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Robotics · arXiv:2610.21915 v1 · submitted 15 Oct 2026 · 63 references

What Should Robot Policies Learn to Predict? Rethinking Supervision Targets in Vision-Language-Action Learning

Haitao Shen, Hanyu Liu, Yihan Lin, Huiping Liu, Junbo Cui, Daoheng Li, Yang Li, Jing Zhang

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Wenxin Li, Yuan Yao

The paper says

“Vision-language-action (VLA) policies are typically trained with action prediction as the primary supervision signal, since robots ultimately execute actions.”

more of the abstract

Auxiliary objectives such as latent-action (LA) and future-vision (FV) prediction are often added to improve policy learning, yet they compete with action prediction for the same training budget. We ask whether, under a fixed budget, allocating a substantial share of training samples to such objectives, rather than to further action prediction, can improve policy learning. We build a unified VLA framework that couples a two-stream multimodal diffusion transformer (MMDiT) with a sample-level router, which assigns each training sample to either action prediction or an auxiliary objective and thus makes supervision allocation explicit. Within this framework, we instantiate three LA targets based on LAPA and its DINO-feature variants, and three FV targets based on DINOv3, V-JEPA 2, and Wan2.2 representations. Across LIBERO, CALVIN, and four real-robot tasks, suitable LA and FV supervision outperforms action-only training under the same budget, even when action prediction receives no more than half of the training samples. FV generally outperforms LA, although the strongest LA target remains competitive on CALVIN. Diagnostic analyses suggest that DINO-based LA targets emphasize relative motion, whereas FV targets emphasize absolute position and task identity. We therefore argue that what robot policies learn to predict, and how training is allocated among these targets, should be treated as explicit design choices rather than defaulting to action-dominant training.

from the abstract

Pith says

Machine review · deepseek-v4-flash · 16 Oct 2026 · what was read was not recorded · not checked by a person

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Holds up, with conditions. A well-disclosed, well-controlled study of supervision allocation in VLA training whose headline future-vision gains are partly confounded by a clean-action conditioning input that is never ablated. This line is wrong

2 major objections · 5 minor

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The paper says, at §3.2, Eq. (6), Appendix A.2

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Pith says: Objection 1 of 2 · major

The FV-versus-action comparison varies two variables at once. FV-routed samples receive the clean demonstrated action chunk as an input with τa fixed at 1, while action-routed samples receive noisy actions, and the source-matched P100 control contains no sample that receives clean actions, so it cannot separate the FV prediction target from the clean-action conditioning.

more of objection 1

The paper discloses this asymmetry ('FV-routed samples condition on clean demonstrated actions, whereas action-routed samples receive noisy actions'), but it never ablates it: there is no FV run with noisy action conditioning on the auxiliary route and no run that removes at from Eq. (6) while keeping the FV loss active. Because the two experts share joint self-attention, the action expert can in principle exploit the clean action tokens during training even though they are unavailable at inference. The headline FV results—including the V-JEPA 2 P25 CALVIN gain (4.522 vs 4.091), the across-budget gains in Table 12, and all four real-robot scores—therefore bundle the predictive target together with an oracle-action input, and the causal reading ('what should policies learn to predict') is not established for FV. The same confound contaminates the FV-over-LA comparison, since the LA route never receives clean actions. Please add the conditioning ablation (e.g., FV P50 with sampled τa on auxiliary samples, or with at removed from the FV expert input), or explicitly reframe the FV findings as gains of the full FV-routing protocol rather than of the prediction target per se.

The paper says, at Tables 1, 6, and 8; §4.2–§4.3

The review did not quote this passage.

Pith says: Objection 2 of 2 · major

The main-text headline numbers are single-evaluation-seed (seed 0), and the three-seed means in Table 6 reverse several close orderings the text relies on. On CALVIN P50, seed 0 favors V-JEPA 2 over LAPA-DINOv3 (4.451 vs 4.434), but the seed-averaged values reverse that order (4.419 ± 0.029 vs 4.471 ± 0.034), so the 'FV generally outperforms LA' claim and the 'strongest LA target remains competitive' hedge both need to be stated from the averaged values.

more of objection 2

The DINOv3 P50 margin over the full-budget action-only baseline shrinks from +0.056 at seed 0 to +0.030 seed-averaged (4.365 ± 0.010 vs 4.335 ± 0.040), i.e., well within one standard deviation. On LIBERO the P50 gains over source-matched controls are +1.10 and +0.60 pp for V-JEPA 2 and Wan2.2 at 60k, and DINOv3 is 0.20 pp below its control (Table 8); with roughly 2,000 rollouts and no repeated-seed or variance report for LIBERO, these margins are close to the noise floor. Please report seed-averaged values (or variances) for every comparison that survives in the main text, and soften the CALVIN-specific formulations where the ordering reverses under averaging.

5 minor objections

The paper says, at Title, abstract, §1

Pith says: minor objection 1 of 5

The text contains several typesetting artifacts ('R ETHINKING', 'V ISION -L ANGUAGE -ACTION', 'V -JEPA 2', 'CAL VIN', and 'Y et' at the start of a sentence in Section 1); these should be cleaned in the final version.

The paper says, at §3.1, abstract

Pith says: minor objection 2 of 5

The budget is defined as sample exposure, and the paper correctly notes this does not establish equal FLOPs or wall-clock time (Section 3.1). Since FV-routed samples additionally run a frozen encoder forward pass (up to roughly 304M parameters for V-JEPA 2), per-sample compute differs substantially by route; the abstract's 'under the same budget' should carry the same qualifier so the claim is not over-generalized.

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The paper says, at Appendix B.4, §4.2

Pith says: minor objection 3 of 5

The per-target LA loss weight λq is selected on LIBERO (Table 10) and then reused on CALVIN and the real robot, so the cross-target LA ranking on LIBERO embeds per-target weight selection. The FV weight is fixed at 1.0 and untuned, so the FV claims are unaffected; please state this asymmetry explicitly where the LA targets are compared with each other.

The paper says, at §4.2, Fig. 4, Table 11

Pith says: minor objection 4 of 5

The source-matched FV P100 controls score below the shared action-only baseline on CALVIN at every budget (Section 4.2, text near Fig. 4), so part of the FV gain over the source-matched control is recovery from a mildly handicapped two-stream control rather than a benefit of the auxiliary target. The paper already reports both reference lines in Figure 4; keeping the plain action-only line in all allocation figures would make this reading easier for the reader.

The paper says, at §4.4, Table 2, Appendix C.1

Pith says: minor objection 5 of 5

The 'unseen tasks' numbers in Table 2 use checkpoints selected on seen validation, and the appendix correctly labels the readout as within-seen generalization; a one-sentence restatement of this in Section 4.4 would prevent the 'unseen' label from being misread as a fully held-out estimate.

What would settle it

Run the V-JEPA 2 FV configuration on CALVIN at P50 with one change: on FV-routed samples, replace the clean demonstrated action chunk in Eq. (6) with a noisy action chunk sampled from the same interpolation schedule used on action-routed samples (so tau_a is sampled and not fixed to 1), keeping the FV flow-matching loss and all other settings identical. Compare Avg. Len. and SR-5 over the same three evaluation seeds against (a) the reported P50 run, (b) its source-matched P100 control, and (c) the full-budget action-only baseline. If the P50-vs-P100 margin collapses or reverses, the headline gain is attributable to clean-action conditioning rather than the future-vision target; if the margin is substantially retained, the confound is not the main driver of the result.

from the skeptic's reading

How the review went

4 readings by deepseek-v4-flash · 16 Oct 2026

  1. Reader holds up, with conditions confidence moderate
  2. Skeptic agrees 30 s · 28,780 tokens read, 3,098 written
  3. Editor wrote the verdict above 51 s · 29,625 tokens read, 5,113 written
  4. Referee major revision: 2 major objections, 5 minor 2 min 10 s · 28,933 tokens read, 14,512 written

Not run on this paper: the simulated authors' defence.

Pith did not check this review's objections against the paper.

The review in full

The review in brief, machine-written

The short version: this is a careful and mostly well-controlled empirical study of whether auxiliary supervision can take most of the training sample budget and still beat action-only VLA training, and the question is new relative to what it cites. The machinery is the right shape: a sample-level Bernoulli router, a two-stream MMDiT with joint self-attention, and source-matched P100 controls for each FV target that hold everything fixed except routing. The paper also reports its own mess honestly — budget means sample exposure, not FLOPs; P25 mostly hurts on LIBERO; some source-matched controls sit below the shared action-only baseline; one close CALVIN ordering reverses under seed averaging. That disclosure is the best thing about it.

The soft spot that matters is the FV conditioning confound, and I think it lands. Per Eq. (6) and Section 3.2, FV-routed samples get the clean demonstrated action chunk as input with tau_a = 1, while action-routed samples get noisy actions. The paper discloses this but never ablates it: no FV run with noisy action conditioning, no control that keeps the FV loss active without clean-action input. Since the experts share joint self-attention, the action expert can attend to those clean action tokens during training. So the FV gains over action-only, and the FV-over-LA comparison, bundle the prediction target with an oracle-action conditioning advantage. The empirical result still stands, but the "what to predict" causal claim is wider than the experiment supports. The LA configurations do not carry this confound, and they give a thinner version of the claim: only LAPA-DINOv3 on CALVIN beats the full-budget action-only baseline.

The rest is minor. Headline numbers are single-seed, but the multi-seed table is there and supports the strongest configs. Real-robot results have no variance estimate and no released artifacts. LA loss weights were tuned on LIBERO and then reported on LIBERO. All three are disclosed. The frozen-encoder diagnostics are suggestive rather than causal, which the paper mostly says itself.

Who it is for: anyone working on auxiliary objectives in VLA or on training-budget allocation. It deserves a serious referee; the main things to ask for are the clean-action ablation, seed-averaged headline numbers, and an abstract that does not outrun the FV evidence.

The strongest objection

The central claim holds only if FV-routed samples differ from action-routed samples in the supervision target. They also differ in input conditioning: Eq. (6) feeds the clean demonstrated action chunk at into the FV expert, and Section 3.2 with Appendix A.2 state that FV-routed samples receive clean actions with tau_a = 1, while action-routed samples receive noisy actions. A P50 FV run therefore gives half of the samples oracle-action information in addition to the FV loss; because the two experts share joint self-attention, the action expert can attend to these clean action tokens during training, even though clean actions are unavailable at inference. The paper discloses this asymmetry (Section 3.2) but never ablates it: there is no FV P50 run with noisy action conditioning, and no control that keeps the FV loss active while removing the clean-action input. Consequently, the observed FV gain over action-only training, and part of the FV-over-LA comparison, may be a teacher-forcing/conditioning effect rather than evidence about which target the policy should predict. This does not invalidate the empirical result, but it does block the causal reading of the paper's framing.

The reader's weakest_assumption identifies the same issue: FV-routed samples receive clean demonstrated actions as conditioning (Eq. 6, Section 3.2, Appendix A.2), while action-routed samples receive noisy actions. This is the most load-bearing concern because it sits directly between the reported numbers and the paper's central interpretive claim that 'what robot policies learn to predict' drives the gains. If the clean-action input is responsible, then the experiment demonstrates a benefit of action-conditioned future-feature prediction with teacher forcing, not a benefit of reallocating supervision away from action prediction toward a different predictive target. The paper is transparent about the design, and the source-matched P100 controls are a genuine strength, but a P100 control only varies routing; it does not vary the action-input cleanliness on auxiliary samples. The proposed test directly removes the confound while keeping the FV loss, routing, architecture, and budget fixed. Secondary concerns, such as single-seed headline numbers and absent real-robot variance estimates, are real but less central; seed-averaged Table 6 already shows the strongest FV result (V-JEPA 2 P25) is robust, and the real-robot results are clearly reported as task scores without variance. The clean-action conditioning issue is the one that, if confirmed, would require rewriting the paper's causal conclusion rather than just adding error bars. Because the reader's verdict is already CONDITIONAL and explicitly asks for this ablation, my assessment does not move the verdict.

The referee's report

If the central claim holds, the paper makes a useful empirical contribution: it challenges the default of action-dominant training and supplies a clean experimental apparatus (sample-level routing plus source-matched P100 controls that fix initialization, data, encoder, architecture, and schedule, changing only routing) for studying supervision allocation. The authors are unusually candid about scope: budget matching is explicitly sample exposure, not FLOPs or wall-clock time (Section 3.1); a three-seed CALVIN table is provided with the caveat that main-text numbers use seed 0 (Appendix A.3); and the diagnostic claims are carefully bounded as descriptive rather than held-out (Appendix C.1). The principal weakness is interpretive: the FV condition conflates the prediction target with clean-action input conditioning, so the paper's 'what to predict' framing is not yet causally established; this is fixable with a targeted ablation and is the main reason the paper needs another round.

Pith's reading of the paper (a machine's summary, not the authors')

Robots are usually trained by making action prediction the dominant supervision signal, with latent-action or future-vision objectives added only as small auxiliaries. This paper asks whether that default is wrong: under a fixed training budget, what happens when a large share of training samples is routed to predicting latent actions or future visual representations instead of predicting actions directly? With a unified framework built from a two-stream diffusion transformer and a sample-level router, the authors find that suitable latent-action (LA) and future-vision (FV) targets outperform action-only training at the same total budget on LIBERO, CALVIN, and four real-robot tasks, even when action prediction receives only half or fewer of the samples. Future-vision targets generally beat latent-action targets, and the best allocation depends on the target, the benchmark, and the budget. If the claim holds, what a policy learns to predict, and how much of the training budget it gets, are design choices rather than fixed defaults.

What carries the argument. Two mechanisms carry the argument. First, a sample-level router: for each training sample, a Bernoulli draw assigns the sample to either the action loss or one auxiliary loss, making the supervision allocation explicit as a routing probability (P25, P50, P75, P100) under a fixed budget $B = N B_{\mathrm{eff}}$ that counts sample exposures. Second, a two-stream multimodal diffusion transformer (MMDiT) on top of a pretrained vision-language model, in which an action expert and an auxiliary expert exchange information through joint self-attention: the auxiliary expert predicts either discrete latent-action codebook indices (LA, from LAPA and its DINO-feature variants) or the flow-matching velocity of a future visual representation (FV, from DINOv3, V-JEPA 2, or Wan2.2 features). The paper notes one asymmetry it does not remove: FV-routed samples condition on the clean demonstrated action chunk, whereas action-routed samples receive noisy actions. Within a matched configuration the router is the only element that changes, which is what allows P25 through P100 allocations to be compared on equal footing, with each FV target having a source-matched P100 control.

Core claim. The paper's central claim is that direct action prediction need not dominate robot-policy training: under a fixed budget of sample exposures, reallocating a substantial share of samples to auxiliary prediction targets can produce better manipulation policies than spending the entire budget on action prediction. Concretely, with half the samples routed to future-vision prediction, all three FV configurations exceed the full-budget action-only baseline on LIBERO (up to 98.15% mean success with the Wan2.2 target), the best FV configuration reaches 4.451 average task-chain length on CALVIN versus 4.314 for action-only training, and on four real-robot tasks every FV configuration surpasses the action-only baseline by up to 20.1 points of task-completion score while no LA configuration does. The paper further claims that FV generally outperforms LA, with the strongest LA configuration (LAPA-DINOv3) remaining competitive on CALVIN, and that the optimal allocation is setting-dependent: on CALVIN the strongest FV target improves even when only a quarter of samples go to action prediction, whereas on LIBERO every tested P25 configuration falls below its control. The authors argue that the two supervision families shape learning differently, with DINO-based LA targets emphasizing relative motion and FV targets emphasizing absolute position and task identity, and both can redirect policy attention toward task-relevant regions.

The premise it rests on. The claim that future-vision prediction itself causes the gains assumes FV-routed and action-routed samples differ only in which loss is active, but FV-routed samples are the only ones that receive the clean demonstrated action chunk as input, and the paper never ablates that conditioning to isolate the target's contribution.

If the paper is right (Pith's inferences, not the authors')

Under a fixed sample budget, spending half or more of the samples on a well-chosen auxiliary target can beat action-only training, so the default of action-dominant supervision should be revisited rather than assumed.

The best routing probability is target- and benchmark-dependent: on CALVIN the strongest FV target improves at P25, while on LIBERO every P25 configuration loses to its control.

Future-vision prediction is the safer default across the tested settings, leading on LIBERO and all four real-robot tasks, with DINO-feature latent actions competitive on CALVIN.

Fair comparison of supervision targets requires source-matched controls that change only the routing, keeping encoder, architecture, data, schedule, and inference fixed.

Because frozen-source readouts show FV representations carry absolute-position and task-identity information while DINO-based LA representations carry relative-motion information, target choice can be informed by what the task demands.

My read: the FV gain bundles the future-vision loss together with teacher-forced clean-action conditioning, so a clean-versus-noisy action ablation on FV-routed samples is the decisive experiment for attributing the gain to the target itself.

The budget is measured in sample exposures rather than FLOPs or wall-clock time, which the paper acknowledges; a compute-matched comparison would test whether the allocation result survives a stricter resource definition.

The setting-dependence of the best routing probability suggests a next step the paper does not take: making the router adaptive, so the action share is learned per sample, per task, or per training stage instead of being fixed in advance.

The relative-motion versus absolute-position readouts imply a testable task-selection rule: manipulation tasks that punish position error may favor FV-style targets, while tasks requiring the policy to discriminate between similar motions may favor DINO-based LA targets.

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The paper

Abstract

Vision-language-action (VLA) policies are typically trained with action prediction as the primary supervision signal, since robots ultimately execute actions. Auxiliary objectives such as latent-action (LA) and future-vision (FV) prediction are often added to improve policy learning, yet they compete with action prediction for the same training budget. We ask whether, under a fixed budget, allocating a substantial share of training samples to such objectives, rather than to further action prediction, can improve policy learning. We build a unified VLA framework that couples a two-stream multimodal diffusion transformer (MMDiT) with a sample-level router, which assigns each training sample to either action prediction or an auxiliary objective and thus makes supervision allocation explicit. Within this framework, we instantiate three LA targets based on LAPA and its DINO-feature variants, and three FV targets based on DINOv3, V-JEPA 2, and Wan2.2 representations. Across LIBERO, CALVIN, and four real-robot tasks, suitable LA and FV supervision outperforms action-only training under the same budget, even when action prediction receives no more than half of the training samples. FV generally outperforms LA, although the strongest LA target remains competitive on CALVIN. Diagnostic analyses suggest that DINO-based LA targets emphasize relative motion, whereas FV targets emphasize absolute position and task identity. We therefore argue that what robot policies learn to predict, and how training is allocated among these targets, should be treated as explicit design choices rather than defaulting to action-dominant training.

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abstract compiled · 2026-10-16

The authors' main claim, as the classifier picked it out 0.81

“We therefore argue that what robot policies learn to predict, and how training is allocated among these targets, should be treated as explicit design choices rather than defaulting to action-dominant training.”

How the main claim is stated: asserted 0.84

What the abstract itself states, as probabilities: claims first 0.05 · states limitation 0.26 · human participants 0.08 · controlled comparison 0.94 · randomized assignment 0.03 · states quantitative result 0.65 · compares with prior results 0.91 · mentions code or data availability 0.03

The abstract, sentence by sentence

This table labels the abstract only (arXiv listing abstract v1). The number is the probability the classifier gave the label.

SentenceRoleThe authors' own workStates the main conclusionStrength
Vision-language-action (VLA) policies are typically trained with action prediction as the primary supervision signal, since robots ultimately execute actions. background 1.00 0.04 0.02 asserted 1.00
Auxiliary objectives such as latent-action (LA) and future-vision (FV) prediction are often added to improve policy learning, yet they compete with action prediction for the same training budget. background 0.94 0.06 0.02 asserted 0.97
We ask whether, under a fixed budget, allocating a substantial share of training samples to such objectives, rather than to further action prediction, can improve policy learning. gap 0.82 0.12 0.05 hedged possibility 0.52
We build a unified VLA framework that couples a two-stream multimodal diffusion transformer (MMDiT) with a sample-level router, which assigns each training sample to either action prediction or an auxiliary objective and thus makes supervision allocation explicit. method 0.95 0.96 0.05 asserted 1.00
Within this framework, we instantiate three LA targets based on LAPA and its DINO-feature variants, and three FV targets based on DINOv3, V-JEPA 2, and Wan2.2 representations. method 0.98 0.90 0.02 asserted 0.99
Across LIBERO, CALVIN, and four real-robot tasks, suitable LA and FV supervision outperforms action-only training under the same budget, even when action prediction receives no more than half of the training samples. result 1.00 0.96 0.70 asserted 1.00
FV generally outperforms LA, although the strongest LA target remains competitive on CALVIN. result 1.00 0.93 0.11 asserted 0.99
Diagnostic analyses suggest that DINO-based LA targets emphasize relative motion, whereas FV targets emphasize absolute position and task identity. interpretation 0.79 0.91 0.06 hedged possibility 0.98
We therefore argue that what robot policies learn to predict, and how training is allocated among these targets, should be treated as explicit design choices rather than defaulting to action-dominant training. interpretation 0.97 0.24 0.90 asserted 0.84

What kind of paper the classifier reports this is: method or tool 0.72 · evidence from observation or experiment 0.99

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Figures (8)
Figure 1 of the paper
Figure 1. Overview. Left: under a fixed training budget, a router sends each sample to the action loss or one auxiliary loss (LA or FV); Px routes x% of samples to the action loss. Middle: two￾stream VLA; FV prediction conditions on clean demonstrated actions. Right: (1) V-JEPA 2 FV vs. its source-matched P100 control; (2) LA and FV means over three targets each at P50 vs. action-only (Act.), arrows marking unrounded FV−LA (real robot: % of max score); (3) per-map normalized LIBERO attention for action-only, +LA (LAPA-DINOv3), and +FV (V-JEPA 2). learning signals about state changes and task…
Figure 2 of the paper
Figure 2. VLM–MMDiT architecture. Action and auxiliary (LA/FV) experts interact through joint self-attention; sample-level routing selects the active loss. Future observations are used only for auxiliary training. Both ft and ft+δ are continuous visual representations. We use ft as an MMDiT input and construct the FV flow-matching target from ft+δ, with δ = 8 for FV. Detailed input formats and feature dimensions for each encoder are provided in Appendix A.1. For both LA and FV, we refer to the encoder m as the source of the target. 3.2 POLICY ARCHITECTURE AND ROUTING VLM conditioning. We use a
Figure 3 of the paper
Figure 3. Allocation at the full budget. Cells show LIBERO success (%) and CALVIN Avg. Len.; darker is higher within each benchmark. Black outlines mark each model’s best allocation. below its P100 control. The appropriate allocation therefore depends on both the target and the benchmark
Figure 4 of the paper
Figure 4. fixes P50 to examine whether the gains persist across training budgets. On CALVIN, all three FV configurations exceed their source-matched controls in average task-chain length at all four tested budgets. These controls, however, score below the shared action-only baseline at every budget, so gains over that baseline are less consistent: V-JEPA 2 exceeds it at three of the four budgets, and among LA configurations only LAPA-DINOv3 does so, at the full budget. On LIBERO, gains vary with the target and budget and do not occur at every stage. Detailed LIBERO and CALVIN scores are…
Figure 5 of the paper
Figure 5. Full sweep over supervision allocation and training budget. Each curve reports gains over the same-stage P100 control: the shared action-only baseline for LA and the source-matched control for FV. Rows show CALVIN ∆ Avg. Len. and LIBERO ∆ success rate (pp). Dashed zero lines indicate parity with the corresponding control. CALVIN panels share a vertical scale; LIBERO panels use target-specific vertical scales to show each trajectory. 4.3 HOW DO LA AND FV COMPARE ACROSS TRAINING REGIMES AND TASKS? We next compare the complete LA and FV configurations, which differ in target sources…
Figure 6 of the paper
Figure 6. Real-robot evaluation: (a) representative executions; (b) partial-credit scores normalized by 160 points per task (20 trials, up to 8 points each). LA/FV use P50. Protocol: Appendix B.7. position errors than all three LA sources on both datasets, whereas both LAPA-DINO variants yield lower relative-motion errors than all three FV sources at every ∆c setting on unseen AgiBotWorld￾Beta tasks; on CALVIN, the leading encoder changes with c. Plain LAPA, which yields the weakest CALVIN readouts, is also the weakest policy configuration on CALVIN (
Figure 7 of the paper
Figure 7. Frozen-source diagnostics on AgiBotWorld-Beta seen validation. (a) Correlation between net-action-change and representation pair distances, plotted against delta-step5 NMSE. (b) Feature￾cluster NMI with displacement-derived action labels and task IDs. Each point is one encoder; details in Appendix C.2. Finally,
Figure 8 of the paper
Figure 8. Qualitative policy attention on two LIBERO observations, one per row. Columns show the input observation and the action-only, LA, and FV policies. Colors show relative intensity within each map. Both rows use the extraction protocol in Appendix C.3. 5 CONCLUSION Robot policies must execute actions, but this does not require most training samples to supervise di￾rect action prediction. In a unified VLA framework with sample-level routing, suitable LA and FV targets can outperform action-only training under the same budget even when direct action prediction receives no more than half…

Figures are the authors', reproduced from the paper.

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