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None of three 2026 real-robot reports offers an offline measure that replaces trials on the robot: if you approve a VLA pilot, approve it as a measurement exercise

Mohammed Cherifi
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18分で読了

要点

Three 2026 real-robot reports on vision-language-action (VLA) models: none offers an offline measure that replaces closed-loop trials on the robot. If you approve a VLA pilot, approve it as a measurement exercise: trials on the cell, a confirmation test fixed in advance, and a smaller baseline trained on the same data.

Summary for the decision

Decision. Whether to commit one cell and engineering time to a vision-language-action (VLA) pilot now, and what evidence to require.

What the reports cannot tell you. Whether the pilot is worth the cell's time. They carry no person-effort, cost or production figures. They bear only on what evidence to require.

Recommendation (interpretation). If you approve the pilot, approve it as a measurement exercise with three parts:

  • closed-loop trials on the cell;
  • a confirmation test whose trial count, conditions, threshold and maximum number of attempts are fixed before it starts;
  • a smaller task-specific baseline trained on the same data.

Do not approve it on benchmark figures, loss curves or a demonstration. None of the three reports shows any of those forecasting behaviour on a new platform.

What that rests on.

  • S1 is a qualitative account of one transfer. Training loss fell to zero and action accuracy reached 1.0 [S1], yet the model showed limited sensitivity to the actual image content [S1].
  • S2 is teams' accounts of choosing checkpoints with few robot trials. It contains no test of whether an offline metric predicted success.
  • S3 measures the question, in one lab on one task. Validation loss was uncorrelated with insertion success over 21 checkpoints of one policy. One smoothness score ordered those checkpoints [S3], retrospectively. The analysis covered diffusion-family policies [S3], not S3's VLA.

Conditions. None of the three settings is a factory. The brief reads three reports, not the literature. Outside work reported to rank or score policies offline or in simulation is listed in the appendix and has not been assessed.

The three studies

Statements are marked reported, derived, assumed or interpretation. Offline means computed on recorded data with no robot moving. Closed-loop means predictions are executed, so each observation depends on earlier predictions. Each report is written by the group that ran the work.

S1S2S3
Setting and robotAuthors' platform: UR5e arm, Robotiq 2F-140 parallel gripperICRA 2026 challenge with simulation, real-robot evaluation and an on-site final on a shared dual-arm humanoid platform [S2]Authors' lab: Franka Research 3 arm, five-fingered Tesollo DG5F hand [S3]
TasksMainly pick-and-place, e.g. "Pick up the apple and place it in the bowl" [S1]Metal Parts Righting, Daily Chemical Bottle Pick-and-Place, Express Package Scanning [S2]RJ45 connector grasping and insertion [S3]; two jig placements [S3]
PoliciesOpenVLA and OpenVLA-OFT [S1]; a ResNet18 behaviour-cloning baseline [S1]π0.5, GR00T N1.7, Diffusion Policy [S2]Seven policy families [S3], including π0.5 fine-tuned with LoRA [S3]
Real behaviour scored asQualitative trajectory behaviour, not aggregated success metrics [S1]Points per task under a time limitStaged outcomes with 95% Clopper–Pearson intervals
Trial countsNone reportedNot reported; a few real-robot evaluation opportunities per team per day [S2]About 1,700 trials over 281 policies [S3]; a session is n=10 [S3]

Figure 1: Conditions of each study. Robots, tasks and scoring differ, so nothing below adds or averages across studies.

None of the three runs one model on both a public benchmark and a real robot, and S1 says its protocol limits direct comparability with existing benchmarks [S1]. The evidence therefore concerns offline measures and, weakly, one competition's simulation stage.

What pre-robot evidence predicted

S1 (reported; one UR5e; no success rates).

  • Offline, the pretrained OpenVLA model reproduced coherent trajectory patterns on data closely related to its training distribution [S1].
  • Zero-shot on the real arm, the motion stagnated after a short execution period [S1], and moving objects in the scene produced no observable change in the executed trajectories [S1].
  • After LoRA fine-tuning, loss and accuracy looked perfect [S1], and comparable training behaviour appeared with black images as input [S1].
  • The authors report a consistent gap between promising offline indicators and unstable closed-loop behaviour on the physical system [S1]. They do not attribute it to the model alone: action semantics, coordinate frames, temporal alignment, image preprocessing and dataset coverage all contribute.
  • Their conclusions apply specifically to OpenVLA and OpenVLA-OFT. [S1]

This documents a case. It is not a test of whether an offline measure ranks checkpoints by success.

S2 (reported; teams' accounts; no test of prediction).

  • NUS-CLEAR deployed the checkpoint with the lowest held-out open-loop error. It says the metric does not perfectly predict closed-loop robot success but gave a practical signal for detecting when fine-tuning began to memorise the small on-site subset.
  • RCL-Lab could not run local closed-loop robot tests and used the last saved checkpoint. It says it could not systematically compare whether lower validation loss, earlier checkpoints or filtered data would have improved real-robot performance.
  • The authors say metrics that reliably predict closed-loop deployment performance remain an important research problem.

An imperfect proxy that a team found useful is not a failed predictor. A proxy that was compared with nothing is untested. S2's simulation stage used Toy Sorting, Parcel Weighing and Conveyor Belt Parts Sorting, not the physical tasks, so it is not a like-for-like predictor (stage shares are in appendix Table A1).

S3 (reported; one lab, one connector task; retrospective). For every checkpoint with robot trials, S3 computed 67 offline metrics on held-out validation episodes and asked whether any tracked robot success. The correlations cover diffusion-family checkpoints only [S3], and π0.5 fine-tuning used no validation split [S3]. A correlation counted as reliable only if it survived Benjamini–Hochberg correction at q=0.05, kept its sign when any single policy was left out, and had at least ten checkpoints.

  • Five of the 67 passed, only for the 21 iDP3 insert checkpoints tested at both jigs (r=−0.70 to −0.80). [S3] They act as a single smoothness score. [S3]
  • Over the same checkpoints, best validation loss was uncorrelated with the insert-given-pick rate (r=+0.08, p=0.72).
  • No cell passed for the centre-only checkpoints or for groups mixing RGB and point-cloud policies [S3], and no metric tracked the pick rate [S3].

"Did not pass" means no association met this criterion in these groups. It does not mean a metric is useless elsewhere. The smoothness result is a correlation found after the trials were run. S3 does not report choosing a checkpoint by the score in advance and then testing that choice.

These statements say what three reports tested, not what offline or simulated evaluation can do. A pre-publication review named five outside studies as ranking or scoring policies offline or in simulation against real-robot results, each with stated limits. They are listed in the appendix and we have not assessed them. If your team proposes to rely on such a method, ask for it to be validated for your policy family, task and platform, and ask whether it ranks candidates or predicts a rate.

What moved results

Interface and configuration (S3, reported).

  • In pairs differing in one setting, a region-of-interest crop raised the iDP3 pick rate from 0 to 100% [S3].
  • Absolute instead of relative actions raised the two-view π0.5 insert from 30 to 100% with a 6D rotation representation, but only from 89 to 100% with Euler angles. [S3]
  • Within the π0.5 family, the best pairing inserted in 100% of trials and the median over 20 pairings in 10%. [S3]

Site data (S2, reported; two teams' accounts, no figures). Task instructions, robot platform and workcell structure were kept unchanged for the on-site final. NUS-CLEAR still found that its Stage-2 checkpoint, deployed directly, performed substantially worse than checkpoints adapted on the small on-site dataset. RCL-Lab found that a small amount of on-site data can be more important than a much larger earlier dataset when it captures the final hardware and scene distribution well.

Backbone (S2, reported; not isolated). The π0.5-based and GR00T N1.7-based entries finished 1.9 points apart [S2], and the authors add that this single competition does not establish model equivalence [S2]. The two entries differ in training steps, action horizon, learning rate, data treatment and checkpoint selection. The gap is therefore not an estimate of what changing the backbone does.

Interpretation. We do not rank these factors against each other; the sources do not allow it. Two narrower points hold for the pilot.

  • Choosing the model does not settle the result. Within S3's π0.5 family, the median pairing inserted in 10% of trials and the best in 100%. [S3]
  • The reports give no transferable interface rule. S3 favours absolute actions for its VLA. S2's two top entries used delta actions (NUS-CLEAR [S2], RCL-Lab [S2]). S1 concludes that delta-based Cartesian control is inherently sensitive to accumulated bias [S1]. These are different robots and action spaces, so settle the question on your platform.

The specialist result

In each study a smaller task-specific policy was competitive on at least one comparison (reported; none is a matched-effort comparison).

  • S1. A behaviour-cloning baseline trained on the same dataset [S1] showed more stable and coherent trajectory behaviour than the VLA-based models [S1]. This is trajectory shape, not task success.
  • S2. Deeptouch.ai achieved the only full score on an individual on-site task with a comparatively small Diffusion Policy trained from scratch.
  • S3. The authors write that the compact point-cloud skill matches the VLA at an eighth of its inference memory [S3]. Their table shows both at 100% insert-given-pick with an interval of [69,100]. [S3] Intervals that wide do not establish equivalence.

Interpretation: three cases are enough to require a baseline arm. They are not evidence that a specialist suits your cell better. S2's authors say large foundation models generally benefit under the broader variation of physical deployment, which they call a tendency rather than a universal rule.

What a success count supports

Derived. Take n trials fixed in advance, on a frozen policy, under one set of conditions, all successful. The two-sided 95% lower bound on the true success rate is 0.025^(1/n). That gives 48% for n=5, 69% for n=10 and 95% for n=73. Ten out of ten is compatible with a true rate of 69%.

What the bound covers. It covers a policy chosen during development and then run through one fresh, pre-specified test, because the choice was made on other trials. It does not cover:

  • a count that includes the trials used to choose the policy;
  • a successful streak picked out after earlier failures;
  • whichever of several attempts happened to pass.

S3's intervals are nominal (interpretation). Promising checkpoints were re-tested in later sessions, while clearly failing configurations were often stopped after two or three trials [S3], and the rates pool every trial of a checkpoint across sessions and pairings [S3]. The pooled counts therefore include the trials that decided which checkpoints got more trials. They are not a confirmed reliability floor.

Sizing one test (assumed thresholds). An acceptance threshold of 95% needs 72 trials, all successful. A threshold of 99% needs 368 (n = ln 0.025 ÷ ln threshold, rounded up). The sources give no threshold; you set it. The formula assumes independent, identical trials, which will not hold exactly on a cell.

Repeat attempts (derived; assumed inputs). Suppose a policy's true rate is 94%, below a 95% threshold.

  • It passes a 72-trial all-success test 1.2% of the time (0.94^72).
  • Across ten such attempts, at least one passes 11% of the time (1 − (1 − 0.94^72)^10).

Reporting how many attempts were made does not correct for this. Either allow one attempt, or declare a maximum number k in advance and size every attempt for 0.025 ÷ k: n = ln(0.025 ÷ k) ÷ ln threshold, rounded up. At a 95% threshold that is 86 trials for k=2 and 94 for k=3. The chance that any below-threshold policy passes anywhere in the declared sequence then stays at or below 2.5% (union bound over the k attempts).

Sizing protects the threshold; it does not make the single-attempt bound valid for the attempt that passed. The lower bound to report for a pass among k declared attempts is (0.025 ÷ k)^(1/n). At k=3 and n=94 that is 95.0%, where the single-attempt formula would give 96.2%.

What an all-success result in one pre-specified test supports

Trials in one pre-specified test, all successful (n): 5. 95% lower bound on true success rate: 47.8%Trials in one pre-specified test, all successful (n): 10. 95% lower bound on true success rate: 69.2%Trials in one pre-specified test, all successful (n): 20. 95% lower bound on true success rate: 83.2%Trials in one pre-specified test, all successful (n): 30. 95% lower bound on true success rate: 88.4%Trials in one pre-specified test, all successful (n): 50. 95% lower bound on true success rate: 92.9%Trials in one pre-specified test, all successful (n): 73. 95% lower bound on true success rate: 95.1%Trials in one pre-specified test, all successful (n): 100. 95% lower bound on true success rate: 96.4%Trials in one pre-specified test, all successful (n): 150. 95% lower bound on true success rate: 97.6%Trials in one pre-specified test, all successful (n): 200. 95% lower bound on true success rate: 98.2%Trials in one pre-specified test, all successful (n): 300. 95% lower bound on true success rate: 98.8%Trials in one pre-specified test, all successful (n): 5. 95% lower bound on true success rate: 47.8%Trials in one pre-specified test, all successful (n): 10. 95% lower bound on true success rate: 69.2%Trials in one pre-specified test, all successful (n): 20. 95% lower bound on true success rate: 83.2%Trials in one pre-specified test, all successful (n): 30. 95% lower bound on true success rate: 88.4%Trials in one pre-specified test, all successful (n): 50. 95% lower bound on true success rate: 92.9%Trials in one pre-specified test, all successful (n): 73. 95% lower bound on true success rate: 95.1%Trials in one pre-specified test, all successful (n): 100. 95% lower bound on true success rate: 96.4%Trials in one pre-specified test, all successful (n): 150. 95% lower bound on true success rate: 97.6%Trials in one pre-specified test, all successful (n): 200. 95% lower bound on true success rate: 98.2%Trials in one pre-specified test, all successful (n): 300. 95% lower bound on true success rate: 98.8%
このグラフのデータ
Trials in one pre-specified test, all successful (n)95% lower bound on true success rate (%)根拠出典
547.8derivedcalculation 1
1069.2derivedcalculation 1
2083.2derivedcalculation 1
3088.4derivedcalculation 1
5092.9derivedcalculation 1
7395.1derivedcalculation 1
10096.4derivedcalculation 1
15097.6derivedcalculation 1
20098.2derivedcalculation 1
30098.8derivedcalculation 1
Two-sided 95% Clopper-Pearson lower bound when every trial succeeds. Valid for one attempt only: a frozen policy, fresh trials, n fixed in advance, one set of conditions, independent trials. A policy chosen on separate development trials is covered. Not valid when the choosing trials are counted, for a streak picked out after earlier failures, or for a pass among several attempts. For a pass among k declared attempts the bound is (0.025/k)^(1/n), which lies below this curve.

Figure 2: Derived; single attempt only. Read your threshold off the vertical axis to size one all-success test. If more than one attempt is declared, size each attempt as above and report the adjusted bound, not a value from this curve.

What to require before and during the pilot

This section is interpretation. The sequence is our proposal; no source tested it as a procedure.

flowchart TD
    G1["1 Replay check on recorded episodes"] -->|"scale, frame, timing agree"| G2["2 Input-response diagnostic"]
    G1 -->|"mismatch"| X1["Fix pipeline before robot time"]
    G2 -->|"output follows the part, not the lighting"| G3["3 Baseline on same data"]
    G2 -->|"otherwise"| X2["Investigate data, preprocessing, conditioning, action interface"]
    G3 --> G4["4 Development trials on cell, with on-cell adaptation"]
    G4 -->|"team freezes the policy"| G5["5 Confirmation attempt: fresh trials; n, threshold and maximum attempts k fixed before attempt 1"]
    G5 -->|"fails, declared attempts remain"| G4
    G5 -->|"fails, no attempts remain"| X3["Stop, or continue with baseline"]
    G5 -->|"meets threshold"| G6["6 Perturbation trials, declared in advance"]

Figure 3: Proposed evidence sequence (interpretation). The reader sets the threshold, n and k before the first confirmation attempt; the sources supply none.

  1. Replay check, before the cell is released. S1's check exposed a consistent underestimation of motion amplitude of approximately 30 to 40% [S1] with no robot moving.

  2. Input-response diagnostic. In S1's noise test the model appeared more sensitive to global luminance distribution than to local object-level content [S1]. Run two checks:

    • Move the part. The predicted action should change the way the task requires.
    • Change brightness without moving anything. The prediction should stay close to where it was.

    A failure is a reason to investigate, not a prescription. S1 says such tests can help detect this but do not resolve it [S1].

  3. Baseline arm. Train a smaller task-specific policy on the same demonstrations and score it under the same protocol.

  4. Development trials on the cell. Run closed-loop, including adaptation on demonstrations from the cell. Log every trial, including runs stopped early. These trials guide the team and may be used to choose the policy. They are not acceptance evidence.

  5. Confirmation test. Before the first attempt, fix the threshold, the conditions, the maximum number of attempts k and the trial count sized for k. k counts every test whose pass you would act on, the baseline's included. Each attempt uses a frozen policy and fresh trials. A pass at any declared attempt counts, reported with the bound adjusted for k. A failure at the last one ends the pilot for that candidate. The simplest rule is k=1.

  6. Perturbation trials. Vary lighting, part pose and tolerance, with the conditions declared in advance. In S3, only a tighter-tolerance socket broke the iDP3 pipeline (0–40%) [S3].

What offline evidence is for. In these reports it has two demonstrated uses: catching a broken pipeline (S1) and, in one retrospective case, ordering insert checkpoints within one policy family (S3). None shows it working as a go/no-go, for comparing policy types, or as a forecast of a move to a new site.

What cannot be sized. Engineering time. The sources give compute, for example approximately 72 hours per training session on four A100 GPUs [S1] in S1, but no person-effort. They agree that robot time is the constraint. S1 says closed-loop rollouts are necessary but costly [S1], and S2 says direct hardware evaluation provides the most reliable signal but is highly inefficient.

What would change this recommendation. Two things would:

  • evidence that a specific offline or simulation method forecasts success for your policy family, task and platform (have your team read the outside studies in the appendix before the pilot is scoped);
  • a matched-effort comparison of a VLA and a specialist on one task.

What this does not show

  • No factory. The settings are two research platforms and a competition venue. There is nothing on cycle time, sustained running, intervention rates or changeover.
  • No case for or against committing the cell. The reports carry no person-effort, cost or opportunity-cost data.
  • No reliability at production scale. The longest all-success record with a stated count is 73 pooled runs of one grasp skill [S3] in S3. It was not a pre-specified test.
  • No offline test of a VLA. S3's correlation groupings contain diffusion-family policies only.
  • No safety or regulatory content. The sources do not address it. That silence is not clearance.
  • No attribution of several practices. S2's filtering, masking and curriculum are not ablated. In S3, the effects of skill decomposition, multi-view perception and recovery demonstrations were not independently isolated [S3].
  • An ambiguity in S1. It is unclear whether the closed-loop comparisons for OpenVLA-OFT and the baseline ran on the physical robot or recursively on recorded data. The baseline's mode is described only as predicted actions recursively fed back into the system [S1].
  • No independent replication in the supplied material. All three were supplied as arXiv preprints.

Technical appendix

Calculations

import math

# Calculation 1: lower bound of the two-sided 95% Clopper-Pearson interval
# when all n trials succeed: (alpha/2) ** (1/n).
# Valid for one pre-specified attempt on a frozen policy with fresh trials.
def lower_bound_all_success(n, alpha=0.05):
    return (alpha / 2) ** (1 / n)

for n in (3, 5, 10, 20, 30, 50, 73, 100, 150, 200, 300):
    print(n, f"{100 * lower_bound_all_success(n):.1f}%")
# 3 29.2%, 5 47.8%, 10 69.2%, 20 83.2%, 30 88.4%, 50 92.9%,
# 73 95.1%, 100 96.4%, 150 97.6%, 200 98.2%, 300 98.8%

# Calculation 2: all-success test size for an assumed threshold when up to
# k attempts are declared in advance. Each attempt is sized so that a policy
# at the threshold passes with probability <= (alpha/2)/k. By the union bound,
# the chance that any below-threshold policy passes in k attempts is <= alpha/2.
def trials_needed(threshold, k=1, alpha=0.05):
    return math.ceil(math.log(alpha / 2 / k) / math.log(threshold))

print([trials_needed(0.95, k) for k in (1, 2, 3)])  # [72, 86, 94]
print([trials_needed(0.99, k) for k in (1, 2, 3)])  # [368, 437, 477]

# Calculation 3: lower bound to report after an all-success pass among k
# declared attempts: (alpha/2/k) ** (1/n). The single-attempt bound of
# Calculation 1 is higher and is not valid after such a selection.
def lower_bound_k_attempts(n, k, alpha=0.05):
    return (alpha / 2 / k) ** (1 / n)

for k, n in ((2, 86), (3, 94)):
    print(k, n, f"{100 * lower_bound_k_attempts(n, k):.1f}%",
          f"{100 * lower_bound_all_success(n):.1f}%")
# 2 86 95.0% 95.8%
# 3 94 95.0% 96.2%

# Calculation 4: unadjusted repeat attempts (assumed inputs).
# True rate 0.94, 72-trial all-success test, 10 independent attempts.
p_pass = 0.94 ** 72
print(round(p_pass, 4), round(1 - (1 - p_pass) ** 10, 4))  # 0.0116 0.1103

# Calculation 5: S2 stage shares = stage contribution / stage maximum
table2 = {  # team: (simulation, real robot, on-site) contributions, S2 Table 2
    "NUS-CLEAR": (16.7, 20.0, 34.3),
    "RCL-Lab": (15.5, 20.6, 33.0),
    "DuanYanWuPing": (16.9, 15.0, 24.7),
    "Youth2Real": (18.8, 16.0, 17.6),
    "mcg": (18.5, 13.2, 19.4),
    "Deeptouch.ai": (7.3, 11.0, 30.8),
}
maxima = (20, 30, 50)
for team, row in table2.items():
    print(team, [f"{100 * v / m:.1f}" for v, m in zip(row, maxima)])

Calculation 1 at n=3, 10 and 73 reproduces the arithmetic of three intervals S3 prints: [29,100] for a skill with three picks, [69,100] and [95,100] [S3]. Matching the arithmetic is not the same as meeting the conditions; see "S3's intervals are nominal".

Table A1: S2 stage shares (derived)

TeamSimulation (÷20)Real robot (÷30)On-site (÷50)
NUS-CLEAR83.5%66.7%68.6%
RCL-Lab77.5%68.7%66.0%
DuanYanWuPing84.5%50.0%49.4%
Youth2Real94.0%53.3%35.2%
mcg92.5%44.0%38.8%
Deeptouch.ai36.5%36.7%61.6%

Derived from the reported stage contributions [S2] and stage maxima of 20, 30 and 50 points [S2]. The two teams with the highest simulation share have the two lowest on-site shares of the six listed. The simulation tasks differ from the physical ones and only six teams are listed. This describes one leaderboard and supports no inference about simulation in general.

Outside the three reports (not assessed)

A pre-publication review named these studies. We have not read them against the standard applied above and do not use them as evidence.

  • RACE (https://arxiv.org/html/2611.05838v1). It is reported to rank checkpoints offline within two policy families, checked against real-robot rollouts. Its authors are reported to call it a relative ranking, not a calibrated success-rate estimate, with selected candidates still requiring deployment validation.
  • CI-MSE (https://arxiv.org/html/2606.29898v2). It is reported to give offline-to-real ranking results for diffusion policies under unseen environments and objects.
  • SIMPLER (https://proceedings.mlr.press/v270/li25c.html). It is reported to show simulated evaluation tracking the relative real-world performance of several policies on matched tasks.
  • AutoEval (https://www2.eecs.berkeley.edu/Pubs/TechRpts/2025/Archive/EECS-2025-42.pdf). It is reported to find that the same kind of simulated evaluation misjudges some policy and task combinations.
  • RoboFQE (https://arxiv.org/html/2610.18699v2). It is reported to estimate success rates offline, not only rankings, for three policies on related block-stacking tasks. Its authors are reported to say it does not establish reliability on tasks absent from the offline dataset.

Inconsistencies in the sources, quoted and not resolved

  • S1, alignment error. The text reads "the RMSE drops further from 0.103m to 0.106m" [S1], which is a drop described with a higher second number.
  • S1, the baseline. It says that across all approaches, including the baseline, coherent one-step predictions do not translate into stable closed-loop trajectories [S1]. It also says the baseline result isolates the limitation to model formulation rather than data alone [S1].
  • S3, robustness. The text says the iDP3 pipeline retained 80–100% of its insertions under changed lighting, background, site and sunlight [S3]. Its robustness table has one cell at 3/5, 4/5 after re-tuning the insert start position for the new site. [S3]

Sources

All were retrieved on 2026-11-14.

  • S1: Hochedel and Lalonde, "Vision-Language-Action Models: Experimental Insights from a Real-World UR5 Platform", arXiv 2606.30456v1.
  • S2: Wang et al., "How to Better Train VLAs: Lessons Learned From the REAL-I Challenge at ICRA 2026", arXiv 2609.13679v2.
  • S3: Abbas et al., "From Teleoperation to Long-Horizon Dexterity: Evaluating Visuomotor Skills and Offline Proxies for Dexterous Manipulation", arXiv 2610.40828v1.

Team, model and product names appear only because the sources use them. No relationship with any author, team or vendor is implied.

AI利用に関する開示: この記事はAIの支援を受けて作成され、Mohammed Cherifiがレビューしました。調査、起草、編集にAIツールが使用されています。 著者が編集上のレビューを行いました。独立した法的レビューは受けていません。

出典

  1. Hochedel and Lalonde - Vision-Language-Action Models: Experimental Insights from a Real-World UR5 Platform, arXiv 2606.30456v1, preprint (retrieved 14 November 2026)
  2. Wang et al. - How to Better Train VLAs: Lessons Learned From the REAL-I Challenge at ICRA 2026, arXiv 2609.13679v2, preprint (retrieved 14 November 2026)
  3. Abbas et al. - From Teleoperation to Long-Horizon Dexterity: Evaluating Visuomotor Skills and Offline Proxies for Dexterous Manipulation, arXiv 2610.40828v1, preprint (retrieved 14 November 2026)
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