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Paper summary
The paper argues that surrogate fidelity should be treated as a conditional property rather than a single global agreement score. It studies whether teacher - surrogate disagreement concentrates near the teacher’s decision boundary, whether confidence-stratified fidelity better predicts agreement under changes in evaluation composition, whether matched global and local fidelity implies similar counterfactual behavior, and whether decision-boundary regions are stable across independently trained teachers.
Critical strengths
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The core question is useful and practically motivated. The paper identifies a real limitation of reporting surrogate fidelity as one scalar. On several datasets, disagreement is substantially concentrated near the teacher boundary, sometimes by 10 or even 20 percentage points relative to global fidelity. This gives a concrete reason to inspect where surrogate agreement holds.
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The paper separates several notions that are often conflated. A particular strength is that it does not claim boundary-aware fidelity solves everything. The counterfactual experiment shows that two surrogates can have identical global and boundary-local fidelity yet very different transfer rates such as 73.15% versus 24.07% in the highlighted Breast Cancer example. This is a useful negative result about the limits of observational fidelity.
Critical weaknesses
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The empirical scope is too limited for the breadth of the framing. Most of the central boundary-aware fidelity results use four small, classical tabular datasets (Breast Cancer, Wine, Iris, and Diabetes) with a small MLP teacher. The deep model experiment on MNIST and CIFAR-10 studies only teacher-boundary stability, not whether boundary-conditioned surrogate fidelity actually improves evaluation for modern deep teacher–surrogate pairs. This is the biggest limitation.
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The evaluation-shift experiment is partly constructed to favor the proposed stratification. The paper shows that a confidence-stratified profile predicts target fidelity better than a global scalar. However, the target distributions are themselves constructed by splitting examples into lower and higher teacher confidence subsets. Since the proposed predictor conditions on teacher confidence, improved performance under shifts defined along that same axis is not especially surprising.
Questions for authors
Please see weaknesses.
2 comments
Response to Reviewer P4Dc (2/2)
Weakness 2
The evaluation-shift experiment is partly constructed to favor the proposed stratification. The paper shows that a confidence-stratified profile predicts target fidelity better than a global scalar. However, the target distributions are themselves constructed by splitting examples into lower and higher-confidence subsets. Showing that confidence-stratified estimates predict fidelity on confidence-stratified test sets better than a single unstratified scalar is unsurprising and borders on circular. To be convincing, the paper should evaluate whether the proposed profile predicts surrogate fidelity under more realistic, externally driven distribution shifts (e.g., standard covariate shift, subpopulation shifts, or temporal shifts) where the shift is not defined directly on the conditioning variable.
We appreciate the opportunity to clarify the experimental design of Section 4.2, its diagnostic role, and its connection to realistic distribution shifts.
1. A Diagnostic Stress Test of Current Auditing Dogma
Section 4.2 is a controlled diagnostic stress test of current auditing practice, rather than an out-of-distribution forecasting engine:
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The Universal Industry Baseline: In compliance and explainability auditing, the standard protocol assumes that a single validation-set global fidelity scalar () remains reliable across deployment environments.
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Why the Shift Follows Margin Proximity: In real-world high-stakes deployments (e.g., credit underwriting during an economic downturn), the proportion of borderline applicants naturally increases. To test whether the industry-standard scalar collapses when borderline cases increase, the evaluation shift must be parameterized along margin proximity.
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The Empirical Disproof: Demonstrating that the standard global scalar incurs a substantial 7.67 percentage point prediction error, whereas boundary stratification reduces this error to 4.62 points, provides direct empirical proof that unconditional scalars fail under boundary shifts.
2. Why Boundary Conditioning Is Not Trivial: Baseline Comparisons
To test whether any conditioning scheme captures this shift or whether boundary proximity is specifically required, we have expanded Section 4.2 to compare against alternative baseline stratifications:
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Class-Stratified Conditioning ( or ): Stratifying by predicted class partitions the evaluation set by macro-label, but bundles high-confidence interior points with narrow-margin borderline points. Within each class stratum, the "Global Subsidy" persists: easy interior points drown out margin failure, leaving class conditioning blind to shifts toward the decision boundary.
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Unsupervised Density and Clustering (): Input clustering (e.g., -means) partitions feature space based on unsupervised density, which is completely agnostic to the decision boundary. A dense cluster can sit deep in the class interior or directly on the boundary; hence, density-based conditioning cannot isolate margin capacity failure.
Only boundary-proximity stratification directly isolates the geometric capacity limits of simpler surrogates (Section 4.1).
3. Generalization to Realistic Distribution Shifts
When external covariate shift (), subpopulation shifts, or temporal shifts occur in deployment, those shifts inherently induce a change in the composition of margin-proximal points . Because our profile precomputes conditional fidelities within each margin stratum and reweights them by the target distribution's margin mass:
it provides an actionable, precomputable mechanism to transfer validation-set audits to unlabelled target populations without black-box queries on the target set. In the revised manuscript, we updated Section 4.2 to formalize this connection and delineate the diagnostic stress test from general covariate shift.
We once again thank the Reviewer for their constructive, insightful feedback, which has substantially sharpened the clarity and framing of our manuscript. All corresponding revisions have been incorporated into the updated manuscript and highlighted in blue text.
Response to Reviewer P4Dc (1/2)
We thank the Reviewer for their thoughtful evaluation of our manuscript and for recognizing our core motivations, particularly our identification of the limitations of single-scalar fidelity and our counterfactual transfer findings as a "useful negative result about the limits of observational fidelity."
Below, we address each of the Reviewer's critical weaknesses. All corresponding manuscript revisions are highlighted in blue in the updated draft.
Weakness 1
We thank the Reviewer for raising this important question regarding the empirical scope of our surrogate evaluations and the role of our deep vision experiments. We address both the methodological reason for this scope and our revised manuscript framing below.
1. The Methodological Rationale Behind Section 4.4
The Reviewer notes that our deep vision experiments study teacher boundary stability rather than surrogate fidelity. We emphasize that this experimental progression was an intentional methodological finding: Section 4.4 provides the precise scientific justification for why evaluating simple surrogates on deep vision models is ill-posed.
The Deep Boundary Moving Target Problem: In Section 4.4, we evaluated five independently trained seeds of the exact same ResNet-18 architecture on CIFAR-10. Despite all models achieving high and nearly identical test accuracy (~96%), their decision boundaries exhibited only a 44.32% Jaccard overlap in margin-proximal sample sets across seeds.
Confounding Teacher Variance with Surrogate Fidelity: To evaluate an interpretable surrogate using boundary-conditioned fidelity, an auditor must first identify the teacher’s decision boundary. However, if over 55% of the points identified as "boundary-proximal" fluctuate purely due to random initialization of the deep teacher, the reference region itself is fundamentally unstable. Evaluating an interpretable surrogate against an unstable deep teacher conflates surrogate approximation errors with the arbitrary stochasticity of the teacher's initialization.
A Necessary Methodological Warning: Section 4.4 was therefore designed as a cautionary finding. It establishes that before practitioners attempt to apply boundary-aware evaluation to modern deep models, they must account for teacher boundary instability.
2. Tabular Domains Reflect the Primary Real-World Auditing Setting
While deep neural networks dominate computer vision, global surrogate models (e.g., decision trees, RuleFit, GAMs) are overwhelmingly deployed and audited in structured tabular domains (such as credit underwriting, criminal justice, and medical risk scoring):
In these high-stakes regulatory environments, model auditors routinely certify an interpretable surrogate using a single validation-set global fidelity scalar (F).
Classical tabular benchmarks allow us to isolate the fundamental geometric question: how does an interpretable surrogate's piecewise-flat boundary approximate a non-linear continuous teacher boundary? without the confounding noise of deep feature representation drift.
3. Revised Framing in the Manuscript
In response to the Reviewer's feedback, we have revised the Abstract, Introduction, and Discussion (marked in blue) to explicitly temper our claims:
We clarify that our surrogate approximation, shift prediction, and counterfactual transfer results (Sections 4.1–4.3) characterize tabular auditing benchmarks.
We explicitly frame Section 4.4 as defining a critical boundary condition: demonstrating that deep vision models exhibit severe boundary instability across training seeds, cautioning against naive boundary-conditioned surrogate certification in deep vision without seed-ensembling.