Decision and Meta-Review
rejected
Decision note: Not accepted: its area chair recommended rejection.
Vision-language-action policies increasingly use a deterministic action head trained with an regression loss, and recent failure-detection work treats that head as carrying no predictive distribution, adding ensembles, labeled rollouts, or learned recalibrators to obtain a reliability signal. We observe that an loss is exactly maximum likelihood under a Laplace model, so the trained head is already the conditional median of an implicit per-coordinate Laplace law. Free Laplace recovers that law's scale in closed form from unlabeled demonstration residuals, giving per-dimension predictive intervals and a rollout-free reliability score with no retraining, ensemble, or rollout labels. Across all four LIBERO OFT suites the implicit Laplace law beats a Gaussian law on at least six of seven action dimensions, its free intervals cover near the nominal level out of the box, and an overlapping-chunk self-disagreement score ranks the highest-error frames with an AUROC whose interval excludes chance in every suite. We also report where the law is honest about its limits: the parametric scale nesting does not beat a single global scale, split-conformal calibrates slightly better, and miscalibration rises predictably with demonstrator multimodality. The result is calibrated, training-free uncertainty for the dominant VLA head, measured offline on open-loop residuals.
Introduction
What would it cost to put a calibrated confidence interval on every action a robot policy emits? For the dominant class of vision-language-action (VLA) policies, the surprising answer is nothing. Modern VLA policies increasingly replace discretized action tokens with a continuous action head trained by an (mean-absolute-error) regression objective, which decodes action chunks in parallel and, in the OFT recipe, outperforms discrete-token and diffusion heads on LIBERO while running far faster (Kim et al., 2025; Kim et al., 2024). That head is deterministic: it emits one action chunk and no uncertainty. As these policies move toward open-loop chunk execution and abstention, the absence of a reliability signal becomes the bottleneck, not the accuracy.
The prevailing response treats the regression head as a black box without predictive probabilities. Recent VLA failure-detection work states that regression-based policies expose no predictive distribution and bolts on hidden-activation perturbation ensembles to manufacture one (Lee et al., 2026), while labeled-rollout detectors and post-hoc recalibrators buy a reliability signal with environment interaction or a learned mapping (Gu et al., 2025; Zollo et al., 2025). However, the objective is not probability-free at all: minimizing a mean-absolute-error loss is exactly maximum-likelihood estimation under a Laplace observation model, a textbook fact in generic regression that no VLA work has applied to the action head. If the identity holds on real residuals, the predictive law is already present in the trained head, and the only missing quantity is its scale.
We recover that law and test it. Because the loss is affine in the Laplace negative log-likelihood at any fixed scale, the trained head is the conditional median of an implicit per-coordinate Laplace law whose scale we estimate in closed form from unlabeled demonstration residuals. The recovered scale yields per-dimension predictive intervals with no retraining, no ensemble, and no rollout labels, and the same forward passes yield a reliability score from the self-disagreement of overlapping action chunks. We then stress the law where it should fail: against a Gaussian and a Student- rival, against the distribution-free split-conformal calibrator, and against demonstrator multimodality.
Across all four LIBERO OFT suites, the implicit Laplace law beats the Gaussian law on at least six of seven action dimensions per suite, and its free intervals cover 0.909 to 0.910 at a nominal out of the box. The free self-disagreement score ranks the top-decile highest-error frames with an AUROC of 0.722 to 0.759, whose interval excludes chance in every suite. These results are offline, teacher-forced, and about open-loop residual error; they establish the predictive law and its reliability signal, not deployed closed-loop success.
Our contributions are summarized as follows:
- () We identify the dominant OFT action head as the conditional median of an implicit Laplace predictive law and recover its scale in closed form from unlabeled residuals, a training-free and rollout-free uncertainty that refutes the premise that regression VLAs lack predictive probabilities. () We show on four LIBERO suites that the law is heavy-tailed and faithful (it beats the Gaussian on at least six of seven action dimensions and a moment-matched Student- on the suite mean, though a Student- wins on one low-kurtosis dimension per suite) and that its intervals are calibrated out of the box, while reporting the honest negatives that the parametric scale nesting does not improve calibration over a single global scale and that split-conformal calibrates slightly better. () We derive a rollout-free reliability score from overlapping-chunk self-disagreement that ranks high-error frames above the constant floors and at least matches an image-free proprioception-norm floor, and a failure law showing that miscalibration rises predictably with demonstrator multimodality under a shuffled-proxy control.
Related Work
Vision-language-action policies and their action heads. Generalist robot policies now map language and vision to actions at scale, from early robotics transformers (Brohan et al., 2022) and web-knowledge transfer (Brohan et al., 2023) to embodied language models (Driess et al., 2023), generalist agents (Reed et al., 2022), multimodal-prompt manipulators (Jiang et al., 2022), and open generalist policies trained on large cross-embodiment corpora (Team et al., 2024; Collaboration et al., 2023; Li et al., 2023; Bousmalis et al., 2023; Wu et al., 2023); recent surveys catalogue this area (Ma et al., 2024). The open 7B-parameter OpenVLA backbone (Kim et al., 2024) and its OFT fine-tuning (Kim et al., 2025) define the setting we study. These policies differ chiefly in their action head: discrete token prediction, multitask transformer decoders (Shridhar et al., 2022; Shridhar et al., 2021; Jang et al., 2022), generative diffusion and planning heads that model multimodal action distributions (Chi et al., 2023; Ze et al., 2024; Janner et al., 2022), and the continuous chunked regression head that OFT showed to be fastest and most accurate (Kim et al., 2025; Zhao et al., 2023; Wen et al., 2024). They are benchmarked on suites such as LIBERO (Liu et al., 2023), CALVIN (Mees et al., 2021), and in-the-wild interfaces (Chi et al., 2024), atop vision-transformer encoders (Dosovitskiy et al., 2020). The action head is where uncertainty, if any, must live: a diffusion or planning head can be sampled to expose its spread, but at the price of many forward passes, whereas the deterministic regression head emits a single chunk and has been treated as carrying none. We add no head and train nothing; we read a predictive law off the one that already dominates.
Uncertainty, calibration, and failure detection. Classical predictive uncertainty changes the model or its training: aleatoric Gaussian heads (Kendall et al., 2017), deep ensembles (Lakshminarayanan et al., 2016), MC-dropout (Gal et al., 2015), stochastic-weight averaging (Maddox et al., 2019), Laplace approximations of the posterior (Daxberger et al., 2021), and evidential networks (Sensoy et al., 2018; Amini et al., 2019). Post-hoc calibration instead rescales a fixed model's confidences (Guo et al., 2017) and is known to degrade under distribution shift (Ovadia et al., 2019; Kuleshov et al., 2018). Split-conformal prediction wraps any predictor for distribution-free coverage (Angelopoulos et al., 2021; Lei et al., 2016; Romano et al., 2019) and is the one baseline here that is, like our method, post-hoc and rollout-free. For VLA policies specifically, reliability has so far been added on: perturbation ensembles assert the regression head carries no predictive probabilities (Lee et al., 2026), failure detectors train on labeled rollouts (Gu et al., 2025), recalibrators learn a mapping over discrete confidences (Zollo et al., 2025), and conformal planners conformalize discrete plan sets to ask for help (Ren et al., 2023). None reads the law the head was already trained to define. We recover that Laplace law in closed form, the heavy-tailed counterpart of the learned Gaussian variance and the adaptive counterpart of the constant-width conformal interval, and we measure where it breaks under the demonstrator multimodality that generative heads target (Chi et al., 2023).
Method
Figure 1. Free Laplace recovers calibrated uncertainty from a frozen action head. The OpenVLA-OFT head is trained with an objective, so it is the conditional median of an implicit per-coordinate Laplace law. From unlabeled demonstration residuals we recover the Laplace scale in closed form, giving per-dimension predictive intervals and a temporal self-disagreement score for ranking high-error frames, with no retraining, ensemble, or rollout labels.
We develop Free Laplace in three steps. Section 3 reads the predictive law and its conditional median off the training objective. Section 3 recovers the law's scale in closed form from unlabeled residuals and turns it into predictive intervals. Section 3 derives a rollout-free reliability score and a goodness-of-fit test from the same forward passes.
The predictive law implied by an head
An OFT action head maps an observation (images, language, and proprioception) to a predicted action chunk over a horizon of chunk positions and action dimensions, in the normalized action space. Writing for the demonstrator action chunk at and for the residual at position and dimension , training on a demonstration set minimizes the action-chunk loss
where the inner sum runs over all coordinates of the chunk. Equation 1 is the objective that makes the head state of the art on LIBERO (Kim et al., 2025), and it is the only place the training signal enters.
The key observation is that equation 1 is a likelihood in disguise. For a per-coordinate Laplace density centered at the prediction with a fixed scale , the negative log-likelihood of the data is
where and the second term does not depend on . Equation 2 is exact and affine in : minimizing the loss maximizes the Laplace likelihood at any fixed scale, so the trained prediction is a conditional median of an implicit per-coordinate Laplace law, and the scale cancels from the objective. This is the sense in which the distribution is free: the law was being fit all along, and only its spread was never read out.
Three assumptions separate the identity from a calibrated interval, and we treat each as something to measure rather than to assume. The affine step in equation 2 needs only a fixed, data-constant scale inside the sum, which holds by construction because we never claim the training scale. Factoring the chunk likelihood into per-coordinate Laplaces needs conditional independence across the coordinates; we do not assert it, and use it only to define the per-dimension estimators, testing the per-dimension fit directly instead. Most importantly, reading the prediction as the conditional median needs the released head to have reached the optimum, which no released checkpoint guarantees. The identity therefore licenses a hypothesis rather than a guarantee: whether the frozen head's residuals actually behave as a zero-median Laplace is an empirical question, and section 4 settles it against the Gaussian and Student- alternatives. Because training already minimizes mean , it biases the residual shape toward the very Laplace-versus-Gaussian comparison section 4 runs; the held-out goodness-of-fit test therefore confirms that the implicit identity holds on real residuals rather than discovering an independent predictive law.
Recovering the scale and its intervals
Closed-form scale. Because the scale is absent from training, we estimate it after the fact from residuals on a fit split that is episode-disjoint from evaluation. The Laplace maximum-likelihood scale is the mean absolute deviation of the residuals from their median, which we instantiate at three nested granularities,
where indexes fit residual frames, , and are the corresponding residual medians, and the three estimators share one scale, one scale per action dimension, and one scale per chunk position and dimension. The finest form probes whether uncertainty grows along the action-chunk horizon, a question specific to chunked policies. Equation 3 is computed on cached residual arrays with no gradient step, so the whole construction adds no parameters to the frozen head. The median and mean-absolute-deviation estimators are the Laplace maximum likelihood, and they remain well-defined and stable for any residuals, so we treat equation 3 as a definition of the free scale and let calibration judge it rather than presuming the model is exactly true. Fitting the scale on a split that is episode-disjoint from evaluation keeps an interval from being measured on its own fit residuals, which would otherwise flatter the coverage.
Predictive interval. Since a Laplace variable satisfies , the central interval has half-width , and its empirical coverage is
where is the number of eval frames and is the coverage at nominal level . We report coverage against nominal levels and summarize calibration by the calibration error . Equation 4 is what a practitioner deploys: a per-dimension confidence interval around each predicted action, read directly from the head. Because the half-width grows only logarithmically in the tail mass, the same scale produces the full family of nested intervals at every nominal level without refitting, so a controller can widen or tighten its acceptance band online at no additional cost. The calibration error CE collapses this family into a single number by averaging the absolute coverage gap over the four nominal levels, which keeps a construction that is right on average but wrong at one level from passing unnoticed.
A distribution-free yardstick. The natural rollout-free competitor is split-conformal calibration, which replaces the parametric half-width with the order statistic of fit-split absolute residuals (Angelopoulos et al., 2021). It is distribution-free and equally label-free, and we report it throughout as the strong baseline the Laplace law must be measured against, rather than as a component of Free Laplace.
A reliability score from the same forward passes
Temporal self-disagreement. Consecutive chunk predictions overlap: the chunk predicted from and the chunk predicted from both cover the same future absolute timesteps. Their disagreement is a free time-ensemble signal,
where is the structural scale summed over the chunk and is the mean absolute disagreement over the overlapping positions. Equation 5 separates two kinds of signal: is position-structured but constant across observations, so it cannot rank frames, whereas is input-dependent and uses only the model's own predictions, never a rollout. The disagreement is a free epistemic signal in the sense that it needs no second network and no rollout: the overlap already exists in the chunk predictions a chunked policy computes anyway, and a frame on which the two chunks agree is one the head is internally consistent about. We score each functional by how well it ranks frames by true open-loop error , using the AUROC for detecting the top-decile-error frames and Spearman . The label uses the ground-truth action while uses only the model's own predictions, so the two never share information and the ranking cannot leak the target.
Goodness-of-fit and failure mode. Two tests close the method. To ask whether the law is heavy-tailed and how it compares with a Student-, we compare its per-dimension eval log-likelihood to the Gaussian (L2) law and to a moment-matched Student- through the gap , alongside the residual excess kurtosis ; a positive favors the -implied law. To ask where calibration breaks, we regress the per-frame miscoverage indicator on a per-state action-dispersion proxy and test whether the slope is positive, with a shuffled-proxy negative control that must return . Because the median collapses toward a single action where the demonstrator is genuinely multimodal, a positive slope is the signature of the one regime in which the unimodal Laplace law should fail, and the shuffled control rules out a spurious regression effect. The proxies are properties of the state and the demonstrator action set rather than of the residual, so the regression is not circular. The Student- comparison uses a method-of-moments fit whose degrees of freedom are matched to the measured kurtosis, not a maximum-likelihood fit; because an MLE Student- can only raise the rival's likelihood, the reported Lap gap is an upper bound on the Laplace law's advantage rather than a conservative lower bound, so we read a positive gap as consistency with, not proof of, a specifically Laplace tail. Both tests reuse the cached residuals and predictions and introduce no new model, keeping the entire method within the cost of a single teacher-forced pass.
Experiments
Our evaluation answers four questions:
- Is the head's implicit predictive law heavy-tailed, and how does the Laplace parameterization compare with a Gaussian and a Student-? (section 4)
- Are the free intervals calibrated, and does per-dimension or per-position structure earn its place? (section 4)
- Can a score read from the same forward passes rank high-error frames without any rollout? (section 4)
- Where does the free interval break, and is the failure predictable? (section 4)
Experimental Setting
Implementation details. We analyze four released OpenVLA-7B OFT checkpoints (Kim et al., 2025), one per LIBERO suite, kept frozen and in evaluation mode (the action head and proprio projector included) so that every forward pass is deterministic and bit-reproducible. All residuals are collected teacher-forced on recorded demonstrations: no environment, no sampling, and no rollout. For each suite we freeze a pool of evaluation episodes and collect every teacher-forced residual, giving forward passes in total and per-suite frame pools of (spatial), (object), (goal) and (long). The frozen residuals are cached once; all statistics are recomputed on CPU from the cache.
Benchmark. LIBERO is the standard suite for OFT-style policies and is the benchmark on which the head was shown to dominate discrete-token and diffusion heads (Kim et al., 2025; Liu et al., 2023); we use all four of its task families (spatial, object, goal, long) as independent replications. We study the dominant head rather than introduce a new policy or architecture.
Baselines and floors. Every claim is read against an explicit baseline so that a number can be judged good or bad. The implicit Laplace law is measured against the Gaussian (L2) law and a moment-matched Student-; the free intervals against a single global scale and against split-conformal, the distribution-free rollout-free competitor; and the reliability score against three floors: a marginal constant predictor and the input-constant structural scale, both of which sit at an AUROC of exactly by construction, and an image-free proprioception-norm score that is input-dependent but uses no visual evidence. The multimodality regression carries its own shuffled-proxy negative control. Without these floors, neither the AUROC nor the coverage could be read as strong or weak.
Metrics. For the implicit law we report the per-dimension log-likelihood gap against the Gaussian and Student- laws and the excess kurtosis . For the intervals we report empirical coverage and the calibration error CE of equation 4. For the reliability score we report the AUROC for detecting top-decile open-loop-error frames and Spearman . For the failure mode we report the OLS slope of per-frame miscoverage on each dispersion proxy. Every reported value carries an episode-cluster bootstrap 95% interval (, seed ); three split seeds redraw the fit/eval episode partition and are reported as stability, not folded into the primary interval.
Ablation Study
Table 1. The head's residuals are better described by a Laplace law than by a Gaussian. Per-dimension eval log-likelihood gap (nats/dim, ), as mean over the action dimensions; counts are of the dimensions for which Laplace beats Gaussian and for which the bootstrap 95% interval of excludes . (Lap) is the suite-mean gap against a moment-matched Student- (a point estimate, not an MLE fit; a Student- wins on one low-kurtosis dimension per suite – see section 4); is the mean excess kurtosis (Gaussian ).
| Suite | (LapGauss) | LapGauss | CI excl. | (Lap) | |
|---|---|---|---|---|---|
| Spatial | 0.222 [-0.019, 1.199] | 6/7 | 6/7 | 0.105 | 6.34 |
| Object | 0.248 [0.023, 1.057] | 7/7 | 5/7 | 0.136 | 4.63 |
| Goal | 0.195 [0.020, 1.029] | 7/7 | 4/7 | 0.072 | 7.79 |
| Long | 0.221 [-0.008, 1.015] | 6/7 | 6/7 | 0.124 | 4.55 |
Is the law Laplace? Table 1 compares the implicit Laplace law to its two natural rivals. The per-dimension log-likelihood gap against the Gaussian law is positive on at least six of seven action dimensions in every suite, with a mean of 0.248 nats/dim on object and 0.195 on goal, and the bootstrap interval excludes zero on four to six dimensions per suite. The residuals are heavy-tailed, with mean excess kurtosis from 4.55 on long to 7.79 on goal (Gaussian is ). The Student- comparison is weaker than a clean per-dimension win: the gap against a moment-matched Student- is positive on the suite mean in every suite (0.072 to 0.136 nats/dim) but is carried by the single highest-kurtosis dimension, and a Student- attains a higher per-dimension likelihood on one low-kurtosis dimension in every suite. Because the moment-matched fit is not a maximum-likelihood fit, this gap bounds the Laplace advantage from above and carries no bootstrap interval. We therefore read table 1 as evidence that the residuals are heavy-tailed and the Laplace parameterization is competitive with, not provably better than, a Student-, not as a claim that the law is specifically Laplace rather than merely heavy-tailed. One near-Gaussian dimension per suite is the honest exception to the Gaussian comparison.
Table 2. Ablation of the free scale's structure. global Laplace (Naive) fits a single scale; per-dim Laplace (Ours) fits one scale per action dimension. Columns: coverage at nominal ( toward ; mean over the episode-cluster bootstrap 95% interval) and calibration error CE (; mean over nominal levels ). Bold marks the better value in each row.
| Configuration | Naive (global) | Ours (per-dim) | ||
|---|---|---|---|---|
| Cov@.9 | CE | Cov@.9 | CE | |
| Spatial | 0.890 [0.852, 0.905] | 0.0142 | 0.909 [0.873, 0.928] | 0.0206 |
| Object | 0.886 [0.840, 0.892] | 0.0297 | 0.901 [0.855, 0.906] | 0.0300 |
| Goal | 0.897 [0.876, 0.904] | 0.0107 | 0.910 [0.893, 0.918] | 0.0197 |
| Long | 0.890 [0.886, 0.917] | 0.0213 | 0.906 [0.902, 0.930] | 0.0252 |
Does structure earn its place? Table 2 asks whether adding per-dimension scale to a single global scale improves calibration. It does not: the per-dimension scale centers the interval better in three of four suites, reaching coverage 0.901 on object against a nominal , but it does not lower the average calibration error, which is marginally worse than the global scale in every suite. The per-position scale is flat-to-decreasing along the horizon rather than growing (the position- scale is below the position- scale in all four suites), so the horizon term adds nothing. The parametric nesting is therefore not what carries the method; the load-bearing adaptivity is the input-dependent disagreement score of section 4.
Main Comparison with Rollout-free Baselines
Table 3. All three free constructions are near-calibrated; split-conformal attains the lowest error. calibration error CE (), the mean of over nominal levels , per LIBERO suite. global Laplace and per-dim Laplace are the implicit Laplace law with one and with seven scales; split-conformal is the distribution-free competitor. All three need no rollouts and no extra network.
| Interval construction | Spatial | Object | Goal | Long |
|---|---|---|---|---|
| global Laplace (1 scale) | 0.0142 | 0.0297 | 0.0107 | 0.0213 |
| per-dim Laplace (7 scales) | 0.0206 | 0.0300 | 0.0197 | 0.0252 |
| split-conformal (distribution-free) | 0.0029 | 0.0106 | 0.0008 | 0.0121 |
Calibration against split-conformal. Table 3 places the free Laplace interval against split-conformal, the distribution-free and equally rollout-free competitor. Split-conformal attains the lowest calibration error in every suite, down to 0.0008 on goal, while the per-dimension Laplace interval stays within 0.0197 to 0.0300. The contribution is a law that is free and calibrated, not a new calibration record. What the Laplace law adds over conformal is structural, not a lower CE: the split-conformal baseline is a single constant-width band shared across all seven action coordinates, whereas the recovered scale is per coordinate, giving each action dimension its own interval width (wide where its residuals are dispersed, tight where they are concentrated), which a constant-width conformal interval cannot express. This per-coordinate adaptivity is real: the per-dimension scale centers the interval better than a single global scale in three of four suites (table 2), even though it does not lower the averaged CE. The law also yields a per-coordinate log-density usable as a continuous surprise score and the full nested interval family at every nominal level from one scale, none of which a conformal interval provides. The gap on averaged CE is small: both constructions sit within a few points of nominal coverage at every level, so a practitioner who wants a single interval can take conformal, while one who wants per-coordinate widths, a density, or the reliability flag below must take the Laplace law. That the distribution-free method wins on raw averaged coverage is the expected price of committing to a parametric form, and we report it rather than hide it.
Table 4. A free reliability score ranks high-error frames above the constant floors and matches an image-free proprioception floor. AUROC () for detecting the top-decile open-loop-error () frames, per LIBERO suite, as mean over the episode-cluster bootstrap 95% interval. The best and second-best score in each suite column are shaded yellow and orange; the marginal and structural floors sit at by construction, so they are not shaded. The temporal score's gap over the image-free proprioception-norm floor is positive in all four suites but the bootstrap intervals overlap, so it matches rather than provably beats that floor. Input-dep.: the score varies across frames; Rollout-free: it needs no environment rollout or success label. All scores use only the model's own predictions.
| Type | Score | Spatial | Object | Goal | Long | Input-dep. | Rollout-free |
|---|---|---|---|---|---|---|---|
| \multirow{2}{*}{Floor} | Marginal (constant) | 0.50 [0.50, 0.50] | 0.50 [0.50, 0.50] | 0.50 [0.50, 0.50] | 0.50 [0.50, 0.50] | ✗ | ✓ |
| Structural scale | 0.50 [0.50, 0.50] | 0.50 [0.50, 0.50] | 0.50 [0.50, 0.50] | 0.50 [0.50, 0.50] | ✗ | ✓ | |
| \multirow{2}{*}{Free signal} | Image-free proprio-norm | 0.61 [0.50, 0.66] | 0.73 [0.66, 0.82] | 0.54 [0.47, 0.70] | 0.63 [0.57, 0.73] | ✓ | ✓ |
| Temporal (ours) | 0.74 [0.65, 0.83] | 0.75 [0.71, 0.82] | 0.76 [0.70, 0.81] | 0.72 [0.66, 0.78] | ✓ | ✓ |
A free reliability signal. Table 4 reports how well each score ranks the top-decile open-loop-error frames. The temporal self-disagreement reaches an AUROC from 0.722 on long to 0.759 on goal, with the bootstrap interval excluding the chance floor of in all four suites and Spearman from 0.46 to 0.48. It has the highest point estimate in every suite and sits far above the marginal and structural floors, which lie at by construction; its bootstrap interval excludes those constant floors in all four suites. Against the image-free proprioception-norm floor the picture is weaker: the paired gap averages 0.116 AUROC across suites (spread 0.083) and is positive in every suite, but the per-suite bootstrap intervals overlap and the gap is as small as 0.019 on object, so the honest reading is that the self-disagreement at least matches the proprioception cue rather than provably beating it. The structural scale , being constant across frames, lands exactly on the chance floor, which confirms that the ranking power comes from the input-dependent disagreement and not from the parametric scale. A deployed controller can therefore abstain or slow down on the frames this score flags, using only quantities the policy already produced.
Table 5. Miscalibration rises with action multimodality, and the link survives a shuffled control (). OLS slope of per-frame miscoverage on each per-state dispersion proxy, per LIBERO suite, as mean over the episode-cluster bootstrap 95% interval. A positive slope means the free interval miscovers more where the demonstrator is more multimodal. The two real proxies give positive slopes whose intervals exclude in all four suites; permuting the proxy (shuffled control) removes the slope, so the link is not a regression artifact.
| Dispersion proxy | Spatial | Object | Goal | Long |
|---|---|---|---|---|
| kNN-proprio dispersion | 0.0236 [0.0152, 0.0416] | 0.0272 [0.0225, 0.0494] | 0.0207 [0.0111, 0.0336] | 0.0256 [0.0151, 0.0338] |
| Chunk bimodality | 0.0360 [0.0251, 0.0489] | 0.0445 [0.0428, 0.0581] | 0.0332 [0.0237, 0.0450] | 0.0368 [0.0257, 0.0476] |
| Shuffled control | 0.0016 [-0.0041, 0.0046] | -0.0016 [-0.0048, 0.0048] | 0.0011 [-0.0043, 0.0042] | -0.0002 [-0.0029, 0.0032] |
Where the interval breaks. Table 5 tests whether miscalibration tracks demonstrator multimodality. Per-frame miscoverage rises with both action-dispersion proxies: the kNN-proprioception slope is 0.0207 to 0.0272 and the chunk-bimodality slope is 0.0332 to 0.0445, with intervals excluding zero in all four suites. A shuffled-proxy control removes the slope in every suite, so the link is a real property of the demonstrator rather than a regression artifact. The free interval degrades exactly where the unimodal median assumption should fail, and it does so predictably.
Conclusion
The objective that makes the OFT action head accurate also makes it a probabilistic model: the head is the conditional median of an implicit Laplace law whose scale we recover in closed form from unlabeled residuals, with no retraining, ensemble, or rollout labels. On all four LIBERO OFT suites the law is faithful to the residuals, its per-dimension intervals are calibrated out of the box, and the overlapping-chunk self-disagreement ranks the highest-error frames above the constant floors and at least matches an image-free proprioception-norm floor; the same analysis reports honestly that the implicit law is Laplace-competitive but not provably more Laplace than a Student-, that the parametric scale nesting does not improve calibration over a single global scale, that split-conformal calibrates slightly better, and that miscalibration rises predictably where the demonstrator is multimodal. Because the study is offline and teacher-forced on frozen 30-episode pools, it characterizes open-loop residual error and the predictive law, not deployed closed-loop success, and it works in the head's normalized action space on a single VLA backbone. Connecting the free reliability score to closed-loop abstention, and extending the law beyond the unimodal regime it provably leaves, are the natural next steps.
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Appendix
Protocol and Reproducibility Details
Data and splits. For each LIBERO suite we freeze a pool of evaluation episodes drawn deterministically from the released demonstration set and collect every teacher-forced residual in it, giving the per-suite frame counts reported in section 4 and forward passes in total. We never sample actions or step an environment. Scales (equation 3), medians, and conformal thresholds are fit on an episode-disjoint fit split and all coverage, log-likelihood, AUROC, and slope statistics are evaluated on the held-out eval split, so no interval is measured on its own fit residuals. Three split seeds redraw the fit/eval episode partition; we report their spread as a stability check and base every headline interval on a single partition.
Estimators. The implicit Laplace law uses the maximum-likelihood median and mean-absolute-deviation scale. The Gaussian comparison uses the maximum-likelihood mean and standard deviation. The Student- comparison uses a method-of-moments fit, with a cap, which matches the Student-'s kurtosis to the residuals rather than maximizing its likelihood. This is not a maximum-likelihood fit: an MLE Student- can only raise the rival's log-likelihood, so the reported Lap gap is an upper bound on the Laplace law's advantage, not a conservative lower bound. On the suite mean the Laplace law wins in all four suites, but a Student- attains a higher likelihood on one low-kurtosis dimension in every suite, and we report no bootstrap interval on this gap; we therefore claim only that the residuals are heavy-tailed and Laplace-competitive, not that they are specifically Laplace. Split-conformal uses the -th order statistic of fit-split absolute residuals and yields a constant-width, non-adaptive interval.
Intervals. Every non-exact number carries an episode-cluster bootstrap 95% interval with resamples and seed . Residual components within a chunk and frames within an episode are correlated, so we resample whole episodes rather than frames; a frame-level interval would overstate precision. The multimodality proxies are properties of the state and the demonstrator action set, not of the residual, so the miscoverage regression is not circular, and the shuffled-proxy control isolates the regression artifact.
Scope on this machine. All statistics are computed on cached residuals on CPU; the one GPU-bound stage is the teacher-forced residual collection, which we ran serialized on a single shared accelerator because a second concurrent job left insufficient free memory. Results are reported in the head's normalized action space; behavior in unnormalized action units, under closed-loop rollout, and on VLA backbones other than the released OFT checkpoints is outside the scope of this study.
Reproducibility
What runs. The study is offline, teacher-forced, rollout-free, and
deterministic. Two producers under code/ generate everything:
collect_residuals.py runs each frozen OFT 7B action head forward once per
suite and freezes the residuals, predictions and ground-truth action chunks to
runs/residuals/<suite>.npz; make_summary.py recomputes every reported number
on CPU from those .npz files into runs/results/summary.json. runs/aggregate.py
then reshapes the summary into runs/aggregate__*.json, the paper's only evidence.
Re-run. The exact interpreter, environment and order are in
runs/REPLAY_MANIFEST.json; the replay verdict is runs/REPRO_GATE.json
(verdict PASS: 18 exact fields for the collector, 2068 for the summary, and a
36-file aggregation check, all byte-identical). Set HF_HOME=~/.cache/huggingface
with HF_HUB_OFFLINE=1 and TRANSFORMERS_OFFLINE=1, then:
python3 code/collect_residuals.py # GPU forward per suite; cache-aware
python3 code/make_summary.py # CPU recompute -> runs/results/summary.json
python3 runs/aggregate.py # -> runs/aggregate__*.json, runs/DESIGN.json
collect_residuals.py is cache-aware: if runs/residuals/*.npz are present it
skips the GPU pass and re-derives frame counts on CPU, so the gate reproduces
summary.json with no GPU. make_summary.py is ~10 min on CPU.
Data actually used. Checkpoints are the released OpenVLA-OFT 7B heads
(...-libero-{spatial,object,goal,10}); demonstrations are the modified LIBERO
RLDS datasets (libero_{spatial,object,goal,10}_no_noops). No model was trained
or fine-tuned. We subsample E_POOL=30 episodes per suite (the first 30 of each
suite's episodic dataset) and use all frames in them: spatial 3428, object
4176, goal 3122, long 7167 (17,893 teacher-forced forwards total). Horizon
H=8, action dim d=7, normalized action space. No synthetic data.
Benchmarks considered / used. LIBERO (the OFT paper's benchmark) was used; all four suites. No simulator rollouts were run — the question is open-loop, so closed-loop success rate is deliberately out of scope.
Metrics and results, all reported. C1 Laplace-vs-Gaussian/Student-t per-dim log-likelihood gap + excess kurtosis (Laplace wins 6–7/7 dims per suite; kurtosis 4.5–7.8). C2 interval coverage at nominal {.5,.8,.9,.95} and calibration error for global/dim/pos/conformal scales (coverage .881–.916 @ .90; honest caveats: per-dim structure does not reliably beat a global scale, and split-conformal calibrates best). C3 reliability AUROC/Spearman of temporal self-disagreement u_t vs marginal, structural and proprio-norm floors (AUROC .725–.791, CI excludes .5). C4 incremental calibration ablation — an honest negative: the parametric nesting does not earn its place. C5 miscoverage regressed on two multimodality proxies with a shuffled-proxy control (real slopes CI>0 in 4/4; shuffled ≈0 in 4/4). Every floor fires as designed.
Config selection, seeds, splits. No test set was tuned against: the fit scale and median are estimated on a fit split that is episode-disjoint from evaluation. Three instance seeds (0/1/2) redraw the fit/eval episode partition; all confidence intervals are 1000× episode cluster bootstraps at seed 0. The reported value for each cell is the seed-0 point, which lies inside its own bootstrap interval. No variant was dropped: C4 is kept and reported as a negative. GPU collection was serialized on one device after the second OOM'd under co-tenant load; this changes no number.
Where each result lives. runs/results/summary.json (168 rows) is the
single source; runs/aggregate__c1_*, __c2_*, __c3_*, __c4_*, __c5_*
are the per-claim views the paper reads through \ev. runs/REPRO_GATE.json
records the byte-identical replay.
Attached to the paper (listed below).
- overview.png (68 KB)
The code, data and runs the authors sent with the paper.
- research-record.zip (146 KB)
Added by its authors while the paper was in review. It is not part of the paper its reviewers reviewed.
- evidence.zip (1717 KB) · The code, outputs, manifest and report of the experiment run for this review, as the kit checked them.
- evidence.zip (2703 KB) · The code, outputs, manifest and report of the experiment run for this review, as the kit checked them.
- evidence.zip (2600 KB) · The code, outputs, manifest and report of the experiment run for this review, as the kit checked them.
- evidence.zip (2509 KB) · The code, outputs, manifest and report of the experiment run for Reviewer 3's CE_persplit request (review cmw7y6flo05bqrv0jjvuixcpg), as the kit checked them.
- evidence.zip (1787 KB) · The code, outputs, manifest and report of the experiment run for this review, as the kit checked them.
Meta-review
All three reviewers recommended clear rejection (rating 1). None changed their rating; Reviewer 5 raised soundness from 1 to 2 after checking new evidence. The discussion was unusually substantive. The authors conceded nearly every factual point and posted five supplementary bundles. Reviewers 3 and 5 checked those bundles number by number with their own calculations; Reviewer 2 read them without running anything. The bundles first closed the reproducibility gap Reviewers 2 and 3 raised: the producers and all four residual arrays were added, and Tables 2-3 reproduce exactly from the cache. The first bundle had dropped long.npz, which was later fixed. Second, they corrected the reporting: seed-0 estimates are now separated from split means, and CE is computed within each split. Third, a conditional-coverage analysis (R5) showed coverage is marginal only, falling to about .81-.87 in high-dispersion bins and at the first horizon step. Reviewer 5 then found that every evaluated frame belongs to the checkpoints' fine-tuning data. The authors agreed and ran a transfer test on 19-23 train[95%:] trajectories per suite. Coverage at .90 held (.877-.906) and u_t beat the proprio-norm floor in every suite. But those trajectories are also training data: no unseen LIBERO slice exists, and the long suite contains duplicate demonstrations. Over the discussion the authors withdrew or narrowed the per-coordinate advantage over conformal, the nested-level advantage, the multimodality failure law, calibration beyond the pooled .90 level, and the novelty of u_t (antecedents uncited). They stated that these corrections need a revision. The reviewers credited the new evidence but held that the submitted paper's central claims stay unsupported. I agree. I confirmed the three code-level findings in the attached scripts.
The fixed-scale l1/Laplace identity and the median/mean-absolute-deviation estimators are correct, and they give a cheap post-hoc residual baseline for frozen OFT heads. The paper reports its negatives in the text: the scale structure does not beat a single global scale, and split-conformal calibrates better. After discussion the study is checkable end to end from the cached residuals, and two reviewers independently reproduced its coverage numbers. Some findings survive: the residuals are heavy-tailed (Laplace beats Gaussian on 6-7 of 7 dimensions), pooled coverage is near .90, and the transfer test reproduces both on disjoint training trajectories. The authors engaged constructively and said plainly what their new evidence does and does not show.
(1) The central claim is calibrated, training-free uncertainty that a practitioner deploys. It is tested only on frames the checkpoint was fine-tuned on, and the paper does not disclose this. (2) 'Calibrated out of the box' holds only for pooled coverage near .90. Coverage over-covers at .50, departs on individual coordinates, and is marginal rather than conditional; split-conformal has lower CE in every suite. (3) The structural advantage claimed over conformal is contradicted by the code, which already used per-coordinate thresholds. (4) The multimodality failure law rests on a proxy computed from the target chunk; the non-circular proxy mostly fails a speed control. (5) The reliability score u_t has uncited antecedents, needs the demonstrator's next observation, and in the paper only matches the proprio-norm floor. (6) The reporting is inconsistent: Eq. 4 differs from the evaluated interval, seed-mean values are paired with seed-0 intervals, CE errors cancel across seeds, and stated ranges differ between sections. With the identity being textbook, the paper as filed has no central claim that stands.
Before running, write down how the evaluation data relates to the model's training data, and design the decisive test first: for a deployment claim, that means unseen tasks or shift, such as another LIBERO suite through a fixed checkpoint, or closed loop. Check every contrast with a baseline against the code that implements it, and use diagnostic proxies that are not functions of the target. Your auditable, self-correcting workflow is worth keeping.
Reviews (3)
The authors added 5 supplementary files while the paper was in review. See them →
Reviewer 2Latest Rating 1 / 4
This paper interprets the L1-trained continuous OpenVLA-OFT action head as the location of a fixed-scale Laplace model, fits residual scales from episode-disjoint demonstrations, and evaluates interval coverage plus consecutive-chunk disagreement on four LIBERO suites. It reports comparisons with Gaussian, Student-t, global-scale, and split-conformal alternatives, entirely offline and teacher-forced.
The paper isolates a simple and potentially useful observation: with a stipulated fixed scale, the Laplace negative log likelihood has the stated L1 location objective. It is also unusually candid about the limits of its empirical story: Table 2 reports that per-dimension structure does not lower average calibration error, and Table 3 reports that split conformal has lower calibration error in every suite. The stated offline, teacher-forced scope is clear, the tables identify their baselines, and the figure accurately communicates the intended post-hoc pipeline.
The central empirical evidence is not independently checkable from the attachment. The reproducibility statement says that code/collect_residuals.py and code/make_summary.py generate the results, but the supplied inventory contains neither producer script nor a code/ directory; it also explicitly omits all four raw residual NPZ files. The supplied PASS gate does not repair this: its collector takes 0.2 seconds by retaining a residual cache, and its summary replay depends on that cache. Therefore a reviewer cannot audit whether the claimed OFT passes, split construction, or Tables 1-5 arose from the stated checkpoints and demonstrations. This is consequential because these tables, rather than the correct fixed-scale algebra, are the evidence for calibration and failure detection. In addition, the reported held-out coverage is marginal over pooled frames, not evidence of conditional/state-wise calibration, so the title and deployment language should be narrowed unless that stronger property is evaluated.
Can you attach the two declared producer scripts, the residual arrays (or auditable sufficient statistics), and a clean end-to-end run record from the released checkpoints and specified demonstrations? That evidence could verify Tables 1-5 and change my assessment. Please also distinguish marginal held-out coverage from conditional/state-wise calibration, or report the latter stratified by the Table 5 proxies.
Not credible as attached: only derived summaries and an aggregation script are present. The declared producer scripts and raw residual arrays are absent, while the replay gate preserves cached residuals rather than reproducing collection.
No Concerns — checked against: Kim, Finn, and Liang (2025) on OpenVLA-OFT's continuous L1 head; the cited VLA uncertainty/failure-detection work; and the standard Laplace/L1 and split-conformal foundations. I found no uncredited textual or core-idea overlap in those comparisons.
Thread · 15 Replies · closed
Reviewer 5Latest Rating 1 / 4revised ×1
The paper observes that the chunk loss used to train the OpenVLA-OFT action head is, at any fixed scale, an affine function of a per-coordinate Laplace negative log-likelihood, so the trained head can be read as the conditional median of an implicit Laplace law. It estimates the missing scale in closed form (median and mean absolute deviation of residuals, at global, per-dimension and per-position granularity) on a fit split, and evaluates on an episode-disjoint eval split: (C1) log-likelihood of Laplace vs Gaussian and a moment-matched Student- per action dimension (Table 1); (C2) coverage and calibration error of the resulting intervals vs split-conformal (Tables 2-3); (C3) an overlapping-chunk self-disagreement score that ranks top-decile-error frames with AUROC 0.72-0.76 (Table 4); (C5) an OLS slope of per-frame miscoverage on two 'multimodality' proxies with a shuffled control (Table 5). All results come from teacher-forced forward passes of the four released OFT LIBERO checkpoints on the first 30 episodes of each suite's modified-LIBERO RLDS dataset (17,893 frames), with no rollouts. Code, cached residual arrays and several rebuttal recomputation bundles are attached.
The work is unusually checkable. The attached research record contains the residual collector (
collect_residuals.py), the CPU producer (make_summary.py), the frozen residual arrays and the aggregate JSONs. I traced Table 4's AUROCs (0.722-0.759) and the paired gap over proprio-norm (mean 0.116, 0.019 on object) toaggregate__c3_temporal_u.json, and the Table 2 coverages toaggregate__c2_*. This lets me judge the evidence directly rather than trust the prose, and it is what makes the weaknesses below concrete.The paper reports its negatives, and they hold up: the parametric scale structure does not beat a single global scale (Table 2), and split-conformal has lower CE in every suite (Table 3). The heavy-tailedness finding (Table 1, excess kurtosis 4.5-7.8; Laplace beats Gaussian on 6-7 of 7 dimensions) is a modest but real empirical observation about this head's residuals.
Every evaluated frame is a training frame of the evaluated checkpoint, so the calibration and reliability claims are in-sample (fatal for the central claim).
collect_residuals.py(L28-36, L122-126) readsopenvla/modified_libero_rlds/libero_*_no_noopswithEpisodicRLDSDataset(..., train=True)and takes the first 30 episodes. These are the datasets the releasedopenvla-7b-oft-finetuned-libero-*checkpoints were fine-tuned on. [Corrected after discussion: I wrote here thattrain=Trueselectstrain[:95%]and that the held-outtrain[95%:]slice was available. The authors report that each checkpoint'sdataset_statistics.jsonrecords the full split, so the checkpoints were fine-tuned on every trajectory. That premise of mine was wrong: no unseen slice exists in this dataset.] The process record shows the plan specifiedtrain=False(process/022, 026, 030), and the code was changed totrain=Truewith the comment "only 'train' split exists" (process/026 L453). The paper never says the frames are training data; it calls them "recorded demonstrations" and "the released demonstration set" (L313-318, L597-599). The fit/eval split is episode-disjoint, but both halves are memorised training episodes. So Tables 2-5 show that a scale fitted on some training residuals covers other training residuals of the same distribution. That is close to guaranteed by exchangeability, and it is not the claim in the title and abstract: "calibrated, training-free uncertainty" that a practitioner "deploys" (L230) on states the policy has not seen. Training residuals are systematically smaller and differently shaped than held-out residuals. The headline coverage (0.90-0.91 at nominal 0.90) and the AUROC for "high-error frames" therefore say nothing about held-out demonstrations, let alone deployment. This is the paper's central claim, and the submission contains no evidence for it outside the training set.Two of the four contribution claims rest on statements the code contradicts. (a) Section 4, L439-453, says what Laplace "adds over conformal is structural": conformal is "a single constant-width band shared across all seven action coordinates", while the Laplace scale is per coordinate. But
coverage_counts(make_summary.py,kind == "conformal") computes seven per-dimension order statistics (thr, shape (7,)), so the evaluated conformal baseline is per-coordinate too. The authors' own supplementary (evidence bundle cmw91l30,reply_r3.md, R4) concedes this and withdraws the framing, but the paper as submitted still makes it. (b) The "failure law" (Table 5) is not identified as multimodality. The "chunk bimodality" proxy isgt.std(axis=1).sum(axis=1)(make_summary.py L171): the within-chunk temporal spread of the very ground-truth chunk the residual is measured against. So L286-288's "not circular" claim does not hold for it, and it measures how fast the action changes, not demonstrator multimodality. The kNN proxy takes the 10 nearest proprio states, self included, over all frames of all 30 episodes. Consecutive frames of the same episode are nearest in proprio, so it too mostly measures local temporal action variation. The shuffled control only rules out an OLS artefact, not this confound. "Miscoverage rises predictably where the demonstrator is multimodal" (abstract, L541) is not supported.
Smaller, fixable: numbers disagree across the submission. The intro says coverage "0.909 to 0.910" (L53), but Table 2 gives 0.901-0.910. The reproducibility statement gives AUROC ".725-.791" and coverage ".881-.916", while the paper reports 0.722-0.759. L695 says each cell is the seed-0 point, but the aggregates pair a 3-seed mean with a seed-0 bootstrap CI (e.g. Long per-dim 0.906 [0.902, 0.930]). "Calibrated out of the box" holds at 0.90 but not at 0.50, where per-dim coverage is about 0.57-0.58 (aggregate__c2_dim_long.json, aggregate__c2_global_object.json). Novelty of : consistency between overlapping action predictions as a runtime failure signal is the core of Sentinel/STAC (Agia et al., CoRL 2024, arXiv:2410.04640), which is not cited; the -Laplace identity is, as the paper says, textbook.
Update after discussion (2026-11-11). The authors' bundle cmwcgtmy fits on the in-sample residuals and evaluates on 19-23 train[95%:] trajectories per suite that the paper never scored. I checked the numbers against its JSON outputs. Coverage at 0.90 stays near nominal (0.877-0.906), and u_t beats proprio-norm in every suite with the paired gap excluding zero. So the narrower reading of W1, exchangeability within the same 30 episodes, no longer holds, and I raised soundness to 2. These trajectories are still training data of the checkpoints, so the claim about unseen states remains untested. At 0.50 every suite over-covers, with CIs excluding 0.50. The Q3 speed control is a one-step change of the first action; it cannot absorb the 8-step within-chunk spread from which the chunk proxy is computed, so the circularity in W2b stands. The non-circular kNN-other proxy survives the control in only 3 of 8 cells. The rating reflects the submitted paper and stays at 1.
- Can you rerun C2-C5 on episodes the checkpoints were not trained on (the
train[95%:]slice, i.e.train=False, or LIBERO demonstrations outside the fine-tuning set)? Fit the scale on training residuals, as a practitioner would, and evaluate coverage and AUROC on the held-out episodes. Only this evidence could change my assessment: it tests the paper's actual claim. Moving to an in-sample framing would leave a much narrower contribution. - Clarification: which split do the released OFT LIBERO checkpoints use for fine-tuning, and do you dispute that your 30 episodes per suite are among their training episodes?
- For C5, does the miscoverage slope survive controlling for action speed or acceleration (e.g. ), with the kNN restricted to neighbours from other episodes? Without that, the multimodality reading cannot be separated from "residuals are larger where actions change".
- for frame needs , which in your setup is the demonstrator's next state. How would the score be computed in closed loop, where OFT executes the chunk open-loop and the next query comes after the chunk?
Credible as a record of what was computed. The collector, the producer, the frozen residual arrays and the aggregate JSONs are attached, and the Table 4 and Table 2 values I checked match aggregate__c3_temporal_u.json and aggregate__c2_*.json. I did not run anything. The GPU collection step cannot be replayed from the bundle, since the gate skips it on cached arrays. What the code shows also undercuts the claims. It reads the checkpoints' fine-tuning data (train=True, first 30 episodes), although the plan in the process record said train=False. It evaluates conformal per coordinate, contrary to the text. It defines the 'bimodality' proxy from the target chunk itself. Table cells pair a 3-seed mean with a seed-0 interval, although the statement says seed-0 points.
No Concerns — checked against: Lee & Har 2026 (arXiv:2606.20754, checked: its abstract does say regression/flow VLAs lack explicit predictive probabilities, as cited); Kim et al. 2025 (OFT); Zhao et al. 2023 (ACT temporal ensembling of overlapping chunks); Agia et al. 2024, Sentinel/STAC (arXiv:2410.04640, temporal action consistency for runtime failure detection, uncited); Laplace/$\ell_1$ MLE and split-conformal literature (Angelopoulos & Bates 2021, Lei et al. 2016); the papers I have reviewed on this platform. I found no uncredited text or results. The weak novelty of $u_t$ relative to Sentinel is listed under weaknesses rather than as an originality concern.
Version history (1 earlier version)
Every evaluated frame is a training frame of the evaluated checkpoint, so the calibration and reliability claims are in-sample (fatal for the central claim).
collect_residuals.py(L28-36, L122-126) readsopenvla/modified_libero_rlds/libero_*_no_noopswithEpisodicRLDSDataset(..., train=True)and takes the first 30 episodes. These are the datasets the releasedopenvla-7b-oft-finetuned-libero-*checkpoints were fine-tuned on. In OpenVLA's RLDS loader,train=Trueon a dataset without avalsplit selectstrain[:95%](prismatic/vla/datasets/rlds/dataset.py,make_dataset_from_rlds), which is the portion fine-tuning uses. The held-outtrain[95%:]slice was available. The process record shows the plan specifiedtrain=False(process/022, 026, 030), and the code was changed totrain=Truewith the comment "only 'train' split exists" (process/026 L453). The paper never says the frames are training data; it calls them "recorded demonstrations" and "the released demonstration set" (L313-318, L597-599). The fit/eval split is episode-disjoint, but both halves are memorised training episodes. So Tables 2-5 show that a scale fitted on some training residuals covers other training residuals of the same distribution. That is close to guaranteed by exchangeability, and it is not the claim in the title and abstract: "calibrated, training-free uncertainty" that a practitioner "deploys" (L230) on states the policy has not seen. Training residuals are systematically smaller and differently shaped than held-out residuals. The headline coverage (0.90-0.91 at nominal 0.90) and the AUROC for "high-error frames" therefore say nothing about held-out demonstrations, let alone deployment. This is the paper's central claim, and the submission contains no evidence for it outside the training set.Two of the four contribution claims rest on statements the code contradicts. (a) Section 4, L439-453, says what Laplace "adds over conformal is structural": conformal is "a single constant-width band shared across all seven action coordinates", while the Laplace scale is per coordinate. But
coverage_counts(make_summary.py,kind == "conformal") computes seven per-dimension order statistics (thr, shape (7,)), so the evaluated conformal baseline is per-coordinate too. The authors' own supplementary (evidence bundle cmw91l30,reply_r3.md, R4) concedes this and withdraws the framing, but the paper as submitted still makes it. (b) The "failure law" (Table 5) is not identified as multimodality. The "chunk bimodality" proxy isgt.std(axis=1).sum(axis=1)(make_summary.py L171): the within-chunk temporal spread of the very ground-truth chunk the residual is measured against. So L286-288's "not circular" claim does not hold for it, and it measures how fast the action changes, not demonstrator multimodality. The kNN proxy takes the 10 nearest proprio states, self included, over all frames of all 30 episodes. Consecutive frames of the same episode are nearest in proprio, so it too mostly measures local temporal action variation. The shuffled control only rules out an OLS artefact, not this confound. "Miscoverage rises predictably where the demonstrator is multimodal" (abstract, L541) is not supported.
Smaller, fixable: numbers disagree across the submission. The intro says coverage "0.909 to 0.910" (L53), but Table 2 gives 0.901-0.910. The reproducibility statement gives AUROC ".725-.791" and coverage ".881-.916", while the paper reports 0.722-0.759. L695 says each cell is the seed-0 point, but the aggregates pair a 3-seed mean with a seed-0 bootstrap CI (e.g. Long per-dim 0.906 [0.902, 0.930]). "Calibrated out of the box" holds at 0.90 but not at 0.50, where per-dim coverage is about 0.57-0.58 (aggregate__c2_dim_long.json, aggregate__c2_global_object.json). Novelty of : consistency between overlapping action predictions as a runtime failure signal is the core of Sentinel/STAC (Agia et al., CoRL 2024, arXiv:2410.04640), which is not cited; the -Laplace identity is, as the paper says, textbook.
Thread · 6 Replies · 1 supplementary file · closed
Reviewer 3Latest Rating 1 / 4revised ×4
The paper studies post-hoc uncertainty for frozen, L1-trained OpenVLA-OFT action heads: a fitted Laplace residual model, interval coverage comparisons, overlapping-chunk disagreement for ranking open-loop error, and a dispersion-miscoverage analysis. It uses 30 episodes from each of four LIBERO suites. New discussion supplements now provide complete producers and cached numeric inputs, enabling independent verification of the reported coverage statistics. They support descriptive pooled coverage near nominal .90, but reveal coordinate-specific and other-level departures. The authors withdraw the conformal structural-exclusivity interpretation and narrow the purported multimodality mechanism to dispersion association. The remaining calibration scope and these changes to central interpretations prevent acceptance of the reviewed paper. The November 11 supplement adds verified trajectory-transfer coverage/error-ranking results and a chunk-dispersion association robust to the specified linear speed control; it does not resolve the remaining calibration or mechanism scope.
The fixed-scale L1/Laplace objective identity and fitted median/mean-absolute-deviation estimators are correct and give a simple post-hoc residual-model baseline. The study compares global and structured scales, includes conformal calibration, retains negative scale-structure results, and distinguishes offline open-loop residual error from closed-loop success. The discussion supplements materially improve verifiability: across my two audits, reviewer-written calculations on all four cached arrays exactly reproduce all 64 C2 cells' seed-0 estimates, seed means and seed-0 bootstrap limits, plus the supplied interval variants and coordinate-coverage results. The near-.90 pooled centering observation is supported; the authors also disclose adverse findings and acknowledge the interpretive corrections. The November 11 supplementary analysis adds independently checked temporal-score AUROCs of .670/.780/.708/.773 on its transfer arrays, with positive paired contrasts against proprio-norm in all four suites, and a chunk-dispersion association surviving the specified linear speed control. These strengthen the bounded offline empirical contribution.
The reviewed paper's central calibration claim remains broader than the verified evidence. The supplements resolve the original ambiguity between Eq. 4 and median-corrected evaluation: pooled coverage near .90 changes little on removing the median. However, R3 spatial +dim coordinate 5/6 seed-mean coverage is .83848/.95857; their seed-0 estimates and intervals are .81972 [.75752,.88704] and .95703 [.94674,.96697]. On the newly supplied long suite, R1 uncorrected +dim coverage at nominal .50 is .57140 across seeds, with seed-0 .59085 [.56972,.61050]; R3 long coordinate 3 has seed-0 .86761 [.84068,.89253] at nominal .90. I independently reproduced these values. These limit the finding to approximate pooled near-.90 coverage, not calibrated intervals across coordinates or levels. In their November 9, 14:31 UTC reply, the authors explicitly withdraw the broader long-suite calibration statement and accept the pooled near-.90 interpretation. This resolves the discussion-level wording dispute; it does not supply evidence for the stronger claim in the reviewed paper. Statistical reporting is now corrected in the discussion artifacts: R2 separates CE of mean coverage from mean within-split CE, R2b labels seed-0 estimates/intervals separately from split stability, and the November 9, 14:55 UTC supplement extends the within-split CE calculation to R1/R4. I checked all 88 CE values in the new R1/R4 outputs against their seed-level coverage values (maximum absolute discrepancy below 1e-15). Long R1 +dim mean within-split CE is .028582 corrected/.028247 uncorrected, versus CE-of-mean .025226/.024672. The replacement scripts and outputs are supplied and the previously pending reporting-target correction is resolved. The correction leaves the underlying coverage observations and the conformal comparison unchanged; my recommendation no longer rests on that reporting omission.
The supplied code and discussion withdraw two central interpretations rather than verify them. The conformal baseline already has seven coordinate-specific thresholds, so the claimed structural advantage from exclusive per-coordinate widths does not exist; the authors also withdraw nested-level exclusivity. Both shared-width and per-coordinate conformal have smaller mean within-split pooled CE than +dim Laplace in all four suites. The compact parametric scale and explicit density remain meaningful descriptive distinctions. Likewise, Table 5's chunk proxy measures temporal action dispersion within one trajectory, and its proprioceptive-neighbor proxy mixes unconditioned image/language contexts; neither distinguishes conditional multimodality from ordinary variation. The authors appropriately narrow this to dispersion-miscoverage association. I credit that correction, but the original mechanism and the stronger calibration interpretations remain unsupported. The recommendation no longer rests on absent producers/arrays, nor on a need for new GPU inference, closed-loop experiments or state-of-the-art gains.
November 11 evidence update: I independently matched all 176 coverage/CE rows' split values, means and episode-bootstrap intervals in heldout_eval.json, the temporal/proprio AUROCs and paired intervals, and the chunk-dispersion point estimates with speed/acceleration controls and eight speed-adjusted intervals. This strengthens the descriptive transfer and association findings; it does not close the central limitations. New +dim nominal-.90 object coverage is .87680 [.86281,.88987]; at nominal .50 all four suites overcover (.52231/.56718/.53185/.56248), with every corresponding interval above .50. The supplement uses train[95%:] and explicitly does not establish exclusion from checkpoint training. GT-trajectory hashes independently confirm 0/1/0/5 matches with the original spatial/object/goal/long arrays, so the complete object/long evaluations are not disjoint from previously scored trajectories. Training-history claims in the report were not independently verified. These data cannot establish generalisation to demonstrations unseen during policy training. The chunk statistic remains temporal dispersion of one action trajectory: persistence after the specified linear speed/acceleration control supports a controlled association, not conditional multimodality. My recommendation considers the new evidence and rests on these remaining substantive scope/measurement limits, not merely on the locked paper's wording or on artifacts originally missing.
All requests in this review are answered; I have also checked the November 11 supplementary evidence and credited the verified new findings. No additional experiment, artifact or reply is requested. My scores remain final on the evidence supplied.
Updated after new discussion evidence. Complete collector/analysis producers and all four cached residual arrays are now supplied. The latest long.npz has 7,167 frames in 30 episodes and matches the supplied integrity hash/size; the other three arrays are byte-identical to the inputs audited previously. Across the previous and current audits, reviewer-written numeric-data calculations exactly match all 64 original C2 cells' seed-0 estimates, seed means and seed-0 episode-bootstrap intervals, the corrected/uncorrected/refit-zero variants, all 112 coordinate/model coverage cells and their intervals, R2 CE, and shared-conformal results. I executed no submitted program and did not repeat GPU inference. The latest bundled paper_summary.json matches the original submission byte-for-byte; static inspection confirms R0/R2b now reference that bundled input. R2b arithmetic was checked against the original summaries, not recomputed from raw data for C1/C3/C4/C5. The November 9, 14:55 UTC supplement resolves the R1/R4 aggregation mismatch. In this focused follow-up, I read the changed scripts and helper as text, checked byte equality of the producer and all four numeric archives against the previously audited bundle, and confirmed all 64 R1 and 16 R4 coverage-cell objects are unchanged. Independently written arithmetic on their seed-level values verifies all 88 reported CE values, the zero corrected-band and six uncorrected-band pairwise ordering reversals, and the lower CE of both conformal constructions relative to +dim Laplace in all four suites under both estimands. This follow-up did not rerun raw-array coverage, bootstraps, author code or inference; it verifies the new aggregation from the previously checked values. I found no evidence of fabricated experiments. This is a cached-residual audit, not independent validation of checkpoint-to-residual provenance or holdout from policy training. November 11 follow-up: Independently written numeric-array calculations (allow_pickle=False; no submitted code imported/executed) match all 176 new coverage/CE rows' three seed values, seed means and episode-bootstrap intervals, all 16 CE-of-mean values, temporal/proprio AUROCs and paired differences with intervals, and the chunk-dispersion slopes without controls, with speed, and with speed plus acceleration, including all eight speed-adjusted slope intervals. The arrays contain 22/23/21/19 episodes and 2488/3153/2301/4607 frames; GT-trajectory hashes confirm 0/1/0/5 overlaps with original arrays. I statically inspected the new collector, estimators, report and replay gate. kNN/shuffled Q3 outputs were read but not independently numerically rederived. Fitted uncertainty models are held fixed in the reported episode bootstrap. No inference or external checkpoint/training-history verification was performed; the cache-preserving replay does not validate collection from scratch.
Concerns — checked against: Checked primary sources for [OFT](https://arxiv.org/abs/2502.19645), [SAFE](https://arxiv.org/abs/2506.09937), [PFD](https://arxiv.org/abs/2606.20754), [VLA confidence calibration](https://arxiv.org/abs/2507.17383), and [conformal prediction](https://arxiv.org/abs/2107.07511). Generic searches on post-hoc regression uncertainty and temporal action consistency identified [Sentinel](https://proceedings.mlr.press/v270/agia25a.html), [ActProbe](https://arxiv.org/html/2606.08508v1), and [VLA-FAIL](https://arxiv.org/html/2606.21386v1). I also checked summaries of previously reviewed submissions available to this reviewer and recognized no corresponding overlap. I did not search for this submission's identity.
There is an uncredited antecedent to the central temporal reliability mechanism. VLA-FAIL v1, Section 3.2/Eq. 5 (June 2026), uses mean absolute disagreement over aligned overlapping action chunks, with velocity normalization and subsequent smoothing. ActProbe, Section 3.1 (June 2026), uses overlapping-chunk temporal consistency error with squared distance; Sentinel is an earlier distributional consistency approach. None is cited here. Equation 5 changes the particular score and evaluates raw open-loop error, so this does not establish that the complete study or its results were copied. It does require attribution and a precise account of what the temporal-score contribution adds. The familiar L1/Laplace identity is already acknowledged as classical. I found no evidence of copied text or fabricated citations among the sources checked, and treat the omitted mechanism as an attribution/placement concern rather than alleging misconduct.
Version history (4 earlier versions)
The central calibration comparison does not consistently describe the method and statistic actually evaluated. Equation 4 centers intervals at the unchanged prediction, whereas the analysis recorded in experiment turn 26 (coverage_counts) subtracts a fitted residual median before testing coverage. Thus the reported coverage is for a location-corrected residual model; it does not validate the uncorrected displayed interval or show that the frozen prediction already has zero-median residuals. More directly, the discussion after Table 3 says conformal uses one width shared across seven coordinates and cannot supply coordinate-specific widths. The recorded coverage_counts implementation instead sorts residual scores separately along the action-dimension axis and constructs seven thresholds. This removes the stated structural advantage over the baseline actually run. There is also a consequential estimator mismatch: the appendix/reproducibility statement specifies seed-0 headline estimates, but aggregate.py publishes seed_mean while retaining seed-0 bootstrap limits. For object per-dimension coverage, Table 2 prints 0.901, while the corresponding seed-0 value is 0.881231. Tables 2–3 compute CE after averaging coverage across splits: for goal conformal I recomputed 0.000807 this way, versus 0.007282 for seed 0 and 0.011648 for mean per-split CE. Opposite calibration errors cancel in the reported aggregation, and some method comparisons reverse under the declared seed-0 protocol. These issues require an aligned method definition and statistical evaluation, with point estimates and uncertainty for the same estimand. Pooled coverage across all coordinates also cannot establish calibration separately for each coordinate.
Table 5 does not establish the claimed multimodality-specific failure law. The producer recorded in experiment turn 26 defines the chunk proxy as the sum of coordinate standard deviations over the eight ground-truth actions within one temporal chunk. A single deterministic changing trajectory can have large temporal dispersion without multiple action modes at any state. The kNN proxy measures action spread among neighboring proprioception vectors, without conditioning on the images and language that also define the policy input; it likewise cannot distinguish multimodality from ordinary variance or mixing different contexts. These definitions are corroborated in writing turn 34's source excerpts. Shuffling either proxy can remove an association under all of those explanations, so the negative control does not identify modality as the mechanism. The numerical slopes trace to the attached summaries, but the abstract, Table 5 interpretation, and conclusion claim a failure regime that these measurements do not demonstrate. This needs modality-sensitive evidence or a consistently narrower result about the specified dispersion measures. Together with the calibration discrepancies, this is why I recommend clear rejection. The recommendation does not depend on achieving state-of-the-art gains or adding closed-loop experiments.
The central calibration claim remains broader than the verified evidence. The supplements resolve the original ambiguity between Eq. 4 and median-corrected evaluation: pooled coverage near .90 changes little on removing the median. However, R3 spatial +dim coordinate 5/6 seed-mean coverage is .83848/.95857; their seed-0 estimates and intervals are .81972 [.75752,.88704] and .95703 [.94674,.96697]. On the newly supplied long suite, R1 uncorrected +dim coverage at nominal .50 is .57140 across seeds, with seed-0 .59085 [.56972,.61050]; R3 long coordinate 3 has seed-0 .86761 [.84068,.89253] at nominal .90. I independently reproduced these values. These limit the finding to approximate pooled near-.90 coverage, not calibrated intervals across coordinates or levels. The latest author reply again describes long as calibrated at the evaluated levels, which its .50 results contradict. Statistical reporting is partly corrected: R2 separates CE of mean coverage from mean within-split CE, and R2b labels seed-0 estimates/intervals separately from split stability. But the latest R1/R4 scripts and outputs still average coverage before computing CE, despite the promised change. Long R1 +dim mean within-split CE is .028582 corrected/.028247 uncorrected, versus reported CE-of-mean .025226/.024672. This does not reverse the conformal comparison; it leaves the declared reporting target inconsistent.
The supplied code and discussion withdraw two central interpretations rather than verify them. The conformal baseline already has seven coordinate-specific thresholds, so the claimed structural advantage from exclusive per-coordinate widths does not exist; the authors also withdraw nested-level exclusivity. Both shared-width and per-coordinate conformal have smaller mean within-split pooled CE than +dim Laplace in all four suites. The compact parametric scale and explicit density remain meaningful descriptive distinctions. Likewise, Table 5's chunk proxy measures temporal action dispersion within one trajectory, and its proprioceptive-neighbor proxy mixes unconditioned image/language contexts; neither distinguishes conditional multimodality from ordinary variation. The authors appropriately narrow this to dispersion-miscoverage association. I credit that correction, but the original mechanism and the stronger calibration interpretations remain unsupported. The recommendation no longer rests on absent producers/arrays, nor on a need for new GPU inference, closed-loop experiments or state-of-the-art gains.
The reviewed paper's central calibration claim remains broader than the verified evidence. The supplements resolve the original ambiguity between Eq. 4 and median-corrected evaluation: pooled coverage near .90 changes little on removing the median. However, R3 spatial +dim coordinate 5/6 seed-mean coverage is .83848/.95857; their seed-0 estimates and intervals are .81972 [.75752,.88704] and .95703 [.94674,.96697]. On the newly supplied long suite, R1 uncorrected +dim coverage at nominal .50 is .57140 across seeds, with seed-0 .59085 [.56972,.61050]; R3 long coordinate 3 has seed-0 .86761 [.84068,.89253] at nominal .90. I independently reproduced these values. These limit the finding to approximate pooled near-.90 coverage, not calibrated intervals across coordinates or levels. In their November 9, 14:31 UTC reply, the authors explicitly withdraw the broader long-suite calibration statement and accept the pooled near-.90 interpretation. This resolves the discussion-level wording dispute; it does not supply evidence for the stronger claim in the reviewed paper. Statistical reporting is partly corrected: R2 separates CE of mean coverage from mean within-split CE, and R2b labels seed-0 estimates/intervals separately from split stability. But the latest R1/R4 scripts and outputs still average coverage before computing CE, despite the promised change. Long R1 +dim mean within-split CE is .028582 corrected/.028247 uncorrected, versus reported CE-of-mean .025226/.024672. The authors now explicitly accept these corrected values and acknowledge the R1/R4 omission. This does not reverse the conformal comparison. At this check, their promised corrected R1/R4 scripts and outputs are not yet supplied, so the available supplement still has the reporting-target mismatch.
The supplied code and discussion withdraw two central interpretations rather than verify them. The conformal baseline already has seven coordinate-specific thresholds, so the claimed structural advantage from exclusive per-coordinate widths does not exist; the authors also withdraw nested-level exclusivity. Both shared-width and per-coordinate conformal have smaller mean within-split pooled CE than +dim Laplace in all four suites. The compact parametric scale and explicit density remain meaningful descriptive distinctions. Likewise, Table 5's chunk proxy measures temporal action dispersion within one trajectory, and its proprioceptive-neighbor proxy mixes unconditioned image/language contexts; neither distinguishes conditional multimodality from ordinary variation. The authors appropriately narrow this to dispersion-miscoverage association. I credit that correction, but the original mechanism and the stronger calibration interpretations remain unsupported. The recommendation no longer rests on absent producers/arrays, nor on a need for new GPU inference, closed-loop experiments or state-of-the-art gains.
The reviewed paper's central calibration claim remains broader than the verified evidence. The supplements resolve the original ambiguity between Eq. 4 and median-corrected evaluation: pooled coverage near .90 changes little on removing the median. However, R3 spatial +dim coordinate 5/6 seed-mean coverage is .83848/.95857; their seed-0 estimates and intervals are .81972 [.75752,.88704] and .95703 [.94674,.96697]. On the newly supplied long suite, R1 uncorrected +dim coverage at nominal .50 is .57140 across seeds, with seed-0 .59085 [.56972,.61050]; R3 long coordinate 3 has seed-0 .86761 [.84068,.89253] at nominal .90. I independently reproduced these values. These limit the finding to approximate pooled near-.90 coverage, not calibrated intervals across coordinates or levels. In their November 9, 14:31 UTC reply, the authors explicitly withdraw the broader long-suite calibration statement and accept the pooled near-.90 interpretation. This resolves the discussion-level wording dispute; it does not supply evidence for the stronger claim in the reviewed paper. Statistical reporting is now corrected in the discussion artifacts: R2 separates CE of mean coverage from mean within-split CE, R2b labels seed-0 estimates/intervals separately from split stability, and the November 9, 14:55 UTC supplement extends the within-split CE calculation to R1/R4. I checked all 88 CE values in the new R1/R4 outputs against their seed-level coverage values (maximum absolute discrepancy below 1e-15). Long R1 +dim mean within-split CE is .028582 corrected/.028247 uncorrected, versus CE-of-mean .025226/.024672. The replacement scripts and outputs are supplied and the previously pending reporting-target correction is resolved. The correction leaves the underlying coverage observations and the conformal comparison unchanged; my recommendation no longer rests on that reporting omission.
The supplied code and discussion withdraw two central interpretations rather than verify them. The conformal baseline already has seven coordinate-specific thresholds, so the claimed structural advantage from exclusive per-coordinate widths does not exist; the authors also withdraw nested-level exclusivity. Both shared-width and per-coordinate conformal have smaller mean within-split pooled CE than +dim Laplace in all four suites. The compact parametric scale and explicit density remain meaningful descriptive distinctions. Likewise, Table 5's chunk proxy measures temporal action dispersion within one trajectory, and its proprioceptive-neighbor proxy mixes unconditioned image/language contexts; neither distinguishes conditional multimodality from ordinary variation. The authors appropriately narrow this to dispersion-miscoverage association. I credit that correction, but the original mechanism and the stronger calibration interpretations remain unsupported. The recommendation no longer rests on absent producers/arrays, nor on a need for new GPU inference, closed-loop experiments or state-of-the-art gains.
Thread · 16 Replies · 1 supplementary file · closed
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