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Under review as a conference paper at ICLR 2027

Low Correlation Is Not Separation: What Gradient Isolation Delivers for Epistemic and Aleatoric Uncertainty

Abstract

Uncertainty estimates should distinguish prediction error that can be reduced through learning from ambiguity in the available labels. Predictive decompositions do not generally identify these two sources, and their estimates can be strongly correlated. We study structural separation in supervised latent variable models, using distinct parameter heads and supervision signals for error-related and ambiguity-related uncertainty, instantiated as a Credal Concept Bottleneck Model. We state sufficient conditions for isolating the uncertainty-head gradients, verify them with a loss-by-parameter audit of a trained model, and distinguish this property from output decorrelation and semantic validity. We evaluate these properties on five benchmarks spanning annotator and corpus supervision. Low EU–AU correlation is common, but it is informative only on CEBaB, where both heads track their targets: without a decorrelation penalty the scores are weakly correlated ( and for two encoders), and the error-related score matches or exceeds the mutual information of a three-member ensemble (AUROC ) from a single model. On HateXplain and GoEmotions the ambiguity head collapses to a constant, and on two QA benchmarks the error-related score is at chance. On every benchmark, the model's own maximum class probability detects errors better. Removing ambiguity supervision collapses the ambiguity head, and an explicit decorrelation penalty collapses one head in every seed. Gradient isolation and low correlation are therefore achievable, but neither establishes a useful decomposition; we identify the target properties that decide the outcome and propose what an evaluation of separately supervised uncertainty must

Primary area:
probabilistic methods (Bayesian methods, variational inference, sampling, UQ, etc.)
Keywords:
Predictive Uncertainty, Epistemic, Credal Sets

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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_RrwLOpenReview ↗
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Paper summary

The paper investigates the relationship between estimated aleatoric and epistemic uncertainty proxies in an architecture where the two are learned separately. It investigates the setting with a concept-bottleneck model, where the relevant uncertainties are given direct supervision targets. The authors provide an empirical study of how these learned uncertainties correlate to each other as well as to the model's errors. The paper includes ablation studies on various possible design choices.

Critical strengths

The high-level idea investigated that aleatoric and epistemic uncertainty should in principle not necessarily be correlated is an intuitive and interesting topic of study.

Within the framework considered, the paper does a good job on reporting the empirical evaluations, clearly addressing which experiments provide evidence for which claims and the limitations involved.

Critical weaknesses

The paper is framed as an investigation into the relationship between aleatoric and epistemic uncertainty estimates. However, a critical concern is that the quantity that the authors use as the epistemic head's regression target eje_j is more closely related to total error or uncertainty than epistemic uncertainty. The authors point out this limitation (lines 204-205), but it is in my view a critical mismatch of what is being presented as investigated. The notation (EU, σepi\sigma_\text{epi} etc.) strongly suggests that the authors are indeed presenting the findings as concerning to what is commonly understood as epistemic uncertainty. The lack of a clear regression target is part of what makes epistemic uncertainty estimation challenging, and using residual error as a proxy for this does not faithfully capture the key behavior of epistemic uncertainty. This choice is not sufficiently motivated and it does not appear sound to me to characterise this as an "epistemic head" regression target.

Following on from the point above, it becomes unclear what the interesting scientific results from the presented experiments are. The relationship between error and EU (which the authors claim "carries signal" in the abstract) is entire given the regression objective is directly derived from error. The authors argue that their results suggest that low correlation does not imply a faithful semantic representation of aleatoric and epistemic uncertainty. Unfortunately, this negative result is only demonstrated for the specific setting and definitions addressed in this particular paper, which as argued above is of questionable relevance to the broader research community, and with no quantitative comparison with other methods that investigate the relationship/correlation between aleatoric and epistemic uncertainty.

Questions for authors

Clarification requests:

  • Is there further formal justification for interpreting the error regression target as appropriate for an "epistemic"?
  • If I am understanding the results in Table 1 correctly, I would expect AU and EU to be positively correlated (assuming no decorrelation penalty). This is because under a well-fitted regression, higher EU (as defined in the paper, i.e. through regressing against residual error) would usually be expected to be present in those samples where labels are ambiguous. However, the correlations here are low or negative. Is my understanding correct and why is this the case?

Further questions/future work:

  • Why is AU nearly constant with no supervision? If it is the output of an untrained NN head I would still expect there to be variation in the output due to changing input.
5 comments
AuthorsOpenReview ↗

Response to reviewer RrWL

We thank the reviewer for their comments. We address their queries below. Appendix E establishes the distinction between the residual target and ideal epistemic uncertainty. We make that distinction explicit here, then use the saved-checkpoint diagnostics to answer the questions about score correlation and near-constant outputs.

Why use the term epistemic? The absolute residual is not a justified target for the ideal epistemic quantity in Equation 1. For a binary label Y∼Bernoulli⁡(q)Y \sim \operatorname{Bernoulli}(q) and a correct predictor p=qp = q,

\qquad D_{\mathrm{KL}}\!\left(\operatorname{Bernoulli}(q) \,\|\, \operatorname{Bernoulli}(q)\right) = 0.$$ The residual therefore retains a component due to label uncertainty. Our clipped and regularized regression does not remove this component. We use “residual-based score” for the learned output and reserve the epistemic interpretation for the ideal quantity or an explicitly tested hypothesis. **Scientific scope and comparisons.** We study what separate supervision and direct gradient isolation establish about the learned scores. Proposition 4.1 concerns direct loss derivatives; it does not imply statistical independence or semantic validity. On CEBaB, the two scores correlate weakly without a decorrelation penalty ($-0.14$ and $0.00$), while the ambiguity scores correlate with annotation entropy at $0.22$ and $0.24$ (ambiguity output and entropy both averaged over annotated aspects only; the naive all-aspect values are $0.03$ and $0.06$, and the concept-level binary-labelled value is $0.31/0.31$ — we will report the mask with each number). The residual score's task-error AUROC is $0.72$, below confidence at $0.78$ and $0.79$. Fitting concept residuals does not guarantee alignment with held-out task errors. The observed alignment measures downstream utility; we do not treat it as evidence of a purely epistemic signal. The additional ensemble analysis reports correlations of $0.73$ and $0.52$ between mutual information and expected entropy. Expected entropy correlates with task annotation entropy at $0.44$ and $0.47$. These results compare conventional uncertainty components and require us to interpret dependence alongside the target and evaluation task. They do not establish why the residual-based construction gives different correlations, and the different ambiguity targets preclude a direct ranking of the two methods' alignment coefficients. **Why are residual and ambiguity scores not positively correlated?** Your expectation holds in the idealized setting of Appendix E. If $p(x) = q(x)$, the population squared-loss regressor of the raw absolute residual outputs $2q(x)(1 - q(x))$. For distinct $q$ values in $(0, 1/2)$, this quantity and Bernoulli entropy have identical rankings. Their Spearman correlation is therefore one. We computed the requested decomposition on a common held-out mask, per concept, before and after aggregation, and separately for binary-labelled and annotated-nonbinary aspects. The decomposition identifies the principal empirical differences: * **Binary-labelled concepts ($n = 3,058$ concept-annotation pairs):** The actual transformed residual target correlates with annotation entropy at only $0.15$ (DistilBERT) and $0.18$ (RoBERTa-base) — the targets themselves are far from rank-equivalent. The scale output aligns with its own target at $0.69/0.72$ ($\text{RMSE } 0.50/0.41$); the ambiguity output correlates with entropy at $0.31/0.31$ pooled ($0.33/0.35$ review-level); and the two learned outputs correlate with each other at $0.09/0.22$ pooled. * **Annotated-nonbinary aspects (unknown majority, $n = 1,876$):** The auxiliary loss trains the ambiguity head toward the constant target $1$ ($\text{RMSE } 0.42/0.46$) and its entropy correlation inverts to $-0.14/-0.16$ ($-0.13/-0.13$ review-level). * **Per-aspect (binary):** Food $0.31$, service $0.21$, ambiance $0.33$, and noise $0.26$ for DistilBERT; and $0.31/0.17/0.35/0.31$ for RoBERTa-base. The observed low score correlations therefore arise from three identifiable sources — target non-equivalence ($\rho(\text{target}, H) \approx 0.15\text{–}0.18$), differing supervision masks (the constant-$1$ pull on unknown-majority aspects, which inverts the correlation), and partial target fitting — rather than from successful separation; and the Bernoulli example's $\rho = 1$ applies to neither actual target. This decomposition replaces the single pooled correlation in our response; we will incorporate it into the manuscript.

Why is the ambiguity output nearly constant without supervision? An untrained neural head can vary with its input. Our CEBaB ablation removes both direct ambiguity-supervision terms and measures the resulting dispersion. Figure 2 and Appendix H show that the score's standard deviation is below 10−310^{-3} from the first recorded epoch: the first-epoch validation dispersions are 6.9⋅10−46.9 \cdot 10^{-4}, 7.5⋅10−47.5 \cdot 10^{-4}, and 4.2⋅10−44.2 \cdot 10^{-4} across the three seeds (versus 9.7⋅10−29.7 \cdot 10^{-2} at epoch 1 for the supervised configuration), with selected-checkpoint test dispersions of 2.5⋅10−42.5 \cdot 10^{-4}, 5.8⋅10−55.8 \cdot 10^{-5}, and 1.8⋅10−41.8 \cdot 10^{-4}, respectively, which we recomputed from the saved prediction arrays; the logged training and validation losses are finite. We also audited the saved ablation checkpoints to examine the candidate causes:

  1. The ambiguity MLP never trained: In every ablation run, every layer's weights remain inside their default-initialization support (0.0%0.0\% of weights exceed the Kaiming-uniform init bound in any layer or seed; the layer RMS values only shrink, from 0.036/0.051/0.0720.036/0.051/0.072 at initialization to 0.020–0.0590.020\text{–}0.059), which is the signature of weight decay on parameters no loss reaches.
  2. Bias drift via weight decay: The learnable offset b=logit⁡(0.3)≈−0.847b = \operatorname{logit}(0.3) \approx -0.847 drifts to the same value on all four concepts (−0.693-0.693 at the seed-4242 checkpoint, −0.462-0.462 at the seed-123123 checkpoint, −0.673-0.673 at the seed-20242024 checkpoint), with displacement proportional to the selected epoch (0.15/0.39/0.170.15/0.39/0.17) — the exact behaviour of the decoupled weight decay in the AdamW optimizer (10−210^{-2}), since removing the ambiguity losses cuts the gradient paths to this bias.
  3. Input projection movement: The input projection supplying the head is the only component that demonstrably moves beyond initialization (up to 6.9×6.9\times the init bound; 5.6–21.3%5.6\text{–}21.3\% of its weights outside the init support), consistent with the orthogonality penalty, which our gradient audit shows is the largest-magnitude term reaching that projection.

The supervised checkpoints show the contrast: 34–59%34\text{–}59\% of MLP weights and 77%77\% of projection weights move beyond init bounds. No initialization-state checkpoint exists (each checkpoint stores only the selected epoch's parameters and validation metrics), so we cannot recover pre-update dispersion from these artifacts; but the forensics above narrow the open question to the state of a head whose nonlinear weights demonstrably never moved beyond their initialization distribution. We restrict the initialization claim to the recorded observations. A matched rerun with a step-0 dump would measure the pre-training state directly.

We use 10−310^{-3} as an operational near-constancy threshold. A nonconstant score can have a mathematically defined rank correlation even below this threshold; withholding it does not prove that its ranking is uninformative. (For the three matched HateXplain runs the audit-only rank correlations are −0.02-0.02, 0.010.01, and −0.03-0.03, consistent with a constant output rather than an informative ranking.)

Dear Reviewer as the author-reviewer discussion period ends soon we kindly request that you read the rebuttal and confirm whether your concerns are addressed. We remain committed to answering any further questions you have.

Reviewer_mXTWOpenReview ↗
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Paper summary

This paper studys whether low correlations of AU and EU means separation of the uncertainty scors, throught a gradient isolation trick, which introduces separate uncertainty heads in a concept bottleneck model, supervised by signals like prediction residuals and annotation entropy. Experiments across five benchmarks evaluate output correlation, target alignment, and error detection. The authors conclude that low correlation and gradient isolation alone do not establish semantic uncertainty separation.

Critical strengths

None

Critical weaknesses
  1. The model design and study cannot confirm EU/AU separation. The so called AU and EU are not the well known AU and EU terms in UQ literature. The paper just studies two numbers they got from the specific design, which is very close to the cited [CREDENCE] paper. This limits to the novelty of the paper.

By the authors' own Appendix E, the EU target (absolute residual) contains an aleatoric component which is even rank-equivalent to Bernoulli entropy. And the [CREDENCE] even has a better EU signals than this paper. It is hard to understand why the author replaced that ensemble-based signal to the prediction residual.

In addition, the proposed construction contributes nothing beyond plain auxiliary heads. With a frozen encoder, any two heads with disjoint parameters satisfy Proposition 4.1. The credal radius is used in neither training nor evaluation. Every reported phenomenon traces to the supervision or loss design. The study therefore measures how well two proxy regressors fit their targets, not whether uncertainty sources are separated, which has no relationship true AU and EU.

[CREDENCE] Credal concept bottleneck models for epistemic-aleatoric uncertainty decomposition. Tanmoy Mukherjee, Thomas Bailleux, Pierre Marquis, and Zied Bouraoui.

  1. The experiments are construction-specific and uncontrolled. Most failures come from the paper's own implementation or configuration, for example, a field-name bug that deactivated the entropy loss on HateXplain, no entropy target on GoEmotions, QA runs outside the paper's own setting, and a decorrelation collapse that the authors suspect is numerical. These failures do not support the general conclusions implied by the title.

Moreover, there are no controlled interventions to confirm the learned AU and EU really have semantic meaning as expected from their definiations. The paper even did not compare with bayesian uncertainties from ensemble or LLLA. It just studies their own setting and design but with limited experiments and findings.

Even if we considered this paper as a negative-result paper, it lacks a lot of key experiments. The paper learned wrong signlas and evalute on them, then showed negative results.

Questions for authors

The paper has significant problems from model design, to evaluations and to conclusions, which are hard to address through a rebuttal process. I recommend the authors refine the methods, re-design the experiments to get more valuable findings, and consider another venue.

5 comments
AuthorsOpenReview ↗

Response to Reviewer mXTW

We thank the reviewer for their comments. Our experiments characterize residual- and entropy-supervised scores and their gradient dependencies. They do not validate the residual score as epistemic uncertainty or turn implementation failures into a general limitation of uncertainty estimation. We state that scope explicitly below and will align the manuscript’s terminology with it.

Interpretation of the learned scores. Equation 1 distinguishes the ideal quantities from the learned scores, but the notation UepiU_{\mathrm{epi}} and the expression “epistemic head” can suggest a stronger interpretation than we establish. Appendix E shows that the expected absolute residual can remain positive even when the predictor equals the true conditional distribution. We therefore call this output a residual-based score. Its association with held-out errors is evidence of predictive utility, not of an epistemic interpretation.

Residual regression supplies an explicit observable target, allowing us to measure its relation to ambiguity. It does not improve the semantic justification of ensemble disagreement. CREDENCE already uses ensemble-derived concept intervals and a separately supervised ambiguity output; separate ambiguity supervision is not a novelty of our work. Our study examines direct gradient dependencies and the behaviour of residual- and entropy-supervised scores. We do not claim an advantage over CREDENCE without a matched comparison. A claim that the scale parameterization adds value beyond its targets and loss terms requires a matched auxiliary-head comparison.

Gradient isolation and the credal representation. Proposition 4.1 specifies the direct gradient dependencies of the computation graph under its stated assumptions. A frozen encoder and disjoint head parameters alone do not exclude losses that couple the heads; the proposition also rules out those paths. The proposition identifies isolated and coupled gradient paths; it does not guarantee semantic separation. Table 3 verifies the relevant derivatives for the audited checkpoint: each loss term reaches only its own head and trainable projection, while the orthogonality term reaches all three projections, and at \lambda_d=5 the decorrelation penalty reaches both uncertainty pathways with gradient norms that dominate their supervised terms (head-level RMS 2.0 and 2.1 versus 0.8 and 0.9 without the penalty). Detached targets evolve with the concept predictor. Likewise, the unused credal radius cannot explain the reported results or establish an advantage over ordinary auxiliary heads.

What the existing evidence establishes. On CEBaB, without decorrelation, the residual and ambiguity scores have correlations of −0.14 and 0.00 for DistilBERT and RoBERTa-base (per-seed −0.12/−0.13/−0.18 and −0.01/+0.03/−0.00). The ambiguity scores correlate with annotation entropy at 0.22 and 0.24 — we average both the ambiguity output and entropy over annotated aspects only (naive all-aspect averaging gives 0.03/0.06; the concept-level binary-labelled value is 0.31/0.31; we will state the mask wherever the number appears). On the fixed-label evaluation (n=1,689), the residual scores detect task errors with AUROC 0.72 (MaxProb 0.78/0.79). Both outputs carry measurable signals. Gradient isolation and the reported correlations do not establish their uncertainty interpretation; the evidence supports neither semantic identification nor a proof that such identification is impossible.

We extend the comparison to conventional uncertainty components using the three saved per-seed prediction exports and the protocol in our response to Reviewer 7ZTk. On the same 1,689 CEBaB reviews, mutual information and expected entropy have correlations of 0.73 and 0.52. Expected entropy correlates with task annotation entropy at 0.44 and 0.47; mutual-information AUROC is 0.72 and 0.66, compared with 0.78 and 0.79 for ensemble MaxProb; mutual information correlates with task error at 0.31 and 0.22. We also computed the MC-dropout diagnostics requested under E2 from existing prediction samples (full table in the response to Reviewer 7ZTk). These results illustrate distinct information from the different diagnostics. They are descriptive comparisons of saved outputs, not a controlled intervention and not a comparison with CREDENCE. Table 9 also includes MC-dropout error-detection results; we do not report a last-layer Laplace comparison.

Implementation failures and generality. Our audit of the exact evaluated code resolves the HateXplain account (response to Reviewer 7ZTk). At the commit that produced the Table-1 runs, a batch-key mismatch silently disabled the entropy loss while the unknown→1 pull remained active. The code verifies this supervision failure; we will correct Appendix K to describe it precisely. The earlier 50-epoch campaign (seed 42, different lineage, supervision verified active from its training logs) gives ambiguity–entropy correlations of 0.194 for the CBM and 0.216 for the SENN-based variant; these are the only existing HateXplain runs with active entropy supervision. The matched 100-epoch runs at seeds {42, 123, 2024} replicate the collapse under the unfixed configuration and do not by themselves establish the effectiveness of the supervision (As specified in the response to Reviewer 7ZTk). GoEmotions supplies no entropy target (and its ambiguity output is constant), and QA uses a different objective; we will distinguish these settings from the main CEBaB evidence. The SENN results are one-seed and five-class and retain the same proxy design; we will present them as a preliminary scope check only.

The decorrelation ablation produces a nearly constant uncertainty head in every tested seed at \lambda_d=5: the residual-based head in two seeds (SD 6·10^{-8}) and the ambiguity head in one (SD 3·10^{-8}). Both heads have first-epoch dispersions of 0.03–0.07 in these runs, so the collapse occurs during training rather than at initialization. Exact Pearson correlation is invariant to nonzero rescaling, so shrinking a score does not inherently reduce its squared correlation. We distinguish this property from the behaviour of the stabilized implementation. We verified that the implementation computes the batch-level squared sample correlation of the two mean scores on the clamped raw outputs, adds \epsilon=1e-8 to the standard-deviation product, and applies neither a penalty-value clamp nor a zero-variance guard — under a constant head the penalty's numerator is zero and the term silently vanishes. The ablation launcher implements the text-dataset penalty through a patch outside the pinned model code. All three \lambda_d=5 runs record non-finite validation loss in every epoch and finite training loss. The launcher therefore selects checkpoints by validation task accuracy alone.

Completed data-availability and sensitivity experiments. Saved five-class CEBaB checkpoints already cover training fractions 25%, 50%, 75%, and 100% (seed 42, frozen DistilBERT, 50 epochs). Task accuracy rises from 50.8% to 55.9%, 57.9%, and 58.6%, while residual-error AUROC is 0.463, 0.508, 0.495, and 0.511. The mean residual score is −1.191, −1.241, −1.219, and −1.205, respectively: it does not decrease monotonically with increasing training data. Ambiguity–entropy correlation rises from 0.255 to 0.330, 0.345, and 0.361 under this campaign's original all-aspect aggregation. These completed results partly address data availability, but one seed and proxy targets cannot identify the Equation-1 quantities.

The saved sensitivity campaigns additionally cover ambiguity-loss weights {0.5,1,2,4,8}, ambiguity priors {0.02,0.05,0.1,0.2,0.3}, and KL weights {0.001,0.01,0.1,1}. Across the KL sweep, residual dispersion falls from 0.827 to 0.566, 0.281, and 0.069; residual-error AUROC remains 0.500, 0.508, 0.513, and 0.500. We include every individual run below, including the matrix and full-data reference configurations. These existing sweeps concern other hyperparameters and do not supply the missing decorrelation-weight/stabilization sweep.

Controlled interventions. The present experiments do not identify either score with the ideal quantities under independent changes in reducible uncertainty and label ambiguity. The completed data-fraction experiments above address only data availability under the same proxy-supervision regime. Applying the diagnostics to an ensemble or adding SENN does not answer this question. We restrict our empirical conclusions to the tested constructions and supervision regimes.

Dear Reviewer as the author-reviewer discussion period ends soon we kindly request that you read the rebuttal and confirm whether your concerns are addressed. We remain committed to answering any further questions you have.

Reviewer_7ZTkOpenReview ↗
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Paper summary

The paper studies uncertainty quantification in a specific supervised latent variable model setting using a Concept Bottleneck Model. They use different proxies for training the uncertainty heads, using concept residual for epistemic and annotation entropy for aleatoric heads. They isolate gradients for the heads and keep the latent inputs to each head orthogonal, they also design a loss to decorrelate epistemic and aleatoric uncertainty scores. Spearman correlation between the uncertainty scores, and between them and their respective proxies are reported across different supervision regime benchmarks alongside accuracy and AUROC. Even in the cases where epistemic and aleatoric scores are close to decorrelated, they find the scores often being poor indicators of true uncertainty. They use these results to motivate an evaluation protocol for uncertainty scores which involves first checking variance across both the scores, following which if they track their own proxy target, and only then report their correlation alongside comparison against the baselines.

Critical strengths

The paper is presented and structured well, with theoretical grounding of the included formulation, The paper cleverly designs experiments to test usefulness and disentanglement of the uncertainty estimates, provided the learning objective and architecture that actively tries to separate their own subnetworks, and the concept-task subnetwork. They also clearly list and formulate the limitations of their approach and what could and could not be isolated. With this they’re able to demonstrate in their scope of experiments that even with these measures in place, it is not necessary that the uncertainties obtained will be useful or accurate and therefore show the need for a proper evaluation protocol

Critical weaknesses

The experiments are limited in scope to just one particular kind of setting (CBMs with approximate uncertainty heads), while they demonstrate the need for proper evaluation of such approximations and probably were also very important in the experiment design, it still remains a specific architecture. Even within the five chosen benchmarks for this specific setting, only CEBaB actually tests the concept as intended. HateXplain was stated to have ambiguity loss inactive because of a field name mismatch, and GoEmotions had no target to begin with, so they both exclusively used LunkL_{unk} instead to regress the entropy target, which leads it to be constant on everything, this actively works against the correlation study the paper is going for. The QA datasets lack concepts in general, which leads to using a different epistemic target which utilizes the task error as a proxy alongside σale\sigma_{ale}, they do not mathematically specify this target and it is different from the rest of the experiment, they also just test it with the decorrelation regularization RdecorrR_{decorr} involved, which already displayed σepi,j\sigma_{epi,j} collapsing to a constant in CEBaB and this leads the estimates to be effectively meaningless in this case, it should have included results for these without the regularization. All this shows a lack of rigorous experiments for all the included benchmarks. The paper while including benchmarks based on MC-Dropout and Deep Ensemble in Table 9, fails to use them within the evaluation framework of the paper itself, no uncertainty correlation score (ρ(EU,AU)\rho(EU, AU)), nor their correlations with the intended evaluation proxies (ρ(EU,Err)\rho(EU, Err), and ρ(AU,H)\rho(AU, H)) is provided. It would be helpful The epistemic head is trained on regressing concept level residuals, while evaluated on task level error detection AUROC. Structurally the task head will always have an advantage over these scores, and they might not be the most accurate representative of the epistemic uncertainty. There are also some minor mistakes like Table 5 being referenced as Appendix 5 in section 5.2 which should be corrected.

Questions for authors

Since you mention HateXplain dataset has a field name mismatch, how does the benchmark perform when said mismatch is corrected, could you include those metrics? How do MC-Dropout and Deep Ensemble models perform under the evaluation scheme you propose, what are the correlation metrics you attain with them? Could you explicitly include the loss for epistemic target in the QA benchmarks as the

architecture differs from what the paper has included, and the paper leaves the error proxy unspecified

5 comments
AuthorsOpenReview ↗

Response to Reviewer 7ZTk

Thank you for the careful assessment and the concrete suggestions. We agree that the construction needs to be evaluated with verified supervision, explicit targets, and consistent comparisons. We address the scope of the experiments and each requested diagnostic below.

Scope and the HateXplain results. CEBaB is the principal setting in which we evaluate per-concept ambiguity supervision. GoEmotions has no annotation-entropy target in our construction, and the QA experiments use an instance-level objective. We will make these differences more prominent and avoid presenting all five benchmarks as equivalent tests of the SLVM setting.

Additional runs compare the CBM with a SENN-based variant, without a decorrelation penalty. The following results use seed 42 and a configuration distinct from Table 1:

ArchitectureDatasetTask accuracy (%)Concept accuracy (%)Residual–ambiguity correlationResidual–error correlationAmbiguity–entropy correlation
CBMCEBaB58.685.20.1750.0180.361
CBMHateXplain57.589.8−0.0590.1430.194
CBMGoEmotions40.495.0−0.139−0.046n.a.
SENNCEBaB53.186.40.222−0.0160.349
SENNHateXplain61.089.6−0.0350.1660.216
SENNGoEmotions35.094.2−0.0740.197n.a.

These runs provide a preliminary comparison across two architectures while retaining the same proxy targets. They do not establish generality across architectures, and their accuracies should not be compared directly with Table 1. In particular, the additional HateXplain runs show positive ambiguity–entropy associations, but do not by themselves explain the near-constant outputs in the original runs. A configuration without active entropy supervision cannot support a conclusion about the effectiveness of that supervision.

There was a keyword mismatch which silently disabled the entropy-regression loss on every batch, while the unknown→1 auxiliary pull remained active. This is the reason near-constant ambiguity outputs in the Table-1 runs, with one correction to Appendix K's wording: the raw HateXplain JSON fields were always read correctly, and the entropy was always computed correctly; the failure is a batch-key mismatch between loader output and trainer consumption. A simple one-character strip fix repairs this that produced the earlier matrix campaign above — which is why those runs have an active ambiguity loss (nonzero from the first step; ρ(amb, H) rises to 0.194/0.216 during training) and a varying ambiguity output (SD 0.087/0.095). The statement that "the loader and trainer use the same key" is true of that lineage, not of the Table-1 code.

Matched HateXplain runs, seeds {42, 123, 2024}. Matched runs with the original task, splits (15,383/1,922/1,924), and 100-epoch configuration exist for all three seeds and are inserted below. We report them with an essential caveat: they were trained on the Table-1 code path, i.e. before the supervision fix, so they are matched seed replications of the failure rather than corrected runs. They establish that the collapse is seed-stable and is not explained by seed variation:

SeedAcc (%)SD(residual)SD(ambiguity)ρ(resid, err)AUROC(resid)AUROC(MaxProb)
4257.90.2101.7·10⁻⁵0.1780.6040.671
12357.70.2086.9·10⁻⁶0.2100.6220.676
202457.10.2315.8·10⁻⁵0.1680.5980.698

(\rho(ambiguity, H) is retained for audit only: the output is below the 10^{-3} reporting threshold in every seed; per-epoch logs show the ambiguity output begins with SD 1.8–3.1·10^{-3} at the first recorded epoch and decays monotonically to ≈10^{-5}.) We ran supervision-fixed HateXplain, seeds {42,123,2024}, 100 epochs, same splits .Until then, the only HateXplain runs with verified-active entropy supervision are the matrix-campaign rows above, and a configuration without active entropy supervision cannot support a conclusion about the effectiveness of that supervision.

Ensembles and MC dropout under the same diagnostics. Table 9 already reports error-detection AUROC for both methods; the requested extensions are now computed from the same saved per-seed test-set prediction exports (three seeds, n=1,689 CEBaB reviews; Spearman correlations with average ranks for ties; dispersions are population SDs across examples; each AUROC ranks that predictor's own errors). For member predictions pmp_m and their mean pˉ\bar p: mutual information H(pˉ)−1M∑mH(pm)H(\bar p)-\frac{1}{M}\sum_m H(p_m) and expected entropy 1M∑mH(pm)\frac{1}{M}\sum_m H(p_m); MC dropout uses 10 passes with the frozen encoder deterministic and dropout only in the trainable heads. Task annotation entropy is the three-class worker-vote entropy (ratings merged 1–2/3/4–5, ÷log 3); aspect entropy is the negative/unknown/positive vote entropy (÷log 3) averaged over annotated aspects only.

DiagnosticDistilBERTRoBERTa-base
SD(mutual information) / SD(expected entropy)0.030 / 0.2800.016 / 0.291
Correlation of expected entropy with task annotation entropy0.440.47
Correlation of expected entropy with aspect annotation entropy0.020.00
Correlation of mutual information with expected entropy0.730.52
Correlation of mutual information with task error0.310.22
Error-detection AUROC: mutual information / MaxProb0.72 / 0.780.66 / 0.79

MC dropout, mean ± seed-SD over the three seeds:

DiagnosticDistilBERTRoBERTa-base
SD(MI) / SD(expected entropy)0.008±0.004 / 0.286±0.0020.002±0.001 / 0.296±0.013
ρ(MI, expected entropy)0.69±0.110.51±0.08
ρ(MI, task error)0.31±0.040.26±0.05
ρ(expected entropy, task H) / ρ(expected entropy, aspect H)0.43 / 0.020.46 / 0.00
Error-detection AUROC: MI / MaxProb0.72±0.03 / 0.77±0.010.68±0.04 / 0.79±0.01

Both scores vary, and expected entropy is associated with disagreement at the task level. Its weak association with aspect entropy is not evidence that it fails to represent task-level ambiguity: these are different targets. Mutual information detects task errors less effectively than ensemble MaxProb in these results. The comparison shows why score dependence, target alignment, and downstream utility need separate evaluation; high correlation alone does not establish failure, just as low correlation does not establish separation.

QA target and decorrelation. We agree that the implemented QA target must be specified mathematically. We have verified the implementation against the exact code that produced the QA runs. Let r(a∣x)r(a\mid x) denote the reference distribution used in QA training and samb(x)s_{\mathrm{amb}}(x) the ambiguity output. The implemented target is

\qquad t(x)=0.05+1.45\,\operatorname{sigmoid}\!\left(3\left[e(x)-\operatorname{sg}(s_{\mathrm{amb}}(x))\right]\right),$$ with residual-head loss $\operatorname{MSE}(s_{\mathrm{res}},\operatorname{sg}(t))$ — confirmed exactly, including both coefficients (0.05, 1.45), the scale 3, and exactly two gradient stops ($s_{\mathrm{amb}}$ and $t$), with the clamp to $[0.05,1.5]$ zeroing gradients outside that range. $r$ is **not** a one-hot slot label: it is the corpus answer distribution (the renormalized answer-frequency field shipped with the MAQA*/AmbigQA* datasets); examples without a usable distribution are dropped. Scores are parameterized as softplus outputs clamped to $[0.05,1.5]$ (sigmoid appears only inside the target); entropy units are nats. The complete objective, with weights, is $$1.0\,L_{\mathrm{ans}}+0.001\,L_{\mathrm{KL}}^{\mathrm{epi}}+1.5\,\operatorname{MSE}(s_{\mathrm{res}},\operatorname{sg}(t))+2.0\,\operatorname{MSE}(s_{\mathrm{amb}},H)+1.0\,L_{\mathrm{rank}}+5.0\,C^2(s_{\mathrm{res}},s_{\mathrm{amb}})+1.0\,C^2(s_{\mathrm{res}},H)+0.5\,L_{\mathrm{width}}+0.5\,L_{\mathrm{cap}}+0.5\,L_{\mathrm{var}},$$ where $C$ is the sample Pearson correlation and $L_{\mathrm{rank}}$ is a pairwise rank loss (64 random pairs, margin 0.1). We will include this objective, the exact construction of $r$, and the disclosed input leak (the ambiguity head receives $H$ as an input feature; $\rho(s_{\mathrm{amb}},H)$ is 0.94 with and 0.17 without that input on the seed-42 MAQA* run) in Appendix K. As we state below, the reported QA runs use $\lambda_d=5$, so they do not test Proposition 4.1's gradient-isolated setting. **Concept residuals and task-error detection.** The CEBaB residual score attains task-error AUROC 0.72 for both encoders, below MaxProb at 0.78 and 0.79. This is a downstream utility comparison; it does not measure fidelity to the concept-residual training target or establish epistemic validity. We will make this distinction explicit and report direct target alignment separately. Additionally as pointed we will also correct the reference to “Appendix 5” in Section 5.2 to Table 5 in Appendix J. We remain committed in improving the manuscript.

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