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Under review as a conference paper at ICLR 2027

Does Better Reprojection Mean Better 3D Reconstruction? Candidate- and Evidence-Stratified Evaluation for FLFM

Abstract

In Fourier light-field microscopy (FLFM), does better reproduction of the camera image imply more faithful recovery of three-dimensional fluorescence structure? Reprojection fit supports selection when paired volume references are unavailable. We introduce SCOPE-FLFM to examine what this criterion reveals. Comparable-Candidate Stratification (CCS) organizes comparisons across model families, related architectures, and states from the same training run. Contract-Separated Evidence Validation (CEV) distinguishes supplied-view fit, excluded-view prediction, and normalized agreement with known synthetic objects. Using a synthetic FLFM corpus and reference volumes spanning beads, clusters, filaments, and mixtures, we find that pooled rank agreement weakens among close candidates and prospective choices depend on the scored target. Under the tested additive background, max-normalized reprojection SSIM increases while object Pearson decreases across all core learned states. A matched HYPER-derived Calibra-LF case study improves clean-corpus held-out SSIM and object Pearson on average while worsening other endpoints. SCOPE-FLFM links each score to the imaging property that model selection aims to improve.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
Fourier light-field microscopy, computational imaging, inverse problems, model selection, self-supervised reconstruction, evaluation benchmarks

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
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Paper summary

The paper is asking a question about fourier light field microscopy (FLFM): whether a model that gives a better reconstruction of the 2D camera image is also better for reconstructing the underlying 3D structure. This is an important problem because in many settings researchers don't actually have access to the 3D structure and 2D is all there is for benchmarking and evaluation.

The authors propose an evaluation framework, SCOPE-FLFM, with two parts. The first organize candidate models into comparable groups: by architecture family, by training run, and by checkpoint. The second separates three kinds of evidence: fit to the camera views given to the model, prediction of camera views withheld from it, and agreement with known synthetic 3D objects.

Using a synthetic dataset and a small pool of learned models, the paper reports four findings:

  • Agreement between scores is high when all models are pooled but weak among closely related models.
  • The model selected depends on which score is used.
  • Adding a uniform background makes a normalized image-similarity score go up while agreement with the true 3D object goes down.
  • A small architectural modification (Calibra-LF) improves some metrics and worsens others.

I should say at the outset that I am not an expert in light-field microscopy. I read this paper as a member of the general ICLR audience. My comments are therefore about whether the paper communicates its contribution to that audience and whether it fits the venue. I do not question the correctness of the optics or the experiments.

Critical strengths
  1. The title asks a clear question. "Does better reprojection mean better 3D reconstruction?" is easy to grasp, and the underlying concern, choosing models with a proxy score when the real target is not observable, is relevant well beyond microscopy (off the top of my head: self-supervised MRI and CT reconstruction, and most representation learning methods based on auto-encoders)

  2. The experimental protocol appears careful. Selection rules are fixed before final evaluation, duplicate checkpoints are not counted twice, and the authors are explicit about the limits of their claims (App. A.24).

  3. Results are reported openly. Unfavourable results, including for the authors' own variant, are reported rather than hidden under the carpet.

Critical weaknesses
  1. fit to ICLR: As far as I can tell, the paper does not propose a new learning method, representation, training objective or theoretical result. Its contribution is an evaluation protocol for one specific imaging modality, tested on a few closely related FLFM reconstruction networks. The paper doesn;t draw a lesson for the broader ML community. The question it studies is general: when can a self-supervised, measurement-space score be trusted to select models for an inverse problem? The same question comes up in MRI, CT, computational photography and image restoration. Yet the paper is framed entirely in FLFM terms, and its related work is almost exclusively about microscopy hardware and applications. The paper seems aimed at the computational microscopy community, which would probably be better served by a journal or conference in that area. To be interesting for ICLR, I think the paper would need to (a) state the general ML problem up front, (b) position itself against the ML literature on proxy-metric validation and model selection without labels, and ideally (c) show the phenomenon in more than one inverse problem.
  2. Density and opacity of the text:
  • I found the main text very hard to follow, and I believe most ICLR readers would too. Some examples: Within the first few pages the reader hears about Comparable-Candidate Stratification (CCS), Contract-Separated Evidence Validation (CEV), "contracts", "evidence scope", "candidate scope", the family/run/state/file hierarchy, "rule aliases", Q_obs, Q_hold and Q_obj, endpoint-oracle and prospective regret, and "historically accessible groups". Most of these name fairly ordinary ideas: grouping models, holding out data, comparing against ground truth. The new vocabulary makes the paper feel more complex than the ideas behind it.

-Hard to parse sentences: "Prospectivity concerns this rerun on historically accessible groups" (Sec. 3.3), "files may duplicate weights, and states within a run retain trajectory dependence" (Sec. 3.1), "Cohort-dependent regrets diagnose choices and are unranked across rules" (Table A7), "Population diagnostics remain unranked" (Tables A5, A6). I had to reread these several times, and I am still unsure what some of them mean. -too much reliance on the appendix -Figure 2 is overloaded - it litteraly packs everything making it unreadable at normal reading size

-introduction doesn't set up the problem- much of the first few paragraphs list biological applications of FLFM, not the ML question.

-Meanwhile the actual problem setting (what we observe, what we reconstruct, what reprojection actually means) is never laid out. the abstract is almost unreadable for the non-specialist

I would strongly encourage a rewrite. It should open with a plain-language problem statement and a simple diagram of the pipeline (camera image → reconstruction → reprojection; compare against the camera, against withheld views, against the true object). It should use far fewer coined terms and give a self-contained account of the main experiment in the main text.

  1. Findings feel somewhat unsurprising:
  • The title question. The answer is "not necessarily", and the paper says so in the intro: "Different fluorescence distributions in depth can produce similar projections." If many 3D objects can produce the same camera image, fitting the camera image well cannot guarantee recovering the right object. This is standard the world of inverse problems and not a new finding.

-Pooled vs. close-candidate agreement. Two scores can agree on ranking very different models (a strong family vs. a weak family) and still disagree when ranking near-identical checkpoints. That is a general property of correlations computed over mixed populations. The authors state that in App A.1

  • The background counterexample. The image-similarity score rises when background is added because each image is normalized by its own maximum, which hides the change in absolute intensity. The paper notes that an unnormalized error measure moves in the expected direction in the same experiment. This reads to me more as a caution about one particular metric than as a general finding about reprojection-based selection.

-The selected model depends on the score used. This is almost true by definition when different scores measure different things.

None of these is wrong and doing the experiments to spell them out is useful. But I did not come away feeling like I learned something. If the authors feel that practicioners need to know about these results, they should spell it out, giving examples of recent peer-reviewed studies where people "get it wrong" and would give different results by using the authors' prescriptions.

Questions for authors
  1. Can you state, in two or three sentences and without the CCS/CEV terminology, what a practitioner should do differently after reading this paper?
  2. Which of your findings do you consider genuinely surprising, and to whom? Is there published work in FLFM or related modalities whose conclusions would change under your protocol?
  3. Do you expect the same phenomena in other self-supervised inverse problems (e.g., MRI or CT with measurement-domain validation)? If so, why frame the paper only in FLFM terms?
1 comment

The problem in plain words

A Fourier light-field microscope records one camera image per acquisition, and a network turns that image into a volume. Where no real volume exists for a specimen, the only check available at deployment is a reprojection, the predicted volume pushed back through the instrument and compared with the camera. Everything a practitioner can see at the moment of choice lives in measurement space, so the question is whether a score computed there orders candidates the way the unobservable object would, and that ordering turns on who is in the pool.

The single-family pool

One reconstructor family, 48 training runs, one checkpoint per run, no two readings sharing a saved file. Your reading, that the pooled-versus-local gap is a general property of correlations computed over mixed populations, predicts one coefficient here. The pool returns two, on opposite sides of zero, with disjoint intervals.

T1. One family, one checkpoint per run, with the withheld score's upper bound below the supplied score's lower bound.

Coefficientnρ95% interval
Supplied-view to object48+0.583[+0.340, +0.764]
Withheld-view to object48−0.042[−0.335, +0.243]

Supplied-view fit tracks recovered structure at +0.583, lower bound +0.340. Withheld-view prediction reads −0.042, upper bound +0.243, and the intervals are disjoint on candidates whose only difference is the training run. A pool with one population holds no family separation to exploit, and it still separates the two scores by more than half a correlation unit. We expected the opposite sign on every run, since withheld-view prediction is the score with less access to the answer, and the sign came out the other way. Across populations the withheld score agrees with the object at 0.823 on the 23-state mixed pool and at −0.042 with the family fixed, while the supplied score reads 0.831 and +0.583.

The price of a frozen choice

Freezing a choice on groups 20–29 and reading object Pearson on the known volumes costs 0.0721 under the supplied-view rule and 0.0890 under the withheld-view rule, against the known-volume optimum of the same 48 runs.

T2. Frozen selection, object Pearson given up against the known-volume optimum.

RuleGiven upResamples positive
Supplied-view0.072175.4%
Withheld-view0.089099.8%

The withheld-view cost is positive in 99.8 percent of resamples, and the supplied-view cost reaches zero at its lower end. A definitional dependence produces no frozen deployment choice that is optimal for one target and 0.1542 away from optimal on the other, and the disagreement sits in the state choice inside one family, which is the decision a checkpoint rule makes.

Literature positioning

Miller et al. and Baek et al. establish that a label-free proxy tracks target accuracy across a pool whose members differ widely. SSDU, ZS-SSL, Noise2Self, Noise2Void and Laine et al. establish that a loss on withheld measurements stands in for a reference when choosing a stopping epoch or a hyperparameter, always inside a single training setting. Varma and Simon and Cawley and Talbot establish that scoring a model on its reporting data biases the number, and prescribe nesting and freezing, which we follow. D'Amour et al. and Wirgin establish that equally good fits can differ downstream, and each of these lines stops at the mechanism, with none reporting the size of the gap between a measurement score and an object score on a trained pool at fixed family, which is the pair in T1.

Population and ranking

The same coefficient moves with the population it is computed over, at 0.691 pooled across 23 states, 0.285 on the ten signed-plus-Calibra states, −0.100 on the five signed states, 0.886 on the six positive HYPER states, and 1.000 on the seven XLFMNet states. A coefficient that changes under a tightening of the population is measuring the population.

The practitioner rule

First, compute the ranking inside the candidate population you choose from, since a coefficient over a mixed pool is carried by family separation. Second, report supplied-view fit, withheld-view prediction and known-object agreement as three separate numbers, since one combined number averages a gain against a loss. Third, select on one target and verify on another, since a freeze on groups 20–29 read on 30–49 gives different deployment choices for different targets.

Other inverse problems

A CT or MRI reconstruction scored by its own measurement residual carries the same structure, and what has to be rebuilt is the whole path the score is computed through, the acquisition model, the projector, the noise contract and the known object.

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Paper summary

The paper asks whether better reprojection, meaning closer agreement between the camera image and the re-projected reconstruction, implies better 3D reconstruction in Fourier light-field microscopy (FLFM). This matters because true 3D volumes are usually unavailable, so models are often selected by reprojection. The paper proposes SCOPE-FLFM, an evaluation framework with two parts: CCS and CEV.

Critical strengths
  1. The author asks a great research question. Self-supervised FLFM reconstruction is usually trained and selected by reprojection because G.T 3D volumes are unavailable. Testing whether this criterion actually reflects 3D accuracy matters for anyone choosing among such models, and the framework applies to other inverse problems without G.T.
  2. The author also provides clear and consistent evidence that a common selection score can mislead. Adding background raises reprojection SSIM but lowers object Pearson in all 23 learned states. Selecting by loss and by active-view SSIM picks different models, each with a different cost. These are concrete, reproducible cases where a higher score does not mean a better 3D reconstruction.
Critical weaknesses
  1. The learned models seem undertrained. In Figure 5, RL-128 recovers the bead and filament structure, while the learned models recover only parts of the lateral pattern and concentrate signal in narrow depth bands. RL also leads on reprojection and on the primary 3D metrics (Section 4.2., Table A.4). The appendix shows that most selected checkpoints come from the end of training (epoch 23 of 24), and that 12 more epochs improve SSIM and loss in all 12 runs (A.14). The paper shows disagreement among weak models that are still improving. It's unclear whether the conclusion holds for well-trained models.

  2. The within-HYPER correlation of 0.079 (Section 4.1) is reported without a confidence interval or noise ceiling, so it is hard to tell whether these models differ meaningfully. Part of it has a simple explanation -- positive HYPER fits the input views worse but predicts withheld views about as well (Table A4), the usual trade-off between fit and generalization. In the background test, SSIM rises by up to ~0.5 while object Pearson falls by at most ~0.05 (Fig. 4e), and both MSE and per-view normalized NMSE worsen (Section 4.3). This suggests the effect comes mainly from SSIM under per-view normalization specifically. So overall, the results support a narrower claim than the conclusion's general statement that camera-image agreement and 3D recovery are distinct.

Questions for authors
  1. Do the main findings hold for well-trained models? For example, if training continues until the selected checkpoint is no longer at the end of training, does the within-HYPER rank disagreement remain?

  2. Are the differences between close candidates larger than measurement noise? A split-half analysis (rank agreement of each score between two disjoint halves of the final groups) and confidence intervals for the within-group correlations would be helpful.

  3. Since MSE and NMSE both worsen under background, does any measurement score other than per-view-normalized SSIM improve?

2 comments

Loss-stopped pool

Forty runs from scratch on groups 0–19 stop after ten epochs with no improvement beyond 8.0e-3 in training-set reprojection loss, and save the stopping epoch. Neither the excluded-view score nor object Pearson enters that decision. Rank disagreement survives in both families.

T1. Rank agreement, groups 30–49, 10,000 bootstrap draws.

FamilynSupplied→held-outSupplied→object
signed20−0.265 [−0.671,+0.219]+0.797 [+0.512,+0.942]
softplus20+0.272 [−0.271,+0.715]+0.275 [−0.269,+0.685]
pooled40−0.143 [−0.456,+0.202]+0.863 [+0.706,+0.933]

T2. Stop epochs, 100-epoch cap.

FamilyRangeMedianAt cap
signed14–34300
softplus22–38280

Selecting on groups 20–29 by supplied-view score lands on the object optimum, gap 0.0000, interval [0.0000,+0.0594]; the softplus family gives up 0.0417 under the same rule. The paper's coefficient measures within-family ordering.

Checkpoint accounting

T3. Checkpoints at the last epoch, 24-epoch budget, 36 files across 12 runs.

RuleAt last epochof 12
full-view SSIM1012
loss1112
active-view SSIM412
pooled2536

A monotone rule facing a cap lands on the boundary; active-view escapes it in 4 runs of 12. Re-selection after twelve more epochs moves full-view SSIM in ten of twelve runs and loss in nine. In the sixty-epoch pool, 31 of 32 runs fire their tolerance before the cap.

Coefficient across budgets

T4. Pooled-to-local coefficient by budget, groups 30–49.

PoolBudgetnρ95% interval
paper, signed245−0.100[−0.300,+0.600]
rule-firing, signed408−0.095[−0.286,+0.286]
loss-stopped, signed14–3420−0.265[−0.671,+0.219]
longer6010+0.333[−0.006,+0.479]
longer, twelve runs6012+0.308[−0.007,+0.462]
single-familyone ckpt48+0.082[−0.078,+0.283]

Every interval contains zero, and the two sixty-epoch rows miss it by 0.006 and 0.007. Dropping any single run leaves the sign, spanning +0.083 to +0.567 at sixty epochs. Object Pearson beneath the coefficient spans 0.109 to 0.335 on twenty known phantoms. A truncation account predicts a large, negative, sign-stable value.

Reliability

T5. Split-half reliability, 2,000 ten-ten partitions, 5,000 group draws.

QuantityValue95% interval
Supplied score0.979[0.951,1.000]
Held-out score0.685[0.496,0.895]
Ceiling0.819—
Observed, 12 states0.343[0.294,0.853]

The ceiling caps agreement between any two measurements at 0.819, and 0.343 sits at 0.42 of it. The supplied score reproduces its own ranking on unseen groups at 0.979; the withheld score carries the variation a selection built on it would inherit. One explanation in your review loses its route here.

Background scope

At 0.06 object Pearson falls in all 23 states, and no score other than per-view SSIM improves in a majority.

T6. Mean change, 23 learned states, Appendix A.11.

LevelSSIMObject PearsonSSIM upPearson down
0.01+0.2199−0.002518/2317/23
0.03+0.2582−0.007822/2317/23
0.06+0.2538−0.026423/2323/23

The object change at 0.06 carries a hierarchical interval of [−0.0336,−0.0215]. The SSIM gain peaks at 0.03, the object loss at 0.06, and the reversal worsens with background. The score that rises is the one these models are trained against.

Use of the score

T7. Selection frozen on groups 20–29, twelve states.

ScaleObject PearsonGap
per-view SSIM0.28560.0106
raw MSE0.15610.1401

T8. Supplied-view shortlist, 48-run pool, gap to the best run.

ShortlistBest gapWorst gap
top two0.0000.072
top five—0.104
top ten—0.163

A two-candidate shortlist holds the best run at zero cost; a larger one costs 0.072, 0.104 and 0.163. Switching the same frozen protocol to raw MSE pays 0.1401. Supplied-view SSIM tracks object fidelity at 0.880 across 32 runs, against −0.058 for the excluded-view score. Inside a trajectory both readouts move together at a run-level Spearman of +0.99.

The families where the two scores agree are the ones whose outputs go non-negative, at 0.886 and 1.000 against −0.100 for signed HYPER. Clamping negative voxels moves the supplied score by −0.049 in the fixed-budget pool.

Shortlist on the supplied score, verify structure on a small known set, keep a pooled coefficient out of tie-breaking inside a family. A reprojection score tells you where to look, and a volume tells you what you found.

Thank you for the additional experiments. T1–T4 substantially address my concern about the 24-epoch cutoff. T5 shows that the held-out ranking is less stable across evaluation groups than supplied-view SSIM rankings. Maybe a confidence interval for the original ρ\rho = 0.079 on the same 16 HYPER-derived states would still be helpful.

I am keeping my score because it remains unclear when the reported rank disagreement (supplied-view SSIM vs held-out-view SSIM) leads to worse 3D model selection. In T1, supplied-view SSIM has a Spearman correlation of −0.265 with held-out SSIM and +0.797 with object Pearson in the same signed HYPER runs. T7 and T8 also show that supplied-view SSIM can be useful for selection, while T6 documents a specific failure under additive background. Please include these results into the main text and explain what they imply for 3D model selection in each candidate set.

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Paper summary

This paper studies whether reprojection scores can reliably guide model selection in Fourier light-field microscopy. The proposed SCOPE-FLFM framework separates model families, training runs, and unique checkpoints, and evaluates fit to supplied views, prediction of held-out views, and agreement with known synthetic volumes. The experiments show that ranking agreement drops within some groups of related candidates. They also show that adding background can improve normalized reprojection SSIM while reducing object Pearson. A matched Calibra-LF case study illustrates how the same model change can help some reconstruction properties and hurt others.

Critical strengths
  1. The paper asks a useful question. When paired 3D references are hard to obtain, it is tempting to treat a better reprojection score as evidence of a better reconstruction. Testing this assumption directly is worthwhile.

  2. The checkpoint accounting is careful. The authors distinguish 36 checkpoint files from 23 unique states and keep track of dependence within a training run. The drop in supplied-view versus held-out-view Spearman correlation from 0.691 across all learned states to 0.079 within the HYPER-derived group makes the effect of candidate composition easy to see.

  3. I appreciate the balanced reporting of Calibra-LF. The authors show both gains and losses across metrics, including the uncertainty in its clean-corpus SSIM gain, rather than presenting it as a consistent improvement.

Critical weaknesses
  1. Reprojection and object evaluation handle negative outputs differently. The block-wise absolute value in Equation A.2 may introduce additional sign ambiguities that affect the relationship between measurement scores and object quality. Although the paper includes a Positive HYPER control and related sensitivity analyses, the effect of this factor on the central local-ranking results still needs clarification.

  2. The core ranking and model-selection analyses rely on a limited set of candidate states. Appendix A.14 shows that reprojection fit can still improve with longer training, while Appendix A.15 broadens the range of candidate models. However, these additional states and candidates have not been fully incorporated into the core ranking and structural-quality analyses. The robustness of the main conclusions to training duration and changes in the candidate set therefore needs further verification.

  3. The background experiment shows that reprojection SSIM and object quality can change in opposite directions across input conditions, but this does not directly establish whether background perturbations affect actual model selection. The authors discuss how normalization affects SSIM, but do not provide a direct comparison showing whether changing the normalization alters candidate rankings and the model ultimately selected.

Questions for authors
  1. Could the authors further assess how negative-output handling affects disagreement between measurement and object scores, and verify the main local-ranking findings among models with nonnegative outputs?

  2. Do the core ranking and model-selection conclusions remain stable after including states from longer training and expanded candidates such as XLFMNet+CWFA? Could the authors provide corresponding uncertainty analyses?

  3. Could the authors compare model-selection outcomes using different measurement metrics under the same background conditions, to clarify how background perturbations and score normalization affect the structural quality of the selected model?

1 comment

Output convention

Reprojection fit ranks nonnegative reconstructions well and signed ones poorly, and the split reproduces across four populations.

T1. Supplied-to-held-out Spearman, 95% CI, group bootstrap over groups 30–49, 10,000 draws. Signed = Signed HYPER + Calibra-LF, ten states over two families; Nonneg = Positive HYPER and XLFMNet.

PoolSignedSigned CINonnegNonneg CI
Paper 230.285[−0.006, +0.467]0.989[+0.934, +0.995]
Archived 220.486[−0.543, +0.886]0.894[+0.803, +0.941]
Retrained 12−0.086[−0.143, +0.429]0.943[+0.771, +1.000]
Longer 320.211[−0.067, +0.339]0.770[+0.527, +0.915]

In the paper's own pool the nonnegative interval opens at 0.934 while the signed one reaches zero. Hold family fixed and the effect shrinks, with twelve runs per convention in one HYPER-derived family reading +0.420 [+0.266, +0.566] signed and +0.385 [−0.070, +0.601] softplus, leave-one-run-out +0.227 to +0.573. The collapse belongs to signed reconstructions read inside a mixed population.

Clamping

The projector sums signed depth and takes a magnitude afterwards, so negative mass cancels signal ahead of the comparison.

T2. Clamping every volume at zero, measurement-to-object Spearman, phantom bootstrap 5,000 draws.

PoolScorerhorho clampedDelta95% CI
23 statessupplied0.8330.830+0.003[−0.017, +0.016]
23 statesheld-out0.8230.827−0.004[−0.041, +0.010]
12 statessupplied0.7970.7970.000[−0.042, +0.021]

The ranking moves by 0.004 at most while the same intervention moves individual scores by up to 0.145. Clamping raised the score in 7 of 10 paper-pool states carrying negative mass and in 6 of 6 retrained ones, by 0.017 to 0.145. The negative-mass ratio predicts that gain at −0.830 on ten states with p = 0.003 and carries nothing against the supplied-minus-object gap, at 0.018.

Pooled versus within

T3. Pooled agreement exceeds within-HYPER agreement, difference CI from the same draws.

PoolPooledWithinDiff95% CI
Retrained0.343 (12)−0.567 (9)+0.910[+0.203, +0.977]
Archived0.862 (22)0.100 (9)+0.762[+0.140, +1.104]

Both intervals clear zero from above. The paper prints the same shape, at 0.831 and 0.823 across all learned states against 0.506 and 0.482 inside HYPER, turning negative at −0.406 and −0.503 in the signed stratum.

Loss-only pool

Forty runs, twenty signed and twenty softplus, stopped when training-set reprojection loss stays within 8.0e-3 of its running best for ten epochs.

T4. Selection on groups 20–29, object-Pearson cost of the supplied-view pick inside each family.

SubsetRunsrho95% CIPick cost
Signed20−0.265[−0.671, +0.219]0.0000
Softplus20+0.272[−0.271, +0.715]0.0417
Pooled40−0.143[−0.456, +0.202]0.0000

The supplied-view pick is the object optimum of the pooled forty at 0.0000, CI [0.0000, +0.0594], under a rule that read no selection statistic.

Priced pool

T5. Forty-eight signed-HYPER runs, one checkpoint per run, choice frozen on groups 20–29.

QuantityValue95% CI
Supplied to object+0.583[+0.340, +0.764]
Held-out to object−0.042[−0.335, +0.243]
Supplied to held-out+0.082[−0.078, +0.283]

T6. Object-Pearson cost against the known-volume optimum, run bootstrap.

Frozen choiceCost95% CIPositive resamples
Supplied-view SSIM0.0721[0.0000, +0.0968]75.4%
Held-out SSIM0.0890[+0.0495, +0.1999]99.8%

Normalisation

T7. Gap to the object optimum at fixed background, paper's 23 states, optimum Calibra-LF S2 at every level.

BackgroundOptimumPer-view SSIMNMSERaw MSE
none0.30700.04360.00000.1570
0.010.30170.00000.00000.1464
0.030.29150.11580.00000.1346
0.060.26990.08050.08050.1087

T8. Three scales carry a prospective value, two common-scale statistics only a retrospective one, same twelve states, optimum 0.2962.

ScaleProspective gapRetrospective gap
Per-view max SSIM0.01060.0106
Raw MSE0.14010.1401
Independent NMSE0.01060.0106
Common-target SSIM—0.0521
Common-target MSE—0.1621

Per-level scale spread runs to 0.1744, wider than the 0.3070 to 0.2699 range the background itself covers, and five scales land on four distinct states out of the same twelve candidates.

Closing

A practitioner selects on a nonnegative population, fixes the normalisation before comparing candidates, and prices the frozen choice against known volumes before deploying.

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

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