- Rating
- 2(+1)
- Confidence
- 2
- Informativeness
- 2
- Presentation
- 2
- Soundness
- 1
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Paper summary
As far as I understand, this paper addresses an training optimization challenge in 4DGS domain, thus how the individual Gaussian primitives themselves are updated during the iterative optimization of dynamic Gaussians. To demonstrate these, authors propose a controlled counterfactual measurement framework to quantify the concentration–predictability gap inherent in dynamic Gaussian optimization. Empirically, they analyze some significant factors within splatting, e.g., the scene, optimization stage, and budget, to evaluate how the value of different Gaussians shifts across the training process. This analysis just support their central observation that the one-step mechanism does not necessarily bring the benefits associated with a robust, fixed mask, thereby revealing the distinction between optimizer-update sparsity and sparse backward execution.
Critical strengths
Based on my knowledge and this work, its strengths are listed below.
The proposed counterfactual measurement framework, constructs a paired counterfactual oracle, transforming the update process for internal Gaussian primitives into a strategy followed by a measurable quantity. By freezing checkpoints and probe views, this study evaluates and updates specific Gaussian points individually by assessing the distinct value each contributes through sequential observation, which iterates through Gaussian points, representing a logically sound method for Gaussian training optimization.
Furthermore, I believe the authors establish a crucial distinction between optimizer-update sparsity and sparse backward execution in 4DGS domain if possible, which is a valuable contribution to the optimization of Gaussian training. Since Gaussian primitives are coupled via shared deformation parameters, suppressing an explicit Gaussian optimizer step does not eliminate their contribution to the shared backward gradient. In relevant experiments of the prototype P, hybrid H and true-sparse T have further validate the rationale behind the authors' analysis.
Critical weaknesses
In my view, the main thread and logic of this work are generally sound. However, the primary shortcoming lies in the experimental setup, which limits the ability to fully validate the final conclusions. To their credit, the authors also acknowledge this point and I appreciate that they explicitly discuss this limitation. Regarding the experiments, the authors primarily validate their findings on only two main backbones, 4D-GS and Deformable-3D-GS. While the consistent observations across these two backbones provide useful supporting evidence, the limited architectural coverage makes it difficult to determine whether the reported optimization behaviors generalize to a broader range of Gaussian Splatting frameworks. Furthermore, the reliance on D-NeRF for testing, specifically the use of synthetic data and a limited dataset, hinders the assessment of the generalizability of the reported findings. Additionally, the work appears to lack validation across a broader range of scenes, leaving this for future research.
Questions for authors
My remaining concerns are as follows:
(1) The experimental validation appears somewhat limited. Could the authors further evaluate the proposed findings on more backbones, real-world dynamic datasets, or diverse scenes to better demonstrate their generalizability? l hope authors can provide some quantitative evidence during the discussion phase.
(2) The authors analyze Gaussian selective updating across several dimensions: scene, stage, budget, and path, Could the author further elaborate on the motivation behind their choice? please disregard this question if this is a standard practice in the field. Furthermore, are these dimensions decisive factors for optimization during Gaussian training, or were they specifically chosen based on the central focus of this study?
(3) Could the authors further unify and polish the presentation of the figures and equations to improve the overall readability and consistency of the paper? This is important for the reader to understand the paper.
3 comments
Dear authors,
Thanks for your rebuttal.
I've read the updated paper, this phase further resolves the most of my concerns.
However, balancing with other comments, I decide to raise score to 2.
Thank You for Your Reconsideration
Thank you for taking the time to carefully read our revised manuscript and reconsider your assessment. We sincerely appreciate your constructive feedback and are glad that the additional evidence has addressed most of your concerns.
Response to Reviewer htLA
Q1. "The validation is limited: more backbones, real-world dynamic datasets, more scenes?"
Concern. Two synthetic backbones are not enough to support the claims.
New evidence. Three expansions, in the order the question asks for them.
Scenes. The grid covers eight D-NeRF scenes. Three of them (bouncingballs, hellwarrior, standup) are held out from every fit, threshold and diagnostic and serve as a quantitative transfer test; the development cells carry two seeds.
Real captures. The protocol is repeated unchanged on nine real dynamic sequences at two seeds each — two HyperNeRF interp scenes (chickchicken, aleks-teapot) and seven NeRF-DS scenes (as, basin, bell, cup, plate, press, sieve). Across the 90 non-Full configurations, 74% stay within 0.1 dB of Full and the worst loses 1.84 dB. Figure 4 provides same-view qualitative comparisons from HyperNeRF and NeRF-DS under matched scheduling settings.
Targeted reproduction, not a further backbone. The backbone question is answered by re-running the controls on the same second backbone the submission already reports, not by adding a third: on Deformable-3D-GS the regime structure, the matched-budget path effect across three seeds and the semantic bridge all reproduce, and restoring dense shared-deformation gradients recovers the prototype trajectory while active-only backward does not. The new work is the real-scene evaluation above and the reproduction of the existing controls on that backbone.
Interpretation. The real captures do not support a per-sequence deployment rule: seed and reference variation are comparable to the skip effect, the pilot does not beat a zero-deficit baseline in pooled error (0.34 against 0.32 dB), and it recovers six of nineteen costly configurations. We report the tolerance distribution and the measured pilot quality rather than claiming a general-purpose detector, and the main text carries that boundary, not only the appendix.
Q2. "What is the motivation behind scene, stage, budget, path — decisive or post hoc?"
They are the arguments of the cost model, each entering with a measured coefficient. Scene enters through the slope κ_scene, which is associated with the scene's Full-run variability on the development scenes. Stage enters through the schedule start a and budget through the local active ratio β, both through the skipped mass s = (1−a)(1−β). Path enters because the realized budget is not the designed one: policy-dependent densification changes how many rows are eligible per step, so two schedules with equal designed budget can differ in measured expenditure. Section 5 states this mapping explicitly, which is what makes the four choices testable rather than rhetorical.
Q3. "Could the authors unify and polish the figures and equations?"
All analytic figures are regenerated as vector PDFs in one style, so labels stay crisp at any zoom and no raster upsampling enters the body; the schematics are re-exported at ≥300 dpi. Figure 3 was redrawn at its printed size after we measured that the earlier version was set too small to read. Symbol and equation numbering are consistent between the body and the appendix.
With the additional real-world experiments and cross-backbone controls, could you clarify whether your original soundness concerns remain? If so, which specific technical issue is still decisive?