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Under review as a conference paper at ICLR 2027

Know What to Trust and What to Check: Calibration-Free Auditing for Concept Bottleneck Models

Abstract

Concept bottleneck models make predictions through interpretable intermediate concepts. When their concept predictions are uncertain, a reviewer needs to know whether this uncertainty can change the decision and which concept to inspect. We study these questions using an input-dependent ellipsoid constructed from ensemble disagreement. For a linear task head, a closed-form margin certifies that the predicted class is uniquely optimal throughout the ellipsoid and its intersection with the probability box. For diagonal geometry, a second diagnostic decomposes the squared first-order sensitivity penalty into concept contributions. Its Shapley interpretation concerns a fixed local surrogate, rather than the task loss after an observed correction. We evaluate the margin and practical ranking rules on concept prediction tasks, separating them from the optional robust training procedure. The reported margin-based selective prediction scores are comparable to confidence and entropy, while training results vary across datasets. On CEBaB, single-concept oracle replacement lowers accuracy under every ranking rule evaluated, including random selection. Additional five-seed CEBaB ablations with matched dropout and initialization give similar accuracy, ambiguity width, and margin-based retained accuracy. The construction provides a conditional account of model sensitivity; it does not establish coverage of the true concepts or guarantee that an intervention will correct a

Primary area:
interpretability and explainable AI
Keywords:
Concept Bottleneck models, margin

Reviews

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

This paper asks when uncertainty in a model's predicted concepts can change its final decision, and which concepts warrant human inspection. It uses disagreement among several concept predictors to define a region around their average prediction, and tests whether a linear classifier gives the same answer throughout that region. It also ranks concepts by combining their uncertainty with the classifier's sensitivity to them. In experiments, this stability score performs similarly to confidence when choosing which predictions to keep, but the tested single-concept correction rules reduce average accuracy on the CEBaB restaurant-review dataset.

Critical strengths
  • The paper tackles a useful problem: uncertainty in the predicted concepts does not necessarily matter for the final decision. It gives a simple way to check whether a linear classifier's answer stays the same over a chosen set of concept values.

  • The evaluation tests the approach across three datasets and compares it with simple uncertainty baselines. It achieves higher average accuracy among retained predictions than raw concept disagreement and performs competitively with confidence-based selection.

Critical weaknesses
  • The experiments do not isolate what the ensemble-based region adds. For selective prediction, the reported margin-based results match or trail confidence. The higher repair and damage rates among flagged examples also lack a comparison with confidence or the gap between the top two class scores at the same review budget. These controls would show whether the method adds information beyond proximity to a decision boundary. Most variance-selected corrections fall outside the region, limiting the certificate's relevance to them. Varying the region's size would show the trade-off between certifying predictions and covering actual corrections.

  • The novelty needs clearer positioning. Mukherjee et al. (ACL 2026) already propagate ensemble-derived concept intervals through a linear classifier. Here, the certificate compares pairs of classes over an ellipsoid. Comparing the assumptions and guarantees would clarify the contribution. The Shapley identity follows directly from the additive game; its value is interpretive.

  • The correction experiment uses only robust training (Mode C), leaving its generality unclear. Repeating it with ordinary task-and-concept training (Mode A) would test whether the harm is specific to that regime. With only four concepts, testing every eligible single correction would also show whether helpful corrections exist but the rankings miss them.

Questions for authors
  1. At matched review budgets, does the margin better identify examples where corrections repair or damage predictions than confidence or the top-two score gap? How does region size affect certification and coverage of corrections?
  2. Does harm persist without robust training? How often can a single correction help, and how often do the rankings find it?
  3. Please clarify novelty with respect to Mukherjee et al.
3 comments
AuthorsOpenReview ↗

Response to reviewer ZQqz

We thank the reviewer for his thoughtful response and question especially specifying controls required to assess the disagreement region. We have now completed matched-budget and exhaustive-correction analyses for both ordinary training (Mode A) and joint robust training (Mode C), and extended the radius analysis to measure actual replacement containment. All results below use CEBaB seeds 0–2 and the same test examples

Matched review budgets. We hold the checkpoint, eligibility mask, and predicted-label gradient correction rule fixed, and vary only the score used to select examples for review. The margin is min⁡c≠y^dc/vcTΣvc\min_{c\ne\hat y}d_c/\sqrt{v_c^T\Sigma v_c}, where vc=Wy^−Wcv_c=W_{\hat y}-W_c and dc=vcTμ+by^−bcd_c=v_c^T\mu+b_{\hat y}-b_c. The baselines are the top-two logit gap and maximum softmax confidence. Each score flags its 495 lowest-scoring examples, including any without eligible annotations; only eligible flagged examples receive a correction. Unflagged examples remain unchanged.

Each cell reports errors captured / repairable errors captured / fixes / breaks; overall accuracy change in percentage points. The change is (fixes−breaks)/1689(\mathrm{fixes}-\mathrm{breaks})/1689, multiplied by 100.

Run (initial errors, repairable)MarginTop-two gapConfidence
C0 (343, 159)206/124/91/119; −1.66209/133/99/113; −0.83209/134/99/116; −1.01
C1 (339, 155)193/115/85/133; −2.84196/121/87/137; −2.96198/125/89/140; −3.02
C2 (353, 134)209/90/68/94; −1.54212/102/75/101; −1.54214/104/77/104; −1.60
A0 (345, 145)207/113/81/131; −2.96217/122/86/118; −1.89221/125/88/118; −1.78
A1 (356, 161)222/124/89/127; −2.25216/126/87/137; −2.96218/128/87/141; −3.20
A2 (369, 140)196/84/63/90; −1.60216/113/82/95; −0.77207/109/80/104; −1.42

Margin captures fewer repairable errors than gap or confidence in every run. Correcting the flagged set reduces accuracy for all three scores in all six runs, with changes from −0.77 to −3.20 points. There is no consistent advantage for margin in net correction outcome. This experiment evaluates one common budget, not a curve over intervention budgets.

For routing without correction, the three-seed mean MRA values for margin/gap/confidence are .8575/.8647/.8646 in Mode C and .8531/.8588/.8588 in Mode A. MRA averages retained accuracy over coverages 0.50,0.60,0.70,0.80,0.90,0.95,1.000.50,0.60,0.70,0.80,0.90,0.95,1.00, with floor counts and stable input-order ties. Euclidean, trace-isotropic, and interval controls give .8623/.8580/.8586 in Mode C and .8590/.8549/.8552 in Mode A. Their denominators are respectively ∥vc∥2\|v_c\|_2, ∥vc∥2tr⁡(Σ)/K\|v_c\|_2\sqrt{\operatorname{tr}(\Sigma)/K}, and ∑k∣vck∣σk\sum_k|v_{ck}|\sigma_k; the last uses the unclipped box μ±σ\mu\pm\sigma. These results do not establish improved routing over gap or confidence.

Region size and actual correction containment. Scaling Σ\Sigma to t2Σt^2\Sigma gives mt=m/tm_t=m/t. It preserves the ranking and MRA, but changes certification to m>tm>t and the flagged set to m≤tm\le t. We have now measured two distinct containment quantities at each radius: whether the selected single-concept gold replacement lies inside the region, and whether the vector matching all eligible annotations, with unknown coordinates left at their means, lies inside it. For diagonal geometry, leaving unknown coordinates at their means minimizes their contribution to the Mahalanobis distance, so the latter checks existence of an in-region completion.

The following are means over seeds, with Mode C values followed by Mode A in parentheses. Certification uses all 1,689 examples; both containment columns use the 1,583 eligible examples. Selection uses the predicted-label gradient rule and is held fixed as the radius changes.

Radius multiplier ttCertified (%)Selected replacement inside (%)Annotated completion inside (%)
0.2593.3 (94.9)0.0 (0.0)0.0 (0.0)
0.586.4 (89.4)3.3 (0.0)1.8 (0.0)
172.0 (79.7)26.6 (4.3)17.6 (2.4)
242.5 (64.9)53.7 (27.0)36.7 (15.1)
44.2 (45.5)80.8 (61.5)60.6 (41.0)

These containment measurements are separate from the outcome rates among flagged examples:

ttAll errors captured (%)Fix rate among flagged errors (%)Break rate among flagged correct (%)
0.2517.4 (13.0)48.5 (45.9)47.3 (43.5)
0.531.2 (23.7)47.2 (43.2)45.2 (43.5)
156.5 (43.3)40.9 (37.6)39.5 (43.1)
284.6 (65.8)34.5 (36.5)26.3 (38.3)
499.6 (85.4)31.7 (33.3)18.1 (29.4)

The rates above are means of per-seed rates, not pooled ratios. Increasing the radius includes more actual replacements but certifies fewer examples. At unit scale, most selected replacements lie outside the specified region, limiting what this certificate can say about their outcomes.

AuthorsOpenReview ↗

Response to reviewer ZQqz

Any prediction-changing replacement on a certified example must leave the region; the converse does not hold. We checked that no certified, in-region selected replacement changes the prediction at any tested radius. We will report the per-seed counts and denominators alongside these summaries in the revision.

Ordinary training and exhaustive single corrections. We enumerate every eligible single-concept gold replacement. An initial error is repairable if at least one such replacement fixes it. The conditional hit rate asks whether the rule selects a fixing concept among those repairable errors. For uniform-random selection, this conditional probability is calculated exactly as the fraction of eligible concepts that fix each repairable example, then averaged over repairable examples.

RunInitial errorsRepairable errors (%)Gradient fixes/breaksGradient conditional hit (%)Uniform-random conditional hit (%)
C0343159 (46.4)120/26475.561.0
C1339155 (45.7)109/25570.365.1
C2353134 (38.0)98/19173.156.2
A0345145 (42.0)104/25471.759.1
A1356161 (45.2)111/24868.964.8
A2369140 (37.9)104/19474.355.4

Mean repairability is 43.3% in Mode C and 41.7% in Mode A. The gradient rule's conditional hit rate is 73.0% versus 60.8% for random in Mode C, and 71.7% versus 59.8% in Mode A. These conditional results do not imply positive intervention utility: the gradient rule also breaks many initially correct predictions, producing mean accuracy changes of −7.56 and −7.44 points. The variance, PL, and weight-only rules also reduce accuracy in every Mode A seed. Thus harm persists without robust training, although these experiments do not establish its causal mechanism.

As a derived hindsight upper bound, an oracle that chooses a fixing concept whenever one exists and otherwise makes no correction would improve Mode C accuracy by 159/1689, 155/1689, and 134/1689: 9.41, 9.18, and 7.93 percentage points. It would break no correct predictions. This uses hindsight and a no-correction option; it is not an achieved performance result or a deployable policy.

Relation to Mukherjee et al. Mukherjee et al. (ACL 2026) construct ensemble min–max concept intervals, propagate them through a linear classifier to obtain exact per-class logit bounds, and study epistemic–aleatoric decomposition. Our focus is pairwise decision stability over a specified ellipsoid and attribution of a fixed local loss penalty, followed by evaluation of correction outcomes. We will acknowledge the standard support-function and additive-game arguments and position the work within concept-space uncertainty analysis.

For the same feasible region, directly minimizing a logit difference avoids combining separately attained class extrema. This observation also applies to boxes and does not establish an advantage of ellipsoids. A diagonal ellipsoid is contained in the box with the same center and coordinate half-widths, but this comparison does not automatically apply to ensemble min–max intervals. We will distinguish these geometries, use the probability-box constraint [0,1]K[0,1]^K, and avoid claiming that changing geometry alone establishes novelty or improved routing.

We remain available to answer further questions or queries.

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

Reviewer_GjgNOpenReview ↗
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Paper summary

The paper investigates whether disagreement among concept predictors can change a model's decision and which concepts contribute most to its local sensitivity. The authors construct an instance-specific ellipsoid from ensemble concept disagreement and derive a closed-form margin certifying prediction invariance, along with a Shapley-based concept sensitivity score. Experiments show that the margin performs comparably to standard confidence measures for selective prediction, while all concept replacement strategies reduce accuracy on CEBaB.

Critical strengths

Meaningful distinction between uncertainty and sensitivity. The paper highlights that high concept uncertainty does not necessarily imply a large influence on the final prediction, and distinguishes prediction stability from correctness.

Critical weaknesses
  1. Limited theoretical novelty. The three formal results are direct specializations of standard tools. Theorem 1 is the support function of an ellipsoid: max⁡∥u∥≤1g⊤Σ1/2u=g⊤Σg\max_{\|u\|\le1} g^\top\Sigma^{1/2}u = \sqrt{g^\top\Sigma g}, a textbook identity from ellipsoidal robust optimization. Theorem 2 applies the same computation to each pairwise logit gap; the margin mc=dc/wc⊤Σwcm_c = d_c/\sqrt{w_c^\top\Sigma w_c} is the Mahalanobis distance from the ensemble mean to the tie hyperplane. Proposition 1 observes that the Shapley value of an additive game v(S)=∑k∈Sakv(S)=\sum_{k\in S}a_k is ϕk=ak\phi_k = a_k, which follows from the additivity axiom and adds no information beyond the per-concept term σk2gk2\sigma_k^2 g_k^2. The paper also concedes that the certificate is only sufficient on the boxed set and that the attribution offers “no optimality guaranty for post-correction accuracy” (l. 194–195). The authors should state what is theoretically new in applying these results to CBMs; as written, the contribution is a repackaging.

  2. No demonstrated practical advantage over trivial baselines. Neither proposed output shows a benefit. For selective prediction (Table 2), the margin’s mean retained accuracy is below confidence on all three datasets (.857 vs .865 on CEBaB, .896 vs .956 on CUB, .509 vs .525 on GoEmotions). For concept auditing (Table 4), every replacement rule lowers accuracy on every seed by 5.8–8.0 points, and random concept selection (−.065) is within noise of the Shapley/gradient ranking (−.076); the authors “do not know why replacement hurts” (l. 354). Robust training (Mode C) gives no consistent gain either (+0.7 on CEBaB, −4.0 on CUB, −0.1 on GoEmotions vs Mode A). The paper’s framing as a tool for knowing “what to trust and what to check” is therefore unsupported: the margin is not a better trust signal than softmax confidence, and checking the flagged concepts hurts.

Questions for authors
  1. Why does Mode C underperform Mode A on CUB, and why does joint robust training not help on GoEmotions? Is robust training part of the contribution, or only an optional ablation?

  2. Several results use a single seed, the two CUB rows in Table 3 “should not be compared directly,” and replacement is evaluated only on CEBaB with four concepts. Can the authors report multi-seed results and replacement on CUB (112 concepts) or GoEmotions (28)?

5 comments
AuthorsOpenReview ↗

Response to reviewer GjgN

We thank the reviewer for recognizing the distinction between concept uncertainty and decision sensitivity. We answer the questions raised below Theoretical contribution. The ellipsoidal support identity and the Shapley values of an additive game are standard. We will identify these ingredients explicitly and narrow the novelty statement. The paper applies them to an input-dependent concept region, separates exact prediction invariance from a first-order loss approximation, and evaluates their relation to correctness and concept correction. The Shapley interpretation concerns a fixed squared-sensitivity game and provides no optimality guarantee for post-correction accuracy. The condition m>1m>1 is necessary and sufficient for unique prediction invariance on the unboxed ellipsoid, and sufficient but not necessary on its intersection with [0,1]K[0,1]^K.

Additional routing controls. We have completed the gap, Euclidean, trace-isotropic, and interval comparisons on the same frozen CEBaB checkpoints, seeds 0–2. Mode C denotes joint robust training; Mode A uses ordinary training followed by the audit. All runs evaluate the same 1,689 examples. MRA is the arithmetic mean of retained accuracy at coverages 0.50,0.60,0.70,0.80,0.90,0.95,1.000.50,0.60,0.70,0.80,0.90,0.95,1.00, with floor counts and stable input-order ties.

ScoreC: seed 0C: seed 1C: seed 2C: meanA: mean
Margin.8617.8598.8509.8575.8531
Top-two gap.8699.8629.8614.8647.8588
Euclidean.8621.8634.8613.8623.8590
Trace-isotropic.8589.8611.8540.8580.8549
Interval.8607.8614.8537.8586.8552
Confidence.8683.8640.8615.8646.8588

For competing class c≠y^c\ne\hat y, let vc=Wy^−Wcv_c=W_{\hat y}-W_c and dc=vcTμ+by^−bcd_c=v_c^T\mu+b_{\hat y}-b_c. The margin, Euclidean, trace-isotropic, and interval scores are respectively the minimum of dcd_c divided by ∑kvck2σk2\sqrt{\sum_kv_{ck}^2\sigma_k^2}, ∥vc∥2\|v_c\|_2, ∥vc∥2K−1∑kσk2\|v_c\|_2\sqrt{K^{-1}\sum_k\sigma_k^2}, and ∑k∣vck∣σk\sum_k|v_{ck}|\sigma_k. The interval control uses the unclipped box μ±σ\mu\pm\sigma, not ensemble min–max intervals. The top-two gap is min⁡c≠y^dc\min_{c\ne\hat y}d_c; confidence is the maximum softmax probability. Spearman correlations between margin and gap are .901, .788, and .661 across the three Mode C seeds (mean .783; Mode A mean .809). The rankings differ, but margin has lower MRA than gap and confidence in both modes.

At a common review budget of 495 examples, mean retained accuracy for margin/gap/confidence is 88.079%/88.331%/88.442% in Mode C and 87.577%/88.247%/88.163% in Mode A. Thus, these controls provide no evidence of an advantage for margin over gap or confidence at this budget. The submitted CUB row reports .956 for both margin and confidence; .896 is the width score. We do not treat the new CEBaB controls as a replication of the CUB or GoEmotions rows, whose matching-checkpoint controls remain unresolved.

Comparison with random correction. Replacement selects one eligible aspect, replaces its predicted probability with its encoded gold value, and leaves examples without an eligible aspect unchanged. Each run has 1,583 eligible examples out of 1,689. The following differences are percentage points of accuracy over all test examples, relative to a 200-draw Monte Carlo estimate of uniform-random selection among eligible aspects.

RuleMode C difference [95% CI]Mode A difference [95% CI]
Variance+0.70 [0.06, 1.35]+0.37 [−0.33, 1.05]
Predicted-label gradient−1.06 [−1.69, −0.42]−0.63 [−1.38, 0.04]
Gold-label gradient (oracle)−0.63 [−1.29, 0.05]−0.18 [−0.95, 0.53]
PL−1.49 [−2.12, −0.89]−0.83 [−1.53, −0.13]
Weight-only−0.76 [−1.47, −0.07]−1.32 [−1.89, −0.74]

For each example, we average the rule-minus-random accuracy change across the three seeds, then resample the 1,689 example IDs 2,000 times and take percentile intervals. This preserves the repeated-example dependence across seeds. The intervals concern test-example variability conditional on these checkpoints and the Monte Carlo baseline; they are not simultaneous intervals or estimates of variability over new training seeds.

The predicted-label gradient differences in Mode C are −1.07 [−2.31, 0.13], −1.33 [−2.42, −0.22], and −0.78 [−1.89, 0.30] points; the Mode A differences are −0.77, −0.32, and −0.81 points. The difference is negative in all six runs, but only one individual-seed interval excludes zero. The Monte Carlo random losses are −7.46, −7.31, and −4.73 points in Mode C (mean −6.50), and average −6.81 points in Mode A. These estimates are distinct from Table 4's single sampled random baseline, whose Mode C mean is −6.49 points. The gold-label gradient is an oracle comparator, not a deployable rule.

AuthorsOpenReview ↗

Response to Reviewer GjgN

Rounding, shuffled annotations, and ordinary training. We have also evaluated the same predicted-label gradient selection rule with three replacement values: the gold value, the model's own hard prediction 1[μk>0.5]\mathbf1[\mu_k>0.5], and a gold value sampled from the pool of eligible records for the same aspect. The last control samples donors with replacement and permits self-donation; it is one draw per seed, not a permutation test. The selected concept, center, and classifier otherwise remain fixed.

Each cell below gives accuracy change in percentage points, followed by fixes/breaks. The rounded and shuffled counts were reconstructed by replaying the saved protocol and reproduce its reported accuracy changes.

RunGoldRounded predictionShuffled gold
C0−8.53 (120/264)−4.80 (83/164)−22.85 (98/484)
C1−8.64 (109/255)−4.68 (72/151)−28.06 (89/563)
C2−5.51 (98/191)−5.92 (65/165)−16.52 (83/362)
A0−8.88 (104/254)−4.38 (85/159)−22.91 (101/488)
A1−8.11 (111/248)−4.14 (76/146)−25.70 (89/523)
A2−5.33 (104/194)−5.03 (72/157)−17.11 (116/405)

Mean gold-replacement losses are −7.56 points in Mode C and −7.44 in Mode A; rounding losses are −5.13 and −4.52. Rounding therefore also causes harm, but its loss relative to gold replacement varies substantially: 56%, 54%, and 107% in Mode C, and 49%, 51%, and 94% in Mode A. We will not characterize this as a causal decomposition or claim that rounding explains a stable fraction of the harm. Harm persists under ordinary training, so robust training is not required for this negative outcome. This does not identify a causal effect of robust training or explain why individual replacements fail.

The same conclusion holds for the other deployable rules in Mode A:

RuleSeed 0: change (fix/break)Seed 1: change (fix/break)Seed 2: change (fix/break)
Variance−7.87 (87/220)−7.64 (106/235)−3.79 (94/158)
PL−9.18 (92/247)−7.52 (84/211)−6.22 (86/191)
Weight-only−9.71 (96/260)−6.45 (126/235)−8.23 (70/209)

Scope of the evidence. These controls strengthen the CEBaB analysis; they do not establish generality across datasets. We have not completed additional matched CUB or GoEmotions routing seeds or a validated replacement study on either dataset. The available CUB targets lack the observation mask required by this replacement protocol, and GoEmotions requires explicit treatment of the fact that its task label is derived from its concepts. The five-seed CEBaB ensemble ablations do not resolve these limitations. We will state this scope explicitly and avoid attributing the mixed robust-training results to an untested mechanism.

We remain available to answer further queries

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

Reviewer_zF8bOpenReview ↗
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Paper summary

The paper studies how concept uncertainty affects the final prediction, in the situation where several concept heads are ensembled. Using the concept predictions, the authors define an disagreement region, and provide a margin certificate of prediction invariance for that region. Additionally, the paper propose a concept-wise sensitivity score which identifies which concept's uncertainty most affects the decision. Also, for the training stage, a robust training objective based on the worst-case loss over the disagreement region is proposed.

Critical strengths

None

Critical weaknesses
  1. I think the writing should be improved. In particular, the abstract and introduction do not provide clear outline of the paper. For instance, the goal or scope of "auditing" is not suggested, the concept of additive game and Shapley value are introduced without context. Also, the contributions of the paper are hard to assess when reading the introduction.
  2. The setting and contribution of the paper seem limited. Why the authors choose the setting where multiple concept predictors are ensembled is not really explained. Also, in this setting, the contributions seem to be restricted. The title and Figure 1 frames the contribution as auditing pipeline composed of margin-based routing, sensitivity score based ranking and robust objective, but in the experiment, only the margin-based routing shows good performance while the other two do not really help.
Questions for authors
  1. The title contains the phrase "calibration-free". What does it exactly imply?
  2. Can you clarify the scope and goal of "audit"?
  3. The choice of using diagonal matrix for \Sigma_epi looks like a big simplification as it ignores possible correlation of concepts in the data. Can you provide some justification for designing the matrix to be diagonal?
5 comments
AuthorsOpenReview ↗

Response to reviewer zF8b

We thank the reviewer for his comments. We will revise the abstract, introduction, and Figure 1 to state the diagnostic questions before introducing their mathematical interpretation.

Scope and contribution. Given a trained CBM and a specified region of concept vectors, the audit asks whether the predicted class remains uniquely optimal throughout that region, and how each concept contributes to a fixed local loss-sensitivity penalty. The condition m>1m>1 certifies prediction invariance on the ellipsoid and its intersection with the probability box. Failure of this test does not necessarily imply a class change inside the box. For diagonal geometry, ak=σk2gk2a_k=\sigma_k^2g_k^2 decomposes the squared local sensitivity penalty, using the nominal predicted label to define the loss at deployment. Neither quantity certifies correctness or guarantees that replacing a concept improves accuracy. The Shapley interpretation follows because removing uncertainty on an axis removes its contribution to this fixed squared penalty; the gradient is held fixed in that game. We will explain this operation before introducing the game terminology.

For example, take a binary linear head with logit-difference weights w=(1,0)w=(1,0), nominal gap d=0.1d=0.1, and mean μ=(0.5,0.5)\mu=(0.5,0.5). The shape matrices diag⁡(0.0025,0.04)\operatorname{diag}(0.0025,0.04) and diag⁡(0.04,0.0025)\operatorname{diag}(0.04,0.0025) have the same trace and give the same nominal prediction and confidence, but their margins are 22 and 0.50.5. Only the first region is certified. This illustrates the geometric distinction; it does not establish an empirical advantage over confidence.

Ensemble construction and calibration. The ensemble supplies an input-dependent disagreement region. Evaluating the audit requires no additional concept or task annotations, although training uses supervision. The certificate accepts any specified mean and positive-semidefinite shape matrix, including singular matrices represented as the image of a unit ball. Shared representations can produce shared errors, so ensemble disagreement does not establish coverage of the true concepts. By “calibration-free,” we mean that evaluating the certificate requires no additional calibration dataset or fitted error threshold. We do not mean that the model probabilities are calibrated. Scaling the shape matrix by t2t^2 divides the margin by tt and changes the certified set.

Diagonal versus correlated geometry. Diagonal geometry makes the fixed squared penalty additive across concepts. It is a modeling simplification, not a claim that the concepts are statistically independent, and it is not required by the margin theorem. With five heads, the empirical covariance has rank at most four and can be poorly conditioned. Regularization changes the region. The separately trained variants in Table 14 do not isolate the effect of retaining correlations.

We have now completed a covariance-only comparison on the original frozen CEBaB Mode C checkpoints, seeds 0–2, with the same 1,689 test examples, saved centers, classifiers, and marginal variances. We regenerated the five head predictions in evaluation mode and verified their agreement with the saved centers and variances; the classifier weights and biases match exactly. No model was retrained.

For each example, we estimated the sample covariance across heads using divisor H−1=4H-1=4, converted it to a correlation matrix RR, and restored the saved diagonal variances DD. We evaluated

Σλ=D1/2(1−λ)R+(λ+η)I1+ηD1/2,η=10−6.\Sigma_\lambda=D^{1/2}\frac{(1-\lambda)R+(\lambda+\eta)I}{1+\eta}D^{1/2},\qquad \eta=10^{-6}.

Here λ=1\lambda=1 gives the original diagonal geometry, λ=0\lambda=0 gives regularized full geometry, and λ∈{0.1,0.5}\lambda\in\{0.1,0.5\} gives fixed shrinkage toward diagonal. These choices were specified before computing the outcomes, without fitting to test labels. Every variant preserves each marginal variance and the per-example trace. The region is μ+Σλ1/2u\mu+\Sigma_\lambda^{1/2}u, ∥u∥2≤1\|u\|_2\le1, with radius multiplier one and no additional multiplication by tr⁡Σλ\sqrt{\operatorname{tr}\Sigma_\lambda}.

The following percentages are means ± sample SD across seeds 0–2. Certification is the fraction with m>1m>1. MRA averages retained accuracy at coverages 0.50,0.60,0.70,0.80,0.90,0.95,1.000.50,0.60,0.70,0.80,0.90,0.95,1.00, using floor counts and stable ties. The fixed-budget comparison flags 495 examples and retains 1,194.

CovarianceCertified (%)Routing MRA (%)Retained accuracy, B=495 (%)
Diagonal71.995 ± 1.14285.746 ± 0.57588.079 ± 0.396
Full, regularized70.081 ± 1.76985.709 ± 0.52887.549 ± 0.211
10% shrinkage70.180 ± 1.44185.738 ± 0.51987.744 ± 0.338
50% shrinkage70.930 ± 1.03285.790 ± 0.51887.856 ± 0.384

The routing differences are small and mixed: 50% shrinkage increases mean MRA by 0.045 percentage points, while full covariance decreases it by 0.037 points.

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Response to reviewer zF8b

Both improve MRA in two seeds and reduce it in one. All correlated variants have lower mean certification rates and fixed-budget retained accuracy. Equal trace does not imply equal volume or calibrated equal coverage, so certification rate alone does not establish which uncertainty estimate is better. These results do not support a general claim that correlations cannot help.

Empirical scope and revisions. The audit provides a statement about a specified region and a decomposition of local sensitivity. Its practical usefulness is assessed separately. On CEBaB, the new comparisons give mean MRA 0.8575 for the diagonal margin, 0.8647 for the top-two logit gap, and 0.8646 for confidence. Predicted-label gradient replacement reduces accuracy in all three seeds. We will make these limitations explicit, identify the loss-gradient score as the primary attribution in Figure 1, and present PL as a comparator. Robust training remains an optional way to construct the ensemble; the available results do not establish a general accuracy benefit or beneficial intervention policy.

We remain available to clarify further queries or questions.

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.

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