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Under review as a conference paper at ICLR 2027

FORGE-CTG: Outcome Queries and Dual-View Distillation for Intrapartum Fetal Acidosis Detection

Abstract

Intrapartum cardiotocography (CTG) is used for fetal surveillance, yet detecting neonatal acidaemia from fetal heart-rate and uterine-contraction traces remains difficult. A pathological trace can trigger intervention without acidaemia, while electrode loss, motion artefact, or prolonged gaps can obscure a trace. Existing learning pipelines face limitations. They reduce a continuous physiological outcome to a single pH threshold, discarding severity structure, and treat missing signal as noise to be imputed rather than as a quality condition that should change supervision. To bridge this gap, we introduce FORGE-CTG, a framework built around complementary ideas. SCOS supervises a shared representation through binary risk, rank-consistent ordinal pH thresholds, continuous pH, and masked base deficit. QVD derives reliability from the raw trace and validity mask, then trains a student against an exponential-moving-average teacher reading a conservative repair; uniform patch weighting keeps quality in the teacher’s view without weakening the student’s learning signal. On the CTU-UHB dataset, FORGE-CTG ranks first among 19 models at 0.7283 record-level AUROC and degrades 4.6×more slowly under increasing missingness, reaching ranking performance with half the training labels. The severity-supervision principle also transfers to clinical time-series tasks, with PTB-XL dataset and CPSC2018 dataset experiments showing a 24% reduction in ordinal severity error with perfect rank consistency. Together, these results support a practical direction for clinical monitoring in which richer supervision and explicit responses to signal quality improve the reliability of risk estimates without requiring larger models.

Primary area:
other topics in machine learning (i.e., none of the above)
Keywords:
Fetal cardiotocography, fetal acidosis detection, clinical time-series analysis, missing-signal robustness, ordinal regression, multi-task learning, knowledge distillation, physiological signal quality

Reviews

Among:
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1234this paper, Bottom 10%
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.
Reviewer_1pTAOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

The paper predicts neonatal acidaemia (umbilical-artery pH < 7.15) from the last 30 minutes of intrapartum CTG (fetal heart rate and uterine contractions, sampled at 4 Hz). It uses the public CTU-UHB database (551 records, 105 positives). The proposed model, FORGE-CTG, is a small patch transformer (about 0.7M parameters) with two additions: 1. SCOS: four learnable "outcome queries" (adapted from FORMED) that predict the binary risk, four nested ordinal pH thresholds (7.20/7.15/7.10/7.05; CORAL-style), the continuous pH (Gaussian NLL), and, when available, the base deficit. 2. QVD: a mean-teacher consistency loss. An EMA teacher sees an FHR trace in which gaps of up to 120 s are linearly interpolated and jumps are median-filtered, while the student sees the raw trace. Hand-crafted reliability features (flatline, jumps, range, and missing runs) are added as patch statistics.

Critical strengths
  1. Clinically motivated ideas. Using the continuous pH and base deficit instead of a single cut-off, and treating signal loss as a quality condition, are sensible choices for CTG.
  2. Broad set of baselines. Clinical-feature models, MiniRocket, many neural time-series models, missingness-oriented models, and pretrained CTG encoders are compared using shared record-level folds.
  3. Additional analyses. Missingness stress tests, label-efficiency experiments, signal-defined subgroups, and ECG experiments give a more complete picture than accuracy alone.
Critical weaknesses

W1. The method combines known techniques, and the gain over simple baselines is small and not significant.

  • SCOS is multi-task learning built from standard components: weighted BCE, CORAL ordinal regression, Gaussian NLL regression, an auxiliary base-deficit head, and the FORMED query interface. • QVD is a mean teacher with an "easier" teacher view. It is closely related to weak/strong-view consistency (e.g., FixMatch) and to learning with privileged information or generalized distillation, neither of which is cited. Also, the teacher is an EMA of the student, not a separately trained model, so calling the method "distillation" is a stretch. • Not better than simple models. FORGE-CTG is not significantly better than 10 of the 18 comparators, including clinical logistic regression (+0.018, CI [−0.017, 0.056]), random forest, XGBoost, a vanilla Transformer, PatchTST, and SAITS. Yet the main text mentions only three of these. All eight significant wins are against models with AUROCs between 0.49 and 0.65, and several of these models appear to be broken. • So the claimed significance for clinical monitoring is not shown: a logistic regression on clinical features performs about as well.

W2. The predicted risks are poorly calibrated, even worse than a constant baseline. This contradicts the claim of "more reliable risk estimates".

  • FORGE-CTG's Brier score is 0.2127 (Table 1), whereas a model that always predicts the prevalence (105/551 ≈ 0.191) has a Brier score of 0.191 × 0.809 ≈ 0.154. So FORGE-CTG's probabilities are less accurate than a constant prediction, and its ECE is 0.26 (Table 3). The likely cause is the positive-class weight (about 4.2×) in the BCE loss, which pushes all predicted risks upward.
  • At 90% sensitivity, specificity is only 27.8%, lower than that of SAITS (35.4%), PatchTST (29.8%), InceptionTime (30.3%), and clinical LR (28.3%). In other words, about 72% of non-acidaemic births would be flagged.
  • The abstract's conclusion that the approach "improve[s] the reliability of risk estimates" is therefore not supported. Recalibration (Platt scaling or isotonic regression, fitted on validation folds) and a decision-curve analysis are needed.

W3. Many baselines appear broken or untuned.

  • Several standard models perform at or near chance: GRU-D 0.4914, FORMED 0.5029, LSTM 0.5177, TimesNet 0.5230, GRU 0.5414, and iTransformer 0.5587.
  • The paper notes that in its GRU-D implementation "an all-observed mask leaves input imputation inactive" (App. D), so GRU-D's key mechanism was in effect switched off. On PTB-XL, the same GRU-D reaches 0.9041, higher than FORGE-CTG (0.8879). This suggests that the CTG adaptation (7,200-step sequences) failed, not that the method is weak.
  • The pretrained encoders (CTGDL-PatchTST, FORMED) are frozen and not fine-tuned.
  • The baselines are single-seed runs whose tuning is not described, whereas FORGE-CTG is a 5-seed ensemble (and seed averaging usually raises AUROC).
  • Established CTG-specific models are missing: feature-based CTU-UHB classifiers (e.g., Spilka et al., IEEE JBHI 2017) and CTG CNNs (e.g., Petrozziello et al., IEEE Access 2019).

W4. The clinical setup is narrow and partly unrealistic. • The paper uses only the final 30 minutes before delivery. This requires knowing the time of delivery, which is future information during labor, and leaves almost no time to act. It also mixes first- and second-stage traces. Results for earlier windows (e.g., 60–90 min before delivery, or the first stage only) are needed to judge clinical usefulness. • The study uses a single small retrospective cohort (n = 551) and has no external validation, as the authors acknowledge. • The clinical LR baseline is never specified (which features does it use?). This matters, because it nearly matches the model. • The paper states that record 1500 has no signal file, so only 551 records are used. However, the public CTU-UHB release lists 552 records. Please confirm whether this is a local data problem.

W5. The subgroup analysis does not show a benefit. • The gap between the pooled AUROC and that of the worst cluster is larger for FORGE-CTG at k = 2 (0.020 vs. 0.004) and k = 4 (0.170 vs. 0.166), and smaller only at k = 3. • The worst cluster at k = 4 (36 records) reaches an AUROC of only 0.558. • The paper does not describe how the clusters were built (features, algorithm) or what the "reference backbone" is.

Questions for authors

Please see Weaknesses above.

2 comments
AuthorsOpenReview ↗

Updated Baseline Comparisons, Risk Calibration, Prediction Timing, and Subgroup Analyses

W1: Contribution and baseline comparison:

The revision defines DPC as a symmetric scalar-risk penalty between two independent dropout passes and relates it to R-Drop. The related-work section also situates training-view consistency alongside FixMatch and generalized distillation. For precision, we describe the raw/repaired mechanism as EMA-teacher feature consistency: the teacher is an exponential moving average of the student, not a separately trained network. The matched ten-seed DPC estimate is +0.0110 AUROC (95% CI [0.0007, 0.0228], raw p=0.038, Holm-adjusted p=0.076); the prespecified five-seed estimate is +0.0167 (95% CI [0.0021, 0.0318], Holm-adjusted p=0.038). The single-head result, 0.7299, is reported separately from these reference-pipeline contrasts. The main benchmark reruns eight baselines on shared record folds and uses paired intervals. The strongest clinical comparator is logistic regression at 0.7139; its paired difference from DPC is +0.0259 (95% CI [-0.0067, 0.0601], p=0.108).

W2: Calibration and operating point:

The revised evaluation reports probability metrics alongside ranking. For ten-seed out-of-fold predictions, DPC changes Brier from 0.1372 to 0.1357 and ten-bin ECE from 0.0248 to 0.0233. The Brier difference is -0.0015 (95% CI [-0.0031, -0.0001]); the ECE interval spans zero. The prevalence-only Brier reference is 0.1542. A threshold of 0.125 selected on validation records for a 90% sensitivity target yields held-out sensitivity 0.905, specificity 0.381, and PPV 0.256. The revised paper also includes a nested calibration audit and decision-curve analysis, with model and seed protocol identified for each result.

W3: Baseline implementation and tuning:

The main benchmark uses eight rerun baselines, each evaluated on the shared five record folds with ten fixed seeds. Trainable baselines use the same three-candidate validation-only selection, a 40-epoch cap, and early stopping. GRU-D receives the validity mask and elapsed-time input. The clinical logistic-regression model uses 19 record-level FHR/UC features with training-fold scaling and validation-fold regularization selection.

W4: Prediction timing and cohort count:

The CTU-UHB release lists 552 recordings. Record 1500 has no signal file, leaving 551 usable records, including 105 with pH < 7.15. Signal-end time equals delivery time in all 552 headers. The revised analysis separates the delivery-anchored window from first-stage-only and earlier landmark windows. The first-stage window is the 30 minutes ending at the annotated stage boundary; on its 505 records (92 positive), DPC AUROC is 0.5617, compared with 0.6259 for clinical logistic regression and 0.7484 for delivery-anchored DPC on the same records. The landmark analysis gives AUROC 0.5683 at 30 minutes earlier (531 records), 0.4286 at 60 minutes earlier (37 records), and no eligible records at 90 minutes. Stage duration defines the retrospective window and is not a model input.

W5: Signal-defined subgroup analysis:

The appendix now specifies the ten label-free FHR/UC statistics, standardisation, and K-means settings (𝑘 = 2, 3, 4, ten initialisations, random state 0). For the five-seed base model, the worst-cluster AUROCs are 0.7080, 0.6740, and 0.5579, with pooled-minus-worst-cluster gaps of 0.0203, 0.0543, and 0.1704, respectively. Cluster sizes are reported, including 36 records in the smallest 𝑘 = 4 cluster.

AuthorsOpenReview ↗

Revision_v3: Updated Baseline Comparisons, Risk Calibration, Prediction Timing, and Subgroup Analyses

Your prevalence calculation and clinical logistic-regression comparison identify the right checks for this task. We used them to examine how well the model orders records, how accurately its probabilities estimate event frequency, and how early the signal is available.

  1. Contribution and comparison with a simple model (W1). SCOS uses the FORMED query interface to predict four related metabolic outcomes. QVD trains the raw-input CTG encoder against a weight-averaged teacher that sees a bounded FHR repair. TFC aligns the tokens used by all four queries across two raw student passes. We cite FORMED, CORAL, Mean Teacher, FixMatch, generalized distillation and R-Drop where those ideas enter the design. The word “distillation” in QVD refers to the student’s feature target from the EMA teacher.

Across the same 551 records, the complete model reaches 0.7329 AUROC against 0.6956 for the pooled binary model (exploratory paired difference +0.0373, 95% CI 0.0071 to 0.0657). Adding SCOS gives the largest individual increment, +0.0302 (nominal CI 0.0063 to 0.0547, Holm p=0.060 over five comparisons). Against a five-seed clinical LR, the full model gains +0.0144 AUROC (95% CI −0.0224 to 0.0514). This cohort leaves their relative performance uncertain.

  1. Probability calibration and practical operating points (W2). You were right that the original Brier score of 0.2127 exceeded the pooled prevalence reference of 0.1542. The revised CTG trainer uses unweighted binary BCE. On the saved five-seed predictions, the full model has Brier 0.1396 and ECE 0.0439, compared with 0.1436 and 0.0164 for the binary arm. The improvement in squared probability error therefore coexists with a higher calibration error under ten-bin ECE. The change in class weighting also affects the comparison with the submitted model.

For the separate five-seed validation-fitted calibration analysis, raw, Platt and isotonic Brier scores were 0.1389, 0.1385 and 0.1496. The reliability plot and decision curves show where net benefit changes with the threshold. In the earlier operating-point experiment, a validation-selected threshold of 0.125 produced held-out sensitivity 0.905, specificity 0.381 and PPV 0.256. At that sensitivity about 62% of negatives would be flagged. The clinical burden you identified persists. Figure 3 and Appendix F give the curves and operating-point results.

  1. Baseline implementation and tuning (W3). Table 1 cites the original comparator models and labels their seed budgets. For eight available reruns we matched the five model seeds and record folds. Baseline hyperparameters were selected on validation records, with model-specific grids and a 40-epoch cap. We supplied the FHR mask and elapsed-time inputs to GRU-D. Its rerun still yields 0.4975 AUROC, so that row describes the performance of our CTG adaptation. The CTGDL-PatchTST and FORMED rows used frozen pretrained encoders. We cite Spilka et al. and Petrozziello et al. as CTG-specific comparators in the literature and identify the clinical-feature LR as our own implementation.

  2. Clinical LR, timing and cohort (W4). The LR uses 19 FHR/UC features covering baseline rate, variability, accelerations and decelerations, threshold durations, contractions and signal loss. Scaling uses training-fold statistics and validation selects the regularization. The appendix gives the full list, including two short-term-variability columns that compute the same quantity. The public CTU-UHB release contains record 1500’s signal file. Its absence was local, and the original folds cover the other 551 records (105 positive).

The input ends at the last available sample. In this cohort, the headers place that sample at delivery. In the historical timing analysis on 505 records (92 positive), the delivery-anchored model reached 0.7484 AUROC. Using the first-stage window gave 0.5617 for the model and 0.6259 for clinical LR. Earlier landmark AUROCs were 0.5683 at 30 minutes (531 records) and 0.4286 at 60 minutes (37 records). No eligible recording reached the 90-minute landmark. We restrict the intended use of these results to retrospective near-delivery ranking. External CTG validation remains open.

  1. Worst-cluster performance (W5). We standardized six FHR summaries and four UC summaries and fitted K-means to all 551 records without outcomes (k=2, 3, 4, ten initializations, seed 0). The earlier reference backbone concatenated FHR and UC tokens used masked-reconstruction pretraining on the training fold, and froze the encoder for the outcome readout. We evaluated both sets of predictions on the same post-hoc clusters. The pooled-minus-worst AUROC gap narrowed only at k=3. At k=4, the submitted model’s worst cluster had 36 records and AUROC 0.5579. Appendix F reports these signal-defined subgroups, their sizes and the same-cluster reference results. We withdraw the general subgroup-robustness claim.
Reviewer_rAGXOpenReview ↗
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1(−1)
Confidence
2
Informativeness
2
Presentation
2(−1)
Soundness
1(−1)
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Paper summary

This paper proposes FORGE-CTG which addresses prediction of neonatal acidaemia from intrapartum fetal heart-rate and uterine-contraction recordings by primarily combining two mechanisms, Severity-Consistent Outcome Spectrum (SCoS) and Quality-Conditioned Dual-View Distillation (QVD). Here, the former is for the supervision of shared representation by using the pH regression and someother measurements. The latter trains a raw-input student using consistency with an EMA teacher processing a repaired signal. The paper evaluates primarily CTU-UHB, where it achieves, 0.7283 AUROC and 0.4226 AUPRC record-level. The authors also conducted the ablations for the components, and their usefulness to the proposed method, where it shows an improvement with the addition of those components from the baseline. Additional analysis gives about robustness to missing observations, label efficiency and the transfer to other targets like PTB-XL, and CPSC2018. The proposed method has improvement over the baselines.

Critical strengths

Following are some of the key strengths of the paper:

  • A clear evidence for robustness of FORGE-CTG: First, the FORGE-CTG achieves best results on the CTU-UHB benchmark [Table 1], and this is compared with several baselines. The controlled component ladder given in Table 2 - page 7, gives a progressive improvements with the help of the components in FORGE-CTG, while the missingness experiment gives a change in degradation slope after adding QVD weights. The uniform-vs-reliability-weighted comparison gives an additional evidence that patch weighting matters for the better prediction, and the depiction of this behaviour is consistent. The paper also addresses a concrete model-behavior question, which is other than just beating the benchmark baselines.

  • Relatively careful experimental interpretation: The study in this paper uses careful splits and includes paired bootstrap comparisons, though they were common for a experimental setup to make the results comparable against each other.

Critical weaknesses

Following are some of the weaknesses of the paper:

  • Methodological contribution: The method or the proposed architecture combines several already established techniques, like: label-query, ordinal-regression, and EMA-consistency technique. Hence, is there a chance like more specific design choices outperform simpler alternatives with equivalent supervision and consistency training. Although the Table 2 with the component ablation shows progressive improvements, but still the evidence does not yet explain that the gains are from the architecture alone or the combination of several techniques. Moreover, component improvements (Table 2) did not report paired uncertainty, and the main result FORGE-CTG does not significantly outperform the strongest benchmark alternatives.

  • Limited demonstrated usefulness: The paper is more about the ranking and it's transfer rather than the usefulness of the method. Its ECG transfer results show gains on constructed ordinal labels rather than a validated clinical severity, with no corresponding improvement in binary discrimination. Also, the evidence for broader clinical or methodological utility remains substantially narrower than the framework's general motivation.

Questions for authors
  1. Can the authors provide paired uncertainty estimates for the Binary to SCoS to QVD improvements (same as Table 1), and clarify whether QVD has been compared with an otherwise identical Mean Teacher using the same input view?

  2. How are multilabel PTB-XL diagnoses mapped to a single severity rank, and how is ordinal MAE computed for the binary-only baseline? Does the ordinal improvement remain consistent across folds and seeds?

  3. Please clarify whether the ECG experiments in Table 5 involve transferring pretrained CTU-UHB model weights to PTB-XL and CPSC2018, or independently training all models on the respective ECG datasets? If the latter, are these experiments intended to demonstrate methodological generalization rather than cross-dataset transfer learning?

  4. In Section 5.3 and Appendix B, the transfer experiments appear to evaluate the proposed learning principles through dataset-specific training rather than cross-dataset model transfer. Could authors please clarify this distinction? Additionally, have the authors considered cross-dataset generalization experiments, particularly training on PTB-XL and evaluating on CPSC2018 (and vice versa), using harmonized prediction targets? Such an evaluation could provide additional evidence about whether the proposed mechanisms generalize across acquisition settings rather than only across independently trained datasets (optional).

3 comments
AuthorsOpenReview ↗

Paired Component Analyses and Clarification of Dataset-Specific ECG Experiments

Q1: Paired uncertainty and same-view teacher control:

Thank you for requesting paired component-level estimates. The appendix now reports the matched output-interface comparisons: query-based multi-outcome versus standard multi-task heads, +0.0053 AUROC (95% CI [-0.0145, 0.0243], p=0.591), and versus weighted binary BCE, +0.0117 (95% CI [-0.0105, 0.0342], p=0.304). For the teacher-view mechanism, the raw/raw EMA comparison is +0.0009 (95% CI [-0.0143, 0.0143], p=0.859); validity-only weighting gives -0.0026 (95% CI [-0.0164, 0.0105], p=0.708); and same-input feature consistency gives +0.0189 (95% CI [-0.0034, 0.0406], p=0.090). All use paired record-level comparisons on matched folds and seeds. We distinguish these controls from the DPC effect in the revised manuscript.

Q2: Diagnosis ordering and binary-only ordinal MAE:

The ECG rank mapping and its role as an auxiliary training target are specified in the appendix. PTB-XL uses the primary superclass order NORM, STTC, CD, HYP, MI; CPSC2018 uses Normal, PAC/PVC, I-AVB/LBBB, STD/AF, STE. These constructed rankings are not clinical severity labels, and the revised results do not use their MAE as evidence of severity prediction. The binary-only configuration has no ordinal head, so its ordinal MAE is undefined. The ECG comparison is evaluated by binary AUROC across five patient/record folds and three seeds.

Q3–Q4: Dataset-specific training and cross-dataset transfer:

The ECG models are trained independently on each dataset with dataset-specific labels and folds; no CTU-UHB weights are transferred. We now call these dataset-specific physiological-signal evaluations and do not describe them as cross-dataset transfer or external CTG validation. Thank you for pointing out the parts of the description that could be misleading; we have made all the necessary corrections.

Reviewer_rAGXOpenReview ↗

Major changes in the paper

Thank you for the response and the extra experiments. The answers to Q3 and Q4 resolve some of my previous concerns. My main concern now here is how much the paper has changed. The title is different and the main contribution is now DPC. DPC itself is an adaptation of R-Drop, and the evidence for it is limited. Why has this been introduced and why there has been a significant change in the whole structure of the paper and content? Even the Figure content has been changed without providing explicit explanation on why the authors decided to make such big changes. Also, the outcome-query part has been removed from the final model along with several key results from the submission. Can the authors please share an update for such major changes? Given these details, I lower my score to 1.

AuthorsOpenReview ↗

Revision_v3: Restoring the Outcome Queries and Testing What Each Consistency Term Adds

We understand why you lowered your score. Our first response changed the title and figures to emphasize dropout prediction consistency (DPC), even though the evidence for its added value was limited. We also removed the four outcome queries from the model we presented and omitted several results from the submission. Thank you for pressing us to explain both that shift in emphasis and what the R-Drop-inspired term contributes to the original model.

Your comments guided our team's experiments and revisions. We restored the original title, the four outcome queries and the full benchmark, and revised Figure 2 to show exactly where each training loss enters the model. Using the same CTG folds and five common seeds, we compared the binary backbone with the four-query model and then added repaired-view alignment, dropout risk agreement and token-level feature agreement in turn. Table 2 reports the change at each step.

  1. Continuity with the submission. We initially emphasized the single-head control because it reached 0.7299 AUROC. Its purpose was to test removal of the queries. Figure 1 now opens with the original motivations, metabolic supervision and incomplete CTG. Figure 2 shows the four SCOS queries and the raw-input student at inference. The repaired-view teacher and second dropout pass are used only during training. Table 1 reinstates all 18 comparators and the submitted model (0.7283 AUROC, 0.4226 AUPRC). We also restored the original missingness figure and identified the configuration used in the label-efficiency study. Appendix A lists the changes side by side, including the switch to unweighted binary loss.

  2. What QVD and TFC add to output agreement. R-Drop (Liang et al., 2021) couples two dropout predictions. Both passes see the same gaps, and agreement on one binary risk leaves the temporal features read by the other three queries unconstrained. QVD supplies a repaired-view teacher and weights FHR feature alignment by observed reliability. TFC aligns corresponding tokens across the two raw passes before query decoding, reusing the second pass without adding parameters. Our output term uses a symmetric positive-class discrepancy. Standard Bernoulli R-Drop also includes the negative-class term. Equations (5)-(7) specify each loss. Table 2 measures its increment within our model. A direct comparison with standard R-Drop remains open.

  3. CTG attribution and the requested controls (Q1). Across five common seeds, the full model reached 0.7329 AUROC versus 0.6956 for the binary backbone (exploratory paired difference +0.0373, 95% CI 0.0071 to 0.0657). Introducing SCOS and its metabolic targets gave the largest step, +0.0302 (nominal p=0.012, five-comparison Holm p=0.060). Adding view alignment, output agreement and TFC gave +0.0005, +0.0047 and +0.0019, respectively, with intervals spanning zero. With identical supervision, the historical query versus conventional multi-task head difference was +0.0053 (95% CI -0.0145 to 0.0243). For the same-view control you requested, repaired-view QVD minus raw/raw EMA was +0.0009 (-0.0143 to 0.0143). Weighting also differed. The earlier DPC comparison (0.7402 versus 0.7293) used ten seeds and a different checkpoint criterion (adjusted p=0.076).

  4. ECG rank targets and ordinal error (Q2). PTB-XL ranks were NORM, STTC, CD, HYP and MI. We mapped the highest-confidence code to its superclass, using the first stored SCP code for ties and excluding ineligible classes. CPSC2018 ranks were Normal, PAC/PVC, I-AVB/LBBB, STD/AF and STE. These are constructed targets. The binary-only evaluator read a severity head that had received no severity supervision. We withdraw the ordinal-MAE reductions and the associated consistency claim.

  5. ECG evaluation (Q3-Q4). Thank you for acknowledging our clarification. We trained each ECG model independently. On CPSC2018, TFC raised AUROC from 0.8507 to 0.8621, with gains at all three matched seeds (paired 95% CI for the ensemble difference 0.0045 to 0.0184, Holm p=0.004 across two ECG tasks). The PTB-XL interval includes zero. Figure 5 and Table 5 report these within-dataset comparisons.

We would appreciate your reassessment of the restored outcome-query model and reconsideration of the score in light of these comparisons. Thank you once again for your careful and patient review.

Reviewer_4jpaOpenReview ↗
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2
Confidence
1
Informativeness
2
Presentation
3
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1
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Paper summary

This paper proposes FORGE-CTG for predicting neonatal acidaemia, defined as umbilical arterial pH below 7.15, from intrapartum fetal heart-rate and uterine-contraction recordings. The SCOS module combines binary classification, nested ordinal pH targets, continuous pH regression, and prediction of available base-deficit measurements through outcome-query heads. The QVD module aligns a raw-input student with an exponential-moving-average teacher that processes a conservatively repaired FHR view; inference uses only the student. The main evaluation uses 551 CTU-UHB records and includes component ablations, synthetic missingness tests, reduced-label experiments, and signal-defined subgroup analyses. Additional experiments on PTB-XL and CPSC2018 examine ECG classification and constructed ordinal targets. The main five-seed CTG ensemble achieves an AUROC of 0.7283 and an AUPRC of 0.4226.

Critical strengths
  1. The method addresses two concrete challenges in CTG learning: loss of outcome information when continuous pH is reduced to a binary label, and unreliable signal observations. Combining complementary outcome targets with asymmetric training views is well motivated. The inference procedure is also straightforward, using the raw-input student without requiring a repaired input or an EMA teacher.

  2. The backbone-matched component ladder provides useful initial evidence for the proposed combination: AUROC increases from 0.7028 with binary supervision to 0.7200 with SCOS and 0.7342 after adding QVD. The missingness experiments complement this comparison by examining sensitivity to corrupted observations. These results make the supervision and training-view choices worth investigating beyond the main benchmark ranking.

Critical weaknesses

1). The evaluation does not sufficiently establish an attributable advantage of the proposed design. The main benchmark compares a five-seed FORGE-CTG ensemble with single-seed baselines. Appendix D also states that the evaluated GRU-D receives an all-observed mask, leaving its input-imputation mechanism inactive. Although FORGE-CTG has the highest AUROC and AUPRC point estimates, its AUROC advantages over the strongest alternatives are not statistically significant, and calibration and operating-point results do not show consistent superiority (Tables 1, 3, and 4). The backbone-matched ablations are useful, but Table 2 primarily evaluates AUROC and its sensitivity to missingness. They do not directly establish improved CTG severity prediction or probability reliability, and they do not separate the contributions of ordinal supervision, continuous pH, base deficit, and outcome queries. In particular, a conventional multi-task model with the same supervision is an important missing control. Matched-budget comparisons, targeted component controls, and direct severity and risk-quality evaluation of the ablated models are needed to substantiate the methodological contribution. The differences between the three-seed protocols producing the different full-model results in Table 2 and Section 5.2 should also be specified. 2). The severity-transfer and quality-conditioned interpretations remain insufficiently validated. Only CTU-UHB directly evaluates fetal acidaemia prediction. The ECG experiments use an imposed ordering of diagnostic categories, which the authors acknowledge is not a validated clinical severity scale. Moreover, the manuscript does not clearly explain how the binary-only comparator produces the ordinal predictions evaluated in Table 7. Consequently, the reported ordinal MAE reductions provide limited evidence for transferable severity modeling. Clean binary discrimination does not improve on either ECG dataset, and the decrease on PTB-XL is statistically significant (Tables 5 and 6). For QVD, the manuscript does not establish that the handcrafted quality indicators distinguish measurement artifacts from genuine physiological variation, or that the repaired view preserves the information needed for outcome prediction. A raw/raw EMA control and a targeted analysis of repair effects would help distinguish the proposed mechanism from ordinary consistency regularization. The synthetic missingness tests alone do not resolve this issue. The authors should also clarify whether the input window is aligned to delivery or to the end of the available recording, including how the interval between these events is handled. Together, these gaps leave the central methodological claims insufficiently supported for acceptance in the current form. Addressing them requires additional evidence or a corresponding reduction in the claimed contribution; acknowledging them as limitations does not resolve them.

Questions for authors

Q1. [Severity transfer / ECG ordinal scale]​ The ECG experiments (PTB-XL, CPSC2018) use a constructed category ordering that the authors acknowledge is not a validated clinical severity scale (Section 5.3, Limitations). Given that clean binary AUROC does not improve on either dataset, and the decrease on PTB-XL is statistically significant (Table 5, Table 6, Table 7a), what is the intended claim for transferability of the SCOS principle? If the ordinal MAE reduction is the primary evidence, how should readers interpret it given the absence of a ground-truth severity continuum? Q2. [Binary-only comparator in Table 7]​ Table 7 reports ordinal MAE for a "binary" supervision configuration. Since binary cross-entropy alone does not produce ranked predictions, please clarify: (a) how were the ordinal predictions for this comparator generated at inference time? (b) Was a threshold sweep, argmax over sigmoid outputs, or a post-hoc calibration used? Without this detail, the 23.8% and 20.9% MAE reductions in Section 5.3 are difficult to interpret. Q3. [QvD: handcrafted reliability features]​ Section 3.3 defines seven components for FHR reliability (validity, missing-run duration, flatlines, jumps, physiological range, UC saturation, local missingness). The manuscript does not establish that these indicators distinguish measurement artifacts from genuine physiological variation (e.g., a true sustained deceleration vs. electrode loss). Could the authors provide: (i) a confusion analysis or (ii) a comparison against a simpler reliability baseline (e.g., validity-fraction-only) to show that the handcrafted features carry information beyond "whether samples are missing"?

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AuthorsOpenReview ↗

Clarified Contributions and New Evidence from Matched Comparisons, Calibration, and ECG Evaluation

Your focus on attribution helped us separate three questions: the effect of DPC within a matched reference configuration, the output-head design, and the performance of the final single-head model. DPC is evaluated against the same multi-outcome reference pipeline with shared folds and records. The ten-seed and prespecified five-seed paired estimates are given above. The single-head model's AUROC is 0.7299; its cross-configuration differences from the ten-seed reference with and without DPC are -0.0102 (95% CI [-0.0265, 0.0057], p=0.210) and +0.0008 (95% CI [-0.0187, 0.0213], p=0.926). These contrasts are not used as an estimate of DPC's effect within the single-head architecture.

We added matched output-interface controls to the appendix. With the same backbone and training budget, the query-based multi-outcome configuration is +0.0053 AUROC over standard multi-task heads (95% CI [-0.0145, 0.0243], p=0.591) and +0.0117 over weighted binary BCE (95% CI [-0.0105, 0.0342], p=0.304). Removing the ordinal, continuous-pH, or base-deficit target also produces paired differences whose intervals include zero. The revised contribution therefore centers on DPC and the raw/repaired training-view design; it does not attribute a distinct gain to the query interface or auxiliary outcome heads. The benchmark now uses eight rerun baseline configurations on the same record folds and ten fixed seeds. The clinical logistic-regression comparator uses 19 fold-processed FHR/UC features. DPC has a higher AUROC point estimate than this comparator (0.7402 versus 0.7139), with paired difference +0.0259 (95% CI [-0.0067, 0.0601], p=0.108). We report this comparison with its uncertainty. The GRU-D rerun receives both the validity mask and elapsed-time input.

The revised tables label their seed protocols separately: ten seeds for the primary baseline and DPC extension, the prespecified five-seed subset for the original DPC estimate, five seeds for the head and teacher-view controls, and three seeds for the independently trained ECG experiments. The earlier three-seed and five-seed CTG full-model figures are not combined as though they came from one protocol.

For probability quality, the ten-seed full-reference DPC predictions have Brier 0.1357 and ECE 0.0233, compared with 0.1372 and 0.0248 without DPC; the paired Brier change is -0.0015 (95% CI [-0.0031, -0.0001]). At the validation-selected threshold of 0.125, held-out sensitivity is 0.905, specificity 0.381, and PPV 0.256. The paper also reports the fold-prevalence Brier reference, reliability curves, and decision-curve analysis. A separate five-seed nested calibration audit reports raw Brier 0.1389 and Platt Brier 0.1385; its paired change is -0.0004 (95% CI [-0.0027, 0.0020]), and the ECE changes from 0.0355 to 0.0469. We keep these audit values separate from the ten-seed out-of-fold diagnostics.

Q1–Q2: ECG severity interpretation and ordinal output:

The ECG experiments test DPC on independently trained diagnosis models; they do not transfer CTG weights or establish a clinical severity scale. For PTB-XL, the primary diagnosis superclass is chosen from the code with the highest confidence and ordered NORM < STTC < CD < HYP < MI. For CPSC2018, the primary classes are ordered Normal < PAC/PVC < I-AVB/LBBB < STD/AF < STE. These constructed orderings are auxiliary training targets, not validated clinical severity labels. The revised manuscript reports binary diagnosis AUROC only: PTB-XL changes by +0.0098 (95% CI [0.0032, 0.0161], Holm-adjusted p=0.002), CPSC2018 by +0.0005 (95% CI [-0.0067, 0.0076]), and Apnea-ECG by -0.0043 (95% CI [-0.0088, 0.0003]). The binary-only model has one binary-risk output and cannot produce ordinal predictions. Accordingly, ordinal MAE is not reported for it, and no threshold sweep, argmax, or post-hoc mapping is used to manufacture an ordinal score. The previous severity-transfer interpretation and ordinal-MAE comparison are absent from the revised claims.

Q3: Reliability features and teacher-view controls:

We now describe the seven signal-derived quantities as reliability inputs computed from the original trace and validity mask. They are not presented as a classifier with ground-truth artifact labels. In matched controls, repaired-view EMA with reliability weighting differs from raw/raw EMA by +0.0009 AUROC (95% CI [-0.0143, 0.0143], p=0.859) and from validity-only weighting by -0.0026 (95% CI [-0.0164, 0.0105], p=0.708). Same-input feature consistency has a paired estimate of +0.0189 (95% CI [-0.0034, 0.0406], p=0.090). These results and the seven feature definitions are now reported together in the method and ablation sections.

AuthorsOpenReview ↗

Revision_V3: Clarified Contributions and New Evidence from Matched Comparisons, Calibration, and ECG Evaluation

Thank you for identifying the comparisons needed to attribute a gain. We evaluated the complete model, then held the outcome targets fixed to test the readout, and finally compared teacher views.

  1. Attribution and ensemble budget (W1). On the same 551 CTG records and common five seeds, the pooled binary model reaches 0.6956 AUROC, SCOS reaches 0.7258 and the full model reaches 0.7329. The exploratory full-minus-binary difference is +0.0373 (paired record-bootstrap 95% CI 0.0071 to 0.0657), positive for all five individual seeds. The SCOS step combines the readout and supervision changes (+0.0302, nominal 95% CI 0.0063 to 0.0547, nominal p=0.012, Holm p=0.060 over five component contrasts). Against a conventional multi-task head trained on identical targets, the historical five-seed query advantage was +0.0053 (95% CI −0.0145 to 0.0243). Dropping the ordinal, pH or base-deficit target one at a time also gave intervals spanning zero. The evidence supports using the outcomes together. It leaves the contribution of each target and the independent value of query attention unresolved.

Table 1 retains all original baseline configurations and identifies their seed counts. We also compared the full model against eight available baseline reruns using the same five seeds. Clinical logistic regression reached 0.7185 AUROC, giving a paired difference of +0.0144 (95% CI −0.0224 to 0.0514). The strongest practical comparator therefore remains competitive. Tables 2 and 3 give the component comparisons and matched baseline reruns, respectively.

  1. Direct outcome errors, risk estimates and the three-seed protocols (Weakness 1). In the same-target controls, query and conventional heads had pH MAE of 0.078 and 0.076, ordinal MAE of 0.687 and 0.668, and standardized base-deficit MAE of 0.653 and 0.660, respectively. On the archived full-model predictions, Brier improved to 0.1396 from the pooled binary model’s 0.1436, while ten-bin ECE rose from 0.0164 to 0.0439. We report both alongside reliability and decision curves. M1’s updated AUPRC of 0.4152 comes from an additional run.

The submitted component table averaged AUROC over 15 individual fold/seed evaluations (0.7342). The separate label-fraction experiment averaged the three risks for each record first, then computed AUROC across the pooled out-of-fold records (0.7268 at full labels). Those statistics answer different questions. The revised CTG ablation uses the latter aggregation consistently with five common seeds.

  1. What transfers to ECG? (Q1). On the original PTB-XL comparison, the full model fell below the binary comparator (paired difference −0.0072, 95% CI −0.0133 to −0.0007). The revised experiment asks a narrower question about adding TFC to an existing diagnosis model, with independent training on each ECG dataset. On CPSC2018 the gain was +0.0114 AUROC (95% CI 0.0045 to 0.0184, two-dataset Holm p=0.004). On PTB-XL it was −0.0007 (−0.0054 to 0.0039). Both estimates average the three shared seeds. This evidence concerns binary diagnosis on these subsets. The imposed diagnosis order provides no clinical severity ground truth.

  2. How was the binary-only ordinal error produced? (Q2). The ECG evaluator read the continuous auxiliary head in every configuration, reversed the training-fold standardization and computed absolute error against the constructed rank. In the binary-only arm, that head had received no severity loss. No threshold sweep, argmax or post-hoc calibration converted binary probabilities to ranks. The saved predictions reproduce the original binary-arm errors of 1.237 and 1.191 to the reported precision. We withdraw the 23.8% and 20.9% reductions and mark binary-only ordinal MAE as undefined. Those percentages compared a supervised predictor with an unsupervised output of the evaluation code.

  3. Reliability features and repair (Q3). With random FHR masking on fixed test records, adding the submitted QVD to SCOS reduced the AUROC degradation slope in magnitude from 0.3126 to 0.0678. This measures sensitivity to deliberately removed samples. In the requested teacher controls, reliability-weighted repaired EMA differed from raw/raw EMA by +0.0009 AUROC (95% CI −0.0143 to 0.0143) and from the validity-only arm by −0.0026 (−0.0164 to 0.0105). The simpler arms used uniform consistency weights, so these comparisons leave the independent effect of repair open. The indicators describe waveform quality heuristically. A confusion matrix for decelerations versus artifacts would require event annotations.

  4. Timing of the input (W2). The code takes the last 30 minutes of the available trace. The local records have a reported zero interval from trace end to birth. In a historical first-stage-only analysis on 505 records, the model reached 0.5617 AUROC and clinical logistic regression 0.6259. Figure 7 and Appendix F give the eligible cohort for each timing analysis. These results support retrospective ranking near delivery.

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