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Robotics · arXiv:2609.39507 v1 · submitted 30 Sep 2026 · 37 references

LIBERO-Agent: Evaluating General-Purpose Agents for Direct Embodied Manipulation

Zijie Diao, Yitong Chen, Sicheng Xie, Tianyi Lu, Wujian Peng, Guojin Zhong, Houze Xu, Ziyi Ye

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Zuxuan Wu, Yu-Gang Jiang

The paper says

“General-purpose agents can plan, use tools, and revise their behavior from feedback, but it remains unclear whether these capabilities transfer from digital environments to embodied manipulation.”

more of the abstract

To investigate this question, we introduce LIBERO-Agent, an agent-native benchmark for evaluating these agents in robot manipulation tasks. Rather than asking agents to submit task-level Python control programs or operate through high-level robot skills, LIBERO-Agent provides an interactive robotic environment where agents can select which observations to inspect, process them with their own tools, and issue native action commands. LIBERO-Agent integrates 200 tasks into a common interaction framework and provides a 30-task primary suite that separates perception, short-horizon execution, and long-horizon composition. Results reveal a pronounced reliability gap: while agents perform well on perception and easy short-horizon tasks, their performance degrades substantially on hard short-horizon and long-horizon tasks. Richer observations improve short-horizon manipulation, while demonstration benefits depend on the agent and format. Among these agents, GPT-6 Astra achieves the strongest overall performance. Further analysis shows its major advantage lies in mechanism interaction, especially when sustained physical contact is needed, while its remaining failures stem from cross-stage interference and geometric errors.

from the abstract

Pith says

Machine review · deepseek-v4-flash · 1 Oct 2026 · 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. Solid benchmark paper whose central directional claim — correct target identification does not reliably become a physical state change — survives scrutiny, but three rollouts per task under one seed leave every magnitude and the fine agent ordering statistically unquantified. This line is wrong

4 major objections · 4 minor

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Not checked: figures, code, what the 37 references say.

The paper says, at §4.1, Eq. (1)-(2)

The review did not quote this passage.

Pith says: Objection 1 of 4 · major

The statistical foundation for the headline numbers is too thin. With the stable criterion requiring success in all three rollouts, per-rollout success p enters as p^3, so each task contributes a binary 0/10 (or 0/20 for hard short-horizon under Eq.

more of objection 1

(2)) to the aggregated Performance Score. Consequently Astra's 40% hard short-horizon rate is exactly two tasks passing 3/3 (Table 12: T12 and T16), and the headline ordering Sol 10.8 vs Qwen 10.5 sits within the flip of a single rollout on a single task. No confidence intervals or significance tests appear anywhere in Section 4.2, and the single fixed simulator seed (100) means the three rollouts sample only run-to-run agent stochasticity, not scene or seed robustness. The authors do disclose this scope honestly in B.3 (the repetitions 'measure variation in agent execution under the same scene conditions'), but the aggregated scores in Table 1 are treated as point estimates supporting fine-grained comparisons. I request per-rollout success estimates with binomial/Clopper-Pearson intervals, additional rollouts or seeds for the claims that separate agents (Sol vs Qwen) and that quantify gap magnitudes (e.g., the 40% hard short-horizon rate), or at minimum an explicit statement that ordering claims within ~10 score points are not supported.

The paper says, at §5.2, Eq. (3)

The review did not quote this passage.

Pith says: Objection 2 of 4 · major

The claim that sustained contact 'is strongly associated with success' (contribution 3, b38) rests on a Pearson correlation of r=0.711 computed over 64 opening operations pooled across the four agents. Since the agent with the highest mean SCR (Astra, 20.63%) is also the agent with the highest opening success, the pooled correlation may be partly an agent-identity artifact rather than evidence that contact causes success within an agent's behavior.

more of objection 2

The authors should report the within-agent correlation (or a per-agent breakdown of the SCR-vs-success relationship); if within-agent r is near zero, the claim should be weakened to an association driven by between-agent differences. In addition, the threshold l_t >= 5 control steps in Eq. (3) is a free parameter and its sensitivity is not reported.

The paper says, at §4.3, Table 2

The review did not quote this passage.

Pith says: Objection 3 of 4 · major

The conclusion that richer observations improve manipulation, and specifically that calibrated depth helps on hard tasks, is carried by very small effective samples in the ablation. In Table 14, Astra's hard-task gain from L2 to L3 (20% to 40% in Table 2) corresponds to a single task flip (T12 moving from 2/3 to 3/3), and most per-cell differences across agents are within one-rollout noise.

more of objection 3

The qualitative direction of the ablation claim is plausible and consistent across agents, but the per-cell magnitudes, and in particular the hard-subset gains attributed to depth, should be reported with per-task detail and uncertainty rather than as clean percentage-point statements.

The paper says, at §5.1, Table 4

The review did not quote this passage.

Pith says: Objection 4 of 4 · major

The stage-level diagnosis, while a good practice, rests on very few stage events per agent (20 stages across five hard long-horizon tasks, with reached counts from 26.7% to 65.0%). The 'Execution SR' for mechanism interaction is computed after excluding cross-stage-interference failures, and the failure-mode percentages may overlap (as the caption notes); it is not stated whether a single failed stage …

more of objection 4

… can contribute to both Local Execution and Cross-stage Interference, which affects how the 66.7% vs 94.1% execution-rate comparison should be read. Clarify the exclusion rule for the denominator and, if feasible, report the stage-level annotation per task so the reader can see how many events each execution-rate figure rests on.

4 minor objections

The paper says, at Figure 3

Pith says: minor objection 1 of 4

Panel (a) shows mean SCR per agent without any measure of spread, while panel (b) reports 95% Wilson intervals; adding per-agent error bars or per-observation scatter to (a) would make the between-agent difference (20.63% vs 4-7%) more interpretable given the small n per agent (9-24).

The paper says, at §5.2, Figure 3(b)

Pith says: minor objection 2 of 4

The binned opening-success rates (0/19, 7/19, 10/15, 11/11) are presented with Wilson intervals but the bin boundaries are chosen post hoc; the authors state that intervals are for visualization only, which is appropriate, but a sentence noting that the binned monotonicity is descriptive while the continuous r=0.711 is the tested quantity would remove ambiguity.

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The paper says, at §B.2, T18

Pith says: minor objection 3 of 4

The tube-insertion checker has several tolerances (lateral error at most 0.018 m, height window, axis alignment at least 0.97, speed caps). These are presented as fixed criteria; a brief note on whether any of them were tuned to observed distribution of agent behavior, or set a priori, would help the reader interpret T18 as the single task where all agents score 0/3 at the primary observation level.

The paper says, at General

Pith says: minor objection 4 of 4

The abstract and Section 4.2 state that the seven agents are 'evaluated under a common protocol,' but the harness versions in Table 5 differ across vendors (Codex 0.154.0 vs Claude Code 2.1.139 vs DeepSeek Harness 0.1.5-rc.2 etc.); a sentence acknowledging that harness differences are part of the measured 'agent' performance would preempt over-reading of cross-vendor comparisons.

What would settle it

Recompute the primary results with more rollouts and an independent seed for at least the four top agents: run the 30-task primary suite under seed 100 with 10 rollouts per task and again under a second seed (e.g., 200), then report binomial or Bayesian 95% confidence intervals on each stable rate and on the Eq. (2) scores. Check three quantities: (1) Does Astra's hard short-horizon stable success stay above 0% and above every other agent once intervals are attached? (2) Do the confidence intervals separate the Sol (10.8) and Qwen (10.5) overall scores, i.e., is the ordering stable to seed and to single-rollout flips? (3) In Table 2, do Astra's Level 1-to-Level 3 gains (30% to 70% overall) survive with intervals, or do they fall within noise given each level is 10 tasks times 3 rollouts?

from the skeptic's reading

How the review went

4 readings by deepseek-v4-flash · 1 Oct 2026

  1. Reader holds up, with conditions confidence moderate
  2. Skeptic agrees 54 s · 23,260 tokens read, 7,543 written
  3. Editor wrote the verdict above 24 s · 24,359 tokens read, 3,069 written
  4. Referee major revision: 4 major objections, 4 minor 36 s · 23,705 tokens read, 5,577 written

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

The genuinely new thing here is the agent-native protocol: agents pick which observations to inspect, process them with their own tools, and emit native OSC_POSE action sequences. That is a real departure from EmbodiedBench's discretized actions and CaP-X's program synthesis over primitives. The 30-task factorization into perception, short-horizon, and long-horizon competence is a good design for localizing where failures arise, and the reporting is unusually transparent for this area: per-task rollout tables in Appendix E, detailed success semantics in B.2 (T08's weigh-by-probing, T18's insertion tolerances, T29's contact threshold), and concrete program traces in Appendix D that ground the "execution is the binding constraint" claim in observable behavior rather than assertion. The sustained-contact analysis is an honest diagnostic — Pearson r = 0.711 over 64 opening operations, computed on the continuous ratio, with the lt >= 5 threshold only shaping the visualization bins. That is not circular.

The soft spot is statistical, not conceptual, and it is exactly where the headline numbers live. Section 4.1 uses three rollouts per task under a single fixed seed and initial state, and Eq. (1)'s stable criterion requires success in all three, so per-rollout success p enters as p3 and each task contributes a binary 0 or 10 points. A single flipped rollout moves an entire task from 0% to 10%. Astra's "40% on hard short-horizon" is two tasks at 3/3, the Sol-versus-Qwen ordering (10.8 vs 10.5) sits inside the noise of one or two flips, and no confidence intervals or significance tests appear anywhere. The authors state in B.3 that the repetitions measure variation under the same scene conditions — transparent scope, not a hidden assumption — but the quantification gap remains where the agent ranking and magnitudes are claimed. The Score weights are free parameters, though the weighting rationale is stated, so that is minor. I cannot verify the closed-model API runs, which is inherent to this kind of evaluation.

The directional claims hold up against the raw per-rollout tables: Sol reaches only 14/30 per-rollout successes on perception tasks while sustaining ~90% target identification, and every non-Astra agent scores zero on hard short-horizon tasks. The magnitudes and finer ordering do not. This deserves a serious referee; the right request is more rollouts or confidence intervals, plus disclosure of the stage-annotation protocol behind Table 4. I would take it, conditional on exactly that.

The strongest objection

The central claim is that correct target identification does not reliably translate into a physical state change, so execution rather than planning is the binding constraint. In direction this claim is robust: the raw per-rollout data in Appendix E corroborate it (e.g., Sol reaches only 14/30 per-rollout successes on the ten perception tasks while sustaining ~90% stable target identification), and Table 12 shows Astra's 40% hard short-horizon rate is exactly 2/5 tasks each passing 3/3. The load-bearing weakness is the statistical foundation of Section 4.1 and Eq. (1): three rollouts per task under a single simulator seed (100) and a fixed task-specific initial state, with the stable criterion requiring success in all three rollouts, so per-rollout success p enters as p^3 and each task contributes a binary 0/10 (or 0/20 for hard short-horizon under Eq. (2)) to the aggregated score. A single flipped rollout moves an entire task from 0% to 10%, so Astra's '40%' rests on two tasks, the Sol-versus-Qwen ordering (10.8 vs 10.5) sits inside the noise of one or two rollout flips, and the credited hard long-horizon SC values likewise come from very few stage events. No confidence intervals or significance tests are reported anywhere, and the single fixed scene and seed mean the three rollouts sample only run-to-run agent stochasticity, not scene or seed robustness. The authors state this scope transparently in B.3 (repetitions 'measure variation in agent execution under the same scene conditions'), so this is an acknowledged limitation rather than a hidden assumption, but the quantification gap it leaves is precisely where the headline comparisons live. The observation and demonstration ablations (Tables 2-3, e.g., Astra Level 1 to Level 3 overall 30 to 70) carry the same small-sample structure.

The reader's weakest_assumption identifies the same load-bearing concern I reach: the three-rollout, single-seed protocol with the all-or-nothing stable criterion in Eq. (1) and no confidence intervals. I agree with that identification because the central claim, that execution rather than planning is the binding constraint, rests on comparisons (perception judgment vs task success, easy vs hard short-horizon, short vs long horizon) whose magnitudes and fine agent ordering are computed from at most three rollouts per task. The direction of the central claim is nevertheless well supported: the per-task raw data in Appendix E (Tables 11-15) show the same pattern that the aggregated stable rates show, so the qualitative finding survives even under a skeptical reading of the statistics. I also considered two alternative candidates and judged them less load-bearing. First, the closed-model API runs (GPT-6 Astra, Claude Opus 5, and others) are cited to published model documentation, so under the review rules they are sourced rather than unverifiable-in-principle claims, and I cannot raise them as a technical defect. Second, the sustained-contact analysis (Section 5.2, r=0.711 over 64 opening operations) is presented appropriately as an association, it is partly definitional for opening operations (a door cannot be opened without retained grip), and it diagnoses the strongest agent rather than supporting the central reliability-gap claim, so it is not the most load-bearing element. The paper deserves credit for transparency: it releases code, reports per-rollout results in the appendix, and explicitly states in B.3 that the repetitions measure execution variation under the same scene conditions, and it acknowledges the cross-stage interference and geometric failure modes it observes rather than hiding them (sentences b189-b193). Those acknowledgements are real evidence of good faith but do not resolve the unquantified sampling noise on the headline numbers. The conditional verdict is therefore the right one: accept with the request that the authors report confidence intervals or additional rollouts and a second seed, and disclose the annotation protocol for the stage-level failure taxonomy. My read does not change the reader's verdict, so verdict_should_be is UNCHANGED.

The referee's report

If the claims hold, this is a useful and well-scoped contribution: it provides an agent-native manipulation evaluation protocol, a capability-factorized task suite, and evidence that for current general-purpose agents the binding constraint in embodied manipulation is physical execution rather than target identification or planning. The design discipline is a genuine strength: the paper ships per-task per-rollout tables (Appendix E), a fixed seeded protocol, private evaluators with stated success semantics (Tables 6-8), and code. The sustained-contact analysis is a diagnostic re-description of measured behavior, not a circular derivation, and the directional core of the central claim is corroborated by the raw rollout data even after discounting the stable-criterion compression (e.g., Sol reaches only 14/30 per-rollout successes on the perception tasks while achieving ~90% stable judgment). The weaknesses are statistical rather than structural: the three-rollout single-seed protocol leaves magnitude claims and the fine agent ordering unquantified, and the pooled SCR correlation is potentially confounded by agent identity.

Pith's reading of the paper (a machine's summary, not the authors')

The paper introduces LIBERO-Agent, a benchmark that evaluates general-purpose agents through direct embodied control: agents must choose which observations to inspect, process them with their own tools, and issue native robot actions, with no task-level primitives supplied. Testing seven agents on 30 tasks split into perception, short-horizon, and long-horizon groups, it finds a pronounced reliability gap: most agents identify targets correctly (90-100% judgment accuracy) yet fail to translate that identification into stable physical execution, especially on hard short-horizon and long-horizon tasks. The strongest agent, GPT-6 Astra, reaches 45.0/100, succeeding on all perception and easy short-horizon tasks but dropping to 40% on hard short-horizon and 22% stable stage completion on hard long-horizon tasks. The paper localizes Astra's advantage to mechanism interaction, where sustained physical contact strongly predicts success, and finds its remaining failures stem from cross-stage interference and geometric errors.

What carries the argument. The paper's central instrument is an agent-native interaction protocol: agents receive the task instruction plus raw published observations (head and wrist RGB, metric depth, camera calibration, robot joint and end-effector states, velocities, torques, and force/torque measurements), and act through a minimal interface exposing three tools - start_episode, osc_sequence, and finish_episode - where each osc_sequence call submits 1-50 native OSC_POSE actions [dx,dy,dz,Rx,Ry,Rz,g] in [-1,1]^7 against a 7-DoF Franka Emika Panda in MuJoCo. Scoring uses stable metrics in which success in all three rollouts is required, and a 100-point Performance Score weights harder and longer-horizon tasks more heavily. The diagnostic load is carried by the sustained-contact ratio SCR, the fraction of control steps in which the gripper maintains a contact run of length at least five with a handle during mechanism interaction, which the paper shows tracks local opening success, and by a manual stage taxonomy separating object manipulation from mechanism interaction and local execution from cross-stage interference.

Core claim. The paper claims that for current general-purpose agents, correct target identification does not consistently translate into reliable physical state change: the binding constraint in embodied manipulation is execution, not planning. Across seven agents, stable perception judgment accuracy is high (90-100% for most), yet perception-focused task success drops to 10-30% for the weaker agents and even the best agent falls from 100% success on easy short-horizon tasks to 40% on the hard subset, while every other agent scores 0% there. GPT-6 Astra achieves the highest Performance Score of 45.0/100, and the paper attributes its lead primarily to stronger mechanism-level execution: Astra reaches a 94.1% execution success rate on mechanism interaction stages and a sustained-contact ratio of 20.63% versus 4.23-7.17% for the others, with sustained-contact ratio correlating at r=0.711 with local opening success. Its remaining failures shift toward cross-stage interference and invalid geometry, indicating that strong local manipulation alone does not yield reliable long-horizon control.

The premise it rests on. Every task is scored on only three rollouts under a single fixed simulator seed and a fixed task initial state, with the stable criterion requiring success in all three rollouts, so the reported agent ordering and the size of the reliability gap rest on very small effective samples with no confidence intervals or significance tests.

If the paper is right (Pith's inferences, not the authors')

Correct target identification does not reliably produce a physical state change for current agents, so evaluation protocols that abstract away observation selection and native control will overstate embodied competence.

Hard short-horizon tasks isolate execution as a distinct bottleneck: precise alignment, direction-sensitive motion, sustained contact, and mechanism interaction drop the strongest agent from 100% to 40% and zero out all other tested agents.

Richer observations - especially calibrated depth and dynamic proprioception - improve short-horizon manipulation across multiple agents, with most gains on easier tasks.

Demonstration value depends on the agent and the format: video improves long-horizon stage completion for some agents but not others, and adding action trajectories does not reliably add further gains.

As local execution improves, the residual failure modes shift to cross-stage interference and invalid geometry, implicating state preservation and downstream anticipation as the next binding constraints.

If the perception-to-execution gap is general, then agent competence measured in digital or tool-use environments may systematically overstate readiness for embodied deployment, where the physical layer, not the reasoning layer, dominates failure.

The finding that calibrated depth and dynamic proprioception outperform demonstration context on short-horizon tasks suggests that for embodied agents, sensor design and low-level feedback may matter more for reliability than scaling demonstration data - a testable hardware implication.

The cross-stage interference failures point toward an explicit preserve-prior-state or avoid-disturbance objective as a design target for future embodied agents, a constraint the paper motivates but does not itself implement.

A natural extension beyond the seven models tested is to use the same 30-task suite to check whether these gaps are stable across seeds and initial states before generalizing the agent ordering.

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The paper

Abstract

General-purpose agents can plan, use tools, and revise their behavior from feedback, but it remains unclear whether these capabilities transfer from digital environments to embodied manipulation. To investigate this question, we introduce LIBERO-Agent, an agent-native benchmark for evaluating these agents in robot manipulation tasks. Rather than asking agents to submit task-level Python control programs or operate through high-level robot skills, LIBERO-Agent provides an interactive robotic environment where agents can select which observations to inspect, process them with their own tools, and issue native action commands. LIBERO-Agent integrates 200 tasks into a common interaction framework and provides a 30-task primary suite that separates perception, short-horizon execution, and long-horizon composition. Results reveal a pronounced reliability gap: while agents perform well on perception and easy short-horizon tasks, their performance degrades substantially on hard short-horizon and long-horizon tasks. Richer observations improve short-horizon manipulation, while demonstration benefits depend on the agent and format. Among these agents, GPT-6 Astra achieves the strongest overall performance. Further analysis shows its major advantage lies in mechanism interaction, especially when sustained physical contact is needed, while its remaining failures stem from cross-stage interference and geometric errors.

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 · 2026-10-01

The authors' main claim, as the classifier picked it out 1.00

“Results reveal a pronounced reliability gap: while agents perform well on perception and easy short-horizon tasks, their performance degrades substantially on hard short-horizon and long-horizon tasks.”

How the main claim is stated: asserted 1.00

What the abstract itself states, as probabilities: claims first 0.08 · states limitation 0.41 · human participants 0.04 · controlled comparison 0.15 · randomized assignment 0.02 · states quantitative result 0.60 · compares with prior results 0.60 · mentions code or data availability 0.05

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.

SentenceRoleThe authors' own workStates the main conclusionStrength
General-purpose agents can plan, use tools, and revise their behavior from feedback, but it remains unclear whether these capabilities transfer from digital environments to embodied manipulation. gap 0.85 0.05 0.03 asserted 0.78
To investigate this question, we introduce LIBERO-Agent, an agent-native benchmark for evaluating these agents in robot manipulation tasks. contribution 0.99 0.89 0.03 asserted 0.90
Rather than asking agents to submit task-level Python control programs or operate through high-level robot skills, LIBERO-Agent provides an interactive robotic environment where agents can select which observations to inspect, process them with their own tools, and issue native action commands. method 0.93 0.75 0.03 asserted 1.00
LIBERO-Agent integrates 200 tasks into a common interaction framework and provides a 30-task primary suite that separates perception, short-horizon execution, and long-horizon composition. method 0.79 0.89 0.04 asserted 1.00
Results reveal a pronounced reliability gap: while agents perform well on perception and easy short-horizon tasks, their performance degrades substantially on hard short-horizon and long-horizon tasks. result 1.00 0.95 0.63 asserted 1.00
Richer observations improve short-horizon manipulation, while demonstration benefits depend on the agent and format. result 0.98 0.88 0.07 asserted 0.98
Among these agents, GPT-6 Astra achieves the strongest overall performance. result 1.00 0.91 0.19 asserted 1.00
Further analysis shows its major advantage lies in mechanism interaction, especially when sustained physical contact is needed, while its remaining failures stem from cross-stage interference and geometric errors. interpretation 0.83 0.92 0.16 asserted 1.00

What kind of paper the classifier reports this is: dataset or benchmark 1.00 · evidence from observation or experiment 0.94

What was examined, and what was not

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Compiled by classifier-1.13.0 via TypeSafe API, question bank abstract-p1-20260923, 2026-10-01: 1 request, 6,275 input tokens.

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Figures (8)
Figure 1 of the paper
Figure 1. Overview of LIBERO-Agent: agent-native interaction, benchmark task suite, and key findings. execution may be abstracted behind benchmark-defined task-level action commands. When adapted to general-purpose agents, such scaffolding can decide what information the agent receives or how actions are composed, making it difficult to determine which embodied capabilities come from the agent itself rather than from the benchmark interface. Moreover, existing benchmarks are rarely structured to diagnose agent capabilities across perception, short-horizon execution, and long-horizon…
Figure 5 of the paper
Figure 5. Shared episode instructions, shown with the T23 task text. The prompt describes the interaction contract and points to the current observation. It supplies no drawer-opening or object-transfer program. For demonstration-conditioned episodes, the following notice is inserted after the task instruction: A demonstration from a separate episode of the same task is available at benchmark_inputs/expert_de mo/. The current scene configuration and object or goal poses may differ. Both demonstration conditions use this notice. The available files determine whether the reference contains…
Figure 6 of the paper
Figure 6. Numerical geometry constructed from public observations in a successful drawer-search episode. The excerpt and output come from the recorded tool call. Coordinates are expressed in the robot-base frame and measured in metres. The agent selects the pixels and subsequent approach targets. D.2 Constructing and reusing a pose-feedback helper In the same T23 episode, Astra creates a local Python helper, robot_pose.py. Each invocation reads the current end-effector pose, computes position and rotation errors relative to command-line targets, clips the resulting normalized control values,…
Figure 7 of the paper
Figure 7. Astra constructs a pose-feedback helper and passes its numerical output to native OSC control. The helper is generated in the session. Its action-generation branch is shown with whitespace expanded; the read-only diagnostic branch is omitted. The shell-command string is split for layout. A receipt establishes execution of the sequence; task completion is checked separately. D.3 Acquiring physical evidence through active probing T08 provides a complementary example in which the necessary evidence is obtained through interaction. Astra successively grasps and lifts the three visually…
Figure 8 of the paper
Figure 8. Active sensing in a successful weighing episode. The same lift-and-hold command pattern is issued for each mug, followed by a state and proprioception read. Values are rounded from the returned observations. Mug locations refer to the initial head-camera view; height is in the robot-base frame and force is in the sensor frame. 22

Showing 5 of the paper's 8 figures. Figures are the authors', reproduced from the paper.

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