acceptodds
Under review as a conference paper at ICLR 2027

EmbodiedHarness: Adaptive Harness Optimization for Self-Evolving Embodied Agents

Abstract

Embodied agents operating in partially observable, long-horizon environments depend on a model-external harness that organizes skills, manages context, verifies completion, and handles failures. Improving this harness from sparse feedback requires deciding not only how to revise a component, but which component to revise. We introduce EmbodiedHarness, a non-parametric framework that adapts these four components from environment interactions while keeping planner and executor weights frozen. The same frozen vision-language model acts as both planner and optimizer in a diagnose-revise-validate loop. To guide component selection, we propose anchored counterfactual replay: restoring simulator state and recorded history at an observable deviation anchor, applying a bounded single-component revision, and comparing candidate and parent outcomes through paired suffix rollouts. Selected revisions undergo paired validation and are accepted only when they improve observed success without losing any parent-solved validation episodes, subject to cost and catastrophic-event constraints. Across three simulated embodied benchmarks, harness optimization improves held-out performance. On VLABench, EmbodiedHarness raises average success from 34.8% to 48.9%; in a separate comparison using SHAPER's backbone, it exceeds SHAPER by 10.2 percentage points over the four jointly reported capability categories. On ESI-Bench, micro accuracy increases from 39.8% to 62.8%. On EmbodiedBench, it achieves 62.0% on Habitat and 65.3% on Navigation, exceeding the reported train-free baselines using the same backbone. Ablations support the contributions of component selection, anchored replay, and validation to effective harness adaptation.

Primary area:
applications to robotics, autonomy, planning
Keywords:
Embodied AI, Self-Evolving Agents, Adaptive Harness Optimization, Counterfactual Credit Assignment, Test-time Adaptation

Reviews

Among:
Shape:
1234this paper, Top 30%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_DhNVOpenReview ↗
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2
Confidence
2
Informativeness
2
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2
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2
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Paper summary

This paper studies how to improve the model-external harness of a frozen embodied agent. The harness consists of skills, context selection, verification, and recovery. A frozen vision-language model diagnoses failed trajectories and proposes bounded revisions to individual components. The main mechanism, anchored counterfactual replay, restores simulator state and the recorded history near an observable deviation, compares candidate repairs through paired suffix rollouts, and selects a revision for further validation. A paired acceptance gate requires a positive observed success gain without losing parent-solved validation episodes, together with cost and catastrophic-event constraints. The paper evaluates the framework on VLABench, ESI-Bench, and the Habitat and Navigation subsets of EmbodiedBench. Reported gains over the corresponding frozen agents include 34.8% to 48.9% on VLABench and 39.8% to 62.8% micro accuracy on ESI-Bench. Ablations examine diagnosis, replay, state anchoring, validation, and the editable component families.

Critical strengths
  1. The paper addresses a meaningful component-selection problem with a concrete testing mechanism. Improving a frozen embodied agent requires deciding which part of its harness to revise, in addition to generating the revision itself. Anchored replay compares candidate edits from the same restored state and history, providing empirical evidence for this decision.
  2. The evaluation includes useful evidence beyond aggregate performance gains. Experiments cover manipulation, spatial reasoning, and navigation, while the ablations examine diagnosis, replay, state anchoring, and validation. For example, Table 4 reports 54.5% success for the full method versus 50.6% without repair probes, and a lower test regression rate with validation than without it. Figures 5–6 also show a candidate being rejected despite repairing one episode because it loses a parent success. These analyses provide useful supporting evidence for the proposed design and help explain how the update process behaves.
Critical weaknesses
  1. The advantage under a matched total optimization budget is not yet sufficiently established. Section 3.3 states that replay costs are charged to the method and competing approaches receive the same total budget. However, Table 4 mainly fixes the optimization schedule, while Appendix E describes different cost treatments for some variants. Reporting total simulator steps and model calls/tokens would help establish whether the gains reflect better allocation of the same resources. A sequential-selection control using the same initial harness, revision generator, validation gate, and total budget would also provide a more direct comparison than published baselines with potentially different development settings. Independent-run counts and uncertainty estimates would strengthen the interpretation of the relatively modest gains from replay and anchoring.

  2. The connection between the artifact specification and the implementation examples needs clarification. Appendix A.3 describes skills as structured JSON rules, whereas Figure 6 presents the candidate as natural-language instructions. These may be compatible representations, but the actual serialized artifact and its mapping to planner inputs or executable behavior would make the intervention easier to understand and reproduce. Figures 7–8 explicitly illustrate acceptance of a multi-component bundle; clarifying how this example relates to the single-component procedure used for the aggregate results would further improve the implementation account.

Questions for authors
  1. Could you report the total optimization cost for each Table 4 variant, including model calls/tokens, simulator steps, and the cost of rejected candidates and validation? Under the same total budget, how does the full method compare with diagnosis-only and sequential component selection using the same initial harness, proposal generator, and validation gate? Please also provide independent-run counts and uncertainty estimates.
  2. Could you provide the parent and candidate artifacts corresponding to Figure 6 and explain how they are converted into planner inputs or executable rules? This would help connect the structured JSON interface in Appendix A.3 with the natural-language representation shown in the figure.
  3. Please clarify whether Tables 1–4 use the single-component update procedure in Algorithm 1, and how the multi-component bundle example in Figures 7–8 relates to those experiments. An accepted single-component example with its replay and validation outcomes would help illustrate the complete procedure.
3 comments

Thank you for the careful review. We address all your questions and concerns below.

W1. "The advantage under a matched total optimization budget is not yet sufficiently established. [...] Reporting total simulator steps and model calls/tokens would help [...]. A sequential-selection control [...] would also provide a more direct comparison. Independent-run counts and uncertainty estimates would strengthen the interpretation."

Equal rounds do not imply equal cost. The ablations of Table 4 hold the optimization schedule, not the total cost, fixed; Appendix E no longer calls the no-gate row cost-matched. New App. G.1 (Table 8) reports the acquisition cost per run of every Table 4 variant, covering trajectory collection, diagnosis and proposals, replay, rejected candidates, canary and validation, and retries (sealed-test evaluation and deployment inference excluded).

Table R1 (= revised Table 8). Table 4 outcomes and cost per run (VLABench).

VariantSuccess (%)Regr. (%)CallsTokens (M)Sim. steps (k)Hours
Full54.51.692029.25107.6
− anchoring51.32.4111039.57009.4
− repair probes50.62.169026.23905.5
− diagnosis39.56.288021.44957.3
− validation gate47.39.2104033.24757.6
− skill evolution47.72.980023.94656.7
− context evolution51.42.283524.84857.0
− verifier/recovery evolution49.52.681025.64556.8
Edit-all45.85.1118036.16309.8

What the cost accounting shows.

  • Three controls spend more and still score lower: no anchoring (+20.7% calls, +37.3% simulator steps, −3.2 pp), edit-all (+28.3% calls, −8.7 pp) and no gate (+13.0% calls, −7.2 pp, regression 9.2% vs 1.6%). Their deficit is not explained by fewer resources.
  • Controls that spend less lose more than they save: random targeting saves 4.3% of calls and loses 15.0 pp; freezing one component family saves 9.2–13.0% and loses 3.1–6.8 pp; diagnosis-only saves 25.0% and loses 3.9 pp. Whether that saved budget could close the gap is the matched-budget comparison below.

Matched total budget (App. G.1). All methods share the initial harness, backbone, proposal generator, data, paired seeds, edit limits and gate, under common caps of 29.2M tokens and 510k simulator steps; budget a control saves funds further attempts. Diagnosis-only uses no probes, sequential selection cycles through the four components in a fixed order, and no anchoring replays from reset. Each method is run five times; run i of every method uses the same seeds and evaluation manifest, and CIs are paired t-intervals (df = 4).

Table R2 (= revised Table 10). Matched total-budget comparison on VLABench (five runs per method).

MethodSuccess, mean ± SD (%)Δ (pp)Paired 95% CI (pp)CallsTokens (M)Sim. steps (k)HoursProm./run
Full54.5 ± 0.55——92029.25107.63.5
Diagnosis-only52.1 ± 0.85−2.4[−3.39, −1.41]76029.04856.53.6
Sequential selection50.7 ± 0.95−3.8[−4.50, −3.10]85028.85037.33.1
No anchoring48.8 ± 1.19−5.7[−6.63, −4.77]81529.15057.02.4

What Table R2 shows. All controls use 28.8–29.1M tokens and 485–505k steps, and none of the paired CIs includes zero.

  • Reinvested budget closes only part of the diagnosis-only gap: 50.6% → 52.1%, still 2.4 pp below the full method, despite slightly more promotions (3.6 vs 3.5). Untested promotions do not substitute for tested ones.
  • Per-failure component choice beats a fixed rotation: sequential selection is 3.8 pp lower with the same generator and gate.
  • Anchoring matters more under a matched budget: replay from reset affords fewer probes, so its loss grows from 3.2 to 5.7 pp.

Other run counts. The restoration-noise study averages three runs (App. G.2) and the twelve-round retention study five (App. G.3). There, the full method's VLABench mean is 48.7% at round 4 and 48.9% at round 12, consistent with the 48.9% sealed-test value of Table 1.

W2. "The connection between the artifact specification and the implementation examples needs clarification. Appendix A.3 describes skills as structured JSON rules, whereas Figure 6 presents the candidate as natural-language instructions. [...] Figures 7-8 explicitly illustrate acceptance of a multi-component bundle."

Thank you for pointing out this inconsistency. We had not clearly distinguished the artifact's storage format from its content. Revised Appendix A.3 and the Figure 6 caption now state the following:

  • A skill is stored as a JSON record of named rules, each with a trigger and an optional precondition.
  • Its content is natural-language guidance.
  • At runtime, this guidance is inserted into the frozen planner's prompt, and the planner issues requests through the existing action interface.
  • The text is not parsed into deterministic executable rules.
  • Context, verification and recovery, by contrast, set structured fields that the runtime enforces directly.

The complete serialized parent and candidate artifacts, with their diff, are in the supplementary material.

Figure 6 parent versus candidate.

  • Parent: instructs the agent to identify the requested object from observations, pick and place it, and re-observe uncertain outcomes.
  • Candidate: adds guidance for selecting objects by semantic attributes, recommends placing immediately after picking, and discourages subsequent lifting.

Only the skill changes. This repairs the cola task, but a previously solved playing-card task that requires a lift then fails. Anchored replay gives a net gain of +0.2 over five complete pairs. The canary then records one repair and one regression (W = L = 1), so the gate rejects the update. Replay selects promising repairs; validation checks whether they harm other tasks.

Figures 7–8 are a multi-component case, and the revision now says so explicitly.

  • They change skill, verification and recovery together.
  • On six reachable development episodes, success rises from 2 to 3 with no parent-solved episode lost, so the update passes the gate.
  • App. F (intro, Fig. 7 caption and F.4) now labels this as a multi-component bundle that shows how the gate treats such a candidate, like the edit-all control. It is not an instance of Algorithm 1.

Q1. Could you report the total optimization cost for each Table 4 variant, including model calls/tokens, simulator steps, and the cost of rejected candidates and validation? Under the same total budget, how does the full method compare with diagnosis-only and sequential component selection using the same initial harness, proposal generator, and validation gate? Please also provide independent-run counts and uncertainty estimates.

Cost per variant. Table R1 (revised Table 8) gives calls, tokens, simulator steps and hours for all nine variants. Rejected candidates and validation are included in their stages (Table 9).

Matched total budget. Table R2 (under W1) answers this directly. Under common token and simulator-step caps, with the same initial harness, proposal generator and gate, the full method reaches 54.5 ± 0.55%. Diagnosis-only reaches 52.1 ± 0.85% (−2.4 pp, paired 95% CI [−3.39, −1.41]) and sequential component selection 50.7 ± 0.95% (−3.8 pp, [−4.50, −3.10]).

Run counts and uncertainty. Table R2 uses five independent runs per method and reports the SD across runs and paired 95% CIs. The restoration-noise study averages three runs (App. G.2) and the retention study five (App. G.3).

Q2. Could you provide the parent and candidate artifacts corresponding to Figure 6 and explain how they are converted into planner inputs or executable rules? This would help connect the structured JSON interface in Appendix A.3 with the natural-language representation shown in the figure.

Artifacts. Both artifacts are JSON records whose rule content is natural-language guidance. The guidance is supplied to the planner as prompt text, and the planner acts through the existing execution interface. It is not converted into executable rules.

What the revision provides. Revised App. A.3 and the Fig. 6 caption explain this. The supplementary material contains both complete serialized artifacts and their diff.

Q3. Please clarify whether Tables 1–4 use the single-component update procedure in Algorithm 1, and how the multi-component bundle example in Figures 7–8 relates to those experiments. An accepted single-component example with its replay and validation outcomes would help illustrate the complete procedure.

Tables 1–4. We clarify here that the EmbodiedHarness rows of Tables 1–4 use Algorithm 1, the default single-component procedure. In Table 4, edit-all and no-gate are the explicit multi-component and ungated controls.

Figures 7–8. Figures 7–8 illustrate the gate on a multi-component bundle, labelled as such in App. F.

Accepted single-component example. Revised App. G.5 (Table 13, top) traces a VLABench run whose three accepted revisions are all single-component promotions:

  • skill: 2 → 3 rules;
  • context: 3 → 5 recent views;
  • verifier: disabled → at most one review call.

We hope these additions address your concerns and welcome further discussion.

Reviewer_UB8KOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper builds harness optimization for self-evolving embodied agents. The problem is clearly identified in line 062: how to sustain structural evolution of the harness under sparse feedback.

The proposed method is intuitive given the problem. They first identify what caused the failure, then select which component to blame according to the diagnosis, and finally do the revision (while trying to avoid destructing established ability on other tasks).

Empirical results on several benchmarks demonstrate the effectiveness of their proposed method compared to some selected baselines.

Critical strengths

Clear motivation with careful formulation. The proposed method is intuitive and easy to understand.

Extensive empirical evaluation on widely used and recent benchmarks.

I especially appreciate the case study provided in the appendix, which shows how embodied harness evolves.

Critical weaknesses

W1. The closed-source models (e.g., GPT-4o) seem "old" (in the sense that this model is no longer available now). This could post challenge of reproducing the numbers.

W2. Some of the potential baselines discussed in the related works are neither compared in the experiments nor differentiated conceptually. Including Zetta, Evo-Harness, and SpaceMind.

W3. Some experiment details are missing, such as the machine configuration used for experiments, execution time cost and token cost. This could post issue on reproducibility as well as engineering practicality.

W4. The backbones are mainly Qwen family models. Model generalizability is not studied (or maybe I've missed).

W5. There isn't detailed documentation (again, maybe I've missed) on the harness being used, including how it is initialized, how strong it is, and how the final evolved harness compares to the initial harness. Also, harness ablation is lacking (e.g., does the final performance associate with a strong initial harness?)

Given these weakness I'm giving a rating of weak rejection in the initial review but I'm open to discussion. If the above concerns are well-addressed for future readers, I'm happy to evolve my evaluation.

Questions for authors

Q1. Besides the sparse feedback, are there any other issues associated with self-evolving embodied agents and does your proposed method address (or partially address) them?

Q2. Maybe there should be some new feedback/reward design to avoid the sparse issue? could you ellaborate your opinion on that (and maybe list some related works) in the revision?

5 comments

Thank you for recognizing the motivation, evaluation, and case study, and for your openness to discussion. We address each concern below. All changes are marked in blue in the revised PDF.

W1. "The closed-source models (e.g., GPT-4o) seem 'old' ... This could pose a challenge to reproducing the numbers."

GPT-4o is a published zero-shot reference from Yang et al. (2025), not a component of our method. Reproducing our paired gains does not require it. Reproducing that reference row would require the original evaluation, or the same model version and protocol.

We clarify here that all closed-source rows (GPT-4o, Claude-3.5, GPT-5) are published references, not components of our method. Our paired comparisons fix the planner and executor (Sec. 4.1). Table 6 records the model identifiers, temperature and hardware.

All models used by our method are served locally (Table 6), so no deprecated API is involved:

  • Default planner and optimizer: Qwen3.8-27B Max.
  • Paper's additional planners: Qwen3.6-27B on VLABench/ESI-Bench, and Qwen3-VL-32B on EmbodiedBench.
  • Added in the revision (W4): InternVL3.5-38B and the non-Qwen Gemma 3-27B-IT as frozen planners.

W2. "Some of the potential baselines discussed in the related works are neither compared in the experiments nor differentiated conceptually. Including Zetta, Evo-Harness, and SpaceMind."

We clarify the conceptual difference here and have added an experimental comparison to the paper (new Sec. 4.4, Table 5).

The conceptual difference is in what gets selected for revision.

  • Zetta evolves critics and recovery modules and validates them with post-update rollouts.
  • Evo-Harness evolves execution wrappers.
  • SpaceMind studies modular skill evolution for on-orbit agents.

Each fixes the component type in advance. EmbodiedHarness instead compares candidate edits to different component types from the same failure anchor, using paired suffix replay, and then applies canary and paired validation (Secs. 3.2–3.5).

Table W2 (= revised Table 5). Cross-method comparison with a matched Qwen3.8-27B planner and executor (%).

MethodVLABench C1–C5EB-HabitatEB-NavigationESI MicroESI Macro
Zetta45.563.061.051.548.0
Evo-Harness46.060.365.757.153.5
SpaceMind37.250.751.040.637.0
EmbodiedHarness48.963.366.362.859.4

What Table W2 shows.

  • EmbodiedHarness leads all five columns. Its margin over the best alternative is +2.9 percentage points (pp) on VLABench and +5.7/+5.9 pp on ESI micro/macro.
  • The largest margins are on ESI-Bench. Its categories reward deliberate re-observation, and Sec. 4.2 traces our ESI gains to context and verifier revisions. This is consistent with the benefit of choosing the component type per failure, rather than fixing it in advance.
  • The EmbodiedBench margins are small. They are +0.3 and +0.6 pp, and the paper states that we do not read them as a separation.

Setup notes.

  • All three methods are run by us through the same interface and executor.
  • SpaceMind is adapted from its on-orbit setting, so its row is not its published result.
  • The VLABench and ESI entries for EmbodiedHarness are the paper's Qwen3.8-27B results (Tables 1 and 3).
  • The EmbodiedBench entries use Qwen3.8-27B here, unlike the paper's Qwen3-VL-32B rows (62.0%/65.3%, Table 2).

W3. "Some experiment details are missing, such as the machine configuration used for experiments, execution time cost and token cost."

We thank the reviewer for highlighting the importance of computational reproducibility. We have expanded Table 6 and Appendix G.1 (Tables 8–9) to provide detailed hardware configurations, execution time, token consumption, and optimization costs.

The optimization protocol is specified in Table 6: 4 rounds, 4 optimization episodes per round, 2 probe replicates, and a maximum of 10 model calls/10 interaction turns per episode. All methods use the same computational resources and concurrency settings to ensure a consistent comparison

Hardware configuration (Table 6, App. G.1)
Planner/optimizer serving4 × A100 80GB, local inference
Simulator/executor host1 × A100 80GB; 64 CPU cores; 256 GB RAM
Concurrency4 rollout workers; same for every method
Timing scopeOptimization only; excludes model loading and final sealed-test evaluation

Computational cost per optimization run (revised Table 9):

BenchmarkPlannerCalls/runTokens (M)/runInteraction steps (k)Hours/run
VLABenchQwen3.8-27B Max92029.25107.6
EB-HabitatQwen3-VL-32B76019.21854.9
EB-NavigationQwen3-VL-32B68017.31604.1
ESI-BenchQwen3.8-27B Max54012.9283.3

Cost in practice.

  • One optimization run costs 540–920 calls, 12.4–27.6M tokens and 3.1–7.6 hours on this hardware.
  • This is a one-time cost. The resulting harness is reused at deployment, where the gate bounds inference cost to at most 1.1× that of the initial harness.
  • Rejected candidates and retries are included in the stage in which they occur. Table 9 (bottom) gives the per-stage decomposition: canary and validation dominate, not proposal generation.
  • Tokens are usage, not API charges.

W4. "The backbones are mainly Qwen family models. Model generalizability is not studied."

We added two frozen planners (new Sec. 4.4; App. G.4, Table 12) and compare frozen and evolved harnesses with each. The executor, evaluation protocol and Qwen optimizer are held fixed.

  • InternVL3.5-38B uses a Qwen3 language backbone.
  • Gemma 3-27B-IT tests planner-side transfer to a non-Qwen family.

These results test planner-side transfer, not optimizer-side independence; the paper states this scope.

Table W4 (= revised Table 12). Frozen versus evolved harness with two additional planners. Each cell gives frozen → EmbodiedHarness performance and the gain in percentage points.

PlannerVLABench avg (%)EB-Habitat (%)ESI micro (%)
InternVL3.5-38B36.0 → 46.2 (+10.2)49.0 (147/300) → 61.7 (185/300) (+12.7)41.1 (95/231) → 58.4 (135/231) (+17.3)
Gemma 3-27B-IT33.4 → 42.6 (+9.2)44.0 (132/300) → 56.7 (170/300) (+12.7)36.4 (84/231) → 52.4 (121/231) (+16.0)
  • VLABench is the category average, EB-Habitat is success over 300 tasks, and ESI is micro accuracy over 231 questions.
  • Both planners improve substantially on every measure, by +9.2 to +17.3 pp.
  • The gains are comparable to, though somewhat smaller than, those with the default planners: +14.1 on VLABench, +17.0 on EB-Habitat (Qwen3-VL-32B) and +23.0 pp on ESI micro. The planner-side improvement therefore transfers beyond the Qwen family.

W5. "There isn't detailed documentation on the harness being used, including how it is initialized, how strong it is, and how the final evolved harness compares to the initial harness."

The paper defines H₀ = (S, C, V, R) as skills, context, verification and recovery (Sec. 3.1; App. A.3). We added App. G.5, which documents three things:

  • Initialization. The optional verifier and recovery interventions are disabled. The context retains the current observation and three recent views. Skill rules map public evidence to the fixed controllers. App. A gives the prompts and artifact contracts, and Table 6 the shared settings.
  • Initial → final harness (revised Table 13, top). One illustrative VLABench run, whose three accepted revisions are all single-component promotions:
ComponentH₀ → H*
Skill2 → 3 rules (1 added, 1 modified)
Context3 → 5 recent views
Verifierdisabled → enabled, at most 1 review call
Recoveryunchanged
  • Initialization strength (revised Table 13, bottom). VLABench category average:
InitializationH₀ (%)Final (%)Gain (pp)
Weakened28.643.8+15.2
Standard34.848.7+13.9
Strengthened42.150.6+8.5

Does final performance depend on a strong initial harness? It depends on it, but is not determined by it:

  • The weakened start gains the most (+15.2 pp). Optimization closes about half of the gap: the final gap between weakened and strengthened starts (6.8 pp) is half the initial gap (13.5 pp).
  • The strengthened start still gains +8.5 pp and finishes highest (50.6%).

Like the other supplementary VLABench values, these use the capability-category average and the supplementary runs. They therefore differ slightly from the single sealed-test value of Table 1 (48.9%) and from the task-family average of Table 4 (54.5%); App. G states this protocol.

Q1. "Besides the sparse feedback, are there any other issues associated with self-evolving embodied agents and does your proposed method address (or partially address) them?"

Yes. We clarify here that, beyond sparse feedback, four issues matter:

  1. Credit assignment across components (the core of the sparse-feedback problem). A binary outcome does not indicate which component failed. Anchored counterfactual replay directly tests competing repair targets from the same restored state (Sec. 3.3).
  2. Regression. A canary regression rejects the edit, and paired validation requires W > L with L = 0 (Eqs. 9–10). This protects the sampled tasks, not every unseen task. App. G.3 measures regression empirically over twelve rounds: 2.5–3.4% with the gate versus 11.9–14.2% without it.
  3. Cost growth. Each edit must satisfy C′ ≤ 1.1 C(H₀) and the absolute inference budget, which prevents cost from compounding across promotions (Eq. 10). Over twelve rounds on VLABench, the inference-cost ratio stays at or below 1.09 (App. G.3).
  4. Catastrophic simulator events. The N_cat = 0 gate rejects candidates that introduce such events (Sec. 3.5; Table 6).

Q2. "Maybe there should be some new feedback/reward design to avoid the sparse issue?"

We agree this is a promising direction. We see three forms of intermediate feedback:

  1. Receipts (ours). Per-step controller outcomes and state changes provide evidence without an additional reward model. They locate deviation anchors (Sec. 3.2, Eq. 5).
  2. Learned step feedback. Process verifiers (Lightman et al., 2024), model-written reward functions (Ma et al., 2024) and runtime critics (Zetta) could score intermediate behavior. They require supervision or calibration; we do not evaluate them here.
  3. Sub-task checkpoints. Intermediate success tests offer more granularity than a final binary outcome.

These signals are complementary to our method. A denser signal would sharpen anchor localization, and replay and validation would still decide which edit to keep. Task outcomes remain necessary, however, because operational success can still violate the instruction, as in the paper's wrong-object example.

We hope these additions address your concerns and welcome further discussion.

Reviewer_h8oGOpenReview ↗
Rating
3
Confidence
4
Informativeness
3
Presentation
3
Soundness
3
Read review
Paper summary

This paper proposes EmbodiedHarness, investigating how to improve the task capabilities of embodied agents by optimizing peripheral components, such as skills, context management, task verification, and failure recovery, while keeping the planner and low-level actuator parameters frozen. The proposed method employs an iterative "diagnose-modify-validate" pipeline. Its core is anchored counterfactual replay: restoring the environment state to the point just before a trajectory deviation, and conducting paired execution for single-component modifications. This allows the system to select optimization directions based on actual repair outcomes. Subsequently, updates are filtered through paired validation and cost constraints, requiring them to fix a portion of failed tasks without degrading previously successful tasks in the validation set. The paper demonstrates significant improvements on manipulation, navigation, and active spatial exploration benchmarks. Ablation studies also support the effectiveness of targeted diagnosis, replay, and validation mechanisms. Overall, this is a highly practical system optimization effort for embodied agents, translating model-generated reflections into a testable and traceable update process.

Critical strengths

S1. The idea of this paper is very practical. It focuses on "Repair Direction Selection" After Embodied Agent Failures, it recognizes that task failures can stem from various stages, and relying solely on a final success or failure signal makes it hard to judge which component actually needs fixing. The authors treat it as a "credit assignment problem" during optimization, and use trajectory evidence to guide the repair direction.

S2. The anchored counterfactual replay design is well-reasoned, providing direct experimental evidence for the proposed modifications. The paper restores the simulator's state and history right before an observable deviation occurs. This allows both the original system and the system with a single modified component to continue executing under identical conditions.

S3. The update mechanism strikes a balance between performance gains and capability retention. Rather than adopting a candidate fix just because it resolves a specific failure, the authors filter updates through a rigorous process: static checks, canary tests, and paired validation. The default requirement is that a fix must resolve at least one task without degrading any previously successful tasks in the validation batch, while also limiting newly introduced risks and inference costs.

Critical weaknesses

W1. The current conclusions of the paper primarily apply to recoverable simulation environments, this is the biggest concern. They have not yet been validated through real-world robot experiments or simulations with state recovery errors, which are necessary to demonstrate the mechanism's effectiveness in actual deployment.

W2. The reporting on optimization costs and result stability is insufficient. Beyond merely collecting failure trajectories, the proposed method also requires diagnosis, candidate generation, paired replay, and multi-stage validation. Therefore, having "a small number of optimization rounds" does not equate to low overall interaction costs. To adequately assess whether the benefits are stable and cost-effective, the authors should provide comprehensive metrics. These should include total environment steps, model API calls, token consumption, and runtime, along with the mean and confidence intervals across multiple independent optimization runs.

W3. The "no-degradation" guarantee is limited to a finite set of validation samples, and there is insufficient evidence for long-term capability retention.

Questions for authors

See weaknesses.

4 comments

Thank you for the constructive review and for recognizing the practicality of the approach. We address each concern below.

W1. "The current conclusions of the paper primarily apply to recoverable simulation environments [...] They have not yet been validated through real-world robot experiments or simulations with state recovery errors."

We agree, and we state this limitation explicitly here: real-world validation remains open. To test state-recovery errors in a controlled setting, we perturb restored object positions and joint angles in VLABench with zero-mean Gaussian noise. Parent and candidate share each perturbed state and replay seed. Each cell averages three four-round optimization runs with Qwen3.8-27B Max (App. G.2, Table 10).

Table R1 (= revised Table 10). Restoration-noise sensitivity on VLABench.

Restore noise σ: mm / degFrozen (%)Full (%)No anchoring (%)Full − frozen (percentage points, pp)Promoted rounds / 12
0 / 034.848.745.8+13.910/12
1 / 0.534.848.245.8+13.410/12
5 / 2.034.846.045.8+11.28/12
10 / 5.034.841.745.8+6.96/12

What the noise sweep shows.

  • Small errors are tolerated. At 1 mm/0.5°, the gain is essentially unchanged (+13.4 vs +13.9 pp).
  • Moderate errors erode the advantage of anchoring. At 5 mm/2°, the full method retains 81% of its gain over the frozen agent. However, its advantage over the no-anchoring control shrinks from +2.9 pp to +0.2 pp, which is within run-to-run variation.
  • Large errors expose a limit. At 10 mm/5°, the method still improves on the frozen agent by +6.9 pp, but anchoring falls 4.1 pp below the no-anchoring control. We report this as a sensitivity limit, not as deployment robustness. It also gives a practical rule: when restoration error is large, replay from reset is the safer fallback, which Sec. 3.3 already specifies when restoration is unavailable.

Averaging protocol (stated in App. G). The 0-noise value of 48.7% is a three-run mean of the capability-category average. Table 1's 48.9% is the single sealed-test value. The no-anchoring 45.8% uses this same category average. It is therefore not comparable with the task-family average of Table 4 (51.3%).

W2. "The reporting on optimization costs and result stability is insufficient [...] total environment steps, model API calls, token consumption, and runtime, along with the mean and confidence intervals across multiple independent optimization runs."

We separate optimization acquisition cost from deployment inference cost. The revised paper reports both:

  • Acquisition cost: summarized in Sec. 4.4; per variant, per benchmark and per stage in App. G.1, Tables 8–9.
  • Inference cost: bounded by the gate at C′ ≤ 1.1 C(H₀).

Cost figures are obtained from our per-stage acquisition accounting and are labelled as such. Hardware: 4×A100 80GB for planner/optimizer serving, and 1×A100 80GB with 64 CPU cores and 256 GB RAM for the simulator. This is listed in Table 6.

Table R2a (= revised Table 8). VLABench ablations with cost per run.

VariantFamily avg (%)Regression (%)CallsTokens (M)Sim. steps (k)Time (h)
EmbodiedHarness (full)54.51.692029.25107.6
− state anchoring51.32.4111039.57009.4
− repair probes50.62.169026.23905.5
− diagnosis39.56.288021.44957.3
− validation gate47.39.2104033.24757.6
− skill evolution47.72.980023.94656.7
− context evolution51.42.283524.84857.0
− verifier/recovery evolution49.52.681025.64556.8
Edit-all45.85.1118036.16309.8

What Table R2a shows.

  • Anchoring pays for itself. Removing it lowers success by 3.2 pp, while simulator steps rise by 37.3% and time by 23.7%.
  • Probes trade cost for accuracy. Removing them saves 27.6% of time but loses 3.9 pp.

Table R2b (= revised Table 9, top). Full-method acquisition cost per optimization run.

BenchmarkPlannerCallsTokens (M)Interaction steps (k)Time (h)
VLABenchQwen3.8-27B Max92029.25107.6
EB-HabitatQwen3-VL-32B76019.21854.9
EB-NavigationQwen3-VL-32B68017.31604.1
ESI-BenchQwen3.8-27B Max54012.9283.3

A full optimization run costs 540–920 model calls and 3.3–7.6 hours. For that one-time cost, the matched-backbone gains are:

  • +14.1 pp on VLABench (34.8 → 48.9%);
  • +16.8 pp on EB-Habitat (45.0 → 61.8%);
  • +16.6 pp on EB-Navigation (49.3 → 65.9%);
  • +23.3 pp ESI micro (39.8 → 63.1%).

Table R2c (= revised Table 9, bottom). VLABench cost decomposition (sums to R2a/R2b).

StageCallsTokens (M)Sim. steps (k)Time (h)
Trajectory collection1604.81201.6
Diagnosis and proposals401.800.4
Anchored repair probes2406.11101.8
Canary and paired validation48016.52803.8
Total92029.25107.6

Canary and validation account for 54.9% of simulator steps and 50.0% of time; repair probes add 21.6% and 23.7%. Candidate testing, rather than proposal generation, dominates acquisition cost. Rejected candidates and retries are included in their stages.

Stability across independent runs. The revision reports independent-run means for the new analyses:

  • Restoration noise: three runs (App. G.2).
  • Retention study: five runs on all four tracks (App. G.3, Table 11).

The five-run round-4 means, measured on an independent evaluation manifest, closely match the main-table values:

BenchmarkFive-run meanMain table
VLABench48.748.9
EB-Habitat62.061.8
EB-Navigation65.365.9
ESI micro62.863.1

W3. "The 'no-degradation' guarantee is limited to a finite set of validation samples, and there is insufficient evidence for long-term capability retention."

We agree, and revised Sec. 3.5 now states the scope explicitly. Property 1 guarantees W > L and L = 0 only on the evaluated pairs against the immediate parent (Eq. 10). It is not a population-level or lifelong guarantee. The root-referenced cost cap bounds the evaluated inference cost, not unseen-task regressions.

To measure longer-term retention empirically, we extend optimization from four to twelve rounds. The evaluation manifest is fixed independently before optimization, and its outcomes never enter editing or stopping decisions. Results are five-run means (App. G.3, Table 11).

Table R3 (= revised Table 11, top). VLABench twelve-round trace (five-run means).

RoundSuccess (%)Regression vs H0 (%)Inference cost / C(H0)
034.80.01.00
345.21.81.06
448.71.71.08
849.42.11.09
1248.92.51.09

Table R4 (= revised Table 11, bottom). Cross-benchmark retention (five-run means). Success is shown as round 4 → round 12; regression is measured at round 12.

BenchmarkFull success (%)No-gate success (%)Round-12 regression: full / no-gate (%)
VLABench48.7 → 48.942.0 → 39.82.5 / 12.8
EB-Habitat62.0 → 61.755.3 → 51.73.2 / 13.6
EB-Navigation65.3 → 65.158.7 → 55.32.8 / 11.9
ESI-Bench (micro)62.8 → 62.555.0 → 51.93.4 / 14.2

What the twelve-round study shows.

  • Gains are retained, not eroded. Over eight extra rounds, full-method success changes by only +0.2 to −0.3 pp. The no-gate variant loses 2.2–3.6 pp.
  • The gate keeps regression low over long horizons. Round-12 regression against H₀ is 2.5–3.4% with the gate versus 11.9–14.2% without it, a 4.2–5.1× reduction.
  • Inference cost stays bounded. The cost ratio stays at or below 1.09.

We hope these additions address your concerns and welcome further discussion.

Thanks for the authors' response. I'm glad to see that you have added more comprehensive experimental details and properly addressed my questions. I think most of my concerns have been solved, and I would like to maintain my rating as Weak Acceptance.

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Dear Reviewers,

Please kindly review the authors' rebuttal and engage in discussions if you have further questions.

Thanks, AC

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