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Withdrawn from ICLR 2027

Learning Safety-Preserving Task Degradation for Fault-Tolerant Robotic Manipulation

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

Learning one secondary-task coefficient offers a narrow interface for fault-tolerant manipulation with given fault reports and priority control. We distinguish changes to a trained policy from useful constrained control. In Isaac Sim, six PPO actors deploy constant full retention despite stochastic training, as established by guarded final-layer logit bounds. A paired intervention removes only their initial full-retention bias, retaining architecture, geometry, optimization, budgets, and the selection rule. Training and selection change the action map and produce variable deployed behavior, but all prespecified constrained-control criteria fail. Across 992 quarter-tolerance tasks per neutral fit, policies have 6-12 primary-crossing cases; a selected margin rule has three and weakly improves recovery count and secondary cost over every fit. A subsequent same-input diagnostic establishes a material replacement of the trained categorical distribution by its mode. A same-weight native deployment intervention then executes both choices: sampling improves some costs and recoveries but introduces 46 primary-crossing episodes across twelve sampled arms, versus zero in their six modal counterparts. None of the three prespecified fixed-penalty fits meets the useful-decoder criterion. Complementary selection and force-budget interventions establish bounded scheduling opportunity; failed gradient, residual, and fixed-probe screens retain their stopping conclusions. Removing constant deployment through initialization is insufficient for constrained-control gains. These findings neither identify a complete explanation of the remaining loss nor establish RL impossibility or a physical safety certificate. Two archived hardware trials from a separately deployed PPO policy document scalar execution.

Primary area:
applications to robotics, autonomy, planning
Keywords:
Reinforcement Learning, Fault-Tolerant Robot Manipulation, Sim-to-Real Transfer, Task Allocation, Structured Action Spaces

Reviews

Among:
Shape:
1234this paper, Bottom 2%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_Gw5NOpenReview ↗
Rating
2
Confidence
2
Informativeness
1
Presentation
2
Soundness
2
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Paper summary

The paper studies learning a single secondary-task coefficient on top of a supplied robot priority controller. The controller computes primary and secondary joint-command channels, and a PPO policy selects α\alpha. Fault reports, kinematics, gravity compensation, and the task hierarchy are given. In Isaac Sim, a global logit bound establishes that, under deterministic maximum-probability deployment, the six originally selected actors always output. Removing an initial full-retention bias and retraining changes deployment behavior, but does not meet the control-benefit criteria. A simple margin rule has fewer failures, no fewer recoveries, and lower cumulative secondary error than every neutral-initialization fit. A separate intervention fixes network weights and compares sampling with maximum-probability deployment, finding some improvements accompanied by additional primary violations. Further diagnostic studies investigate limited scheduling opportunities, and two archived trials from a separate Panda policy illustrate scalar execution.

Critical strengths
  • The constant-deployment diagnosis is stronger than a finite collection of observed trajectories. Section 5 and Appendix C establish a positive global logit-gap bound for each of the six selected original actors under the stated activation and arithmetic conditions. This verifies that their deterministic decisions cannot depend on observations, even though training changes weights and probabilities. It provides concrete evidence for the distinction between changes to a network and changes to its deployed decisions.

  • The interventions and negative results are reported with appropriate limits. The paper distinguishes changing initialization and retraining from changing only the deployment rule of fixed weights. Tables 2 and 3 retain all fitting seeds and report violations separately from recovery and secondary error. The authors also distinguish independent scenarios from masks and action streams, and avoid claiming a physical safety certificate or general RL impossibility. These choices make the limited empirical conclusions easier to assess.

Critical weaknesses
  • The expected value of the learning scheme remains insufficiently supported. Sections 2–3 explain that torque limits, inertia, and transients during faults and the restoration of actuator effectiveness can cause secondary commands to affect the primary task, motivating state-dependent adjustment of the secondary coefficient. The paper aims to improve control performance through learning and treats an advantage over existing feedback rules as the test of the learning scheme's value. However, in Table 2, the margin rule is no worse than all six neutral-initialization PPO fits on the three aggregate metrics of failures, recoveries, and cumulative secondary error, and the learning scheme does not meet the prespecified control-benefit criteria. The paper does not sufficiently explain which important decision difficulties in the chosen tasks are hard for simple feedback rules to handle. An unsuccessful scheme can still be worth studying, but the importance of the chosen problem and why this negative result deserves other researchers' attention require clearer justification.

  • The new insights and value of the failure diagnosis for other work remain unclear. Section 10 states, "We do not claim initialization sensitivity itself as new." The main deployment bound follows directly from bounded activations and output-layer parameters and establishes a property of particular selected models. The original case uses an initial full-retention bias of 4, an output-layer initialization gain of 0.01, a fixed training budget, and update-12 checkpoints; neutral initialization changes deployment behavior but still does not meet the prespecified control-benefit criteria. Appendix C.1 also shows that untrained neutral actors already produce 20–21 action categories on the same validation observations visited by the selected policies. These findings support diagnosis of the current system, but do not sufficiently identify diagnostic principles that other researchers can apply beyond existing knowledge of initialization sensitivity and training/deployment differences, or establish the conditions and evidence supporting such use. The ideal retiming, finite-option, hidden-budget, gradient, residual, and probe analyses provide local boundaries or screening conclusions, but their connection to the main feedback experiment's remaining performance gap is still unclear. The main simulation also lacks corresponding coefficient and primary/secondary-error trajectories, while the hardware traces concern a separate policy; Appendix B lists baseline parameters but does not fully define the margin signal, slope estimate, or coefficient update rule. These gaps make it difficult to understand the failure behavior, reproduce the central comparison, and assess which lessons can inform other work.

Questions for authors
  • Expected value of the learning scheme: The paper treats an advantage over feedback rules as the test of learning's value. Which specific decision difficulties in the chosen tasks make learned coefficient adjustment worth investigating, and what advantages is it expected to offer over simple feedback rules? Are there explicit objectives beyond improved control performance, and how does the existing evidence support them?
Reviewer_RbkgOpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
1
Soundness
2
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Paper summary

This paper studies whether reinforcement learning can improve secondary-task scheduling for a redundant robot arm under fixed task-priority control with joint faults and repairs. The priority allocator, fault reports, and kinematics are given, and a PPO policy learns only a single coefficient that scales the secondary-task command, with the goal of improving secondary-task recovery after repair without violating primary-task tolerances. In Isaac Sim experiments on a Franka FR3, the authors first show via a logit-gap bound that the originally trained PPO actors deterministically output full retention for every input, due to a biased initialization of the output layer. Removing this initial bias yields input-dependent policies, but the retrained policies fail the prespecified evaluation criteria, and a simple hand-designed margin rule outperforms all PPO fits in failures, recoveries, and secondary-task cost. The authors further show that deterministic (argmax) deployment differs substantially from the trained stochastic policy, but deploying the same weights with sampling introduces additional primary-task violations and also fails the prespecified criteria. Overall, the paper is primarily a negative-result and diagnostic study, concluding that removing constant deployment is insufficient to obtain constrained-control gains.

Critical strengths
  1. Rigorous and transparent experimental protocol. Evaluation criteria are specified before testing, all seeds and fitted models are retained rather than selecting the best run, and unsuccessful comparisons are reported rather than omitted. The authors also carefully distinguish between what their results show and what they do not show.
  2. Careful diagnostic design. The paper isolates specific factors through controlled interventions: the logit-gap bound verifies that the original policies are constant for every input, the initialization intervention changes only one bias term, and the same-weight comparison changes only the deployment rule (argmax vs. sampling). This makes each individual comparison easy to interpret.
  3. Useful analysis of scheduling headroom. The analysis in Section 9 and Appendix F shows that, under idealized assumptions, full secondary retention is optimal, so any benefit of scheduling comes from non-ideal effects such as damping, inertia, and force limits. Together with the force-budget experiment, this helps explain why simple rules are already strong in this setting.
Critical weaknesses
  1. Limited insight into the main negative result. The paper rules out several explanations (constant deployment, deterministic decoding) but does not identify why the retrained PPO policies underperform a simple margin rule, as the authors acknowledge in Section 11. There is no analysis of what the learned policies actually do, for example when they reduce α or which inputs they rely on, and no comparison with the behavior of the margin rule, which directly uses primary-task margin information that is also available to PPO. As a result, the reader is left without a clear or generalizable lesson.
  2. Missing comparison with existing priority-learning methods. Section 10 cites several methods that learn task priorities or weights within a hierarchy (e.g., Karimi & Ahmadi, 2022; Testa et al., 2025; Penco et al., 2020), but none are used as baselines. The comparison is limited to PPO variants and hand-designed rules, which makes it difficult to judge whether the negative result is specific to this PPO setup or applies to learning in this interface more broadly.
  3. Narrow and artificial setting. The study learns a single scalar coefficient on one simulated robot, with a synthetic fault model (attenuation of joint increments rather than an identified hardware failure) and experimental tolerances without an application-specific justification. All masks are seen during training. This limits the generality of the conclusions.
Questions for authors
  1. Comparison with prior priority-learning methods. Section 10 discusses methods that learn task priorities or weights within a hierarchy (e.g., Karimi & Ahmadi, 2022; Testa et al., 2025; Penco et al., 2020).

  2. Leveraging the strong baseline. Since the margin rule is the strongest comparator, did the authors consider initializing PPO from it (e.g., via behavior cloning) or learning a residual on top of it with RL? The fixed residual family in Appendix H.1 is screened but not learned; would a learned residual be a more direct test of whether feedback learning can add value?

  3. Main takeaway. Given that the paper rules out several explanations without identifying the cause of the remaining performance gap, what do the authors see as the main lesson for practitioners designing learned components within fixed priority controllers?

Reviewer_CBXnOpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
1
Soundness
2
Read review
Paper summary

This paper studies a secondary-task recovery coefficient under fixed-priority control. It uses 62 six-bit primary/secondary coordinate masks and three tolerance scales, with joint increment fault attenuation and post-repair recovery. The initialization fix cannot improve constrained control. It is not an RL impossibility result or safety proof. Hardware tests come from two archived Panda robot runs.

Critical strengths
  1. Experimental honesty. Every failed learned comparison stays in the body tables. Negative result plus complete traceability deserves credit.
  2. The logit-gap bound is a clever small diagnostic tool. Others deploying RL can use this tool.
Critical weaknesses
  1. The contribution does not meet the main conference. No usable method is proposed, no new theorem, and the empirical result is negative and scoped to a single scalar coefficient.
  1. The writing is severely unreadable . The density of hedging and disclaimers prevents ordinary readers from extracting the conclusions, which affects the evaluation of the contribution itself, not just style.
  2. The link to the community is unargued. Why is learning one scalar coefficient under a given allocator worth 2.6M simulated episodes?
Questions for authors
  1. Do you have a hypothesis for why the margin rule wins so decisively ? A "why learning loses" section would make the negative result far more valuable.
  2. All 62 masks appear in training and generalization is scenario-level. With held-out unseen masks, do the logit-gap bound and constant deployment still hold?
  3. Would you consider adding a one-sentence plain-language "conclusion of this section" to each experimental subsection?

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

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