acceptodds
Withdrawn from ICLR 2027

You Cannot Recover What Was Never Measured: Quantifying the Information Ceiling of Ultra-Low-Field MRI Super-Resolution

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

Generative super-resolution models can turn portable 64 mT MRI into images that look like 3T scans, and the field evaluates them with PSNR, SSIM, and pixelwise uncertainty, most often on pairs built by synthetically degrading high-field images. Prior work acknowledges that these models hallucinate and that the problem is ill posed, but to our knowledge no study measures how much information about the individual subject the real low-field scan actually contains. We measure it. Using paired 64 mT and 3T scans of the same subjects from three public datasets, and a measurement protocol validated on tests whose correct answer is known in advance, we find that, judged over the whole brain, real 64 mT scans carry structure specific to the individual only down to approximately 3 to 4 mm half-pitch in plane, and coarser still through plane. Standard synthetic degradations preserve subject information roughly 1 mm beyond this ceiling, so models trained and benchmarked on synthetic pairs are evaluated on information that real scanners never record. We then test trained diffusion models and a publicly released external model on real paired acquisitions; 24 trained runs of five architectures (GAN, diffusion, and transformer families) give the coverage of the audit. On every subject where faithfulness can be measured, fine output detail is no more correlated with the subject's own 3T scan than with a stranger's, while sample-variance uncertainty does not distinguish fabricated structure from reconstruction difficulty. Because PSNR and SSIM score resemblance to a reference rather than whether detail belongs to the subject, a benchmark scored by them cannot tell recovery from fabrication. Code for the measurement protocol will be released so that recoverability claims can be tested for newer models.

Primary area:
datasets and benchmarks
Keywords:
hallucination, trustworthy machine learning, evaluation and benchmarking, uncertainty quantification, inverse problems, super-resolution, generative models, low-field MRI, medical imaging, reliability

Reviews

Among:
Shape:
1234this paper, Bottom 2%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_CScLOpenReview ↗
Rating
1
Confidence
3
Informativeness
2
Presentation
2
Soundness
1
Read review
Paper summary

This paper investigates whether generative super-resolution models can genuinely recover subject-specific anatomy from ultra-low-field (64 mT) MRI, or if fine details are hallucinated. Using real paired scans from public datasets, the authors measure an empirical information ceiling via cross-modal Fourier shell correlation, reporting that real 64 mT scans retain reliable subject-specific structure only down to approximately 3–4 mm half-pitch in-plane. They further demonstrate that standard synthetic degradations preserve finer information than real acquisitions. By auditing trained models with a stranger-controlled test, they find that fine output details are no more correlated with the subject’s own 3T scan than with a stranger’s, indicating fabrication at fine scales. Since PSNR and SSIM score resemblance to a reference rather than subject-specific fidelity, benchmarks relying on them cannot distinguish recovery from hallucination. The validation employs known-answer tests, registration controls, synthetic and oracle baselines across multiple architectures, including GANs and diffusion models.

Critical strengths
  1. I find the central question of this paper highly important: are the fine details in model outputs genuinely recovered from the input, or are they generated by learned priors, potentially amounting to hallucinations? This question is more clinically meaningful than simply pursuing higher PSNR/SSIM scores. Indeed, it extends beyond ultra-low-field MRI super-resolution to medical image super-resolution more broadly: can information that has been lost or smoothed away during acquisition truly be created from nothing? Rather than merely criticizing existing models, the authors attempt to measure how much subject-specific structural information remains in real 64 mT scans. This shifts the discussion from subjective visual assessment to a quantifiable measurement. Framing the problem in terms of an “information ceiling of recoverability” is both direct and insightful.

  2. The experiments are carefully designed. The paper is grounded in real paired 64 mT/3T scans rather than relying solely on synthetic degradation, which makes its conclusions more convincing than those based purely on synthetic experiments. In addition, the authors employ known-answer tests, registration-error controls, intensity-normalization checks, stranger controls, synthetic-degradation controls, raw-input baselines, and oracle controls, demonstrating an awareness that frequency-domain measurements are not inherently reliable. Both the main text and the appendix clearly discuss the boundaries of the proposed methodology and describe failure cases, which is commendably transparent.

Critical weaknesses
  1. The paper’s central model-level claim relies primarily on direct audits of only four held-out subjects, of which only two are fully certified. This evidence base is too small to support broad conclusions across models and datasets, and the results may be sensitive to individual registration quality, contrast differences, or data anomalies. Because faithfulness is not computable for most of the 24 audited runs, these four cases carry nearly all of the direct evidence. If any one of them contains an undetected bias, the main conclusion would be substantially weakened. Furthermore, the ceiling estimates themselves are computed on small cohorts (n = 8, 10, and 11 across the three datasets), the standard error of the ceiling estimates is substantial, revealing that the result is highly sensitive to the specific subjects included in the sample.The authors’ disclosure of this limitation is appreciated, but it does not mitigate the serious impact this small evidence base has on the paper’s central support.

  2. The paper’s significance lies mainly in raising an important evaluation question rather than in methodological novelty. It shows that low-field MRI super-resolution may fail to distinguish genuine recovery from plausible hallucination, which is clinically relevant. However, for the ICLR main track, the technical novelty is limited: the paper does not propose a new model, learning algorithm, training objective, or broadly reusable benchmark/metric. It mainly applies existing frequency-domain measurements and control-based comparisons to a specific low-field MRI setting. Moreover, the limitations of PSNR and SSIM are widely recognized in the low-level vision community. Even without strong methodological novelty, the contribution could be much stronger if the scope were broader. Similar recoverability-versus-hallucination issues may exist in many other medical imaging tasks, such as low-dose CT to standard-dose CT, or non-contrast CT to contrast-enhanced CT. Demonstrating that the proposed audit generalizes across such settings would make the paper more compelling for a machine-learning venue. As it stands, the work is valuable but may be insufficient for a strong acceptance at the ICLR main track.

Questions for authors
  1. The central model-level claim relies on only four held-out subjects, of which only two are fully certified. Could the authors expand the number of auditable cases? Many runs are not computable due to registration, anchor, frame-consistency, or data-quality issues. Could the authors provide a complete accounting of all attempted subjects/runs and failure reasons, and discuss whether the excluded cases could systematically affect the conclusion? This is my primary concern. Given the insightful perspective of this paper, I would not want to assign a low score for this reason alone. However, the current experimental evidence is simply too limited. If the authors can expand the auditable cases and strengthen the empirical support, I would be willing to raise my score.

  2. The direct evidence mainly comes from single-contrast T1w diffusion models and a small number of subjects. To what extent do the authors believe the conclusion generalizes to other modalities, and clinical data containing lesions or abnormal anatomy? Similar hallucination issues may arise in other medical imaging tasks, such as low-dose CT to standard-dose CT, or non-contrast CT to contrast-enhanced CT. Have the authors considered extending the proposed audit to these settings? If not, what are the main limitations?

  3. Since PSNR, SSIM, and sample-variance uncertainty do not distinguish genuine recovery from fabrication, what evaluation protocol would the authors consider that may be suitable for low-field MRI super-resolution work in the future? Is there a reusable audit procedure that worth to explore?

1 comment
AuthorsOpenReview ↗

Response to Reviewer CScL

We thank Reviewer CScL for the constructive framing of what would raise confidence.

Primary concern, and Q1: expand the auditable cases and provide a complete accounting. This is what we did. We audited the external tool on a pre-registration frozen before scoring: 22 attempted subjects, which decompose as 19 auditable (16 fabrication, 3 coarse recovery; 17 new subjects plus the two Zenodo pilots sub-0048 and sub-0064), 1 gated out (sub-HYPE16, NC-ANCHOR), and 2 OpenNeuro pilot consistency reruns (sub-HYPE21, sub-HYPE22) that reproduce the submitted values and are not counted again; 0 exceedances. The four pilot values reproduce exactly. A complete accounting of every attempted run-subject combination, with gate outcomes and reason codes, is posted as a separate comment in this thread. The recalibrated ledger is stated plainly: Tier 1 rests on one fully certified trained-model subject and six certified external-tool subjects (sub-0048 among them), and the frame-internal invariant holds on 19 of 19 external subjects and 8 of 8 final-epoch runs. We also tested the reviewer's point that the ceilings may be sensitive to which subjects the cohorts contain. A leave-one-out jackknife over the three ceiling cohorts shows they are not: every leave-one-out median stays inside the published confidence interval, and removing any single subject shifts a cohort median by at most 0.10 mm half-pitch. The reviewer wrote that expanded auditable cases would be grounds to reconsider; that expansion is above.

Q2. Does the protocol generalize to other modalities, for example CT or lesion cohorts? The protocol requires paired acquisitions of the same subject and nothing modality-specific: gates with known answers, a per-subject anchor, a raw-input benchmark, and the stranger control. It transfers wherever such pairs exist. Lesion cohorts and CT are future work that the released protocol enables, and we do not claim them here.

Q3. Is the evaluation protocol reusable? Yes. We release the measurement protocol as a reusable audit comprising the gate battery with known answers, per-subject anchors, the raw-input benchmark, the stranger control, the reason-code taxonomy, and the frozen pre-registration manifests used in this work. It is designed to run on any paired-acquisition super-resolution system.

Reviewer_BwQXOpenReview ↗
Rating
2
Confidence
3
Informativeness
1
Presentation
2
Soundness
1
Read review
Paper summary

This paper evaluates whether generative super-resolution models can recover subject-specific anatomical details from real 64 mT MRI scans, finding that synthetic degradation overestimates recoverable information and that generated fine details are not reliably supported by the individual subject’s scan. The authors highlight the limitations of conventional metrics such as PSNR, SSIM, and sample-variance uncertainty, emphasizing the need for evaluation methods that distinguish genuine anatomical recovery from hallucinated detail.

Critical strengths

An empirical examination of the gap between real and synthetic low-field acquisitions. Using paired 64 mT and 3T scans, the paper compares real acquisitions with several noise-matched synthetic degradations and reports sensitivity analyses. This provides useful evidence that common synthetic pipelines may not reproduce the frequency-dependent correspondence observed in real data. Although interpreting these differences as an information ceiling requires further justification, the empirical comparison is a substantive strength that supports the paper’s value as an evaluation study.

Critical weaknesses

The central metrics do not establish the claimed information ceiling or identify hallucinations specifically. A cross-FSC half-bit crossing measures frequency-dependent correspondence under a particular preprocessing protocol; the paper does not establish that it bounds recoverability for all reconstruction methods, including those exploiting nonlinear or cross-frequency relationships. This undermines the interpretation of the measurements underlying the paper’s main claims.

The direct validation is limited and contains an unresolved certification inconsistency. Faithfulness is computable for only four single-contrast diffusion runs across four subjects; the remaining 20 runs do not substantiate cross-architecture conclusions. Moreover, Table 5 reports that the OpenNeuro certification compares a dataset interval measured in the E1 frame with subject anchors measured in the v3 frame, while Appendix F states that this dataset-level gate should be undefined across frames. This conflicts with the claim that sub-HYPE21 passes all checks. Combined with checkpoint selection on the same held-out subjects, these limitations substantially weaken the independent evidence supporting the paper’s broad conclusions.

Questions for authors

1.How does the proposed framework distinguish missing direct measurements from accurate prior-based inference? A structure absent from the corresponding input frequency band may still be correctly inferred from other observed features. What theoretical assumptions or experimental evidence justify treating the measured frequency cutoff as a limit on such recovery?

  1. What evidence shows that the proposed test specifically detects hallucinations and offers additional value over existing assessments? Low subject specificity may reflect smoothing, noise, misregistration, or correctly recovered shared anatomy. Can the authors demonstrate that their test distinguishes these cases from fabricated structures, and that stranger control provides an advantage over reference-only frequency-based comparisons?
3 comments
AuthorsOpenReview ↗

Response to Reviewer BwQX

We thank Reviewer BwQX for the focused reading of the measurement and the controls.

W1. Standard metrics neither establish the ceiling nor identify hallucination. We agree, and we no longer rest the claim on a resolution proxy. The ceiling is renamed the measured subject-specific correspondence limit and serves only to locate the scale below which to test. The test itself is the stranger control. A reconstruction that recovered this subject's fine structure by any route would match the subject's own 3T better than a rigidly aligned stranger's, giving REC above SWAP below the crossing. Structure that is inferable without this subject's scan matches a stranger as well as the subject, by construction, and is absorbed by SWAP. Across every trained diffusion system and the external tool, on every auditable subject, the forbidden signature of sustained REC above SWAP where the input shows no correspondence does not appear.

W2. The certification is inconsistent, rests on four subjects, and uses test-subject selection. The reviewer is correct on all three. sub-HYPE21 does not pass all checks, and under the consistent within-frame standard no OpenNeuro subject does, so we rescope the claims to the tier structure rather than asserting uniform certification. On the within-frame recertification the v3 ceiling is unreliable (median 82.7 mm HP, 5 of 11 capped) and within-v3 certification is vacuous; the valid ceiling is on E1 and reproduces the published CI. On the checkpoint control, with no selection 0 of 8 merges beat benchmark and the two marginal exceedances vanish. On the external arm, the invariant holds on 19 auditable subjects with 0 exceedances. The direct claim is carried by the certified Zenodo arm and the mechanism-agnostic stranger test.

Q1. How do you separate a genuinely missing measurement from accurate prior-based inference? The stranger test absorbs any inference route. Prior-based inference produces population-typical structure, which by construction matches a stranger as well as the subject and raises SWAP, not REC. Only subject-specific recovery lifts REC above SWAP below the crossing, and that does not occur. A learned nonlinear attribution probe on the input side is pre-registered as a follow-up to strengthen this separation further.

Q2. What does the stranger control add over a reference-only comparison? Reference-only metrics cannot separate smoothing, misregistration, and correctly recovered shared anatomy from fabrication, because each can move a reference metric in the same direction. SWAP calibrates the no-information floor per band and per subject, so the comparison is against what a stranger's anatomy scores rather than against zero. The oracle and raw-input controls show the readout reports recovery when recovery is present: the S-KSP+N oracle merges at 2.5 mm FP on the OpenNeuro subjects, and the raw-input controls merge at their own benchmarks.

The author has adjusted the proposed definitions and the scope of the discussion, but these changes lack supporting evidence and fail to address my concerns; therefore, I maintain my negative rating.

We thank the reviewer for the reply. The response above reports completed experiments alongside the definitional changes: a within-frame recertification of every gate, a selection-free final-epoch control on all 8 runs, and a pre-registered 22-subject external audit with a per-subject accounting posted in this thread. One concern we could not close with completed work is a fabrication-positive validation of the test itself; that control is pre-registered and stated as future work, not claimed.

Reviewer_b9HfOpenReview ↗
Rating
1
Confidence
2
Informativeness
1
Presentation
2
Soundness
2
Read review
Paper summary

This work aims to reconstructing subject-specific details in ultra-low-field MRI super-resolution. It uses Fourier shell correlation between paired 64 mT and 3T scans to estimate a recoverability limit. It also compares model outputs with the subject's own reference and another subject's reference at different spatial scales. The experiments demonstrate that fine details generated by the evaluated models may not match the subject's anatomy, while conventional image-quality metrics and uncertainty maps provide limited evidence of faithfulness.

Critical strengths
  1. This work addresses a meaningful problem, i.e., determining whether generated details belong to the individual subject is relevant to the reliability of medical image reconstruction.
  2. The experiments use real paired low-field and high-field scans and include synthetic degradation controls, different intensity normalizations, and a publicly released model.
  3. The comparison with another subject provides a useful perspective on reconstruction faithfulness. The authors also proposed failed validation checks and limitations of the evaluation pipeline.
Critical weaknesses
  1. The interpretation of Fourier shell correlation as an information ceiling is not sufficiently justified. Low correlation within a frequency band does not imply that the input contains no information about the corresponding structure. Nonlinear and cross-scale relationships may still support reconstruction. This work should distinguish an empirical correlation threshold from a limit on what any model can recover.
  2. The registration procedure introduces uncertainty into the experimental results. For example, Table 5 compares the OpenNeuro dataset interval measured in the E1 frame with subject measurements from the v3 frame. Using the same frame changes which subjects pass the validation check. The authors should resolve this inconsistency before describing these subjects as certified.
  3. The effective validation is relatively limited. Although the audit includes 24 runs and five architectures, faithfulness cannot be computed for 20 runs. The direct evaluation includes only four subjects, and only two are reported to pass all checks. Broader evaluation with reliable registration and stronger reconstruction models would strengthen this work.
  4. The test subjects are also used for model selection. Appendix G states that the checkpoint is selected using PSNR on the same held-out subjects, without a separate validation set. This makes the final evaluation dependent on model selection. An independent test set or subject-level cross-validation is needed.
  5. The conclusions about image-quality metrics and uncertainty are stronger than the experimental results. Section 5.3 acknowledges that the audit cannot evaluate whether PSNR or SSIM track faithfulness across models. Sample variance also achieves an error-detection AUROC of approximately 0.77. These results show limited specificity.
Questions for authors

See strengths and weaknesses, please.

1 comment
AuthorsOpenReview ↗

Response to Reviewer b9Hf

We thank Reviewer b9Hf for the detailed technical reading.

W1. FSC is a resolution proxy, not an information bound. We concede the proxy gap: FSC does not itself bound information. We rename the measured quantity from information ceiling to measured subject-specific correspondence limit.

The stranger control answers this question. Any reconstruction that recovered subject-specific fine structure by any route, linear or nonlinear, within-band or cross-band, measurement or prior, would show REC above SWAP below the crossing, because its output would match the subject's own 3T better than a rigidly aligned stranger's. Across the trained systems and the external tool, on every auditable subject, it does not. Prior-based inference that produces population-typical structure is what the SWAP term absorbs: structure inferable without this subject's scan matches a stranger as well as the subject, by construction. The correspondence limit locates where to look; the stranger test is the evidence, and the forbidden signature, sustained REC above SWAP where the input shows no correspondence, is empty in every system we audit.

W2. The OpenNeuro certification is inconsistent across frames (Table 5). This is a genuine inconsistency, exactly the class of defect our controls exist to catch. We recomputed every gate within a single frame. On the v3 audit frame the cross-field ceiling cannot be established (median 82.7 mm HP, 5 of 11 at the grid cap), and within-v3 certification is vacuous: subjects pass by having worse anchors and fail by having better ones. The valid ceiling exists only on E1, where our recomputation reproduces the published values. We restructure the audit into certification tiers: a certified Zenodo arm and a frame-internal, correspondence-limited OpenNeuro arm. Two Zenodo subjects do not pass the within-frame anchor gate and move to the correspondence-limited tier, sub-0064 (anchor above the CI) and sub-0023 (below it). What changed is the OpenNeuro dataset ceiling, now reported on E1 with the audit frame labeled v3. What did not change is the OpenNeuro faithfulness result, which compares each model to its own input control on the same frame. Residual registration is bounded separately: a 1 mm injected shift moves the FSC crossing by 0.473 mm FP, a bound the reported gaps must exceed.

W3. The effective validation is limited. We expanded the direct evidence. The external tool is audited on 19 auditable subjects across both datasets, with 0 exceedances; the full accounting with reason codes is posted separately in this thread. The recalibrated ledger: Tier 1 certification rests on one fully certified trained-model subject (sub-0048) and six certified external-tool subjects (sub-0048 among them), and the frame-internal invariant that no model beats its own input benchmark holds on 19 of 19 external-tool subjects and 8 of 8 final-epoch runs.

W4. Checkpoints were selected on the test subjects. Correct, and this was a flaw in the protocol. Checkpoints were chosen by validation PSNR on the same held-out subjects used for evaluation. This selection favors checkpoints that score well against the subject's own 3T, so it tilts the audit toward finding recovery; we found fabrication anyway. The concern also pointed at a real effect, the two marginal sub-benchmark merges. We reran the audited runs at the final training epoch with no selection. None of the 8 merges is finer than its benchmark, and both exceedances return to it (sub-HYPE22 12 to 16, sub-HYPE21 pooled stranger 5 to 6 mm FP). With four audit subjects a separate validation set was not available, so we removed selection entirely, which is the stronger control. The paper's footnote read the two exceedances differently; that reading was wrong, and we correct it here.

W5. The UQ conclusions read as stronger than the results. The 0.771 voxel AUROC is part of our result, not a point against it. Variance does carry error signal, and the paper reports the AUROC as the evidence for that. The limitation is that the signal is not specific to fabrication: variance tracks a stranger's error almost as well as the subject's own (RHO_own 0.390 versus RHO_stranger 0.307 on the fine bands). The paper draws this line itself: "Sample-variance uncertainty flags reconstruction difficulty, not fabrication," and the variance map "is, however, largely non-specific ... so it locates hard regions rather than fabricated content."

On standard metrics the claim is a within-audit dissociation, not a cross-model ranking. We do not claim that PSNR or SSIM fail to rank models. The paper's evidence is that metrics do not track faithfulness in either direction: healthy on pure invention (NIST PSNR 25.6 to 32.3 dB, no verifiable content) and varying for reasons unrelated to verifiability (Zenodo T1w diffusion PSNR 10.5 to 12.0 dB, computed fabrication). We rescope the abstract claim here accordingly.

Comments on the paper

3 comments
AuthorsOpenReview ↗

New experiments completed during the discussion period

We thank the reviewers for a careful reading that identified three real problems, each of which we have addressed with experiments completed during the discussion period.

Three concerns were correct: (a) a cross-frame gate inconsistency in the OpenNeuro certification (b9Hf W2, BwQX W2); (b) checkpoint selection on the held-out subjects (b9Hf W4, BwQX W2); and (c) a small direct-evidence base (b9Hf W3, CScL). We summarize the new results here and detail them per reviewer.

External-arm expansion. We audited the deployed external tool (SynthSR) on a pre-registration frozen before scoring: 22 subjects attempted. These decompose as 19 auditable subjects (16 fabrication, 3 coarse recovery to the input limit; 17 new subjects plus the two Zenodo pilots sub-0048 and sub-0064), 1 subject gated out (sub-HYPE16, NC-ANCHOR), and 2 OpenNeuro pilot consistency reruns (sub-HYPE21, sub-HYPE22) that reproduce the submitted values and are not counted again. The tool's output is never finer than its own raw-input benchmark on any subject, with 0 exceedances in both the pooled and single-stranger estimators. The four pilot values (16/24/6/16 mm FP) reproduce exactly.

Within-frame recertification. The reviewers are right that the OpenNeuro certification mixed frames, and we recomputed every gate within a single frame. The result is that no OpenNeuro subject can be anchor-certified: the cross-frame comparison is undefined, and the v3-frame ceiling cannot be trusted (median 82.7 mm HP, with 5 of 11 subjects at the grid cap). We now report certification in explicit tiers. The fabrication conclusion rests on the certified Zenodo subjects, where the recomputed E1 ceiling matches the published CI of [2.456, 3.609] mm HP.

Final-epoch checkpoint control. We reran the audited runs at the final training epoch, with no checkpoint selection. None of the 8 final-epoch merges is finer than its input benchmark, and the two marginal exceedances we had disclosed disappear: sub-HYPE22 moves from 12 to 16 mm FP and sub-HYPE21 from 5 to 6 mm FP (pooled stranger), both landing at the benchmark. The exceedances came from checkpoint selection. The paper's footnote interpreted them differently; that reading was wrong, and the numbers reported here are the corrected ones.

Terminology. We agree that the measured quantity is not an information bound, and we no longer call it one. We now call it the measured subject-specific correspondence limit. The model-level claim rests on the stranger test, which does not depend on how a model recovers structure.

A complete accounting of every attempted run-subject combination, with gate outcomes and reason codes, is posted as a separate comment in this thread, as requested by Reviewer CScL.

AuthorsOpenReview ↗

Complete accounting of the external-tool arm (1/2: table)

Complete accounting of the external-tool arm (requested by Reviewer CScL). Part 1 of 2: the table. The legend and notes follow as a reply to this comment.

Every attempted subject in the external-tool (SynthSR) audit, on its validated analysis frame. Merges are the Algorithm-5 two-band persistence merge in mm (full-pitch), smaller is finer; the input benchmark is the subject's registered 64 mT scan through the identical readout. Both stranger estimators are shown: pooled leave-one-out (primary) / single fixed partner. A subject is an exceedance only if the SynthSR merge is finer than its input benchmark in either column.

Headline: 22 subjects attempted = 19 auditable (16 fabrication, 3 coarse recovery to the input limit; 17 new plus the two Zenodo pilots sub-0048 and sub-0064) + 1 gated out (sub-HYPE16, NC-ANCHOR) + 2 OpenNeuro pilot consistency reruns (sub-HYPE21, sub-HYPE22; reproduce the submitted values, not counted again). 0 exceedances in either estimator.

SubjectDataset (frame)Whole-brain FSC (mm FP, row frame)Input benchmark (pool/sgl)SynthSR merge (pool/sgl)RegimeGate / reason code
sub-0011Zenodo (E1)9.654 / 624 / 24fabricationPASS (align)
sub-0015Zenodo (E1)5.745 / 516 / 24fabricationPASS
sub-0023Zenodo (E1)6.356 / 616 / 12fabricationPASS
sub-0025Zenodo (E1)7.036 / 612 / 12fabricationPASS
sub-0027Zenodo (E1)8.056 / 616 / 16fabricationPASS
sub-0035Zenodo (E1)7.828 / 624 / 24fabricationPASS (align)
sub-0048Zenodo (E1)6.905 / 516 / 16fabricationPASS
sub-0064Zenodo (E1)14.0416 / 1624 / 24fabricationPASS (align)
sub-HYPE00OpenNeuro (v3)10.736 / 68 / 10fabricationPASS
sub-HYPE01OpenNeuro (v3)17.2812 / 1212 / 12coarse recoveryPASS
sub-HYPE02OpenNeuro (v3)13.198 / 810 / 10fabricationPASS
sub-HYPE03OpenNeuro (v3)12.036 / 610 / 10fabricationPASS-CAPPED
sub-HYPE04OpenNeuro (v3)9.776 / 68 / 6fabrication (pool); boundary flipPASS-CAPPED
sub-HYPE09OpenNeuro (v3)15.698 / 812 / 12fabricationPASS
sub-HYPE13OpenNeuro (v3)13.028 / 810 / 10fabricationPASS
sub-HYPE14OpenNeuro (v3)21.3216 / 1616 / 16coarse recoveryPASS
sub-HYPE15OpenNeuro (v3)24.1116 / 1616 / 16coarse recoveryPASS
sub-HYPE16OpenNeuro (v3)9.435 / 58 / 8not countedNC-ANCHOR (gated out)
sub-HYPE18OpenNeuro (v3)22.086 / 816 / 12fabricationPASS
sub-HYPE20OpenNeuro (v3)11.815 / 610 / 12fabricationPASS
sub-HYPE21OpenNeuro (v3)10.906 / 66 / 6consistency rerun, not countedPASS (rerun)
sub-HYPE22OpenNeuro (v3)21.6016 / 1616 / 16consistency rerun, not countedPASS (rerun)
AuthorsOpenReview ↗

Complete accounting of the external-tool arm (2/2: legend and notes)

Part 2 of 2: legend and notes for the accounting table above.

Legend. Regime: fabrication = SynthSR merge coarser than the input benchmark (structure finer than the merge is fabricated); coarse recovery = merge equal to the input benchmark (recovers to the input limit, nothing finer); exceedance = merge finer than the benchmark (none occur). (rerun) = pilot consistency rerun, reproduces the submitted merge and is not counted again. (align) = low coarse-scale alignment annotation (sub-0011, sub-0035, sub-0064), merge coarse regardless. All scales in mm, full-pitch.

Three layers in this table. (1) The Input benchmark and SynthSR merge columns, and the Whole-brain FSC column, are computed on each row's stated frame (E1 for Zenodo, v3 for OpenNeuro); the Whole-brain FSC column is a descriptive scale. (2) The gate (PASS, PASS-CAPPED, NC-ANCHOR) is a presence check that a valid E1 anchor crossing exists for the subject; for OpenNeuro subjects it is computed through the subject's v3-to-E1 transform. NC-ANCHOR means that crossing is null (sub-HYPE16). PASS-CAPPED means the E1 anchor crossing is at the grid resolution limit (half-pitch 0.576 mm); the subject is kept in the ceiling cohort and flagged (sub-HYPE03, sub-HYPE04). (3) Certification is a separate, stricter test that this table does not assert: the within-frame anchor compared against the dataset ceiling confidence interval of [2.456, 3.609] mm HP. Under it sub-0064 (7.30 mm HP) and sub-0023 (2.36 mm HP) fall outside the interval and are not certified.

Note on scope. This table is the external-tool arm. The full 24 trained reference systems carry their own reason codes (NC-ANCHOR, NC-EPI, NC-XDEV) for the arms where faithfulness is not computable, as in the paper's model-audit table; those codes are unchanged.

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

Related papers

Discussion (0)

Sign in to comment.