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Under review as a conference paper at ICLR 2027

What Does a Skill Vocabulary Cost? A Closed-Loop Decomposition over Demonstrated Motions

Abstract

Discrete skill policies execute motions drawn from a finite vocabulary. In most current methods this vocabulary is a latent codebook, learned jointly with a selector and a decoder and validated by offline reconstruction. When such a policy fails in closed loop, the failure cannot be traced to the vocabulary, to the choice of skill, or to its execution. We present Movement Prototype Quantization (MPQ), which separates these costs by placing the vocabulary after the policy instead of inside it. The library stores demonstration segments as B-spline control points. At execution time, MPQ replaces each predicted action chunk with its nearest library element and corrects that element toward the prediction, within a bound given by the spread of the demonstrations themselves. MPQ trains no parameters. Across six architectures in simulation, including a 7B vision-language-action model, the wrapped policy is statistically equivalent to the original. Its success changes by +0.6 points on average, less than the spread between repeated evaluations of the same checkpoint. A reference policy executed through the library therefore sets a ceiling for any selector over the same library. Replacing the reference's components with those of a trained selector, one at a time, then attributes the selector's shortfall to its parts. On LIBERO-90 with 256 prototypes, quantization costs nothing and the selector's choice costs 2 points, whereas its learned heads lose 15, nearly the entire gap. Offline reconstruction predicts none of these differences, and it misjudges library size, library design, and transfer across benchmark suites.

Primary area:
applications to robotics, autonomy, planning
Keywords:
Discrete Skill Policies, Movement Primitives, Imitation Learning

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_zaeaOpenReview ↗
Rating
2(+1)
Confidence
4
Informativeness
1
Presentation
1
Soundness
3
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Paper summary

The paper builds a library of short robot movements taken from demonstrations. It takes an already trained robot controller and replaces each movement it proposes with a similar movement from this library, allowing limited adjustments. The authors report that this usually preserves the controller’s ability to complete tasks.

They then train another controller to choose a stored movement and predict how to rotate and adjust it for the current situation. They test which part causes failures by replacing these predictions with ones obtained from the original controller. For their ACT-based controllers, most of the performance loss comes from how the chosen movement is rotated and adjusted; the choice of movement matters much less.

Critical strengths

The authors show that several trained robot controllers can have their proposed movements restricted to stay near demonstrated movements, with limited adjustments, while largely retaining task performance

Critical weaknesses
  1. The small loss from movement choice is measured with substantial help from ACT. ACT still predicts the full action sequence. MPQ uses this prediction to rotate and adjust the chosen movement. The experiment shows that the learned choices work well with this help. It does not show that movement choice is generally a minor source of failure. Section 3.1 acknowledges this condition. The paper’s broader conclusions should state it too.

  2. The predicted adjustments do not depend on the movement chosen. This design choice could explain their poor performance. The tests across six architectures only show that MPQ largely preserves task success. They do not establish the same cause of failure across six architectures. Appendix F also shows difficulties in applying the method to policies that use trained action decoders. Using stored movements and adding corrections are already established ideas. The paper therefore needs to provide new insight into why learned controllers fail. The evidence does not show that its explanation holds across other strong controller designs. The authors also do not demonstrate a better controller built using this insight.

Questions for authors
  1. What should a researcher designing a robot controller learn or do differently after reading this paper? Please give one concrete example supported by your experiments. What does the analysis establish beyond identifying a weakness in the particular ACT-based controllers you trained?

  2. The controller you train predicts adjustments without using the chosen movement. Could this design explain its poor performance? Do you have results where the adjustment depends on the chosen movement?

  3. Why call ACT’s score after applying MPQ a “ceiling”? Couldn't another controller perform better with the same movement library?

3 comments

We thank the reviewer for the detailed review and questions. Revisions in the PDF are marked in blue. Apart from the points below, the revision reports both substitution orders across seeds (Table 3, SBWK) and limits its claims to selectors built on a reference's network or features (Mf55). New results use three seeds (mean ±\pm sd).


Q1 / W2: What should a researcher do differently, beyond our ACT-based controllers?

We apologize that the manuscript did not make this clearer. The revision states these consequences more explicitly in the introduction and conclusion. Our experiments support three recommendations, and the external library enables a new kind of edit.

1. Validate a skill library in closed loop, not by reconstruction. As Mandlekar et al. (CoRL 2021) found for policy checkpoints, offline criteria fail for skill libraries. Reconstruction would choose a library several times larger than needed, rank first a design that costs 5 points, and miss a transfer loss of 4 to 8 points (Sec. 6).

2. When a discrete, inspectable and editable skill library is required, wrap a trained continuous policy instead of learning a discrete output head. On all three references, the wrapped policy matches or exceeds its learned selectors. ACT's selector, with regression heads, falls 13.1 points below the wrapped policy (67.1 against 80.2). Heads that generate placement and correction by flow matching or diffusion, as the reference generates actions, close the gap on the DiT (83.0 against 83.4) and leave 10.9 points on Diffusion Policy (82.0 against 92.9, Table 3).

3. To improve a learned selector, work on placement and correction, not on the choice. The decomposition shows that on every reference the choice of prototype costs at most 2.7 points, and that the loss lies in how the selector places and corrects it (Table 3). Changes to these heads do improve a selector. Conditioning them on the chosen prototype raises the ACT selector's success by 4.1 points (Sec. 5.3).

Example application. Because the library sits outside the policy, it can be edited after training. In a new experiment (Sec. 4.2), we delete the fastest 25% of the prototypes. Without retraining, the share of executed chunks above that speed falls from 28% (bare ACT) to 12% at unchanged success (79.0 against 79.3). Halving the bound lowers this to 4.5%, at a cost of 10 points. This constrains commanded motion but is not a safety guarantee.


Q2: Adjustments that depend on the chosen movement.

We thank the reviewer for this suggestion and added the experiment to the revision (Sec. 5.3). When the yaw and residual heads of the ACT selector are conditioned on the chosen prototype, success rises from 65.6 to 69.7 over a control with the same capacity (+4.1±3.1+4.1 \pm 3.1, positive on every seed). The conditioned selector still stays about 10 points below the library reference (80.2), almost all of it in execution. Diffusion Policy's selector, whose heads also see the chosen prototype, still loses 10.3 points in execution (Table 3). Conditioning therefore explains only part of the execution loss.


W1: The small loss from movement choice is measured with ACT's help.

This is correct, and the abstract, introduction and conclusion now state the condition. We also tested whether ACT's help hides poor choices (Sec. 5.2, Fig. 6). If it did, poor choices would also cost little. Under ACT's placement and correction, forcing the 5th-nearest or a random prototype instead of the nearest costs 18.9 and 68.7 points, while the selectors' choices cost at most 2.1. Without correction, the 5th-nearest costs about 25 points and an ACT selector's choices 2.9. The selection cost is small because the learned choices are good.


Q3: Why "ceiling"?

We agree that "ceiling" was too strong, since another selector could do better with the same library. Sec. 3.1 now calls the quantity the library reference, "a baseline rather than an upper bound".


W2: Established ideas and trained action decoders.

We do not claim stored movement prototypes or corrections as contributions. The contribution is placing them after a trained policy with no learned decoder in between, and the closed-loop findings that this placement makes measurable. A trained decoder would entangle selection and execution, as App. F shows for QueST, so the decoder-free design is deliberate.


We hope these results address the reviewer's questions, and we are glad to discuss any remaining points.

Thank you for the new experiments which answer my question about conditioning on the chosen movement and resolve my concern about calling the reference a “ceiling.” The extra tests across controllers make the results more convincing. My main concern is still how much we learn beyond the familiar point that lower offline loss does not always mean better task success. The smaller correction network used for the Diffusion Policy selector also leaves open how much of its performance gap comes from that design choice. I am raising my score from 1 to 2, but I still find the new insights and practical benefits too limited to support acceptance.

Thank you for raising your score. We are glad that the new experiments resolve the concerns about conditioning and the term "ceiling".

Beyond offline loss versus task success. We agree that this gap is familiar in general (Mandlekar et al., CoRL 2021), and it is not our main finding. The main finding is where discrete skill policies lose success: not in the vocabulary or the choice of skill, but in placing and correcting the chosen motion. In latent-codebook methods, a learned decoder entangles these costs, so they cannot be separated.

Size of the Diffusion Policy selector's correction network. The reviewer is right that its U-Net is narrower than Diffusion Policy's. We retrained it at Diffusion Policy's width, with down dimensions 512 and 1024 (its first two levels, since a third does not fit the ten control points). This raises the generator from 6.5M to 72.7M parameters, about eleven times the capacity. Over three seeds, success rises from 82.0 to 85.8 (+3.7±0.4+3.7 \pm 0.4, positive on every seed), so the narrow network explains about a third of the gap to the library reference. Even at eleven times the capacity, a gap of 7.1 points remains, and the decomposition again attributes most of it to execution: 6.3 points, against at most 1.9 for the choice. The revised PDF includes this result (Sec. 5.3, App. E).

We appreciate your time and the constructive questions.

Reviewer_SBWKOpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This paper introduces Movement Prototype Quantization (MPQ), a parameter-free execution layer that maps a continuous policy’s predicted action chunk to a nearest demonstration-derived B-spline movement prototype, then applies a tolerance-bounded correction toward the policy prediction. The paper uses this wrapper to define a “library ceiling” and an algebraic decomposition of a discrete selector’s closed-loop gap into library quantization, selection, and execution components. Experiments on LIBERO, RoboCasa, observation shifts, and one real-robot task argue that MPQ approximately preserves reference-policy success, that a particular staged selector loses primarily in its learned placement/residual heads, and that offline reconstruction does not reliably select useful libraries.

Critical strengths
  1. The central experimental intervention is well motivated and technically clean. Unlike a learned VQ decoder, MPQ’s prototypes are executable B-spline trajectories and the decoding map is fixed.

  2. Figure 1 communicates the method and intended decomposition effectively. In particular, Figure 1b makes clear that MPQ is not merely nearest-neighbor retrieval: the selected prototype is yaw-aligned to the policy prediction and then corrected within a prescribed budget.

Critical weaknesses
  1. The term “library ceiling” is stronger than what is established, and the causal interpretation of Equation 1 needs to be narrowed. Equation 1 is an exact telescoping identity for the particular policies and hybrids evaluated, but it does not establish that SR_ceil is an upper bound for “any selector over the same library.” A selector can in principle choose different prototypes and corrections that outperform the reference-conditioned nearest-prototype execution; indeed, MPQ occasionally improves success over the bare reference in Table 1. Thus the reported SR_ceil is better described as a reference-conditioned comparator or reference-preserving library evaluation, not a ceiling over the achievable performance of all discrete policies using P.

  2. The conclusion that execution dominates the performance gap remains specific to the implemented selector and intervention protocol. In the hybrid policy, the correction is recomputed from the reference’s complete continuous prediction for whichever prototype the selector chooses. By contrast, the learned residual head is not conditioned on the selected prototype and is supervised relative to the prototype assigned to the demonstration (Section 5 and Appendix E). The small measured selection cost is consequently conditional on access to a strong reference execution mechanism that can compensate for alternative prototype choices. It should not be interpreted as an intrinsic measure of selection quality. Moreover, Equation 1 is an additive identity whose attribution depends on the intermediate policies: the reverse-order experiment in Appendix E assigns a 19.1-point loss to execution and a 1.3-point gain to selection, demonstrating substantial component interactions. The frozen-encoder, unbounded-residual, and reverse-order controls provide useful support for an execution bottleneck in the tested implementation, but do not establish its generality across discrete skill policies. Comparisons with capacity-matched residual heads conditioned on the selected prototype, together with both intervention orders evaluated across seeds, would help distinguish a broader learning bottleneck from limitations of the chosen parameterization.

Questions for authors

See Weaknesses

1 comment

We thank the reviewer for the constructive feedback. Revisions in the PDF are marked in blue. Apart from the points below, Sec. 3.1 now defines the skill heads and both hybrids in one paragraph, a new experiment edits the library after training (Sec. 4.2), and the limitations state that we tested only selectors built on a reference's network or features (Mf55). New results use three seeds (mean ±\pm sd).


W1: "Library ceiling".

The quantity is now the library reference SRref\mathrm{SR}_\mathrm{ref}, "a baseline rather than an upper bound, since a selector that chooses or corrects better could exceed it" (Sec. 3.1).


W2a: Order dependence of Eq. 1.

Sec. 3.1 now calls the order of Eq. 1 choice-first and defines the reverse order as correction-first. Table 3 reports both orders on all three seeds. The staged selector shows the interaction the reviewer describes (4.4 points). Still, for every selector and in either order, the choice changes success by at most 2.7 points, so the conclusion does not depend on the order.


W2b: Conditional selection cost.

The selection term is defined under the reference's correction (Sec. 3.1), and the abstract, introduction and conclusion now state this condition too. Within it, the term is sensitive to choice quality. Under the same correction, a forced-rank control (Sec. 5.2, Fig. 6) gives costs of 18.9 points for ACT's 5th-nearest prototype and 68.7 for a random one, against at most 2.1 for the selectors' choices. The correction does not hide poor choices.


W2c: Prototype-conditioned heads.

We trained capacity-matched MLP heads with and without an embedding of the chosen prototype, and a conditioned variant supervised on the selector's own choice (Sec. 5.3). Conditioning gains 4.1±3.14.1 \pm 3.1 points, positive on every seed, and removes most of the order interaction. Supervising on its own choice adds nothing. Execution still costs about 10 points, and Diffusion Policy's selector, whose heads see the chosen prototype, loses 10.3 (Table 3). The missing conditioning explains part of the execution loss, not most of it.


W2d: Generality.

Selectors on the flow DiT and Diffusion Policy show the same small choice cost (Table 3). Their execution loss differs: 0.0 with flow-matching heads on the DiT and 10.3 with diffusion heads on Diffusion Policy, against 12.1 with ACT's regression heads. Since the DiT's selector reaches its library reference (83.0 against 83.4), the execution loss is not inherent to a discrete selector.


We hope these results address the reviewer's questions, and we are glad to discuss any remaining points.

Reviewer_Mf55OpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper studies how to separate the performance costs of a discrete motion vocabulary, skill selection, and execution.The authors introduce MPQ, which takes a continuous policy’s predicted action chunk, matches it to a demonstration-derived motion prototype, and applies orientation alignment and a bounded correction. This allows them to test whether executing through the library reduces the reference policy’s success rate. They then replace the reference-based selection and execution components with those of a learned selector to measure the resulting performance changes. MPQ largely preserves reference-policy performance across the tested architectures and benchmarks. For the ACT-based selector, most of the gap appears when the learned execution heads replace reference-derived execution. Experiments on library size, design, and transfer also show that better offline reconstruction does not necessarily lead to better closed-loop performance.

Critical strengths
  1. The paper offers a useful way to examine where a discrete skill policy loses performance. Using executable prototypes and a fixed decoder makes the comparison easier to interpret than a jointly learned codebook and decoder. The evaluation across six architectures and multiple benchmarks also provides substantial evidence that MPQ can preserve the performance of existing policies.
  2. The comparison between offline reconstruction and closed-loop success is informative. Increasing the library size or improving reconstruction does not always improve task success, and reconstruction can miss losses when transferring a library across benchmarks. These results are useful for deciding how to build and evaluate motion libraries.
Critical weaknesses
  1. The full diagnostic is evaluated more narrowly than the execution layer. The multi-architecture experiments provide substantial evidence that MPQ can preserve the performance of different policies. However, the full selection–execution decomposition remains centered on ACT-derived selectors. Compatibility with multiple policies does not by itself demonstrate that the decomposition provides useful diagnoses across selector designs. The fixed-decoder requirement also limits direct application to learned-codebook methods, as the paper acknowledges. These restrictions do not invalidate the framework, but leave its broader diagnostic applicability less established than its execution-layer compatibility. Applying the decomposition to another selector architecture would strengthen this contribution; otherwise, the main claims should consistently reflect the demonstrated scope.
  2. The sensitivity of the selection term to selection quality remains unclear. Measuring selection loss under reference-derived placement and bounded correction is a valid conditional comparison. However, the current experiments do not show how strongly the resulting success rate responds to changes in selection quality. Comparing learned choices with lower-ranked or random prototypes under the same correction rule and budget would clarify how much the reference correction reduces sensitivity to prototype choice. The reported small selection term supports a small selection cost under the tested protocol, but its interpretation as evidence about the relative importance of selection would be stronger with this control.
Questions for authors
  1. Clarification — scope of the diagnostic framework. The multi-architecture experiments establish MPQ’s compatibility as an execution layer, whereas the full decomposition is evaluated on ACT-derived selectors. Which aspects of the diagnostic do the authors expect to carry over to other selector architectures, and under what assumptions? Is there additional evidence beyond the ACT-derived selectors supporting this applicability? This would help assess the framework’s scope independently of whether different architectures exhibit the same bottleneck.
  2. Clarification and additional evidence — sensitivity to prototype choice. How sensitive is the hybrid policy’s success to the quality of the selected prototype under reference-derived placement and bounded correction? Have the authors evaluated lower-ranked or random prototypes using the same correction rule and budget? If such results are unavailable, please clarify whether the small selection term is intended strictly as a conditional result under this execution mechanism, or as evidence that selection is a minor contributor more generally. The suggested control would strengthen the latter interpretation.
3 comments

We thank the reviewer for their valuable feedback and suggestions. Revisions in the PDF are marked in blue. Apart from the points below, the revision includes three changes in response to the other reviewers: it renames the "library ceiling" to library reference (SBWK, zaea), reports both substitution orders of Eq. 1 across seeds (SBWK), and adds heads conditioned on the chosen prototype (SBWK, zaea, Sec. 5.3). New results use three seeds (mean ±\pm sd).


W1 / Q1: Does the diagnostic carry over beyond ACT-derived selectors?

Yes. We applied the full decomposition to two more references, the flow-matching DiT and Diffusion Policy. Each selector keeps its reference's encoder frozen, and its skill heads generate placement and correction the way the reference generates actions, by flow matching on the DiT and by diffusion on Diffusion Policy (Sec. 5.1, Table 3).

referenceskill headsSRref\mathrm{SR}_\mathrm{ref}SR(L)\mathrm{SR}(L)selectionexecution
ACTregression80.267.1±3.567.1 \pm 3.5−0.9±1.2-0.9 \pm 1.2−12.1±1.6-12.1 \pm 1.6
flow DiTflow matching83.483.0±0.083.0 \pm 0.0−0.4±1.0-0.4 \pm 1.0$ 0.0 \pm 2.0$
Diffusion Policydiffusion92.982.0±2.082.0 \pm 2.0−0.5±1.1-0.5 \pm 1.1−10.3±1.9-10.3 \pm 1.9

Terms in the choice-first order of Eq. 1. In the correction-first order, the two terms shift by at most 3.1 points (Table 3). The DiT selector scores 83.0 on each of the three seeds.

What carries over: on every reference the choice costs at most 0.9 points, and nearly all of the remaining gap lies in execution. The decomposition also locates where selectors differ. Execution costs 12.1 points with ACT's regression heads and 10.3 with Diffusion Policy's diffusion heads, whereas the DiT's flow heads lose nothing and reach the library reference. A single success rate would not show where these differences arise. The limitations now state that we tested only selectors built on a reference's network or features.

Assumptions (Sec. 3.1): the decomposition assumes no particular architecture, only a discrete selector over library elements that execute without a learned decoder. As the reviewer notes, this excludes jointly learned codebooks (App. F). It is a deliberate design choice. With no decoder between the chosen element and the executed motion, every executed skill can be inspected, the library can be edited after training, and choice and execution separate in closed loop.


W2 / Q2: Sensitivity to prototype choice.

We ran the proposed control (Sec. 5.2). The reference supplies placement and correction with the same rule and budget, and the executed element is forced to be the rr-th nearest prototype to the reference's chunk. Fig. 6 shows that success falls steeply with rank for ACT, the DiT and Diffusion Policy. For ACT, the 5th-nearest prototype costs 18.9±2.618.9 \pm 2.6 points and a random one 68.7±1.768.7 \pm 1.7. The selectors' choices cost at most 2.1 points, although they often differ from the nearest prototype. Without any correction (β=0\beta = 0), the 5th-nearest prototype costs about 25 points, and an ACT selector's choices 2.9 (Sec. 5.2).

The selection term is conditional by definition (Sec. 3.1), and the revision now states this throughout. Within this condition, the control supports the stronger reading: the term responds strongly to choice quality, and it is small because the selectors choose well, not because the correction hides poor choices.


We hope these results address the reviewer's questions, and we are glad to discuss any remaining points.

Thank you for the clarifications and additional experiments. I appreciate the evaluation framework, although I still find its practical guidance for policy design limited. I maintain my rating of 3, and my support for acceptance is not strong.

AuthorsOpenReview ↗

Practical guidance for policy design

Thank you for the reply. We answer briefly on practical guidance.

A discrete skill vocabulary makes every executed motion inspectable and editable after training (Sec. 4.2). The paper gives two routes to one, and the revised conclusion states both.

Wrap a trained policy. A continuous policy, such as a flow-matching one, gains the vocabulary without retraining. Success is unchanged on six architectures.

Train a discrete selector directly. Then invest in executing the chosen skill, not in choosing it. On three backbones, the selectors choose well and lose success in placing and correcting the chosen motion (Sec. 5). Our experiments suggest that this loss depends on how the selector generates the placement and correction. A flow-matching selector reaches the success of the wrapped policy, while regression and diffusion selectors fall short of it.

We thank the reviewer again for the constructive review.

Comments on the paper

1 comment
AuthorsOpenReview ↗

General response and summary of revisions

We thank the reviewers for their careful reading and the AC for handling the submission. We posted a reply to each reviewer and a revised PDF. Below, we briefly restate the contribution and then summarize the revision.

What the paper contributes. The paper places a library of demonstrated motions after a trained policy, with no learned decoder in between. MPQ replaces each predicted action chunk with its nearest library element, corrects it toward the prediction within a bound, and trains no parameters. This placement makes three things measurable in closed loop, which the reviewers also note as strengths:

  • Across six architectures, including a 7B VLA, the wrapped policy is statistically equivalent to the original, at +0.6 points on average (Mf55, zaea).
  • The reference policy executed through the library is a baseline. A discrete selector's shortfall against it splits into the cost of choosing a skill and the cost of executing it. On three backbones, the choice costs little, and the loss lies in placing and correcting the chosen motion. Mf55 finds this "easier to interpret than a jointly learned codebook and decoder", and SBWK calls it "well motivated and technically clean".
  • Offline reconstruction misjudges library size, design and transfer across benchmarks, which Mf55 finds "useful for deciding how to build and evaluate motion libraries".

New evidence in the revision. All new results use three seeds.

  • Sensitivity of the selection term (all reviewers; Sec. 5.2, Fig. 6). The selection cost is measured with the reference's placement and correction, which could make poor choices look cheap. Under the same correction, forcing the 5th-nearest prototype costs 18.9 points and a random one 68.7, while the selectors' own choices cost at most 2.1. The term is small because the choices are good.
  • Two further backbones (Mf55, zaea; Table 3). The decomposition now covers selectors on the flow-matching DiT and Diffusion Policy. On every backbone the choice costs at most 0.9 points. Execution costs 12.1 points for ACT's selector, 10.3 for Diffusion Policy's and nothing for the DiT's, which reaches its library reference. The decomposition thus shows where selectors on different backbones lose, which a success rate alone does not, and the execution loss is not inherent to a discrete selector. A wider correction network for Diffusion Policy's selector recovers about a third of its loss, and the rest remains in execution.
  • Heads conditioned on the chosen prototype (SBWK, zaea; Sec. 5.3). Against a control with the same capacity, conditioning raises success by 4.1±3.14.1 \pm 3.1 points. About 10 points of execution loss remain, so the missing conditioning explains only part of it.
  • Both substitution orders of Eq. 1 on all seeds (SBWK; Table 3). The choice costs at most 2.7 points in either order, so the conclusion does not depend on the order.
  • Editing the library after training (zaea; Sec. 4.2). Because the library sits outside the policy, a constraint on executed motion can be imposed after training by editing the library alone. Deleting the fastest quarter of the prototypes lowers the share of fast executed chunks from 28% to 12%, at unchanged success and without retraining.

Clarifications. The "library ceiling" is now the library reference, "a baseline rather than an upper bound" (SBWK, zaea; Sec. 3.1). The introduction and conclusion now state the practical consequences more clearly: validate a library in closed loop, wrap a trained policy when a discrete library is needed, and improve a selector's placement and correction rather than its choice (zaea). The limitations state that we tested only selectors built on a reference's network or features (Mf55).

All changes are marked in blue in the revised PDF. We would be glad to hear whether the revision addresses the reviewers' concerns, and we will respond promptly to any remaining questions before the discussion period closes.

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

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