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Under review as a conference paper at ICLR 2027

Reference-Aware Fairness Auditing: Separating Label Artifacts from Model Bias

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Abstract

Fairness audits compare model errors across subgroups, but rely on the assumption that evaluation labels are equally accurate for every subgroup. When label noise differs across subgroups, part of the reported disparity can come from the labels rather than the model. We show that the two can be separated when label errors are not systematically related to the model's own errors, and propose Reference-Aware Fairness Auditing (RAFA): estimate the label noise per subgroup, subtract its variance from the measured error, and report the adjusted disparity alongside the conventional one. In simulation, unequal label noise alone makes a fair model appear unfair, and RAFA removes 93% of the label-induced disparity. In controlled experiments on real lung-nodule and chest X-ray predictions, we inject label-noise and model-error disparities of known size. RAFA removes the label-induced part and preserves the known model part: adjusted and known model gaps differ by 0.003–0.004 on the nodules and below 0.002 on the X-rays, while the injected gaps reach 0.9 and 0.6. We then apply the full procedure to fetal-weight estimation from ultrasound (31,386 examinations, 17 hospitals), where the evaluation label is birth weight projected back to scan time, so its noise grows with the scan-to-delivery interval, as a growth model predicts. RAFA attributes 73% of the measured disparity to unequal label noise (bootstrap median 64%, 95% CI 37–83%). Finally, we give three explicit conditions that determine when RAFA applies and show how to check them in practice, using committee-labeled nodules and crowd counting as diagnostic examples.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
Fairness auditing, label noise, algorithmic fairness, medical imaging

Reviews

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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_nSEqOpenReview ↗
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Paper summary

This paper proposes Reference-Aware Fairness Auditing (RAFA), which aims to separate the fairness disparity caused by label noise from the actual model error. The method is based on a variance decomposition under the assumption that model errors and label noise are uncorrelated. The authors conduct synthetic noise injection experiments on LIDC-IDRI and CheXpert, and apply RAFA to fetal-weight estimation. They also discuss failure cases on crowd-counting datasets.

Critical strengths
  • The paper studies a meaningful problem. Evaluation labels are not always reliable, and different label quality across subgroups can indeed affect fairness evaluation.

  • The paper is clearly written, and the motivation is easy to understand.

  • The authors discuss the assumptions and limitations of the method, including failure cases where model errors and label noise are correlated.

Critical weaknesses

I have one major concern for this article:

The experiments do not sufficiently validate recovery against independently established ground truth.

The authors conduct controlled noise injection on LIDC-IDRI and CheXpert, but the original labels are already potentially noisy. The experiments only show that RAFA can remove artificially injected independent noise, while the actual model error against the true target remains unknown. In the fetal-weight experiment, the true target is also unavailable, making it difficult to verify whether the adjusted gap is correct. I think a more convincing evaluation should start from a task with reliable ground truth, introduce controlled subgroup-dependent label noise, and directly compare the RAFA-adjusted disparity with the true model disparity. It is also important to test correlated label and model errors, since this is likely to happen in real applications.

Other concerns:

  • The main real-world experiment divides samples according to the scan-to-delivery interval, rather than demographic or protected attributes. This is more like an analysis of measurement reliability across different conditions. Also, RAFA only considers the variance of continuous prediction errors, while common fairness metrics such as FNR and AUC are not covered. The general significance for fairness auditing is therefore limited.
Questions for authors

See the weakness.

2 comments
AuthorsOpenReview ↗

Response to Reviewer nSEq, Part 1:

Thank you for recognising the importance of label reliability in fairness evaluation and the value of reporting assumptions and failure cases. Your main concern is whether RAFA recovers the correct model disparity. We clarify below what is known in each experiment and distinguish controlled validation from the clinical application.

1. Recovery when the answer is known

In the fully synthetic simulation, the target and model errors are known by construction. This provides a direct test of recovery against known truth.

The real-data experiments then test whether RAFA can distinguish two controlled changes: increased label noise and increased model-error disparity. We vary these separately across a 7 × 7 grid. The original labels define the controlled reference, and the injected noise variance is supplied to RAFA.

The adjusted gap tracks the known controlled model gap, with mean recovery errors of 0.003–0.004 on LIDC and below 0.002 on CheXpert. These experiments therefore test both removal of added label noise and preservation of model differences.

Your distinction concerning the original labels is valid: the grids do not recover unknown errors already present in those labels. They establish recovery relative to the controlled reference, not independently measured biological truth. We will make this distinction explicit.

2. Estimating noise before correction

The paper also tests the estimation step. Appendix B estimates noise from repeated corrupted labels rather than supplying its variance. Using real LIDC predictions and equal model behaviour across four synthetic groups, the gap decreases from 0.370 to 0.094 with estimated noise, compared with 0.077 with exact noise, over 300 seeds.

Thus, the existing experiments provide three complementary tests: recovery with synthetic truth, preservation of controlled model gaps on real predictions, and correction after estimating noise. We will make these roles clearer in the main text.

An additional real-world task with independently established ground truth would strengthen validation. We do not present the fetal analysis as supplying that ground truth.

3. Correlated model and label errors

We added a sensitivity analysis that explicitly varies the assumed within-group correlation between model error and label noise, holding estimated label-noise variances fixed.

Assumed correlationEstimated fetal gap reduction
073%
0.1061%
0.2047%
0.3031%

Starting from the original fetal estimate, the interpretation that more than half the gap is explained stops holding at approximately 0.18.

This directly examines correlation rather than only changing noise magnitude. It quantifies how the clinical interpretation depends on the assumption; it is not an estimate of the actual correlation or a known-truth recovery experiment.

The crowd-counting analysis provides a separate empirical example where shared difficulty undermines the conditions for adjustment. Reporting this case is part of the intended use of RAFA: an unsupported noise estimate should not be used to explain away an observed disparity.

Part 2 presents the additional clinical robustness checks and demographic comparisons.

AuthorsOpenReview ↗

Response to Reviewer nSEq, Part 2:

This continues our response to Reviewer nSEq.

4. What supports the fetal application?

Direct scan-time weight is unavailable. We therefore tested whether the result remains when we change how noise is estimated.

We added a fetal-weight predictor by fine-tuning the UltraDINO ultrasound foundation model (Ambsdorf et al., 2025). All evaluated women were excluded from fine-tuning and model selection. We call this predictor DINO below.

The three approaches are a supervised image model, a biometry formula and a fine-tuned foundation model. We estimated noise using only Hadlock and DINO, then audited DL. DL contributed nothing to its own noise estimate.

Both comparisons below use the same 31,346 examinations with all three predictions:

Noise estimatorDL gap before → afterPoint reductionBootstrap median [95% interval]
DL–Hadlock0.237 → 0.07070%61% [32–82%]
Hadlock–DINO0.237 → 0.05079%61% [11–88%]

We used 1,000 paired bootstrap repeats, resampling whole women and refitting the noise law. The estimated reduction remains when DL is excluded, although its magnitude is uncertain.

We also reversed the roles and audited DINO using noise estimated from DL and Hadlock. Its gap decreased from 0.350 to 0.248, a 29% point reduction with a bootstrap interval of 13–38%. A substantial gap remained: the adjustment does not produce the same reduction for every predictor.

These findings support robustness to estimator choice. They do not establish independent predictor errors or replace validation against directly measured scan-time weight.

5. Connection to demographic fairness

We agree that STD groups alone are not demographic groups. Their role is to examine a source of unequal label reliability that can also affect comparisons between patient groups.

The controlled CheXpert experiments already use race and age groups. We have now also applied the fetal audit to maternal-age groups and added exploratory BMI and pixel-spacing comparisons.

The table reports the highest-minus-lowest group error SD. Brackets give 95% intervals from 500 bootstrap repeats, resampling whole women and refitting the pooled noise law.

GroupingBefore adjustmentAfter adjustment
Maternal age0.060 [0.019–0.118]0.099 [0.029–0.206]
BMI0.078 [0.039–0.121]0.145 [0.076–0.222]
Pixel spacing0.071 [0.037–0.112]0.045 [0.013–0.121]

The age analysis includes 20,877 of 31,386 examinations. Age groups have similar mean STD, 37.9–39.1 days, and therefore similar estimated noise under the pooled law. Removing equal independent noise variance can widen an SD gap because common noise compresses differences on that scale.

Pixel spacing describes acquisition rather than a demographic attribute. Its groups have different mean STD, 32.1–47.4 days, and their point-estimated gap decreases. BMI describes patient groups, but remains exploratory because covariance checks suggest differences the pooled timing law may not capture.

These examples show how the audit extends beyond timing groups and that adjustment can increase or decrease a gap. Their interpretation remains conditional on the noise model. The intervals describe each gap separately, not the before–after change.

The practical question is: how does a group comparison change when evaluation-label reliability is accounted for? The controlled experiments test recovery where the answer is known; the natural-data applications provide conditional estimates with uncertainty.

6. Scope of the fairness metrics

As already stated in our limitations, RAFA currently addresses group differences in continuous signed-error spread. FNR and AUC do not follow the same variance decomposition; extending the correction to these metrics requires separate development and remains future work.

We will also report mean signed errors alongside the variance audit so that systematic over- or underprediction remains visible.

We hope these analyses address your concerns and clarify the contribution and its scope.

Reference: Ambsdorf et al. (2025), General Methods Make Great Domain-specific Foundation Models: A Case-study on Fetal Ultrasound. https://arxiv.org/abs/2506.19552

Reviewer_BT41OpenReview ↗
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Paper summary

This paper points out that the uneven distribution of label noise across different subgroups may amplify observed fairness gaps. Furthermore, when label errors are uncorrelated with model errors, the portion attributable to labels can be distinguished from model errors. The proposed RAFA method estimates the variance of label noise for each subgroup and subtracts it from the observed error variance. The paper evaluates RAFA in three ways:

  • Simulation experiments. RAFA eliminated 93% of the disparities caused by label noise.
  • Injecting controlled noise into the predictions of LIDC-IDRI and CheXpert, and providing the variance of the injected noise to the auditor.
  • A fetal weight case study (31,386 examinations). Label noise was estimated based on the error covariance between the audited model and the Hadlock formula. RAFA attributed 73% of the disparity across “scan-to-delivery” (STD) strata to label noise (bootstrap median 64%, 95% confidence interval 37–83%).

The paper also identifies three validity conditions (R1–R3) and reports cases where these conditions are not met.

Critical strengths
  1. RAFA adjusts the evaluation only that does not require retraining. This makes the method easy to implement.
  2. This paper clearly articulates the conditions under which the method is effective and openly explains the scenarios in which noise estimation fails (CheXpert, LIDC, crowd counting), as well as the sensitivity of the results to noise estimation errors (Appendix C). This enhances the reliability of RAFA for reuse.
Critical weaknesses

W1: This paper discusses the more intuitive aspects of RAFA (Equations 3–6), but the most critical part—noise estimation—is only specifically mentioned in Section 4. Furthermore, the controlled experiments only validated the subtraction step, which corresponds to “known to the auditor here: this tests the adjustment itself, not the estimation of label noise” (L204–206). Experiments on real-world data succeeded only once (fetal weight); CheXpert, LIDC (Section 5, Appendix E), and crowd counting (Appendix F) all failed to produce accurate estimates, suggesting that the robustness and validity of RAFA require further investigation.

W2. The paper’s main results are based on assumptions that cannot be externally verified. Specifically, in hypothesis R2, the two predictors used in Equation (7) are both based on the same ultrasound examination. The common error between them leads to an overestimation of the noise estimate. The paper’s own crowd counting experiment indicates that such common errors may be the dominant factor (accounting for 73–87% of the error variance). R3. Label errors caused by backprojection may also be correlated with model error. Appendix C only altered the magnitude of the noise and did not change this correlation. However, within each stratum, the estimated noise values were as large as the adjusted model error (Table 2); therefore, the figure of 73% may lack robustness.

Minor issues.

  • This paper contrasts RAFA with methods that operate by “correcting labels or modifying training” (L048–049). This is inconsistent with the evaluation-related studies cited in the text (Fogliato et al., 2020; Adebayo et al., 2023). The text does not discuss the literature on imperfect reference standards.
  • The abstract states that the paper explains how to validate these conditions in practice, but the main text asserts that R2 and R3 cannot be tested using audit data (L161–162).
  • Only continuous errors are covered; FNR or AUC are not addressed.
  • The term “Reference” in the method name is not defined.
Questions for authors

Q1: Is it possible for both predictors in the R2 hypothesis to be wrong at the same time?

For scans performed one or two days before delivery, the label noise should be close to 0. What is Cov(e_DL, e_Hadlock) for this subset? If it is close to σ0² (σ0 = 0.351, L353), it would suggest that the estimated “noise” actually absorbs the common error of the two predictors.

Is it possible to add a third predictor for double-check? After controlling for gestational week, will the noise curve (Eq. 8) change?

Q2: In the R3 hypothesis, within each stratum, assume the correlation coefficient between model error and label error is ρ. How does the 73% figure vary with ρ? At what value of ρ does the statement “unequal label noise explains most of the measured disparity” no longer hold?

Q3: RAFA only requires second-order statistics for each group. Please disclose the number of examinations in each STD stratum, as well as Var(e_DL), Var(e_Hadlock), and Cov(e_DL, e_Hadlock). This would allow Table 2 and Eq. 8 to be reproduced without disclosing the private dataset. We also recommend adding a table describing the data characteristics: how out-of-sample predictions are made, the reference baseline for z-scores, which version of Hadlock is used, and exclusion criteria.

Q4: Aside from the “failure signal,” how can auditors verify that R1–R3 hold true so they can confidently use the adjusted figures?

How does this approach differ from the sensitivity analysis in Fogliato et al. (2020) and the correction methods for “imperfect reference standards” in medicine? Is it possible to conduct an experimental comparison?

Q5:

  • What does σ0 = 0.351 on Line 353 represent? When STD approaches 0, there should be almost no projection error.
  • The term “Reference” used in the method title "R"AFA is not defined.
  • Why is the 73% point estimate noticeably higher than the bootstrap median of 64%?
  • Since s(g) is the standard deviation of the error after removing the mean, a certain group being systematically overestimated or underestimated is not within the scope of this analysis. How should this be interpreted? (The paper assumes E[ε|g] = 0.)
  • Ethical review and data usage terms for fetal data (there is no ethics statement in the full text).

Q6: Apply this to demographic groups to see if it changes the conclusions regarding fairness; extend this to classification metrics (FNR, AUC).

2 comments
AuthorsOpenReview ↗

Response to Reviewer BT41, Part 1:

Thank you for the detailed questions. Appendix B already tests noise estimation followed by correction. We now add a third predictor, an audit excluding DL from noise estimation, correlation sensitivity analyses and demographic comparisons. Part 1 addresses W1, W2 and Q1–Q3; Part 2 addresses Q4–Q6.

W1. Validation of noise estimation

The grids test correction using known noise variance. Appendix B separately estimates noise before applying RAFA. Using real LIDC predictions, we add different Gaussian label-noise levels across four synthetic groups, estimate variance from repeated corrupted labels, and apply RAFA over 300 seeds.

The gap decreases from 0.370 to 0.094 with estimated noise, compared with 0.077 with exact noise: 74.6% versus 79.2% reduction. We will make these complementary validation steps clearer in the main text.

This validates recovery under controlled added noise, not whether the original labels are error-free. The fetal study remains our main positive natural-data application under the stated assumptions. The other cases document why candidate noise estimates should sometimes be rejected.

W2 / Q1. Shared errors, near-birth scans and a third predictor

Yes, both predictors can make errors on the same examinations. We do not infer independence from their different architectures.

Our current near-birth analysis uses STD ≤3 days, rather than the requested one–two-day window. Across 986 examinations, DL–Hadlock covariance is 0.149, with woman-level bootstrap SE 0.039, compatible with the fitted intercept variance 0.123.

This is consistent with your concern that the intercept may contain shared predictor error. It does not identify how much: less growth back-projection is needed near birth, but label uncertainty can remain. Thus, σ0=0.351\sigma_0=0.351 is the square root of the fitted zero-day intercept variance, not a direct measurement of pure projection noise.

We added a fetal-weight predictor by fine-tuning the UltraDINO ultrasound foundation model (Ambsdorf et al., 2025). All evaluated women were excluded from fine-tuning and model selection. We call it DINO below.

The three predictors use a supervised image model, a biometry formula and a fine-tuned foundation model. Covariance increased with STD for all pairs: slopes were 0.00480 for DL–Hadlock, 0.00432 for DL–DINO and 0.00608 for Hadlock–DINO.

We then estimated noise using only Hadlock and DINO and audited DL. DL contributed nothing to its own noise estimate. Both comparisons use the same 31,346 examinations:

Noise estimatorDL gap before → afterPoint reductionBootstrap median [95% interval]
DL–Hadlock0.237 → 0.07070%61% [32–82%]
Hadlock–DINO0.237 → 0.05079%61% [11–88%]

The 1,000 paired bootstrap repeats resample whole women and refit the law. The reduction remains when DL is excluded. This tests estimator robustness, not independence. The higher point estimate does not establish a better estimator: both have the same bootstrap median, and the Hadlock–DINO interval is wider.

Holding the law fixed still gives a diagnostic interval of 16–88% when group variances and timing are resampled. Group-estimation uncertainty also contributes; this diagnostic does not replace the full interval.

Within three broad scan-gestational-age groups, slopes remained positive: 0.00391, 0.00616 and 0.00451. The pattern persists among scans taken at more similar pregnancy stages. This is a partial control, not complete separation of gestational age and STD.

Q2. Model–label error correlation

Holding estimated label-noise variances fixed, we varied assumed within-group correlation:

CorrelationEstimated reduction
073%
0.0567%
0.1061%
0.1554%
0.2047%
0.3031%

The “more than half” interpretation stops holding at approximately 0.18. Separately, treating 10%, 20% or 30% of fitted covariance as shared predictor error gives 62%, 53% and 44% reductions. These scenarios start from the original estimate and vary the concerns separately; they do not estimate the actual violations.

Q3. Disclosure statistics

STD (days)ExamsWomenVar(DL)Var(Hadlock)Covariance
≤228,1391,7500.3280.4710.188
23–387,6461,6840.4220.5810.254
39–547,7281,8410.5020.7090.364
≥557,8732,1800.6550.7660.443

There are 31,386 examinations from 6,220 women; women may appear in multiple rows. We will add fine-bin statistics for reproducing the timing fit. Prediction and label-construction details continue in Part 2.

Reference: Ambsdorf et al. (2025), General Methods Make Great Domain-specific Foundation Models: A Case-study on Fetal Ultrasound. https://arxiv.org/abs/2506.19552

AuthorsOpenReview ↗

Response to Reviewer BT41, Part 2:

Q3 continued: Evaluation labels and prediction protocol

The evaluation label is recorded birth weight scaled back to scan gestational age using the sex-specific growth curves of Maršál et al. (1996). Labels and predictions use z-scores, z = (x − μ)/(0.12μ), where μ is the sex-specific expected weight at scan gestational age.

Hadlock predictions use the three-measurement formula (Hadlock et al., 1985): head circumference, abdominal circumference and femur length recorded by the clinician. Examinations without valid measurements are excluded.

DL predictions come from the held-out test set of a patient-level 85/5/10 training/validation/test split, without patient overlap. The analysis includes singleton, third-trimester examinations after 28 weeks.

Q4: How can auditors assess the assumptions? How does RAFA relate to prior work?

Audit data alone cannot establish the required absence of model–label or predictor–predictor error correlation. Our checks can reveal problems and test robustness, but passing them does not prove independence. We will revise the abstract’s wording about “validating” conditions to make this distinction clear.

In practice, we recommend reporting the original and adjusted gaps together, explaining the evidence supporting the noise estimate, and showing sensitivity to plausible violations. When the available evidence does not support noise estimation, an adjusted result should not be presented as a reliable estimate of model disparity.

We also agree that our contrast with training-time methods was too broad: evaluation-focused work already exists. Fogliato et al. (2020) study fairness evaluation under noisy labels for binary outcomes. RAFA focuses on group differences in continuous error variance, using estimates of group-specific label-noise variance. We will clarify this relationship and discuss Adebayo et al. and imperfect-reference-standard methods explicitly.

We have not run a direct experimental comparison. A meaningful comparison would need to align the target metric and the information available to each method.

Q5: Definitions, uncertainty, mean error and ethics

“Reference” means the evaluation label against which predictions are compared. The fitted zero-day term σ₀ = 0.351 is discussed in Part 1; its source cannot be identified from covariance alone.

The original 73% point estimate and 64% bootstrap median need not coincide. The gap is a nonlinear statistic: it takes square roots and selects the largest and smallest group errors. Resampling changes these values and can change which groups define the gap. We will report point estimates and intervals together.

Error SD does not capture systematic over- or underprediction. At STD ≥55 days, mean signed errors are −0.226 for DL and −0.275 for Hadlock, indicating underprediction relative to the evaluation label. We will report these alongside the variance audit. Their shared direction does not identify whether the cause is the predictors or the label.

The zero-mean label-noise assumption is distinct from requiring zero mean model error. Subtracting a group mean does not change its error variance, but the variance correction does not recover or correct systematic bias.

The fetal data were collected under a waiver of patient consent and data-protection approval, and the present secondary analysis is covered by the relevant permissions. We will add an anonymised ethics and data-access statement. Identifying approval details will be provided in the final version; individual-level data remain subject to access restrictions.

Q6: Demographic groups and other fairness metrics

We applied RAFA to maternal-age groups and added exploratory BMI and pixel-spacing comparisons. Pixel spacing describes image acquisition; it is not itself a demographic attribute.

The table reports gaps between the highest and lowest group error SD. The 95% intervals use 500 woman-level bootstrap repeats, refitting the pooled noise model each time.

GroupingGap before adjustmentGap after adjustment
Maternal age0.060 [0.019–0.118]0.099 [0.029–0.206]
Maternal BMI0.078 [0.039–0.121]0.145 [0.076–0.222]
Pixel spacing0.071 [0.037–0.112]0.045 [0.013–0.121]

The age analysis covers 20,877 of 31,386 examinations. Mean STD is similar across age groups (37.9–39.1 days), giving similar estimated noise. Removing common independent noise can widen differences on the SD scale. Pixel-spacing groups have different mean STD (32.1–47.4 days), and their estimated gap decreases.

BMI remains exploratory because its covariance pattern suggests that one pooled timing model may be incomplete. All interpretations depend on the noise assumptions. The intervals describe each gap, not the before–after change.

As already stated in the limitations, extending RAFA to FNR and AUC requires separate development. The current method audits the spread of continuous signed errors.

Reviewer_U4PmOpenReview ↗
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Paper summary

This paper investigates how group-dependent evaluation-label noise affects algorithmic fairness auditing. Standard fairness audits assume that ground-truth evaluation labels are equally reliable across demographic or clinical subgroups. When label noise varies by group, standard audits can report spurious performance disparities that stem from measurement artifacts rather than intrinsic model bias.To address this, the authors introduce Reference-Aware Fairness Auditing (RAFA), a measurement-error framework for evaluating models on continuous signed errors. Under the assumption that model error and evaluation-label noise are uncorrelated within subgroups (Cov(em,ϵ∣g)=0\text{Cov}(e_m, \epsilon \mid g) = 0), the observed error variance decomposes additively into model-error variance and label-noise variance. RAFA estimates the subgroup-specific label-noise variance σ^label2(g)\hat{\sigma}_{\text{label}}^2(g) using external knowledge, repeated measurements, or shared error covariances between distinct predictors, and subtracts it from the observed error variance.

Critical strengths
  • Most existing literature addressing group-dependent label noise focuses on modifying the training objective or re-annotating training data. In contrast, this paper frames fairness auditing itself as a classical measurement-error problem, demonstrating that subgroup evaluation disparities can be decoupled on the variance scale without altering the model or requiring retraining. This separation is consequential because it provides auditors of black-box, proprietary, or frozen clinical models with a mathematically grounded, post-hoc metric adjustment that distinguishes genuine algorithmic disparities from reference-label artifacts.
  • Rather than presenting the method solely in settings where it succeeds, the paper formalizes explicit validity conditions and pairs positive validations on clinical benchmarks with transparent negative controls. Specifically, the extensive empirical analyses of where RAFA breaks down, such as committee disagreement failing to track consensus errors on LIDC-IDRI and shared task difficulty causing models and annotators to co-fail in crowd counting, are consequential because they establish practical guardrails against misapplying variance subtraction when model and label errors are correlated.
Critical weaknesses
  • My biggest concern is that RAFA's variance subtraction strictly requires zero covariance between model error and reference-label noise within each audited subgroup (Cov(em,ϵ∣g)=0\text{Cov}(e_m, \epsilon \mid g) = 0). As the authors acknowledge, this covariance cannot be identified, estimated, or tested from the audit data alone. When positive covariance exists, which occurs naturally whenever images exhibit low resolution, artifacts, or intrinsic anatomical ambiguity that confound both annotators and machine learning models, the adjustment underestimates model error and can obscure genuine model disparity. In high-stakes algorithmic auditing, under-reporting model disparity creates a false sense of security by certifying a biased model as fair. The authors' own crowd-counting analysis vividly demonstrates how easily shared task difficulty induces positive covariance, causing the framework to misattribute real model failures to label noise.
  • All the datasets used in this paper are computer vision datasets. I am unsure whether the proposed approach is still useful for other data modalities. In my personal opinion, this paper might be more fit into a computer vision venue rather than ICLR.
Questions for authors
  1. The two-predictor noise estimator assumes zero covariance between the predictors' own errors (Cov(em,1,em,2∣g)=0\text{Cov}(e_{m,1}, e_{m,2} \mid g) = 0), arguing that the deep-learning model relies on pixel data while the Hadlock baseline is a fixed biometry formula. However, the anatomical biometric measurements used by Hadlock (head circumference, abdominal circumference, femur length) are extracted from the very same ultrasound examinations. If maternal habitus, acoustic shadowing, or poor fetal positioning degrade image quality, both sonographer caliper placements and the deep neural network's visual features could co-fail on the same examinations. As shown in the crowd-counting experiments, shared task difficulty induces positive error covariance, inflating the estimated noise and over-subtracting model error. How do you rule out shared image-quality degradation as a confounder in Cov(eDL,eHadlock∣g)\text{Cov}(e_{\text{DL}}, e_{\text{Hadlock}} \mid g) across scan-to-delivery strata? Can youprovide an empirical check (e.g., stratified by maternal BMI or image quality score) showing that predictor errors remain uncorrelated?
  2. Equation (6) applies a zero-clip (s^adj(g)=max⁡(Var(e∣g)−σ^label2(g),0)\hat{s}_{\text{adj}}(g) = \sqrt{\max(\text{Var}(e \mid g) - \hat{\sigma}_{\text{label}}^2(g), 0)}), which the authors note induces an upward bias when true model error is small. In typical fairness audits, minority demographic subgroups have substantially smaller sample sizes than majority groups, increasing the finite-sample estimation variance of both Var(e∣g)\text{Var}(e \mid g) and σ^label2(g)\hat{\sigma}_{\text{label}}^2(g). Because negative variance differences are clipped to zero, does sample size imbalance systematically inflate the adjusted error of smaller groups, potentially manufacturing a false disparity or obscuring a real one? What is the minimum recommended subgroup sample size before finite-sample clipping distortion materially affects Δadj\Delta_{\text{adj}}?
2 comments
AuthorsOpenReview ↗

Response to Reviewer U4Pm-Part1

Thank you for recognising the value of auditing imperfect labels without retraining. Our new experiments address your main concerns: the fetal DL gap still decreases when DL is excluded from noise estimation, and none of the 1,000 bootstrap repeats in this comparison required clipping. Part 1 addresses shared errors; Part 2 addresses small groups and relevance beyond vision.

1. Shared errors and the fetal noise estimate

Different methods can make mistakes on the same examinations. We added a third fetal-weight predictor by fine-tuning the UltraDINO ultrasound foundation model (Ambsdorf et al., 2025). All evaluated women were excluded from fine-tuning and model selection. We call this predictor DINO below.

The predictors use different approaches: a supervised image model, a biometry formula and a fine-tuned foundation model. Covariance increased with scan-to-delivery time for all pairs: slopes were 0.00480 for DL–Hadlock, 0.00432 for DL–DINO and 0.00608 for Hadlock–DINO. The pattern therefore extends beyond the original pair.

We then estimated noise using only Hadlock and DINO and audited DL. DL contributed nothing to its own noise estimate. Both comparisons use the same 31,346 examinations:

Noise estimatorDL gap before → afterPoint reductionBootstrap median [95% interval]
DL–Hadlock0.237 → 0.07070%61% [32–82%]
Hadlock–DINO0.237 → 0.05079%61% [11–88%]

We used 1,000 paired bootstrap repeats, resampling whole women and refitting the noise law. The reduction remains when DL is excluded, although its magnitude is uncertain. This tests estimator robustness, not independence of errors.

We also ran your suggested BMI check. Across low, middle and high BMI groups, covariance differed from the pooled timing fit by −0.048, +0.022 and +0.034. We will report this BMI-related pattern. Pixel-spacing groups showed smaller differences without a clear ordered pattern: +0.006, −0.004 and +0.003.

Within scans taken no more than seven days before birth, where less growth back-projection is needed, covariance did not increase across BMI groups: 0.165, 0.164 and 0.117, with overlapping woman-level bootstrap intervals. Pixel spacing also showed no clear ordered pattern. These checks examine measured difficulty factors; they cannot prove independence or establish how shared error changes across the full timing range.

We distinguish two shared-error concerns. Model–label error correlation affects the variance correction itself; correlation between predictors' errors affects the covariance-based noise estimate.

We tested these separately. Starting from the original 73% estimate, assuming within-group model–label error correlation of 0.10 gives a 61% reduction; it reaches 50% at approximately 0.18. Separately, assigning 10% of fitted covariance to shared predictor error gives a 62% reduction; assigning 30% gives 44%. These are sensitivity scenarios, not estimates of the actual violations.

Together, these analyses support the fetal result beyond the original predictor pair and quantify its dependence on assumptions. RAFA provides an adjusted audit under stated conditions, not a certificate that a model is fair. We will report adjusted results alongside original gaps and sensitivity analyses, so the correction does not replace or hide the observed disparity.

Reference: Ambsdorf et al. (2025), General Methods Make Great Domain-specific Foundation Models: A Case-study on Fetal Ultrasound. https://arxiv.org/abs/2506.19552

AuthorsOpenReview ↗

Response to Reviewer U4Pm-Part2

This continues our response to Reviewer U4Pm, addressing small-group estimation and relevance beyond vision.

2. Clipping, small groups and minimum sample size

None of the 1,000 fetal bootstrap repeats in the new predictor comparison required clipping. Those reductions therefore did not arise from replacing negative estimates with zero.

We also simulated four groups with equal true model error. Any estimated gap is therefore introduced by estimation. With true model SD 0.40 and the simulated noise levels, the probability of a gap above 0.10 fell from 47% at 300 observations per group to 6% at 1,000. With one small group and three groups of 5,000, it fell from 15% at 300 observations in the small group to 2% at 1,000.

Clipping raises negative variance estimates to zero, but its effect on adjusted SD and group gaps also depends on square roots and comparing group extremes. Our simulation measures the resulting gap distortion; it does not isolate systematic upward bias in the smaller group's SD.

Recovery was slower near zero true model error, so a universal minimum group size would be misleading. Reliability depends on the noise level and how close the corrected variance is to zero.

Fetal timing groups contain 7,646–8,139 examinations from 1,684–2,180 women per group. The simulation uses independent observations and known noise variance; the fetal bootstrap accounts for repeated scans by resampling whole women and refitting the estimated noise law. Sampling uncertainty remains and is reported. We will include both the simulation and the clinical bootstrap results.

3. Relevance beyond vision

The central question is whether a fairness audit can distinguish differences in model performance from differences in evaluation-label quality. This is an evaluation problem that also arises outside vision: an observed group gap can reflect both model errors and unequal label reliability.

RAFA addresses this question through a variance decomposition for continuous signed errors. It requires predictions, evaluation labels, group membership and a supported estimate of label-noise variance, without access to images or internal model representations. The vision datasets demonstrate applications, while the image-free simulation tests the underlying mechanism.

Our empirical applications are currently vision-based, and we will state that scope clearly. The contribution is a framework for interpreting group performance gaps under imperfect labels, rather than a vision-specific prediction method.

We hope these additional analyses address your concerns and clarify the contribution and its scope.

Comments on the paper

1 comment
AuthorsOpenReview ↗

General response for the main findings and revisions

We thank the reviewers for their careful feedback. Their main concerns were whether noise estimation is reliable, whether shared predictor errors could affect the fetal result, and how the method connects to demographic fairness. We address each concern in our individual replies. Here we summarise the main evidence.

1. The fetal gap reduction remains when the audited model is excluded from noise estimation.

We added a third fetal-weight predictor, fine-tuned from UltraDINO, with all evaluated women excluded from fine-tuning and model selection. We then estimated noise using only Hadlock and this third predictor, and audited the original DL model.

On the same 31,346 examinations, the original estimator reduced the DL gap by 70%, while the estimator excluding DL reduced it by 79%. Both had a bootstrap median reduction of 61%. Their 95% intervals were 32–82% and 11–88%, respectively, using 1,000 woman-level bootstrap repeats with the noise model refitted each time.

The reduction therefore persists without DL contributing to its own noise estimate. Its exact size remains uncertain, and this check does not establish independence between predictor errors.

2. We examined how shared errors would affect the interpretation.

We added checks using maternal BMI, pixel spacing, near-birth scans and gestational-age groups. We also varied the assumed correlation between model error and label noise. In the original full-cohort analysis, the estimated reduction changes from 73% at zero correlation to 61% at 0.10 and 47% at 0.20.

These results show which conclusions remain supported under the tested assumptions. We will report them alongside the original and adjusted gaps, rather than present 73% as an exact or assumption-free answer.

3. We clarified what the controlled experiments validate.

The synthetic simulation has known ground truth. The controlled real-data grids test whether RAFA removes added label noise while preserving known model differences relative to the original labels. Appendix B also tests estimating noise from repeated corrupted labels before adjustment: the gap falls from 0.370 to 0.094, compared with 0.077 using exact noise.

These experiments validate different parts of the method. They do not establish the unknown scan-time fetal weight, and we will make that distinction clearer.

4. We extended the group comparisons and checked finite-sample behaviour.

We added maternal-age and exploratory BMI comparisons, alongside a pixel-spacing acquisition comparison. The adjustment can increase or decrease the measured gap; it does not automatically make group performance appear more equal. These interpretations remain conditional on the noise model.

We also tested unequal group sizes in simulation and accounted for repeated examinations through woman-level resampling. No clipping occurred in the 1,000 bootstrap repeats of the DL estimator comparison, so those reductions were not caused by replacing negative variance estimates with zero.

We will incorporate these analyses, the requested data summaries, mean signed errors, clearer related-work discussion and an anonymised ethics statement into the revised manuscript.

RAFA provides an adjusted audit under stated conditions, not a certificate that a model is fair. Its contribution is to make the role of evaluation-label reliability explicit when interpreting group performance differences.

We hope these analyses and the planned revision address the reviewers’ concerns and clarify the contribution.

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

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