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Under review as a conference paper at ICLR 2027

HoRD: Robust Humanoid Control via History-Conditioned Reinforcement Learning and Online Distillation

Abstract

Humanoid robots hold great promise for general-purpose embodied intelligence, but their control policies often suffer significant performance drops under small changes in robot and environmental dynamics. Dense full-body references simplify tracking but impose a restrictive deployment command, whereas sparse targets leave uncommanded joints underdetermined. We present HoRD, a two-stage learning framework for whole-body humanoid control under partial observability and varying dynamics. A teacher first learns dense-reference tracking under episode-level domain randomization. Its control behavior is then transferred through online distillation to a student that receives partial observations and Standardized Sparse-Joint Representation (SSJR) commands over a fixed set of future key-joint targets. Both policies use a History-Conditioned Dynamics Representation (HCDR), a history encoder that summarizes recent state–action interactions into a control-oriented representation. HoRD achieves State-Of-The-Art (SOTA) performance across four conditions spanning Isaac Lab and Genesis, including zero-shot cross-simulator transfer under fixed and randomized dynamics. Ablations show that episode-level domain randomization and HCDR play complementary roles under dynamics shift. Qualitative Unitree G1 rollouts further illustrate real-world deployment without fine-tuning.

Primary area:
reinforcement learning
Keywords:
Robot Learning, Humanoid Control, Policy Distillation, Partial Observability

Reviews

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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_63suOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

HoRD studies robust humanoid motion tracking from sparse commands under varying dynamics. The method uses a two-stage teacher–student framework. A teacher is trained with full-state observations, dense motion references, and domain randomization. Its behavior is then distilled into a student that operates on partial observations and sparse future motion targets. Both policies use an HCDR module to encode recent observations and actions for dynamics adaptation. The authors evaluate 873 held-out AMASS motions in Isaac Lab and Genesis, with ablations on domain randomization, history conditioning, and encoder design. Qualitative demonstrations on a Unitree G1 are also provided.

Critical strengths
  1. Strong results under cross-simulator transfer. I find the Genesis + DR results particularly convincing. Compared with GMT/ResMimic, HoRD improves success from 78.4% to 84.4%, while reducing global and local position errors from 321 mm to 171 mm and from 184 mm to 108 mm. Evaluating under randomized dynamics in an unseen simulator provides useful evidence beyond performance in the training environment.

  2. The ablations show the importance of history conditioning under dynamics changes. Removing HCDR has little effect on success under standard Isaac Lab dynamics, but performance drops considerably under randomized dynamics and in Genesis. The results also show the importance of domain randomization. These comparisons help explain when history conditioning is actually useful.

Critical weaknesses
  1. The evaluation lacks uncertainty estimates, and some reported success rates are difficult to reconcile with the stated protocol. Tables 1 and 2 do not clearly report the number of independent training runs or provide uncertainty estimates. This is particularly relevant to the small success-rate differences of 0.9 and 1.0 percentage points in the Isaac Lab settings. Testing 873 motions provides broad coverage, but does not address run-to-run variability. I also could not reconcile the success rates in Table 6 with the stated evaluation counts. Appendix A.5 describes six motions with ten rollouts each. Assuming binary success and equal pooling over 60 rollouts, the reported 81.2% and 80.6% would not follow directly.

  2. The encoder comparison does not account for differences in model capacity. Table 3 compares several history encoders under the same input and training settings, but their trainable parameter counts are not reported. Matching the latent width and training budget does not necessarily make the models comparable in capacity. Without this information, it is difficult to judge whether the Q-Former's advantage comes from its architecture or a larger parameter budget.

Questions for authors
  1. How many independent training runs and evaluation rollouts were used for Tables 1 and 2? Are uncertainty estimates available, particularly for the smaller performance differences?

  2. How exactly were the 81.2% and 80.6% success rates in Table 6 calculated? The stated six motions and ten rollouts per motion do not seem to produce these values under simple binary-success averaging.

  3. What are the trainable parameter counts of the encoders compared in Table 3? Were their parameter budgets matched?

1 comment
AuthorsOpenReview ↗

Rebuttal by Authors

We thank the reviewer for the constructive feedback and for recognizing our cross-simulator results and the benefits of history conditioning.


W1 & Q1: “How many independent training …? Are uncertainty estimates available…?”

Training and evaluation settings. Each method and ablated variant in Tables 1 and 2 was trained using one independent training run. Cross-training-run uncertainty estimates are therefore not available.

Evidence supporting our main conclusions. Our central empirical finding concerns transfer under dynamics and simulator shifts. In Genesis + DR, Table 1 reports 84.4% success for HoRD versus 78.4% for the strongest reported baseline, together with a reduction in Eg-mpjpeE_{\mathrm{g\text{-}mpjpe}} from 321 mm to 171 mm. These results show an observed improvement in both task completion and tracking accuracy.

The history ablation provides complementary evidence. Removing HCDR from both policies and retraining leaves nominal Isaac Lab success nearly unchanged, but reduces Genesis success from 86.0% to below 10%, demonstrating the importance of the learned history representation for cross-simulator transfer.


W1 & Q2: “How exactly were the 81.2% and 80.6% success rates in Table 6 calculated?”

Table 6 was evaluated on the full AMASS evaluation motion set. The reference to “six motions” in Appendix A.5 is a writing error. The six representative motions were used for training and testing the encoder variants in Table 3. Table 6 instead evaluates already-trained policies on the full AMASS evaluation set under the diagnostic conditions, without retraining.

We will correct Appendix A.5, the Table 6 caption, and the accompanying discussion.


W2 & Q3: “What are the trainable parameter counts of the encoders compared in Table 3? Were their parameter budgets matched?”

Q-Former and LSTM have nearly identical trainable parameter counts, while their observed performance differs substantially. Although the parameter budgets for these five architectures are not exactly the same, most of them are quite close.

All configurations use an eight-step state–action history with 522 dimensions per step and produce a 256-dimensional latent representation. Their configuration-based parameter estimates and Table 3 results are:

History encoderTrainable Parameters↓Succ. ↑Eg-mpjpeE_{\mathrm{g\text{-}mpjpe}} ↓
MLP2.795M63.3277
GRU3.299M23.3667
LSTM4.354M21.6655
Transformer3.293M<10728
Q-Former4.349M95.0134

The Q-Former–LSTM comparison is particularly informative. Both have approximately 4.35M trainable parameters, yet Q-Former achieves 95.0% versus 21.6% success, a difference of 73.4 percentage points, and reduces EmpjpeE_{\mathrm{mpjpe}} from 655 to 134 mm. Under these estimates, Q-Former’s advantage over LSTM is not accompanied by a larger parameter budget. This contrast supports the relevance of encoder design beyond total parameter count in the six-motion diagnostic.

We will add the architecture and parameter-estimation details, clarify the capacity differences, and highlight the Q-Former–LSTM comparison when interpreting Table 3.


Together, we hope our detailed responses and the additional experiments have adequately addressed your concerns, and we would be very grateful if you might consider raising your score in light of these updates.

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

HoRD studies humanoid motion tracking from sparse future commands under changes in robot and simulator dynamics. A dense-reference teacher is trained with privileged observations and episode-level domain randomization. Online distillation then trains a student receiving partial observations and future pelvis, hand, and ankle targets. In each policy, a Q-Former encodes recent observations and actions into a History-Conditioned Dynamics Representation (HCDR), which conditions the current action. Only the student is deployed. Evaluation covers 873 held-out AMASS motions in Isaac Lab and Genesis, with fixed and randomized dynamics. The paper reports 84.4% success under Genesis + DR, compared with 78.4% for the strongest listed baseline. It also presents history/randomization ablations, a six-motion encoder comparison, dynamics-switching diagnostics, and qualitative Unitree G1 deployment.

Critical strengths
  1. HoRD improves tracking under the reported cross-simulator transfer protocol. On 873 held-out motions in Genesis + DR, Table 1 reports 84.4% success versus 78.4% for the adapted GMT/ResMimic baseline, with global joint-position error reduced from 321 to 171 mm.

  2. The history ablation shows that interaction history helps transfer across dynamics. With domain-randomized training fixed, removing HCDR reduces Genesis success from 86.0% to below 10% (Table 2). Nominal Isaac Lab success remains similar at 90.7% with HCDR and 91.3% without it.

Critical weaknesses
  1. HoRD's framework contribution needs clearer separation from OmniH2O. The introduction (lines 70–79) says sparse motion specification and dynamics adaptation have largely been studied separately. Yet OmniH2O, §3 and Appendix F already combines sparse commands, observation/action history, domain randomization, and a privileged teacher supervising student-visited states for humanoid whole-body control. This same-setting precedent calls for a narrower research-gap statement.

    HoRD adds five-point future commands, separately trained Q-Former history encoders, and a dynamics-transfer study. OmniH2O emphasizes implicit velocity and robustness, so the shared framework does not establish equivalent adaptation capabilities. Please explain what the command and encoder changes add to the existing framework and distinguish those methodological changes from the empirical transfer findings.

Questions for authors
  1. Relative to OmniH2O's combination of sparse commands, history, domain randomization, and online teacher–student supervision, which specific mechanism accounts for HoRD's claimed methodological advance? Please distinguish that mechanism from the empirical contribution of the transfer evaluation.

  2. Tables 1–3 evaluate the complete student with SSJR but do not isolate its keypoint set or look-ahead information. What methodological benefit is claimed for these choices beyond providing a workable sparse interface? Please explain the input trade-off and identify controlled evidence if an independent advantage is claimed. Also specify whether Table 2 removes HCDR from both policies or only the student.

1 comment
AuthorsOpenReview ↗

Rebuttal by Authors

We thank the reviewer for the thoughtful feedback and for recognizing our cross-simulator results and the benefits of history conditioning.


W1 & Q1: “…which specific mechanism accounts for HoRD's claimed methodological advance? Please distinguish that mechanism from the empirical contribution of the transfer evaluation.”

Methodological contribution. Our proposed changes concern the motion-command representation and the mechanism for conditioning control on interaction history. In HoRD, SSJR specifies future trajectories of the pelvis, hands, and ankles, providing explicit root-motion and foot-placement targets alongside upper-body motion intent. HCDR uses dedicated history encoders to summarize recent state–action interactions into compact representations that condition the teacher and student policies. These are the specific command and history-encoding changes we introduce within the shared teacher–student framework.

Empirical finding. Our evaluation reveals that similar nominal success rates can conceal substantially different transfer capabilities. In Table 2, removing HCDR leaves nominal Isaac Lab success nearly unchanged (91.3% without HCDR versus 90.7% with HCDR), but reduces zero-shot Genesis success from 86.0% to below 10%. Thus, within our evaluation setting, history has a much greater impact on success under simulator shift than under fixed nominal dynamics.


Q2: “…What methodological benefit is claimed for these choices beyond providing a workable sparse interface?…”

SSJR as a structured representation of motion intent. We formulate sparse-command tracking as learning whole-body control from partially specified motion goals. SSJR projects a dense future reference onto selected pelvis, hand, and ankle targets, explicitly specifying root motion, upper-body intent, and foot placement while leaving the remaining body coordination unspecified.

Controlled dense–sparse comparison. We retrained a student with dense commands, keeping all other settings unchanged, including the look-ahead horizon, and using the same held-out evaluation protocol as Table 1.

Student commandsIsaacLab nominalIsaacLab + DRGenesis nominalGenesis + DR
Succ. ↑Eg-mpjpeE_{\mathrm{g\text{-}mpjpe}} ↓EmpjpeE_{\mathrm{mpjpe}} ↓Succ. ↑Eg-mpjpeE_{\mathrm{g\text{-}mpjpe}} ↓EmpjpeE_{\mathrm{mpjpe}} ↓Succ. ↑Eg-mpjpeE_{\mathrm{g\text{-}mpjpe}} ↓EmpjpeE_{\mathrm{mpjpe}} ↓Succ. ↑Eg-mpjpeE_{\mathrm{g\text{-}mpjpe}} ↓EmpjpeE_{\mathrm{mpjpe}} ↓
SSJR90.70102.0076.0088.40124.0087.0086.00162.0096.0084.40171.00108.00
Dense97.3784.1698.2093.9392.37105.1597.2591.23100.9295.6595.27103.29

Dense commands improve success and global tracking accuracy, while SSJR achieves lower local EmpjpeE_{\mathrm{mpjpe}} in three of four conditions. This comparison quantifies the performance trade-off associated with sparse motion specification under a look-ahead setting.

Our central contribution concerns history-conditioned whole-body control and its transfer across dynamics under sparse motion commands. The new comparison provides controlled evidence for the dense–sparse trade-off.


Q2: “…specify whether Table 2 removes HCDR from both policies or only the student.”

Scope of the no-H ablation. In Table 2, HCDR was removed from both the teacher and student networks, and both policies were retrained. The ablated system did not reuse the teacher from full HoRD. The comparison therefore evaluates the contribution of history conditioning across the two-stage pipeline. The similar nominal success rates and markedly different Genesis results highlight the importance of history for transfer within this pipeline.

We will incorporate the dense–sparse comparison, clarify SSJR’s input requirements and the scope of its supporting evidence, and specify the retraining procedure in the Table 2 caption.


Together, we hope our detailed responses and the additional experiments have adequately addressed your concerns, and we would be very grateful if you might consider raising your score in light of these updates.

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

HoRD addresses humanoid motion tracking under partial observability and dynamics variation. A privileged teacher learns dense-reference tracking with domain randomization, then supplies action targets at student-visited states. The student uses sparse future trajectories for the pelvis, hands, and ankles (SSJR), together with a Q-Former encoding recent observations and actions (HCDR). Experiments evaluate a Unitree G1 in Isaac Lab, zero-shot transfer to Genesis, and qualitative hardware deployment. The problem is relevant, and the reported cross-simulator results are promising. However, the present evidence does not sufficiently establish the contribution of the proposed components or the reliability of the comparisons.

Critical strengths
  1. Meaningful transfer results. In Genesis + DR, HoRD improves success from 78.4% to 84.4% over the strongest reported baseline and reduces global pose error from 321 mm to 171 mm (Table 1). The pose-error improvement is substantial.
  2. Coherent system design. Dense teacher supervision, sparse deployment commands, and interaction history address complementary practical constraints.
  3. Useful breadth of evaluation. The manuscript includes 873 held-out motions, two simulators, encoder ablations, dynamics-switching diagnostics, and hardware demonstrations.
  4. Appropriately qualified hardware claims. Appendix D explicitly limits the real-world evidence to deployment feasibility, acknowledging the absence of instrumented conditions and repeated-trial comparisons.
Critical weaknesses
  1. The novelty and component contributions are insufficiently isolated. The framework combines established ingredients: privileged teacher–student learning, online action distillation, sparse motion commands, domain randomization, and history conditioning. The manuscript needs stronger evidence for what its particular combination adds. There is no controlled comparison of sparse versus dense student commands, alternative keypoint selections, or direct sparse-command RL versus teacher distillation. Despite Section 4 announcing an evaluation of online distillation, no online-versus-offline distillation comparison is presented. Consequently, the benefits attributable to SSJR and the training procedure remain unclear.

  2. Baseline comparisons confound the controller with command information and implementation choices. Appendix A.4 retains each baseline’s own command formulation. HoRD receives future pelvis and ankle trajectories, potentially providing materially different locomotion information from other interfaces. The resulting table compares complete systems but cannot isolate the proposed learning method. Moreover, GMT and ResMimic are combined into one locally implemented controller, leaving unclear which method is actually represented. The severe failures of several baselines warrant implementation validation and more detailed adaptation descriptions. A shared-command comparison against the strongest baselines would be especially valuable.

  3. The evidence supports history dependence more directly than dynamics adaptation. Removing HCDR also removes temporal information useful for state estimation, filtering, and motion-phase inference. Table 2 therefore does not establish that HCDR specifically identifies or adapts to dynamics. The encoder comparison helps, but uses only six motions and does not report parameter counts, compute, tuning effort, or uncertainty. The Transformer’s below-10% success particularly needs explanation. History-reset, shuffled-history, or action-history ablations, together with recovery curves after dynamics changes, would better distinguish the proposed mechanism.

  4. Important reproducibility and evaluation details are missing or ambiguous. The appendix does not specify the actual history length, command horizon, observation vectors, query-token count, latent dimensions, or complete policy architecture. The SSJR coordinate frames and configuration contents are also insufficiently defined. Table 7 omits contact-parameter randomization despite its mention in the method, and provides push intervals without magnitudes. The stress ranges, terrain geometry, and perturbation magnitudes are unspecified. Early termination also makes it essential to explain whether pose errors use surviving prefixes, completed episodes, or some treatment of the remaining trajectory. Appendix B.2’s “local” MPJPE definition needs clarification: subtracting initial positions is not, by itself, the usual per-frame root-relative alignment.

  5. Statistical reporting contains an unresolved inconsistency. No training-seed variability or confidence intervals are reported, making the 0.9–1.0 percentage-point in-simulator success gains difficult to assess. More concretely, Table 6 specifies six motions with ten rollouts each. A binary episode-success rate over 60 trials must change in increments of approximately 1.67 percentage points, yet reported values include 81.2% and 80.6%. Additional averaging could explain this, but is not documented. The aggregation procedure and underlying counts should be provided

Questions for authors
  1. How much of the improvement remains when the strongest baselines receive exactly the same SSJR commands and future horizon?
  2. What are the teacher’s performance and the student’s distillation gap? How do direct sparse-command RL and offline distillation compare?
  3. Can you provide history-intervention experiments and time-resolved recovery after dynamics switching?
2 comments
AuthorsOpenReview ↗

Rebuttal by Authors [1/2]

We thank the reviewer for the thoughtful and constructive feedback, and for recognizing our cross-simulator results.


W1 & Q2: “... contributions are insufficiently isolated.” “...teacher’s performance and the student’s distillation gap?”

We provide a controlled command ablation, teacher–student diagnostics, and clarification of the training rationale.

Dense versus sparse student commands. We retrained a student with dense commands, keeping all other settings unchanged and using the same held-out evaluation protocol as Table 1.

Student commandsIsaacLab nominalIsaacLab + DRGenesis nominalGenesis + DR
Succ. ↑Eg-mpjpeE_{\mathrm{g\text{-}mpjpe}} ↓EmpjpeE_{\mathrm{mpjpe}} ↓Succ. ↑Eg-mpjpeE_{\mathrm{g\text{-}mpjpe}} ↓EmpjpeE_{\mathrm{mpjpe}} ↓Succ. ↑Eg-mpjpeE_{\mathrm{g\text{-}mpjpe}} ↓EmpjpeE_{\mathrm{mpjpe}} ↓Succ. ↑Eg-mpjpeE_{\mathrm{g\text{-}mpjpe}} ↓EmpjpeE_{\mathrm{mpjpe}} ↓
SSJR90.70102.0076.0088.40124.0087.0086.00162.0096.0084.40171.00108.00
Dense97.3784.1698.2093.9392.37105.1597.2591.23100.9295.6595.27103.29

SSJR achieves lower EmpjpeE_{\mathrm{mpjpe}} in three of four conditions, while specifying future targets for the pelvis, hands, and ankles and leaving the remaining coordination to the learned controller. This demonstrates whole-body tracking from partially specified motion goals with reduced reference-information requirements at deployment. Dense commands improve success and global alignment, quantifying the associated performance trade-off.

HCDR learns a latent representation. Table 2 evaluates its contribution while keeping SSJR commands fixed: removing HCDR from both policies and retraining reduces Genesis success from 86.0% to below 10%, demonstrating the importance of this learned history representation for zero-shot cross-simulator transfer.

Teacher–student gap. In separate training-motion diagnostics, the teacher completes 98.61% trajectories, with 95.70 mm Eg-mpjpeE_{\mathrm{g\text{-}mpjpe}}, across three terrains under nominal and randomized dynamics. Paired flat-ground evaluations use identical motions, evaluation seeds, and dynamics samples. The sparse student has approximately 5–8 mm higher Eg-mpjpeE_{\mathrm{g\text{-}mpjpe}}, with similar success rates.

Online distillation. Our learning problem is to transfer a privileged, dense-reference teacher’s whole-body behavior to a student operating from sparse commands. Teacher action targets provide supervision for body coordination that is not explicitly specified by those commands. We query the teacher at student-visited states, including tracking deviations, so that supervision follows the state distribution the student actually encounters. This addresses the coverage mismatch that can arise with a fixed dataset of teacher-generated trajectories.

The paired training-motion diagnostics above show similar teacher–student success rates with a 5–8 mm global tracking-error gap, supporting effective dense-to-sparse transfer in this setting. Our experiments evaluate this transfer pipeline; a comparison against direct sparse-command RL or offline distillation is beyond the scope of this paper.

We will incorporate these results, distinguish held-out evaluations from training-motion diagnostics, and revise Section 4 to align its claims with the completed comparisons.


W2 & Q1: “…command information and implementation choices…” “…exactly the same SSJR commands and future horizon?”

Baseline implementations. All baselines in Table 1 follow their published method descriptions and are adapted to our common G1 benchmark. MaskedMimic, OmniH2O, ExBody2, and HOVER are adapted from released implementations; GMT and VisualMimic are local reimplementations. Specifically, the entry labeled “GMT/ResMimic” evaluates the GMT base policy described in ResMimic. We will correct this label accordingly. All methods share the split, evaluation criteria, and zero-shot Genesis protocol.

Command information. Our strongest baseline GMT retains dense reference targets for all 29 joints, whereas HoRD receives sparse future pelvis, hand, and ankle targets. Despite these disadvantages, HoRD achieves 84.4% versus 78.4% success in Genesis + DR, with global MPJPE reduced from 321 to 171 mm. Our newly controlled student ablation (above) shows that dense commands further improve HoRD’s success and global tracking accuracy, quantifying the information trade-off within our pipeline. SSJR reduces the need to supply complete whole-body reference motions at deployment while allowing the controller to learn the remaining coordination.

AuthorsOpenReview ↗

Rebuttal by Authors [2/2]


W3 & Q3: “…history dependence…dynamics adaptation…” “…history-intervention experiments and time-resolved recovery after dynamics switching?”

Table 2 establishes the contribution of history under dynamics shift. We remove HCDR from both policies and retrain both, keeping commands and DR unchanged. Nominal IsaacLab success remains comparable (90.7% with HCDR versus 91.3% without it), whereas removing HCDR reduces success from 88.4% to 70.5% under IsaacLab + DR and from 86.0% to below 10% in Genesis. The strongest success-rate benefit therefore emerges precisely when latent dynamics or the simulator change.

Table 6 extends this evidence to nonstationary dynamics. On the full AMASS evaluation motion set, HoRD achieves 81.2% success under stress and 80.6% under mid-episode dynamics switching, compared with 62.2% and 53.2% for the strongest comparator in each condition. The controller remains effective when dynamics change during execution, beyond transfer to a different fixed simulator.

Together, Table 2 identifies history conditioning as a key contributor to transfer, while Table 6 demonstrates robustness during dynamics changes. These results support implicit history-conditioned adaptation at the control-policy level. These results demonstrate the importance of HCDR’s learned history representation for robust whole-body tracking under dynamics variation and zero-shot cross-simulator transfer.


W4: Reproducibility details and evaluation metrics.

History encoder. HCDR uses 8 learnable query tokens, each 256-dimensional, to attend to an eight-step state–action history. Each history step contains 493 state dimensions and 29 action dimensions. The state comprises root height, root-relative body positions, body rotations, and linear/angular velocities. The Q-Former has 4 layers, 8 attention heads, hidden width 256, and FFN width 1,024, and outputs a 256-dimensional history representation.

Control and randomization. Physics runs at 200 Hz, with policy control at 50 Hz (decimation 4). Future reference targets are sampled at 20 ms intervals. In Isaac Lab, body masses, joint friction and armature, and PD proportional/derivative gains are scaled by factors sampled uniformly from [0.9, 1.1]. The gravity randomizer adds a vertical perturbation sampled from [−0.1, 0.1] m/s².

Evaluation protocol. All methods within each experiment use the same motion set, failure criterion, metric definitions, and aggregation rules. Automatic resets are disabled: rollouts continue until the reference motion ends, and errors after failure remain included. Errors are averaged over each motion’s duration and then across motions. A motion fails if its per-frame mean global joint-position error exceeds 0.5 m at any point. This follows the full-duration accounting in MaskedMimic’s Repo.

Local MPJPE. At each frame, executed and reference joint positions are independently centered at their respective roots and aligned using their respective inverse root headings: p~t,j=Rz(−ψt)(pt,j−pt,root).\tilde p_{t,j}=R_z(-\psi_t)\left(p_{t,j}-p_{t,\mathrm{root}}\right). Local MPJPE averages the Euclidean distances between these transformed positions. Global MPJPE uses world-frame positions and retains translation and heading discrepancies.

We will add these specifications to the appendix, distinguish training termination from evaluation accounting, and correct Appendix B.2 to state the per-frame root-relative, heading-aligned definition.


W5: Statistical uncertainty and the evaluation counts in Table 6.

Table 6 uses 873 AMASS evaluation motions. The six representative motions were used to train and evaluate the encoder variants in Table 3. Table 6 instead evaluates already-trained policies on the full AMASS evaluation set under stress and dynamics-switching conditions, without retraining. The six-motion description in Appendix A.5 and the Table 6 caption is a writing error.


Together, we hope our detailed responses and the additional experiments have adequately addressed your concerns, and we would be very grateful if you might consider raising your score in light of these updates.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Rebuttal Summary

Dear AC and Reviewers,

In this work, we introduce HoRD, a two-stage learning framework for whole-body humanoid control under partial observability and varying dynamics. Experiments show that HoRD achieves SOTA performance in zero-shot transfer across simulators under both fixed and randomized dynamics. We thank all reviewers for their constructive feedback and for recognizing the following strengths of HoRD:

  • Strong zero-shot cross-simulator transfer (VdFm, mGhK, 63su),
  • Clear benefit of history conditioning under dynamics shift (mGhK, 63su)
  • Coherent design and broad evaluation (VdFm).

In the rebuttal, we:

  1. Added a controlled dense vs. sparse command ablation (VdFm, mGhK). We added this comparison to Section 4.3 as a new Table 2. Dense commands improve success, while HoRD with SSJR achieves lower local MPJPE in 3/4 conditions using far fewer deployment targets.

  2. Reported the teacher–student gap (VdFm). We added these diagnostics to Appendix A.2 and labeled them separately from the held-out evaluations. On six training motions, HoRD's sparse student reaches success rates similar to the teacher's, with only 5–8 mm higher global MPJPE. This shows that HoRD's online distillation transfers the dense teacher's behavior effectively on these motions.

  3. Reported encoder parameter counts (63su, VdFm). We added them to Table 4 and its discussion in Section 4.4. Q-Former and LSTM have nearly identical trainable parameter counts (~4.35M), yet HoRD's Q-Former-based HCDR reaches 95.0% success vs. 21.6% for LSTM on the six-motion Genesis + DR diagnostic.

  4. Clarified Table 6 (VdFm, 63su), now Table 7 in the revised manuscript. It is evaluated on all 873 motions. “Six motions” was a writing error. We corrected it in Appendix A.5, the Table 7 caption, and the accompanying discussion. On this full set, HoRD achieves 81.2% success under stress vs. 62.2% for ExBody2, and 80.6% under mid-episode dynamics switching vs. 53.2% for OmniH2O.

  5. Clarified positioning vs. OmniH2O and the ablation scope (mGhK). We also stated in the Table 3 caption that HCDR is removed from both policies, which are then retrained. HoRD's methodological contributions are SSJR and HCDR, and without HCDR, HoRD's Genesis success drops from 86.0% to below 10%.

  6. Provided reproducibility details (VdFm), including the HCDR architecture (Appendix C.3), randomization ranges (Appendix C.2, Table 8), the evaluation protocol and failure accounting (Appendices A.4 and B.1), and the corrected local MPJPE definition (Appendix B.2). The code is included in the supplementary material, and all datasets generated by HoRD will be publicly released.

Detailed responses to each reviewer are provided in the individual threads. We hope these revisions address your concerns. We are happy to clarify any remaining questions during the discussion period.

Best regards,

The authors

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