acceptodds
Under review as a conference paper at ICLR 2027

Envision: Geometry-Aware Setwise Ranking for Facial Surgery Visualization

Abstract

Stochastic image editing can generate several plausible facial surgery visualizations, but selecting one without postoperative ground truth is difficult. Identity preservation and visual realism alone do not establish whether an edit captures the intended anatomical change. We introduce Envision, a geometry-aware setwise ranker for rhinoplasty, blepharoplasty, and rhytidectomy. A fixed FLUX.1-Fill backbone generates candidate pools using different random seeds and edit intensities. The ranker combines procedure-normalized morphometric changes, geometric information pooled across candidates, and learned appearance features. A procedure-conditioned direction predictor assesses how each candidate's change relates to the estimated case-level direction. Paired postoperative images provide teacher supervision during training, whereas inference uses only the preoperative portrait, procedure label, and generated candidates. Across a 125-case evaluation cohort combining validation and test, Envision improves mean teacher SurgicalScore over a handcrafted selector by 0.034 with 15 candidates and 0.038 with 25 candidates, recovering approximately 19% and 18% of the available oracle headroom, respectively. The gains chiefly reflect better agreement in the direction and magnitude of geometric change and are strongest for rhytidectomy, although cached-vision ablations do not isolate a benefit from the setwise or geometric branches alone. Performance levels off beyond 15 candidates, and the test-only improvements remain statistically inconclusive. These results suggest that geometry-aware selection can improve surgical visualizations without changing the generator. They do not establish that the selected images predict individual clinical outcomes.

Primary area:
generative models
Keywords:
Facial Surgery Visualization, Diffusion Models

Reviews

Among:
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1234this paper, Top 30%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_QruWOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper investigates the candidate selection problem in visualizing postoperative results of facial plastic surgery. A fixed FLUX.1-Fill generator generates multiple candidate images for each case by varying the random seed and editing intensity (25%/50%/80%), but it lacks postoperative ground truth at deployment, requiring the selection of one image for display. The authors propose Envision, a setwise ranker shared across three procedures: rhinoplasty, blepharoplasty, and facelift. It combines three types of information: procedure-specific 5D morphological measurement changes, case-level editing directions predicted after mean pooling of the candidate set, and appearance features encoded by a trainable ViT. During training, Huber regression is performed using the SurgicalScore with the postoperative ground truth as the teacher score; during inference, only the preoperative image, procedure labels, and candidate set are needed.

Critical strengths

The article honestly presents the raw results.

Critical weaknesses
  1. The experimental results fail to substantiate the conclusions. This paper's primary results (n=125) aggregate 76 validation set samples, which had previously been used for checkpoint selection based on the same "oracle-gain" criterion with only 49 held-out test set samples. Consequently, the reported significance is not an independent estimate. When considering only the held-out test set, the performance gains are marginal and statistically insignificant (+0.029 with p=0.17 for K=15; +0.023 with p=0.23 for K=25), with "blepharoplasty" even showing a performance decline. Results from the ablation studies also fail to support the claimed benefits of the "geometry-aware" and "setwise" designs. Table 4 shows that removing set context or geometric information actually yields a higher score than the full model (0.633 vs. 0.618), and the end-to-end ablation results in Table 10 (using a single random seed and excluding set information) differ from the full model by only 0.001. Furthermore, a simple baseline model using "frozen DINO features + ridge regression" achieves a score of 0.601.

  2. The results presented in the paper are inconsistent. There are contradictions among several key data. Section 4.4 reports a gain of +0.032 (p=0.023) over Envisage for a sample pool of K=5, whereas the data provided in Tables 2 and 6 indicate a gain of only +0.002 (p=0.43). The text claims that "rhytidectomy" recovered 67% of the performance headroom at K=25, but this figure actually corresponds to the value for K=15 in Table 3 (at K=25, the proportion is approximately 48%); regarding the p-value calculations for the primary results, Section 4.1 specifies B=5,000 iterations, whereas Appendix C describes a resampling scheme involving 100,000 iterations. Given such weak effect sizes, I cannot determine which results are correct.

Questions for authors

FLUX.1-Fill is not a state-of-the-art model. I suggest the authors try using a more advanced model as the backbone.

4 comments
AuthorsOpenReview ↗

Reply — W1, W2, Q1, ethics: independent evidence and corrected protocol

We addressed your central experimental concern with untouched, subject-disjoint tests, and corrected all three numerical inconsistencies you identified. The standard 278-case checkpoint, fixed before these evaluations, yields:

Cohort, KnRuleEnvisionΔPaired p
Locked multi-procedure, 151600.5880.624+0.0360.0022
Locked multi-procedure, 251600.5830.622+0.0390.0016
External ASPS/PCA, 152110.6050.637+0.0320.0028
External ASPS/PCA, 252110.6020.638+0.0360.0014

The original 49-case test result remains in the appendix. The matched three-seed end-to-end ablation on the locked 160 cases gives full 0.624, no set context 0.610 (−0.014, p=0.038), no geometry 0.604 (−0.020, p=0.015), and no direction gate 0.601 (−0.023, p=0.009). Thus every component improves the model under a common protocol. The original Table 4 inversion arose under a different cached-feature, mixed-development setup, which cannot isolate its cause. On the same locked set, a frozen DINOv2-CLS + Ridge visual baseline scores 0.598 versus full Envision's 0.624 (paired p=0.008); its selected geometry scores are also lower (direction A 0.542 vs 0.582; magnitude B 0.378 vs 0.453). The matched ablations provide component-level evidence; Ridge supplies a complementary visual-only baseline.

We corrected the three numerical/protocol errors in both prose and tables:

  1. The original pooled 125-case K=5 gain is +0.002 (p=0.43), not the +0.032 mistakenly assigned to it in prose. The new locked 160-case K=5 result is separately +0.005 (p=0.29).
  2. For original-development rhytidectomy, oracle-gap recovery is 67.3% at K=15: (0.674−0.598)/(0.711−0.598); and 47.9% at K=25: (0.656−0.598)/(0.719−0.598). The former gain is +0.076, not +0.087.
  3. Every current paired permutation result uses a two-sided sign-flip test with B=5,000; case-bootstrap 95% intervals use B=3,000. The stale 100,000-resample description and combined p-values were removed, and the appendix now maps each table to its cohort and n.

We chose FLUX.1-Fill-dev for its mask-conditioned inpainting workflow and held both the generator and candidate pools fixed across Envision and the deploy Rule, following Envisage. This cleanly attributes the measured gain to selection. The near-constant outside-mask score (E≈0.994) is achieved by hard pixel compositing. The revision separately evaluates single-output external generators; matched multi-candidate pools would test selector transfer beyond FLUX.

Finally, revised Figures 1, 4 and 11 embed opaque eye-region redaction in every patient panel, including inputs and targets. The Ethics Statement names the source datasets and reuse limits, and the code package excludes patient portraits. The paper also states the residual privacy risk and confines consent or institutional claims to documented evidence.

Thank you for your response and the additional experiments. While they resolve some of my concerns, the poor performance on blepharoplasty remains unaddressed because no per-procedure results were provided for the new test sets. I will maintain my current score for now.

AuthorsOpenReview ↗

Per-procedure results on both held-out test cohorts

Thanks for following up, and sorry we left out the per-procedure results in our earlier reply. For blepharoplasty, Envision scored higher than the Envisage rule in both held-out cohorts at K=15 and K=25. The paired gains were +0.012 and +0.016 at K=15, and +0.025 and +0.026 at K=25, on the locked and external HDA cohorts, respectively.

The tables below report all three procedures for the same frozen checkpoint trained on 278 cases. Envision and the Envisage rule were evaluated on identical candidate pools. Δ is the paired mean SurgicalScore difference (Envision minus Rule). Confidence intervals use 3,000 case bootstrap resamples, and p-values use 5,000 resamples from a two-sided paired sign-flip test.

Locked multi-procedure test set (N=160)

KProcedure (n)Envisage ruleEnvision [95% CI]OraclePaired Δ [95% CI]p
5Rhinoplasty (66)0.5910.593 [0.556, 0.630]0.768+0.002 [−0.024, +0.028]0.44
5Blepharoplasty (48)0.5820.579 [0.538, 0.620]0.674−0.003 [−0.031, +0.025]0.41
5Rhytidectomy (46)0.5930.611 [0.571, 0.651]0.685+0.018 [−0.008, +0.044]0.14
15Rhinoplasty (66)0.5890.618 [0.580, 0.656]0.834+0.029 [+0.002, +0.056]0.038
15Blepharoplasty (48)0.5810.593 [0.551, 0.635]0.728+0.012 [−0.008, +0.032]0.24
15Rhytidectomy (46)0.5940.665 [0.628, 0.702]0.736+0.071 [+0.037, +0.105]<0.001
25Rhinoplasty (66)0.5850.620 [0.581, 0.659]0.848+0.035 [+0.005, +0.065]0.024
25Blepharoplasty (48)0.5690.594 [0.551, 0.637]0.758+0.025 [−0.003, +0.053]0.084
25Rhytidectomy (46)0.5950.654 [0.616, 0.692]0.751+0.059 [+0.024, +0.094]0.0014

External HDA cross-procedure test set (N=57)

KProcedure (n)Envisage ruleEnvision [95% CI]OraclePaired Δ [95% CI]p
15Rhinoplasty (21)0.5840.618 [0.562, 0.674]0.812+0.034 [+0.001, +0.067]0.046
15Blepharoplasty (27)0.5750.591 [0.541, 0.641]0.715+0.016 [−0.011, +0.043]0.22
15Rhytidectomy (9)0.5920.673 [0.608, 0.738]0.723+0.081 [+0.022, +0.140]0.012
25Rhinoplasty (21)0.5810.618 [0.561, 0.675]0.826+0.037 [+0.002, +0.072]0.039
25Blepharoplasty (27)0.5700.596 [0.545, 0.647]0.741+0.026 [−0.008, +0.060]0.13
25Rhytidectomy (9)0.5890.652 [0.585, 0.719]0.733+0.063 [+0.009, +0.117]0.024

In an exploratory analysis pooling all 75 held-out blepharoplasty cases, the paired gain was +0.013 at K=15 (95% CI [−0.004, +0.030], p=0.14) and +0.025 at K=25 (95% CI [+0.002, +0.048], nominal p=0.036). The two cohorts show the same pattern of point estimates, with a small positive gain at K=15 and a larger estimate at K=25.

The updated manuscript summarizes the blepharoplasty results in Section 4.2 and presents the full per-procedure breakdown in Appendix Table 11 (page 18).

Thank you for providing the detailed per-procedure breakdown. While the gains on blepharoplasty alone remain statistically insignificant in each individual cohort, the new results confirm that the model no longer degrades performance on this procedure and achieves significant improvements on both rhinoplasty and rhytidectomy. Since most of my primary experimental concerns have been addressed, I will raise my score to 3.

Reviewer_kYBLOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

The paper proposes a geometry-aware selection framework to rank facial surgery visualizations from candidate images generated by a diffusion model. The system makes the selection without accessing the post-operative ground truth. The authors train a ranking model combining procedure-specific morphometry changes, pooled geometric information across candidates, a fined tuned ViT, and a procedure-conditioned direction predictor. The method is evaluated on rhinoplasty, blepharoplasty, and rhytidectomy with an improvement over hand-crafted selector.

Critical strengths
  • practical problem formulation to separate selector quality from generator performance.
Critical weaknesses
  • dataset is too small for obtaining meaningful model
  • validation set is combined to achieve significant gain. On pure test set, gain is non-significant.
  • No sufficient data to support the proposed framework
Questions for authors
  • I suspect the rather weak result is coming from very small learning dataset, do you agree?
2 comments
AuthorsOpenReview ↗

Reply — W1–W3, Q1, ethics: scaling, untouched tests, privacy

W1 + W3 + Q1 — Data scaling.

We strongly agree that data scale deserves a direct test. We trained identical three-seed ensembles on stratified subsets and evaluated every checkpoint on the same untouched 160-case, K=15 test set. The standard 278-case checkpoint is the primary comparison; 410 cases extends the curve with 132 additional non-overlapping training pairs.

Training cases50100200278 (primary)410
Mean SurgicalScore0.5930.6040.6160.6240.633
Δ vs Rule (0.588)+0.005+0.016+0.028+0.036+0.045
Paired p0.380.110.0140.00220.0004

Selected-candidate geometric direction A rises from 0.538 to 0.596 across the same training sizes. The gain reaches p=0.014 by 200 cases and continues to +0.045 (p=0.0004) at 410. Crucially, the primary 278-case model already reaches +0.036 (p=0.0022) on the untouched test set. The curve quantifies the benefit of more data while establishing the submitted model's generalization.

W2 — Significance on independent test data. The original 49-case test-only comparison was not significant (+0.029, p=0.17 at K=15); the 125-case pooled comparison included 76 validation cases. We replaced it as the headline with the unchanged primary 278-case checkpoint evaluated on untouched, subject-disjoint cohorts:

Untouched cohortnK=15 Δ (p)K=25 Δ (p)
Locked multi-procedure160+0.036 (0.0022)+0.039 (0.0016)
External ASPS/PCA rhinoplasty211+0.032 (0.0028)+0.036 (0.0014)
HDA cross-procedure57+0.033 (0.028)—

All four locked/external comparisons at K=15/25 reach p<0.005 with no validation cases in the test cohorts. The 57-case HDA result adds cross-procedure evidence. Patient-level deduplication was checked across these cohorts and training/validation data; at K=15 they total 428 cases and 6,420 candidate images. The original 49-case test-only result remains in the appendix. Each p-value is a two-sided 5,000-resample paired sign-flip test for its own cohort and K; confidence intervals use 3,000 case bootstraps.

Ethics flag — Image privacy and redistribution. The revision changes the actual figures: every facial panel in Figures 1, 4 and 11, including inputs and postoperative targets, has opaque eye-region pixels; in eyelid examples the eye opening is covered while skin folds remain assessable. The Ethics Statement identifies the sources and HDA's academic/noncommercial, no-redistribution terms; the code package excludes original and generated patient portraits and postoperative targets. The appendix discloses the 403-case internal cohort's automatically estimated sex, age and skin-tone composition, alongside exploratory subgroup results and sparse-cell uncertainty. Redaction lowers exposure but leaves other identifiable facial features. Patient-level publication permissions and any institutional determination require separate source documentation.

Together, the scaling curve, three independent test cohorts, and pixel-level figure redaction make the revised evidence substantially stronger and more transparent.

AuthorsOpenReview ↗

A quick follow-up on the held-out results

Thanks again for your review! Your question about training set size prompted us to test it directly. On the same 160-case held-out set at K=15, the gain over the Envisage rule grew from +0.036 with 278 training cases (p=0.0022) to +0.045 with 410 (p=0.0004). The original 278-case model also gained +0.032 on the separate 211-case ASPS/PCA test set (p=0.0028).

One update from the other review discussions: we’ve now added the full per-procedure breakdown for both held-out multi-procedure cohorts. On the 160-case set at K=15, the gains were +0.029 for rhinoplasty and +0.071 for rhytidectomy. The blepharoplasty estimates were smaller and positive in both cohorts (+0.012 and +0.016), with both confidence intervals crossing zero. The full results are in Appendix Table 11 and are summarized in Revision Summary: Envision at the top of the discussion page.

If you get a chance to take another look before the discussion closes, we’d love to hear whether the scaling and held-out results address your main concerns. We’re happy to clarify anything that’s still open.

Reviewer_bngLOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
1
Soundness
1
Read review
Paper summary

The paper addresses a selection problem in surgical visualization. A diffusion editor can generate many plausible "after surgery" images for one patient, but at deployment there is no postoperative photo to tell which candidate is best. The authors propose Envision, a learned ranker that picks one candidate from a pool produced by a fixed FLUX.1-Fill inpainting model. The pool is varied by random seed and by three edit intensities. The method covers rhinoplasty, blepharoplasty and rhytidectomy.

A direction predictor estimates the expected direction of change for the case and slightly up-weights candidates that agree with it. The ranker is trained by regressing a "teacher" score, SurgicalScore from prior work (Envisage). The teacher uses the real postoperative photo and combines direction agreement, magnitude agreement, photometric fidelity, realism and outside-mask preservation, behind an identity gate.

On 125 cases (76 validation and 49 test), Envision improves the mean teacher score over the handcrafted Envisage selection rule by about 0.034 with 15 candidates and 0.038 with 25. That recovers about 18 to 19 percent of the gap to the oracle. The gains come mostly from direction and magnitude agreement and are largest for rhytidectomy. The authors openly report that test-only differences are not statistically significant, that performance plateaus beyond 15 candidates, and that several ablations do not support the geometric and setwise components.

Critical strengths
  1. Well-posed and practically relevant problem. Treating surgical visualization as selection from a stochastic pool, with no ground truth at deployment, is a clear framing. The oracle-headroom and selection-regret view usefully separates generator quality from selector quality.
  2. All selectors are compared on identical, nested candidate pools. This removes generator variability and makes the gains attributable to selection.
  3. The authors report negative and inconclusive findings, a power analysis, split-specific results, failure cases and the limits of their claims. They explicitly avoid clinical-outcome claims. This transparency is commendable.
  4. Comparisons use paired permutation tests, bootstrap intervals, and Holm correction for the single-signal ablations.
  5. Decomposing the teacher score shows where the gain comes from (direction and magnitude agreement, with appearance terms tied). Pool-composition, intensity-selection histograms and cross-procedure transfer experiments add useful insight.
  6. Efficiency and reproducibility. Ranking cost is negligible next to generation, and code is released.
Critical weaknesses
  1. Training target and evaluation metric are the same. The ranker is trained to regress the teacher score and then evaluated with that same score. The improvement therefore shows better fitting of SurgicalScore, not better visualizations. There is no human or clinician evaluation, and the teacher itself has not been validated against expert judgment.
  2. The teacher may share a bias with the ranker. Direction and magnitude agreement in the teacher, and the morphometry inputs of the ranker, both come from MediaPipe landmarks. The measured gain lies almost entirely in these landmark-based terms, so the ranker may be learning landmark-detector behavior rather than real anatomical correctness.
  3. The teacher is not established. It comes from a single recent preprint, with fixed weights and an arbitrary identity threshold of 0.65. Its outside-mask preservation term is nearly constant (about 0.994) because of hard compositing, so it adds no discriminative signal.
  4. The headline numbers include the validation set. Pooled results mix 76 validation cases, used for checkpoint selection and hybrid tuning, with 49 test cases. The pooled estimates are therefore optimistically biased. The only clean evaluation, the 49-case test split, is not significant (p-values of 0.17 and 0.23), with statistical power of about 0.17.
  5. Effect sizes are small. The gain is about 0.03 on a 0 to 1 scale, while the gap to the oracle stays around 0.15. Within-case rank correlation with the teacher is only about 0.25, and the selector matches the oracle candidate in under a fifth of cases.
  6. Ablations do not support the core claims.
  7. The "setwise" aspect is limited. Training uses a pointwise Huber loss. Set information enters only through a mean-pooled context vector and a small multiplicative direction gate, whose modulation is capped at ten percent. Listwise and pairwise losses were tried but not used. 8. The direction predictor is computed from the candidate average, which effectively favors consensus, despite the stated intent not to assume the most common change is correct.
  8. The selector is unstable. The three independently trained rankers agree on the chosen candidate in only 18.4 percent of cases, and their score correlations range from 0.28 to 0.61. This suggests the ranking signal is weak and largely driven by optimization noise.
  9. The dataset is poorly documented and raises ethics concerns.
  10. Clinical risk is not discussed in depth. Showing patients an image chosen for high agreement with a retrospective metric could shape expectations. The paper acknowledges that its images are not outcome predictions, but does not discuss how misleading selections might be detected or communicated.
Questions for authors
  1. Has SurgicalScore been validated against judgments by surgeons or patients? Could you run the prepared blind two-alternative human study before the camera-ready version, at least on a subset?
  2. The teacher's geometric terms and the ranker's morphometry inputs both use MediaPipe landmarks. How do you rule out that the ranker exploits detector-specific behavior? Could you evaluate geometric agreement with an independent landmark detector or with manual annotations?
  3. Can you report all main results on the untouched 49-case test split only, and treat the pooled numbers as secondary? Would you consider a larger held-out test set or cross-validation over the full 403 cases to address the power problem?
  4. How does Envision compare with random selection, with always choosing the strongest intensity, and with choosing the largest geometric change? How much of the rhytidectomy gain remains after controlling for edit intensity?
  5. Given that removing geometry or set context does not hurt, and sometimes helps, which evidence supports calling the method "geometry-aware" and "setwise"? Can you repeat the end-to-end ablations with three seeds and paired tests against the full model?
  6. Why does a pointwise regression loss outperform the pairwise and listwise objectives you tried? Can you report those results?
  7. The three trained rankers agree on the chosen candidate in only 18 percent of cases. How should a user interpret a selection that changes with the training seed?
  8. Could you compare against general learned preference or quality models, or a vision-language judge, used as selectors on the same pools?
  9. For the external editors, can you generate the same number of candidates and apply both the rule and Envision? This would separate generator quality from selector quality.
  10. Which public repositories make up the dataset? What are their licenses and consent terms? Was ethics approval obtained, and do the patients shown in the figures permit publication?
  11. What is the demographic composition of the cohort, and does selection quality vary across age, sex or skin tone?
  12. How are pre- and postoperative photos aligned in pose and lighting before computing the teacher score? How sensitive is the teacher to such differences?
  13. How was the identity threshold of 0.65 chosen, and how many candidates fail it per case?
  14. Can you clarify which p-value protocol is used for each reported result? Can you justify combining seeds evaluated on the same cases with Stouffer's method?
  15. Is there a way to detect at deployment the failure cases where the ranker picks a candidate with the wrong direction, for example through disagreement between seeds or with the rule?
7 comments
AuthorsOpenReview ↗

Reply 1 — W1, W2, Q1, Q2: anatomical validity and detector independence

We tested the metric-validity and detector-coupling concerns with two independent landmark systems. The locked, previously untouched 160-case test set was audited with FAN facial landmarks; the cervicomental angle additionally uses an independent neck-contour detector. Measurements are compared with each case's postoperative image, and the Rule and Envision are evaluated on the same fixed candidate pool at K=15.

Postoperative-referenced MAE (↓)nRuleEnvisionPaired p
Goode tip-projection ratio660.0570.0480.019
Nasolabial angle (degrees)665.784.860.022
Palpebral fissure ratio480.0340.0320.31
Lateral canthal tilt (degrees)482.382.240.35
Cervicomental angle (degrees)467.585.34<0.001
Jawline angle (degrees)464.793.560.002

The independently recomputed geometric direction and magnitude components increase by +0.052 (p=0.0018) and +0.088 (p<0.001), respectively. A second 3DDFA-V2 audit on the original 125-case development cohort gives an independent-detector SurgicalScore gain of +0.031 at K=15 (p=0.026) and +0.035 at K=25 (p=0.039). The improvement therefore survives detector replacement and, on the locked cohort, coincides with lower postoperative-referenced anatomical error. The two eyelid measures show directional but statistically inconclusive changes.

This is direct evidence for anatomical fidelity beyond the original teacher and MediaPipe detector. Our claim is better candidate selection for preoperative goal visualization. A blinded clinician/patient study addresses a separate question—clinical preference and outcome validity—and remains a deployment-stage evaluation, as in the Envisage benchmark.

AuthorsOpenReview ↗

Reply 2 — W4, W5, W6, Q3–Q5, Q14: independent tests, magnitude, ablations

The revision replaces the pooled 76-validation-plus-49-test headline with three subject-disjoint, untouched cohorts. The standard 278-case training checkpoint is frozen for these comparisons; no validation cases enter the test sets.

Test cohortnKRuleEnvisionΔPaired p
Locked multi-procedure160150.5880.624+0.0360.0022
Locked multi-procedure160250.5830.622+0.0390.0016
External ASPS/PCA rhinoplasty211150.6050.637+0.0320.0028
External ASPS/PCA rhinoplasty211250.6020.638+0.0360.0014
Subject-disjoint HDA cross-procedure57150.5810.614+0.0330.028

The original 49-case test-only estimates (+0.029, p=0.17 at K=15; +0.023, p=0.23 at K=25) remain in the appendix for full traceability. Each new p-value is a two-sided paired sign-flip test with 5,000 resamples on that cohort and K; intervals use 3,000 case bootstraps. The revision removes Stouffer-combined p-values and provides a per-table sample-size/protocol manifest. Patient-level deduplication was checked across the 160, 211, and 57 cases. At K=15, these cohorts total 428 cases and 6,420 candidate images.

The +0.036 locked-set gain closes 19.4% of the Rule-to-oracle gap. On the same 160 cases, Envision (0.624) exceeds random selection (0.585; p=0.0015), always selecting i80 (0.602; p=0.024), and maximum displacement (0.566; p<0.001). In the 46-case rhytidectomy subset, fixing all candidates to i50 still yields +0.059 over the corresponding rule (p=0.0024). The gain persists at controlled intensity, while unrestricted intensity selection degrades identity preservation.

The matched three-seed, end-to-end ablation on those 160 cases is: full 0.624; without set context 0.610 (−0.014, p=0.038); without geometry 0.604 (−0.020, p=0.015); without direction gate 0.601 (−0.023, p=0.009). Every proposed component contributes under the common end-to-end protocol. The earlier inversion came from a cached-feature experiment on a mixed development cohort; its different setup prevents a causal reading of the discrepancy.

AuthorsOpenReview ↗

Reply 3 — W3, W7–W9, Q6, Q7, Q12, Q13: teacher, setwise learning, stability

We expanded the teacher and scoring protocol. SurgicalScore is an input-anchored retrospective training target with five components and a 0.65 ArcFace identity gate inherited from Envisage; its component weights and gate were fixed before our selector comparison. At inference, Envision does not see a postoperative target or the teacher score. The original 125-case K=15 decomposition illustrates where gains occur:

ComponentRuleEnvision
A: geometric direction0.5270.577
B: geometric magnitude0.3510.447
C: local appearance0.6910.689
D: identity0.8780.873
E: outside-mask preservation0.9940.994

E is effectively tied because the surgical mask is hard-composited; the measured gain is concentrated in geometric A/B. The 0.65 ArcFace gate follows the benchmark protocol and serves as an identity screen. We now describe it as an operational threshold, leaving clinical calibration and rejection-rate sensitivity as open evaluations. Local masked LPIPS restricts appearance scoring to the edit region; the postoperative-referenced FAN and 3DDFA-V2 audits in Reply 1 directly test the geometry under different detectors. We have kept alignment claims to preprocessing that is documented in the paper.

Set pooling gives each candidate a learned case context and retains its own geometry. It is neither a vote for the modal edit nor a penalty on high-intensity edits. For example, on the original K=25 development pools the deploy rule selected no i80 candidates, while Envision selected 22. The original 125-case loss comparison is likewise more specific than a generic preference for pointwise losses:

LossMean scoreTop-1 oracle hit
Pointwise Huber0.62117.6%
Pairwise RankNet0.60414.4%
Pairwise margin0.60113.6%
Listwise0.59712.8%

Pointwise Huber gives the highest mean score and oracle Top-1 hit rate in this matched comparison. Near-tied candidates offer a plausible explanation for the ranking-loss gap; the table establishes the empirical difference. We also report seed statistics with distinct definitions: 18.4% strict three-way single-seed Top-1 agreement, 33.6% pairwise Top-1 agreement, and 54.2% pairwise Top-3 candidate overlap. The 41.6% figure is the ensemble's oracle Top-3 hit rate. The fixed three-seed ensemble scores 0.621 versus 0.587 for the Rule (p=0.023) on the development cohort and produces a deterministic selection for a fixed pool. Retraining agreement remains a separate stability target; locked-test significance is reported in Reply 2.

Comments on the paper

3 comments
AuthorsOpenReview ↗

Revision Summary: Envision

Envision addresses a practical decision in preoperative visualization: which image to show when a generator produces several plausible candidates and no postoperative reference is available at inference. We hold the generator and candidate pools fixed to isolate the effect of selection. Across 428 held-out cases, Envision improves on the Envisage rule. Matched ablations quantify the contributions of geometry, set context, and direction gating. Independent anatomical measurements also show lower error on several measures of agreement with postoperative images.

1. Independent evaluation across 428 cases. The primary model trained on 278 cases was evaluated on three untouched, patient-disjoint cohorts, with validation cases excluded from every test.

Untouched cohortnKRuleEnvisionΔPaired p
Locked multi-procedure160150.5880.624+0.0360.0022
Locked multi-procedure160250.5830.622+0.0390.0016
External ASPS/PCA rhinoplasty211150.6050.637+0.0320.0028
External ASPS/PCA rhinoplasty211250.6020.638+0.0360.0014
HDA cross-procedure57150.5810.614+0.0330.028

At K=15, these cohorts comprise 428 cases and 6,420 candidate images. The +0.036 locked-set gain recovers 19.4% of the Rule-to-oracle gap. Each cohort and pool size has its own two-sided paired sign-flip test (B=5,000) and case-bootstrap interval (B=3,000). The appendix also retains the original 49-case test-only estimates: +0.029 (p=0.17) at K=15 and +0.023 (p=0.23) at K=25.

Per-procedure results. Section 4.2 summarizes the blepharoplasty findings, and Appendix Table 11 (p. 18) reports the full breakdown for both held-out multi-procedure cohorts. At K=15, the estimated gains were +0.012 on the locked cohort (n=48) and +0.016 on external HDA (n=27), with both confidence intervals crossing zero. At K=25, the estimates rose to +0.025 and +0.026, respectively. An exploratory analysis pooling all 75 held-out blepharoplasty cases estimated a gain of +0.025 at K=25 (95% CI [+0.002, +0.048], nominal p=0.036).

2. Matched experiments identify the source of the gain. On the locked 160 cases, three-seed end-to-end variants score 0.624 full, 0.610 with set context removed (−0.014; p=0.038), 0.604 with geometry removed (−0.020; p=0.015), and 0.601 with the direction gate removed (−0.023; p=0.009). Frozen DINOv2-CLS + Ridge scores 0.598 (paired p=0.008 versus full). Envision also exceeds random (0.585), always-i80 (0.602), and maximum-displacement (0.566) selection; the rhytidectomy gain persists in a fixed-intensity subset (+0.059, p=0.0024). Training on 50, 100, 200, 278, and 410 cases yields locked-test gains of +0.005, +0.016, +0.028, +0.036, and +0.045, respectively. The 278-case model is the primary result; the post hoc 410-case extension maps the scaling trend.

3. Independent detectors verify anatomical agreement. On the locked 160 cases, FAN facial landmarks plus an independent neck-contour detector reduce postoperative-referenced Goode-ratio MAE from 0.057 to 0.048 (p=0.019), nasolabial-angle MAE from 5.78° to 4.86° (p=0.022), cervicomental-angle MAE from 7.58° to 5.34° (p<0.001), and jawline-angle MAE from 4.79° to 3.56° (p=0.002). Independently recomputed geometric direction and magnitude increase by +0.052 (p=0.0018) and +0.088 (p<0.001). A separate 3DDFA-V2 audit retains the selection advantage. The two eyelid measurements show directional, statistically inconclusive changes. Together, these detector-independent analyses connect selection gains to postoperative-referenced facial geometry. Clinician and patient preference is the next complementary evaluation.

4. Reporting, privacy, and clinical-use protocol are explicit. The revised manuscript gives the original K=5 gain as +0.002 (p=0.43) and rhytidectomy oracle-gap recovery as 67.3% at K=15 and 47.9% at K=25. A per-table protocol lists cohort sizes, paired tests, and bootstrap intervals. The Ethics Statement names the image sources and reuse limits; Figures 1, 4, and 11 have opaque eye-region masking embedded in every facial panel, and the code release excludes patient portraits and postoperative targets. Exploratory demographic and subgroup tables expose cohort composition and sparse-cell uncertainty. The paper distinguishes source access from patient-level publication permissions and institutional determinations. Its clinical-use protocol presents Top-3 visualizations with surgeon explanation; a retrospective disagreement flag captures six of eight severe relative losses while retaining 106/125 cases.

All changes described above are highlighted in blue in the revised manuscript.

AuthorsOpenReview ↗

Locations of Changes in the Revised Envision Manuscript

The Point column refers to the numbered items in Revision Summary: Envision. Key changes are highlighted in blue in the revised manuscript.

LocationChangePoint
AbstractUpdated the headline results to report the locked 160-case test and the independent ASPS/PCA and HDA evaluations. Summarized the matched three-seed ablations.1, 2
§4.1, Table 8Defined the three test cohorts and documented patient-level deduplication and validation exclusion. Specified the paired sign-flip and case-bootstrap protocols.1, 4
§4.2, Table 1Replaced the pooled headline comparison with results on three untouched cohorts totaling 428 cases. On the locked cohort at K=15, Envision gains +0.036 over the rule (p=0.0022), recovering 19.4% of the oracle gap.1
§4.2, Appendix Table 11 (p. 18)Added the full breakdown by procedure for the locked and external HDA cohorts. Blepharoplasty has positive point estimates in both cohorts at K=15 and K=25. The individual confidence intervals cross zero. The exploratory pooled estimate across 75 cases is +0.025 at K=25 (nominal p=0.036).1
§4.3, Table 2Added matched three-seed end-to-end ablations. Removing set context, geometry, or direction gating lowers the locked-test score by 0.014, 0.020, or 0.023, respectively.2
§4.3, Appendix Table 13Added random, strongest-intensity, and maximum-displacement baselines. The rhytidectomy gain remains positive when edit intensity is fixed (+0.059, p=0.0024).2
§4.3, Appendix Table 20 and Fig. 12Added a training-size sweep from 50 to 410 cases on the same locked test set. The gain over the rule rises from +0.005 to +0.045 across the sweep.2
§4.3, Appendix Tables 17–19Added anatomical evaluations using FAN, an independent neck-contour detector, and 3DDFA-V2. The locked-cohort audit shows lower error on several nasal and neck measurements. The two eyelid measurements remain statistically inconclusive.3
§4.5, Appendix Table 16Described how surgeon-guided review could use morphometric disagreement. In the retrospective analysis, flagging 19 of 125 cases captures six of the eight severe relative losses.4
Appendix Tables 9–10Retained the original 49-case test results separately from the validation results. Corrected the original pooled K=5 gain and clarified the rhytidectomy oracle-gap recovery at K=15 and K=25.1, 4
Appendix Table 22Added the frozen DINOv2-CLS + Ridge comparison on the locked test set. Ridge scores 0.598 versus 0.624 for Envision (paired p=0.008).2
Ethics Statement, Figs. 1, 4, and 11, Appendix Table 7Documented image sources and reuse limits, embedded opaque eye-region masking in the figures, and reported exploratory cohort demographics and subgroup results.4
Reproducibility StatementClarified which artifacts the code release provides and how to obtain evaluation images under their source terms.4
AuthorsOpenReview ↗

Brief Summary of the Review Discussion

Dear Area Chair,

Thank you for your time and for overseeing the discussion. We would like to briefly summarize how the evaluation of Envision changed during rebuttal.

The ratings moved from 2/2/2 to 3/2/3. We added evaluations on three held-out cohorts totaling 428 cases, a training-size study, and a per-procedure breakdown. Reviewer bngL thanked us for addressing their concerns and raised their rating. Reviewer QruW raised their rating after reviewing the per-procedure results and noted that most of their main experimental concerns had been addressed. As of this comment, we have not received a follow-up from Reviewer kYBL.

Envision addresses a practical question in preoperative visualization: which image to show when several candidates are available and there is no postoperative reference at inference. Holding the generator and candidate pools fixed lets us measure what the selector itself contributes. The new evaluations show gains over the Envisage rule across all three held-out cohorts. The per-procedure results show where those gains are strongest and where the estimates remain uncertain. The supporting results and manuscript locations are listed in Revision Summary: Envision.

Thank you for considering the revised evidence.

Best regards,
Authors of Submission 23072

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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