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Withdrawn from ICLR 2027

Towards a Systematic Study of Embodied System 2 over Full Task Execution Cycles

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

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Abstract

An embodied brain, or System 2, must turn an abstract goal into actions while discovering relevant scene conditions and checking whether executed skills achieved their intended effects. Open-loop evaluations cannot test observations shaped by an agent’s decisions, while some closed-loop evaluations provide limited evidence during execution or assume idealized skill outcomes. We introduce SCOPER, a suite for studying observation-grounded planning, execution, and recovery. SCOPER-bench combines high-level goals, ongoing visual observations, a shared rule-based System 1 for low-level actions, and controlled execution failures. Its construction and validation pipeline yields 870 tasks across BEHAVIOR and ProcTHOR, complemented by about 3,500 situated questions tied to the evaluated agent’s execution. Benchmark results reveal difficulties in retaining scene evidence, monitoring progress, and recovering from unexpected outcomes. To address these difficulties, SCOPER-harness combines Evidence Memory and Progress Verification with a dynamic task agenda and bounded exploration, without additional model training. Across two evaluated open-source backbones and two simulators, the harness improves task success by 11.1–28.6%; a harnessed 9B model outperforms a directly executed 27B model on both simulators. In an offline next-action evaluation using observations from 200 real-robot demonstrations, the harness also improves full-call accuracy by 14.7% and 15.3%. SCOPER provides a setting for diagnosing and improving embodied reasoning throughout a complete task execution cycle.

Primary area:
applications to robotics, autonomy, planning
Keywords:
Embodied reasoning, Embodied AI

Reviews

Among:
Shape:
1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_DaJsOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper introduces SCOPER-bench and SCOPER-harness for observation-grounded planning and recovery. The benchmark comprises 870 tasks from 35 base templates and their compositions, combining shared rule-based skills, controlled execution failures and situated QA. The training-free harness integrates evidence memory, progress verification, an adaptive agenda and anti-deadlock control.

Critical strengths

S1. Systematic benchmark construction and validation.

S2. Clear gains with informative component ablations.

Critical weaknesses

W1. Architectural gains are not isolated from extra inference and control. A direct baseline sharing the controller and a comparable inference budget is needed to establish the distinctive benefit of the memory and verification design.

W2. Task-aware binding narrows the grounding challenge. The runtime resolver can select privately designated task instances among same-category objects, so the executor supplies part of target disambiguation. This support is disclosed, but its effect on SR and model rankings is unquantified. The results therefore leave open how well System 2 performs instance grounding without task-aware selection.

W3. Situated QA can affect task-execution outcomes. QA answers during execution consume the same 24/36/48-call budgets as physical actions, while trajectories trigger different numbers of questions. This can leave unequal remaining budgets for execution. A QA-free or separate-budget control is missing. Therefore, the diagnostic protocol's effect on SR remains unclear.

W4. Real-observation repair results mix distinct phenomena. The evaluation pools naturally occurring anomalies with incomplete-action nodes created by truncation, which need not represent actual failures or retries. Table 3 does not report separate node counts or accuracies for these sources. Consequently, it seems that the reported 28.4-point repair gains do not establish the improvement on natural anomalies specifically.

Questions for authors

Q1. Does a direct policy with the same anti-deadlock controller and comparable inference budget retain the performance gap? Please also report token usage and latency.

Q2. How often does task-aware binding disambiguate same-category objects, and how does performance change when resolution uses only observation-derived candidates?

Q3. Are task-success rankings and harness gains stable when QA has a separate budget? Please distinguish answers given during execution from those after stopping.

Q4. What are the episode/node counts and repair-call accuracies for natural anomalies and truncated-action cases separately?

Q5. What decoding settings, random seeds and repeat counts were used, and what are the paired confidence intervals for the memory/recovery ablations?

Reviewer_BSSLOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The work aims to analyze the System 2 (VLM) ability with a mocked System 1 module. SCOPER-bench is proposed with 870 tasks on BEHAVIOR and ProcTHOR. Focusing on evidence memory and progress verification, SCOPER-harness is proposed to achieve improvements on the benchmark.

Critical strengths

1.The benchmark consists of routine execution, observation-dependent, failure recovery, and composite task groups. The failure recovery task is innovative and valuable, as it reflects the ability to handle failures and corrections in real-world scenarios. It covers diverse, well-designed tasks with both closed-loop and open-loop (tool-call QA) evaluations. 2. A comprehensive set of models is included in the comparison, covering embodied models, general models, and the strongest API model. 3. Based on the experimental results, SCOPER-harness emphasizes visual evidence and verification, which achieves consistent improvements.

Critical weaknesses
  1. The action definition is too coarse and loses sufficient visual information for models. In ProcTHOR, actions are coarse and discrete, and object_ref can be ambiguous. It loses the continuous failure progress that would tell the model why it cannot reach the object. Consequently, a number of bug fixes are required, including the anti-deadlock mechanism. Actions are defined in inconsistent ways: both fine-grained pick/place and coarse-grained heat/slice operations appear in the same skill dictionary. This limitation stems from the simulation setting and has not been properly addressed.
  2. The benchmark lacks an important test of 3D recognition. Navigation is too easy, since the agent merely needs to name the destination. Using object_ref as a parameter ignores object recognition ability, which is a substantial capability for VLMs. These are the abilities at which embodied models excel compared with general open-source models.
  3. The analysis could be deeper. For example, it would be interesting to investigate why GPT-6 Astra performs best, delving into the fundamental capabilities of the model; it would also be worthwhile to explore why embodied-finetuned models underperform general-purpose models, a finding that is not consistent with their real closed-loop performance.

In summary, the revealed problems and the harness improvements are influenced by the simulation setting. The benchmark can reveal model shortcomings, but it is not suitable for guiding model improvement.

Questions for authors

In the blind evaluation, would replacing the image with its image caption, rather than a black image, change the reported performance?

Reviewer_v6nPOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper presents SCOPER, a benchmark plus a harness. SCOPER-bench runs on BEHAVIOR and ProcTHOR; navigation, observation, and manipulation are executed by a shared rule-based System 1, and the evaluated model only makes high-level decisions. From 35 base templates the authors build 870 tasks, 420 on BEHAVIOR and 450 on ProcTHOR, 200 of them composite. Tasks come with controlled failure injection, six execution-failure mechanisms plus scene disturbances, and about 3,500 situated multiple-choice questions whose answers are resolved from the evaluated episode's actual state. SCOPER-harness is training-free and consists of Evidence Memory, Progress Verification, a dynamic agenda, and an anti-deadlock controller, all calling the same backbone through role-specific prompts. Eight models are evaluated under direct execution; the harness is applied to Qwen3.5-9B and Qwen3.8-27B and raises overall success rate by 11.1 to 28.6 percentage points, with 9B plus harness beating 27B direct. A three-component ablation and an offline next-tool-call evaluation on 200 AgiBotWorld demonstrations are also reported.

Critical strengths
  1. The evaluation setting fills a real gap. Existing benchmarks either fix the observations, as in video QA, or assume skills always succeed; none evaluates deciding what to do from what you see and noticing that a skill failed and recovering inside one closed loop. SCOPER removes low-level execution variance with a shared rule-based System 1 and manufactures controlled failures through template-level injection. That is a measurement instrument that does not exist elsewhere. The protocol details hold up: success is determined from environment state plus a stop requirement, not from the model's claim; coverage counts only execution-confirmed actions; QA keys are resolved from the evaluated episode rather than copied from reference traces; a black-image blind test is included. This is what keeps me from a clear rejection. Even with the harness removed, the benchmark would be useful to people building embodied agents.

  2. The failure analysis gives concrete, checkable signal. Across 4,813 failed episodes of six open-source models, 47.7% stopped early, 30.7% exhausted the budget, and 40.2% contained at least three identical consecutive tool calls. These numbers tell the reader that open VLMs break in closed loop by stopping too early and by looping, not primarily by misreading images. That diagnosis is worth more than another leaderboard, and it is also what makes the ablation interpretable.

Critical weaknesses
  1. The harness gains are not backed by adequate controls, and the ablation points to a different mechanism than the one the paper credits.

The paper attributes the harness to Evidence Memory and Progress Verification; the abstract, the introduction, and the Section 4 headings all say so. In Table 2 the largest effect belongs to anti-deadlock control: removing it drops overall SR by 11.8 and 17.6 points on ProcTHOR and BEHAVIOR. Removing Evidence Memory drops only 1.3 and 5.5 points and slightly improves the routine group on ProcTHOR; removing recovery drops 1.8 and 13.3, concentrated in the failure-recovery group. Read together with the failure analysis above, the picture is fairly clear: the models' main problem is repetition and premature stopping, and the component doing most of the work is a deterministic controller that forbids repetition and forces the model to act. That does not match the narrative of retaining scene evidence and verifying outcomes.

More importantly, nothing rules out simpler explanations. The only baseline is single-call direct execution, while Appendix L reports the harness uses about 3.7x the model calls. There is no compute-matched simple baseline such as direct execution with a free-text scratchpad or self-reflection step, no one-line baseline that disallows a call after N identical repetitions, and none of the agent frameworks the paper itself cites in Section 2, Cortex, Thea, Mimir, or Reflexion-style methods. GPT-6 Astra plus harness is excluded in Section 5.1 for limited gains and higher cost, and the numbers are not given. If gains on the strongest model really are limited, that supports the reading that the harness mainly compensates for weaker models' degenerate behavior; the number should be in the paper, not left out.

Why this drives my recommendation: contributions 2 and 3 rest on the harness. With the current evidence I cannot tell how much of the 11 to 29 point gain comes from the design the paper claims, how much from 3.7x inference, and how much from a single anti-repetition rule. This is fixable: add a compute-matched baseline and a repetition-rule baseline, report GPT-6 plus harness, and rewrite the attribution to match the ablation.

  1. The benchmark measures observation-grounded decision making and failure recovery more weakly than claimed.

First, instance binding. Appendix H.2 states that when resolving a category-level reference at runtime, a task- or subtask-designated object can take precedence over background objects. The model names a category and the infrastructure uses construction-time private bindings to select the right instance. In scenes with several same-category objects the model never has to visually tell them apart. With black images, GPT-6 Astra still reaches 44.7% coverage on ProcTHOR and 38.5% on BEHAVIOR, so a sizable part of the action structure is derivable from the instruction and category names. This does not mean vision is unnecessary, since blind SR is near zero, but it sits uneasily with the positioning that observations determine the required work, and it should be addressed head-on.

Second, task groups confound complexity with failure presence. GPT-6 Astra scores 76.2% SR on the BEHAVIOR failure-recovery group versus 42.0% on routine execution; direct Qwen3.8-27B shows 20.8 vs. 13.0. Table 12 explains why: the injected-failure templates are almost all single-step placements of a mug on a table, while the routine group includes wash, heat, slice, and distractor-aware sorting. So the per-group comparison in Table 1 cannot show that recovery is hard, and the abstract's claim of difficulty recovering from unexpected outcomes currently has no direct evidence. The failure-recovery group also includes initially present anomalies, for example the Place and handle dirty dish template, which by the paper's own definitions are observation-dependent tasks.

Third, one asymmetry in the information boundary. Appendix A.1 says execution-admission signals are used by the harness's deterministic controller for gating and budget accounting, while the direct baseline only ever sees a call-finished message. The controller's reselection reason is fed back to the policy; whether admission information reaches the harnessed model through that path is not stated.

Why this drives my recommendation: contribution 1 is a validated benchmark that jointly tests observation-grounded task decomposition, execution, and failure recovery. If part of instance-level grounding is done by the infrastructure and recovery difficulty cannot be separated from task complexity, the benchmark's diagnostic value is reduced, and diagnostic value is exactly what distinguishes it from EmbodiedBench and EmbodiedEval. The fixes are clear: a paired injection-on and injection-off experiment on the same template and scene; the fraction of multi-instance tasks and model performance on them; and either giving the direct baseline t

Questions for authors

Clarifications that would affect my score:

  1. Are Tables 1 and 2 single runs? What temperature and decoding settings were used for the Qwen models? If multiple runs exist, please report standard deviations.
  2. What are the actual numbers for GPT-6 Astra plus harness? How many points is the limited gain?
  3. What fraction of tasks contain multiple same-category instances in the scene, and in those tasks how often did the task-designated-instance rule in H.2 actually decide the resolution?
  4. Does the controller's reselection reason contain, or allow inferring, the admission outcome? Would the direct baseline change if given the same information?
  5. How many decision nodes are scored in Section 5.4, and how many in the repair subset? The repair-call gain is exactly +28.4 for both models; coincidence or small n? Who reconstructed the instructions, and was there a second annotator?
  6. How does the 12.8% parsing-failure rate split per model? How much of the embodied models' low score is format failure?

Suggestions, not requirements:

  1. Add one rule to direct execution that disallows a call after N identical consecutive calls, and report how much of the harness gain it recovers. The experiment is cheap and decisive for attribution.
  2. Run a paired injection-on and injection-off experiment on the same template and scene and report the difference; that is the measurement of recovery ability.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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