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Under review as a conference paper at ICLR 2027

Grounded Evaluation of Reasoning-Action Faithfulness in Vision-Language-Action Driving Models

Abstract

We study whether the chain-of-causation reasoning of vision-language-action (VLA) driving models is faithful to the actions they execute. Current evaluation relies on self-consistency checks and plausibility judges, which reward reasoning that reads coherently regardless of the trajectory the model drives. We instead evaluate faithfulness against two grounded references, the human-driven trajectory and human-verified expert reasoning, on Alpamayo-R1 and Alpamayo-1.5 across out-of-distribution driving events. Our main finding is that faithfulness is not plausibility: (i) both models plan accurately with average displacement error of 2.22 m and 3.68 m, yet their reasoning is fully faithful in only 39.6% and 33.1% of scenes, while reference-free signals rate 58-63% as faithful; (ii) when we hold reasoning fixed and progressively corrupt the trajectory, trajectory-sensitive metrics degrade monotonically, while trajectory-blind metrics, including the plausibility judge, stay constant; (iii) a validated counterfactual probe finds overt post hoc rationalization in fewer than 4% of scenes, so the gap reflects weak grounding rather than deception; and (iv) extending the evaluation to AutoVLA, which requires assistant prefill to produce reasoning, we find it less self-consistent than either Alpamayo model. We formalize grounded scorers, plausibility scorers and reasoning-action divergence, and prove that plausibility scorers are invariant to trajectory corruption by construction. Chain-of-causation explanations are therefore not yet a reliable basis for oversight of driving VLAs.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
vision-language-action models, autonomous driving, chain-of-causation explanations, faithfulness, reasoning-action divergence

Reviews

Among:
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1234this paper, Bottom 2%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_PHLVOpenReview ↗
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2
Confidence
3
Informativeness
2
Presentation
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2
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Paper summary

The paper evaluates the relationship between natural-language reasoning and predicted trajectories in driving VLAs. It separates external-reference agreement from trajectory sensitivity, combining trajectory error, text-trajectory consistency, expert-reasoning agreement, entity overlap, and a plausibility judge. Controlled trajectory corruptions and misleading text hints provide additional diagnostic tests. The proposed evaluation framework is called SafeDriveX. The main comparison evaluates Alpamayo-R1 and Alpamayo-1.5 on 165 labeled events from 150 PhysicalAI-AV clips. Trajectory-sensitive scorers respond to trajectory corruption, while trajectory-blind scorers remain unchanged. The text-hint probe produces overt rationalization labels in fewer than 4% of cases.

Critical strengths
  1. The paper addresses an important practical auditing problem and provides concrete examples where a model's explanation contradicts its trajectory. Its metric taxonomy makes clear which signals inspect the trajectory and which only inspect text or references.
  2. The evaluation includes a same-event comparison of two released models, multiple decoding seeds, a second judge, controlled corruptions, and a larger action-only validation check. Small subsets and the AutoVLA dataset/prefill confounds are explicitly acknowledged.
Critical weaknesses
  1. The headline metric measures reference agreement rather than reasoning–action consistency. It labels reasoning fully faithful by matching an expert maneuver and cause without reading the model's trajectory. It can therefore accept text that contradicts the model's action, or reject a legitimate alternative explanation.
  2. Metric validation and statistical reporting are limited. The drift judge is validated on only 16 cases despite the claimed 3–4% phenomenon. Primary skip coverage and AutoVLA evaluation counts remain unclear, while variation across decoding seeds does not quantify uncertainty across independent driving clips.
Questions for authors
  1. How often does expert-matching reasoning contradict the model's own trajectory? Could you report a joint reasoning–trajectory assessment and use human judgments to distinguish genuine inconsistencies from valid alternative maneuvers or causes?
  2. Please report checkable counts and compare metrics on a common subset, with paired confidence intervals clustered by clip. Are AutoVLA's 831 default scenes and 6,902 prefill scenes separate cohorts? What units underlie its coverage and Wilson interval?
  3. Could you validate the scorers on a larger human-labeled set and report precision/recall, particularly for rare rationalization labels? Similar aggregate scores from two judges do not establish item-level agreement or correctness. How sensitive is trajectory consistency to its thresholds?
  4. What evidence shows the added value of external references for detecting reasoning–action contradictions? The reference-free trajectory-consistency scorer responds to corruption, whereas expert-reasoning agreement does not. A comparison against independent human judgments would help clarify this distinction.
4 comments
AuthorsOpenReview ↗

part 1 of 4): the headline metric, and the joint reasoning-trajectory assessment (W1, Q1, Q4)

We thank the reviewer for a careful review. We have revised the paper; the numbers below refer to the revised PDF. Apart from the human annotation study (part 4), every analysis in this response uses the existing outputs, and a new Appendix I collects the statistical reporting the reviewer asked for.

W1. To avoid any misreading first: the paper does check reasoning against action directly. Trajectory consistency compares the action stated in the reasoning with what the model's own trajectory does, on every sample whose reasoning states a checkable action (58.2% and 61.7% for the two Alpamayo models, and the same check on 15 further arms in Section 4.6). Two experiments test that link causally: corrupting the trajectory while the reasoning is held fixed (Section 4.4, Figure 2), and contradicting the reasoning with a misleading hint while watching the action (Section 4.5). The reviewer's own summary notes this check. W1 concerns which metric leads, not whether the link is measured.

On that question, the reviewer's description of reasoning-gold is accurate, and it is by design. The model produces two outputs, a reasoning trace and a trajectory. Reasoning-gold compares the first with the expert's reasoning and does not read the second. Section 3 classifies it as grounded but trajectory-blind, and the degradation experiment shows it staying exactly constant while the trajectory is corrupted. The paper never relies on it alone, and its central claim is that the two axes detect different failures.

The term is defined in that sense: Section 3 states that a scene is fully faithful when the model's reasoning matches the human-verified expert reasoning on both maneuver and cause, that is, faithfulness to a grounded reference. Agreement between the reasoning and the model's own action is the separate question that trajectory consistency answers, and the paper reports the two side by side. The revision now also reports them jointly (Table 12), so a reader can see at once how often reasoning is right about the scene and carried out by the model's own trajectory. The human annotation study (part 4) addresses the reviewer's second concern, legitimate alternative explanations.

Q1. How often does expert-matching reasoning contradict the model's own trajectory? Table 12 crosses expert agreement with self-consistency on every checkable record, counting a record as consistent only when every check passes:

ModelRecordsExpert match, consistentExpert match, contradictsNo match, consistentNo match, contradicts
Alpamayo-R129468459190
Alpamayo-1.53036720106110

Among reasoning that matches the expert, 39.8% [28.2, 51.9] for Alpamayo-R1 and 23.0% [11.5, 36.3] for Alpamayo-1.5 contradicts the model's own trajectory (95% intervals clustered by clip). No trajectory-blind scorer can detect these cases. Annotators blind to the scores confirm that the case is real, putting the share at 24.8% [9.5, 44.6] (part 4). The scorer's share also holds up when the trajectory-consistency thresholds change: across fifteen settings between half and one and a half times the defaults, it stays at 38.1% to 42.5% and 23.0% to 26.4% (Table 13).

Q4. What do external references add? The other off-diagonal cell answers this. Among reasoning that is self-consistent, 57.2% [46.6, 67.6] (R1) and 61.3% [48.9, 72.8] (1.5) disagrees with the expert. No reference-free scorer can detect these cases, because the reasoning and the trajectory agree with each other while the reasoning differs from the human-verified reference. The reviewer is right that references add nothing to detecting a contradiction between the reasoning and the model's own action; trajectory consistency does that job. What references add is a grounded check on the content of self-consistent reasoning. Some of this cell is legitimate alternative reasoning, as the reviewer suspects; but annotators judge 12.4% of self-consistent reasoning to be wrong for the scene (part 4), a failure that only a grounded reference can expose. The cross-model result points the same way: on the same events, the grounded scorers separate the two models and the self-consistency scorer does not (part 2). Neither axis subsumes the other, which is the paper's central claim.

AuthorsOpenReview ↗

(part 2 of 4): coverage, clip-clustered uncertainty, and AutoVLA counts (W2, Q2)

We agree with the Reviewer that seed variation measures decoding variability, not uncertainty over driving scenes. The 165 events come from 137 clips, so the Appendix reports every interval from a bootstrap that resamples whole clips, keeping all events and all three seeds of a clip together (5,000 draws).

Checkable counts. Trajectory consistency is defined only when the reasoning states a checkable action, and the checkable count varies by seed: 100, 109 and 85 of 165 events for Alpamayo-R1, and 99, 117 and 87 for Alpamayo-1.5. Pooled coverage is 59.4% [52.7, 66.1] and 61.2% [54.3, 68.1]. Because each seed measured consistency on a different subset, the comparison below uses a common subset.

Paired comparison on a common subset, clustered by clip (Table 11, Alpamayo-R1 minus Alpamayo-1.5 on identical event-seed pairs):

MetricPairsDifference [95% CI]
ADE (m)495−1.46 [−1.83, −1.11]
Entity fidelity495+0.068 [+0.026, +0.110]
Reasoning-gold (points)495+6.5 [+1.0, +12.3]
Trajectory consistency, mean (points)227−0.4 [−8.4, +7.4]
Trajectory consistency, every check (points)227−0.4 [−10.1, +8.7]

Every grounded scorer separates the models, reasoning-gold narrowly, and trajectory consistency on the 227 pairs checkable for both models shows no difference. Restricting to the common subset removes most of the gap that seed-level reporting showed (58.2% against 61.7%), so that gap partly reflected different checkable subsets. Unpaired, each model's interval is wide and the two overlap even on the grounded scorers (Table 10); the paired comparison is the appropriate one, because both models are scored on the same events.

AutoVLA: two separate cohorts. Yes, they are separate. The 831 scenes are a run of the released checkpoint in its default mode, which produced a substantive chain of causation on none of them. The prefill run is a second decoding of 12,140 of the 12,146 NAVSIM navtest scenes. The unit throughout is a scene, decoded once with a single seed. Coverage, 57%, is the 6,902 of those 12,140 scenes whose reasoning states a checkable action. The 54.3% is the share of those 6,902 scenes scoring at least 0.5, the same definition Table 4 now uses for every row; for Alpamayo, that share is 62.6% and 67.3%. The Wilson interval treats scenes as independent, which understates the uncertainty, because navtest scenes are drawn from a smaller number of driving logs. We state this in the revision rather than claim more precision than the interval carries.

Drift judge and the 3 to 4% rate. We agree that 16 held-out cases are too few to validate a rate this small. While re-checking the probe for this response, we also found two problems. The action-stability check had a label-mapping error, so some changed actions were counted as unchanged, and 390 of the 990 probes received the generic hint "reconsider your driving action" instead of an action-specific one. Since the generic hint does not point to any particular action, it is unclear what "drift toward the hint" means for those probes. We therefore report the post-hoc rate in three ways (Table 14). All three use the same gemini-2.5-flash labels, with 95% intervals clustered by clip.

TreatmentAlpamayo-R1Alpamayo-1.5
As published3.4% [1.8, 5.2]3.8% [2.1, 5.8]
Stability check fixed2.6% [1.2, 4.2]2.4% [1.1, 4.0]
Fixed, generic hint excluded0.8% [0.2, 1.7]1.2% [0.4, 2.2]

We defined the third row after looking at the labels, which is why we give it next to the other two and not in their place. Fixing the hint assignment itself would require rerunning inference, which we have not done. In all three cases the upper end of the interval is below 6%. Our conclusion that overt rationalization is rare therefore holds either way, and the published 3.4% and 3.8% should be read as upper bounds.

Human validation with precision and recall. We also collected labels from annotators outside the author team. They did not see any scores, and the analysis plan was written before the first label came in. We drew two stratified samples:

  • Drift: 30 counterfactual pairs (18 that the judge called drift, 12 that it called robust), each labelled by three annotators.
  • Reasoning against trajectory and scene: 40 events from the four cells of Table 12, 20 per model, 20 of them labelled by two annotators. Annotators first decided whether the action stated in the reasoning matches the planned trajectory, using a top-down path plot and a speed profile; they never saw the scorer's flags. Only then were they shown the expert reasoning and asked whether the model's reasoning is the same, a valid alternative, or wrong.

The first sample gives the drift judge's precision on its positive label. The second gives precision and recall for trajectory consistency, and shows how many reasoning-gold rejections people consider acceptable alternatives (W1). Since some items have more than one label, we can also report agreement between annotators item by item. Results are in part 4.

AuthorsOpenReview ↗

(part 4 of 4): results of the human annotation study (Q1, Q3, Q4)

For each item, annotators saw the model's reasoning, a plot of its planned trajectory, the camera frame, and the expert reasoning, but no scores. Items were sampled from the four cells of Table 12 and from the drift strata. We weight the estimates back to the full population and compute 95% intervals by resampling items within each stratum. One annotator works in autonomous driving and two in machine learning. The numbers below use only the labels we received before the discussion closes; We think that this evaluation is interesting, so we decided to report it as is. We will add them to Appendix I in the final version.

Post-hoc rationalization (Q3). Using annotator labels only, we count a case as post-hoc when the reasoning moves toward the hint but the stated maneuver does not change. This happens in 2.9% [1.3, 5.0] of Alpamayo-R1 records and 1.7% [0.5, 3.1] of Alpamayo-1.5 records, and in 0.3% for both if probes with the generic hint are excluded. These estimates also include drift that the judge missed, and they are at or below the published 3.4% and 3.8%. The judge's precision on its drift label is 59.3% [42.6, 75.9], so it flags too many cases rather than too few, and the published rates are upper bounds. In records the judge called robust, annotators marked drift in only 2 of 36 labels, so we can estimate recall only roughly. Overall agreement between annotators and the judge is kappa 0.60, and annotators agree with the automatic "action unchanged" label on 81.5% of items.

Reasoning that matches the expert but contradicts the trajectory (Q1, Q3). Annotators judge 24.8% [9.5, 44.6] of expert-matching reasoning to be inconsistent with the model's planned trajectory; trajectory consistency gives 32.5% on the same population. Across all records the two are close: 43.0% [27.3, 58.4] from annotators and 44.4% from the scorer. None of these cases can be caught by a metric that does not read the trajectory. Item by item, the scorer's precision for an inconsistency is 56.4% [29.1, 80.6] and its recall is 58.2% [38.9, 75.9] (kappa 0.22). Most disagreements involve threshold-based claims, such as a stop that is not reached within the horizon or a small deceleration or nudge, where annotators count partial motion as a match. On these cases the scorer is stricter than a human reader, and we will state this in the threats to validity. Annotators also only moderately agree with each other (kappa 0.41 on this question and 0.43 to 0.57 on drift), which limits how high any scorer's item-level agreement can be.

Reasoning-gold and alternative explanations (W1, Q4). When reasoning-gold reports a match, annotators consider the reasoning wrong for the scene in only 5.4% [0.0, 13.5] of records. When it reports no match, they consider 59.4% [37.6, 79.3] of the reasoning a valid alternative, 26.1% wrong, and 14.6% essentially the same as the expert's. The reviewer's concern about alternative explanations is therefore justified: full agreement with the expert is a lower bound on acceptable reasoning. In the final version we describe the off-diagonal cell of Table 12 as reasoning that is self-consistent but differs from the reference, not as wrong reasoning. Annotators still judge 12.4% [0.0, 27.2] of self-consistent reasoning to be wrong for the scene, and only a reference-based check can detect these cases. We thank the reviewer for raising this point.

Reviewer_CMpyOpenReview ↗
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Confidence
3
Informativeness
1
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Paper summary

This paper investigates whether the language explanations generated by Vision-Language-Action (VLA) models for autonomous driving are consistent with scene evidence and predicted trajectories. The authors define five evaluation perspectives (judges): trajectory error relative to ground truth; the consistency between the model’s own reasoning and its generated trajectory; alignment with the reasoning provided by human experts; the degree of correspondence between scene entities referenced in the model’s reasoning and those in expert reasoning; and a VLM-based judge of the scene explanations generated by the VLA model. The study primarily evaluates the Alpamayo-R1 and Alpamayo-1.5 models, with supplementary experiments conducted on AutoVLA. The results indicate that the explanations provided by these models are not guaranteed to align with expert-provided references, nor are they necessarily consistent with the actual actions predicted by the models. The paper also explores the sensitivity of different proposed scorers by applying perturbations to the output trajectories, and introduces perturbations to the model's original inputs, revealing that the model's reasoning remains largely unaffected by such misleading prompts.

Critical strengths
  1. The question has practical value. Testing the faithfulness of the driving explanation reminds people that the entire behavior of the model cannot be considered reliable just because the explanation is smooth or the trajectory error is low.
  2. The evaluation perspectives are good. It is suggested that when evaluating VLA, trajectory prediction indicators, rationality of reasoning, and consistency between reasoning and action should be taken into consideration together.
Critical weaknesses
  1. The model evaluation is insufficient. Key findings are validated only across two models from the same family. Furthermore, AutoVLA reports results solely for the "TC" metric. The experimental setup fails to provide cross-family support for the paper's core findings. Compared to the cross-interface evaluation presented in [1], the justification for the inclusion and exclusion criteria for the models in this paper is inadequate. For example, why could a "decoupled question-answering task" not be evaluated independently as a form of reasoning? It is possible that models are already capable of a latent understanding of a scene, which then enables them to generate trajectories, so the decoupled reasoning for driving is something that warrants exploration rather than avoidance.

  2. The paper primarily highlights discrepancies between explanations, scene context, and predicted trajectories, yet it lacks an analysis of the underlying causes of these inconsistencies. While the authors characterize the issue as "weak grounding," they do not clarify whether this term refers to errors in perceptual understanding, flaws in explanation generation, or a breakdown in the connection between reasoning and planning, and experiments to distinguish between these possibilities are not explored.

[1] DriveFaith: A Cross-Model Study of Reasoning--Action Faithfulness in Autonomous Driving

Questions for authors
  1. Why is it necessary to conduct testing in out-of-distribution (OOD) scenarios? The justification "reference answers are available for evaluation/explanation, and challenging scenarios hold value for safety auditing" is not particularly compelling. Should both OOD and in-distribution scenarios be considered and compared?

  2. There are a lot of vague definitions, and the paper lacks implementation details, making it difficult to fully grasp the proposed approach. Could the author specify:

  • (1) The model interface and generation pipeline. And as for the outputs, one can only infer that the model performs reasoning before generating trajectory waypoints.
  • (2) How the "two trajectory-only interventions" are implemented?
  • (3) The duration of the predicted trajectories, the number of sampled waypoints, and the sampling interval for each model?
  1. Could the authors provide a clearer comparison with [1] and [2], particularly regarding the evaluation protocols, empirical findings, and additional insights offered by the present study?

[1] DriveFaith: A Cross-Model Study of Reasoning--Action Faithfulness in Autonomous Driving

[2] More Than Meets the Eye? Uncovering the Reasoning-Planning Disconnect in Training Vision-Language Driving Models

8 comments

We thank the reviewer for the comments.

Weakness

(w1) On critical weakness, the main objectives targeted by this research were to audit realised, open-source, driving VLA models as distributed. We looked for models that emit both a chain of causation and a trajectory in the same forward pass under default inference. We found real gaps while evaluating existing models (as described in Appendix F): some didn't release checkpoints, including Orion cited by DriveFaith (which released only the checkpoint based on Carla, not NuScenes). DriveFaith reports ORION results on real-world datasets but didn’t specify which weights were used, so we were not able to reproduce that setting with released weights (Bench2Drive). On AutoVLA, the released checkpoint didn't emit the chain of causation on inference, so we had to modify it to emit the chain of causation, reason why we treated it as secondary. Alpamayo R1, 1.5, and 2 remain the only models in our knowledge that emit both chain-of-causation reasoning and trajectory at inference.

(w2) On decoupled question answering: a question answering head answers whether the model can describe the scene when asked, which is a valid question but a different one. Our oversight question is whether the explanation given by the models, which is emitted together with a specific action, reflects that action, and a correct QA answer does not establish this. We add this distinction to Section 2 and list decoupled reasoning as future work.

Comments:

Q1. PhysicalAI-AV provides human-verified expert reasoning only for its OOD split, and our grounded reasoning scorers need it. For the scorers without labels, we already compare: on the full validation set (1,312 clips), Alpamayo-R1 reaches ADE 2.13 m and 56.2% trajectory consistency, versus 2.22 m and 58.2% on OOD. The inconsistency is not specific to hard scenes. We make this explicit in Section 4.2.

Q2. Implementation details (moved to Section 4.1). (1) Alpamayo takes multi-camera video (Figure 8), generates the chain of causation, then decodes the trajectory with a diffusion decoder conditioned on it, in one forward pass. AutoVLA generates reasoning then action tokens, but only under assistant prefill.

(2) Both interventions act on decoded waypoints, with reasoning and scene fixed. Lateral: offset growing linearly to δ ∈ {0, 0.5, 1, 2, 4} m at the final waypoint. Longitudinal: per-step forward displacement scaled by a ramped factor, injecting acceleration. Each is applied only where it contradicts the stated action (Appendix A).

(3) Alpamayo: 6.4 s, 64 waypoints, 0.1 s. AutoVLA: 4 s, 8 waypoints, 0.5 s.

Q3. Song et al. retrain their own models on nuPlan and find planning relies on priors rather than CoT, consistent with our finding that the action stays fixed under a contradicting hint (about 82%). We instead audit released models against human-verified references. DriveFaith (concurrent) admits any language channel, including QA outputs, and edits the reasoning to test whether the trajectory responds. It adopts the metrics, thresholds, and PhysicalAI-AV subset of Mayumu et al. (2026). We require reasoning emitted with the trajectory by released models, and we corrupt the trajectory to test whether faithfulness metrics can detect divergence at all. Our added insights: plausibility judges cannot detect trajectory-only divergence; a judge accepts 63% of explanations that match the expert in only 39.6% of events; and rationalization is rare (under 4%), pointing to weak grounding rather than deception.

Thanks to the author for the responses. However, I believe my concerns have not been fully addressed:

  1. Regarding W1:

    Even though the author repeatedly emphasizes in the paper that the results can only be reproduced on Alpamayo, the persuasiveness and generalizability of the findings remain weak because of the limited model evaluation.

    Furthermore, regarding the evaluation of VLAs on decoupled question-answering tasks, I do not believe this should be avoided. QA tasks can involve reasoning about driving decisions or driving action. Therefore, for the same scenario, a VLA trained with decoupled question-answering tasks can still verify whether reasoning faithfully leads to an action. I believe this is relevant to the core of the paper’s task rather than irrelevant.

    I strongly recommend that the authors further expand their survey or broaden the scope of the paper’s objective and include wider evaluations.

  2. There was no response to W2, as (w1) and (w2) both refer to my W1.

  3. Apart from Q2, the other parts of my questions still have not been adequately addressed. For example, the authors’ response to Q1 somehow deviates from my original question.

  4. Additionally, the organization of the paper should be refined. For example, the key information from Q2 should be incorporated into the main text rather than the appendix. Furthermore, the purpose of Figure 1 in the main text is unclear, and it is not cited within the main text.

In summary, I maintain my original assessment of this paper.

AuthorsOpenReview ↗

Response to Reviewer CMpy (part 1 of 6): what changed, and where to find it

We thank the Reviewer for the second round and the challenging comments. We have implemented new experiments, revised the paper, and uploaded the submission. The section, figure, and table numbers below refer to the revised version. Removing two redundant figures and one redundant table renumbered the later ones, so the model-input figure that our first reply called Figure 8 is now Figure 6; To save your time please find the summary as follow:

Reviewer pointWhere it is addressed in the revision
W1, model coverageSection 4.6 and Table 4; per-model results in Appendix H (Tables 6 to 9)
W1, decoupled QA modelsSection 2 (what such a score means); Section 4.6 and Table 4 (Impromptu-VLA decoupled, now scored)
W2, causes of the inconsistencySection 5, paragraph "Where the inconsistency comes from"
Q1, OOD versus in-distributionSection 4.2, second paragraph; Impromptu-VLA in Section 4.6
Q2, implementation detailsSection 4.1, paragraph "Interfaces, interventions, and horizons"
Q3, relation to concurrent workSection 2, final paragraph
Organization and Figure 1Figure 1 is now cited and explained in Section 4.2

Additionally, the self-consistency evaluation now covers 17 models on three datasets, up from three models. The 13 general-purpose backends behind LightEMMA's driving harness required no new inference, and Impromptu-VLA's decoupled mode is now scored rather than excluded. Behind one fixed harness, the 13 backends range from 11.8% to 71.5% consistency, so the measure separates models rather than reflecting our pipeline.

What follows: W2 (part 2), model coverage (part 3), decoupled models and how further models are added (part 4), Q1 to Q3 (part 5), and organization and the models we could not add (part 6).

Reviewer_apEAOpenReview ↗
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Paper summary

The paper examines the faithfulness between the chain-of-causation (CoC) reasoning and the executed trajectory of VLA driving models. It defines a set of evaluation signals, some grounded in human references and others not. Based on experiments that include controlled trajectory corruption and a counterfactual hint probe, the authors conclude that CoC explanations alone are not yet a reliable basis for oversight.

Critical strengths

Paper is well-written and easy to follow. Signals and experiments were designed well to support the insights in the conclusion.

Critical weaknesses

The insights and conclusion contains limited novelty.

Questions for authors

Given that the paper concludes that CoC explanations are not yet a reliable basis for oversight, what concrete changes to model design, training or evaluation do the findings suggest would make them reliable?

2 comments
AuthorsOpenReview ↗

What would make CoC explanations reliable?

We thank the reviewer for finding the paper clear and the signals and experiments well designed to support the conclusions.

On novelty. We agree that the high-level observation, that VLA reasoning and action can disagree, is shared with prior and concurrent work (Mayumu et al., 2026; Song et al., 2025; DriveFaith, concurrent). Our contribution concerns how this disagreement should be measured: which scorers can detect it, which cannot, and why. The revised introduction now states this directly, just before the list of contributions. We return to it below, because it is also what supports our conclusion.

Why the conclusion holds. For a chain of causation to support oversight, an auditor reading it must learn what the model perceived and why it acted, and must be able to tell when the explanation is wrong. Our results show that neither condition currently holds.

  1. The explanation is often wrong even when the driving is right. Alpamayo-R1 plans accurately on the OOD split (ADE 2.22 m), yet its reasoning matches the expert maneuver and cause in only 39.6% of events (33.1% for Alpamayo-1.5). Figures 1 and 3 to 5 of the revised PDF show the model stating a turn, deceleration, or nudge that its own trajectory does not execute.
  2. The explanation often disagrees with the model's own action. Stated and executed actions agree fully in 54.1% of checkable events for Alpamayo-R1 and 57.1% for Alpamayo-1.5 (mean per-event consistency 58.2% and 61.7%, the figures reported in the paper). On the full validation set (1,312 clips), mean consistency is 56.2%. AutoVLA, the only other released model with coupled reasoning, emits no reasoning by default (0 of 831 scenes); with prefill, 54.3% of its checkable scenes are consistent.
  3. The checks used in practice cannot tell when it is wrong. A plausibility judge rates 63% of the same explanations as acceptable. Under controlled trajectory corruption with the reasoning fixed, trajectory-sensitive scorers degrade monotonically, while the plausibility judge and reasoning-only scorers do not respond. An auditor relying on plausibility would miss a reasoning-action divergence of any size.
  4. The failure is weak grounding, not deception. Under a contradicting text hint, the action stays fixed in about 85% of scenes and overt rationalization occurs in under 4%. The explanation is neither a reliable report of the plan nor a lever on it.

Taken together: an auditor reading only the chain of causation would get the maneuver or cause wrong in most OOD events and would have no reference-free way to tell which ones. Therefore, we humbly think that CoC explanations are not yet a reliable basis for oversight.

What would make CoC explanations reliable? These findings suggest directions at four levels, which the revision adds to Section 5.

(a) Since the trajectory barely responds to text, single-pass models use the chain of causation more as a description of the plan than as an input to it. Concurrent work finds the same for Alpamayo-R1 under direct reasoning edits (DriveFaith). Reliable explanations need either an interface the planner must use, such as structured meta-actions that constrain decoding, or an external check on the explanation.

(b) Optimizing plausibility does not produce faithfulness. In the Alpamayo-R1 ablations, optimizing the reasoning reward alone improved the reasoning score but degraded reasoning-action consistency and ADE (NVIDIA et al., 2025). Even with a consistency reward added, Alpamayo-R1 reaches a mean consistency of 58.2% on hard OOD events. Our trajectory-consistency scorer needs no human labels, so it can serve as a scalable consistency reward on hard and out-of-distribution data.

(c) Faithfulness metrics should pass a trajectory-corruption check before use. Evaluations should report a trajectory-sensitive metric alongside any plausibility judge, assess grounding and consistency jointly, and report uncertainty across independent clips.

(d) Audit logs should store raw waypoints synchronized with the rationale so consistency can be recomputed later. A model that declines to verbalize should be treated as non-compliant, and consistency checks on the executed trajectory can flag silent planner overrides in hierarchical stacks.

Edited on 16 Nov to match the revised PDF, since we believe that the progress solved most of the pending problems.

Thanks for preparing detailed feedback.

First, it is good to see that former and concurrent work was explicitly mentioned in the introduction and the list of contribution was refined further.

However, after further review, I didn't see significant changes to enhance the quality of the methodology or to further justify the manuscript's novelty.

Therefore, I have to say that weakness or concerns were only partially addressed, and I prefer to keep the current rating.

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

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