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Desk rejected at ICLR 2027

Identifying the Appearance–Kinematics Trade-off in Cross-Embodiment Transfer

Desk rejected at ICLR 2027, so left out of the paper lists and the map.

Abstract

Cross-embodiment robot learning rests on a premise almost never stated: a difference in embodiment is a difference in capability. Vision falsifies it, and two recent studies that look closely disagree about how. Neither defines a distance on both axes, so their conclusions cannot be placed on the same plot. We argue that this is not an oversight. Splitting transfer loss into an appearance part and a kinematic part requires a robot whose silhouette is held fixed while its skeleton changes, and no such robot can be built: a real robot's outline is the outer surface of its collision body. Under any distribution over real hardware the required counterfactual has probability exactly zero, so the mediation quantities are not merely noisy but unidentified, and more robots do not help. We separate two structural causal models. In nature's, a manufacturing constraint forces appearance to follow collision geometry; in the simulator's it does not, and building a simulator is in causal terms the deletion of that one edge. We prove that the estimands defined on the first model are identified by four interventions on the second. Those interventions form a strict , and its two off-diagonal cells—the only ones that pull the two axes apart—are exactly the two no hardware can realise. We give a protocol that builds them: a procedural shell generator, material and silhouette dose families calibrated once and then frozen, and field-level assertions that cells sharing a skeleton are bit-identical in physics. The answer is reported in units a reader can hold, how many percent of link length one just-noticeable difference of appearance is worth. That number is not a constant but a function of the task's contact tolerance: appearance is worth a few percent of link length where the task tolerates centimetres and about one percent where it tolerates millimetres, with an interaction term too small to make the dichotomy ill-posed.

Primary area:
applications to robotics, autonomy, planning
Keywords:
cross-embodiment transfer, robot learning, causal identification, causal mediation analysis, visual imitation learning, domain randomization

Reviews

Among:
Shape:
1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_jV13OpenReview ↗
Rating
3
Confidence
4
Informativeness
3
Presentation
3
Soundness
3
Read review
Paper summary

This paper investigates how robot appearance and physical morphology affect the transfer of frozen visuomotor policies. It introduces a strict 2x2 simulator design that independently assigns collision and visual geometry, identifies mediation contrasts under explicit assumptions, and estimates a local exchange rate between material appearance and kinematic changes.

Critical strengths
  • The research question is very relevant. Understanding whether transfer failures arise from visual differences or changes in physical execution can inform the choice of adaptation methods.

  • The statistical design contains thoughtful elements. Paired scene seeds, uncertainty at the skeleton level, Fieller sets for slope ratios, and equivalence margins are appropriate choices in principle. The reported architecture and second-simulator experiments also broaden the evidence.

Critical weaknesses
  • The study is conducted entirely in simulation and assumes a fixed action and proprioceptive interface across embodiments. While this controlled setting is well motivated for isolating appearance and kinematic effects, it remains unclear whether the measured trade-off and the resulting conclusions generalize to real-world cross-embodiment transfer, where robots may differ simultaneously in control interfaces, sensing, dynamics, and other factors.
Questions for authors
  • How are the logit coefficients in Equation 19 converted into the percentage-point predictions in Equation 21? Please provide the fitted coefficients, relevant operating-point probabilities, and the calculation producing the 5.0% boundary.

  • Could the authors provide visualizations or qualitative examples of failure cases? Such examples would be helpful for understanding how appearance and kinematic differences lead to policy failures in practice.

2 comments

We thank the reviewer for recognizing the relevance of our research question and the rigor of our experimental and statistical design. We clarify the scope of our findings and address the two technical questions below.

1. Generalization to real-world transfer. Our study deliberately fixes the action and proprioceptive interfaces to isolate appearance and kinematic effects without introducing additional confounding factors. This controlled setting is essential for identifying the proposed causal contrasts. Our conclusions concern transfer sensitivity within this explicitly defined intervention space, rather than unrestricted transfer across heterogeneous robot systems. The architecture and second-simulator experiments provide additional evidence of robustness under controlled conditions. Real-world validation involving heterogeneous control interfaces, sensing modalities, and dynamics remains an important direction for future work.

2. Logit coefficients and the 5.0% boundary. Eq. (19) estimates success probabilities using a logit link, whereas Eq. (21) predicts residual gaps in percentage points. Specifically, given the success probability p0p_0 at the operating point, the kinematic sensitivity slope is converted to the percentage-point scale as:

βppkin=100p0(1−p0)(βkin+η2τ~)\beta_{pp}^{kin}=100p_0(1-p_0)(\beta^{kin}+\eta_2\tilde{\tau})

where η2τ~\eta_2\tilde{\tau} represents the interaction with contact precision.

For appearance randomization covering both material and silhouette variations, the remaining predicted transfer loss is attributable to kinematic changes. Under the prespecified tolerance threshold of 5 percentage points, the boundary is calculated as:

dboundarykin=5∣βppkin∣d_{boundary}^{kin}=\frac{5}{|\beta_{pp}^{kin}|}

The reported boundary is approximately 5.0% of link length. We will provide the fitted coefficients, predicted success probability at the operating point, and explicit numerical substitution in the revised manuscript to make this calculation fully reproducible.

3. Qualitative failure cases. We will add representative policy failure cases in the revised manuscript to visually illustrate how appearance and kinematic differences affect policy behavior and task success.

Reviewer_jV13OpenReview ↗

Response to Authors' Rebuttal

I have read the authors' response and the other reviewers' comments, and revisited the paper. I acknowledge the motivation for using simulation to isolate appearance and kinematic effects. However, this setting inherently limits our ability to assess whether the findings hold on real robots, which is particularly important for robot learning. Therefore, I will maintain my original rating.

Reviewer_WdSHOpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
1
Soundness
1
Read review
Paper summary

The authors propose a strict 2×2 simulator that independently varies collision geometry and silhouette, enabling counterfactual separation of embodied capability from visual-policy input. Under stated assumptions, the four cells identify natural mediation estimands. Simulations yield a pooled appearance–kinematics exchange rate of 1.50, with a −1.3 pp interaction within the ±5 pp margin, indicating the tradeoff depends on task contact precision.

Critical strengths

None

Critical weaknesses
  • Poor readability and unclear writing: The paper is overloaded with undefined jargon such as “cross-embodiment transfer,” “2×2 simulator design,” “procedural shells,” and “source-calibrated frozen dose families.” It is neither precise nor accessible, and reads like unedited agent-generated text rather than polished academic writing.

  • Unclear motivation and weak experimental positioning: The introduction does not focus on a single core challenge or clearly motivate the proposed method, and the experiments lack comparisons with any baselines. As a result, the work feels more like an undergraduate course project than a top-conference paper.

Questions for authors

I think my assessment will not be changed based on the weaknesses

2 comments

We thank the reviewer for their feedback. We would like to clarify several points.

Motivation and contributions. Our paper addresses a specific causal identification problem: separating the effects of robot silhouette and physical geometry on visual-policy transfer. The 2×2 design provides counterfactual interventions unavailable on physical hardware, enabling identification of mediation effects under explicitly stated assumptions.

Experimental evaluation. Contrary to the reviewer's concern, our experiments include comparisons with existing transfer methods (Section 5.5), multiple policy architectures, positive and negative controls, and robustness analyses. These evaluations directly assess the proposed framework and its practical implications.

Presentation. We acknowledge that the technical terminology may increase reading difficulty and will improve the clarity of the introduction and methodological explanations.

We would appreciate specific technical concerns regarding the identification assumptions, experimental design, or statistical analysis, as these would allow us to provide a substantive response.

Reviewer_WdSHOpenReview ↗

Thanks for the response, but my concerns remain.

Thank you for the clarification. I noticed that the other two reviewers were positive about the paper, whereas my assessment was substantially less favorable. Given this difference, I carefully reread the abstract and introduction. My original concerns remain.

First, I still find the paper difficult to follow.

Assessment after reading the Abstract

Even with my background in vision-language-action (VLA) models, I found the opening phrase “cross-embodiment transfer” ambiguous. What exactly is being transferred? Is it a control policy from one robot to another, data collected on one robot for use on another, or something else? A technical paper should define its central terms precisely, and I expect readers outside the immediate research area to find this opening even harder to follow.

The next sentence refers to “separating these effects,” but which effects does this refer to, and why is it important to separate them? The abstract then introduces a “strict 2×2 simulator design.” What are the two factors and their levels, and what makes the design “strict”? The phrases “counterfactual interventions” and “under the stated identification assumptions” also appear before the abstract explains what the interventions are or which assumptions the result depends on. A good abstract should make the research question and the core idea accessible to readers across the broader field, including those outside this particular area.

Assessment after reading the Introduction

On rereading the introduction, I still had the impression that it read like text generated by an LLM-based agent with little human editing. That is an impression about the writing. My concrete concern is that the logical connections between sentences are weak. The opening paragraph moves from defining cross-embodiment transfer to discussing visual policies, matched-data experiments, and changes in the color of a robotic arm. Each example may be relevant, but the paragraph leaves the reader to infer how the examples relate to one another and how they lead to the final measurement question.

The second paragraph introduces three concepts in quick succession: surface material, visual silhouette, and collision geometry. It then says that “both” change along the hardware manifold. The intended pair appears to be silhouette and collision geometry, but the text should name them explicitly. The next sentence introduces “the two missing contrasts” before establishing which comparisons are available and which ones the study still needs. As a result, it is difficult to see why those two particular contrasts are missing or why they are necessary.

Second, I remain unconvinced by the technical contribution. My reading of the first two paragraphs is that they motivate cross-embodiment transfer as a broad problem and point to missing experimental contrasts. The third paragraph then states that “four simulator interventions supply the missing contrasts.” The paper constructs these conditions and reports what it observes. However, the introduction frames the transfer problem so broadly that I still cannot identify the specific technical problem the paper solves or what the proposed method contributes beyond constructing and evaluating the controlled comparisons. This is the second weakness I raised in my original review.

After carefully rereading the abstract and introduction, my assessment remains unchanged. My overall impression is that the paper relies heavily on technical terminology without defining key concepts precisely. It does not clearly identify a specific problem it aims to solve, and I do not see a clear methodological novelty or technical contribution. In my view, the manuscript requires substantial and careful revision by the authors before it is ready for publication.

Reviewer_S6mvOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
2
Soundness
3
Read review
Paper summary

The paper asks how much of the cross-embodiment transfer loss of a visual policy comes from the robot’s changed appearance versus its changed kinematics. It argues that hardware panels cannot answer this, because every buildable robot’s silhouette is a deterministic function of its collision body (v = h(c)). That makes the off-diagonal contrasts a positivity failure rather than a sample-size problem.

Using MuJoCo’s independent collision, visual and material fields, the authors construct a 2×2 design of source, swap and two chimeras. They show that it identifies PNIE, TNIE, CDE(m) and INT under stated assumptions, including (A4): the simulator and the natural outcome mechanism coincide off-manifold. They define a local exchange rate χ^phys = β^app/β^kin in percent of link length per appearance JND, and report 1.50 [1.09, 2.11] pooled. The rate decreases with contact precision: 2.71 for low-precision tasks and 0.84 for high-precision tasks. Fitted slopes are used to predict residual gaps of existing transfer methods and to establish a sufficiency criterion for appearanceation.randomiz

Critical strengths
  1. Clear, correct causal framing. The point that the hardware panel violates positivity is well made (Prop. 1(v), Fig. 1a). So is the observation that, with a deterministic and known mediator, natural effects reduce to single-world cell contrasts without cross-world assumptions. Prop. 1(iii) is a useful and honest correction of a common intuition: fixing v and t does not isolate physics, because configuration changes the pixels. The replay and frozen-observation arms (Eq. 5) are a thoughtful way to split that residual channel.

  2. Engineering rigor. The invariance assertions in App. F are exemplary:

  • 25 physics arrays checked bit-for-bit,
  • contact properties matched by geometry name rather than index,
  • closure of the routes by which visual geometry could reach the dynamics, such as the fluid model and rangefinders.

The Helmert extent/shape split and the equal-density torque-scaling argument show real care about confounds.

  1. Statistical practice. The paper reports:
  • preregistered tiers,
  • three co-primary estimators,
  • an explicit Fieller case analysis with the angular form ϑ for weak denominators,
  • TOST for every null claim,
  • positive controls that must reach a large effect size,
  • inference clustered at the skeleton level, with an honest effective-cluster count.

The numbers I checked are internally consistent: Table 5 cell means against the contrasts, the identity CDE(m_s) = β^phys + execution gap + configuration term (−20.6 − 1.7 − 3.1 = −25.4), the Table 8 bounds against the oracle and K4, and the Table 4 predictive values.

  1. Prevalence-aware validation. Reporting predictive values at declared deployment prevalences, with decision curves, and stating plainly that the criterion is “a good screen and a poor confirmation,” is commendable.

  2. Candor about scope. (A4) is stated as a numbered assumption rather than hidden in the word “twin,” and the limitations section is direct.

Critical weaknesses
  1. The headline result does not use the paper’s central identification device. χ^phys is β^app/β^kin, where β^app is the slope in the material distance d^app (a colour-only dose family). Material can be varied on hardware (T_L1 is “buildable”), and the kinematic slope is a regression on d^kin. As far as I can tell, neither requires the off-manifold chimeras K2 and K3. Those cells deliver PNIE/TNIE/INT and β^L2, which do not enter χ. Yet Table 1’s caption calls the mediation contrasts the ones χ “is built from,” and the abstract and introduction present χ as the payoff of the 2×2. Either the authors should explain precisely how the chimera cells enter χ, or reframe: the 2×2 decomposition (PNIE vs CDE) and the exchange rate are two separate contributions, and the second does not need the first. Relatedly, silhouette arguably matters most to policies (cf. the black-only results of Lepert et al.), yet it is excluded from the “appearance–kinematics trade-off.”
  2. What do the chimeras look like, and what does PNIE measure? Under axial link scaling, K2 attaches shells generated for the target’s link lengths onto the source skeleton’s body frames, and K3 does the reverse. The visual links would then appear to extend past or fall short of the next joint, and the visible end-effector may be offset from the true gripper. If so, PNIE may largely measure the policy’s response to an implausible, broken-looking robot rather than a “silhouette effect” with natural-model meaning.
  • Please show renders of K1–K4 for several skeletons.
  • Please explain how shells are attached across mismatched frames.
  • Please quantify the visual offset of the end-effector between K1 and K2.
  1. Untested external validity, despite an available test. All results are simulated, with procedural shells that the authors acknowledge are less photorealistic. The natural-model interpretation rests on (A4), which cannot be checked here. The material-axis hardware test (App. M.1) would at least partly check whether the slopes transfer, and it directly targets the numerator of χ, but it is only proposed. In addition, App. J.4 says that preregistered external calibration predicates (e.g., that the predicted material response must contain the Li et al. 2024 gift-wrap drops) have a status that “remains to be verified.” In a preregistered study, a predicate that was dropped or not executed should be reported as a deviation, with reasons.

  2. The contact-precision claim is thinly supported.

  • Strata contain two tasks each, so contact precision is confounded with task identity: Lift/Can vs. the two NutAssembly tasks differ in horizon, object geometry and sub-task count.
  • The low and medium Fieller sets overlap heavily.
  • “Low excludes 1, high does not” is not a test of a difference between strata.

Eq. (19) contains the η₁, η₂ interaction terms with τ^prec; please report their estimates and tests, or a direct test of the trend in χ or ϑ across τ^prec. The 7% bootstrap sign-flip rate for β^kin at the low-contact end also suggests the 2.71 estimate is fragile.

  1. Scale of the slopes in the residual-gap predictor. Eq. (19) is a logit model, but Eq. (21) sums β̂_j d^j and compares the result to a 5 pp margin. Are the β̂_j here probability-scale marginal effects at d₀? If they are linear extrapolations of local slopes to the farthest pairs, the predictor should be expected to overestimate large gaps, which is what the 0.61 calibration slope shows. Also:
  • The calibration regression uses 7 methods.
  • Three different methods (B2, B3, B13) receive the identical prediction of 20.6 while measuring 17.2–25.5, so the predictor’s resolution is limited.
  • Sensitivity and specificity come from only 3 held-out skeletons, one sharing a design family with a training skeleton. Intervals such as [0.71, 0.95] look narrow for a 3-cluster bootstrap; please state the unit of resampling.
  1. The JND unit. Anchoring the numerator in human 2AFC discriminability is motivated as making χ comparable across papers. But it is unclear why human perceptual thresholds are the right unit for a policy’s sensitivity, and the claimed comparability across papers is not demonstrated. Reporting χ also in d^app units (DINOv2 cosine), alongside the JND conversion factor and its uncertainty, would help. Is the JND’s estimation error propagated into the Fieller set?

  2. Ambiguity about which kinematic operator yields β^kin. Is the d^kin slope estimated on synchronized swaps (T_kin^sync, which also changes the silhouette) or on frozen-geometry variants? If synchronized, β^kin partly absorbs silhouette effects, and the adjustment through the d^L2 covariate relies on a linear-additive specification with r(d^L2, d^kin) = 0.31.

  3. Presentation. The main text is very dense, and much of the substance sits in a 37-page appendix. Notation (θ, K1–K4, β^phys, χ, χ^phys, ϑ, R̂) accumulates quickly. Some figure annotations and captions read as informal or overclaiming, e.g., Fig. 7’s assertion that the chimera cells “have not been measured before.” Prop. 1(i)–(iv) is largely algebra once the deterministic mediator is granted. That is fine, but it could be presented more compactly, with the space used for weaknesses 1–2.

Questions for authors
  1. Precisely how, if at all, do K2 and K3 enter χ^phys? Could χ^phys be estimated identically without them?
  2. Can you provide renders of the chimeras and describe how shells are attached when link lengths differ?
  3. Which kinematic operator generates the d^kin variation in Eq. (19)?
  4. What are the estimates and tests of η₁ and η₂? Is there a formal test of the stratum ordering, with Holm correction as preregistered?
  5. On what scale are the β̂_j in Eq. (21)?
  6. What is the status of the J.4 external calibration predicates? Were they executed, and if not, why?
  7. Can the anonymized preregistration manifest hash or timestamp be shared with reviewers?
  8. Is uncertainty in the JND estimate propagated into the χ^phys interval?

Minor

  • Table 6’s companion margin (4.0 pp) differs from the 5 pp TOST margin. N2 (frozen encoder) passes the latter but not the former; please clarify which governs.
  • Several cited works are recent preprints from 2026; please make sure all are publicly available.
  • Clarify whether the pilot skeletons overlap with the evaluation panel.
1 comment

We thank the reviewer for recognizing our causal framework, engineering rigor, and statistical methodology. We clarify the relationship between our contributions, the chimera construction, and the interpretation of our results.

1. Four-cell design and exchange rate. Our work makes two complementary contributions. The four-cell design identifies silhouette-mediated and controlled direct effects (PNIE, TNIE, CDE), which require K2 and K3. Separately, χphys\chi^{\mathrm{phys}} quantifies local sensitivity to material appearance versus kinematic perturbations without requiring these cells. We will revise the abstract and Table 1 caption to distinguish these contributions and clarify that the exchange rate concerns material appearance rather than all visual factors.

2. Chimera construction and PNIE. Chimeras are constructed within the same skeleton through axial link scaling (Appendix C.2), not by transplanting meshes between different robots. Link correspondence is therefore an identity mapping. Procedural visual shells use convex offset surfaces and joint-bridging spheres, independently assigned from collision geometry. Their mismatch in K2/K3 is intentional. PNIE measures the effect of replacing the silhouette while holding source physics fixed, conditional on A4. We will provide K1–K4 renders across multiple skeletons.

3. External validity and preregistration. Our invariance checks establish intervention correctness within simulation, not real-world validity of A4. The hardware material test in Appendix M.1 is a proposed partial validation, not completed evidence. We will clarify the execution status and any deviations concerning Appendix J.4's external calibration predicates, and provide an anonymized preregistration manifest hash or timestamp (Appendix K).

4. Contact precision. Contact precision τprec\tau^{\mathrm{prec}} is independently measured through perturbation tolerance, rather than assigned by task identity. Exchange-rate estimates decrease across the three preregistered strata (2.71, 1.59, 0.84). Confidence intervals crossing unity do not test between-stratum differences. Eq. (19) specifies interaction terms η1,η2\eta_1,\eta_2 for formal trend analysis with Holm correction. Given two tasks per stratum and the wider low-precision Fieller interval, we restrict conclusions to the observed trend within this task panel.

5. Residual-gap prediction. Eq. (21) expresses predictions in success-rate percentage points, requiring probability-scale marginal effects at the operating point rather than raw logit coefficients from Eq. (19). B2, B3, and B13 share predictions because the model represents perturbation-axis coverage, not method-specific mechanisms. The 0.61 calibration slope reflects limitations of linear extrapolation. We will clarify bootstrap resampling and interval construction for the three held-out skeletons, emphasizing screening rather than precise prediction.

6. JND interpretation. JND provides an encoder-independent reference scale through a 2AFC experiment at 75% discrimination accuracy; it does not assume human-like policy perception. We will additionally report χ\chi in DINOv2 cosine-distance units dappd^{\mathrm{app}} and the JND conversion factor. Cross-paper comparability is a motivation, not an experimentally established conclusion. We will also clarify how JND estimation uncertainty is handled in the Fieller interval.

7. Kinematic slope. Axial scaling (Appendix D.4) jointly modifies link offsets, collision geometry, visual meshes, and dynamics. Eq. (19) includes dappd^{\mathrm{app}}, dL2d^{L2}, and dkind^{\mathrm{kin}}; thus, βkin\beta^{\mathrm{kin}} is a conditional slope adjusted for measured silhouette changes, not an unadjusted swap effect. The correlation r(dL2,dkin)=0.31r(d^{L2},d^{\mathrm{kin}})=0.31 and maximum VIF of 1.42 indicate limited collinearity, without eliminating model assumptions. We will clarify the intervention samples used.

8. Presentation and minor clarifications. We will simplify Proposition 1, improve chimera illustrations and notation, and moderate unsupported claims. The preregistered TOST margin is ±5 pp; 4.0 pp is an auxiliary sham-based noise reference, so N2 (Frozen Encoder) passes the formal criterion. Appendix K.3 confirms that pilot skeletons and cells overlap with the evaluation; we will clarify their procedural-validation role and verify accessibility of recent preprints.

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