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Withdrawn from ICLR 2027

What Makes a Good Pre-training? Dissecting Pre-training Science for Cross-Embodiment Transfer

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

The success of vision-language-action (VLA) models has fueled the consensus that aggregating cross-embodiment data is key to generalist policies. However, given the significant structural heterogeneity across robot embodiments, the efficacy of simple data scaling remains questionable. To address this, we systematically investigate the efficacy of cross-embodiment pre-training. Through real-world manipulation experiments and controlled comparisons on RoboTwin 2.0, we identify kinematic similarity as an important consideration for pre-training data selection. In simulation, pre-training on ARX, which is kinematically closer to Piper, improves downstream performance, whereas FR3 pre-training yields negative transfer. Furthermore, we demonstrate that scaling data diversity, dataset size, and training duration all improve performance on downstream tasks. Our findings suggest that future generalist robot learning paradigms must shift from random data collection to strategic data curation.

Primary area:
applications to robotics, autonomy, planning
Keywords:
Cross-Embodiment, Pre-training

Reviews

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1234this paper, Bottom 10%
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.
Reviewer_7SLFOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This paper investigates how pre-training data composition affects cross-embodiment transfer in vision-language-action models. Using a fixed π₀ architecture, the authors examine source embodiments, scene/object/task diversity, dataset size, and pre-training duration. Evaluation includes RoboTwin 2.0 manipulation tasks and real-world pants folding on Piper.

The experiments show that ARX pre-training improves transfer to Piper, whereas FR3 pre-training produces negative transfer under the tested shared joint-action representation. Under a fixed trajectory budget, expanding the task set provides larger gains than the tested visual-diversity interventions. Additional data and longer training improve performance in some settings. The authors interpret these observations using a manipulability-based kinematic distance and visual and joint-trajectory diversity metrics.

Critical strengths
  1. The source-embodiment comparison reveals a practically relevant negative-transfer phenomenon. With the architecture, pre-training steps, and downstream adaptation protocol held fixed, Table 1 reports that ARX pre-training increases mean success across six downstream tasks from 0.28 to 0.38, whereas FR3 pre-training reduces it to 0.04. This substantial difference demonstrates that demonstrations from another embodiment do not necessarily improve target performance under the tested representation and training protocol. The observation is directly relevant to cross-embodiment data mixing.
  2. The task-diversity experiment evaluates a concrete data-allocation decision. Under a fixed budget of approximately 5,000 trajectories, expanding pre-training from 10 downstream-aligned tasks to 47 tasks improves downstream performance despite reducing demonstrations per task. This provides useful evidence for choosing between increasing demonstration density on aligned tasks and broadening task coverage.
Critical weaknesses
  1. The morphology analysis provides limited validation of kinematic similarity as a source-selection criterion. Table 1 evaluates transfer from two source embodiments, ARX and FR3, to one target, Piper. The kinematic-distance ordering in Table 2 agrees with these outcomes, but agreement on two source-to-target comparisons offers limited evidence of predictive value beyond this setting. Section 3.3 also uses embodiment-specific normalization, zero-padding, and a shared action head for joint-position prediction, whereas the distance compares local manipulability matrices at matched end-effector poses. Compatibility of the inherited joint-coordinate mapping is therefore a plausible alternative explanation that the current comparison does not isolate. Appendix D strengthens the numerical analysis of the metric, but does not establish its predictive relationship with additional transfer outcomes. The authors acknowledge the limited embodiment coverage in Section 5; nevertheless, this remains consequential because morphology-aware source selection is a central practical recommendation.
  2. The diversity and training-duration analyses support narrower conclusions than the broader pre-training guidance emphasized by the paper. Table 3 compares useful interventions under a fixed trajectory budget, but expanding from 10 to 47 tasks is not calibrated against a comparable magnitude of scene or object diversification. The results establish the advantage of this particular task expansion more directly than a general priority for task diversity over visual diversity. Likewise, the VDS–JSD analysis shows that trajectory diversity accompanies improved performance, but does not establish whether JSD predicts transfer beyond these six dataset configurations. Finally, Figure 4(a) reports mean sub-goal completion, and Section 4.1.2 supplements this with qualitative observations about complete-sequence execution. This is suggestive evidence, but the aggregate metric alone cannot distinguish improvements in individual components from improvements in completing the entire sequence. These distinctions matter for a paper whose main contribution is explanatory guidance about pre-training rather than a new policy architecture.
Questions for authors
  1. Predictive value of kinematic distance: Are additional source–target transfer results available to test whether the proposed distance predicts transfer gains? Appendix D includes UR5 in the distance analysis; are corresponding transfer results available? Such evidence would directly affect my assessment of the source-selection criterion.
  2. Effect of action representation: Were action-output reinitialization, embodiment-specific action projections, or related controls evaluated to diagnose how much of the ARX–FR3 difference depends on the shared joint-action representation? These controls would not isolate every embodiment-dependent factor, but could help establish the scope of the morphology conclusion. As Section 4.2.1 acknowledges, the mixed-source comparison also reduces ARX exposure and therefore does not independently isolate interference from FR3 data.
  3. Result stability and skill composition: How many independent training runs underpin the main comparisons, and what performance variation or uncertainty estimates are available? For the pre-training-duration experiment, can the authors provide full-task success and individual sub-goal completion at the evaluated checkpoints, or identify where these are reported? These results would help assess the reliability of smaller differences and distinguish component-level improvement from improved complete-sequence execution.

These questions concern evidence that could materially change my assessment of the current claims, rather than requests for unrelated future work.

Reviewer_GGjKOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

The paper studies how the choice of pre-training data affects transfer to an unseen target robot. It pre-trains π0 on other robots and fine-tunes on a dual-arm Piper robot, in RoboTwin 2.0 simulation and on one real pants-folding task. It reports three findings: pre-training on ARX (kinematically similar) helps, FR3 pre-training causes negative transfer, and more task diversity, more data and longer training all improve results. Its most original piece is a carefully computed kinematic distance based on manipulability, but it is validated on only two source robots. The only solid results are the FR3 negative transfer and the large real-world gain (0.73 vs 0.03), and the latter comes from pre-training that is 97% ARX on mostly folding data, so it is closer to near-same-robot, same-task transfer than true cross-embodiment. The other effects come from single runs without seeds and sit within noise. The FR3 result is also confounded: FR3's 7th joint sits in the action slot ARX and Piper use for the gripper, so the drop may come from that mismatch rather than from kinematics. Overall it is a clean but under-powered setup whose main messages largely repeat prior work, several pieces of it uncited, and its "paradigm shift" claims go well beyond the evidence.

Critical strengths

The study is well controlled, well written, and asks a clear, practical question. It pre-trains on one robot, fine-tunes on a robot it has never seen, and keeps the data budget fixed while comparing different sources and types of diversity, which makes the results easy to interpret and repeat.

It also introduces a careful new way to measure how similar two robots' kinematics are, backed by inverse-kinematics checks, bootstrap intervals and sensitivity tests. This gives others a reusable tool for choosing which robots to pre-train on, although so far it has only been validated on two robots. The work also deploys on real robots so that variation in actuator noise, controller gains, and similar values such as joint friction can be seen as overcome. The result for transfer to Franka is clearly negative, but it is not completely determined kinematic diversity is the only reason.

Critical weaknesses
  1. Limited novelty on morphology. Grouping robots into kinematic families for training is established: House of Dextra trains a policy per family, Abe et al. (which the paper cites) group robots by morphology to reduce gradient conflict, and ManyQuadrupeds does the same for quadrupeds. Training experts per embodiment and distilling them into one policy is also established (GET-Zero; Furuta et al.). Negative transfer from naively pooling robots has been reported too (Shi et al. 2025; Wang et al. 2602.09722). The paper never discusses work that finds transfer across very different robots (Yang et al. 2024; Ai et al. 2025).
  2. Two source robots can't support the kinematic claim. The distance metric is never shown to predict transfer. Its confidence intervals for FR3 and UR5 overlap, the translation-only variant ranks UR5 closer than FR3, and UR5 is never used for pre-training.
  3. The negative transfer is confounded. FR3's 16-dimensional action vector shifts the meaning of every action slot from index 6 onward, so its 7th joint sits where Piper's gripper goes. There is no control with aligned slots, end-effector actions or an embodiment token.
  4. Diversity metrics aren't validated. The visual and joint-space metrics are compared over only 6 datasets with no correlation analysis. Joint-space diversity rises by construction when tasks are added, and the extra tasks also bring new objects, so task diversity is never isolated.
  5. No analysis of which state-space diversity matters. The paper never says which joints, workspace regions or motions drive transfer, so it gives no guidance on what data to collect.
  6. The scaling results are already known. Data scaling and composition effects are reported by Lin et al. (2410.18647), Saxena et al. (2506.13536) and TRI LBM (2507.05331). Here, success is flat from 25% to 75% of the data, and one task (Lift Pot, 0.25→0.85) drives the jump at 100%. The "emergence" curve is a single run, with each checkpoint scored on 10 trials.
  7. Weak statistics. Every result is one run, with no seeds and 10–20 rollouts per task. Only the FR3 drop clears a 95% confidence interval. The headline ARX gain (+0.10) has an interval of [−0.10, +0.31].
  8. Not really cross-embodiment. Piper was chosen for its similarity to ARX. The real-world pre-training data is 97% ARX and 70% folding, so the transfers that work are near-same-robot and largely same-task.
  9. Internal inconsistencies.
    • The same ARX-only recipe differs by up to 0.70 per task between Tables 1 and 4.
    • The appendix states 40 trials per task, but the reported values only fit 10 or 20.
    • The task sets differ across tables.
    • Fig. 1(a) shows a real-world Franka experiment that is never reported.
  10. Overclaimed conclusions. One model, one target robot, joint-position actions only and no released code don't support a "paradigm shift" claim.
Questions for authors
  1. Is the negative transfer due to kinematics or to action padding? Please report pre-training on UR5, which shares Piper's action layout but is kinematically farther from Piper than FR3. Please also report FR3 with its action dimensions aligned to Piper's.
  2. Are the gains larger than run-to-run noise? Please report multiple seeds for Tables 1 and 3. Please also explain why the same ARX-only setup differs by up to 0.70 per task between Tables 1 and 4.
  3. Is task diversity actually isolated from visual diversity? Does the aligned-task dataset use randomized scenes? Do the 37 extra tasks introduce new objects?
  4. Does the real-world gain come from cross-robot transfer or from same-task pre-training? How does a model pre-trained without any folding data perform?
  5. Does the kinematic distance predict transfer? Please show it on more than two source robots, for example additional arms or perturbed ARX variants.
Reviewer_4bpZOpenReview ↗
Rating
1
Confidence
2
Informativeness
1
Presentation
3
Soundness
1
Read review
Paper summary

The paper explores how pretraining data affects downstream performance on a different embodiment. The study axes include: how pretraining embodiment morphology choice affects transfer, what benefits the different axes of variations: scene, task, and object, bring to the transfer; and effect of pretraining data quantity and train steps on transfer.

Critical strengths
  • Diverse task set: pick-place and cloth folding (long horizon) explored.
  • Generally easy to follow, with a clear description of the experimental setup.
Critical weaknesses

Overall, the current claims are weak, and do not provide enough new insights into what makes good pretraining data for cross-embodiment, despite the strong motivation with the main limitation being the 2 pretraining and 1 target embodiment, which severely weakens the study.

  • The limited diversity weakens the support for claim 1: "pretraining on morphologically similar robots improves downstream performance". It could be that having a broader diversity in embodiments is generally useful for transfer: since the target robot is not known in advance, and selecting a particular embodiment pretraining is not feasible (requires models trained on different data distributions).
  • While I agree that kinematic similarity could play an important role for an effective transfer, the current experiments/discussion do not sufficiently prove that it is the only cause: visual similarity of VIPER and ARX and/or similar gripper style, for example, could also have led to easier adaptation.
    • That is, I find the first claim weak: embodiment diversity is limited, and experiments do not provide evidence against other possible explanations.
  • The second claim: "that between visual coverage and behavioral coverage, behavioral is better" is weak: for random eval, diverse scenes attain a similar success rate as the diverse task setting. The gain from diverse tasks of about 0.04 points for clean eval, I believe, is currently weak (please include a confidence interval). In particular, it is again possible that both help comparably. Figure 4b only shows the Pareto front: more visual diversity and more task diversity help. The two axes are not calibrated, so it is hard to establish which is more important.
  • The third claim: "the pretraining data quantity: the more is better for transfer." I believe this claim can be said to be well established in the machine learning community (the cross-embodiment setting may not matter, since the visual diversity itself can help with transferability) and may be somewhat trivial to present as a finding.
Questions for authors
  • Figure 4a: Which model variant is it? (among direct ft, arx only, fr3 only, arx+fr3)
  • Since the target robot is not known in advance, are there recommendations on how the pre-training embodiment mixture should be done (given we cannot select the morphologically similar robot)
  • For L407 and L412: scene diversity vs task diversity. Does the claim apply only to cross-embodiment transfer, or more generally? it would be good to see if a similar trend exists when the target robot is the same as the pretraining robot, to understand whether the observation specifically stems from a cross-embodiment setting, or holds more generally.
  • OXE provides data for diverse embodiments. is there a reason the dataset was not used in the study? It would help broaden the pretraining embodiment set.

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

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