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Under review as a conference paper at ICLR 2027

"Where Can I Trust You?": Boundary-Aware Evaluation of Surrogate Fidelity

Abstract

Surrogate models are commonly evaluated by how often they agree with their teacher model over an evaluation set. Local variation in this agreement is well known, but its structure and consequences are less clear. We ask whether disagreement is systematically concentrated near the teacher's decision boundary and whether retaining that structure provides information beyond a single global score. Across several datasets and surrogate model classes, we find substantially lower fidelity near teacher decision boundaries under two different methods of identifying near-boundary examples. Moreover, conditioning agreement on confidence-defined regions improves prediction of teacher–surrogate agreement when evaluation-set composition changes, relative to the global score alone. Yet surrogates that agree equally well with the teacher both globally and near the decision boundary can respond very differently to changes selected using the surrogate itself. Finally, we show that independently trained deep teachers can agree on most predictions while identifying different examples as lying near their decision boundaries, complicating the use of those boundaries as stable reference regions for evaluating surrogates. Together, these results show that surrogate fidelity depends not only on how often a surrogate agrees with its teacher, but also on where that agreement holds and, for deep models, how stable the teacher's decision boundary is across training runs.

Primary area:
interpretability and explainable AI
Keywords:
surrogate models, model fidelity, explainable AI, decision boundaries, counterfactual explanations, distribution shift, uncertainty estimation, model interpretability

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.25 over 4 reviews, above 2% of the others.
Reviewer_P4DcOpenReview ↗
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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
  1. 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.

  2. 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
  1. 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.

  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 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
AuthorsOpenReview ↗

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

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.

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 (FF).

  • 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.

AuthorsOpenReview ↗

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:

  • The Universal Industry Baseline: In compliance and explainability auditing, the standard protocol assumes that a single validation-set global fidelity scalar (FF) remains reliable across deployment environments.

  • 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.

  • 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:

  • Class-Stratified Conditioning (YY or Y^\hat{Y}): 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.

  • Unsupervised Density and Clustering (p(x)p(x)): Input clustering (e.g., kk-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 (P(X)P(X)), subpopulation shifts, or temporal shifts occur in deployment, those shifts inherently induce a change in the composition of margin-proximal points Ptarget(Rk)P_{\text{target}}(R_k). Because our profile precomputes conditional fidelities within each margin stratum and reweights them by the target distribution's margin mass:

F^target=∑kF(Rk)Ptarget(Rk),\hat{F}_{\text{target}} = \sum_k F(R_k) P_{\text{target}}(R_k),

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.

Reviewer_doSsOpenReview ↗
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Paper summary

This paper investigates the limitations of global fidelity as an evaluation metric for surrogate models, arguing that teacher–surrogate agreement should be assessed conditionally across different regions of the input space, particularly near the teacher's decision boundary.

Critical strengths
  1. Boundary-aware fidelity: The authors introduce confidence-based and approximate geometric measures of proximity to the teacher's decision boundary. Across several tabular datasets and surrogate model families, they find that teacher–surrogate agreement is often substantially lower near decision boundaries than globally.
  2. Confidence-stratified fidelity prediction: The authors propose a confidence-stratified fidelity profile that estimates target-set fidelity by reweighting agreement rates across teacher-confidence regions. This method reduces mean absolute prediction error from 7.67 to 4.62 percentage points compared with using global fidelity under controlled changes in evaluation-set composition.
  3. Counterfactual transfer: The paper demonstrates that surrogate models with identical global and boundary-local fidelity can exhibit significantly different example-based counterfactual transfer rates, indicating that observational agreement does not guarantee equivalent downstream behavior.
  4. Teacher boundary stability: Experiments on MNIST and CIFAR-10 show that independently trained deep teachers can exhibit high global prediction agreement while identifying substantially different sets of near-boundary examples.
Critical weaknesses

W1. Unclear practical utility of boundary-aware fidelity.

The paper shows that surrogate fidelity decreases near teacher decision boundaries, but does not establish how this improves model reliability or explanation quality. Since faithfully reproducing a teacher's predictions does not guarantee their correctness, the practical value of boundary-aware fidelity remains unclear.

W2. Limited methodological novelty and insufficient baselines.

Prior work has already explored local variations in surrogate fidelity. The proposed confidence-stratified profile mainly relies on simple partitioning and reweighting. Comparisons with alternative stratification methods are needed to demonstrate the specific value of decision-boundary information.

W3. Limited evaluation under distribution shifts.

The evaluation sets are constructed based on teacher confidence, which is also used by the proposed method. This setting may favor the approach, and its effectiveness under more realistic distribution shifts remains unclear.

W4. Limited connection between fidelity and downstream behavior.

The counterfactual experiments show that similar fidelity can lead to very different transfer rates. However, the paper does not demonstrate whether boundary-aware fidelity can better predict or improve such downstream behavior.

W5. Limited experimental generalizability.

The main surrogate-fidelity experiments rely on small tabular datasets and binary classification tasks. Evaluation on larger and more complex datasets would strengthen the generalizability of the findings.

Questions for authors

Q1. What is the practical utility of boundary-aware fidelity beyond measuring teacher–surrogate agreement? The paper demonstrates that surrogate fidelity often decreases near the teacher's decision boundary. However, low teacher confidence does not necessarily indicate prediction errors, and high teacher–surrogate agreement does not imply correctness with respect to ground-truth labels. Could the authors report teacher accuracy and surrogate accuracy across the same confidence-defined regions? More importantly, can boundary-aware fidelity help identify teacher errors, improve explanation usefulness, or support more reliable downstream decisions?

Q2. Is the improvement of confidence-stratified fidelity specific to decision-boundary information? The proposed fidelity profile performs a relatively straightforward stratification and reweighting of conditional agreement rates. Could the authors compare it against alternative stratification strategies, such as grouping examples by predicted class, input-space clustering, sample density, or other uncertainty measures? This would help clarify whether the predictive gains arise specifically from decision-boundary information or from conditional evaluation more generally.

Q3. How well does the fidelity profile generalize to realistic distribution shifts? The evaluation-composition experiments construct target distributions by selecting lower- and higher-confidence subsets, while the proposed profile itself also uses teacher confidence. Could the authors evaluate the method under broader forms of distribution shift, such as covariate shift, class-prior shift, or out-of-distribution data? This would provide stronger evidence that the method is useful beyond the confidence-based evaluation setting considered in the paper.

Q4. How stable are the conclusions across teacher architectures, calibration methods, and boundary definitions? The proposed boundary regions rely on teacher logits or approximate geometric proximity, while the deep-teacher experiments show that near-boundary sets are only partially stable across training runs. Could the authors investigate whether confidence calibration, alternative uncertainty measures, or different teacher architectures substantially change the identified boundary regions and the resulting fidelity conclusions?

4 comments
AuthorsOpenReview ↗

Response to Reviewer doSs (1/4)

We thank the Reviewer for their thoughtful and detailed feedback concerning our manuscript. We address each listed weakness and question below.

Weaknesses 1 & 4, and Question 1

W1. Unclear practical utility of boundary-aware fidelity.

W4. Limited connection between fidelity and downstream behavior.

Q1. What is the practical utility of boundary-aware fidelity beyond measuring teacher–surrogate agreement? The paper demonstrates that surrogate fidelity often decreases near the teacher's decision boundary. However, low teacher confidence does not necessarily indicate prediction errors, and high teacher–surrogate agreement does not imply correctness with respect to ground-truth labels. Could the authors report teacher accuracy and surrogate accuracy across the same confidence-defined regions? More importantly, can boundary-aware fidelity help identify teacher errors, improve explanation usefulness, or support more reliable downstream decisions?

We thank the Reviewer for raising this fundamental question regarding the practical utility of surrogate fidelity and its relationship to ground-truth accuracy. We first discuss the difference between fidelity and accuracy, then we discuss the concrete practical utility of this study.

1. The Core Mandate of Surrogate Auditing: Fidelity vs. Accuracy

In post-hoc explainability and model auditing, the surrogate's primary objective is fidelity to the black-box teacher, not ground truth classification accuracy. This is because a surrogate is trained without the ground truth, instead aiming to mimic the outputs of the teacher model.

  • Faithful Surrogates Must Mirror Teacher Errors: The goal of an auditor is not to deploy the surrogate as a replacement classifier, but to inspect, explain, and audit the actual behavior of the deployed black box (Craven & Shavlik, 1996; Guidotti et al., 2018). If a black box makes an erroneous or biased prediction in credit underwriting or medical triage, the surrogate must faithfully reproduce that error so that auditors and regulators can detect the failure mode (Jacovi & Goldberg, 2020). A surrogate that predicts ground-truth labels instead of the teacher would act as an independent classifier, hiding the black box's mistakes from auditors. As recent work has formalized, conflating surrogate fidelity with ground-truth accuracy represents a category error in model evaluation (Eshbaugh, 2026).

  • Accuracy Across Margin Regions: By standard statistical learning theory, classification error naturally concentrates where the margin is narrow and class overlap is highest (Bartlett & Wegkamp, 2006; Geifman & El-Yaniv, 2017). In our experiments, while teacher and surrogate accuracy both decrease in low-confidence regions, teacher–surrogate agreement drops substantially faster than accuracy. This proves that the surrogate's capacity limits compound prediction error near the margin, creating an illusion of high fidelity in the interior.

2. Concrete Practical Utility: Safe Recourse Certification

The immediate practical utility of boundary-aware fidelity is serving as an essential diagnostic risk filter for algorithmic recourse:

  • The Failure of Global Fidelity: In high-stakes settings, surrogates are used to generate counterfactual recommendations (explaining how an individual can change their features to cross the decision boundary). Under current standards, an auditor relying on global fidelity (FF) would treat two surrogates achieving ~90% fidelity as interchangeable.

  • The Downstream Consequence: Our Breast Cancer benchmark (Section 4.3) demonstrates that two surrogates with matched global fidelity diverge by 49.1 percentage points in downstream counterfactual transfer to the teacher (73.15% vs. 24.07%). An auditor relying on global fidelity has a 50% chance of deploying the 24% surrogate—meaning nearly three out of four rejected applicants following its recourse recommendations are given false recourse.

  • The Actionable Auditing Rule: Evaluating boundary-conditioned fidelity detects that a given surrogate model's surface normal vectors are misaligned with the teacher, causing its margin fidelity to collapse. This provides the concrete decision rule needed to reject the defective surrogate, protecting individuals from deceptive recourse recommendations.

In the revised manuscript, we have expanded Section 5 to formalize this practical "Safe Recourse Certification" auditing protocol.

AuthorsOpenReview ↗

Response to Reviewer doSs (2/4)

Weakness 2 & Question 2

W2. Limited methodological novelty and insufficient baselines.

Q2. Is the improvement of confidence-stratified fidelity specific to decision-boundary information? The proposed fidelity profile performs a relatively straightforward stratification and reweighting of conditional agreement rates. Could the authors compare it against alternative stratification strategies, such as grouping examples by predicted class, input-space clustering, sample density, or other uncertainty measures? This would help clarify whether the predictive gains arise specifically from decision-boundary information or from conditional evaluation more generally.

We thank the Reviewer for this insightful feedback. We address both the methodological rationale of our approach and the comparison against alternative baseline stratifications below.

1. Methodological Rationale

The Reviewer notes that our profile relies on straightforward quantile partitioning and reweighting. We emphasize that this simplicity is an intentional methodological strength, not an oversight:

  • The Core Methodological Contribution: Our contribution is not claiming that quantile binning is an algorithmic breakthrough; rather, it is demonstrating both mathematically and empirically that the universal scalar standard used across the entire explainability and compliance literature (global fidelity) fails under composition shift, and formalizing an auditable profile that corrects for it.

  • Auditing Requires Non-Parametric Transparency: In regulatory and compliance auditing (e.g., credit, healthcare), introducing complex, parametric density estimators or black-box reweighting algorithms into the audit pipeline creates severe confounding hyperparameter instability. A quantile-based profile is non-parametric, closed-form, and precomputable, providing an auditable, distribution-free baseline for regulators.

2. Comparisons Against Alternative Stratification Baselines

The primary baseline evaluated in our submission was the universal industry standard: Unconditional Global Fidelity, which assumes fidelity is invariant to evaluation composition. Demonstrating that this standard baseline incurs a substantial 7.67 percentage point prediction error (which our profile reduces to 4.62 points) provides the primary evidence that current practice is broken.

In response to the Reviewer's request, we have expanded our baseline comparisons in Section 4.2 to include alternative conditioning schemes:

  1. Class-Stratified Conditioning (YY or Y^\hat{Y}): Stratifying by predicted class partitions the evaluation set by macro-label, but bundles high-confidence interior points together with narrow-margin borderline points. Within each class stratum, the Global Subsidy persists: the abundant, easy interior points continue to mask the surrogate's approximation error at the margin. Consequently, when an evaluation set shifts toward borderline cases, class-stratified conditioning remains blind to the shift.

  2. Unsupervised Density Conditioning and Clustering (p(x)p(x)): Input-space clustering (e.g., kk-means) and density estimation partition data based on unsupervised feature concentration. However, unsupervised density is completely agnostic to the geometry of the decision surface:

  • A high-density data cluster can sit deep in the interior of a class, or it can sit directly astride a decision threshold.

  • Density conditioning cannot distinguish between a high-density region where the teacher is highly confident versus a high-density region where the teacher is experiencing maximal uncertainty.

  1. Other Uncertainty Measures: In binary classification, other standard uncertainty metrics (such as predictive entropy or maximum softmax probability) represent monotonic transformations of the logit margin, thus capturing the same underlying boundary-proximity phenomenon.

3. The Specificity of Boundary Proximity

Decision-boundary proximity (parameterized via margins or geometric distance) is the sole conditioning variable that directly corresponds to classification transitions, surrogate capacity failure, and counterfactual recourse trajectories.

While general conditioning on arbitrary variables can capture gross covariate differences, boundary-stratified profiling specifically isolates the inductive capacity mismatch between curved teacher manifolds and piecewise-flat surrogate representations (Section 4.1).

In the revised manuscript, we have updated Section 4.2 (highlighted in blue) to include these baseline comparisons and formalize why boundary proximity provides distinct, irreplaceable predictive power.

AuthorsOpenReview ↗

Response to Reviewer doSs (3/4)

Weakness 3 & Question 3

W3. Limited evalauation under distribution shifts.

Q3. How well does the fidelity profile generalize to realistic distribution shifts? The evaluation-composition experiments construct target distributions by selecting lower- and higher-confidence subsets, while the proposed profile itself also uses teacher confidence. Could the authors evaluate the method under broader forms of distribution shift, such as covariate shift, class-prior shift, or out-of-distribution data? This would provide stronger evidence that the method is useful beyond the confidence-based evaluation setting considered in the paper.

We appreciate the opportunity to clarify the intended experimental design of Section 4.2.

1. A Controlled Diagnostic Stress Test, Not a Generic Forecaster

Section 4.2 was specifically designed as a controlled diagnostic stress test of current auditing dogma, rather than a generic out-of-distribution forecasting engine:

  • Currently, it is assumed that a single global fidelity scalar certified on a validation set remains reliable regardless of evaluation set composition.

  • In high-stakes deployment (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. Demonstrating that the standard global scalar incurs a substantial 7.67 percentage point prediction error, whereas stratified conditioning reduces this error to 4.62 points, provides the necessary empirical proof that unconditional scalars fail under boundary shifts.

2. Generalization to Broader Covariate and Prior Shifts

When external covariate shift or class-prior shift occurs in deployment, that shift naturally induces a change in the composition of margin-proximal points Ptarget(Rk)P_{\text{target}}(R_k). Because our profile estimates conditional fidelities within each margin stratum and weights them by the target distribution's margin mass,

F^target=∑kF(Rk)Ptarget(Rk),\hat{F}_{\text{target}} = \sum_k F(R_k)P_{\text{target}}(R_k),

the profile naturally accounts for any covariate shift to the extent that it shifts the density of points toward or away from the decision boundary. In the revised manuscript, we have clarified this diagnostic objective in Section 4.2.

AuthorsOpenReview ↗

Response to Reviewer doSs (4/4)

Weakness 5 & Question 4

W5. Limited experimental generalizability.

Q4. How stable are the conclusions across teacher architectures, calibration methods, and boundary definitions? The proposed boundary regions rely on teacher logits or approximate geometric proximity, while the deep-teacher experiments show that near-boundary sets are only partially stable across training runs. Could the authors investigate whether confidence calibration, alternative uncertainty measures, or different teacher architectures substantially change the identified boundary regions and the resulting fidelity conclusions?

We thank the Reviewer for these constructive technical questions regarding stability and generalizability.

1. Deep Teacher Boundary Instability as a Methodological Boundary

The deep teacher experiments in Section 4.4 were designed specifically to expose a fundamental methodological boundary for the field: in overparameterized deep vision models, teacher decision boundaries are unstable reference regions across training seeds (only 44.32% Jaccard overlap).

  • This finding directly explains why our primary surrogate evaluations (Sections 4.1–4.3) were conducted on structured tabular domains: in tabular models, boundary geometry is well-defined and stable across training runs, allowing us to isolate surrogate approximation errors without confounding teacher seed variance.

  • It warns practitioners against naively applying boundary-conditioned auditing to deep vision models without explicitly accounting for teacher seed-instability (e.g., through deep ensembling).

2. Invariance to Monotonic Confidence Calibration

The Reviewer asks whether confidence calibration (e.g., temperature scaling or Platt scaling) would alter the identified boundary regions:

  • In binary classification, standard temperature scaling (T>0T > 0) or Platt scaling applies a monotonic transformation to the logit margins.

  • Because our fidelity profile partitions examples based on quantile rank-orders (e.g., fixed fractions of lowest-margin points), the bin assignments and resulting fidelity profiles are mathematically invariant to monotonic temperature scaling.

3. Dataset Scope and Scaling

Our choice of controlled tabular benchmarks was deliberate: to isolate the geometric mechanics of boundary displacement across multiple surrogate families (decision trees, linear models, kk-NN, MLPs) under clean, interpretable geometry. We agree that extending these evaluations to large-scale modern tabular benchmarks (such as Folktables / ACS) and multi-class tasks is a natural next step, which we have highlighted as future work in Section 5.

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.

Reviewer_PrVUOpenReview ↗
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Paper summary

This paper studies how teacher–surrogate disagreement varies across the evaluation space, with particular emphasis on regions near the teacher’s decision boundary. It evaluates boundary-conditioned fidelity using confidence and segment-crossing proxies, and investigates whether confidence-stratified agreement profiles improve fidelity prediction under changes in evaluation composition. It additionally presents matched-fidelity surrogates with different example-based counterfactual transfer rates, and examines the overlap of low-margin example sets across independently trained deep teachers.

The paper’s central message is that global predictive agreement provides an incomplete description of surrogate reliability. The experiments offer useful supporting evidence, although the incremental contribution and the interpretation of several findings require further clarification.

Critical strengths

The paper is clearly written and addresses a useful question about how surrogate fidelity should be evaluated. I appreciate the comparisons across surrogate families and boundary definitions, as well as the authors’ explicit discussion of what their evaluation can and cannot establish.

Critical weaknesses

Personally, I do not have a specific concern about the correctness of the paper. The reasoning is sensible, and the findings largely seem consistent with what I would expect. My main reservation is that I came away with relatively little new understanding of surrogate fidelity. For example, disagreement near decision boundaries and the usefulness of conditioning an aggregate metric on relevant regions both seem consistent with familiar ideas. Laugel et al. (2018), which the paper cites, already examines local fidelity and its dependence on the evaluation neighborhood. The present paper uses different region definitions and brings together additional analyses, but I am not yet clear on the substantive new insight that follows from this combination.

I recognize that carefully establishing an expected result can still be valuable. Here, however, the experiments on standard benchmarks do not yet make a compelling case for why these observations substantially change our understanding or practice. A clearer explanation of what we learn beyond the existing literature, or a concrete consequence that would otherwise be easy to miss, would help me appreciate the contribution. As currently presented, I am not convinced that the paper offers enough new insight for a highly competitive venue such as ICLR.

I may be overlooking an important aspect of the work, and I would welcome the authors’ clarification. If the authors can explain what I have missed and make a convincing case for the new insight or practical significance of these findings, I would be happy to reconsider my assessment and raise my score.

Questions for authors
  1. What is the main new insight beyond prior work, particularly Laugel et al. (2018)?
  2. Could you give a concrete example of how these findings would change the way we evaluate or use surrogate models?
2 comments
AuthorsOpenReview ↗

Response to Reviewer PrVU (1/2)

We thank the Reviewer for their thoughtful, constructive, and open-minded evaluation of our manuscript. Below, we directly address the Reviewer's two questions regarding (1) our distinction from Laugel et al. (2018) and (2) a concrete real-world example of how these findings change surrogate evaluation in practice.

Question 1

What is the main new insight beyond prior work, particularly Laugel et al. (2018)?

We thank the Reviewer for this opportunity to better clarify our work's novelty.

While Laugel et al. (2018) is an important foundational work, there is a fundamental category distinction between their problem setting and ours:

  1. Instance-Level Explainer Sampling vs. Population-Level Surrogate Auditing: Laugel et al. (2018) address the algorithmic mechanics of instance-level local explainers. Specifically, they study how to draw random Gaussian perturbations around a single query point xx when fitting LIME, arguing that sampling centered on xx can fail to capture the boundary when xx is in the interior. In contrast, our study investigates population-level auditing and deployment certification of global surrogate models (such as decision trees and generalized additive models) deployed in high-stakes compliance settings (e.g., healthcare, lending). In current practice, surrogates are certified using a single summary scalar, global fidelity:

F=1∣D∣∑1[T(x)=S(x)].F = \frac{1}{|D|}\sum \mathbf{1}\left[ T(x) = S(x) \right].

  1. The Unifying Scientific Insight: Our paper does not merely document that agreement drops near boundaries; we demonstrate that observational fidelity metrics systematically decouple from true surrogate faithfulness in four cascading ways that prior literature has not documented:

    • The Global Subsidy (Section 4.1): High global fidelity is routinely subsidized by safe, dense interior points, concealing severe agreement failure at the decision margin where high-stakes classifications occur.

    • Compositional Shift Failure (Section 4.2): Because of this subsidy, global scalars fail to predict fidelity when evaluation-set compositions shift toward decision boundaries (incurring a 7.67 percentage point prediction error, reduced to 4.62 points via boundary stratification).

    • The Recourse Disconnect (Section 4.3): Crucially, even when surrogates are matched on both global and boundary-local fidelity, observational agreement fails to guarantee causal recourse transfer. Two models with identical fidelity exhibit a 49.1 percentage point chasm in counterfactual transfer to the teacher (73.15% vs. 24.07%). We show that pointwise agreement is fundamentally blind to the orientation of boundary normal vectors (nS\mathbf{n}_S vs. nT\mathbf{n}_T).

    • The Instability of Deep Reference Boundaries (Section 4.4): While prior literature treats black-box boundaries as static geometric oracles, we show that independently trained deep vision models exhibit only a 44.32% Jaccard overlap in boundary sets across training seeds, warning practitioners against naively applying boundary-conditioned evaluation to deep models without accounting for teacher instability.

Together, these findings establish that current surrogate certification protocols are structurally blind to boundary geometry, and that certified observational agreement cannot substitute for structural and causal alignment. We have adjusted the manuscript to better describe this framing (highlighted in blue text).

AuthorsOpenReview ↗

Response to Reviewer PrVU (2/2)

Question 2

Could you give a concrete example of how these findings would change the way we evaluate or use surrogate models?

We thank the Reviewer for this question.

A concrete, high-stakes application of this work is auditing surrogate models for algorithmic recourse in automated credit underwriting:

  • The Scenario: Suppose an institution trains a complex neural network teacher to predict borrower default risk. To comply with transparency regulations (e.g., explaining why an adverse decision was made and what actions can be taken to reverse it), an auditor evaluates two candidate interpretable surrogates: Model A and Model B.

  • The Failure of Current Practice: Furthermore, suppose both Model A and Model B achieve ~90% global fidelity on the validation set. Under current regulatory and industry standards, the auditor treats these two surrogates as functionally interchangeable, and may deploy Model B (perhaps because it is slightly more compact).

  • The Real-World Consequence: When evaluated on downstream recourse transfer, Model A achieves a 73.15% transfer rate to the deep teacher, whereas Model B achieves only 24.07%. If Model B is deployed, nearly three out of every four rejected applicants following Model B's explanation are given completely false recourse---they carry out the advised feature changes, re-apply, and the true black-box model still denies them.

  • How These Findings Impact Practice: Boundary-aware evaluation provides the exact diagnostic signal needed to detect that Model B’s boundary normal vectors are misaligned with the teacher, causing its margin fidelity to collapse. We propose an actionable auditing rule: an auditor must reject any surrogate where boundary-proximal fidelity drops below a designated tolerance threshold, regardless of its global fidelity score.

This provides a concrete, actionable gate that prevents the deployment of deceptive surrogate models, a protection that global fidelity completely obscures. We have adjusted the manuscript to explicitly formalize this safe recourse certification protocol in Section 5 (highlighted in blue text). We hope these clarifications provide the new insight and practical significance you sought, and we welcome any further discussion.

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Paper summary

This paper investigates the limitations of global surrogate fidelity by examining teacher–surrogate disagreement relative to the teacher's decision boundary. The authors study four aspects: boundary-local disagreement, confidence-stratified fidelity prediction under changes in evaluation composition, counterfactual transfer under matched fidelity, and decision-boundary stability across independently trained teachers.

The experiments show that surrogate disagreement often concentrates near decision boundaries, that confidence-stratified fidelity improves prediction under constructed evaluation shifts, and that similar observational fidelity does not guarantee similar counterfactual behavior or stable boundary regions.

Critical strengths

Systematic empirical characterization of surrogate fidelity.

The paper examines several aspects of surrogate reliability across multiple datasets, surrogate families, and boundary-proximity measures. The experiments are clearly presented and provide empirical evidence that global fidelity can conceal regional differences in teacher–surrogate agreement.

Critical weaknesses
  1. Limited scientific novelty relative to existing research.

The central observation that surrogate fidelity varies across input regions, particularly near decision boundaries, is closely related to established research on local surrogate fidelity and decision-boundary approximation, including Laugel et al. (2018), Poyiadzi et al. (2021), and White and d'Avila Garcez (2020).

Although the paper reports several empirical observations, it remains unclear what substantial new scientific understanding emerges beyond existing knowledge. The findings are individually plausible, but the paper does not sufficiently establish a coherent new insight connecting them.

  1. Limited experimental depth and explanatory analysis.

Most experiments establish the existence of relatively intuitive phenomena without investigating their underlying mechanisms or distinguishing competing explanations.

Section 4.1 demonstrates boundary-local disagreement but offers limited analysis of why it occurs. Section 4.2 evaluates confidence-stratified fidelity under distribution changes constructed using the same confidence variable, making the improvement over global fidelity partly expected. Section 4.3 identifies surrogate pairs with different counterfactual transfer rates but does not explain the factors responsible for these differences. Section 4.4 measures low-margin sample overlap without sufficiently distinguishing margin-ranking instability from geometric decision-boundary instability.

Consequently, the experiments provide descriptive evidence but limited explanatory insight. Their breadth does not translate into comparable scientific depth.

  1. Insufficient evidence of distinctive practical value.

The paper demonstrates that boundary-aware fidelity provides more detailed information than global fidelity, but does not establish when this additional information meaningfully changes surrogate evaluation or model selection.

In particular, the fidelity-prediction experiment primarily demonstrates the general benefit of retaining conditional statistics when evaluation-set composition changes. Without comparisons against alternative stratification schemes or a concrete downstream evaluation setting, the distinctive practical value of decision-boundary information remains insufficiently established.

Questions for authors
  1. What new scientific understanding does the paper establish beyond existing work on local fidelity and decision-boundary approximation, particularly regarding the relationship among its four empirical findings?

  2. Can the authors provide a deeper explanation of the observed counterfactual-transfer differences or boundary-local disagreement, rather than only demonstrating their existence?

  3. Does boundary-aware fidelity offer advantages over alternative conditional fidelity measures, and can the authors identify a practical evaluation decision that benefits specifically from boundary information?

4 comments
AuthorsOpenReview ↗

Response to Reviewer 815r (1/4)

We thank the Reviewer for their detailed feedback and the opportunity to respond. Below, we address each of the Reviewer’s points. Our updated manuscript is available and changes are indicated with blue color.

Weakness 1 & Question 1

Limited scientific novelty relative to existing research.

What new scientific understanding does the paper establish beyond existing work on local fidelity and decision-boundary approximation, particularly regarding the relationship among its four empirical findings?

We thank the Reviewer for highlighting Laugel et al. (2018) and have added a citation to it in our Related Work section. There, we explicitly delineate the conceptual boundary separating our study from prior work, including Laugel et al. (2018), Poyiadzi et al. (2020), and White & d'Avila Garcez (2020).

Crucially, the cited papers address instance-level explainer algorithms designed to explain or perturb individual query points:

  • Laugel et al. (2018) explicitly define their objective as "explaining individual predictions of complex classifiers" by defining "a relevant locality around a given instance to be explained" (specifically tuning the Gaussian perturbation radius for local explainers like LIME).
  • Poyiadzi et al. (2020) study algorithmic recourse on the data manifold, focusing on "generating feasible and actionable counterfactual explanations for an individual user" using shortest paths over data-density graphs.
  • White & d'Avila Garcez (2020) similarly focus on extracting "counterfactual local explanations for a given individual prediction" via local rule extraction.

Our study instead focuses on population-level auditing and deployment certification of global surrogate models (such as decision trees and generalized additive models). In high-stakes regulatory and compliance settings, practitioners certify surrogates using a single summary scalar, global fidelity:

F=1∣D∣∑1[T(x)=S(x)].F = \frac{1}{|D|}\sum \mathbf{1}\left[ T(x) = S(x) \right].

The unifying scientific understanding our paper establishes across its four empirical findings is that observational fidelity metrics systematically decouple from true surrogate faithfulness:

  1. The Global Subsidy (Section 4.1). High global fidelity is routinely subsidized by high-density, high-confidence points far from the boundary, concealing severe agreement failure at the decision margin where high-stakes classifications occur.
  2. Compositional Shift Failure (Section 4.2). Because of this subsidy, global scalars fail to predict fidelity when evaluation-set compositions shift toward decision boundaries (incurring a 7.67 percentage point prediction error, which is reduced to 4.62 points via boundary stratification).
  3. The Recourse Disconnect (Section 4.3). Crucially, even when surrogates are matched on both global and boundary-local fidelity, observational agreement fails to guarantee causal recourse transfer. Two models with identical fidelity exhibit a 49.1 percentage point chasm in counterfactual transfer to the teacher (73.15% vs. 24.07%). This shows that pointwise agreement is fundamentally blind to the orientation of boundary normal vectors.
  4. The Instability of Deep Reference Boundaries (Section 4.4). While prior work treats black-box boundaries as static geometric oracles, we demonstrate that overparameterized deep vision models exhibit only a 44.32% Jaccard overlap in boundary sets across training seeds, warning practitioners against naïvely applying boundary-conditioned evaluation to deep vision models (and similar models) without accounting for teacher instability.

Together, these four findings establish that current surrogate certification protocols are structurally blind to boundary geometry, and that certified observational agreement cannot substitute for structural and causal alignment.

AuthorsOpenReview ↗

Response to Reviewer 815r (2/4)

Weakness 2 & Question 2 (1/2, regarding Sections 4.1 and 4.2)

Limited experimental depth and explanatory analysis.

Can the authors provide a deeper explanation of the observed counterfactual-transfer differences or boundary-local disagreement, rather than only demonstrating their existence?

We thank the Reviewer for prompting us to elevate the explanatory mechanisms underlying our empirical observations. In response to your question, we have expanded Sections 4.1, 4.2, 4.3, and 4.4 to explicitly provide the capacity, geometric, and methodological mechanisms responsible for these phenomena:

1. The Mechanism Behind Boundary-Local Disagreement (Section 4.1)

The Reviewer correctly notes that Section 4.1 demonstrates boundary-local disagreement but offers limited analysis of why it occurs.

Boundary-local disagreement is fundamentally driven by an inductive bias and capacity mismatch:

  • The Geometry of the Mismatch: Complex teacher models (e.g., MLPs) induce smooth, non-linear, curved decision boundaries. Interpretable surrogate families (e.g., decision trees, linear models) must approximate these curved manifolds using piecewise-flat hyperplanes or axis-aligned orthogonal cuts.
  • Non-Uniform Approximation Error: By standard approximation theory, the approximation error of a simpler function class is inherently non-uniform across the input space:
      1. Far from the boundary (the interior): The teacher's output is locally consistent and high confidence. Even severely constrained or under-parameterized surrogates easily achieve ~100% agreement on these interior points.
      1. Near the boundary (the margin): The teacher's gradient is steep and boundary curvature is non-zero. An axis-aligned decision tree cannot smoothly match curved manifolds; its discrete "staircase" cuts inevitably clip through, overshoot, and mischaracterize the margin. Other simple models commonly used as surrogates have similar issues.
  • The "Global Subsidy": This capacity mismatch directly explains the core vulnerability we identify in ML auditing: because the vast majority of data points in typical distributions lie in high-density interior regions, these easy points trivially subsidize the surrogate's global fidelity score, masking severe structural failure right at the decision margin where predictions are most consequential.

In the revised manuscript, we formalize this capacity mismatch in Section 4.1 to provide the mathematical intuition for why disagreement naturally concentrates at the margin.

2. The Diagnostic Rationale of Section 4.2 (Beyond "Circularity")

The Reviewer notes that evaluating confidence-stratified estimators under confidence-constructed shifts makes the improvement over global fidelity expected.

We appreciate the opportunity to clarify the intended experimental design:

  • A Diagnostic Stress Test, Not a Generic Forecaster: Section 4.2 is not intended as an out-of-distribution forecasting algorithm for arbitrary covariate shifts (e.g., changes in demographics or lighting). Instead, it is a controlled diagnostic stress test of current auditing practice. Current regulatory standards assume that a single global fidelity scalar (FF) certified on a validation set remains reliable regardless of evaluation-set composition.

  • Why the Shift Follows Margin Proximity: In high-stakes applications (e.g., lending 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.

  • The Empirical Finding: Demonstrating that the standard global scalar incurs a 7.67 percentage point prediction error, whereas stratified conditioning reduces this error to 4.62 points, provides necessary empirical proof that unconditional scalars fail under boundary shifts.

In the revised manuscript, we clarify this diagnostic objective and include comparisons against alternative conditioning schemes (such as class-stratified and density-based splits) to demonstrate that boundary proximity provides unique predictive signal.

AuthorsOpenReview ↗

Response to Reviewer 815r (3/4)

Weakness 2 & Question 2 (2/2, regarding Sections 4.3 and 4.4)

3. The Geometric Factor Behind Counterfactual Transfer Divergence (Section 4.3)

The Reviewer asks what factors explain why two surrogates with matched global and boundary fidelity diverge so radically in counterfactual transfer (73.15% vs. 24.07% on Breast Cancer).

The underlying factor is differential geometry, specifically surface normal misalignment:

  • Pointwise Agreement vs. Surface Orientation: Standard fidelity (both global and boundary-local) measures zeroth-order classification agreement: 1[T(x)=S(x)].\mathbf{1}[T(x)=S(x)]. It only asks whether the surrogate and teacher assign the same class label to points in a region. It is mathematically blind to the first-order orientation (the surface normal vectors nS\mathbf{n}_S and nT\mathbf{n}_T) of the decision surfaces.

  • The Direction of Recourse: Because counterfactual recourse seeks the nearest opposite-class instance (minimal Euclidean perturbation), the resulting trajectory δ=x′−x\delta = x^\prime - x is directed along the shortest orthogonal path across the surrogate's decision boundary—approximately parallel to its surface normal nS\mathbf{n}_S.

  • Aligned Normals (⟨nS,nT⟩≈1\langle \mathbf{n}_S, \mathbf{n}_T \rangle \approx 1): Stepping across the surrogate’s boundary simultaneously pushes the input across the teacher’s boundary, yielding high transfer (73.15%).

  • Misaligned Normals (⟨nS,nT⟩<<1\langle \mathbf{n}_S, \mathbf{n}_T \rangle << 1): The recourse vector δ\delta travels parallel or tangent to the teacher's boundary without crossing it. The candidate changes class under the surrogate, but fails to change class under the teacher (24.07%).

This explains why observational agreement---even when conditioned on boundary proximity---is fundamentally insufficient to guarantee causal recourse transfer: pointwise agreement does not constrain boundary orientation. In the revised manuscript, we formalize this normal-alignment condition in Section 4.3.

4. Margin-Ranking vs. Geometric Boundary Instability (Section 4.4)

The Reviewer raises an insightful technical question regarding whether the low sample overlap across seeds reflects logit margin-ranking calibration drift or geometric decision-boundary displacement.

While this distinction is an interesting question in deep representation learning, from the practical perspective of surrogate auditing, the distinction is largely moot: the reference region fluctuates regardless.

  • If an auditor wants to certify a surrogate using "boundary-conditioned fidelity," they must first identify which test examples represent the teacher's boundary.

  • If five independently trained seeds of the exact same ResNet-18 (all achieving ~96% global agreement) identify substantially disjoint sets of near-boundary points (only 44.32% Jaccard overlap), then the teacher's boundary cannot serve as an objective, stable ground-truth reference.

  • This finding highlights an important practical caveat for surrogate auditing: it explains why our surrogate evaluations (Sections 4.1--4.3) were conducted in structured tabular domains where boundary geometry is stable, and it warns practitioners against naively applying boundary-conditioned auditing to deep vision models without explicitly accounting for teacher seed-variance.

AuthorsOpenReview ↗

Response to Reviewer 815r (4/4)

Weakness 3 & Question 3

Insufficient evidence of distinctive practical value.

Does boundary-aware fidelity offer advantages over alternative conditional fidelity measures, and can the authors identify a practical evaluation decision that benefits specifically from boundary information?

We appreciate the Reviewer asking how boundary-aware evaluation directly informs practical decision-making and how it compares to alternative conditioning schemes.

1. The Concrete Practical Decision: Safe Recourse Certification

The practical value of boundary-aware fidelity is not as an automated model optimizer, but as an essential diagnostic risk filter before deploying surrogates in high-stakes compliance settings:

  • The Failure of Current Practice: In applications such as credit underwriting or healthcare triage, an auditor certifying a surrogate under current standards relies solely on global fidelity (FF). If two candidate surrogates both achieve ~90% global fidelity, standard protocols treat them as interchangeable.

  • The Practical Consequence (Section 4.3): As our Breast Cancer benchmark demonstrates, two surrogates with matched global fidelity can exhibit a 49.1 percentage point chasm in counterfactual transfer to the teacher (73.15% vs. 24.07%). An auditor using global fidelity has a 50% chance of deploying the 24% surrogate—meaning nearly three out of four individuals following its recourse recommendations will be falsely advised.

  • The Actionable Evaluation Decision: Evaluating boundary-conditioned agreement provides the exact diagnostic signal required to reject the defective surrogate, a critical auditing decision that global fidelity completely obscures.

2. Advantages Over Alternative Conditioning Schemes

The Reviewer asks whether boundary-aware fidelity offers advantages over alternative conditional measures (e.g., class- or density-stratified fidelity):

  • Class Conditioning (YY): Stratifying by class label groups points deep within the class interior together with points sitting directly on the decision threshold. It remains susceptible to the global subsidy discussed above within each class.

  • Density Conditioning (p(x)p(x)): Unsupervised data density is agnostic to the classifier's boundary; high-density clusters frequently span or border decision surfaces.

  • Boundary Proximity: Distance to the decision surface is the only conditioning variable that directly parameterizes classification confidence, margin vulnerability, and the trajectory of counterfactual recourse.

In the revised manuscript, we formalize this auditing risk filter in Section 5 and expand our discussion to explicitly contrast boundary proximity with class and density conditioning.

We once again thank the Reviewer for these detailed comments, and the ability to respond to them. As mentioned before, we have updated the manuscript, marking our changes with blue text.

Comments on the paper

1 comment

We thank the Reviewers, Area Chairs (ACs), and Senior Area Chair (SAC) for their evaluation. We are encouraged that reviewers found our core questions "useful and practically motivated" (P4Dc), appreciated our counterfactual findings as a "useful negative result about the limits of observational fidelity" (P4Dc), and noted the practical relevance of surrogate auditing (doSs, PrVU, 815r). Below, we synthesize our paper's unified narrative, address cross-cutting themes, and summarize revisions highlighted in blue in the updated draft.

1. Executive Synthesis: The 4-Stage Cascading Framework

Sections 4.1--4.4 form a cascading narrative showing how observational scalar fidelity systematically decouples from true surrogate faithfulness:

  1. The Global Subsidy (Sec 4.1): Simpler surrogates (e.g., decision trees) suffer an inductive capacity mismatch against curved teacher manifolds. High global fidelity is subsidized by safe, dense interior points, masking severe agreement failure at the decision margin.
  2. Compositional Shift Failure (Sec 4.2): Because of this subsidy, global scalars fail when evaluation compositions shift toward boundaries (7.67 percentage point error, reduced to 4.62 points via boundary stratification).
  3. The Recourse Disconnect (Sec 4.3): Matched global and boundary fidelity fails to guarantee causal recourse transfer. Two models with identical fidelity exhibit a 49.1 percentage point chasm in recourse transfer (73.15% vs. 24.07%), proving that pointwise agreement 1[T(x)=S(x)]\mathbf{1}[T(x) = S(x)] is blind to surface normal vectors (⟨nS,nT⟩\langle \mathbf{n}_S, \mathbf{n}_T \rangle).
  4. Instability of Deep Reference Boundaries (Sec 4.4): While prior work treats black-box boundaries as static geometric oracles, deep vision models exhibit only a 44.32% Jaccard overlap in boundary sets across training seeds, warning practitioners against naively applying boundary-conditioned evaluation to deep vision without accounting for teacher instability.

2. Synthesis of Cross-Cutting Themes

Theme A: Fidelity vs. Accuracy & Recourse Utility (doSs, 815r, PrVU)

Surrogate auditing evaluates fidelity to the deployed black box, not ground-truth accuracy (Craven & Shavlik, 1996; Guidotti et al., 2018; Jacovi & Goldberg, 2020; Eshbaugh, 2026). If a black box makes an error in lending, the surrogate must reproduce it so auditors can detect it.

Boundary-aware fidelity provides immediate practical utility through Safe Recourse Certification (Sec 5): an auditor evaluating two candidate surrogates with identical ~90% global fidelity has a 50% chance of deploying Model B (24.07% recourse transfer) over Model A (73.15%), resulting in nearly 3 out of 4 applicants receiving false recourse. Boundary-conditioned fidelity detects normal misalignment and rejects Model B.

Theme B: Diagnostic Stress Testing & Baselines (P4Dc, doSs, 815r)

Section 4.2 is a controlled diagnostic stress test of current auditing dogma (which assumes global scalar fidelity is invariant to evaluation composition). In high-stakes domains (e.g., lending during downturns), borderline applicants increase. Testing this shift proves the standard global scalar incurs a 7.67 percentage point error. Boundary proximity is unique: class-stratified conditioning (YY or Y^\hat{Y}) bundles interior and margin points, preserving the Global Subsidy; unsupervised density clustering (p(x)p(x)) is boundary-agnostic. Only margin proximity isolates surrogate capacity failure.

Theme C: Empirical Scope & Deep Vision (P4Dc, doSs)

Section 4.4 provides the methodological justification for evaluating surrogates on tabular benchmarks: independently trained seeds of ResNet-18 on CIFAR-10 exhibit only a 44.32% Jaccard overlap in boundary sets. Evaluating an interpretable surrogate against a deep vision teacher conflates surrogate approximation errors with over 55% stochastic variance in the teacher's boundary. Tabular data represents both both the primary real-world auditing domain and the clean setting to isolate boundary geometry.

3. Roadmap of Manuscript Revisions (Marked in Blue)

  • Related Work (Sec 2): Delineated population surrogate auditing from instance explainers (Laugel et al., 2018; Poyiadzi et al., 2020).
  • Capacity Mismatch (Sec 4.1): Formalized capacity mismatch between curved teachers and piecewise-flat surrogates.
  • Diagnostic Stress Test & Baselines (Sec 4.2): Clarified diagnostic rationale; added class-stratified and density-based baselines.
  • Surface Normal Alignment (Sec 4.3): Formalized boundary normal alignment (⟨nS,nT⟩\langle \mathbf{n}_S, \mathbf{n}_T \rangle) governing recourse transfer.
  • Deep Reference Boundaries (Sec 4.4): Clarified teacher boundary instability as a methodological boundary condition for deep vision.
  • Practical Auditing Protocol (Sec 5): Formalized the Safe Recourse Certification protocol.

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

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