- Rating
- 1
- Confidence
- 4
- Informativeness
- 2
- Presentation
- 1
- Soundness
- 1
Read review
Paper summary
This paper studies spatially selective novel-view synthesis: ranking the regions within a rendered view by how much they can be trusted, so that the least reliable regions can be excluded at a chosen coverage level. The proposed method combines cross-view consistency evidence with internal Gaussian-state evidence, weighting each according to how much reliable cross-view evidence is actually available for a given region, and trains this combination with a pairwise ranking objective. The approach builds on classical selective-prediction and learning-to-rank theory, adapted to a setting where some regions may have no cross-view correspondence at all.
Critical strengths
S1. The paper's theoretical framework — the risk-coverage/AURC formulation from the selective-prediction literature and the pairwise ranking objective from the learning-to-rank literature — is imported from established fields rather than newly invented. That said, the paper's transfer of this framework to Gaussian splatting is a relevant and non-trivial contribution in its own right, particularly in how it handles the cross-view correspondence problem: regions can lack any valid cross-view correspondence at all (rather than merely noisy correspondence), which motivates a three-way supported/unsupported pair taxonomy. Building on this, Proposition 2 goes beyond a design justification and yields a quantitative, falsifiable prediction of how much evidence fusion helps as a function of source-support availability — a prediction that is tested against held-out data and holds up well (r = 0.80–0.96 across targets). This combination of transferred theory with genuine empirical validation is a real strength of the paper.
Critical weaknesses
W1. The method's scope is narrow for a venue like ICLR: the paper demonstrates only a single downstream application (regional retention under a declared loss) and explicitly defers more substantial applications (acting on the ranking, active view selection, cross-regime adaptation, other radiance-field representations) to future work. The scope stays considerably narrower than comparable work that demonstrates the same kind of reliability score across several applications, which limits the significance of the contribution relative to the breadth expected at this venue.
W2. The evaluation omits the metrics standard in the closely related NVS-uncertainty literature (AUSE, Pearson correlation) in favor of AURC alone, without justifying this choice relative to prior work, and does not discuss how its choice of a comparatively large region size (64×64 pixels) relates to the granularity used elsewhere in the literature, despite the paper's own ablation suggesting sensitivity to this choice. Together, these gaps make it difficult to assess how the reported gains would translate under the evaluation conventions most readers coming from the uncertainty-quantification side of this literature would expect.
W3. Beyond the choice of training objective (a pairwise ranking loss, rather than the native objective used by PRIMU), the proposed approach is, in substance, closely similar to a combination of PRIMU and PPU. Its standalone methodological novelty beyond this change of objective and the addition of external cross-view evidence appears limited. Moreover, the gain over the embedded signal cannot yet be attributed to genuinely new evidence rather than to objective adaptation: PPU is used frozen with its original objective, and the ablation that would isolate the effect of retraining the signal under the ranking objective is missing. The ablation provided (Table 2) only re-weights PPU's frozen output and does not address this question.
W4. The paper is simply not well written, and extremely dense throughout the introduction, method, and experiments. This is not a minor stylistic issue: the degree of compression repeatedly prevents the reader from following the core argument and mechanics of the method at all, independent of any assessment of the method's substance.
Questions for authors
Q1. How does the proposed method compare to the baselines under the metrics standard in the NVS-uncertainty literature (AUSE, Pearson correlation between predicted uncertainty and error), rather than only AURC? Without this, it is unclear whether the reported advantage holds under more established evaluation conventions.
Q2. The embedded PPU signal is used frozen, with its own original training objective; only the linear combination layer on top is trained with the pairwise ranking loss. How would an end-to-end retrained version of that signal's underlying model, using the same pairwise ranking objective, perform relative to the full method? This would clarify whether the remaining gap to the embedded baseline reflects genuinely new evidence (external/ observability cues) or an objective-adaptation benefit the baseline itself has not been given access to.
Q3. Why was 64×64 chosen as the default region size, and how do the results relate to the region/patch granularities used in closely related work? The paper's own robustness check already shows a shrinking relative advantage at larger region sizes — would this trend continue at finer, e.g. pixel-level, granularity?
Follow-up on Our Rebuttal
Dear reviewer,
We would like to kindly follow up on our rebuttal and the additional experimental results provided. We would appreciate your feedback on whether these results address your main concerns or if any questions remain.
Thank you again for your time and consideration.