks a useful question: how much does successful task completion tell us about an agent's understanding of action effects? The distinction between action names and full operator definitions is particularly helpful. For DeepSeek Flash, providing full definitions raises single-step prediction accuracy from 18.6% to 52.6%, while end-to-end success remains only 12.5% (Appendices L.13 and H.11). These results give a concrete account of the gap between receiving rules and using them to complete a task.

  2. The interface comparison is the strongest part of the paper. Table 3 evaluates 400 paired instances per task, and both models benefit substantially from the programmable interface on F4. The workflow results are also informative: Flash performs worse with this interface, whereas Qwen improves. Inspecting successful programs reveals that many Qwen programs simply submit a fixed plan. This analysis helps establish why successful program execution alone does not show that the program performed planning or search.

Critical weaknesses
  1. The interface experiments change several factors at once, leaving the source of the performance gap only partly explained. Equal oracle caps do not imply equal query use, memory, execution or error recovery. On F4, Flash's average query count increases from 32.20 to 213.27, and Qwen's from 14.99 to 205.68 (Table 18). The authors acknowledge this, and the full-definition and format-retry experiments address some alternative explanations. Still, the contributions of search organization, query throughput and error handling remain unclear. The overall interface effect is supported, but the explanation of the "planning wall" is less conclusive.

  2. Action-knowledge acquisition is not measured directly enough. Table 1's CA is inferred from interaction trajectories, and Appendix H.1 shows that it can substantially exceed the model's stated mapping accuracy. L2 has no valid reported evaluation, leaving the separation of exploration from interpretation incomplete. The search-based identification methods also receive known operator vocabularies and executable simulators (Appendix L.17). These results demonstrate that structured identification can work, but do not establish how the methods compare under the same prior knowledge and access permissions.

Questions for authors
  1. Do any existing experiments compare the programmable interface with a conversational agent that explicitly maintains a search tree or supports batched queries? This would help determine how much of the current gap comes from the particular conversational scaffold.
  2. Can you report the relationship between direct post-interaction knowledge accuracy and task success on the same episodes? This would help distinguish failure to identify the mapping from failure to use it.
  3. Which conclusions about action-knowledge acquisition have independent support when trajectory-proxy CA and comparisons with different simulator access are set aside?
Reviewer_ysE4OpenReview ↗
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Paper summary

This paper introduces AlienBody, a benchmark designed to evaluate the ability of LLM-based agents to acquire action models through interaction and utilize the acquired knowledge for planning, while disentangling this capability from prior knowledge about familiar action names.

The benchmark comprises 900 grid-world instances, six families of action dynamics (F1–F6), ranging from simple directional movements to orientation-dependent, conditional, relational, compositional, and history-dependent effects. Agents must first 1) infer action effects by experimenting with them and observing the resulting state transitions, 2) reach a goal state utilizing the knowledge acquired during exploration and/or information provided by the environment. Additional interventions vary action labels, supplied action information, and the interface available for planning and execution.

The authors argue that LLM-based agents: (i) struggle to reach goal states under anonymized action labels across text-only and image-plus-text inputs, model sizes, and model families; (ii) are sensitive to the labels assigned to controls, particularly misleading labels; (iii) remain below symbolic planners on some task families, especially Relational tasks, even when provided with ground-truth action-effect mappings as names, while programmatic interfaces can improve performance; and (iv) struggle with zero-shot action-model induction, although verification-guided approaches improve results in some settings.

Critical strengths
  • The research question is interesting, and the proposed interventions offer a useful way to distinguish understanding of action dynamics from prior knowledge acquired during pretraining.
  • Separating exploration to learn an environment’s action dynamics (Phase 1) from goal-directed execution (Phase 2) is a promising experimental design.
  • The figures and tables are generally well presented, although several legends would benefit from clearer explanations.
Critical weaknesses

Weaknesses

1. Substantial problems with clarity limit assessment of the contributions

I found the paper exceptionally difficult to follow due to several presentation issues, including but not limited to: convoluted language; dense combinations of undefined terms and jargon; explanations that too often defer details to the appendices; historical experiments and protocol revisions interleaved with the principal results; unclear interpretation of findings; and abrupt introductions of new concepts that are never defined in the main text.

In my assessment, these issues are substantial enough to warrant rejection, as they prevent a reliable evaluation of the methods, results, contributions, and the paper's overall significance.

I provide representative examples at the end. I strongly encourage the authors to revise the manuscript extensively, especially if substantive parts of the text was written with the assistance of AI.

2. Limited realism and unclear relevance of the benchmark

The primary benchmark consists of relatively simple, synthetic grid-world environments. Although such environments can be useful for isolating specific capabilities, the paper does not sufficiently establish how its findings relate to the challenges faced by LLM agents in more realistic settings.

The additional evaluations involving Kirby's Dream Land, Crafter, and Boolean workflows provide some diversity, but their introduction and experimental methodology are insufficiently explained. Furthermore, it is unclear to what extent these experiments establish generality beyond relatively constrained and artificial environments.

This concern is relevant because several LLM agents perform poorly even when provided with truthful action names or additional information about the action effects. It is therefore difficult to determine whether the observed failures reveal limitations in action-model acquisition and planning, or instead arise from the particular environment design, prompting strategies, and agent implementations.

I would encourage the authors to better motivate the relevance of the proposed environments and discuss what conclusions can reasonably be generalized from them.

3. Unclear agent memory and retention of information between phases

An important aspect of the benchmark is that agents are expected to acquire information during calibration and use it during the subsequent execution phase. However, the manuscript does not adequately explain how this information is preserved and made available to the LLM agents.

My understanding is that at least some implementations rely primarily on the conversation history containing previous observations, actions, and feedback. If this is the case, context-window limitations and history truncation could directly affect the agents' ability to use information acquired during exploration (which seems to be acknowledged only in appendix J)

If informative observations are removed from context before or during execution, poor performance may reflect loss of previously acquired evidence, rather than difficulty identifying action dynamics or planning effectively. This is an important potential confound given the paper’s objective of distinguishing action-model acquisition from its subsequent use.

The authors should describe the memory mechanisms more clearly in the main text and explain their implications for interpreting the results. If agents rely solely on a truncated conversation history, evaluating alternatives such as persistent summaries of observed action effects would help determine how much the reported failures reflect loss of exploration evidence rather than difficulties in action-model acquisition or planning.

4. Missing methodological details and unclear status of experimental components

Several experimental components are introduced without sufficient methodological detail, making it difficult to understand their role in the study and assess the corresponding claims. For example:

  1. The paper introduces L2 as part of its diagnostic framework but repeatedly acknowledges that it was not evaluated. Could the authors explain more directly why an unevaluated condition is included in the main diagnostic framework and which parts of the proposed decomposition remain untested without it?

For reference, here are some passages:

Section 3.2:

"L2 is specified but not evaluated here, so no L2 result is claimed: the archived runs cover two models only, and the summary artifact they injected was not preserved"

Section 4 (experimental setup):

"L0 is the main anonymous setting, L1 and L3 are targeted probes, and L2 is specified but not evaluated.

The whole section "H.3 L2 Is specified but not evaluated"

The L2 protocol (systematic action tests in Phase 1, followed by a structured observation summary for execution) is part of the design but is not evaluated in this paper, and no L2 number is claimed anywhere in the main text. Three reasons, none of them a result.

Could the authors clarify the section "H.3 L2 Is specified but not evaluated"? For instance, how should readers interpret this? How important is this to the paper's claims?

First, the protocol as implemented and as specified diverged: the archived runs use a Phase-1 round count that the specification does not license, so what ran is not the treatment L2 names. Second, the summary text actually injected in those runs has no preserved artifact—the code path that builds it changed afterwards, so byte-identity with the current build_phase1_summary cannot be established; the protocol may be described as specified, not as executed.

  1. Insufficient specification of the Kirby’s Dream Land experiment. This environment appear as part of Figure 1 summarizing major results and the results in Section 4.2. However, I could not find a sufficiently detailed specification of the environment, the complete action interface, the exact prompts, or the experimental protocol.

Given its prominence in the presentation and its role in supporting claims about the generality of action-naming effects beyond grid-world environments, these details seem important for interpreting and assessing the results. Could the authors provide a more complete and reproducible description of this experiment?

Examples of clarity issues

Section 3.2

This passage defines the metrics for interpreting the results. Could the authors clarify it and move any necessary details from the appendix to the main text? For instance, what does it mean to "apply fixed rules"? What is an "archived forward model"?

Exploration coverage (EC) measures the fraction of actions tried; P1 is Phase-1 length. We report three diagnostics: calibration-accuracy (CA) proxy (Table 1) applies fixed rules to each action’s first observed transition; stated-effect accuracy scores the model’s answers to effect questions, with prior/post-interaction comparisons; and held-out prediction accuracy tests archived forward models on unseen state–action contexts. Stated-effect and held-out probes cover the subsets in Appendix H. We report success rate (SR); action counts enter the efficiency indices in Appendix N.

Section 4

We use the diagnostic interventions of Section 3 as operational diagnostics for Explore, Interpret, and Plan: L0 is the main anonymous setting, L1 and L3 are targeted probes, and L2 is specified but not evaluated (Appendix H.3). We compare heuristic baselines (Random, Systematic, Bayesian), Qwen3.5 across sizes and modalities, and five further models (Table 1). Oracle+BFS supplies a known-dynamics reference; Forward-Model Babbling (FMB) variants appear in Section 5. We report success rate (SR) together with calibration efficiency (CE/CEcond), the trajectory-only CA proxy, exploration coverage (EC), and Phase 1 length (P1; definitions in Section 3 and Appendix H).

Could the authors clarify:

  • What is "Oracle+BFS"?
  • Why "L2 is specified but not evaluated" and the relevance of this passage?

Section 4.1 (main results)

Interpretation of results in this section are limited because:

  • Lack of clarity of metrics as shown in excerpt from Section 3.2 above
  • The implementation details of baselines (Random, Systematic, and Bayesian) have no substantive explanation in the manuscript
  • Calibration Efficiency (CE), bold-highlighted in Table 1, is not formally defined until Appendix N, which is never directly referenced to explain the metric

Exploration strategy is one contributor: a Bayesian baseline over permutation matrices (SR 22.7%) and a Systematic one-test-per-action heuristic (17.7%) beat every open-weight vision-language model (VLM) under image input (best 15.7%),

What are "permutation matrices"?

"as the model-output-based replacement for the trajectory-only CA proxy, held-out next-state prediction reaches 0.71–0.89 against 0.05–0.08 for controls"

What is "trajectory-only CA proxy"? How does it connect to the (vague) description of CA in section 3.2?

Section 4.2

Several conditions and terms are introduced without adequate explanation. Several passages combine experimental results, statistical details, and interpretation in ways that make their intended conclusions difficult to identify.

We rerun Adapt and Spatial (50 envs each; GPT-4o and Gemini 3.1 Pro, image+text) under three labelings: anonymous (AlienBody default), named-true (labels match effects), and named-misleading (every label wrong). A familiarity-only control helps only modestly (Appendix L)

What is a "A familiarity-only control"? What it means for it to "helps only modestly"? Why is this relevant here?

"The effect is large and model-specific, and it runs in both directions (Figure 2(a); paired bootstrap CIs; environment-level exact two-sided sign tests count each environment once, pooled-counting values in Appendix L.1)."

What what are "pooled-counting values" and why are they relevant here? Could the authors clarify how to interpret the "both directions"?

"On Spatial, true labels raise GPT-4o's SR from 25% to 40% (+15pp, 95% CI [+1, +29]; p=0.071, a direction rather than an established effect)"

What do the authors mean by "a direction rather than an established effect" and why? Is this because of the p-values (also undefined)? What threshold was chosen to determine statistical significance?

Could the authors clarify the conclusion to derive from this?

The design is floor-bound rather than an equivalence test, since at 1–2% SR a drop has little visible room (the floor truncates the downward direction) while the observed upward differences are also small. It does locate where the name prior stops being measurable: for a model with no room to move, label manipulations leave no trace.

The Kirby's Dream Land is first and abruptly introduced here without any context:

The same confound appears outside the grid, but not always in the same direction. On Kirby’s Dream Land (Game Boy via PyBoy; qualitative, three runs per condition, below the preregistered paired target), GPT-4o plays 300 visual steps under the three labelings (Table 2, left): named buttons (whose descriptions are supplied) reach 8.7 checkpoints (scroll 20.7), category hints (scrambled labels) yield partial progress (scroll 8.7) with more damage, and anonymous IDs leave every run at spawn (max scroll 1.0).

Could the authors clarify:

  • What is a preregistered paired target?
  • PyBoy?
  • How are the three labelings determined in this environment?
  • (scroll a.b)?
  • What "leave every run at spawn" means?
  • How these results connect to the previous passages?

On Crafter Hafner (2022), already flagged for leaking action names in Appendix Table 4, we removed the glosses and re-ran the contrast under a fully shared protocol (17 actions, 20 paired seeds, 150-step cap; Table 2, right).

Could the authors clarify:

  • What "already flagged for leaking action names" means? Does this compromise the whole evaluation? Why is it relevant here?
  • What it means to "the glosses and re-ran the contrast" under a "fully shared protocol"?

The v1 ordering inverts: true names yield 0.10 mean achievements against 1.85 (anonymous) and 2.45 (category rank labels); named-anonymous -1.75, bootstrap 95% CI [-2.25, -1.30], exact Wilcoxon p=9.7×10-5; category vs. anonymous is within noise (+0.60, p=0.09). The post-episode probe reads named 0.79 > category 0.36 > anonymous 0.12, and named runs try only 4.3 of the 17 actions against 13.3 for anonymous (Table 2, right; per-action mix in Appendix L). The earlier v1 advantage, from a prompt that supplied effect descriptions and gave no condition history, is not reproduced here (Appendix L). Thus, higher stated effect accuracy coexists with narrower action coverage and lower task progress. This is consistent with label-dependent exploration but not established here.

Could the authors clarify this discussion? Also, could they explain what is "v1" and move it from appendix L.2? What does it mean: "the v1 ordering inverts" and "the earlier v1 advantage"? Why this matters?

Section 4.3

Unclear experimental conditions and terminology. Terms such as "complete prose definitions" are introduced without sufficiently explaining what information is supplied to the agents or how it differs from the preceding conditions.

More fundamentally, the very low performance observed on F4, even when action mappings or operator definitions are supplied, raises questions about what capability the experiments are measuring. Is the difficulty primarily due to the complexity of the relational operators, limitations of the LLM-agent implementations, or planning itself? The authors should more carefully distinguish these possibilities.

Abrupt introduction of additional experiments. For example, the paragraph beginning:

"In the L3 condition of the planning wall (Figure 3) the mapping reaches the agent as effect names inside the state, with no operator definitions, no oracle, and no episode history. Asked to predict a single transition on exactly that information [...]"

introduces a one-step transition prediction experiment immediately after discussing Figure 3, which reports end-to-end success rates.

The relationship between these experiments, their different evaluation settings, and their respective roles in supporting the paper's claims are not sufficiently established. The reference to Figure 3 further complicates the presentation because the subsequent results concern a different measurement.

Similarly:

"In a separate registered end-to-end study, supplying the full operator definitions raises DeepSeek V4 Flash's success from 5.0% to 12.5%, while for Qwen3.5-35B-A3B no significant change is detected [...]"

introduces another experimental comparison without adequately explaining its setup or connection to the preceding results.

The gap accompanies distinct behavioral patterns—high action entropy with 26% oracle-plan agreement for Gemini 3.1 Pro, degenerate repetition for a local Qwen model (Appendix L.11)—yet success collapses in both;

No context about action entropy and again, deferring to appendix.

Section 4.4

The three principal experimental conditions (Draft, Oracle, and Program) are only briefly described in the main text. For example, what exactly constitutes a "persistent draft"? What information does it contain, how is it updated, and how does the agent use it? I could not find a sufficiently concrete explanation of its intended contents. Likewise, the operational differences between conversational oracle access and the programmable interface should be made explicit before presenting their comparative results.

"All arms share the task's real-action limit, and oracle arms share its query cap (1,024 on Relational grids; 4,096 on workflow)."

What is a query-cap?

Table 3:

"BFS (J5): 400/400 per task under the same oracle cap."

BFS (J5) is first introduced in the caption of this table and it seems to be only partially explained in Appendix H.7. Could the authors further explain what it means and why is it relevant here?

"The conversational arms run under linear history scaffolding; tree-search agent architectures Zhou et al. (2024a); Hao et al. (2023) are not among the arms evaluated here."

What exactly is meant by "linear history scaffolding"? Why is the absence of tree-search architectures relevant to interpreting the experiments? The authors should explain these considerations rather than introducing them without context.

Section 5

Several undefined terms, appendix deferrals, and vague definitions, in my perspective, compromises all the interpretation of results in this section, despite its potential relevance to the paper's main contributions.

Here is the first time the authors introduce "FMB", as follows:

"We call this plan-over-model pattern Forward-Model Babbling (FMB): babble to identify action schemas, then plan with BFS over a ForwardModelSimulator that applies typed effects—translate, rotate, relational, composite, temporal—without calling the VLM (Appendix K)."

This description introduces several concepts without sufficiently explaining the actual procedure. What constitutes "babbling" in this implementation? How are action schemas represented and inferred? What does the ForwardModelSimulator do, and which components are learned versus predefined?

Supplying a lookup primitive does not by itself close the gap: across one generation on the same relational split, interface only arms stay at 0–4%, a conversational next_state tool at 10–26%, and a Python read-eval-print loop (REPL) at 90–100% (Appendix H.6; unmatched budgets, rematched in Section 4.4).

Could the authors clarify what exactly these are and how they relate to the section's purpose?

  • the "lookup primitive"?
  • a conversational next_state tool at 10–26%
  • Python read-eval-print loop (REPL) at 90–100%?
  • (Appendix H.6; unmatched budgets, rematched in Section 4.4).

Also, several important concepts are introduced without adequate explanation in the main text, including:

  • "Public operator vocabulary"
  • "Enumerate+Verify"
  • "FMind"
  • "Active FMB"
  • "Exact-assignment search"

The notation (n) and (|H⋆), as well as the meaning of "perfect-score ties," should be clearly defined and explained in the main text.

"At n=8 Relational it reaches 90%: remaining failures are perfect-score ties (|H⋆|>1), not verification misses."

"Active FMB (AFMB) selects disagreement probes that split H⋆, lifting the same split to 100% and Temporal Tier-M from 90% to 100%; ablations without information-gain selection fall back to 90–92%"

At n=8, LLM proposers stay weak even with the same verifier (GPT-4o 2%; DeepSeek V4 Pro 6%/4%): verification helps when a strong search proposes candidates, but does not substitute for one. At n=12, an exact-assignment search still reaches 56% while FMind stays at 0%

Unclear LLM-based model induction procedure. In particular, the paper should clearly explain what information is provided to the LLMs when they infer action models, what output they are expected to produce, how candidate models are verified, and how verification feedback is incorporated.

The final paragraph abruptly introduces training as a "complementary stress test," but does not adequately explain its motivation or how it relates to the preceding methods.

The discussion also introduces terms such as "emission," "ground-truth injection," and "verification-filtered self-training" without sufficient explanation.

"the bottleneck is emission, not planning—the same ground-truth injection yields 100% while a content-permuted schema returns 2%"

"verification-filtered self-training does not internalize the search signal on Relational either"

Section 6 — Conclusion

Overall section could be use much less vague language, and explicitly connect to the results observed (esp. lines 479 to 485).

Introduction

Consider adding more specific language and context about the benchmark before describing results; I was only able to parse the content after line 077 after reading the paper several times.

Questions for authors

See weaknesses.

Reviewer_ZqKQOpenReview ↗
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Paper summary

This paper mainly trying to explore if LLM agents can explore and understand the tools, and complete tasks with these knowledge. Under 6 families, there are 900 synthetic tasks constructed to test the agents capability of using the tools. The results provides more insights on how such tools affect agents under different model families.

Critical strengths

Interesting questions to study.

Critical weaknesses

will to hear more during rebuttal

findings

1.1 Core findings related to action semantics, Search, Verification seems already studied before. How's their relationships or what new failures are reveals are still unclear. What are new mechanisms or generalizable insights? What are the applications of this findings? some experiments changed a lot of factors

1.2 How this findings are helpful for designing agents or tools? How the intervention is designed based on findings?

1.3 The comparison in the empirical study are not fair enough to ensure the robust of the findings.

1.4 [not exactly a weakness]Why different model family have different sensitivity to action names remain unclear?

as a benchmark

2.1 how this benchmark test the ability differences of agents compares with others? Do you have stronger agent to test on this benchmark? How this diagnostic evidence support agents performance on other tasks?

AFMB

3.1 Limited of innovation and generalization of FMB, how is it solve the problem that is not under operation vocab? Not comparing with some other strong baselines. Not running on other tasks

Questions for authors

please see weakness

Reviewer_ngptOpenReview ↗
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Paper summary

This paper investigates whether agents can learn novel actions through interaction and whether the information acquired can be utilized for planning. The authors construct 900 environment instances featuring six categories of action rules, with randomized action mappings. The model first explores the environment, after which the goal is revealed and the model attempts to execute the task. The authors then systematically alter action labels, provide explicit rules, or switch execution interfaces to pinpoint the specific stage at which failure occurs.

Critical strengths
  • By modifying action labels while keeping environmental dynamics constant, the study effectively tests whether performance relies on semantic priors.
  • The evaluation compares different interfaces across 400 instances per category, revealing findings that challenge conventional assumptions—specifically, that a programmatic interface significantly improves success rates in relational grid-world tasks.
Critical weaknesses
  • In the main experimental tables, the CA is derived from interaction trajectories via external heuristic rules; this may not accurately reflect which rules the model has truly mastered. For instance, in Table 9, DeepSeek shows a CA of 0.800, yet its rule-statement accuracy is only 0.470—a discrepancy also observed with GPT-4o.
  • While the current experiments demonstrate that failure can occur even when relevant information is available, they do not consistently distinguish between cases where a model has failed to identify a rule versus cases where it has identified the rule but lacks the planning capability to apply it.
  • As shown in Table 18, the average number of simulated queries for the "relational" task increases significantly—from 32.20 to 213.27 for Flash, and from 14.99 to 205.68 for Qwen. Further analysis of this planning bottleneck may require disentangling the contributions of query throughput from the underlying computational approach.
Questions for authors
  1. Which specific models, environments, and trajectories from the main tables are covered by the direct rule-identification and state-prediction probes?
  2. If direct measurements were used in place of CA, would the conclusions regarding the specific stage of failure change?
  3. Is it possible to report success rates as a function of the actual number of simulated queries, and to compare the interfaces under conditions that more closely reflect real-world query consumption and error-handling scenarios?
Reviewer_S1qWOpenReview ↗
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Paper summary

The authors claim that understanding what an action means for an LLM is distinct from the LLM recognizing the name of the action and working using that. they do experiments where they anonymize action names, or jumble them, and allow the agent to discover their inherent meaning via interacting with the actions (tools) and environment.

Critical strengths

The concept that the paper is studying is interesting. Disentangling name recognition from action understanding seems like a good interpretability study.

Section 3.1, and the variants studied are quite comprehensive.

Critical weaknesses

The paper is extremely poorly written.

In the introduction, tasks, methods and terminology (relational tasks, executable dynamics, persistent draft ) from the author's custom benchmark are referred to without introducing or defining them anywhere, which makes the text hard to follow. One first has to go to section 3 then come back to section 1.

The motivation of the paper is weak. The premise would be better studied from a mechanistic interpretability lens, where model activations are studied when names are changed.

What is not clear to me is, why can't understanding of the name and task be the same thing? The authors are need to show that, under the anonymized or jumbled setting, the learning from the exploration phase are not just name learning. In case it is name learning, then the whole premise is wrong. The authors just show the change in performance under these settings, and a drop was expected anyway.

In section 3.1, the authors study the following controls among others:

  1. actions without revealing names + exploration phase
  2. actions with names, without exploration phase

This is a flawed experiment, as the true control for 1. would have been actions with names + exploration phase. By not giving it, the confidence in the main premise is low.

Questions for authors

Why not include an action name + exploration ablation?

Why not study how the model processes action names internally, using token level, activation state studies and mechanistic interpretability?

Reviewer_obMsOpenReview ↗
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Paper summary

This paper a benchmark called AlienBody for studying LLM based agents learn what unfamiliar actions do and use that knowledge to complete tasks. The paper has experiements to vary action names, info given to the agent and the interface used for planning. The main finding of the paper is that knowing the action mapping does not necessarily lead to successful control. Also, access to a programmable interface can make a substantial difference.

Critical strengths
  1. Good experimental framing. Every alternative explanation gets its own control: knowledge access, name informativeness, interface, and trainability are each isolated in a separate intervention.
  2. The transition probes and program audit help explain the results in a better way. The observation that many successful programs simply submit fixed plans is particularly interesting finding.
Critical weaknesses
  1. The programmable interface changes several factors together at once like query organization and error handling. A stronger conversational search baseline will help explain what drives the gains.
  2. Sample sizes are small at places in the parts of the paper. Two models for the naming study and three runs for the game experiment. Also there is almost no coverage of reasoning models on the hardest family. More models and seeds would be better for strong claims in the paper.
  3. The planning wall is difficult to interpret and is never actually a planning measurement. With names only, model cannot predict even one step. With full definitions given it is right less than half of the time. So, the failed episodes point to the transition errors rather than plan construction. The programmable arm mostly removes the wall at places where transitions are reliable.
Questions for authors
  1. Will the interface gap reduce by using batched oracle queries or the explicit search scaffold?
  2. Is it possible to run and test one current reasoning model through the full anonymous suite and mapping supplied condition at the same scale as the other agents?. Now the paper has only single probes mentioned.
  3. When transitions are made reliable, will plan plan construction still fail? For ex: For ex: with cheap exact transition function the agent can call

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