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Under review as a conference paper at ICLR 2027

Offline Meta Reinforcement Learning with Bayesian Task Relabelling

Abstract

Offline Meta-reinforcement learning faces two challenges when transferring from collected data to online adaptation. Behaviour-dependent task inference arises when an encoder identifies tasks from collector-specific patterns rather than task properties. Belief distribution shift can lead to poor actions when the policy encounters unfamiliar beliefs about the task. We introduce Bayesian Task Relabelling (BTR) to address both challenges using a learned Bayesian task model. We build on the Bayesian linear task model and identify how its conditional reward and next-state likelihoods exclude collector behaviour as separate evidence of task identity. To broaden belief coverage, BTR samples imaginary tasks using a posterior-based approximation and generates their corresponding imaginary rewards along collected histories. The same model combines these imaginary rewards with collected next states to update task beliefs in closed form, providing additional data for policy training. Task sampling is not restricted to training tasks or achieved goals, and reward generation requires no known task-specific reward function. In comparisons with recent or representative baselines trained on the same data, BTR achieves the highest mean return on all eight control benchmarks under online adaptation and seven under offline-context evaluation.

Primary area:
transfer learning, meta learning, and lifelong learning
Keywords:
Meta-RL, Offline Meta-RL, Bayesian RL

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_ZAntOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

The paper proposes Bayesian Task Relabelling (BTR) for offline meta-RL. It builds on the Bayesian linear task model from GLiBRL, samples reward parameters from an approximation to the posterior, and generates new rewards along recorded trajectories while retaining their states and transitions. Sequential Bayesian updates produce additional task representations for policy training. The actor uses posterior-mean features, while an asymmetric critic receives extra task information. Experiments compare online adaptation and offline-context evaluation on eight benchmarks, with additional goal-extrapolation tests and ablations of relabelling, task sampling, and critic inputs.

Critical strengths
  1. The method makes practical use of the Bayesian model: one sampled reward function generates a consistent task across each set of history segments, and the same model updates the task representation. Retaining recorded next states avoids adding dynamics-model errors. The paper is clear about which parts come from GLiBRL and about the approximation used for task sampling.

  2. The results are promising across both evaluation protocols, with the highest mean return on all eight standard-split online tests and seven offline-context tests. Some gains are substantial: Ant-Dir OOD return reaches 308 versus 58 for the best external baseline, and standard-split Walker-Param-Sparse reaches 103 versus 83 (Tables 1–2). The shared datasets and three-seed comparisons provide useful evidence for the complete method.

Critical weaknesses
  1. The no-relabelling ablation changes more than the rewards. Original tuples use the same context belief at both ends of a transition, whereas relabelled tuples receive sequential belief updates (Section 3.3; Appendix A.4). Relabelling also adds training tuples, and the two branches handle terminal flags differently. Removing that branch therefore removes several training changes at once. In particular, Walker-Param improves from 216 to 450 even though the environment's reward function is shared across tasks (Table 5). This could come from training on evolving dynamics beliefs, as the authors themselves suggest. A control using original rewards with the same sequential updates, initialisation, sample count, and terminal handling is needed to establish the additional value of imaginary tasks.

  2. The existing-task comparison does not isolate the benefit of sampling beyond training tasks. BTR samples around the source task's posterior, while the alternative selects a different training task's posterior mean (Appendix C). Meanwhile, half of the relabelled segments start from a belief inferred using the source task's original rewards (Appendix A.4). This can give the alternative a less appropriate starting belief, alongside changing the reward model's centre and its sampling variance. A comparison with the source task's own posterior mean, retaining the same reward noise, would isolate parameter sampling more directly. Comparing both samplers from the prior would also remove the initialisation concern. Without these controls, I find it difficult to attribute the large gains in Table 9 specifically to posterior task sampling.

Questions for authors
  1. Additional control: How does BTR compare with training on the same history segments using original rewards and sequential belief updates, with the same initial beliefs, number of tuples, and terminal handling? This would help separate task relabelling from the change in policy-training protocol.

  2. Task-sampling ablation: What happens when the sampled reward parameters are replaced by the source task's posterior mean, keeping the reward-noise model unchanged? Does the advantage over the existing-task variant persist when both start exclusively from the prior?

  3. Implementation clarification: What is the training context size k, and how are original and relabelled losses weighted? Appendix A.4 retains terminal flags for original tuples but uses non-terminal targets for relabelled segments. Are genuine environment terminations excluded from those segments, or are they bootstrapped through?

Remark: I'm willing to adjust my score if the authors can properly address my concerns above.

2 comments

We thank the reviewer for the insightful feedback. We will take the chance to clarify as follows:

W.1 The no-relabelling ablation removes sequential beliefs, extra tuples and the terminal handling together with the rewards, so Table 5 cannot credit Walker-Param to imaginary tasks. and Q.1 How does BTR compare with the same segments, original rewards and sequential updates, with matched initial beliefs, tuple count and terminal handling?

BTR has two components: (1) the first offline BLTM-based OMRL (2) easy belief relabelling. Running the first component alone under the same experiment setting will test the control you ask for. It keeps everything in BTR (segments, starting beliefs, step-by-step updates, etc) with the only difference that the recorded reward was used and nothing is relabelled.

Envcomponent (1) onlyBTR
Ant-Dir498 ± 34511 ± 24
Cheetah-Vel-30 ± 1-27 ± 2
Cheetah-Vel-Sparse324 ± 11327 ± 6
Hopper-Param335 ± 20341 ± 22
Hopper-Param-Sparse101 ± 3105 ± 4
Walker-Param506 ± 10450 ± 48
Walker-Param-Sparse107 ± 1103 ± 1
Point-Robot-Sparse31 ± 129 ± 7
Ant-Dir OOD / ID294 ± 43 / 550 ± 14308 ± 45 / 518 ± 14
Cheetah-Vel OOD / ID-62 ± 14 / -24 ± 1-54 ± 6 / -24 ± 1
Cheetah-Vel-Sparse OOD / ID190 ± 53 / 359 ± 4241 ± 5 / 363 ± 3
Point-Robot-Sparse OOD / ID12.6 ± 6.1 / 31.1 ± 7.86.6 ± 0.0 / 28.4 ± 5.1

It is correct that the gain in Walker-Param is indeed from the offline OMRL rather than the relabelling. We thank the reviewer for pointing this out. Nonetheless, the relabelling is still improving most of the standard split / OOD performance as expected. In the revised paper, we will include this table to identify the gain introduced by difference components of BTR more clearly.

W.2 The existing-task comparison changes the sampling centre, the variance and the starting belief at once, so Table 9 does not isolate sampling beyond training tasks. and Q.2 What happens with the source task's posterior mean instead of a sample, keeping the reward noise? Does the advantage over the existing-task variant hold when both start from the prior?

We ran the settings that vary one factor at a time (sampling centre, sampling procedure, segment start).

centreproceduresegment startAnt-DirCheetah-VelCheetah-Vel-SparsePoint-Robot-Sparse
other training taskpointmixed89 ± 24-172 ± 19124 ± 206.5 ± 5.4
other training taskpointprior273 ± 57-67 ± 9208 ± 108.8 ± 3.1
source posteriorsampleprior300 ± 27-65 ± 2228 ± 326.6 ± 5.4
source posteriorpointmixed294 ± 17-84 ± 27235 ± 94.5 ± 3.1
source posteriorsamplemixed308 ± 45-54 ± 6241 ± 56.6 ± 0.0

The first row is Table 9, and the last row is the full BTR. This shows the performance of different factors combined together. The setting BTR by default uses is the best overall.

For the first subquestion of Q2 (row 4 against row 5): using posterior mean rather than using samples make the result worse.

For the second subquestion of Q2 (row 2 against row 3): yes, though by a smaller margin.

Q.3 Context size k, loss weighting, and terminals inside relabelled segments.

k is drawn uniformly from [0, 200]. There is no separate weights, and every transition, original or relabelled, has equal weight in one shared actor and critic loss.

Regarding termination flags: the seven MuJoCo datasets contain no terminal flags, and Point-Robot-Sparse terminates at the goal. So for MuJoCo envs, both original and relabelled bootstrap through episode ends. For the Point-Robot-Sparse, the original does not bootstrap through, while the relabelled does on purpose because we have no termination model for the sampled goal.

As the rebuttal period is ending in a couple of days, could we kindly ask if the response has addressed your concerns? We are happy to provide further clarification.

Reviewer_P5q1OpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This paper proposes Bayesian Task Relabelling (BTR) for offline meta-RL. Building on GLiBRL’s Bayesian linear task model, it uses conditional reward and transition likelihoods for task inference, then generates imaginary rewards and sequential beliefs along recorded trajectories to augment policy training. Three-seed evaluations against MetaSTAR, UNICORN, and CORRO show the highest mean online return on all eight standard-split benchmarks, with more mixed results under task extrapolation.

Critical strengths
  1. Practical data reuse. BTR generates additional reward–belief training samples without supplied reward functions, new training interactions, or simulated dynamics.

  2. Useful empirical gains. BTR achieves the highest mean online return on all eight standard-split benchmarks, with a particularly strong improvement on Ant-Dir OOD.

  3. Reasonably thorough evaluation. Comparisons include recent and representative baselines on matched datasets. Ablations examine relabelling, task sampling, asymmetric critics, and next-state generation.

Critical weaknesses
  1. The methodological novelty is primarily in combining existing components. The contribution primarily combines inherited Bayesian inference with existing task-generation and relabelling ideas. Its distinction from closely related approaches, particularly the omitted BATI, needs clearer justification.
  2. Dependence on the low-dimensional reward model is insufficiently characterized. Virtual tasks depend on rewards being adequately represented by eight shared learned features. The paper provides limited analysis of reward-model error, posterior calibration, or sensitivity to feature dimension.
  3. Limited OOD advantage. BTR leads in only two of four online OOD environments, and dynamics extrapolation is not evaluated. Broader generalization benefits therefore remain uncertain.
  4. The ablations do not directly validate the two proposed shift-mitigation mechanisms. Component ablations demonstrate performance benefits but do not directly establish collector robustness or improved coverage of online beliefs. Controlled collector changes and belief-coverage measurements would strengthen these explanations.
Questions for authors
  1. What motivates reporting episode 2 for the standard split and episode 5 for the ID/OOD split? Do the conclusions hold under common interaction budgets and cumulative adaptation return?
  2. What training-time, memory, and online inference costs does BTR introduce relative to its no-relabelling variant and strong baselines? How do these costs affect the practical value of its gains?
3 comments

We thank the reviewer for the insightful feedback. We will take the chance to clarify as follows:

W.1 The novelty is a combination of existing components, and the distinction from BATI is unclear.

We respectfully disagree with the first statement on the novelty. BTR has two main components: (1) the first offline BLTM-based OMRL (2) easy belief relabelling. Neither of them is existing. First, it is correct that BLTM was there for online models, but its use in offline settings remains unexplored. Second, relabelling in previous work usually requires known reward models or is limited to seen goals or intermediate steps. On the contrary, BTR does relabelling in a very flexible way with BLTM using imaginary tasks, hence does not need any of these assumptions.

We thank you for pointing out BATI (Ma et al., ICML 2025), and we will include that in the related work. However, we believe it is substantially different from BTR, in

  • BATI maintains a finite table of training tasks, and hence constrained to use finite existing training tasks. BTR returns a posterior over continuous reward and dynamics parameters, providing more flexibility and easily extending to unseen tasks.
  • BATI does not propose a data augmentation mechanism, while BTR makes data augmentation for OOD generalisation possible.

W.2.1 Reward-model error is not reported. and W.2.3 Sensitivity to the reward feature dimension is not analysed.

We retrained BTR with d_R in {4, 8, 16, 32} on the four reward-varying environments. On the return:

online ep. 2 / offline returnd_R = 48 (paper)1632
Ant-Dir486 ± 22 / 475 ± 39511 ± 24 / 522 ± 17513 ± 9 / 504 ± 23507 ± 15 / 503 ± 18
Cheetah-Vel-26 ± 4 / -25 ± 2-27 ± 2 / -26 ± 2-26 ± 1 / -25 ± 1-25 ± 1 / -23 ± 1
Cheetah-Vel-Sparse326 ± 12 / 324 ± 3327 ± 6 / 320 ± 3327 ± 10 / 325 ± 5320 ± 21 / 318 ± 6
Point-Robot-Sparse32 ± 8 / 36 ± 129 ± 7 / 41 ± 527 ± 5 / 44 ± 223 ± 7 / 41 ± 2

In terms of return, BTR performs robustly as the dimensions do not affect the performance by much. On the OOD reward error:

RMSE / std, 30 context lengthd_R = 48 (paper)1632
Ant-Dir0.24 ± 0.000.24 ± 0.000.24 ± 0.000.25 ± 0.01
Cheetah-Vel0.16 ± 0.000.14 ± 0.000.15 ± 0.000.14 ± 0.00
Cheetah-Vel-Sparse0.36 ± 0.010.35 ± 0.010.36 ± 0.010.36 ± 0.02
Point-Robot-Sparse0.90 ± 0.010.86 ± 0.010.58 ± 0.120.63 ± 0.05

We report the model error in RMSE divided by the std of the rewards in corresponding environments in OOD setting so that the results are more comparable cross-environment.

W.2.2 Posterior calibration is not reported.

We report the probability of the absolute value of z = (recorded reward - predicted mean) / predicted std < 2. A calibrated model will have this probability equals ~0.954, following the 2-sigma rule.

P(abs z < 2), target 0.9510 context transitions30100
Ant-Dir1.00 ± 0.000.99 ± 0.000.97 ± 0.00
Cheetah-Vel1.00 ± 0.001.00 ± 0.000.99 ± 0.00
Cheetah-Vel-Sparse1.00 ± 0.000.99 ± 0.000.98 ± 0.00
Point-Robot-Sparse1.00 ± 0.000.99 ± 0.000.99 ± 0.00
Hopper-Param1.00 ± 0.001.00 ± 0.000.99 ± 0.00
Hopper-Param-Sparse1.00 ± 0.001.00 ± 0.000.99 ± 0.00
Walker-Param1.00 ± 0.000.99 ± 0.000.96 ± 0.00
Walker-Param-Sparse1.00 ± 0.001.00 ± 0.000.98 ± 0.00

The posterior is conservative when the number of transitions is small, and getting closer to well calibrated as the number of transitions grows, which is expected.

W.3 BTR leads in only two of four online OOD environments, and dynamics extrapolation is not evaluated.

On the OOD: BTR ranks the first for two envs and second for one env. For all main experiments in the main experiments (Table 1 and 2), out of 24 entries BTR places the third only in one of them. BTR places the first in 21 out of 24, and the second in 2 out of 24.

On the dynamics: We strictly followed the SOTA work MetaSTAR's evaluation pipeline, where they have not explored the dynamics ID/OOD splits.

W.4 The ablations do not test the two mechanisms: collector robustness and coverage of online beliefs.

On the collector robustness: proposition 1 has shown that posterior ratio between tasks does not depend on the collector, for any collector. It is something we have proven and not necessary to be evaluated empirically.

On the coverage of the beliefs, for each environment we record the belief after every step of the five adaptation episodes on held-out tasks and count the fraction within the 95th-percentile nearest-neighbour radius of the training beliefs, with the training set taken from the original tuples alone or with the relabelled beliefs added.

coverage of adaptation beliefs, OODoriginal tuples+ relabelled
Ant-Dir0.27 ± 0.100.36 ± 0.08
Cheetah-Vel-Sparse0.55 ± 0.040.63 ± 0.03
Cheetah-Vel0.10 ± 0.020.14 ± 0.01
Point-Robot-Sparse0.17 ± 0.030.34 ± 0.15

With relabelling, the coverage on OOD splits are indeed broadened compared to the version without.

Q.1 Why episode 2 for the standard split and episode 5 for the ID/OOD split? Do conclusions hold under common budgets and cumulative return?

These numbers are chosen strictly following the SOTA, MetaSTAR's evaluation protocal. Using similar numbers to report adaptation performance is very common in Meta-RL. For example, PEARL [Rakelly et al., ICML 2019] uses 2 and VariBAD [Zintgraf et al., JMLR'21] uses 5 to 6.

Q.2 Training, memory and online inference costs relative to no relabelling and the baselines?

We run on one RTX 4090, six runs in parallel with 8 CPU threads of an i7-13700K.

First, the time with and without relabelling on four environments with different work of relabelling. We use four environments of different relabelling work to show a rough estimate of the costs:

relabelled rowsBTRno relabellingUNICORNCORRO, SAC stageCORRO, encoder stageMetaSTAR
Ant-Dir200302317194474
Cheetah-Vel50251716185957
Hopper-Param-Sparse1002922162110171
Point-Robot-Sparse30191412142237

Relabelling takes slightly more time compared to the versions without. And the time grows together with the number of relabelling rows. BTR remains 2x to 3x faster than the SOTA, MetaSTAR.

Second, the GPU memory. The most memory consuming environment is Ant-Dir, which uses 724 MB with relabelling and 682 MB without. MetaSTAR uses ~2.4 GB, UNICORN and CORRO uses 668 MB. BTR is 3.5x more memory efficient than MetaSTAR.

Third, the cost of online inference. BTR is the fastest: ~7 ms for a single belief update, compared to 9-10 ms for UNICORN and CORRO, and ~25 ms for MetaSTAR.

As the rebuttal period is ending in a couple of days, could we kindly ask if the response has addressed your concerns? We are happy to provide further clarification.

Reviewer_826oOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper proposes Bayesian Task Relabelling (BTR) for offline meta-reinforcement learning, targeting behaviour-dependent task inference and the mismatch between training and adaptation-time task beliefs. BTR builds on the Bayesian linear task model and closed-form inference inherited from GLiBRL. It samples reward-function parameters from a posterior-based approximation, generates rewards along collected trajectories while retaining their transitions, and sequentially updates task beliefs. Original and relabelled data train a SAC policy with an asymmetric critic; the actor receives posterior-mean task features. Experiments cover eight control benchmarks, online adaptation, offline-context evaluation, and held-out goal ranges. BTR reports the highest mean return on all eight standard-split online benchmarks and seven offline-context benchmarks, with additional component ablations.

Critical strengths
  1. A practical approach to augmenting offline adaptation data. BTR connects task sampling, learned reward generation, and analytical task inference within one model. It requires neither additional environment interaction nor known task-specific reward functions. Retaining collected transitions also avoids introducing synthetic next-state errors into policy training. This is a useful contribution for settings where interaction is unavailable and reward functions cannot be directly queried.

  2. Strong empirical performance across several task families. The evaluation includes reward-varying and dynamics-varying environments, dense and sparse rewards, and both agent-collected and dataset-provided contexts. All compared methods use the same datasets and task splits. Some improvements are substantial: standard-split online Ant-Dir return increases from the strongest baseline’s 440 to 511, and OOD Ant-Dir return increases from 58 to 308. The component ablations also demonstrate that the complete system benefits from relabelling and privileged critic information in several environments. These results provide meaningful evidence of the method’s practical potential.

Critical weaknesses
  1. The ablations do not isolate the central contribution of posterior task sampling. Removing relabelling also removes sequential belief updates, prior-started histories, and additional policy-training tuples: original tuples instead use the same fixed context at both current and next states (Section 3.3 and Appendix A.4). Consequently, Tables 5–6 cannot distinguish the benefit of imaginary rewards from that of training on evolving contexts or additional data. This is particularly consequential for the large Walker-Param improvement, where the underlying tasks differ only in dynamics. Likewise, the “existing task” comparison changes both the sampling centre and the sampling procedure: it uses another training task’s posterior mean, whereas BTR samples around the source task’s posterior. Tables 8–9 therefore do not isolate the benefit of sampling beyond training-task estimates.

  2. The relationship between the training construction and adaptation-time belief dynamics remains insufficiently validated. Appendix A.4 initializes half of the relabelled histories from a context containing the source task’s original rewards, then continues with rewards from a newly sampled task. Such contexts are not generally histories generated by a single stationary imaginary task. Original tuples additionally freeze the belief across transitions, while online adaptation updates it after every observation. Finally, the actor receives only posterior means, so beliefs with different uncertainty—and different subsequent updates—can have identical policy inputs. These are permissible practical approximations, but their consequences are central to the proposed explanation of improved belief coverage. The paper does not directly measure coverage of adaptation-time beliefs or establish the sensitivity to these choices. This leaves uncertainty about whether the generated training histories address the intended distribution shift reliably.

Questions for authors

none

2 comments

We thank the reviewer for the insightful feedback. We will take the chance to clarify as follows:

W.1.1 Removing relabelling also removes sequential beliefs, prior-started histories and extra tuples, so Tables 5 and 6 cannot separate imaginary rewards from training on evolving contexts. The Walker-Param improvement is the case most affected, since its tasks differ only in dynamics.

BTR has two components: (1) the first offline BLTM-based OMRL (2) easy belief relabelling. Running the first component alone under the same experiment setting will test the control you ask for. It keeps everything in BTR (segments, starting beliefs, step-by-step updates, etc) with the only difference that the recorded reward was used and nothing is relabelled.

Envcomponent (1) onlyBTR
Ant-Dir498 ± 34511 ± 24
Cheetah-Vel-30 ± 1-27 ± 2
Cheetah-Vel-Sparse324 ± 11327 ± 6
Hopper-Param335 ± 20341 ± 22
Hopper-Param-Sparse101 ± 3105 ± 4
Walker-Param506 ± 10450 ± 48
Walker-Param-Sparse107 ± 1103 ± 1
Point-Robot-Sparse31 ± 129 ± 7
Ant-Dir OOD / ID294 ± 43 / 550 ± 14308 ± 45 / 518 ± 14
Cheetah-Vel OOD / ID-62 ± 14 / -24 ± 1-54 ± 6 / -24 ± 1
Cheetah-Vel-Sparse OOD / ID190 ± 53 / 359 ± 4241 ± 5 / 363 ± 3
Point-Robot-Sparse OOD / ID12.6 ± 6.1 / 31.1 ± 7.86.6 ± 0.0 / 28.4 ± 5.1

It is correct that the gain in Walker-Param is indeed from the offline OMRL rather than the relabelling. We thank the reviewer for pointing this out. Nonetheless, the relabelling is still improving most of the standard split / OOD performance as expected. In the revised paper, we will include this table to identify the gain introduced by difference components of BTR more clearly.

W.1.2 The existing-task variant changes both the sampling centre and the sampling procedure, so Tables 8 and 9 do not isolate sampling beyond training-task estimates.

We ran the settings that vary one factor at a time (sampling centre, sampling procedure, segment start).

centreproceduresegment startAnt-DirCheetah-VelCheetah-Vel-SparsePoint-Robot-Sparse
other training taskpointmixed89 ± 24-172 ± 19124 ± 206.5 ± 5.4
other training taskpointprior273 ± 57-67 ± 9208 ± 108.8 ± 3.1
source posteriorsampleprior300 ± 27-65 ± 2228 ± 326.6 ± 5.4
source posteriorpointmixed294 ± 17-84 ± 27235 ± 94.5 ± 3.1
source posteriorsamplemixed308 ± 45-54 ± 6241 ± 56.6 ± 0.0

The first row is Table 9, and the last row is the full BTR. This shows the performance of different factors combined together. The setting BTR by default uses is the best overall.

W.2.1 Coverage of adaptation-time beliefs is not measured.

For each environment we record the belief after every step of the five adaptation episodes on held-out tasks and count the fraction within the 95th-percentile nearest-neighbour radius of the training beliefs, with the training set taken from the original tuples alone or with the relabelled beliefs added.

coverage of adaptation beliefs, OODoriginal tuples+ relabelled
Ant-Dir0.27 ± 0.100.36 ± 0.08
Cheetah-Vel-Sparse0.55 ± 0.040.63 ± 0.03
Cheetah-Vel0.10 ± 0.020.14 ± 0.01
Point-Robot-Sparse0.17 ± 0.030.34 ± 0.15

With relabelling, the coverage on OOD splits are indeed broadened compared to the version without.

W.2.2 Half the relabelled histories start from a source-task context and continue with imaginary rewards, so they are not histories of one stationary task.

The results in W.1.2 has demonstrated empirical evidence that uses the mixed start benefits the learning in general.

W.2.3 Original tuples freeze the belief across the transition, while online adaptation updates it every step.

This is simply a design choice that is shared by every setting in W.1, including the baselines, so it does not affect any comparison.

W.2.4 The actor receives posterior means only, so beliefs with different uncertainty have identical policy inputs.

This is simply following the setting in GLiBRL, where excluding the uncertainty leads to higher performance.

As the rebuttal period is ending in a couple of days, could we kindly ask if the response has addressed your concerns? We are happy to provide further clarification.

Comments on the paper

1 comment
Area_Chair_x5EeOpenReview ↗

AC Reminder: Please Confirm Whether Your Concerns Are Addressed

Dear Reviewers,

The authors posted detailed responses on 8 Nov, added further results on 13 Nov, and followed up on 15 Nov. Please read the response addressed to your review and let us know whether your concerns are now resolved. If not, please state briefly which issues remain and what would settle them; if yes, a short confirmation (and an updated rating where appropriate) would be very helpful. The authors have also offered to provide further clarification, so please raise any remaining request before the discussion period closes.

Thank you for your time. Area Chair

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

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