- Rating
- 3
- Confidence
- 3(+1)
- Informativeness
- 2
- Presentation
- 3
- Soundness
- 2
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Paper summary
This paper investigates how state-space curvature affects error accumulation in behavioral cloning. Using Jacobi-field analysis on constant-curvature manifolds, it separates the propagation of inherited state errors from the injection of fresh action errors. Under a local, direction-averaged oracle model with no state-dependent policy amplification, the authors derive a second-moment recurrence whose leading-order approximation exhibits three regimes: a bounded error floor under positive curvature, diffusive RMS growth in flat space, and exponential local amplification under negative curvature. The paper also provides conditional orientation bounds, studies action chunking at fixed decision/noise-injection counts, and proposes propagation diagnostics for learned policies. Validation includes controlled simulations on spheres, Euclidean and hyperbolic spaces, and SO(3), alongside learned-policy evaluations and a simulated 7-DOF Panda execution pipeline. The simulations support the recurrence within its local validity regime, while matched-one-step-error comparisons show that measured propagation response provides additional information about rollout performance.
Critical strengths
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Clear and quantitatively testable separation of two error mechanisms. The Jacobi-field analysis distinguishes inherited state-error propagation from fresh action-error injection, yielding different geometric coefficients for each. This provides an interpretable account of how curvature influences error accumulation under the stated local assumptions. Controlled simulations support the quantitative predictions, with reported second-moment agreement within approximately 3% on and . This strengthens my assessment that the proposed decomposition captures a meaningful mechanism rather than merely describing qualitative trends.
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Controlled evidence that propagation measurements complement one-step accuracy. The Panda evaluation extends the investigation to fully self-fed execution through inverse kinematics, joint servoing, and robot dynamics. Five matched policy pairs, repeated across three training seeds and checked on held-out calibration states, consistently associate lower measured amplification with lower rollout error. In a particularly close comparison, mean one-step errors are approximately 0.1074 and 0.1075 rad, while late-half tracking errors differ at 0.527 and 0.472 rad. These results substantiate the practical value of measuring propagation response alongside prediction accuracy and strengthen the paper’s relevance beyond its oracle model.
Critical weaknesses
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The learned-policy sensitivity diagnostic lacks sufficient justification and empirical support. The theoretical is defined intrinsically using parallel transport, whereas the experiments estimate a representation-space finite-difference sensitivity. Without a quantitative relationship between these quantities, comparisons against are difficult to interpret.
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The connection between the local geometric recurrence and long-horizon learned-policy behavior remains incomplete. The three regimes follow from a reduced recurrence under direction averaging, transported oracle actions, and conditionally zero-mean isotropic errors. The paper does not provide finite-horizon approximation bounds or conditions ensuring that the original process remains within the local regime. The large theory–simulation discrepancies reported in Appendix F illustrate why this matters. The learned-policy experiments provide useful supporting evidence, but the Panda comparisons hold geometry fixed and primarily establish the relevance of general propagation response. Consequently, the paper’s strongest practical results do not directly validate its curvature-specific quantitative predictions. This limits my assessment of how much the analysis establishes about error accumulation in actual behavioral cloning beyond the controlled oracle setting.
Questions for authors
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Clarification of the sensitivity diagnostic. How does the representation-space estimate of relate quantitatively to the intrinsic sensitivity defined in Section 3.1, and what makes comparisons with meaningful across representations?
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Clarification of the recurrence’s validity range. I understand that the three-regime result applies to the reduced local recurrence. Do the existing analysis or experiments provide a quantitative criterion, involving noise magnitude, step size, accumulated separation, and horizon, for when this recurrence accurately approximates the original process? Such a criterion would help assess the practical significance of the predicted error floor and exponential amplification, particularly given the discrepancies in Appendix F.
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Evidence connecting geometry to learned-policy behavior. Can the full-versus-clamped measurements in Appendix L quantify how much of the observed self-fed rollout difference is explained by geometric propagation and how much by policy response? In interpreting the learned-policy diagnostics, how are differences between calibration perturbations and actual rollout error directions and the evolving previous-action input accounted for? Analysis of the existing measurements would help establish the strength of the connection between the geometric theory and the practical results.
4 comments
I thank the authors for their detailed response and the additional analyses. Re-estimating policy sensitivity using decoded, parallel-transported tangent vectors, and dropping the unified cross-representation threshold comparison, has essentially resolved my concerns about the sensitivity diagnostic. Measuring along the true error directions on states actually visited by the learned policy also makes the connection between local propagation response and self-fed execution behavior clearer.
Regarding the validity range of the recurrence, the exact chord-distance recurrence and the exit-probability bound provided by the authors directly address my main concern. I will examine the theorem statements and proofs in the technical supplement more closely. I would like the revision to distinguish explicitly between two kinds of results: the global conclusions established for chord distance under the direction-averaged oracle model, and the conclusions established for geodesic error at a given radius and horizon. Concretely, do the present results guarantee that trajectories remain within the region where the local approximation is valid with high probability, or do they also control the contribution of trajectories that exit this region to the unconditional second moment of geodesic error, ?
As for the Panda experiments, the fact that the 15 matched policy pairs preserve identical rankings across different probing methods further supports the empirical value of the propagation diagnostic. I would also ask the authors to explain how the previous-action perturbation is constructed, in particular, whether its magnitude and direction reflect the action-history discrepancies that actually arise between the learner and the expert in self-fed execution. This response has substantially alleviated my earlier concerns; the remaining question mainly concerns the scope within which these quantitative conclusions apply to more general learned policies.
Follow-up Reply to Reviewer bUVB: Chordal vs. Geodesic Guarantees and the Previous-Action Probe
Thank you for the careful follow-up. We will make the following distinctions and the probe construction explicit in the revision.
1. Global moments and local validity. Under the direction-averaged oracle assumptions of "Technical Supplement, Part 1", the recurrence for is exact, with no small-error restriction. On , the exit-probability bound of Part 2 guarantees that trajectories stay within radius through horizon with the stated probability. By itself, it does not control what exiting trajectories contribute to the unconditional geodesic second moment.
We also obtain unconditional bounds on the geodesic second moment that include trajectories leaving the local region. Two of them are already in Part 2: on , when ; on , . The bound on is new. It uses only the identity of Part 1 and Jensen's inequality, with no further assumption. Let be the exact chordal second moment of Part 2. Since is an increasing convex function of , Jensen's inequality gives . Solving for gives
These bounds control the total second moment; they do not establish that the contribution from exiting trajectories is negligible. On with and (200,000 rollouts), the resulting bound on the geodesic RMS error is 1.00, 1.01, 1.05, 1.10, 1.08, 1.06 times the simulated RMS error at ; the corresponding RMS prediction from the reduced recurrence is 1.00, 1.02, 1.12, 1.57, 6.06, 35.6 times the simulated RMS error.
We do not claim a matching lower bound on . The small-error expansion connects the exact recurrence to the paper's reduced recurrence, whose accuracy is assessed numerically. The unconditional upper bound above remains valid beyond the local regime. In the revision, we will add this bound to the results of Part 2 and present three kinds of statement separately: the global chordal identity, the unconditional geodesic bounds, and the local results (the distance comparison within a radius and the probability of staying there).
2. Previous-action perturbation. Its direction is taken from the actual learner-expert history discrepancy in self-fed execution. Let be the learner's previous output, which is fed back as an input, and the expert's previous action encoded in the same policy-specific input representation. At probed states with tracking error rad, we perturb the end-effector orientation toward the expert by rad and, at the same time, replace by
The history input therefore moves along the observed discrepancy, by the same fraction as the state. This makes it a local probe, not a full-size replay of the discrepancy. The perturbed orientation is realized through IK, and the probe uses the same servo/MuJoCo execution chain as the original measurement.
This joint probe preserves the reported ordering in all 15 matched policy pairs. So does a full-amplitude version, in which the policy is executed from the expert's state with the expert's previous action as input. Both probes move the state and the history together, so they test whether the ordering holds, not how much the history input contributes by itself. We will describe this construction in the revision and present the consistent ranking as an empirical robustness check of the diagnostic on the tested policies.
3. Scope for learned policies. The quantitative theorems are for the direction-averaged oracle; for learned policies our claim is diagnostic. Within the modeled geodesic dynamics, the geometric step map conditional on the executed action applies regardless of how that action is selected; Appendix L's clamp test agrees with Remark 7 to within . The propagation response can also be measured through the full execution chain. The policy response is measured empirically rather than predicted by the oracle theory. The association between the measured propagation response and rollout-error rankings is empirical: the three model spaces of Appendix L, SO(3), and the Panda chain. The revised abstract, Section 4.5 and limitations will state this scope explicitly.
Thank you for the detailed follow-up and the additional analyses. The distinction among the global chordal identity, the unconditional geodesic upper bounds, and the local validity results clarifies the scope of the theoretical claims. The explanation of the previous-action perturbation, together with the consistent rankings under both local and full-amplitude probes, also addresses my question about how the diagnostic accounts for action-history discrepancies.
Overall, the rebuttal has largely addressed my concerns. I appreciate the explicit separation between the theoretical guarantees for the direction-averaged oracle model and the empirical evidence for learned policies, and I encourage the authors to incorporate these clarifications and the additional results into the revised manuscript. These responses strengthen my confidence in the paper, and I maintain my original rating.
Reply to Reviewer bUVB: Sensitivity Diagnostic, Validity Range, and Geometry in Learned Policies
We thank Reviewer bUVB for the careful review.
Please see Question 1.
The bounds are now available; see Question 2. We agree with how you divide the evidence: Panda supports measuring propagation, and the curvature-specific evidence on learned policies is the Appendix L experiment (pp. 29-30); see Question 3. We will move it into Section 4.5 and add "Local" to the title.
They cannot be compared against one threshold, so we drop that comparison. We re-estimated L as Section 3.1 defines it, from decoded tangent vectors after parallel transport (95th percentile). Across the 24 configurations, the intrinsic estimate is 0.27 to 2.5 times the representation-space estimate. The sensitivity-approximation trade-off remains in all four designs: for design A, the intrinsic L grows from 0.016 to 3.51 while the one-step geodesic error falls from 0.194 to 0.115 rad.
We will redraw Figure 6(a) with intrinsic quantities, report the measured β_emp, and move β_eff and L_crit to the appendix as diagnostic proxies.
Yes. In "Technical Supplement, Part 1" on this page, we state and prove, under direction-averaged oracle assumptions, an identity for the oracle process itself, with no remainder dropped and no small-error restriction, in the chordal distance χ_t = χ(e_t) defined there (close to e_t for small errors):
E[χt+12∣Gt]=aχt2+bfor every t, almost surely,
with explicit constants a = β_det + O(ε²) and b = σ²_noise ε² + O(ε³). The bounds below are proved in Part 2. The criterion has three parts:
For the error floor: under positive curvature (0 ≤ a < 1), E[χ_t²] ≤ b/(1-a) at every horizon. On S² with v = 0.3 and ε = 0.01, this chordal RMS floor is 0.0475, and the simulated geodesic RMS error is 0.0478.
Appendix F's discrepancies arise where the error is far outside such a radius. In chordal distance, the theory-to-simulation ratios for the five chunk sizes of Table 3 are 1.000, 1.001, 0.999, 1.001 and 1.008 (200,000 rollouts each). We will add the theorem to Section 3.3 and a chordal row to Table 3.
At the level of one step, yes. From the Appendix L runs at v = 0.3 (the clamp and contrast rows are new numbers from these runs; the contrast is taken per condition):
The clamped values differ across manifolds as the geometry predicts, while the full-minus-clamp contrast is similar on all three. The contrast is a signed response that includes geometry-policy interaction, not an additive share.
Over many steps the two interact, so we report the rollout outcome rather than a percentage split. The fixed-history amplification describes how an inherited error propagates locally, while a self-fed rollout also keeps adding prediction error and changes in the history input; an amplification below 1 therefore does not exclude threshold crossings. At matched one-step error, 42% / 58% / 94% of fully self-fed trajectories on S² / R² / H² cross the error threshold 1 within 150 steps.
Along the actual rollout error direction, at learner-visited states, the amplification keeps S² < R² < H² in all five error groups (0.944 to 0.990, 0.978 to 0.993, 1.015 to 1.030).
For the previous-action input, on Panda (60 held-out test trajectories), all 15 matched pairs keep the order of their self-fed late-half errors under four probes, including the actual error direction and a perturbed previous action. We will add these analyses to Appendices L and M.