The main results are inconsistent with the category-level results under the stated aggregation protocol.
Appendix A.4 states that metrics are computed per scenario and then averaged over scenarios. Sections 4.1 and A.1 specify 70 single-presenter, 20 complex-action, and 60 two-person scenarios. Therefore, each overall metric should equal the category means in Table 6 weighted by 70/150, 20/150, and 60/150. Several reported values do not satisfy this requirement:
Metric Overall implied by Table 6 Reported in Table 1
LipSync 6.775 6.960
Desync 0.0693 0.0570
Listener (%) 80.77 78.50
WER (%) 1.047 0.850
Spk-Sim 0.5789 0.5960
ID-Sim 0.6847 0.6960
These differences exceed the displayed rounding precision. In contrast, the same calculation reproduces Long Consistency as 0.971 and ColorΔ as approximately 0.00149, making a uniformly different aggregation rule an insufficient explanation without further detail. The all-scenario results in Tables 2 and 4 repeat several Table 1 values. The authors should reconcile the tables against one set of per-scenario outputs and state whether different subsets, runs, or checkpoints were used.
The comparative evidence does not adequately separate the proposed framework from backbone strength and evaluation conditions.
MiniMax-H3 supplies the frozen audio generator, teacher, synthetic training trajectories, and initialization, yet its native generation performance is not included in Table 1. This leaves the incremental benefit relative to the source model unclear. Appendix A.4 also evaluates some methods for 30 seconds and others for 60 seconds, restricts single-subject audio-driven methods to a subset of categories, and retains native resolutions and frame rates. Further, SteadyTalk receives synthesized interviewer audio, whereas methods without audio input generate those segments from transcripts. These are understandable capability differences, but a single table does not provide a fully matched estimate of relative performance. The user study appropriately truncates paired videos for the 30-second baselines; analogous matched-duration and matched-category quantitative comparisons are missing. A native-backbone reference and matched subsets of the existing evaluations would make the claims substantially more convincing.
The principal long-term memory claim is not sufficiently distinguished from simpler speaker references.
The benchmark contains four answers per minute, each participant answers only twice in two-person scenarios, and speaker identity, appearance, voice, and scene descriptions are supplied repeatedly in the prompts (Appendix A.1). Appendix A.7 includes examples of a speaker returning after 20 seconds of silence, which is relevant evidence, but the quantitative evaluation does not stratify results by absence duration or number of intervening turns. Moreover, Table 3 does not compare the full reservoir and retrieval policy against a fixed first-utterance/first-crop reference for each participant. The visual-only and audio-only tagged variants both already achieve zero swaps. Thus, the results support the value of participant-specific conditioning, but do not establish the added necessity of gated storage and prompt-guided retrieval. A simple fixed-reference comparison and a breakdown of existing cases by speaker absence would directly address this gap.
Preserving normalized audio latent patterns does not establish preservation of decoded content and timing.
Section 3.4 argues that Eq. (4) changes channel moments while keeping normalized temporal structure, and therefore moves timbre toward the reference “without altering what is said or when.” The algebra establishes an affine transformation of latent channels; it does not establish that the MiniMax-H3 audio decoder disentangles speaker identity from phonetic content, prosody, or timing in those moments. The cited instance-normalization motivation is not itself a validation of this particular audio representation. Table 4 provides encouraging average WER and LipSync results, but does not measure paired changes in transcripts or timing before and after correcting the same generated latent. Also, ColorΔ and Long Consistency explicitly reward color-statistical stability, which is directly targeted by Eq. (3); their gains alone cannot distinguish removal of unwanted drift from suppression of intended visual changes. The authors should narrow the invariance claim and provide a focused paired check of audio preservation, along with evidence that intended changes such as removing a jacket remain intact.
Important details needed to reproduce the mechanism and interpret its cost are missing.
Section 3.3 does not operationally specify how participant crops are detected and matched to appearance descriptions, or identify the aesthetic scorer, blur check, and quality threshold in Eq. (2). Appendix A.3 omits the color blending coefficient α. The LoRA configuration, exact initial checkpoint, sampler settings, and synthetic trajectory filtering procedure are also not sufficiently specified. Section 3.2 describes ground-truth clean audio during training, whereas Appendix A.2 describes generated audio within student rollouts; the relationship between these training conditions needs clarification. Finally, bounded context tokens do not imply bounded total storage or constant retrieval cost, as Appendix A.8 itself explains. Measured chunk latency, peak memory, reservoir growth, and retrieval overhead are not reported. This matters because the proposed schedule adds a ten-step audio stage before a four-step video stage, even though no real-time performance claim should be inferred solely from few-step video sampling.