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Under review as a conference paper at ICLR 2027

Closed-Loop Adaptation of Frozen Vision–Language–Action Models

Abstract

Execution errors can prevent vision-language-action (VLA) policies from completing tasks they solve under nominal robot dynamics. Correcting these errors changes both motion and the observations driving subsequent policy commands. We present an execution interface, calibrated from fault-free motion, that estimates one additive offset per modeled command coordinate and applies bounded correction with frozen policy weights. To analyze the resulting closed-loop system, we introduce crossed command-stream replay, which separates direct correction from changed-command effects while retaining observer feedback. Geometric and finite-horizon analyses relate physical repair to response direction, correction authority, motion-error persistence, and information delay. Our simulation study spans , , OpenVLA-OFT, and GR00T N1.5/N1.7 in four robot interfaces. Across four LIBERO benchmark suites, success under additive command faults rises from 58/220 to 121/220 over two sampler seeds on the same 110 task/state cases held out from calibration and method selection; healthy success changes from 209/220 to 213/220. With four previously untested rotation-offset vectors in forty new task/state cases, adaptation increases success from 48/160 to 125/160; healthy success is 37/40 with and without adaptation. The averaging gain selected for development is 0.16 versus 0.08 in the initial-state holdout. Panda-arm calibration transfers to OpenVLA-OFT and GR00T N1.7. With commands fixed, correction reduces median endpoint deviation from 13.7 to 7.8 mm. Replay shows that changed commands can reduce or increase reference-relative translation path-deviation cost. Separate predictor interventions distinguish identification accuracy from task recovery.

Primary area:
applications to robotics, autonomy, planning
Keywords:
vision-language-action models, test-time adaptation, robot learning, adaptive control, fault recovery, closed-loop control

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
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Paper summary

The paper proposes an execution-level adapter for frozen vision-language-action (VLA) policies. A predictor calibrated on healthy motion estimates expected robot responses; an observer uses prediction residuals to estimate additive command offsets and applies bounded corrections. The paper also introduces crossed command-stream replay to distinguish correction effects from effects associated with changed policy commands.

On Panda/LIBERO, adaptation raises faulted success from 58/220 to 121/220 on held-out initial states evaluated under two sampler seeds. A separate unseen-offset evaluation improves success from 48/160 to 125/160. Additional simulations examine other policies, robot interfaces, and limits imposed by correction authority, delay, and predictor mismatch.

Critical strengths
  1. Substantial recovery with credible held-out evidence - Faulted success improves by 28.6 percentage points [16.2, 41.5] in the main holdout, with similar gains under both sampler seeds. The separate unseen-vector evaluation further supports generalization beyond one offset. Healthy controls are included, and historical evaluations with selection overlap are clearly distinguished from holdout evidence.

  2. A useful diagnostic protocol with appropriately cautious interpretation - Crossed replay imposes recorded command streams while allowing the observer to update from its own measurements. The reference-sensitivity analyses and task-level counterexamples strengthen the study by showing what the trajectory contrasts can and cannot establish.

Critical weaknesses
  1. The advantage of the specific NT observer is unclear - Under equal candidate budgets, the nominal-error integral controller achieves 138/160 unseen-fault successes versus NT’s 125/160, with a paired advantage of 8.1 points [1.9, 14.4]. Healthy-performance differences remain unresolved. The APEX-style comparison does not establish superiority over published APEX because it is explicitly an approximate reconstruction. The results support calibrated execution feedback more strongly than the particular NT design.

  2. Replay conclusions depend on the reference and retained population - All five tested π₀.₅ NT stream-effect intervals include zero under alternative healthy references. Moreover, matched faulted π₀.₅ replay retains 27/40 cases, while GR00T NT retains 30/40 and omits two entire tasks. These checks are transparently reported, but leave uncertain whether the physical effects characterize the full task-evaluation population.

  3. Cross-robot coverage does not establish a common online recovery method - Panda adapts within the evaluated episode; ALOHA, GR1, and WidowX estimate corrections in preceding faulted episodes and then hold them fixed. GR1 and WidowX also use different healthy-control schedules. Broader physical-fault evidence is weaker: the combined friction-shift gain is unresolved, and locking remains unsuccessful.

  4. The theory remains primarily explanatory - Response geometry characterizes realized trajectories, while the memory–authority–delay result assumes idealized scalar dynamics and exact fault-sign information after a specified delay. The prospective study produces no decisive benefit bounds, and its sign accuracy matches an always-benefit baseline. The analysis therefore does not yet offer a demonstrated rule for anticipating when adaptation will help or harm.

The technical contribution is primarily in execution-level adaptive control. While the interaction between correction and frozen VLA behavior is relevant to ICLR, the control analysis is more developed than the new insights into learned-policy behavior, which limits the paper’s contribution to the machine learning venue.

Questions for authors
  1. What demonstrated advantage motivates choosing NT over the nominal-error integral controller?

  2. How do retained and excluded replay cases differ in task outcomes and available trajectory characteristics?

  3. Can the non-Panda results be evaluated under matched online and healthy-control protocols?

  4. Can the analysis predict beneficial or harmful adaptation on new executions beyond a simple baseline?

2 comments

Thank you for the careful review. We agree that the results support calibrated execution feedback more than the normalized-target (NT) update rule, so the revision makes the feedback interface, with interchangeable update rules, its first contribution. New experiments test how frozen policies respond to offsets and correction, and evaluate adaptation within the episode on ALOHA with matched fault-free controls. "Item N" refers to row N of the results table in our general response.

Insight into learned-policy behavior

The revision reports five findings about VLA policies, all in simulation. Findings 1, 2, and 5 are new, and the revised introduction states the first four.

  1. A frozen policy can complete tasks with part of an offset left uncorrected. Under a +0.05 offset on all six arm coordinates, π0.5 succeeds in 166 of 220 held-out evaluations when we subtract only the rotation part of the true offset, against 60 with nothing subtracted and 212 with all of it (item 5).
  2. Fine-tuning SmolVLA specialized it to one known offset, and random offsets in the training data did not teach it to compensate. Fine-tuned on fault-free demonstrations with actions shifted to cancel a +0.05 offset, it succeeds in 371 of 430 episodes under that offset but in only 8 on the fault-free robot. Fine-tuned instead with a random offset per demonstration, it succeeds in 13 and 7 of 430 under two test offsets, against 6 and 2 for the base policy, and its fault-free success falls from 363 to 212 (item 13).
  3. Under offsets, the policy's reaction to corrected motion does not undo the correction. Crossed replay re-executes the commands recorded with and without correction from a shared simulator state, with correction on and off. Under a +0.10 offset on all six arm coordinates and with the commands held fixed, NT's correction lowers rotation error in all 30 replays per policy that pass our checks (for π0.5, from an earlier replay collection than the one in Q2). With the policy's reaction included, NT and the disturbance-observer rule (DOB), which is NT without its gate and attenuation, still lower rotation error in all 113 faulted replays of Q2. Proposition 1 shows that the changed commands help only if they point back toward the fault-free path, and the larger their effect relative to the remaining deviation, the more directly they must point back. In translation, which neither rule corrects, they point back in 83 of the 113 (Appendices C.4 and C.9).
  4. A better offset estimate need not raise success. On LIBERO-Spatial, constraining the motion predictor's rotation-y gain to its probed value cut the bias of the rotation-y offset implied by each step's prediction residual by about a third, without raising task success (Section 5.3). The same is true of path deviation: in one π0.5 episode correction lowered the deviation but lost the task, and in another it raised the deviation but saved the task (Section 5.2).
  5. π0.5 tolerated a longer uncorrected start than SmolVLA. On LIBERO-Spatial, canceling the known +0.05 offset from step 20 instead of the first step lowers SmolVLA's success from 363 to 212 of 430 (item 2). Over the four suites, the same change takes π0.5 from 212 to 206 of 220, and starting at step 40 gives 180 (item 5). The evaluation loops also differ: SmolVLA executes ten actions per policy call and π0.5 five.

Q1. Advantage of NT over the nominal-error integral

We found none, so the revision treats the update rule as a replaceable part of the interface, which carries the contribution. We ran all update rules together on the 220 held-out Panda evaluations. The nominal-error integral, which integrates the deviation of measured motion from the motion predicted for the policy's own commands, succeeds in 145, NT in 119, and no correction in 60 (integral minus NT +11.8 percentage points, 95% CI [4.7, 19.3]), in line with the result you cite on unseen offsets. Without the offset, every rule succeeds in 211 to 215 of 220, against 211 without correction (Appendix F.2, item 4).

After the runs, we found that the rules' settled rotation estimates follow the order of their stationary values from Section 4. NT attenuates the offset implied by each step's residual before averaging it, so its estimate settles furthest below the true offset, while the integral's settles near it.

The APEX-style comparison

We agree with you; it compares NT with our own reconstruction and cannot show superiority over published APEX. We could not reproduce APEX's discrete coefficient updates from the published description, so the revision reports the reconstruction only in Appendix C.7. We also ran A2C2, a delay-correction head learned from demonstrations, with its authors' code (item 9, Appendix F.7).

Q2. Retained and excluded replay cases

Excluded cases are shorter and more often solved without correction, so the retained cases over-represent the policy's failures, and the physical effects describe only the retained cases. Cases drop out when a run is shorter than the 80 steps replay needs, when runs diverge before correction starts, or when replay fails to reproduce the recorded motion; Appendix F.9 gives the counts. Table entries are task successes without and with correction, and each row's retained and excluded cases add up to the 40 assigned to replay.

Policy and ruleRetained casesExcluded cases
π0.5, NT2/27 → 9/274/13 → 5/13
π0.5, DOB2/27 → 8/274/13 → 6/13
GR00T, NT0/30 → 8/304/10 → 3/10
GR00T, DOB0/29 → 6/294/11 → 4/11

The median fault-free episode lasts 81 steps in excluded GR00T cases, and 106.5 in retained ones (92 and 107 for π0.5), and GR00T loses two whole tasks to the checks. The only two episodes that correction turned from success into failure, one per policy under NT, are both excluded, so the physical effects of all four replay sets come from cases that correction saved or left unchanged. Task success still counts all 40 cases, and the π0.5 episode in Section 5.2 that fails only with correction comes from an earlier replay collection.

Q3. Matched online and fault-free protocols beyond Panda

For ALOHA, yes. GR-1 and WidowX keep their original evaluations, which estimate the offset in preceding faulted episodes and hold it, without matched fault-free controls, and Section 6 now lists this as a limitation.

On 40 new ALOHA seeds, with fault-free controls on the same seeds, we ran adaptation from a zero estimate within each episode under a +0.02 rad offset on the six left-arm joint targets. We first ran NT with its submitted settings, then ran all conditions below together in a second run, which the table reports (successes out of 40).

CorrectionFault-freeUnder the offset
None140
NT, submitted (gain 0.08)130
NT, faster (gain 0.5)1310
DOB, faster (gain 0.5)1518
Estimated on one preceding episode, then held1110
True offset subtractedn/a13

With the submitted settings, NT repairs none of the faulted episodes. An earlier observer study (Appendix B.4) had selected the faster settings on other seeds. For NT, they also changed the cap and normalizer. With them, NT raises faulted success from 0 to 10 of 40 (+25.0 percentage points, 95% CI [12.5, 40.0]) and DOB to 18 of 40, while fault-free success is 13 and 15 of 40, against 14 without correction. DOB exceeds NT on this one task and fault, but we cannot distinguish either rule from the held estimate or from subtracting the true offset (Appendix F.11, item 12).

Physical faults beyond command offsets

We agree that this evidence is weaker. Friction and locking depend on the motion and need not be equivalent to any command offset. Correction partly repairs a joint-3 friction increase present from the first step (from 0 to 13 of 40 episodes), and joint locking scores 0 of 20 with and without correction. The new time-varying offsets (item 3) are still command offsets. In a new test (item 10), we applied the weight of a 1.0 or 1.5 kg payload to the hand. Uncorrected success falls from 73 to 65 and 51 of 80 episodes. Early identification, which estimates an offset from the first 20 control steps and holds it, restores success to 76 and 74, against its 75 without the weight, because in early motion the weight acts like a command offset. Section 6 states these limits.

Q4. Predicting benefit or harm on new executions

Our prospective forecasts of physical benefit always predicted that adaptation would help, so their sign accuracy equaled that of always predicting benefit. Section 4 now states that its results inform the choice of mask and cap but do not forecast task outcomes. Lower path deviation also need not mean higher task success (finding 4). The analysis did predict some physical effects before the runs. We expected constraining the predictor to raise the median rotation-y estimate late in the episode to at least 70% of the offset, and it reached 81.5% on LIBERO-Spatial and 70.5% on LIBERO-10; a ten-step delay and a halved cap raised the physical cost in 18 and 14 of 19 test episodes.

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Paper summary

This paper proposes a closed-loop execution adaptation framework for frozen Vision-Language-Action (VLA) models to correct robot execution errors without updating policy parameters. The approach calibrates a motion predictor using fault-free trajectories, estimates additive command offsets from the residuals between predicted and observed motion, and applies bounded corrections to subsequent commands. To analyze the resulting closed-loop behavior, the authors introduce Crossed Command-Stream Replay, which distinguishes direct physical correction from the effects of changes in subsequent VLA commands. The paper also provides control-theoretic analyses of correction authority, information delay, and motion-error persistence. Experiments across multiple VLA backbones and four simulated robot interfaces demonstrate substantial improvements in task success under additive command faults, along with some transferability across models and robot platforms.

Critical strengths
  1. Meaningful research problem and practical method design. The paper addresses execution errors and physical faults in VLA deployment, which are important challenges in real-world robotic manipulation. Adapting the execution interface rather than fine-tuning the VLA is a reasonable and computationally efficient approach. The proposed method is lightweight and modular, requiring neither policy-weight updates nor access to internal VLA representations, and allows calibration to be reused across different VLA backbones sharing the same physical interface.

  2. Relatively comprehensive experimental evaluation. The authors evaluate the approach across multiple VLA backbones, robot interfaces, and LIBERO tasks. The experiments include disjoint calibration, held-out initial states, multiple random seeds, and previously unseen fault vectors. The results demonstrate substantial improvements in task success rates under additive command faults.

  3. Transparent reporting of experimental limitations. The paper explicitly reports healthy-performance regressions, cases where competing baselines outperform the proposed method, replay reproducibility issues, and limitations of the theoretical predictions. Such analyses help provide a more balanced understanding of the method's effectiveness and applicability.

Critical weaknesses
  1. Limited methodological novelty and unclear advantages over classical control methods. The proposed execution adapter primarily combines established components, including motion prediction, residual estimation, disturbance observation, and bounded command compensation. The Normalized-Target (NT) update mainly introduces gating and attenuation, making its technical distinction from existing adaptive control methods relatively modest. Moreover, in the unseen-fault evaluation, the nominal-error integral baseline achieves 138/160 successes, outperforming NT's 125/160, which further raises questions about the necessity and advantages of the proposed update rule.

  2. Reference dependence and limited task-level relevance of Crossed Replay. The conclusions drawn from Crossed Command-Stream Replay depend heavily on the choice of reference trajectory. When the healthy, unadapted trajectory is used as the reference, its deviation is zero by construction, while Appendix C.11 shows that some significant stream effects disappear under alternative healthy references. Furthermore, the paper observes that reduced trajectory deviation does not necessarily translate into improved task success, leaving the practical significance of these replay-based analyses unclear.

  3. Limited generalization beyond idealized command faults. The strongest experimental results are obtained under artificially injected additive command offsets, which represent only a restricted class of execution errors. Evidence for more realistic physical dynamics changes is considerably weaker: the improvement under friction shifts is inconclusive, and joint-locking faults remain unrecovered. This limits the generality of the claimed execution adaptation capability.

  4. Limited evidence for online adaptation and real-world deployment. The main faulted evaluations on ALOHA, GR-1, and WidowX follow an identify-then-hold protocol, where offsets are estimated in preceding episodes and the corrections are then fixed during evaluation. This differs substantially from online fault recovery within a single task execution. Moreover, all experiments are conducted in simulation, leaving the effectiveness of the method under real-world sensor noise, contact dynamics, and model mismatch unverified.

  5. Incomplete physical and task recovery. In the main Panda experiments, adaptation improves faulted task success to only 55%, still substantially below the approximately 95% success rate under healthy conditions. The paper does not sufficiently disentangle whether the remaining failures primarily result from inaccurate fault estimation, insufficient correction authority, accumulated trajectory errors, or the VLA policy's inability to recover from deviated states.

Questions for authors
  1. Methodological novelty. What is the key technical novelty of the NT update compared with standard disturbance observers or model-based residual compensation? Are there specific conditions under which NT provides advantages that cannot be achieved by simpler classical controllers, especially given the stronger performance of the nominal-error integral baseline in the unseen-fault experiments?

  2. Comparison with APEX. The authors acknowledge that the APEX-style reconstruction is not a faithful reproduction of the original method. How representative is this comparison of the published APEX approach? Could the authors provide a more faithful implementation or further clarify the limitations of the comparison?

  3. Practical implications of the theoretical analysis. Can the theoretical results be translated into actionable control strategies, such as adaptive selection of correction bounds, observer gains, or adapter activation? Otherwise, what additional insights do these results provide beyond established control-theoretic analyses?

  4. Calibration requirements and robustness. How much fault-free data and additional probing are required to calibrate a new robot or control interface? Would recalibration be necessary when the payload, controller parameters, or other physical conditions change during deployment?

  5. Real-world deployment. Have the authors attempted to evaluate the method on physical robots? If not, what are the main technical challenges preventing real-world deployment, particularly regarding motion measurement latency, sensor noise, and control frequency?

  6. Analysis of incomplete recovery. Given the substantial gap between adapted faulted performance and healthy performance, could the authors provide a more detailed breakdown of the remaining failures? In particular, how much can be attributed to estimation errors, insufficient correction authority, accumulated trajectory deviations, and limitations of the underlying VLA policy?

3 comments

Thank you for the careful review. The revision restricts our claims to additive command offsets, treats our normalized-target (NT) update rule as one of several interchangeable rules, replaces the APEX-style comparison with learned baselines, and adds experiments on the remaining failures, recalibration, and online adaptation on ALOHA. "Item N" refers to row N of the results table in our general response.

Q1. Novelty of the NT update

The revised paper's first contribution is the calibrated execution interface around a frozen VLA, and NT is one replaceable rule inside it. NT is a calibrated disturbance observer with a dead-zone gate for small residuals and attenuation for large ones. The interface's gains do not depend on NT, and the AgiBot X2 Ultra experiment uses a different rule, the innovation rule of Appendix B.1. The nominal-error integral, which integrates the deviation from the motion predicted for the policy's commands, does better than NT on the rotation offsets we withheld during development, as you note, and on our main held-out cases (item 4). Under a +0.05 offset on all six arm coordinates, it succeeds there in 145 of 220 episodes and NT in 119 (+11.8 percentage points, 95% CI [4.7, 19.3]), against 60 without correction.

For a learning audience, what is new is that we adapt the execution interface while leaving the policy frozen, with no gradient steps, fault-labeled training data, or access to the policy's internals. To our knowledge, no prior VLA study combines such an interface with crossed replay, which separates direct correction from the effect of changed commands. We test the interface on six VLA variants, four simulated robots, and the left arm of an AgiBot X2 Ultra humanoid, and we run crossed replay with π0.5 and GR00T N1.7 on LIBERO. Unlike APEX, the interface uses a calibrated model of fault-free motion, and unlike J-PARC, A2C2, and TAM, it trains no network. We added early identification (EI), which estimates the offset during the first 20 control steps of an episode and holds the estimate if it exceeds a threshold set on fault-free runs. We compared EI with a residual policy trained on rollouts with known offsets (item 8). When both correct all six coordinates, EI cannot be distinguished from the residual trained on 800 rollouts and outperforms the one trained on 200.

Q2. Comparison with APEX

It does not represent published APEX, and we could not build a more faithful version. The published description does not determine APEX's discrete update or its mapping to our pose interface, and no implementation was available to us. Our reconstruction also lacks NT's fault-free calibration, so the comparison does not isolate the update rule, and the reconstruction's best rate may lie beyond the largest we tried. We moved it to Appendix C.7. Section 5.1 now compares the interface with three learned corrections instead, including the A2C2 correction head, which we ran with its authors' code (items 8, 9, and 13).

Q3. Practical use of the theory

In part. Section 4 helps choose the mask, which selects the corrected coordinates, and the cap on correction size. Before deployment, we can compute the command error that a given mask and cap leave uncorrected for a hypothesized offset, such as the translation our rotation-only mask does not correct (Q6). The delay result ties the cap to when correction starts. On Panda, whose fitted response integrates command error, a correction that learns the sign of an offset of size F only at step τ can bring the worst-case displacement at step N to zero exactly when its cap is at least F·N/(N−τ). Our cap, three times the held-out offset, meets this for N ≥ 1.5τ. Exact cancellation from step τ still leaves the displacement accumulated before τ, which costs success when τ is two seconds (Q6).

For choosing a rule (i.e., interface method), Section 4 predicts where each rule's estimate settles under model mismatch: with our held-out calibration, lowest for NT, at the true offset for the integral, and at one value in between for an L1-style adaptive rule and for the disturbance-observer rule (DOB), which is NT without its gate and attenuation. The settled rotation estimates, examined after the runs, follow this order.

Standard disturbance-observer analysis assumes a known controller, but a frozen VLA reacts to corrected motion in ways we cannot model. Proposition 1 needs no such model and shows that the policy's changed commands help only if they point back toward the fault-free path, and the larger their effect relative to the remaining deviation, the more directly they must point back. In 113 crossed replays under offsets, correction lowers rotation error in every one, with the reactions of π0.5 and GR00T included. In translation, which it does not correct, their changed commands point back in 83 (Appendices C.4 and C.9).

Q4. Calibration and recalibration

A new interface needs a few fault-free trajectories and a short probe. On Panda, ten fault-free episodes fit the motion predictor, and twelve open-loop replays of one 70-command episode, each offsetting one coordinate, show the motion's sensitivity to command offsets. EI adds four fault-free executions per task as references, and the other robots used six to ten trajectories (Appendix F.10).

Whether to recalibrate depends on the change (Appendix F.8). We applied a constant downward force equal to the weight of a 1.0 or 1.5 kg payload. With no recalibration and no command offset, EI succeeds in 76 and 74 of 80 episodes, compared with 75 without the added weight. Changes in controller stiffness or measurement latency do require recalibration, because EI then holds a wrong correction. Re-recording these references under the new condition left no measurable loss without an offset and recovered most, though not all, of the loss under it. The always-on integral was never measurably worse than no correction under these changes.

Q5. Real-world deployment

Yes, in a hardware experiment that the revision adds (Section 5.1 and our comment to all reviewers). On the left arm of an AgiBot X2 Ultra humanoid, gravity sag creates a sim-to-real execution gap for a π0.5 policy fine-tuned only in simulation. Online correction cut the joint tracking error from 0.23 to 0.055 rad without retraining the policy, and 3 of 5 runs succeeded with correction versus 1 of 5 without correction. All other results are in simulation. We expect the main challenges to be measuring motion at the control rate and keeping the predictor valid in contact. In simulation, white noise of up to 5 mm and 5 mrad on pose readings caused no statistically clear change in success, although at that level EI applied a correction in 70 of 80 fault-free episodes. Latency mattered more. Even with references re-recorded at the deployed latency, EI's success under the offset falls from 76 of 80 episodes to 72 at 100 ms and 58 at 250 ms. The interface takes 0.174 ms per control step and a π0.5 call takes 895 ms in our setup, so a 20 Hz loop needs the policy to run asynchronously with action chunks.

Q6. The remaining failures

Most remaining failures disappear when we cancel the known offset exactly. Of NT's 101 failures on the 220 held-out evaluations of items 4 and 5, 95 succeed when we cancel all six coordinates and one more only when we cancel rotation alone. The other five also fail on the fault-free robot without correction (Appendix F.2).

  • Estimation error accounts for part of the gap. Canceling the rotation part exactly, which is all that NT corrects, turns 61 of NT's failures into successes.
  • The rotation-only mask limits correction authority. Compared with rotation alone, canceling translation as well turns 49 failures into successes, and 3 successes into failures.
  • When correction starts late, the policy does not always recover from the deviation accumulated before it. Starting exact cancellation one second late makes no statistically clear difference, but starting it two seconds late costs 14.5 percentage points (95% CI [6.0, 24.6]).

Replay and its reference

Fault-free replay results do depend on the reference. Under a fault, correction with the commands held fixed lowers rotation error in all 30 valid replays of each backbone, as the introduction now reports. A separate test uses a reference that involves no choice, where the same commands are executed without the fault. In that case, correction lowers the median endpoint deviation from 13.74 to 7.80 mm. We agree that lower deviation need not mean task success. Replay separates the correction's effect from that of the policy's changed commands, and our task success counts include cases that replay excludes.

Faults beyond command offsets

The integral rule raises success under rotation offsets that drift, oscillate, or switch on and off (item 3), but these are still command offsets. EI raises success under constant forces by treating them as an offset (item 10). For friction and locking, which depend on the motion, we have only the original results. The correction partly repairs a joint-3 friction increase present from the first step and does not repair locking, which removes a degree of freedom and has no command-offset equivalent (Section 6 and Appendix D).

Online adaptation beyond Panda

On ALOHA, a new study on one task adapts within the episode, with matched fault-free controls (item 12). None of the 40 faulted episodes succeed without our correction interface. With faster settings chosen earlier on other seeds, NT succeeds in 10 and DOB in 18, with fault-free success of 13 and 15, compared with 14 without correction.

I appreciate the authors' detailed response and additional experiments. However, my main concern remains. The framework largely relies on established control techniques, while Crossed Command-Stream Replay provides limited actionable insights beyond retrospective analysis. I therefore maintain my original assessment.

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Paper summary

The paper places a disturbance observer between a frozen VLA and the robot controller: a FIR model of healthy motion is calibrated from fault-free runs, the residual between predicted and measured motion is mapped through a probed sensitivity matrix to a constant command-offset estimate, and a capped, gated correction is subtracted from the policy’s output. It then introduces a 2×2 replay protocol to separate direct correction from the policy’s visual reaction to corrected motion, and gives scalar control bounds on recovery under cap and delay. All results are in simulation.

Critical strengths

The experimental discipline is good: pre-registered protocols with dated amendments, pinned sampler seeds, a 110-case holdout excluded from both calibration and method selection, 880 episodes with no exclusions, and consistent reporting of null and unresolved results rather than only favorable ones. The crossed command-stream replay is a clean and reusable protocol for separating direct physical correction from a visually closed-loop policy’s reaction to it.

Critical weaknesses

Clarity: The paper never states its thesis, and its framing consistently claims more than the evidence supports. The abstract is a list of raw counts with protocol caveats and a hyperparameter inlined, from which a reader cannot recover what is primary, what is registered, and what is null. The title and abstract speak of “execution errors” and “adaptation of VLA models,” but the fault class is a constant additive command offset (lines 134–140) and nothing about the VLA is adapted; the physical faults that would justify the broader term appear in two sentences of Limitations, where the method fails. “Four robot interfaces” conceals that online adaptation is evaluated only on Panda and the other three hold a fixed estimate (1066). “Previously untested” fault vectors are new combinations within the same family, inside the correction mask (1337). Section 5.1 reports beating an “APEX-style” comparator that the appendix admits is neither faithful nor an ablation (1399–1403). The “control-theoretic limits” are scalar-integrator identities with a known fault that the authors themselves say do not bound the deployed system (267–268). Key terms are undefined at first use and the sensitivity-matrix probe is never specified.

Significance: The error being corrected is ordinary calibration error, and the paper’s own results show a simpler fix is at least as good. The two real-world sources it names: a miscalibrated joint zero and wrong action-normalization statistics (135–138), are resolved once by standard practice. The headline fault on the Panda delta-pose interface is a per-step velocity bias amounting to centimeters per second of drift, visible immediately, not a latent fault. The mid-episode onset in D.5 is injected at a scheduled step; no evidence is given that such biases arise in deployment, and the natural detect-and-recalibrate baseline is not run. Where one-time identification is compared with the online adapter, it wins decisively: hold 15/40 versus NT 0/40 on ALOHA and 22 versus 1 on GR1 (1068–1070), with the known-fault oracle at 57/60 (Table 21); the corresponding Panda experiment is missing. The method itself is a textbook disturbance observer, and its specific design choices do not help: the nominal-error integral beats NT by 8.1 points [1.9, 14.4] on unseen faults (Table 4), and the paper concedes no observer ranking is established (1097).

Result: The results are narrow and the secondary findings are largely null. Everything is in simulation. The headline recovers roughly half the gap (55% versus 95% healthy, 322–323), on a fault class identical to the estimator’s hypothesis class. The one non-injected class: friction, torque, locking, fails or is unresolved (483–485, D.2, D.4). There is no comparison to prior VLA correction methods (JPARC, A2C2, TAM) or to fine-tuning and residual-policy baselines. Healthy noninferiority is not established, and correcting all six channels regresses healthy runs, so the rotation-only mask is a workaround: the method cannot correct translation faults without harming healthy execution. The theory does not connect to task outcomes: better identification yields no task gain (Table 5).

Questions for authors
  1. State in one or two sentences the claim the paper asks readers to accept, and name the single experiment that is primary evidence for it. Which of the remaining results are registered primaries, and which are unresolved secondaries?

  2. Is there any fault that is not representable as a constant additive command offset on which the method improves task success? If not, should the title, abstract and the term "execution errors" be narrowed to that class?

  3. On the Panda holdout (same 110 cases, same seeds), how does identify-for-one-episode-then-hold compare with online NT? Given hold beats NT 15/40 vs 0/40 on ALOHA and 22 vs 1 on GR1 (1068–1070), what evidence shows online adaptation is ever preferable to one-time identification?

  4. What deployment scenario produces a constant command bias that appears mid-episode (D.5) and would not be caught by a residual-threshold detector followed by re-identification? Can that baseline be run on the D.5 setup?

  5. Why is NT the headline law when the nominal-error integral outperforms it by 8.1 points [1.9, 14.4] on unseen faults and L1-style also scores higher (Table 4)? What property of the gate and attenuation justifies them, given they erase correct initial estimates on ALOHA and GR1?

  6. Can the method correct a translation-coordinate fault on any interface without healthy regressions? The paper's own named real-world source, a joint-zero offset, affects translation on a Cartesian interface; how would the rotation-only mask handle it?

  7. Since the APEX-style comparator is acknowledged as neither a faithful reproduction nor an ablation (1399–1403), what does the 18.2-point result in Section 5.1 establish? Why is there no comparison with JPARC, A2C2, TAM, or a residual-policy baseline trained on the same calibration data?

  8. Specify how M is measured: probe magnitude, window length, averaging, and the configuration used. Given the reported 107% change in translation-z sensitivity under one configuration change (1046–1047), why is a single M valid across an episode?

2 comments

Thank you for the careful review. The revision limits the claims to additive command offsets, makes the interface with interchangeable update rules the main contribution, and adds most of the comparisons you requested. "Item N" is row N of the results table in our general response.

Ordinary calibration error

We agree that an offset present from the first step is a calibration error, best removed at its source once known. Our results address an unknown offset. The revision adds early identification (EI), which estimates the offset in the first 20 control steps and then holds it. On 40 new held-out cases, EI raises π0.5's success under a +0.05 offset in normalized units on the six arm coordinates from 21 to 76 of 80 episodes (item 1).

Fault-free success

You are right that noninferiority is not established. On the 220 held-out Panda evaluations, the submission's normalized-target (NT) rule gives 213 fault-free successes with the interface and 209 without. The same holds for the nominal-error integral, which integrates measured motion minus the motion predicted for the policy's commands, with 212 fault-free successes against 211 without correction (item 4).

Q1. Main claim and primary evidence

We claim that, in simulation, feedback between a frozen vision-language-action (VLA) policy and the robot, calibrated only on fault-free motion, recovers much of the success lost to additive command offsets. The primary evidence is the held-out Panda evaluation: under the offset, π0.5 succeeds in 58 of 220 episodes without correction and in 121 with rotation-only NT (+28.6 points, 95% CI [16.2, 41.5]). The introduction now states both.

Appendix F.1 lists the evaluations specified before data collection. Most expected outcomes held, including the main held-out gain, the gain under rotation offsets withheld during development, and EI's gains on new Panda cases and with SmolVLA. For SmolVLA, we chose a 10-step window on development states after the 20-step window gave 188 of 430 successes.

Q2. Faults that are not constant offsets

Yes, when the fault acts like an additive offset. The integral repairs rotation offsets that drift, oscillate, or switch on and off (item 3). With no command offset, EI raises success under a 5 N m joint-torque bias from 41 to 63 of 80 episodes, and under a downward force equal to a 1.0 kg payload's weight, which in early motion acts like an offset (item 10). In a hardware experiment on the left arm of an AgiBot X2 Ultra humanoid, the joint controller's gravity sag acts as an offset that changes with posture, a sim-to-real execution gap for a π0.5 policy fine-tuned only in simulation. Online correction cuts joint tracking error from 0.23 to 0.055 rad, and 3 of 5 runs succeed with it versus 1 of 5 without it (Section 5.1 and our comment to all reviewers). The correction only partially repairs the friction increase present from the start and does not repair joint locking, which removes a degree of freedom and has no command-offset equivalent.

We removed "execution errors" and restricted the abstract and introduction to additive command offsets. As you note, the "previously untested" vectors are new combinations inside the correction mask, so we now call them withheld. We kept the title, since "frozen" already says the policy is unchanged.

Q3. Holding an estimate or adapting online

On the 220 held-out evaluations, holding a rotation estimate identified on one preceding episode yields 132 successes, and online NT yields 119, a difference that is not statistically clear (item 6). Online updating did better when the integral continued from the held estimate (166 against 135 for holding it) and when offsets began at an unknown time (Q4). Unlike a held estimate, it can also follow offsets that vary over time (item 3).

On the withheld offsets, EI and the always-on integral do not differ clearly overall. On ALOHA, holding beats online NT with the submission's slow settings. With faster settings chosen earlier on other seeds, it does not differ clearly from NT or from the disturbance-observer rule (DOB), which removes NT's gate and attenuation (item 12, now in Table 1).

Q4. Mid-episode offsets and a detector

We have no evidence that such offsets arise mid-episode in deployment. The study in Appendix D.5 only tests whether the interface must be told when a fault starts. On its 40 cases, we ran the detector you proposed, which re-identifies and holds the offset after each detection. It caught all 39 onsets, yet succeeded in 24 of 40 episodes against 29 for the always-on integral (−12.5 points, 95% CI [−22.5, −2.5]; item 7), so missed onsets do not explain the gap.

Q5. NT's gate and attenuation

NT is now one of several interchangeable rules inside the interface, which carries the paper's contribution. NT led the submission because we fixed it before the held-out evaluation. Its gate, which ignores small residuals, and its attenuation, which shrinks large ones, did not measurably raise success in our tests, and Section 4 predicts their cost: they put NT's resting point, where its estimate stops changing, below the true offset, so NT can erase a correct initial estimate, as on ALOHA and GR-1.

The integral rests at the offset itself and succeeds in 145 of the 220 held-out evaluations, against 60 without correction and 119 for NT (+11.8 points over NT, 95% CI [4.7, 19.3]; item 4). An L1-style adaptive rule also beats NT, with 138. After the runs, we found that settled estimates follow the order of the resting points. DOB and the L1-style rule share one, yet succeed in 122 and 138, so whether resting points rank rules by success is open.

Q6. Translation without fault-free losses

Yes, with EI, which compares the first 20 control steps with a fault-free reference for the same task and corrects only if its estimate clears a fault-free threshold. On the 40 new cases, it raises success under a translation-only offset from 68 to 77 of 80 episodes. Fault-free, it gains one episode and loses none, while always-on six-coordinate correction gains 3 and loses 7, a difference that is not statistically clear (Appendix F.4). On the 220 fault-free evaluations that informed its design, EI gains one and loses two. A joint-zero error is an additive offset on a joint-position interface. On Panda's Cartesian interface, it depends on the configuration and lies outside the class we correct, as Section 3.1 now says.

Q7. APEX-style result and baselines

The APEX-style result establishes nothing about published Adaptive Policy Execution (APEX), because the comparator is our own reconstruction of APEX. We moved it to Appendix C.7. No implementation of APEX or J-PARC, a fault-supervised residual calibrator, was available to us, and we could not faithfully connect the Torque Adaptation Module (TAM), which learns torque residuals, to LIBERO's pose interface.

With its authors' code, A2C2, a delay-correction head learned from demonstrations, gives SmolVLA 9 of 500 successes under the offset, compared with 5 without it and 127 with our rotation-only integral (item 9). SmolVLA fine-tuned for a known offset succeeds under that offset but almost never without it (item 13).

A residual policy trained on fault-free data alone would have all-zero targets, so we trained one on rollouts with known offsets (item 8). On six coordinates with 800 rollouts, it succeeds in 217 of 240 episodes, compared with 223 for EI. With 200, the budget closest to EI's 160 fault-free calibration runs, it falls clearly below EI at 189.

Q8. Measuring the sensitivity matrix M

We replay one fault-free 70-command episode (Spatial task 0, initial state 25) open loop, once unchanged and twelve times with ±0.02 normalized units on one coordinate. Column j of M is the mean measured increment under +0.02 on coordinate j minus that under −0.02, divided by 0.04, over the steps that both replays complete (61 to 70 of the 70). We agree that M is local to a configuration (Appendix B.2). Even within one episode, a single M does not hold for translation z: its entry changes 2.6-fold between the first 20 steps and the full window, against at most 18.3% for the other five. EI therefore uses the sensitivity of its own 20-step window. We did not measure M beyond 70 steps (Appendix F.10).

Theory and task outcomes

The connection is only partial. We now present the theory as an analysis of how correction bounds, accumulated motion error, and information delay limit recovery, and Section 4 states that it guides the choice of mask and cap but does not forecast task outcomes. Canceling the known offset on the 220 held-out evaluations measures the task cost of these limits (item 5): 166 successes for its rotation part alone, 212 for all six coordinates, and 180 when full cancellation starts two seconds late. A better offset estimate alone need not raise success (Appendix D.1).

Comments on the paper

3 comments

We thank the reviewers for their constructive reviews. The revision narrows the claims to additive command offsets, adds the experiments summarized in our second comment and a hardware experiment on an AgiBot X2 Ultra humanoid, and rewrites the main text for readability. We have uploaded the revised PDF, with new results in Section 5 and Appendix F, and a supplement with the protocol, code, and episode outcomes of every new simulation experiment. Below we address the shared concerns. "Item N" is row N of the table in our second comment.

1. Scope of the claims (8SX3, QPHh, 3jyu)

We agree that the submission overstated its scope. The abstract and introduction now restrict the claims to additive command offsets, without "execution errors", and the "previously untested" vectors are now "withheld". The introduction states one claim: that feedback outside a frozen VLA, calibrated only on fault-free motion, restores a substantial part of the success lost to these offsets, with the Panda holdout (58/220 to 121/220) as its primary evidence.

2. The normalized-target (NT) update rule (8SX3, QPHh, 3jyu)

Our first contribution is the calibrated interface, with the update rule as one replaceable part. On the 220 holdout evaluations, every rule we tested raises success, from 60 without correction to 119 with NT, 122 with a disturbance observer, 138 with an L1-style rule, and 145 with the nominal-error integral (item 4). To our knowledge, no prior VLA study combines such an interface with crossed replay, which separates direct correction from the effect of changed commands. We test the interface on six VLA variants, four simulated robots, and an AgiBot X2 Ultra humanoid.

3. Fault-free losses under six-coordinate correction (8SX3)

In the submission, online correction of all six coordinates lowered fault-free success. Section 3 now adds early identification (EI), which estimates all six coordinates in the first 20 control steps and holds the estimate only if it exceeds a fault-free threshold. On new held-out cases, EI raises success under the offset from 21/80 to 76/80, with fault-free success 77/80 against 76/80 without correction (item 1).

4. Fault class and simulation (8SX3, QPHh, 3jyu)

We added a hardware experiment on the left arm of an AgiBot X2 Ultra humanoid (Section 5.1). For a π0.5 policy fine-tuned only in simulation, the interface largely corrected the sim-to-real execution gap caused by the arm's gravity sag, cutting joint tracking error from 0.23 to 0.055 rad. All other results remain in simulation, and Section 6 now states the scope and what deployment requires. The correction does not fix joint locking and only partially corrects the friction increase present from the start. Under a friction shift, we cannot tell whether it helps. Under the joint-5 torque bias of item 10, online correction with masked allocation lowers success from 36/60 to 15/60, while weighted allocation gives 41/60 (Appendix D.2). The new experiments extend the evidence to time-varying offsets and, for EI, to constant forces including this torque (items 3 and 10).

5. Learned baselines (8SX3, QPHh, 3jyu)

We added three learned baselines: a residual policy trained on rollouts with known offsets (item 8), the Asynchronous Action Chunk Correction (A2C2) delay-correction head learned from demonstrations (item 9), and fine-tuning SmolVLA on relabeled demonstrations (item 13). With six coordinates, EI exceeds the residual trained on 200 rollouts. Under the offset, SmolVLA succeeds in 5/500 episodes, 9/500 with the A2C2 head, and 127/500 with our rotation-only integral.

6. Theory and the remaining failures (8SX3, QPHh, 3jyu)

Section 4 now states that its results inform the choice of mask and cap but do not forecast task outcomes. To locate the remaining failures, we canceled the known offset exactly, which turns 95 of NT's 101 failures in item 4 into successes. Estimation error and the rotation-only mask each account for part of the gap (items 4 and 5).

7. Replay reference and retained cases (QPHh, 3jyu)

We agree that fault-free replay effects depend on the reference. The introduction now reports the faulted result, where correction with the commands fixed lowers rotation error in all 30 valid NT replays per backbone. Appendix F.9 shows that the policy more often solves the shorter, excluded cases without correction, so the physical effects describe the retained cases.

8. Insight into learned policies (3jyu)

The introduction now states our findings about frozen policies. A frozen policy can succeed with part of an offset left uncorrected (item 5), and fine-tuning SmolVLA on relabeled actions specializes it to the labeled offset (item 13). Under faults, the direction and magnitude of the policy's changed commands matter, and a better offset estimate need not increase success.

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Summary of new experiments

All results in this table are from simulation. Intervals are 95% bootstrap intervals over tasks or, for ALOHA, over seeds; an interval that includes zero means we cannot distinguish the two. Separate runs of the same method can differ by a few successes. No correction and NT score 58/220 and 121/220 in the original holdout run and 60/220 and 119/220 in item 4, and EI scores 226/240 over the three offsets of item 1 and 223/240 on the same cases in item 8.

#ExperimentResultWhere
1EI on 40 new cases, two seeds (of 80)+0.05 offset 21 → 76 (known offset canceled 78). Translation-only offset 68 → 77. Mixed-sign offset 7 → 73. Fault-free 76 → 77§5.1, F.4
2EI with SmolVLA (of 430)With π0.5's 20-step window, 6 → 188. Canceling the known offset from step 20 gives 212, against 363 from step 0. A 10-step window, then chosen on development states, gives 323 on the same cases. Fault-free 363 → 368Table 1, §5.1, F.12
3Rotation offsets that drift, oscillate or switch on and off (of 80)The integral raises success from 22–26 to 69–73, NT to 61–64§5.3, F.13
4Update rules, 220 held-out evaluationsNo correction 60, NT 119 (125 at gain 0.16), disturbance observer (DOB) 122, L1-style 138, integral 145. Integral − NT +11.8 points [4.7, 19.3]. DOB − NT +1.4 [−5.9, 7.9]. L1-style − DOB +7.3 [−2.3, 16.8]. Fault-free 211–215. After the runs, we found that settled rotation estimates follow the order of the Section 4 targets§4, §5.1, F.2
5Known offset canceled, same 220 evaluationsNothing canceled 60, rotation part 166, all six coordinates 212 (fault-free 211). With all six canceled, 95 of NT's 101 failures succeed. All six from step 20 give 206, which we cannot tell apart from 212. From step 40, 180 (−14.5 points [−24.6, −6.0])§5.3, F.2
6Hold or continue, same 220 evaluationsHolding an estimate from one preceding episode gives 132 (NT) and 135 (integral). Held NT − online NT +5.9 points [−0.5, 12.9]. Continuing from the held estimate gives 133 (NT) and 166 (integral, +14.1 points [8.3, 20.4] over holding)§5.1, F.3
7Detector with re-identification, offset starting at a hidden step (of 40)Detector 24, no correction 12, integral 29 (detector − integral −12.5 points [−22.5, −2.5]). It caught all 39 onsets that occurred§5.3, F.5
8Learned residual trained on rollouts with known offsets. One network per data budget and one training seed, applied through a six-coordinate or a rotation-only mask, with settings chosen at 800 rolloutsSix coordinates (of 240). EI 223, residual 217 with 800 rollouts (EI +2.5 points [−0.8, 5.8]) and 189 with 200, the budget closest to EI's 160 fault-free executions (EI +14.2 [8.8, 20.4]). Under the forces of item 10, absent from its training, EI 213, residual 202 (EI +4.6 [−2.1, 11.7]). Rotation only on the withheld vectors (of 160). Residual 154 with 800 rollouts and 128 with 200; integral 138 (800-rollout residual − integral +10.0 points [5.0, 15.0]). In a second run, 800-rollout residual 152, EI 133, integral 136 (EI − residual −11.9 [−18.8, −5.0])§5.1, §5.3, F.6
9A2C2 with its authors' code, SmolVLA under the offset (of 500)Base policy 5, with the A2C2 head 9. With our rotation-only integral added, 127 and 172§5.1, F.7
10Constant forces without a command offset (of 80)A constant downward force equal to the weight of a 1.0 or 1.5 kg payload lowers success from 73 to 65 and 51, and a 5 N m joint torque to 41. EI gives 76, 74, and 63, and 75 without a force. The rotation-only integral gives 61, 52, and 38. In early motion, the downward force acts like a constant command offset§5.3, F.8
11Changed stiffness or latency, under the offset (of 80)EI needs task references recorded at the deployed setting. With the original references, it scores 47 and 56 at stiffness ×0.7 and ×1.5 and 56 and 18 at 100 and 250 ms latency, against 76 unchanged. Re-recording them gives 73, 69, 72 and 58§5.3, F.8
12ALOHA, adaptation within the episode, 40 new seeds (of 40)Under the offset, 0 without correction and 0 with the submitted settings. With faster settings chosen earlier on other seeds, NT 10 and DOB 18 (DOB − NT +20.0 points [5.0, 37.5], one task and fault). An estimate held from a preceding episode gives 10 (DOB − held +20.0 [−2.5, 40.0]). Fault-free 13 (NT), 15 (DOB) and 11 (held), against 14 without correctionTable 1, §5.1, F.11
13Fine-tuning SmolVLA on fault-free demonstrations with relabeled actions (of 430)Relabeled for the known +0.05 offset, 371 under it, 8 fault-free and 0 under another offset (EI with the base policy 323, 368 and 246). With one random offset per episode in the labels, 13 and 7 under the two offsets (base policy 6 and 2) and 212 fault-free (base policy 363)§5.1, F.14
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Hardware experiment on AgiBot X2 Ultra

We added a hardware experiment to the revised PDF (abstract, Section 5.1, and Appendix F.15). It shows that the interface can largely correct a sim-to-real execution gap that a frozen policy encounters at deployment. On the left arm of an AgiBot X2 Ultra humanoid, with a frozen π0.5 policy fine-tuned only in simulation, online correction cut the joint tracking error from 0.23 to 0.055 rad, and 3 of 5 runs succeeded against 1 of 5 without correction. Figure 5 in Appendix F.15 shows the robot's head-camera and wrist-camera views of one successful run with online correction. The supplementary material now also contains a side-by-side video, played at 1.5× speed, of one run with online correction, in which the arm places the bowl on the plate, and one run without correction, in which the arm does not pick up the bowl.

The arm follows joint targets through the vendor's joint controller, which, under gravity, lets the shoulder sag about 0.2 to 0.3 rad from its targets. This sag acts as an additive offset on the joint targets that changes with posture. The policy never encountered it, because it was fine-tuned only on demonstrations generated in a simulation of this robot, where targets are reached exactly, and it was never trained on data recorded on the robot itself. On a bowl-to-plate task, we interleaved five runs without correction and five runs in which the innovation-based update rule we use on GR-1 corrects the joint targets online, with the training simulation as its fault-free model.

Without correctionWith online correction
Task successes (of 5 runs)13
Mean joint tracking error0.23 rad0.055 rad
Mean hand lag8.3 cm1.5 cm

Joint tracking error is the largest gap over the seven joints between the measured angles and the policy's targets, and hand lag is the largest per-axis gap between the hand positions at those targets and at the measured angles, both averaged over each run. Every corrected run tracked the policy's targets more closely than every uncorrected run (exact permutation test, p = 0.008).

The experiment extends our evidence from offsets injected in simulation to a sim-to-real execution gap produced by the robot's own controller. The interface largely corrects it without retraining the policy, so it can help when a policy fine-tuned in simulation is deployed on a robot whose controller does not reach its targets exactly.

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

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