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Paper summary
This paper studies post-hoc uncertainty estimation for Gaussian Splatting: predicting rendering error for a novel view without altering the trained scene representation. Prior work relies on multi-view coverage statistics obtained by rendering and back-projecting training views. This paper shows that simple appearance and depth statistics computed from a single novel-view rendering already carry much of that predictive signal, and that combining the two sources, together with a rank-based representation robust to view-dependent feature drift, improves on the strongest published post-hoc baseline and enables a single estimator that transfers across scenes without per-scene fitting.
Critical strengths
S1. The diagnosis that monotone, view-dependent feature drift can bias the evaluation of post-hoc uncertainty estimators, and the resulting design choice to represent features by their within-view rank rather than their raw value, is a small but genuine and non-obvious contribution, even though the underlying invariance property itself is a classical result.
S2. The experimental methodology is generally careful, in particular the controlled ablation (Table 6) that isolates the contribution of the regressor architecture from the contribution of the input features under identical inputs — exactly the kind of disentangling ablation that would strengthen comparisons of this sort.
S3. The paper is easy to follow. A strength, which carries a new meaning and becomes noteworthy in these days of papers densified by AI until the information content per sentence grows beyond readability.
Critical weaknesses
W1. The paper's contribution is too incremental for a venue like ICLR. Most of the paper's experimental structure already mirrors that of the embedded baseline (PRIMU) itself: the main uncertainty-estimation comparison (same three datasets, same AUSE/Pearson metrics), the feature-combination ablation, and the cross-scene generalization experiment all closely follow PRIMU's own published evaluation design, with PRIMU's released feature family simply extended by new inputs. The genuinely new empirical content is narrower than the full experimental section suggests: it rests on the new feature families themselves and on the rank-invariant evidential extension, while the surrounding experimental scaffolding is largely reused. Conversely, two of PRIMU's own experiments — a foreground/background breakdown and a downstream active-view- selection evaluation — are not carried over, which relates to the scope concern below.
W2. The scope is narrow for a venue like ICLR: the paper evaluates purely at the level of uncertainty-estimation metrics (Pearson, Spearman, AUSE) and never demonstrates that the improved numbers translate into a benefit for a downstream task (e.g., active view selection, anomaly detection, or scene change detection), even though such downstream validation is standard in closely related work on the same problem, see FisherRF, PRIMU and also Galappaththige et al. (ECCV 2026).
W3. Two aspects of the paper's framing overstate what is actually shown. First, the central contrast ("existing methods need multi-view coverage, we show one rendering suffices") conflates a one-time, inexpensive per-scene setup cost with an untested assumption about the baseline's requirements, since both approaches (the proposed one and PRIMU) need only a single rendering to evaluate a new pose once that one-time setup is done. The core reason is that both works build on a pixel-wise regressor. One image contains enough pixels to learn the task. Second, labeling the two components of the evidential decomposition as "aleatoric" and "epistemic" uncertainty is adopted to 3DGS without discussing whether this terminology is meaningful for a static, deterministic scene representation, where the usual justifications/assumptions for this distinction do not obviously apply. The use of "aleatoric" and "epistemic" should be reconsidered.
W4. The paper omits any related-work discussion or empirical comparison with Galappaththige et al. (ECCV 2026), which addresses the same problem (primitive-/ rendering-based uncertainty estimation for Gaussian Splatting) on the same benchmark (Mip-NeRF 360). On the one metric that is directly comparable across the two papers' publicly reported numbers (AUSE on the L1 target, Mip-NeRF 360), the two methods appear to perform essentially on par. A preprint of this work was available many months before the ICLR submission deadline. However, since the ECCV release is fairly new, this concern is mostly to be taken into account for future submissions.
Questions for authors
Q1. How does this work relate to Galappaththige et al. (ECCV 2026), which addresses the same problem on the same benchmark and was public in terms of a preprint well before this submission's deadline? A direct empirical comparison, in particular on AUSE under the L1 target where the two methods' publicly reported numbers appear comparable, is currently missing.
3 comments
W3 (framing). Both points are fair; we have revised the corresponding wording.
"One rendering suffices." You are right that per-pose inference needs one rendering for both methods, and that both use a pixel-wise regressor. That sharpens the real question: what must the target scene supply? Coverage maps need every training view rendered, compared with ground truth and back-projected (60–120 s per scene, Table 4); the eight single-rendering maps need only the rendering being evaluated (about 4 s). The revised Introduction now explicitly states the eight-map configuration and its target-scene input requirements. We also ran the direct test, a global estimator on the eight single-rendering maps only (leave-one-scene-out, 23 folds):
| Inputs | Global Pearson / AUSE | Requires target-scene training views + GT |
|---|---|---|
| Coverage only (13 maps) | 0.292 / 0.388 | Yes |
| Single-rendering maps (8) | 0.309 / 0.365 | No |
| All (21 maps) | 0.383 / 0.316 | Yes (coverage part) |
The coverage-free estimator reaches Pearson 0.309 compared with 0.292 for the coverage-only global estimator, and is within 0.002 of coverage-only per-scene fitting (0.311). Given a frozen target-scene GS model, it requires no target-scene training images, ground-truth images or target-scene regressor fitting. We do not claim these differences are significant, and the full combination performs best among these configurations. Global and per-scene fits use different pixel budgets, as stated in the paper.
Aleatoric/epistemic. We agree that the classical justification does not obviously apply to a deterministic static scene. We have renamed the terms "noise term E[σ²]" and "evidence term Var[μ]" and explicitly stated this naming convention, without claiming that the two components identify distinct physical sources of uncertainty.
W4 and Q1 (Galappaththige et al.). Thank you; we have added this work to Related Work and clarified its relationship to our approach. On Mip-NeRF 360 they report AUSE(L1) 0.328 and Pearson(L1) 0.369; our full representation gets 0.324 and 0.299. AUSE is on par and their Pearson is higher. As we understand it, the protocols differ (they fit on training-view residuals; we train on one hold-out view and evaluate on disjoint views), so we report the published numbers side by side without claiming a win. A like-for-like comparison would require running their code under our protocol, which we have not done.
Overall assessment. We have corrected the framing and terminology and added the missing related-work discussion. We have also conducted the additional evaluations reported above. Our claims are scoped to per-pixel RGB error prediction on static scenes. If a specific soundness concern remains, we would welcome the opportunity to address it directly. We would be grateful if you could reconsider the soundness and overall scores in light of these clarifications, additional results and the revised manuscript.
Dear Reviewer 6vWx,
We would like to briefly follow up on our updated responses. The revised PDF clarifies the target-scene input requirements, revises the evidential terminology, and adds the missing related-work discussion. Our responses also report the additional sparse-view, 2DGS, and pixel-error-ranking evaluations.
If these revisions and results alleviate your concerns, we would be grateful if you could consider raising your soundness and overall ratings. We would be happy to clarify any remaining issues.
Thank you for your time and consideration.
Dear Reviewer 6vWx,
Thank you for a careful review. Your strengths S1–S3 describe what we hoped the paper would offer, and your weaknesses are specific enough that we could act on each.
Revision status. We have now uploaded a revised PDF. We have clarified the eight-map configuration and transfer scope, corrected Table 1 LLFF PSNR to 23.70, updated the FisherRF reference to ECCV 2024, and reconciled Figure 3 and its caption with the 18-scene means reported in the text. The additional experimental results are reported below.
Our response in three points.
W1 (the contribution is too incremental). You are right that the datasets, metrics, ablation structure and regressor follow PRIMU. As you note in S2, this is what makes the attribution clean: everything else is held fixed. We do not claim a new regressor. The contribution is a set of findings that, to our knowledge, PRIMU does not report: a Sobel gradient map used directly, with no training, reaches Pearson 0.292 against 0.311 for the full 13-map coverage pipeline (23 scenes, Table 2); appearance and coverage contribute about equally (Shapley split 49.7% / 50.3%) and are weakly related (prediction-level r× = 0.29); a single global regressor trained on the other 22 scenes matches per-scene fitting on average (Δ = +0.002 Pearson, p = 0.93; this is not an equivalence test), whereas PRIMU trains per scene; and same-view pixel splits raise gradient-boosting Pearson from 0.378 to 0.637, so the evaluation split alone changes conclusions about feature utility. This reply adds the coverage-free estimator (W3), sparse views, and zero-shot transfer to 2DGS renders (Pearson 0.310 on four scenes against 0.333 on 3DGS). We agree with S1 that rank invariance is classical; what we contribute is the diagnosis that view-dependent drift can bias this evaluation, and the data on how large the split effect is.
W2 (no downstream task). We added a deployment-style evaluation on all 23 scenes. For each view we discard the top-f fraction of pixels ranked by each estimator's predicted uncertainty and compute PSNR on the retained pixels only (300k sampled pixels per view). The splatting is unchanged by every estimator (renders are bit-identical, Appendix B), so this measures ranking quality, not rendering quality. Mean retained-pixel PSNR (dB):
The full representation beats coverage-only at every f (+0.48 dB at 10%, +1.12 dB at 50%; paired p < 0.001) and on every dataset; Φapp∪Φgeo alone is on par with coverage-only. Ranking whole views by mean predicted uncertainty does not differ significantly between estimators. In a preliminary active-view-selection run (4 scenes, 3 seeds) our selectors did not improve final PSNR over random selection (19.4 and 19.6 dB against 20.85 dB), so we make no claim for view selection; AVS, anomaly detection and change detection will be listed as open.