Bringing physics-based controller policies to virtual reality
Joan Llobera, Pierre Nagorny, Balint Hodossy, Valérie Juillard, Caecilia Charbonnier
Abstract
The use of physics-based controllers in video games and virtual reality (VR) is now technically possible, but little attention has been paid to evaluating the movement quality generated by such controllers, particularly when high-quality motions are needed. Moreover, these controllers have been developed in research-oriented physics engines, which are not suitable for production projects, where game engines like Unity3D or Unreal Engine are preferred. Nowadays, it is easy to set up any element of a VR experience so users can interact with it physically, except for interactive VR characters. Can we extend this to animated VR characters?
In this work, we studied whether physics-based character animation (PBCA) controllers can produce high-quality movement in VR-compatible environments (Unity3D, WebXR). Since VR experiences typically use rigged and textured characters, we evaluated the quality of the movement by capturing and manually retargeting eight walking styles to two rigged and textured characters, which served as reference animations for comparison with the motions generated by the PBCA controllers. We also found that showing the training results on rigged and textured characters helped highlight the controller policies’ animation inaccuracies.
We evaluated the quality of the results, as well as the losses at each stage of the processing pipeline: data ingest, training and inference. For data ingest, we computed accuracy metrics related to the retargeting method used. For training, we computed accuracy metrics related to different training policies and different training environments. We developed new JAX implementations of state-of-the-art PBCA controllers (DeepMimic, AMP and ADD) which can be trained in MuJoCo-MJX in minutes, 50 times faster than in a traditional CPU-based training environment. The benefit of these particular implementations is that the resulting control policies can be readily transferred to Unity3D and support cross-platform compilation, including Android, something critical for use in VR production. For inference, we tested these controller policies in Unity3D and WebXR. Our results suggest that DeepMimic and ADD trained in MuJoCo-MJX generate controller policies with better animation fidelity than other methods.
To simplify the comparison between controller policies, and different reference animations, we implemented an animation fidelity index (afi). Its results are analogous to other more common metrics, but afi is more intuitive to interpret and thus simplifies the comparison of training methods across the successive stages of the processing pipeline. We also did an expert comparison between the reference motions and the end result.
Our results suggest that any use of PBCA in production projects should be approached with caution. Some inaccuracies readily visible to an animator were difficult to detect with the different metrics commonly used, and the overall quality of the results varied considerably depending on different choices made across the processing and delivery pipeline. Finally, we provide the animation data and code to facilitate the transfer of physics-based control research results to the artistic and production communities.
Review reports
Reviewer3 (AI review)
AI Review (reviewer3.com)
Comments (8)
1. Table 1 vs Table 3 MAE joint-angle error values — Minor
Other metrics lead to similar conclusions. In supplementary section B, we show that the more common mean absolute joint-angle error (MAE) leads to similar conclusions when comparing playground policies.
In Table 1, the mean absolute joint-angle error (MAE, in degrees) for the playground policies on characters MM and LL is reported as 2.6° and 3.2° for DeepMimic (mean 2.9°), 3.8° and 4.2° for ADD (mean 4.0°), and 5.6° and 6.0° for AMP (mean 5.8°). However, in Section 4.3 (page 7), the text refers to supplementary section B for "the more common mean absolute joint-angle error (MAE)", where Table 3 reports the mean per-joint orientation error (in degrees) at Unity3D deployment as 6.9° for DeepMimic, 9.4° for ADD, and 22.1° for AMP—values that are two to four times larger than those in Table 1, with no single walk in Table 3 reaching the averages listed in Table 1.
2. Duplicate bibliography entries for DeepMimic, AMP, and ADD — Editorial
VR-compatible environments (Unity3D, WebXR). We evaluated the quality of the outcome of three physics-based controller poli- cies ( DeepMimic [23], AMP [25], ADD [38]), and compared it with the outcome of a simpler and slower CPU-based training pipeline.
The References section contains duplicate entries for three core papers, which are cited interchangeably across sections: DeepMimic appears as both [22] and [23], AMP appears as both [25] and [26], and ADD appears as both [37] and [38].
3. Unblinded author names on page 1 vs anonymization placeholders — Editorial
The manuscript includes full author names, affiliations, and contact email on page 1 (as well as a self-identifying reference in Footnote 6 / Section 3.2.2), but Section 4.4 and the Supplementary Materials / Author Contributions / Acknowledgments sections on page 8 use [removed for submission anonymity] placeholders.
4. Section 4.3 mean differences contradict Table 2 averages — Major
In this regard, where DReCon has the best score of the modular- agents controllers, DeepMimic outscores all other playground con- trollers ( AMP shows a mean difference of 0 . 143 , p < 0 . 0001; ADD shows a mean difference of 0 . 058 , p = 0 . 0021). If we focus only on playground controllers, we observe that ADD is a clear improve- ment over AMP (mean difference of 0 . 085 , p < 0 . 0001), but still does not match DeepMimic (mean difference 0
In Section 4.3 (page 7), the prose reports mean differences between the playground controllers that do not match the averages in Table 2, and the pairwise differences are even arithmetically inconsistent with each other. Specifically, the text states that DeepMimic outscores AMP by a mean difference of 0.143 and ADD by a mean difference of 0.058, and in the very next sentence states that ADD improves over AMP by 0.085 (note 0.143 - 0.085 = 0.058) "but still does not match DeepMimic (mean difference 0.038, p = 0.0042)". Thus, the DeepMimic vs. ADD mean difference is stated as both 0.058 and 0.038 in consecutive sentences. Moreover, according to Table 2, the overall averages are 0.718 (DeepMimic), 0.679 (ADD), and 0.594 (AMP), which yield differences of 0.718 - 0.594 = 0.124 (DeepMimic vs. AMP), 0.718 - 0.679 = 0.039 (DeepMimic vs. ADD), and 0.679 - 0.594 = 0.085 (ADD vs. AMP).
5. Training speedup factor: 50x in Abstract vs 60x in Section 3.3.1 — Editorial
environments. We developed new JAX implementations of state-of- the-art PBCA controllers ( DeepMimic , AMP and ADD ) which can be trained in MuJoCo-MJX in minutes, 50 times faster than in a tra- ditional CPU-based training environment. The benefit of these par-
The Abstract states that the MuJoCo-MJX (playground) implementations can be trained "50 times faster than in a traditional CPU-based training environment." However, Section 3.3.1 states that 100M simulation steps "took approximately 40 hours for each training run based on modular-agents, and 40 minutes for each training run based on playground", which is a 60x speedup (2400 minutes vs. 40 minutes).
6. Figure 4 caption omits MJX stage shown in plot — Editorial
The three playground controllers, in blue, show the losses at different stages of the processing pipeline (rig → MuJoCo C (CPU) → Unity3D).
In Figure 4, the three blue playground panels (a, b, c) plot four columns labeled on the x-axis as Retarget, MJX, MuJoCo C / WebXR, and Unity3D. However, the caption states that the three playground controllers in blue show the losses at the stages (rig->MuJoCo C (CPU)->Unity3D), omitting the MJX stage from the description of the blue columns (whereas Section 4.2 prose describes the playground pipeline stages as MJX -> MuJoCo C -> Unity3D).
7. Mismatched main paper title in Supplementary Materials — Editorial
This document accompanies the main paper “Animation fidelity in physics-based humanoid controllers”.
The title of the main paper on page 1 is "Bringing physics-based controller policies to virtual reality", whereas the introductory paragraph of the Supplementary Materials on page 10 refers to the main paper as "Animation fidelity in physics-based humanoid controllers".
8. Table 1 vs Table 2 and Figure 4 afi scores — Critical
Table 1: Our three playground controller policies, computed on the same 48 CPU rollouts (eight walks per cell).
Table 1 reports afi scores for the playground controllers on characters MM and LL as: DeepMimic (0.90, 0.87), ADD (0.85, 0.82), and AMP (0.71, 0.69), with averages across both characters of 0.885, 0.835, and 0.70. However, Figure 4 and Table 2 report completely different afi scores for the exact same playground controllers across all stages (MJX, MuJoCo C / WebXR, and Unity3D): in Figure 4, the means across all stages are around 0.71–0.72 for DeepMimic, 0.68 for ADD, and 0.57–0.59 for AMP, and in Table 2 (Unity3D deployment), the averages across the 16 motions are 0.718 for DeepMimic, 0.679 for ADD, and 0.594 for AMP. Furthermore, in Table 2, not a single individual walking style on either character achieves an afi score as high as the averages reported in Table 1 (the maximum in Table 2 is 0.809 for LL Happy with DeepMimic, whereas Table 1 reports an LL average of 0.87).
xPeerd (AI review)
AI Review (xPeerd — DAReview)
Summary
This manuscript, titled “Bringing physics-based controller policies to virtual reality,” studies whether physics-based character animation (PBCA) controllers can produce sufficiently high-quality movement for VR-compatible production environments such as Unity3D and WebXR. The paper’s central contribution is a GPU-accelerated JAX/MuJoCo-MJX training pipeline for DeepMimic, AMP, and ADD, plus an evaluation framework that traces animation-fidelity losses from source animation through retargeting, training, sim-to-sim transfer, and deployment . A notable strength is the attempt to evaluate motion quality not only with standard metrics but also with a newly proposed animation fidelity index (afi) and expert visual inspection on rigged, textured characters rather than ragdolls alone . The main empirical conclusion is cautious: DeepMimic and ADD perform best among the tested methods, yet even the best controllers still exhibit a persistent “animation fidelity gap,” especially excessive chest motion and secondary artifacts in the arms and head . The manuscript is timely and practically motivated, but several claims about novelty, metric validity, expert evaluation, reproducibility, and generalizability remain under-justified. Some methodological choices are sensible, yet key details needed for rigorous verification appear incomplete or relegated to supplementary material.
Potential Major Revisions
-
Novelty claims need sharper delimitation against prior work. The manuscript claims three main contributions, including “A GPU-accelerated pipeline with JAX implementations of state-of-the-art PBCA controller policies,” “A high-quality animation benchmark,” and “An evaluation of animation fidelity losses for different policies” . However, the paper also acknowledges that the field already contains large-scale GPU-based pipelines and recent strong baselines such as PULSE, SONIC, BeyondMimic, CLoSD, and MotionBricks . The manuscript would be stronger if it explicitly separated what is genuinely new from what is an engineering integration. At present, the incremental and novel parts are somewhat conflated. For example, the authors state that “we developed new JAX implementations of state-of-the-art PBCA controllers (DeepMimic, AMP and ADD) which can be trained in MuJoCo-MJX in minutes” , but it remains unclear whether the main novelty lies in the implementation, the deployment path to Unity3D/WebXR, the benchmark design, or the afi metric. A clearer novelty map against the strongest 2024–2026 literature is necessary.
-
The proposed afi metric requires stronger validation. The paper states, “To simplify the comparison between controller policies, and different reference animations, we implemented an animation fidelity index (afi). Its results are analogous to other more common metrics, but afi is more intuitive to interpret” . Later, the metric is defined as a weighted combination of root linear celerity, joint angular celerity, and end-effector celerity correlations . This is plausible, but the validation standard is not yet sufficient. The manuscript argues that afi agrees with MAE and MPJPE “on the overall ranking” , yet agreement in ranking is weaker than showing that afi is more sensitive, more perceptually aligned, or statistically better calibrated than existing measures. Since the paper’s practical message depends heavily on afi detecting fidelity losses across pipeline stages, the authors should provide stronger evidence of construct validity, perceptual validity, and robustness to alignment assumptions. The line “m = 0 because we assume signals are temporally aligned” is especially important . Because phase shift is itself one of the artifacts the paper says visual inspection reveals, an index assuming perfect temporal alignment may undercharacterize perceptually important differences.
-
The expert visual evaluation is under-specified and potentially vulnerable to confirmation bias. The manuscript states that “The professional animator who retargeted and cleaned the animations (co-author [removed for submission anonymity]) did a systematic review” . This is a concern. The same person who helped construct the reference motions and clean them then evaluates the quality of the resulting controller outputs. That does not invalidate the assessment, but it does create a risk of evaluator dependence and bias. The paper’s argument that “showing the training results on rigged and textured characters helped highlight the controller policies’ animation inaccuracies” is persuasive in principle , yet the evidence is still largely qualitative. If expert review is central to the claim that standard metrics miss salient artifacts, the methodology for that expert evaluation should be formalized: criteria, blinding, rating scales, inter-rater reliability if possible, and examples of disagreements between quantitative and qualitative judgments.
-
Generalizability is limited by the task design, yet some conclusions are phrased broadly. The authors explicitly justify focusing on walking styles because “they should be relatively easy for a PBCA policy to learn” . They further acknowledge that future work should extend the evaluation “to motions involving richer contacts and object interaction” . This is appropriate, but some broader interpretive claims should then be softened. For instance, “There remains a significant gap between the reference animation and the movement generated by the controller policy” may be true for the evaluated setting, yet the manuscript cannot strongly generalize this as a fundamental limitation of PBCA broadly without including more varied tasks, more controllers, or stronger comparative literature synthesis. The discussion does attempt a mechanistic explanation based on early balance-preserving behaviors and chest movement learned during training , but this remains a hypothesis rather than a tested causal account.
-
Reproducibility details appear incomplete in the main text. The paper emphasizes deployment-sensitive choices such as using ONNX Runtime instead of Sentis because “practical differences in implementation” changed actions materially . It also notes manual parameter tuning to reduce MJX-to-MuJoCo-C discrepancies and substantial effort in software-package selection and controller debugging . These are exactly the kinds of details that determine whether others can reproduce the reported pipeline. Yet many of them seem confined to supplementary appendix A or anonymized repositories. Since the core contribution is a production-oriented pipeline, the main paper should include a more explicit reproducibility summary: exact observation spaces, reward terms and weights, PPO settings, discriminator architecture, deployment runtime settings, retargeting workflow, and how the “small hybrid task reward component (5–15% weight)” for ADD was selected and whether it was fixed or motion-dependent .
-
Some causal interpretations are stronger than the evidence shown. The manuscript claims, regarding ADD, that “the discriminator saturates rapidly... and this saturation is a fundamental architectural limitation... not a tuning problem” . This is a strong statement. It may be correct, but in the present form it reads more like a theoretical assertion than a fully demonstrated empirical conclusion. Likewise, the explanation that early non-falling behavior causes excessive chest movement that later rewards do not overwrite is plausible, but again not directly tested . These passages should either be reframed as hypotheses supported by observations or be backed by ablation experiments, training-trajectory analyses, or discriminator-dynamics evidence.
-
The evidence base is small for benchmarking claims. The benchmark uses “two volunteers —a 10-year-old girl (LL) and a 35-year-old man (MM)” performing “8 different styles” . This is useful as a controlled testbed, but still quite small. The manuscript presents the benchmark as a contribution , yet its scope is limited in demographics, motion diversity, and sample size. The authors should be careful not to oversell it as a broadly representative benchmark without qualification. At minimum, the limitations should be stated more explicitly in the discussion.
-
Fraud/paper-mill risk assessment. I do not see strong signs of paper-mill fabrication. The manuscript is coherent, technically situated within a recognized scientific paradigm, and its claims are generally internally consistent. It includes concrete implementation tradeoffs, nuanced negative findings, and explicit limitations, which are usually reassuring signals . That said, because several strong claims depend on supplementary material, the reviewability of the work would improve if more primary evidence were moved into the main paper.
Potential Minor Revisions
- Writing and grammar issues. Several typographic or lexical issues should be corrected:
- “seemless transfer” should be “seamless transfer” in Appendix A: “A significant effort of this work has been finding the right combination of software packages that enable seemless transfer...”
- “Playgorund pipeline” appears to be a typo for “Playground pipeline” in the numbered list discussing sim2sim transfer
- “as have done virtually all recent contributions” is ungrammatical; likely “as virtually all recent contributions have done”
- “doing so specifically for challenging animations” appears in the conclusion with awkward phrasing; it could be tightened for readability
- Consistency and presentation issues.
- The title visible in the file is “Bringing physics-based controller policies to virtual reality” , but the supplementary material says it accompanies the main paper “Animation fidelity in physics-based humanoid controllers” . If the submission package includes both main and supplementary text under different titles, this should be clarified to avoid confusion during review.
- The paper cites both [37] and [38] for ADD, apparently corresponding to arXiv and conference versions . The bibliography should standardize whether both are needed.
- A few passages rely on supplementary sections for crucial evidence, especially expert evaluation and alternative metrics . Important results should be summarized in the main paper.
- Formatting issues.
- Figure and table cross-references should be checked for readability in anonymized PDF export; in the snippets, some line breaks and symbol rendering are unstable.
- Some mathematical notation and special characters appear distorted in extracted text, suggesting that final camera-ready typesetting should be checked carefully, especially around equations and citations .
- AI content analysis for this post-2021 manuscript. Estimated AI-generated content: low to moderate, approximately 10–20%. Rationale: the manuscript shows domain-specific argumentation, nuanced limitations, and technically grounded comparisons that are more characteristic of expert human drafting than generic synthetic prose. However, a few passages use polished, repetitive contrastive phrasing and broad literature summarization that could have been lightly AI-assisted, especially in overview sections such as the background and high-level framing . I do not identify obvious large sections that read as machine-generated filler. If AI assistance was used, its epistemic impact appears limited because the core contribution depends on implementation details, experimental results, and critical interpretation rather than generic exposition. Still, the authors should ensure that all strong claims—especially around “fundamental” limitations—are evidence-led rather than rhetorically amplified.
Recommendations
The paper has a credible practical motivation and a valuable negative result: current PBCA pipelines, even when technically deployable to Unity3D/WebXR, may still fall short of production-grade animation fidelity. That message is useful. To make the paper stronger, I recommend:
- clarify the precise novelty relative to 2024–2026 PBCA literature;
- strengthen validation of afi beyond ranking agreement with existing metrics;
- formalize and de-bias the expert visual evaluation protocol;
- temper broad claims about fundamental limitations unless supported by targeted ablations;
- move critical reproducibility details from supplement to main text;
- state benchmark limitations more explicitly.
Overall, I see this as a promising and technically engaged manuscript with practical relevance, but one that still needs stronger evidentiary support around metric validity, evaluation methodology, and scope of inference before its conclusions can be fully persuasive.
XSci (AI review)
Summary
The manuscript asks whether physics-based character animation (PBCA) controllers can drive VR characters at production animation quality. Eight walking styles are captured from two actors of very different proportions (a child, LL, and an adult, MM) and manually retargeted by a professional animator onto rigged, textured characters. The authors provide JAX/MJX reimplementations of DeepMimic, AMP and ADD that train in about 40 minutes against about 40 hours for a CPU-based Unity3D/ML-Agents pipeline, and deploy the exported ONNX policies in Unity3D (including Android) and WebXR. Fidelity is tracked at each stage with MAE, MPJPE, NPSS and a new animation fidelity index (afi), and complemented by an expert animator's review. A visible fidelity gap remains, dominated by the training stage.
Contribution and Significance
The contribution that matters is the end-to-end path from an FBX animation to a physics-based controller running on a standalone VR headset and in a browser, with a stage-by-stage accounting of where animation quality is lost and an animator's assessment of what is lost. The practical knowledge in Sections 3.2.1, 3.3.2 and Appendix A — recompiling MuJoCo for Android, the divergence between Sentis and ONNX Runtime, the choice of policy observations — is hard to obtain and not otherwise written down.
Relative to the closest prior work the advance is one of integration and evaluation, not of control. DReCon [3] placed a physics-based controller on a production character in a game engine, Grandia et al. [8] argued for artist-authored references when fidelity matters, MotionBricks [34] integrated policies into Unreal, and Li et al. [15] reported that explicit rewards beat adversarial ones for single-motion fidelity, which Tables 1-3 reproduce. The afi is new, but as defined and validated here it adds nothing over MAE or MPJPE (Major Concern 1). The durable result is the negative one: on simple walk cycles, with matched proportions and manual retargeting, current controllers do not reproduce the reference closely enough for production.
Strengths
- Table 4 is the most valuable part of the paper: 32 policy-animation pairs scored 0-100 with written diagnoses, converging on one repeatable artefact (excess chest motion propagating to arms and head, plus foot skating) explained in Section 5.4.
- The stage decomposition of Figure 4 (retarget, MJX, MuJoCo C, Unity3D) is the right instrument here, and the finding that the loss concentrates in training rather than transfer is useful and not obvious.
- Identifying simulator-specific observations such as cinert as the cause of MJX-to-MuJoCo-C divergence (Section 3.2.1) is a concrete insight other groups can reuse.
- The released benchmark of Section 3.1 — two very different body proportions, eight styles, manual retargeting, ragdolls matched to the skeletons — is better controlled than what the PBCA literature normally trains on.
Recommendation
Major Revision for ACM SIGGRAPH MIG. The pipeline, the released benchmark and the expert evaluation are a contribution this venue's readers would use, and the central negative finding is credible. The quantitative half of the paper, however, cannot currently be relied on: Table 1 cannot be reconciled with Tables 2 and 3, two mean differences in Section 4.3 contradict Table 2, and afi is defined inconsistently with the properties claimed for it and never validated against the expert scores already collected. All of this is repairable within the authors' own approach, hence a revision rather than a rejection.
Major Concerns
-
The animation fidelity index is inconsistent with the properties claimed for it, and is not validated (Section 3.3.3, Equations 1-3; Sections 4.1, 4.3, B). Equations 1-3 fix "m = 0 because we assume signals are temporally aligned", so afi is a zero-lag normalised inner product with no lag search; it cannot therefore be, as Section 4.1 and Appendix B both assert, a measure that "tolerates small phase shifts". The denominators are also products of squared norms rather than of norms, so the reference compared with itself scores 1/||x||^2, not 1, contradicting Section 4.3 (the reference "has by construction a score of 1 for any animation"); non-negativity of the celerities gives only afi >= 0, not afi <= 1.
The deeper problem is that afi is offered as capturing what standard metrics miss, yet the data that would test this is never used: Table 4 scores the same pairs as Table 2, and no correlation is reported. Where the two can be compared, afi does not track the expert. ADD on LL Wounded scores 0.629, barely below ADD on LL Neutral (0.674), although the animator scores the first 10 ("She does not manage to move forward") and the second 75. ADD on LL Fashion has the second-highest afi of the LL block (0.765) with an expert score of 50, while DeepMimic on that motion scores 0.664 with an expert score of 60 — afi reverses the expert ranking. Correlating afi, MAE and MPJPE against the 32 expert scores would settle whether afi earns its place.
-
The reported numbers do not agree across Tables 1-3 and the text. Table 1 gives afi of 0.90/0.87 for DeepMimic, 0.85/0.82 for ADD and 0.71/0.69 for AMP (MM/LL); the per-animation means in Table 2 are 0.734/0.701, 0.685/0.673 and 0.594/0.594. Since Section 4.2 and Figure 4 report the losses after training as negligible, both tables cannot be right. The same holds for joint error: Table 1 reports MAE of 2.6/3.2, 5.6/6.0 and 3.8/4.2 degrees, whereas Appendix B states that Table 3 scores "the same 16 controller/reference pairs" with the pose-error metric and gives column means of 6.9, 22.1 and 9.4 degrees — a factor of 2.5 to 4.5 that varies by method, so not a stage or unit offset. Table 1's root-relative MPJPE of 1.3-1.5 mm is likewise implausible beside a joint error of a few degrees, since 2.6 degrees across a 0.4 m segment already gives about 18 mm. Section 4.3 compounds this: the DeepMimic-AMP mean difference is reported as 0.143 where Table 2 gives 0.718 - 0.594 = 0.124, and the DeepMimic-ADD difference is given as 0.058 and then, two sentences later, as 0.038 (Table 2 gives 0.0384). Please recompute every value from one set of rollouts and state which stage each table reports.
-
The controller comparison is not like-for-like and rests on one run per cell (Sections 4.1, 4.3, Appendix A). By the authors' own account ADD was given "a small hybrid task reward component (5-15% weight)" to overcome discriminator saturation, which adds an explicit tracking signal to an adversarial method, while AMP was left with a reference-resampling seam that, in Appendix A, "AMP's discriminator amplifies" and whose removal "could improve AMP". The ranking DeepMimic > ADD > AMP, and the production recommendation built on it, therefore compare controllers under unequal conditions. Each cell also appears to be a single training run: no seeds or variances are reported, and the Wilcoxon tests treat the 16 animations as the only source of variability, so a difference of 0.038 afi is read as real without knowing the run-to-run spread of an RL training. Relatedly, p = 0.27 is taken to show the GPU pipeline gives "equivalent results", which with n = 16 is not evidence of equivalence. Re-running each controller with matched reward structures, the seam fixed, and at least three seeds per cell would settle all three points.
Minor Comments
- The abstract claims training "50 times faster", but Section 3.3.1 reports 40 hours against 40 minutes, a factor of 60; the comparison also changes hardware, RL library, physics backend and controller at once, so it does not isolate GPU against CPU.
- Section 4.1 states that "all controllers evaluated achieve 100% survival ... across all 16 motions" but also refers to "ADD rollouts that terminate early", and Table 4 scores ADD on Wounded at 10; define survival and report it per motion.
- Since the Figure 4 caption states that the WebXR afi "is numerically identical to that column" (MuJoCo C), the claim that WebXR fidelity is comparable to Unity3D follows from the architecture, not from a measurement.
- The expert evaluation (Section 4.4) uses a single unblinded rater who is a coauthor and produced the reference animations; a second rater, blind to the policy, would make Table 4 much stronger.
- There is no validation with participants although afi is motivated by perceptual studies, and a directly relevant work is missing: P. S. A. Reitsma and N. S. Pollard, "Perceptual metrics for character animation: sensitivity to errors in ballistic motion", ACM Transactions on Graphics 22(3):537-542, 2003.
- The claim in Section 5.4 that no PBCA article maps controller poses onto a rigged and textured character should be qualified, since DReCon [3] and ASE [24] both show skinned characters.
- No inference cost is reported: CPU time per frame, frame rate, or how many characters fit a standalone Android headset's budget.
- Equations 1-3 are garbled (term 2 appears with an empty denominator), and the reduction of the 19 per-joint and 4 end-effector signals to one scalar per term is unspecified.
- The reference list duplicates the same works, cited inconsistently: [22] and [23] (DeepMimic), [25] and [26] (AMP), [37] and [38] (ADD).