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Under review as a conference paper at ICLR 2027

Memorize, Adapt, Ignore: Diagnosing Robot Learning Mechanisms under Training Data Variation

Abstract

Training data variation, whether through designing a domain randomization (DR) scheme in simulation or curating demonstrations for imitation learning, is a primary lever for improving the robustness of robotic manipulation policies. Yet its underlying mechanisms remain poorly understood, and practitioners typically select randomization parameters through expensive trial and error. We investigate these mechanisms through a series of case studies, randomizing object size, color, and type as well as scene lighting and linguistic prompts across settings including pick-and-place RL in ManiSkill and fine-tuning of vision-language-action (VLA) models on LIBERO and RoboTwin. We examine both model behavior and internal representations, using the empirical neural tangent kernel (NTK) as our primary diagnostic tool. We show that the NTK distinguishes a shift in the internal learning mechanism from different situations with insufficient variation (e.g. learning what to do for a large cube, and what to do for a small cube) to to the situation at hand with sufficient variation. An NTK-based signal-to-noise ratio also helps distinguish when policies have learned to task-irrelevant factors (e.g. treating blue and red cubes identically, instead of learning a blue sub-policy and a red sub-policy). We use these diagnostics to develop practical guidance for designing DR schemes, selecting models, and detecting shortcut learning. We further compare different kinds of representations and validate our findings with real-world hardware experiments using ACT-based imitation learning.

Primary area:
applications to robotics, autonomy, planning
Keywords:
robot learning, robotic manipulation and grasping, foundation model, domain randomization, neural tangent kernel

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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_gzpfOpenReview ↗
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Paper summary

This paper provides diagnostics for understanding how training-data variation affects robot policies. Using empirical NTKs, factor-sensitivity ratios, signal-to-noise ratios, effective rank, and CKA, it characterizes policies as memorizing, adapting to relevant variation, or ignoring irrelevant variation. The diagnostics are conducted across a toy visual task, ManiSkill RL, ACT imitation learning, VLA policies, and a small hardware lighting experiment.

Critical strengths
  • The paper looks beyond task success rates and asks what mechanisms might explain why data variation improves or fails to improve robustness. The use of the NTK has a clear local interpretation in terms of how an update on one probe affects another.
Critical weaknesses
  • Memorize, adapt, and ignore are operational interpretations of kernel structure and ratios, but the paper does not establish that these are unique or causal learning mechanisms. The measures can depend on the chosen probes, factor parameterization, checkpoint, and representation. Strong correlations do not by themselves validate the mechanistic interpretation.
  • The practical predictive claim is supported by a limited set of tasks and factors. The VLA model-selection example covers three models under lighting perturbations, while the hardware study has one task and ten trials per condition. It is unclear how reliably the metrics generalize to new tasks, nuisance factors, or probe distributions.
Questions for authors
  1. How stable are the proposed regime labels and FSR/SNR trends across training seeds, probe sets, and alternative factor parameterizations?
  2. Can the authors validate the diagnostic on additional tasks or factors where probe construction is not closely matched to the evaluation distribution?
  3. What is the real-world trial protocol and uncertainty for the hardware lighting result, and do the diagnostics predict performance on conditions not used to construct probes?
3 comments

We thank the reviewer for the insightful feedback.

W1 (mechanistic interpretation / causality) We agree with the reviewer that “memorize / adapt / ignore” are operational descriptions of kernel structure, not proven unique or causal mechanisms, and that the term “mechanism” can overstate this. Our goal is a diagnostic: a way to tell, without rollouts, how a policy treats a factor of variation. For this purpose, a reliable association between the kernel statistics and policy behavior is what matters, and we do not claim that the regimes cause robustness.

Our revised introduction defines each regime in terms of what the kernel shows: “memorize” means different values of a factor form separate clusters, “adapt” means they share a common structure, and “ignore” means the representation is relatively insensitive to that factor. We will state in the limitations that the statistics depend on the probe design, factor parameterization, checkpoint, and representation.

We also note two points that support the diagnostic use. First, the training data variation is controlled (e.g., the N_color sweep, confounded vs. independent variation, and the step-matched control in Fig. 4b), so changes in the statistics follow from a deliberate change in the data. Second, Appendix A.2 shows that eNTK similarity predicts how a gradient step on one input changes the output on another (ρ = 0.97 ± 0.06), whereas activation similarity does not (best layer ρ = 0.22 ± 0.28). This gives the kernel a direct, local interpretation in terms of training transfer.

W2 and Q1 (scope and stability of the predictive claims) We thank the reviewer for this fair comment. We agree that the evidence for the predictive use of these metrics is limited. In particular, the VLA model-selection example covers only three models, and the hardware study covers one task with ten trials per condition. We view these as supporting evidence rather than conclusive validation.

Our goal is to introduce the “memorize, adapt, ignore” framework as an initial step and to draw attention to an underexplored connection between representation-kernel metrics and the learning mechanisms of robot policies. Establishing how reliably the metrics generalize across all tasks, nuisance factors, and probe distributions would require a more extensive study than this paper provides.

To address stability (Q1), we report the following:

Seeds. Every ACT result (Tables 1 and 2b) is a 3-seed mean, and the SNR orderings hold in every seed; we will add the standard deviations. The toy sweep uses 10 independent color subsets per N_color, each with its own seed, and the SNR trend and its Spearman correlation with OOD success (ρ = 0.92 over 80 runs) are computed across all of them. The RL, RoboTwin, and hardware policies are single runs, and we now state this explicitly.

Probe sets. Fig. 3b already reports mean ± std over 5 disjoint probe groups. On a second ACT probe grid and on separately rendered bimanual probes, the metric magnitudes shift but every ordering is preserved.

Factor parameterization. Our framework does not fix how a factor is parameterized. A probe set is defined only by the factor of interest, with all other inputs held fixed, and it can be drawn from the training distribution, from the OOD evaluation distribution, or from outside both. For example, the hardware probes are synthetic lightness perturbations of training frames, while the evaluation uses real lighting changes. A formal, structured treatment of how to specify and choose probe parameterizations is beyond the scope of this paper, and we leave it to future work.

Beyond this, the experiments span a wide range of settings: a toy illustration, RL with CNN policies, imitation learning with transformer visuomotor policies, VLA applications (model selection and shortcut detection), and hardware validation. Across these, the kernel metrics consistently distinguish different learning behaviors. We believe this breadth supports our core claim that kernel metrics are a useful diagnostic for robot learning, even though each individual setting has limited coverage.

Following the reviewer’s feedback, we have rewritten the introduction to clarify the motivation and scope. We have also added these concerns about limited coverage to the limitations section.

Q2 (probe construction different from evaluation distribution) Our probes are defined by the factor of interest alone, and in three of the paper's experiments they are drawn from neither the training nor the evaluation distribution; we will make this explicit in the revision.

  • Toy CNN (Fig. 1). Policies are trained on discrete subsets of a 27-color palette, while OOD evaluation uses continuous color randomization together with randomized object scale, background and surface texture. The SNR probes are 5 fixed palette colors at 3 states, i.e. a different color set from training and a different distribution from evaluation. Across all 80 runs (8 values of N_color x 10 subsets), Spearman correlation between SNR and OOD success is 0.92.
  • Hardware ACT (Fig. 6, Table 3). Probes are synthetic brightness/contrast/gamma edits of validation frames. Evaluation is physical lamp changes on the real robot. The SNR gap (2.5 vs 5.5) tracks the measured success gap (1/10 vs 8/10 bright, 1/10 vs 6/10 dark).
  • VLA model ranking (Fig. 3). Probes are RGB-multiplier edits of LIBERO frames, while the validation target is LIBERO-plus's Light suite, whose perturbations are applied inside the simulator by the benchmark authors.

Q3 (hardware protocol and uncertainty) Probe construction. Probes are built from training-episode frames by applying synthetic lighting changes (brightness, contrast, and gamma; Fig. 6b) with standard image processing. Probe construction therefore uses only held-out validation data and does not involve the test lighting.

Real-world evaluation. We evaluate an ACT cube pick-and-place policy under three lighting conditions: Base (matching the training distribution), Bright (OOD), and Dark (OOD). The OOD conditions are produced by changing the physical lights in the lab (Fig. 7). Each condition is evaluated over 10 trials, comparing a baseline policy against a policy trained with Lightness DR. These real lighting conditions are unseen in both the training data and the probe construction, so the diagnostic is tested on conditions it was not built from. The training SNR rises from 2.5 to 5.5 with Lightness DR (Fig. 6a), consistent with the real-world gains: OOD success improves from 1/10 to 8/10 (Bright) and from 1/10 to 6/10 (Dark), and in-distribution success improves from 6/10 to 10/10 (Table 3).

Uncertainty. With only 10 trials per condition, the uncertainty in the success rates is substantial. We therefore view this study as a consistency check on one comparison between two policies, not as statistical validation of the diagnostic’s predictive power. We will state this explicitly in the limitations section.

Thank you for the response. I maintain my score.

Reviewer_RtMUOpenReview ↗
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3
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Paper summary

This paper proposes a representation-kernel-based diagnostic framework to investigate how training data variation affects robot learning. Using eNTK, effective rank, SNR, and CKA, the authors aim to distinguish three learning mechanisms: Memorize, Adapt, and Ignore. Experiments cover RL policies in ManiSkill, ACT-based imitation learning, and VLA models on LIBERO and RoboTwin, with additional real-world robot experiments. The results suggest that these metrics can help assess OOD robustness and guide DR strategies.

Critical strengths
  • The problem is well-motivated. While existing DR research often evaluates generalization through success rates, this paper aims to understand how training data variation affects a model's internal learning mechanisms. This provides a useful perspective for analyzing robot policy robustness.
  • The experiments cover a reasonably broad range of settings, including RL, imitation learning, and VLA models on ManiSkill, LIBERO, and RoboTwin, as well as real-world robot experiments. These results provide some evidence that kernel-based diagnostics can be useful across different learning settings.
Critical weaknesses

My main concern is whether eNTK offers sufficient practical advantages over simpler diagnostic methods. While the paper emphasizes that kernel-based diagnostics can assess generalization without extensive evaluation rollouts, computing eNTK can also be expensive, especially for large VLA models. Furthermore, constructing controlled probe sets requires prior knowledge of task-relevant and task-irrelevant factors. Without a clear comparison of computational cost and diagnostic performance against simpler alternatives, it is difficult to assess the practical benefit of the framework.

Questions for authors
  1. For large VLA models, what are the computational and memory costs of eNTK evaluation? Can the authors compare its cost and diagnostic performance against simpler alternatives, such as action consistency or hidden-feature sensitivity?
  2. Can the authors provide more direct task-level evidence for the shortcut learning analysis? When the visual-language correlation is broken, does a reduction in scene-to-language FSR consistently correspond to improved OOD generalization?
1 comment

We thank the reviewer for the careful feedback.

W1/Q1 (eNTK comparison)

Thank you for this helpful comment. We agree that our original abstract and introduction were misleading in placing a strong focus on eNTK. We have revised the framing: the contribution is a representation-kernel framework (effective rank, FSR/SNR, CKA computed on a chosen kernel), and eNTK is one instantiation of it. We do not claim eNTK is the best choice.

We use eNTK as the default for two reasons. First, it has a direct interpretation for training: it describes how a gradient step on one sample changes the prediction on another. In Appendix A.2, eNTK similarity predicts measured transfer with ρ = 0.97 ± 0.06, versus 0.22 ± 0.28 for the best activation layer. Second, it aggregates information across layers, so it avoids the blind spots of single-layer kernels.

On cost, we compute eNTK only over LoRA adapter parameters and on small probe sets (e.g., 80 grasp-frame probes), with no policy rollouts. The added computation is therefore modest.

Finally, the Representation Kernel Comparison section (Sec. 4, Table 2) evaluates last-hidden and output kernels within the same framework. In practice, they can work well. For example, last-hidden and eNTK both detect the alleviated shortcut at 10/10 checkpoints, and the output kernel is best for head-specific structure in the bimanual task. Since they are much cheaper, the kernel can be chosen case by case. We have made this clearer in the revision.

Q2 (shortcut OOD test)

The scene-to-language FSR measures the policy’s relative sensitivity to scene versus instruction. Its Stage 2 drop shows the scene no longer dominates the instruction once the correlation is broken. The new factor-specific decomposition (linear CKA between the eNTK and scene/language label kernels, new appendix figure) shows that relative to the Stage 1 mean, language CKA rises to 4.3× in Stage 2 (2.1× in the step-matched control) while scene CKA stays within 0.9 to 1.1×.

In the bottle setup, the only possible OOD test is a scene-instruction pairing the policy has never seen, and succeeding there requires compositional generalization: knowing what “shake” means on a bottle it has only ever lifted. Whether a policy has that depends on its language grounding from pretraining, on the architecture’s language pathway, and on how much instruction diversity the fine-tuning data covers. None of those are controlled by the Stage 2 intervention, which only removes the visual shortcut. So removing the shortcut is necessary for instruction-conditioned generalization, not sufficient, and the diagnostic measures the necessary part. We will state this scope explicitly.

For task-level evidence that breaking a confound improves OOD generalization, Figure 5 provides it on a task where OOD evaluation is defined: novel-category action error 0.0755 vs 0.0846 for independent vs confounded variation at equal data budget.

Reviewer_mqFpOpenReview ↗
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Paper summary

This paper investigates how training-data variation shapes robot policies’ representations and generalization. The proposed framework combines controlled probes with representation kernels, primarily the empirical neural tangent kernel (eNTK). Effective rank, factor sensitivity ratios, and centered kernel alignment are used to characterize memorization of separate conditions, sharing across conditions, and invariance to task-irrelevant variation.

The empirical study covers synthetic size prediction, ManiSkill reinforcement learning, ACT imitation learning, and VLA policies on LIBERO and RoboTwin, together with hardware validation under lighting changes. The authors examine associations between kernel diagnostics and OOD performance, visual–language shortcut learning, and independent versus confounded training variation. They also compare the complementary diagnostic blind spots of gradient-based, hidden-layer, and output representations.

Critical strengths
  1. Controlled probes provide an informative perspective beyond conventional validation metrics. In Table 1a, the ACT policy with the lowest validation loss has the worst OOD success among the three evaluated configurations, while both activation-based and eNTK-based SNR agree with the robustness ordering. This is a concrete example of how representation diagnostics can reveal sensitivity to nuisance factors that validation loss fails to capture.
  2. The comparison of representation spaces identifies specific diagnostic blind spots. The grasp-frame experiment illustrates how output representations can miss instruction distinctions when the required actions coincide, while the bimanual experiment shows how shared hidden representations can miss dependencies introduced by separate action heads. Appendix A.2 further supports the motivation for gradient-based analysis by comparing kernel similarity with measured output changes after a single SGD update. Together, these experiments clarify which aspects of a policy different representations can reveal.
Critical weaknesses
  1. The behavioral shortcut interpretation goes beyond what the Figure 4 analysis directly establishes. Adding the third task reduces scene-to-language FSR relative to the extended-stage-1 control, providing evidence of a change in relative representational sensitivity that is not explained solely by training duration. However, the added task also changes the instruction-dependent prediction problem. Lower FSR therefore does not by itself demonstrate that the policy relies less on misleading scene cues when executing the original tasks. Section 3 appropriately acknowledges that a ratio cannot identify which factor changed and introduces CKA for factor-specific analysis; the Figure 4 shortcut argument would benefit from an analogous decomposition and an independent behavioral check. This matters because detecting visual shortcuts without task-level evaluation is a central proposed application, and instruction-sensitive gradient structure alone does not establish correct instruction-conditioned behavior.
  2. The Figure 5 comparison does not isolate the contribution of factor independence from broader object coverage. The described confounded condition fixes one object–texture pair per category, whereas the independent condition samples multiple objects with different textures within each category, including similar but nonidentical shapes. Matching the number of training episodes controls data-collection budget, but does not separate the effect of changing shape–texture associations from that of exposing the policy to more object instances and shapes. The lower novel-category action error supports the effectiveness of the tested data scheme, but provides less specific evidence for attributing the improvement to factor independence. Moreover, the kernel-rank comparison in Figure 5b is conducted on the toy environment, while Figure 5c reports the RoboTwin action errors. The figure therefore does not directly demonstrate that the proposed kernel transition explains the improvement in the robot experiment. This limits the mechanistic and data-design conclusions drawn from this comparison.
Questions for authors
  1. Figure 4: Can you report scene and language distances separately, or corresponding factor-specific alignment measures, on a fixed probe set from the original tasks? Does the FSR decrease correspond to improved instruction following when scene cues are held fixed or conflict with the instruction? Such evidence would distinguish a representational change from reduced behavioral shortcut reliance.
  2. Figure 5: Are the sets and frequencies of object instances, shapes, and textures matched between conditions? If not, what evidence separates the effect of factor independence from broader object coverage? A comparison preserving factor marginals while changing their pairing would directly address this attribution.
  3. Reliability of policy comparison: Figure 3 reports SNR means and standard deviations, which is useful. What sources of variation do these summarize, and do the main model rankings remain stable under probe resampling and reasonable changes to the LoRA parameter subspace? The question concerns the stability of the diagnostic conclusion, rather than requiring the restricted kernel to reproduce the full eNTK.
1 comment

We thank the reviewer for the careful and constructive feedback.

W1 / Q1 (Figure 4) We agree that FSR is a representation-level signal and does not by itself show reduced shortcut reliance, especially since the third task also changes the prediction problem. Following the reviewer’s suggestion, we now report factor-specific alignment separately for scene and language (new figure in the revised paper appendix). We compute linear CKA between the eNTK and a scene-label kernel and a language-label kernel, on a fixed probe set from the two original tasks (40 scenes × {adjust, shake}, 80 probes), using the same raw kernel as the FSR curve in Figure 4(b). Relative to the Stage 1 mean, scene CKA stays within 0.9 to 1.1× in all three runs, whereas language CKA rises to 4.3× in Stage 2 and to 2.1× in the step-matched control. The FSR decrease is therefore driven by the language factor, not by a change in scene sensitivity, and the rise is larger when the third task is added than under continued training alone. The third task makes the representation more sensitive to language while retaining its sensitivity to the scene.

W2 / Q2 (Figure 5) Both conditions use the same number of training episodes, which matches the data-collection budget that our guidance targets. The two conditions cover the same object categories, and objects within a category have very similar shape and affordance. The comparison is between two data-collection schemes that differ in how instances are sampled. The confounded scheme uses one instance (one fixed shape-texture pair) per category. Because each instance carries a fixed texture, shape and texture can only be made independent by sampling multiple instances per category, so the independent scheme inherently includes broader instance coverage. It is therefore not possible to hold both the category set and the instance set fixed while breaking the shape-texture association. We chose to hold the category set and the episode count fixed, since this reflects how such data would be collected in practice.

We also agree that Fig. 5b (toy environment) and Fig. 5c (RoboTwin) are separate settings, so together they do not show that the kernel transition explains the RoboTwin improvement. Computing the effective-rank transition from “memorize” to “adapt” requires a series of checkpoints trained with different amounts of variation along one factor axis, which is computationally heavy for RoboTwin. We add this to the limitations section. Fig. 5b serves only as intuition, and the claim that independent variation is better is supported directly by the RoboTwin action-error results in Fig. 5c.

Q3 (Figure 3 reliability) The ± is the population standard deviation over five disjoint groups of probe scenes. Each group has 25 images: 5 mid-trajectory LIBERO-Spatial frames from different episodes, each rendered under the same 5 lighting conditions. It therefore captures sensitivity to the choice of probe scenes.

The main ranking is stable under probe resampling. OpenVLA has the lowest SNR in all 5 of 5 groups, and the ranges do not overlap: its highest per-group value (3.048) is below the lowest value of either of the other two models (3.195). We will add the per-group values to the appendix. RIPT-VLA and OpenVLA-OFT are not separated, so we treat them as a tie, consistent with their near-identical OOD success (88.4% vs. 88.7%). We claim only that OpenVLA is the most lighting-sensitive model, matching LIBERO-plus, and make no fine-grained ordering claim between the other two. Probes can come from the evaluation distribution, or outside it, and are defined only by the factor of interest.

On representation choice, the eNTK is a default, not a requirement. Activation and output kernels also work in several settings (see “Representation Kernel Comparison”). The eNTK predicts how a training update on one input changes the output on another (Appendix A.2: ρ = 0.97 vs. 0.22 for the best activation layer). LoRA is a common fine-tuning technique that covers the crucial parameters of the network, so the eNTK restricted to LoRA parameters reflects the trend of LoRA fine-tuning updates.

Comments on the paper

2 comments

Summary of Revisions to the Paper:

  • Completely rewrote the Introduction section to provide clearer motivation and better contextualization of the research.
  • Added a new Limitations section to clarify the scope of the current work and discuss potential directions for future research.
  • Added two new appendices:
    • Appendix A.3: Separate Scene and Language CKA in the Shortcut Analysis
    • Appendix A.4: Stability of the VLA Model Ranking Across Probe Groups
  • Made minor revisions to the Abstract and Conclusion sections.
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