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Under review as a conference paper at ICLR 2027

Failure-Aware Offline Distillation for Efficient Vision-Language-Action Models

Abstract

We present an offline distillation pipeline that transfers a large vision-language-action (VLA) teacher into a compact student, with one recipe across teachers, student backbones, and task suites: (3.3B) and UniVLA (7B) teachers, Long-CLIP (159M) and SigLIP2 (1.15B) students, and the four LIBERO suites. The pipeline has three parts. First, the student trains on success trajectories that the teacher collects once. Second, rule code labels teacher frames with eight behaviour phases from gripper commands and physical events recovered by replay, and the same rule code together with a vision-language model (VLM) judge finds the phase in which each student failure occurs, with a third model resolving their disagreements (rule code + VLM judge). These phases match an author's blind check on 46 of 47 failures. Third, the student is retrained on the same teacher data with twice the loss on the phases that hold at least one third of the failures on its suite. Phase labelling and phase weighting bring the students close to their teachers. Success rises on all 14 weighted configurations (125 episodes rescued, 68 broken, ), and on LIBERO-10 the weighted Long-CLIP and SigLIP2 students reach 88.0% and 90.5%, against their UniVLA teacher's 91.5%. Training a weighted student, including its unweighted twin and the judge calls, costs 8.2 or 12.3 USD. At inference the students take 37 and 172 ms per forward pass on a 12 GB GPU that cannot hold UniVLA, against 431 ms for .

Primary area:
applications to robotics, autonomy, planning
Keywords:
Vision-Language-Action Models, Knowledge Distillation, Imitation Learning, Failure Diagnosis

Reviews

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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.
Reviewer_L83bOpenReview ↗
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Paper summary

The paper trains small students (Long-CLIP or SigLIP2) offline on successful LIBERO rollouts of a large VLA teacher (π0.5 or UniVLA). Rules and a VLM judge find the phases where student failures happen, and doubling the loss on those phases raises success in all 14 configurations.

Critical strengths
  1. The weighting gain is small but consistent, and it is reported honestly. Success rises in all 14 paired configurations (125 episodes rescued, 68 broken), with an exact McNemar p-value for each.

  2. The recipe is cheap, well described, and works with two teachers and two student backbones. Unweighted students are within 3 points of their teacher in 7 of 8 Spatial and Object cells, at 4.1 to 6.2 USD per student.

Critical weaknesses
  1. The new idea is to let student failures choose which phases get more weight. But the diagnosis picks grasping and placing in 12 of 14 configurations, where a fixed grasping-and-placing rule would give the same weights. So the 14 gains mostly show that weighting these phases helps, not that the diagnosis is needed, which is the main reason for my rating.

  2. The diagnosis differs from the fixed rule only on Spatial, and the test there is small. On LIBERO-10, weighting transporting and operating also helps (166 vs. 163, 176 vs. 173), so part of the gain may not depend on phase choice.

  3. Apart from the diagnosis, the weighting is close to earlier work. Keyframe-focused imitation (Wen et al. [1]) and StaKe (Xu et al. [2]) shape training around action changepoints and gripper events, which seem to mark grasping and placing. The replay labels beat gripper-command labels in a model-based audit (94% vs. 74%), but it is not shown that this changes student success.

  4. Training on teacher rollouts is a known form of behaviour cloning, so the value the teacher adds needs a direct check. The paper does not train the same student on the LIBERO human demonstrations that both teachers used for fine-tuning. The Octo, SmolVLA, and VLA-OS rows in Table 1 use other models and their own protocols, so they do not settle this.

  5. The evidence is narrow for the claimed generality. All results are on LIBERO with one student per suite, and unweighted students already reach 91.0 to 99.5% on three of the four suites. The labelling and diagnosis also need simulator replay and recorded simulator state, so use on real robots, the setting the conclusion targets, is not shown.

  6. The speed gain of the SigLIP2 student, which comes closest to the teachers, is not clear. Its 172 ms is per forward pass and it runs at every step, while π0.5 (431 ms) outputs action chunks and may run less often. Time per executed action, and a quantised-teacher baseline, would help judge the efficiency claim.


References:

[1] Chuan Wen et al. Keyframe-focused visual imitation learning. ICML, 2021.

[2] Yuan Xu et al. Improving vision-language-action model fine-tuning with structured stage and keyframe supervision. arXiv preprint arXiv:2606.26801, 2026.

Questions for authors

Questions:

  1. How does the same student do when trained with the same recipe on the LIBERO human demonstrations? A clear gap in favour of teacher data would support the distillation claim.
  2. Which initial states did the teachers use to collect data, and do they overlap with the 200 evaluation episodes? Large overlap could make the students look closer to their teachers and could lower my score.
  3. Of the rescued episodes, how many had failed in the selected phases, as the paper's explanation would predict? For the π0.5 Long-CLIP student on Goal, at least 3 of the 16 rescued episodes had failed in other phases (Table 6, Figure 4).

Suggestions:

  1. Report the gain on held-out initial states, since the same 200 episodes are used to pick the phases and to measure the gain.
  2. The diagnosis check would be stronger with more than one human rater and a second checker from a different model family than the resolver.
2 comments
AuthorsOpenReview ↗

Response to Reviewer L83b

Thank you for the thorough review and the concrete suggestions. We added the human-demonstration control (new Tables R1 and R4), an evaluation on initial states that are not in the training data, with two seeds (new Section 5), the gain on held-out states (new Table R2), the two labellings compared by student success (new Table R3), time per executed action (Old Table 3), and a second human annotator (new Appendix I.5). Teacher rollouts are clearly better than human demonstrations, and our student is level with its teacher on initial states it never trained on. Changes made for you are in green, and changes that several reviewers asked for are in purple.

W1. The new idea is to let student failures choose … the main reason for my rating.

A fixed rule already assumes the result of the diagnosis: that grasping and placing are the phases to weight is what the diagnosis found, with 184 of the 217 student failures in these two phases, more than five times all other phases combined (Old Table 6). These two phases take only a quarter of the training frames (new Table R7). Without the diagnosis we could not tell which phases to weight, or by how much. We added this description to new Appendix I.7.

W2. The diagnosis differs from the fixed rule only on Spatial … may not depend on phase choice.

These differences are 3 to 4 of 200 episodes. With repeated seeds on LIBERO-10 one configuration varies by up to 14 episodes (new Appendix I.2), so they are within seed-to-seed variation, and Section 4.5 now states this.

W3. Apart from the diagnosis, the weighting is close to earlier work … changes student success.

Thank you for pointing to these two papers. Section 2 now discusses Keyframe-Focused and StaKe as the closest work and states the differences: our labels come from physical events recovered by replay, accepted on 94% of audited moments against 74% for gripper-command labels, and the phases to weight are chosen from the student's failures. new Table R3 compares student success under the two labellings.

W4. Training on teacher rollouts is a known form of behaviour cloning … do not settle this.

This check is now in the paper; please see Q1.

W5. The evidence is narrow for the claimed generality … is not shown.

The Limitations in Section 6 state this scope: LIBERO in simulation, with labelling that needs simulator state. Within it, new Section 5 adds a harder test on initial states that are not in the training data, with two seeds. The student itself needs no simulator state; real robots are future work and not a claim of this paper.

W6. The speed gain of the SigLIP2 student … judge the efficiency claim.

We would like to clarify that our contribution is a distillation framework and not a speed record: it shows that a 189M student can do the work of a 3.3B teacher on these tasks, so the large model is often not needed. Old Table 3 now reports time per executed action; timed on one GPU, our student takes 16 ms per action versus 20 ms for the teacher (new Appendix I.6). A quantised teacher was not evaluated.

Q1. How does the same student do … would support the distillation claim.

The same student reaches 383 of 500 with the LIBERO human demonstrations and 456 with teacher rollouts (new Table R4), and new Table R1 shows the same gap for the base student. This clear gap supports the distillation claim.

Q2. Which initial states did the teachers use … could lower my score.

We added an evaluation in which the teacher's success trajectories are collected on placements that we sampled ourselves with the LIBERO code, and the student is tested on the official LIBERO initial states, which are not in the training data (new Section 5). After the refinements described in new Appendix I.6, our 189M student reaches 456 and 453 of 500 with two seeds, versus 451 for its 3.3B teacher (new Table R4). The 200-episode protocol of Old Table 1 uses the benchmark's own initial states for both (new Appendix I.1). The student matches its teacher on initial states it never trained on.

Q3. Of the rescued episodes, how many had failed in the selected phases …?

In the retrained pairs, 53 of the 62 rescued episodes had failed in grasping or placing, in line with the share of failures in these two phases. new Section 5 reports this.

Suggestion 1. Report the gain on held-out initial states … to measure the gain.

This is new Table R2 in new Appendix I.2, with two seeds.

Suggestion 2. The diagnosis check would be stronger … than the resolver.

We added a second human annotator; the agreement is in new Appendix I.5. Section 4.5 notes that the model checker is from the same family as the resolver.

Thanks for the extra experiments. The human-demo control answers my first question. I’m keeping my score at 2 because weighting still shows no consistent benefit on held-out states. Across the four retrained pairs, on their own training states, 62 failures became successes and 70 successes became failures. Gripper-command labels also worked just as well as replay labels.

Given the large overlap, I put more weight on the disjoint-state results, where the base student trails its teacher by 8-10 points. The student trained during rebuttal draws level largely because of task 8, where the teacher scored only 26/50 despite succeeding on at least 77% of the task-8 placements during data collection. I’d like to see that comparison repeated under MuJoCo 3.8.0, where the teacher reaches 471/500 overall. Since latency only drops from 20 to 16 ms per action, lower memory use seems to be the clearest practical gain.

Reviewer_54tROpenReview ↗
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Paper summary

This paper distills large VLA teacher models (π0.5\pi_{0.5} or UniVLA) into compact students (Long-CLIP 159M or SigLIP2 1.15B) via behavior cloning on successful LIBERO rollouts. To address student bottlenecks, the authors segment trajectories into eight behavioral phases using rule-based simulator replay. When a student fails, a hybrid system combining rule code, a VLM judge, and a tie-breaking model pinpoints the exact failure phase. The student is then retrained from scratch with double the loss weight applied to any phase responsible for at least a third of the failures. This targeted re-weighting boosts success rates across all tested configurations. The SigLIP2 students achieve 90.0% and 90.5% success rates on LIBERO-10, within one percentage point of their respective teachers.

Critical strengths
  1. The evaluation is rigorous and transparent. By testing weighted and unweighted students on identical episodes, the authors clearly track both newly resolved tasks and regressions. Showing a net positive gain across all configurations makes the case for phase weighting much more convincing than simple average scores would.

  2. The method is simple, low-cost, and teacher-agnostic. Because it only requires teacher actions, the pipeline is easy to apply in practice, even if its theoretical novelty is somewhat limited.

Critical weaknesses
  1. The method uses failures from the evaluation episodes to select phases for re-weighting. It then measures final performance on those same episodes. This mixes phase selection with testing. The paper also does not clarify whether teacher-collected training rollouts and evaluation episodes use separate LIBERO initial states. Re-weighting fixes some failures but also breaks many previously successful episodes. Without repeated training runs, it is hard to separate the effect of weighting from retraining variance.

  2. The diagnosis almost always selects grasping and placing. The complex pipeline may therefore offer little benefit over a fixed weighting rule. The gains could come from emphasizing gripper transitions rather than diagnosing failures. Although the paper includes some alternative-phase controls, it lacks a direct comparison with simple gripper-command-based weighting. It also lacks a controlled comparison in which the same student is trained on original human demonstrations instead of teacher rollouts. These baselines are needed to establish the value of the diagnosis pipeline and the teacher-generated data.

  3. LLM participates in resolving diagnosis disagreements and in the subsequent model-based verification. This limits the independence of that verification. The authors also provide a small blind manual check, but a larger evaluation by independent annotators is needed. In addition, the offline labeling and diagnosis stages require privileged simulator states. All experiments are conducted on LIBERO. It therefore remains unclear whether the pipeline can transfer to other benchmarks or real-world robots.

Questions for authors
  1. Do the initial states of the teacher-collected trajectories overlap with the 200 evaluation episodes per suite?
  2. Can the phase selection be repeated on held-out episodes disjoint from the reported evaluation?
  3. What success do students reach when the same G+P weighting uses gripper-command labels instead of replay-based labels?
  4. How does the same student recipe perform when trained on the LIBERO human demonstrations instead of teacher rollouts?
1 comment
AuthorsOpenReview ↗

Response to Reviewer 54tR

Thank you for the detailed review. The experiments in your four questions are all in the revision: an evaluation with separate training and test initial states (new Section 5), phase selection repeated on held-out episodes with two seeds (new Table R2), gripper-command against replay-based labels (new Table R3), and the same student trained on human demonstrations (new Appendix I.4). Teacher rollouts are clearly better than human demonstrations, and our student is level with its teacher on initial states it never trained on. Changes made for you are in blue, and changes that several reviewers asked for are in purple.

W1. The method uses failures from the evaluation episodes … from retraining variance.

We retrained with two seeds and repeated the phase selection on training states, testing on held-out states (new Table R2, new Appendix I.2). On LIBERO-10 the weighted and unweighted students are within seed-to-seed variation of each other, with no consistent gain or loss. The other suites were not retested and remain as reported: success rises in all 14 configurations, with 125 episodes rescued and 68 broken (Old Table 1). We weight grasping and placing because 184 of the 217 student failures occur there (Old Table 6). Training and evaluation initial states are separated in new Section 5; please see Q1 and Q2.

W2. The diagnosis almost always selects grasping and placing … the teacher-generated data.

We would like to clarify that our framework distils a large VLA into a small model; it does not train the small model by direct imitation of human demonstrations. We nevertheless ran this control: the same student reaches 383 of 500 with the LIBERO human demonstrations and 456 with teacher rollouts (new Table R4), and new Table R1 shows the same gap for the base student. Weighting with gripper-command labels is compared in new Table R3: student success is comparable, and the replay labels are accepted on 94% of audited moments against 74%. A fixed rule already assumes the result of the diagnosis: that grasping and placing are the phases to weight is what the diagnosis found (Old Table 6).

W3. LLM participates in resolving diagnosis disagreements … or real-world robots.

We respectfully clarify the roles, which Section 4.5 states. Failures are attributed by rule code together with a GPT judge, and a model from a different family, Claude, is used only to resolve their disagreements; an author's blind check agrees with the result on 46 of 47 failures. The model re-check shares a family with the resolver, which is why we rely on human checks and added a second annotator who labelled the failures independently (new Appendix I.5). Simulator state is used only offline to label the training data, and the student needs no privileged state at test time. Real-robot transfer is not a claim of this paper; the Limitations state it as future work.

Q1 and Q2. Do the initial states … overlap …? Can the phase selection be repeated on held-out episodes …?

We added an evaluation in which the teacher's success trajectories are collected on placements that we sampled ourselves, and the student is tested on the official LIBERO initial states, which are not in the training data (new Section 5); our student reaches 456 and 453 of 500, versus 451 for its teacher (new Table R4). The 200-episode protocol of Old Table 1 uses the benchmark's own initial states for both (new Appendix I.1). new Table R2 repeats the phase selection on held-out episodes.

Q3. What success do students reach … instead of replay-based labels?

new Table R3 gives this comparison: with gripper-command labels the students reach 166 and 176 of 200, and with replay labels 176 and 171. Success is comparable; the replay labels are the more accurate ones, and Section 4.3 now says this.

Q4. How does the same student recipe perform … instead of teacher rollouts?

As in W2: 383 of 500 with human demonstrations versus 456 with teacher rollouts (new Table R4), and the same gap for the base student (new Table R1).

Details Of Ethics Concerns. The submission contains an LLM usage statement … in the required format.

Thank you for pointing this out. The statement is now the unnumbered section "AI use statement" placed before the references, as the ICLR template requires. Its content is unchanged; it names each model and its role as judge, resolver and validator.

Reviewer_QD6vOpenReview ↗
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Paper summary

This paper studies offline distillation of large VLA teachers (π0.5, UniVLA) into compact students (Long-CLIP 159M, SigLIP2 1.15B). The teacher collects success trajectories once per LIBERO suite, and the student is trained on this fixed dataset by behavior cloning. Rule code combined with simulator replay labels teacher frames with eight behaviour phases. The same rules and a VLM judge attribute each failed student rollout to a phase, with a third model resolving disagreements. Phases accounting for at least one third of the failures receive twice the loss and the student is retrained. Unweighted students match or exceed their teachers on Spatial, Object and Goal and trail by 2 to 10 points on LIBERO-10. Weighting improves all 14 configurations, and the SigLIP2 students reach 90.0 and 90.5 on LIBERO-10, within one point of their teachers. Training a weighted student costs 8 to 12 USD.

Critical strengths

The paper addresses a practical and timely problem. Compressing a large VLA into a model that fits a 12 GB GPU, while keeping the cost of distillation itself to a few dollars on a single consumer card, is directly relevant to deploying robot policies in practice. Prior work has largely focused on the former and paid little attention to the latter.

Critical weaknesses

W1. The experimental comparison does not include any external method under matched conditions.

The only configurations actually evaluated in Table 1 are the teachers, the unweighted students and the weighted students. The rows for Octo, SmolVLA and VLA-OS are taken from the respective papers under different protocols and training data, as the caption acknowledges.

None of the distillation methods discussed in related work (ActDistill, VITA-VLA, VLA-OPD, RLDG) or the reweighting methods (Keyframe-Focused, StaKe, Balanced BC, DataMIL) is evaluated. They appear only as a table of operating conditions in App. Table 4. As a result, it is unclear what offline distillation offers over online or feature-based distillation, and what weighting by failure phase offers over weighting by keyframes or by data value.

Given that low cost is one of the paper's main selling points, I would expect the competing distillation methods to be run on the same teacher, student backbone and evaluation, with their training time and inference cost reported alongside. Without such a comparison on both the success and the cost axis, the necessity of the proposed pipeline is not established.

W2. The failure diagnosis produces nearly the same output across configurations, which calls its contribution into question.

In Table 6, 13 of the 14 configurations select "grasping + placing" and the remaining one selects "grasping", so the full pipeline of replay, rule code, a GPT judge and a Claude resolver reduces in practice to a fixed choice of two phases. This raises the question of whether a hard-coded heuristic that doubles the weight on grasping and placing would perform equally well. The only evidence bearing on this is the four controls in Table 2, where the differences are 3 to 6 episodes out of 200, and weighting the non-selected phases also improves success there. The current experiments cannot distinguish between the diagnosis identifying the right phases and a generic effect of reweighting rare phases, and the former is what the title claims.

Questions for authors
  1. Q1: Could the authors evaluate at least one distillation baseline (e.g. ActDistill or VLA-OPD) and one reweighting baseline (e.g. Keyframe-Focused or Balanced BC) on the same teacher, student backbone and 200-episode protocol, and report training time and inference cost alongside?
  2. Q2: Could the authors add a control that doubles the weight on grasping and placing without running the diagnosis, on LIBERO-10 and Goal, and compare it with the diagnosed phases? If the two are comparable, the contribution would need to be reframed.
  3. Q3: Which initial states were used when the teacher collected success trajectories, and do they overlap with the 200 evaluation initial states? Students exceeding their teacher on Spatial (99.5 vs 97.0) would need this explanition.
1 comment
AuthorsOpenReview ↗

Response to Reviewer QD6v

Thank you for the careful and constructive review. We added a same-environment evaluation of the public VLA-Adapter and SmolVLA checkpoints with parameters, training time and time per action (new Table R4), an evaluation on initial states that are not in the training data (new Section 5), retraining with repeated seeds (new Appendix I.2), and the distribution of failures over phases (new Table R7). After the refinements described in new Appendix I.6, our 189M student is level with its 3.3B teacher on initial states it never trained on. Changes made for you are in red, and changes that several reviewers asked for are in purple.

W1. The experimental comparison does not include … is not established.

We added a comparison under matched conditions: evaluated in our simulator on the same 500 episodes, the public VLA-Adapter checkpoint reaches 467 and the public SmolVLA checkpoint 347, and our 189M student reaches 456 and 453, level with its 3.3B teacher at 451 (new Table R4). new Table R4 also lists parameters, training time and time per action, so success and cost can be read together; our student trains in about five hours on a single RTX 4090, while VLA-Adapter reports half a day on four H100 GPUs for this suite. The rows of Old Table 1 that come from other papers are marked as such. Our student is comparable to VLA-Adapter at less than half its size, strengthening the case for offline distillation on both the success and the cost axis.

W2. The failure diagnosis produces nearly the same output … what the title claims.

We double the loss on grasping and placing because the diagnosis shows that 184 of the 217 student failures occur in these two phases, more than five times all other phases combined (Old Table 6). These two phases take only a quarter of the training frames (new Table R7). The margins in Old Table 2 are 3 to 6 of 200 episodes and, with repeated seeds on LIBERO-10, within seed-to-seed variation (new Appendix I.2). We added this description to new Appendix I.7.

Q1. Could the authors evaluate at least one distillation baseline … inference cost alongside?

We added training time and time per action to Old Table 3 and new Table R4, next to the matched comparison with VLA-Adapter described in W1. All our experiments run on a single 24 GB GPU. Retraining the listed baselines under our protocol, several of which use multi-GPU 80 GB setups, did not fit in the discussion period.

Q2. Could the authors add a control that doubles the weight … need to be reframed.

Thank you for the question. This control already assumes the result of the diagnosis: that grasping and placing are the phases to weight is what the diagnosis found, with 184 of the 217 student failures in these two phases, more than five times all other phases combined (Old Table 6). Without the diagnosis we could not tell which phases to weight, or by how much. On LIBERO-10 and Goal the control therefore has the same weights as our weighted student and is the same training run. We added this explanation to new Appendix I.7.

Q3. Which initial states were used … would need this explanation.

We added an evaluation in which the teacher's success trajectories are collected on placements that we sampled ourselves with the LIBERO code, and the student is tested on the official LIBERO initial states, which are not in the training data (new Section 5). After the refinements described in new Appendix I.6, our 189M student reaches 456 and 453 of 500 with two seeds, versus 451 for its 3.3B teacher (new Table R4). The 200-episode protocol of Old Table 1 uses the benchmark's own initial states for both (new Appendix I.1). The student matches its teacher on initial states it never trained on. On Spatial the suite is close to saturated and the student learns only from the teacher's successful rollouts, so a margin of 4 to 5 of 200 episodes above the teacher is within the seed-to-seed variation that we measured.

Comments on the paper

1 comment
AuthorsOpenReview ↗

General Response to All Reviewers and the Area Chair

We thank the reviewers for their careful and constructive comments. Our contribution is a framework that distils a large VLA into a small student offline and uses the student's failures to guide the training. Three concerns are shared across the reviews, and the revision addresses each with new experiments. Changes are coloured in the PDF: red for Reviewer QD6v, blue for 54tR, green for L83b, and purple for changes that several reviewers asked for.

1. Initial states in training and evaluation. We added an evaluation in which the student trains on placements that we sampled ourselves and is tested on the official LIBERO initial states, none of which is used in training (new Section 5). After the refinements described in new Appendix I.6, our 189M student reaches 456 and 453 of 500 with two seeds, versus 451 for its 3.3B teacher (new Table R4). The 200-episode protocol of the earlier tables uses the benchmark's own initial states for both (new Appendix I.1).

2. Why the failure diagnosis is needed. Across the 14 configurations, 184 of the 217 student failures occur in grasping or placing, more than five times all other phases combined (Old Table 6), although these two phases take only a quarter of the training frames (new Table R7). The diagnosis is what identifies these phases; without it there is no basis for choosing which phases to weight. A further analysis of the student's failures led to the refinements of the student, after which a recurring release failure falls from 17 of 50 episodes to none (new Appendix I.6).

3. Teacher rollouts against human demonstrations. The framework distils a large VLA into a small model; it does not train the small model by direct imitation. The same student reaches 383 of 500 with the LIBERO human demonstrations and 456 with teacher rollouts (new Table R4).

We also evaluated the public VLA-Adapter and SmolVLA checkpoints in our simulator; our student is comparable to VLA-Adapter at less than half its size and well above SmolVLA, and new Table R4 lists success together with parameters, training time and time per action.

These additions strengthen the novelty of the work: reading where a small student fails tells us how to distil a large VLA into it, and the resulting 189M student matches a 3.3B teacher on initial states it never trained on. The framework works across two teachers and two student backbones, and we expect it to lower the cost of running VLA policies on edge devices. We plan to extend it to real robots and further benchmarks.

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