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Under review as a conference paper at ICLR 2027

An Operator-Theoretic Characterisation of Label Noise Detection

Abstract

Label noise detectors inspect neighbours, model predictions, or training history, yet ask the same question: does a recorded label agree with evidence from other examples? Designing a detector means choosing what evidence to use, how examples interact, and how their agreement is judged. Exploring these choices through repeated experiments is expensive. We give a unified operator-theoretic characterisation that organises them into a common search space for detector design. The theory identifies the information needed to characterise a detector's response to a proposed change and bounds the error when its effect is approximated. This enables a constructive strategy: predict how alternatives will behave before fully evaluating them, and run exact experiments where uncertainty could change the choice. In experiments varying training and scoring while keeping features fixed, this strategy matches the selection accuracy of evaluating every alternative across all 18 cases, with up to speed-up over an optimised implementation. The result connects unification to algorithm design for label noise detection through a shared language for proposing changes and a principled way to make the search cheaper. Experimentation code: https://anonymous.4open.science/r/label-noise-operator-164B.

Primary area:
learning theory
Keywords:
Label Noise Detection, Operator Theory, Adaptive Configuration Search

Reviews

Among:
Shape:
1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_35JyOpenReview ↗
Rating
3
Confidence
2
Informativeness
3
Presentation
3
Soundness
3
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Paper summary

This paper focuses on the label noise detector design issue and formulates the detector design as common search space search. This paper also provides a characterization of exactly what information determines a detector's response to a proposed intervention, then a mechanism for turning that characterization into cheaper algorithm search. The three contributions 'Unified characterisation', 'Mechanism prediction' and 'Economical algorithm search' are tightly cooperated.

Critical strengths
  1. The source–operator–query decomposition is clean, genuinely unifying, and maps credibly onto the major detector families.

  2. Four Theorems are proposed to ensure the therotical proof of the solution.

  3. The experiment discussion are sufficient.

Critical weaknesses
  1. The evaluation datasets are small. More large-scale dataset is highly suggested. Also, the advantage of Economical algorithm search can be tested.

  2. In the related work section, the cited works are old. More recent works should be discussed.

  3. Overclaims issue. Some exepriment results can not support the claims in the abstract, such as "zero development regret under 0.1 pp tolerance" will not reassure a reader who cares about whether the selected detector actually generalizes.

Questions for authors

Some visualization results of the label denoising are suggested via the proposed method.

3 comments
AuthorsOpenReview ↗

Response to Reviewer 35Jy (Part 1/2)

We thank the reviewer for their constructive assessment and suggestions. We have revised the manuscript and updated the accompanying anonymous code package with the additional experiments and reproduction instructions. In particular, we have added larger-scale and broader search evaluations, strengthened the discussion of recent related work, clarified the connection between development-set selection and population performance, and included an image-level visualisation. We address each concern below.

Response to Weaknesses

W1. Scale, diversity and economical algorithm search. In direct response to this concern, we have conducted new large-scale experiments for this rebuttal on CIFAR-100N, using 40,000 training examples, all 100 classes and human-corrupted labels. Three fresh seeds and two candidate layouts give six search families, each containing 486 detector–training configurations. Screening, certified search and successive halving each recover all six exhaustive development optima with zero observed selection regret. This complements our existing 40,000-example Food-101N evaluation across all 101 classes.

The new rebuttal experiments directly measure the advantage of economical search against both optimised exhaustive evaluation and successive halving. Three clean paired repetitions on a predeclared CIFAR-100N case give median screening speed-ups of 13.57× over exhaustive evaluation and 6.67× over halving. Certified search achieves 7.71× and 3.79×, respectively. The existing large Food-101N experiment independently demonstrates a 6.83× certified speed-up over exhaustive evaluation.

For this rebuttal, we also completed a new 60-family robustness study across Dry Bean, PenDigits, Food-101N and human-noise CIFAR-10N, varying seeds, Cartesian and irregular candidate layouts, and 8–64 feature components. The unchanged four-trajectory screen recovers every development optimum. Searches vary detector readouts—loss and area under the margin—example weights, regularisation, learning rates and stopping times. Together with the propagation-selection study and the new controlled feature-learning extension, this consistency supports the generality of the information–prediction–selection approach across datasets and algorithmic mechanisms.

To extend the scale further, we are additionally in the process of evaluating the entire Food-101N dataset, which has more then 290,000 training examples covering all 101 classes -- over seven times our current largest training population. We will provide an update to our rebuttal once we have obtained the respective results. Together, these evaluations broaden the evidence across training populations, class counts, representations and candidate families. If the reviewer has further suggestions with regards to this point, we would welcome them.

W2. Recent related work. We have expanded and reorganised Section 7 to distinguish recent detector developments from broader frameworks that organise the detector algorithm space. The revised discussion includes model probing (George et al., TMLR 2024), which organises detector construction through models, probes, ensembles and aggregation, and ADGym (Jiang et al., NeurIPS 2023), which constructs and selects component-based anomaly-detection pipelines. We also added discussion of DynaCor (CVPR 2024) and LEMoN (ICML 2025) to connect this conceptual positioning to contemporary detector developments.

The distinction matters because our principal contribution concerns a characterisation of the algorithm space and a principled way to navigate it. Entirely new organising paradigms and unified characterisations are comparatively uncommon; newer individual detectors often develop particular mechanisms within an existing paradigm. Within this specific conceptual scope, our literature review has not identified a more recent direct precedent for the characterisation-to-search programme developed here.

To our knowledge, ours is the first unified operator-theoretic characterisation of label-noise detection that connects intervention-specific information requirements to reusable performance predictions and economical configuration selection with explicit selection-error control. The revised related-work discussion makes these connections and their relationship to existing approaches explicit.

We would welcome specific references the reviewer considers relevant, particularly newer organising frameworks, and would be pleased to discuss their relationship to our contribution.

AuthorsOpenReview ↗

Response to Reviewer 35Jy (Part 2/2)

W3. Development selection and generalisation. We have revised the abstract to state explicitly that the method matches “development-set selection accuracy”, identifying the objective on which the reported comparison is established. The revised search-cost table also distinguishes zero observed development regret from the prescribed 0.1-pp certification tolerance.

Matching exhaustive selection is useful for configuring a detector for the dataset under investigation. To address the additional question of population performance, we now make the statistical consequence explicit in Section 4 and Appendix J.1. For a fixed candidate family and an independent, representative development sample, simultaneous empirical–population AUROC error at most ϵ\epsilon gives

\leq \tau + 2\epsilon,$$ where $\tau$ is the computational selection regret and $2\epsilon$ is the statistical uncertainty. The uniform bound accounts for selection across the candidate family, including adaptive computational refinement. We state the sampling and independence assumptions explicitly; constructing additional candidates using development labels requires further statistical control. This connects our computational guarantee to population performance through standard model-selection reasoning. Please also see our response to Reviewer guvR, W3 and Q4, for further discussion of the statistical assumptions, control of development-set selection overfitting, and held-out evaluations. **We have also added substantial held-out evidence for this rebuttal.** Relative to the predefined interior reference configurations, the new 60-family study yields **59/60 positive held-out changes**, with median **$+2.334$ pp**. The new large-scale CIFAR-100N study yields **6/6 positive held-out changes**, with median **$+4.653$ pp**. These are dependent family-level comparisons that reuse datasets and partitions. The earlier mixed held-out outcomes remain reported. The revised manuscript therefore presents three complementary pieces of evidence: **computational accuracy relative to exhaustive selection, a population-regret consequence under stated assumptions, and measured held-out performance**. The abstract now describes the first precisely, while the main text provides the statistical connection and empirical transfer results. ### Response to Questions **Q1. Qualitative visualisation.** We have added a 16-image Food-101N illustration in **Appendix T.3, Figure 4**, showing how the selected configuration changes individual review decisions. **Review rank** orders images from most to least suspicious according to the detector’s score: rank 1 receives the highest review priority. With a review budget of 80 images, ranks 1–80 enter the review queue. Each arrow shows the rank under the reference configuration followed by the rank under the selected configuration upon applying our method. Recorded labels and their correctness statuses are supplied by Food-101N. The illustration contains four categories: - **Incorrect labels brought into review:** The first three columns of the top two rows show six annotation errors previously outside the review queue. For example, an image incorrectly labelled *crème brûlée* moves from rank **436 to 35**, while another incorrectly labelled *peking duck* moves from **286 to 56**. These errors become accessible within the same review budget. - **Incorrect labels narrowly missed:** The final column of the top two rows shows errors promoted to ranks **98 and 94**. Their priority improves, often quite significantly (from 168 and 225 respectively), but they remain just outside the queue. - **Correct labels removed from review:** The first three columns of the bottom two rows show six correctly labelled images no longer flagged. For example, a correctly labelled pancake image moves from **36 to 608**, and a correctly labelled chicken-curry image moves from **62 to 503**, avoiding unnecessary review. - **Correct labels still flagged:** The final column shows remaining false alarms near the cutoff, with modest rank changes of **78 to 70** and **68 to 63**. These examples make the practical consequence of configuration selection concrete: changing the configuration can surface previously missed annotation errors and release correctly labelled examples from unnecessary review. Together with the quantitative selection and timing studies, the panel illustrates what economical configuration search enables at the sample level, while also showing the mistakes that remain.
AuthorsOpenReview ↗

Large-scale Evaluation and Further Evidence on Held-out Generalisation

We have now completed the promised large-scale evaluation on the full Food-101N dataset, which comprises 310,009 images of which the train set has 294,851 images across all 101 classes and the remainder is split into development and test. This setting is this over seven times larger than the initial 40,000-example subset evaluated in the original submission. The results are incorporated into Section 5 and Appendix T.5, and the anonymous code package has been updated.

a. Selection accuracy at substantially larger scale

The full-population core study uses three fresh seeds and two candidate layouts, giving six search families, each containing 486 detector–training configurations. Screening, certification and optimised successive halving recover every exhaustive development optimum, with zero observed selection regret. The prescribed certification tolerance remains 0.1 pp.

These experiments use fixed image features and trainable multiclass prediction models. We additionally completed twelve full-population searches at 32 and 64 feature dimensions; point prediction, four-trajectory screening and halving again recover every optimum. Training uses recorded labels, with verification statuses reserved for evaluation.

b. Further held-out evidence at scale

Our previous responses introduced the population-selection analysis and expanded cross-dataset held-out evaluation. The new Food-101N study adds evidence at a substantially larger training scale.

Every configuration selected in the six full-population core families improves held-out detection AUROC over its predefined interior reference, with a median improvement of +5.301 pp. Configuration choices are fixed before held-out scores are evaluated.

These results extend the held-out evidence already reported for CIFAR-100N and the cross-dataset robustness study. The population bound and assumptions described in our previous responses continue to provide the statistical interpretation of selection.

c. Computational efficiency against stronger baselines

We compare our forecasting, screening and certified-selection procedures against optimised successive halving and exhaustive evaluation. The three variants of our method serve different purposes:

  • Point prediction chooses a promising training trajectory from inexpensive forecasts and then executes it.
  • Four-trajectory screening forecasts candidate performance, trains four promising trajectories and selects using their scores.
  • Certified selection additionally maintains performance bounds, refining comparisons or evaluating further trajectories until no alternative can improve upon the selected configuration by more than 0.1 pp, under the stated assumptions.

On a predeclared full-population case, three paired repetitions give:

Search policyRoleMedian search time
Point predictionOur simplest forecasting control8.022 s
Four-trajectory screeningOur economical search procedure9.104 s
Query-refined certificationOur certified search procedure15.349 s
Optimised successive halvingComparison baseline18.028 s
Optimised exhaustive evaluationExact reference baseline33.201 s

Our screening procedure is 1.99× faster than halving and 3.66× faster than exhaustive evaluation. Our certified procedure achieves corresponding speed-ups of 1.17× and 2.16×. Every repetition has zero observed development regret.

Point prediction remains cheapest; screening provides additional verification, while certification supplies explicit selection-error control. Appendix T.5 reports the complete accuracy–cost comparison.

Reviewer_guvROpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
1
Soundness
1
Read review
Paper summary

This paper proposes an abstract framework for describing the mechanisms underlying a broad range of label-noise detection methods. The framework represents detectors in terms of sources, interactions, and queries, and characterizes the information required to predict their responses to proposed interventions. It aims to provide a unified perspective on different forms of detector evidence and design choices.

The paper also develops computational procedures for efficient hyperparameter and detector-configuration selection, with its training-based implementation restricted to fixed-feature softmax regression. Candidate training trajectories are approximated using cached feature moments, reducing repeated computation while retaining the label-dependent gradient term exactly. In the two-stage screening procedure, these approximations predict candidates’ development-set performance; a shortlist of promising trajectories is then trained exactly, and the final configuration is selected from their evaluated readouts.

Separately, the certified procedure propagates approximation-error bounds through training and detector scoring to obtain development-set AUROC intervals. It adaptively refines unresolved comparisons, using exact evaluation when necessary, until the selected configuration is guaranteed to lie within a prescribed tolerance of the best candidate in the finite search family. This is a guarantee on development-set selection regret, rather than a generalization guarantee. Empirical studies examine selection accuracy, computational efficiency, and confidence-dependent failures of gradient-agreement detectors. The reported efficiency gains depend on the setting, and certification can incur substantial verification costs

Critical strengths
  • The approximate-gradient procedure is an interesting technique for accelerating the evaluation of candidate configurations.

  • The certified selection procedure provides a theoretical upper bound on development-set AUROC regret relative to the best candidate in the search family.

  • Section 6 contains insightful observations about the behavior and limitations of label-noise detectors.

Critical weaknesses
  • Presentation and clarity. The paper is difficult to follow, and several potentially valuable insights are obscured by the presentation. Concepts, terminology, and mathematical notation are frequently introduced without sufficiently clear definitions or explanations at the point of use. Many paragraphs present abstract statements before establishing their motivation or providing concrete examples. Transitions between paragraphs and sections are often abrupt, making the overall argument difficult to reconstruct.

  • Disconnect between the framework and the algorithmic contribution. The paper presents an ambitious unifying framework, but its practical value is insufficiently established. The concrete algorithmic contribution is comparatively clear: accelerating candidate evaluation through approximate training and controlling the resulting development-set selection regret. However, this contribution is embedded in an extensive abstract framework whose terminology and relationship to the algorithm are not adequately explained. Given the substantial existing literature on label noise and statistical learning, the paper should clarify what additional explanatory or algorithmic benefits the proposed framework provides. In particular, it is unclear which aspects of the algorithm follow substantively from the framework, rather than being independently motivated by the structure of Softmax regression.

  • Restricted applicability and scope of the guarantee. The training-based procedure is tailored to fixed-feature Softmax regression, which limits the breadth of the demonstrated algorithmic contribution relative to the generality of the framework. Its applicability to more complex models, particularly end-to-end neural networks, remains unclear. Furthermore, the selection-regret guarantee concerns a fixed development set that is also used for configuration selection. Although useful as a computational approximation guarantee, it does not establish generalization to unseen data or control potential overfitting to the development set.

Questions for authors
  • Definitions and notation. Could the paper provide clear, self-contained definitions of “source,” “intervention,” “query,” and “required changes” at their first occurrence? Please also explicitly define the objects and domains appearing in Equation (3), as well as π+\pi_+​ and π−\pi_- in Theorem 2. More generally, the notation and terminology would benefit from a systematic consistency check.

  • Data-generating assumptions and label ambiguity. What data-generating process underlies the framework, and how are clean and noisy labels formally distinguished? Does the analysis assume a unique deterministic clean label, or does it accommodate an intrinsically uncertain clean-label distribution? For example, how would an image containing both a dog and a bird be treated, and how is legitimate label ambiguity distinguished from corruption?

  • Value of the abstract framework. What is the substantive connection between the configuration-selection procedure and the proposed framework? Which algorithmic choices or guarantees are enabled by the framework, and what benefits does it offer beyond established statistical-learning formulations?

  • Broader applicability and generalization. Can the training-based procedure be evaluated beyond fixed-feature Softmax regression? Can the development-set selection guarantee be complemented by an analysis of population performance or overfitting induced by configuration search?

  • Efficiency–accuracy trade-off. Why does Table 3 report computational improvements without also reporting the corresponding selection regret? Reporting both would make it easier to assess whether the speedups preserve selection quality.

9 comments
AuthorsOpenReview ↗

Response to Reviewer guvR (Part 1/4)

We thank the reviewer for the careful review and constructive questions. We have revised the manuscript and updated the accompanying anonymous code package to address the concerns raised. The revisions clarify definitions and the framework–algorithm connection, add controlled information-retention and feature-learning studies, and make the population implications of the selection guarantee explicit. Changes in the manuscript are highlighted in blue, and the code package includes reproduction instructions for the new experiments. We respond point by point below.

Response to Weaknesses

W1. Presentation and clarity: We are currently in the process of revising the paper section by section to improve readability, presentation and clarity. The revision focuses on introducing concepts and notation before using them, motivating formal statements through concrete examples, and explaining how each paragraph and section advances the argument. We are also simplifying terminology and strengthening transitions between the characterisation, prediction and selection results. We will again update the paper with these changes shortly.

Several changes have already been made in response to the reviewers’ comments:

  • Definitions at first use: We now explain sources, propagation, queries and interventions when they first appear.
  • Explicit mathematical notation: We specify the dimensions and domains of the maps in Equation (3) and explain π+\pi_+ and π−\pi_- immediately before Theorem 2.
  • Clearer label semantics: We distinguish uncertainty in a legitimate annotation from corruption of its recorded label.

Beyond these specific corrections, we have made the constructive sequence explicit:

\;\longrightarrow\; \text{Predict intervention effects} \;\longrightarrow\; \text{Bound ranking uncertainty} \;\longrightarrow\; \text{Refine consequential comparisons}.$$ The new information-retention study (Section 5, under “Testing which information to retain”, with the main results in Table 2. Appendix T.1, “Intervention-aware retention at a fixed label-cache size”) provides a concrete illustration of this sequence. We are applying the same explanatory structure throughout the manuscript so readers can understand each result’s motivation and consequence before following its technical details. Beyond these, if the reviewer has specific concerns about the clarity of certain sections of the paper, we would be grateful if they could point it out so that we can do a more targetted revision. **W2. Disconnect between the framework and the algorithmic contribution:** Broadly, the framework enables a division between designing the detector algorithm space and navigating it efficiently. Researchers define and expand that space by proposing new detector constructions; the framework supports automated configuration selection through reusable predictions and targeted evaluation, reducing the need to run every candidate in full. Specifically, its practical contribution is to determine what information an intervention requires and how accurately its effects must be predicted for detector selection. Softmax regression supplies a tractable update equation, while polynomial approximate statistics provide an established computational tool through which we demonstrate these principles. **a. Intervention-aware information retention.** The softmax gradient identifies weighted label moments. Our characterisation establishes when retained statistics suffice for a declared intervention family and quantifies the ambiguity when they do not. A cache sufficient for the original run can therefore be insufficient for predicting a changed run. This criterion guides which additional statistics to retain. We now isolate this consequence in **Section 5, Table 2 and Appendix T.1**. At identical four-matrix capacity and with the approximation method fixed, intervention-aware retention reduces forecast error from **$0.70876$ to $0.00018$ pp** and improves point-selection optimum recovery from **$3/9$ to $9/9$**. Four-trajectory verification succeeds for every cache; the measured benefit concerns forecasts and point selection. **b. Detector-dependent refinement.** The training equation alone does not specify the approximation accuracy needed to preserve a detector ranking or configuration choice. The framework connects source and trajectory errors to the detector’s readout, AUROC uncertainty and selection regret. This supplies the refinement and stopping criterion: allocate exact computation to comparisons that could change the choice. Holding forecasts fixed, sharper bounds reduce additional exact trajectories from **$23$ to $1$**. These are the substantive connections to algorithm design: **retain information according to the intervention, and refine according to the detector-selection objective**. Polynomial degree and shortlist size remain implementation choices. [Continues in the next part.]
AuthorsOpenReview ↗

Response to Reviewer guvR (Part 2/4)

W2 continued. The framework also provides explanatory benefits beyond this implementation. Section 6 predicts confidence-dependent reversal versus invariance in gradient comparisons. As part of this rebuttal, we introduced Appendix U, which extends local prediction to learned representations, identifying evolving Jacobians and neural curvature as additional response information; retaining them improves forecasts in all twelve learned-feature families.

W3. Restricted applicability and scope of the guarantee. Below, we discuss how our evaluation protocols were motivated by standard practices in learning theory literature, which we chose to declare to make the scope of our work explicit for the sake of transparency. However, to address the reviewer's concerns, we have broadened the demonstrated applicability and clarified the relationship between the computational guarantee and statistical generalisation.

Applicability beyond fixed features.
The global training characterisation and its principal certified implementation concern fixed-feature softmax models. Studying such tractable regimes is established practice in learning theory, illustrated by NTK analyses and subsequent feature-learning limits (Jacot et al., NeurIPS 2018; Yang and Hu, ICML 2021).

So even though our results were initially demonstrated in the fixed feature regime, the significance of our work lies in establishing a principled route from a unified characterisation of label-noise detectors to economical configuration search, a possibility hitherto undemonstrated in existing literature. The fixed-feature setting makes these connections mathematically explicit and experimentally assessable, providing a foundation for extensions to learned representations.

As part of this rebuttal, we now additionally provide a local neural response derivation and controlled feature-learning study in Appendix U. Two-layer tanh networks train both layers on two datasets, across three seeds and two intervention radii. Hidden representations change by 125125–146%146\% of their initial norm, and tangent operators by 4949–78%78\%. Tracking evolving Jacobians and residual curvature improves forecasts in every learned-feature family; four exact trajectories recover 12/1212/12 optima, compared with 9/129/12 for halving. Matched frozen-layer controls agree as predicted. This establishes a controlled extension to learned representations; the neural screening results are empirical, and certification requires additional curvature control.

Generalisation and development-set overfitting.

The computational guarantee controls approximation to exhaustive selection on the development objective. This follows an established distinction in model-selection theory between computational accuracy in optimising validation performance and statistical accuracy in estimating population performance. For example, Oymak et al. (ICML 2021) connect approximate validation minimisation to population guarantees under sampling and regularity assumptions, while Makarova et al. (AutoML 2022) explicitly decompose population suboptimality into validation optimisation regret and statistical estimation error. Our analysis supplies the computational guarantee and composes it with statistical control under stated assumptions. For a fixed candidate family and an independent, representative development sample, simultaneous empirical–population AUROC error at most ϵ\epsilon gives

\leq \tau + 2\epsilon,$$ where $\tau$ is the computational selection regret and $2\epsilon$ is the statistical uncertainty. We now make this connection explicit in Section 4 and Appendix J.1, including the assumptions required to control selection overfitting. For $M$ candidate score functions fixed independently of a representative development sample containing $n_+$ corrupted and $n_-$ clean examples, simultaneous AUROC error is bounded, with probability at least $1-\delta$, by $$\epsilon= \sqrt{\frac12\left(\frac1{n_+}+\frac1{n_-}\right) \log\frac{2M}{\delta}}.$$ Consequently, empirical selection regret at most $\tau$ implies population regret at most $$\max_a A_a-A_{\widehat a}\leq \tau+2\epsilon.$$ This controls selection over the fixed family, including adaptive computational refinement. Constructing new candidates using development labels requires further statistical control; the bound can also be loose at the available sample sizes. We report held-out outcomes separately, retaining the earlier negative cases. The expanded 60-family study yields **$59/60$ positive held-out changes**, with median **$+2.334$ pp**. These dependent families provide additional transfer evidence alongside the explicitly stated statistical assumptions.
AuthorsOpenReview ↗

Response to Reviewer guvR (Part 3/4)

Response to Questions

Q1. Definitions and notation. We have revised the definitions at first use in the main development and clarified the distinction between a proposed change and the information needed to predict its effects.

Core terminology, Section 2.

  • Source: an example’s contribution to the evidence used by a detector, such as its recorded-label vector or prediction residual.
  • Intervention: a specified change to the detector or its training procedure, such as changing example weights, learning rate, neighbourhood scale or score readout.
  • Query: the rule that converts aggregated evidence into a detection score.
  • Required information: the information that must be retained to determine the response to a declared intervention or query. We distinguish this from the intervention itself and clarify ambiguous references to “required changes” accordingly.

Objects and domains in Equation (3).
At a fixed fitted state, zz denotes source-side features and uu indexes the requested query. With CC recorded-label classes,

A_{u,z}:\mathbb R^C\to\mathbb R^r,\qquad K_{u,z}:\mathbb R^m\to\mathbb R^r.$$ The $c$th column of $R_z$ encodes the source for recorded class $c$; the corresponding column of $A_{u,z}$ specifies its required contribution to query $u$. The factorisation $$A_{u,z}=K_{u,z}R_z$$ exists for every query precisely when $$\ker R_z\subseteq\bigcap_u\ker A_{u,z}.$$ Both kernels lie in $\mathbb R^C$: any label combination discarded by the source must be irrelevant to every requested evidence map. **Probabilities in Theorem 2.** Immediately before the theorem, we now define $\pi_+$ and $\pi_-$ as alternative conditional probabilities of the **same recorded class**, taking values in $[0,1]$ and agreeing on every retained statistic: $$\int v\,\pi_+\,d\mu=\int v\,\pi_-\,d\mu \qquad\text{for every }v\in V.$$ They represent two label distributions compatible with the retained information. We are also checking terminology, dimensions, indices and symbol reuse throughout the main text and appendix, including consistency between theorem statements, proofs and experimental descriptions. **Q2. Data-generating assumptions and label ambiguity.** The framework accommodates **an uncertain clean-label distribution**, while distinguishing that uncertainty from corruption of the recorded annotation. We consider **single-label multiclass classification**, as in standard label-noise formulations such as Confident Learning (Northcutt et al., JAIR 2021). Multilabel classification is beyond the scope of this work. **Data-generating process.** For an input $X=x$, a latent clean annotation is drawn according to $$Y^\star\mid X=x\sim\eta(x), \qquad \eta_c(x)=\Pr(Y^\star=c\mid X=x).$$ The recorded label is then generated through a potentially instance-dependent corruption process, $$T_{cr}(x)=\Pr(\widetilde Y=r\mid Y^\star=c,X=x).$$ The corruption indicator is $$D=\mathbf 1\{Y^\star\neq\widetilde Y\}.$$ Thus, $\eta(x)$ need not concentrate on one class: **a unique deterministic clean label is not assumed**. If $T(x)=I$, then $\widetilde Y=Y^\star$ and $D=0$, even when $\eta(x)$ is uncertain. **The dog-and-bird example.** The task’s annotation policy determines which single labels are legitimate—for example, labelling the most salient object. If either dog or bird is a legitimate annotation, $\eta(x)$ can assign positive probability to both. Recording the sampled clean annotation introduces no corruption. A task requiring both labels simultaneously would instead be a multilabel problem, and would hence lie beyond our scope. Specfically in our setting, corruption is defined by a change from the latent annotation $Y^\star$ to the recorded label $\widetilde Y$, under the task’s specified annotation policy. This distinguishes uncertainty in the clean annotation from the subsequent corruption process. Inferring that distinction from noisy observations requires additional information or identifiability assumptions, as studied by Liu et al., ICML 2023. These definitions appear in **Appendix I, “Latent Labels and the Oracle Query,”** with the distinction between annotation uncertainty and corruption now introduced in **Section 2**.
Reviewer_dqT6OpenReview ↗
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2
Confidence
2
Informativeness
3
Presentation
2
Soundness
2
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Paper summary

This manuscript proposes a label-noise detector through sources, propagation operators, and queries. For fixed-feature softmax training it characterizes the information needed to predict interventions, derives approximation bounds for configuration selection, and predicts a confidence-induced reversal in gradient agreement. Validation includes search on three datasets, propagation-selection studies, and frozen-feature mechanism tests.

Critical strengths

This paper explains what compression preserves or loses, while trajectory and AUROC bounds turn that analysis into a usable search procedure rather than a taxonomy alone. Besides, the experimental controls isolate useful mechanisms. Four-trajectory screening finds an optimum in all 24 prospective families at a median 5.49x exhaustive-search speed; holding forecasts fixed isolates the effect of tighter bounds. The separate AGRA comparison supports the normalization/reversal analysis.

Critical weaknesses

The practical value of this paper remains limited by its scope and experimental validation. Comparable savings are not established beyond fixed-feature, deterministic training, and the characterization’s necessity result does not establish minimal information requirements for the trajectories used in practice. The 24 search families share three datasets, a common configuration structure, and only two seeds, limiting evidence of broader transfer. Certified search is slower than successive halving on median and corrects no consequential selection errors, leaving its advantage over cheaper screening unclear. Development-AUROC guarantees also do not ensure held-out improvement, with declines of 2.13 and 2.45 percentage points relative to the reference. Finally, the ablations do not fully isolate the characterization’s incremental benefit over cached polynomial statistics combined with ordinary screening.

Questions for authors

Can quantities available before search identify when certification will outperform successive halving, including cases where wide uncertainty intervals make certification costly? What controlled comparison distinguishes the benefit of intervention-aware information retention from that of cached polynomial statistics combined with standard screening? How robust are optimal-configuration recovery and computational speed-ups to changes in the candidate grid or feature dimensionality beyond the tested experimental setup? What evidence supports expecting configurations selected for optimal development performance to improve label-noise detection on unseen examples?

6 comments
AuthorsOpenReview ↗

Response to Reviewer dqT6 (Part 1/3)

We thank the reviewer for their constructive assessment and specific questions. We have revised the manuscript and updated the accompanying anonymous code package with additional theoretical results, controlled experiments and reproduction instructions. In particular, we have added a trajectory-specific information characterisation, a matched information-retention study, broader seed and configuration coverage, larger-scale evaluations, and a controlled extension to learned representations. We address each concern below.

Clarification of the paper’s contribution. We would first like to clarify an important point in the summary: our contribution is an operator-theoretic characterisation of label-noise detection, rather than a new label-noise detector. Sources, propagation operators and queries describe how existing detectors construct and interpret evidence, providing a unified space in which to analyse detector behaviour and guide algorithm design.

The algorithmic contribution is economical configuration search within that space: identifying the information needed to predict proposed changes, reusing that information to forecast their effects, and directing exact computation towards comparisons that could affect the selected configuration. The confidence-reversal study provides a complementary explanatory consequence, showing how the characterisation distinguishes detector mechanisms and predicts their behaviour. We are revising the exposition to make this contribution hierarchy clearer throughout the paper.

Response to Weaknesses

W1. Applicability beyond fixed-feature, deterministic training. The global training characterisation and its principal certified implementation concern fixed-feature softmax models. This tractable setting makes the connection between information retention, intervention prediction and configuration selection mathematically explicit. Studying such regimes is established practice in learning theory, illustrated by NTK analyses and subsequent feature-learning limits (Jacot et al., NeurIPS 2018; Yang and Hu, ICML 2021).

For this rebuttal, we have added a local neural response derivation and controlled feature-learning study in Appendix U. Two-layer tanh networks train both layers on two datasets, across three fresh seeds and two intervention radii, with matched frozen-hidden-layer controls. Hidden representations change by 125–146% of their initial norm and tangent operators by 49–78%, confirming that we are operating in the feature learning regime.

Tracking evolving Jacobians and residual curvature improves forecast accuracy in all twelve learned-feature families. Four exact trajectories recover 12/12 development optima, compared with 9/12 for successive halving. Dedicated paired timings give approximately 1.92× speed-ups over exhaustive evaluation on both datasets; costs relative to halving are close to parity and setting-dependent. These additions establish a controlled extension to learned representations.

W2. Necessity for the trajectories used in practice. We agree that the original necessity statement concerns reproducing training responses across all initial states. We now state this scope explicitly and add a complementary query-specific characterisation along a fixed trajectory, summarised in Section 3 and developed in Appendix S.

For a binary logistic trajectory and a specified smooth detector readout, a discrete adjoint identifies a label test ψ\psi describing which label information influences that readout. If the retained tests span a closed space VV, and the nominal label probabilities lie in [r,1−r][r,1-r], the largest first-order response to information-preserving perturbations of size at most rr is exactly

r dist⁡L1(μ)(ψ,V).r\,\operatorname{dist}_{L^1(\mu)}(\psi,V).

Thus, retaining ψ\psi is necessary and sufficient for first-order determination of that query under the stated perturbations. A finite-change remainder provides score-error and pairwise-ranking control. An explicit example demonstrates that a particular query can require strictly less information than the full training map.

This result combines classical adjoint sensitivity with retained-information duality. Computing the required test uses the nominal trajectory and a reverse pass; its contribution here is a sharper information characterisation.

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Response to Reviewer dqT6 (Part 2/3)

W3. Limited seed, dataset, configurational coverage. We believe the reviewer is referring to our follow-up study comparing forecasting, screening and certified search. We ran this comparison on three datasets, with two random seeds per dataset and tested four intervention regimes, which varied the strength of the changes to example weights, regularisation and training duration. These combinations produced the 24 search families discussed in the review. This was separate from the earlier experiment evaluating certified selection, which used three seeds for each experimental setting and comprised 18 cases overall. Thus, the two-seed observation applies to the follow-up comparison, rather than to all experiments in the paper.

However, to address the reviewer's concern and to broaden evidence, we have completed a new 60-family study using three fresh seeds, Cartesian and irregular candidate layouts, and ten dataset–dimension settings: Dry Bean and PenDigits at 8/16 components, Food-101N at 8/16/32/64, and human-noise CIFAR-10N at 8/16. Candidate ranges are matched across layouts; partitions and recorded labels are matched across dimensions.

The unchanged four-trajectory screening rule recovers all 60 exhaustive development optima, as does halving. Cubic certification recovers all 24 predeclared eight-component optima. Three clean paired timings on each of six preselected families give median screening speed-ups of 5.44× over exhaustive evaluation and 2.83× over halving. Full protocols and outcomes appear in Appendix T.2.

We additionally evaluate 40,000 CIFAR-100N training examples, all 100 classes, three fresh seeds and two layouts in Appendix T.4. Screening, certification and halving each recover all six development optima. Timing repetitions are reported separately and are not counted as additional accuracy evaluations.

W4. Certification’s advantage over cheaper screening. The computational products serve different requirements. Screening uses forecasts to choose a small shortlist for exact evaluation; certification additionally supplies a prescribed bound on development-set selection regret. The initial 24-family study establishes that screening is economical, while certification’s additional verification cost can outweigh its savings. No point-selection error exceeding the prescribed 0.1-pp tolerance is corrected in that study.

The new larger-population CIFAR-100N experiment identifies a setting where certification is also economical: three paired repetitions on a predeclared case give certified speed-ups of 7.71× over exhaustive evaluation and 3.79× over halving, with zero observed regret.

The matched-bound experiment separately isolates the analysis’ contribution to verification cost. Holding every forecast fixed, sharper bounds reduce additional exact trajectories from 23 to one on Food-101N. The revision distinguishes forecast-based acceleration, the additional guarantee, and its measured computational cost.

W5. Development guarantees and held-out improvement. Our original objective was to establish how a characterisation of label-noise detectors can support economical search through their algorithm space. We therefore first studied whether intervention predictions could reproduce the configuration choice obtained by exhaustive evaluation, while reducing computation.

Generalisation beyond the development set introduces an additional statistical question: when does accurately selecting a configuration on the observed sample also identify a good configuration for the underlying population? Answering this requires assumptions about sampling, candidate construction and the relationship between development and future examples. We explicitly declared this distinction so that our computational guarantee would have a precise interpretation.

Separating optimisation accuracy from statistical estimation error is established practice in learning theory. For example, Oymak et al. (ICML 2021) study generalisation in train–validation architecture search, while Makarova et al. (AutoML 2022) distinguish validation optimisation error from uncertainty about population performance. These works provide useful foundations for developing the statistical consequences of our detector-specific search framework.

In response to the reviews, we have extended both the theoretical analysis and the held-out evaluation. Section 4 and Appendix J.1 now provide a population-selection consequence. For a fixed candidate score family and an independent, representative development sample, simultaneous empirical–population AUROC error at most ϵ\epsilon, together with development selection regret at most τ\tau, gives

\leq \tau + 2\epsilon,$$ where $\tau$ is the computational selection error and $2\epsilon$ is the statistical uncertainty. [This is not the end of this answer. It continues in the next part.]
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Response to Reviewer dqT6 (Part 3/3)

W5 contd. This controls population regret relative to the best candidate in the family. The uniform statistical bound accounts for selection across that family, including adaptive computational refinement.

We also conducted broader experiments for this rebuttal. Relative to predefined interior reference configurations, the new 60-family study yields 59/60 positive held-out changes, with median +2.334 pp. The new 40,000-example CIFAR-100N study yields 6/6 positive changes, with median +4.653 pp. These are dependent family-level comparisons, which signficantly outweigh the earlier negative outcomes, both in scale and variety.

Our central contribution remains the characterisation and its consequences for prediction and economical search. The revision now establishes an explicit statistical connection and broader empirical transfer evidence. A comprehensive treatment of increasingly adaptive detector design, development-data reuse and transfer across datasets forms a further research programme opened by this approach; the present results provide a concrete starting point for that development.

W6. Incremental benefit over polynomial caching and ordinary screening. We have added a matched information-retention experiment in Section 5, Table 2 and Appendix T.1, holding label-cache capacity and the approximation method fixed.

The original cache already preserves the information required by its original intervention family. We therefore introduce a third intervention direction and compare same-size four-matrix caches that retain either an unrelated direction or the newly required direction. All methods share feature approximation, initialisation, candidates and readouts.

Across nine fresh seeded cases on Dry Bean, PenDigits and Food-101N, intervention-aware retention reduces mean AUROC forecast error from 0.70876 to 0.00018 pp, improves point-selection optimum recovery from 3/9 to 9/9, and reduces maximum point-selection regret from 2.816 to zero pp. The retained statistics match richer-cache and direct-integration controls. Replacing polynomial feature integration with exact integration preserves the incomplete cache’s errors, isolating the missing label information.

Four-trajectory verification recovers an optimum for every cache. The measured incremental benefit therefore concerns forecast accuracy and point selection at fixed label-cache capacity.

Response to Questions

Q1. Can pre-search quantities identify when certification will outperform successive halving? We have not established a validated pre-search predictor of that comparison. Sample size, retained dimension and candidate count describe the computational opportunity; contraction factors and training horizons indicate approximation-error accumulation. These quantities inform implementation choices, but do not yet provide a reliable certification-versus-halving decision rule. The previously tested measured-cost hybrid also failed to improve median economics.

The new CIFAR-100N results establish a larger-sample setting where certification beats halving, alongside the smaller settings where it loses. W4 and Appendix T.4 report this comparison. We retain both outcomes and distinguish an observed favourable regime from a validated rule for identifying it beforehand. Pursuing this question would be a relevant and interesting follow-up work.

Q2. What controlled comparison establishes the benefits of intervention-aware information retention? Please see W6 and Appendix T.1. The comparison changes which label statistics are retained while fixing their capacity, polynomial approximation, candidate family and selection policies. Exact feature-integration controls isolate label-information loss from numerical approximation, while richer-cache and direct-integration controls verify sufficiency. Reporting point selection separately from four-trajectory verification makes clear where the measured benefit arises.

Q3. How robust are recovery and speed-ups to different grids and feature dimensions? Please see W3 and Appendix T.2. The new study varies candidate layout and feature dimension while preserving intervention ranges, partitions and labels for matched comparisons. Screening recovers all 60 optima; its six preselected timing settings give paired median speed-ups ranging from 2.74–5.95× over exhaustive evaluation and 1.60–3.10× over halving. The additional CIFAR-100N study extends this evaluation to a larger training population.

Q4. What supports expecting improved detection on unseen examples? Please see W5 for the population-selection bound and expanded held-out results newly added as part of this rebuttal. The bound relates approximate development selection to population performance under explicit sampling and independence assumptions. The held-out evaluations provide separate empirical evidence. Together, they clarify when an expectation of transfer is justified.

Comments on the paper

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Highlights from Rebuttal

We thank all reviewers for their constructive feedback. During the rebuttal, we have substantially expanded the theoretical and empirical evidence, revised the manuscript for clarity, and updated the anonymous code release. We summarise the principal changes below.

1. Full-dataset Food-101N evaluation at over seven times the original training scale.
We completed experiments using the full 310,009-image Food-101N archive, yielding 294,851 training images across all 101 classes, compared with 40,000 training examples in the original submission. Across six core searches, each containing 486 detector–training configurations, our screening and certified procedures recover every exhaustive development optimum. On a predeclared full-population case, paired timing experiments show screening and certification are respectively 1.99× and 1.17× faster than optimised successive halving, with zero observed selection regret (Section 5; Appendix T.5).

2. A deeper theoretical and empirical study of generalisation.
We investigated when economical configuration search also benefits detection on unseen examples. The new population analysis connects our computational selection guarantee to statistical generalisation: under the stated sampling and candidate-independence assumptions, population selection regret is bounded by computational regret plus twice the uniform statistical estimation error (Section 4; Appendix J.1).

The expanded evaluation provides substantially stronger held-out evidence. Relative to predefined reference configurations:

  • 59 of 60 search families improve held-out AUROC in the expanded cross-dataset study, with a median gain of 2.334 percentage points.
  • All six full-population Food-101N searches improve held-out AUROC, with a median gain of 5.301 percentage points.
  • All six new CIFAR-100N searches, using human-corrupted labels across 100 classes, improve held-out AUROC, with a median gain of 4.653 percentage points.

Together, these studies strengthen the evidence across training scales, noise sources, representations and candidate layouts (Appendix T).

3. Substantial improvements to presentation and clarity.
We completed a section-by-section readability revision, introducing motivation and concrete examples before formal results, clarifying terminology and notation, and strengthening transitions. The revised narrative explicitly connects information retention, intervention prediction, ranking uncertainty and targeted evaluation. A new Glossary and Equation Guide in Appendix V provides linked explanations of concepts, symbols and results. Manuscript changes are highlighted in blue.

4. Additional evidence for the framework’s algorithmic consequences, feature learning, and broader applicability.
An experiment on storage isolates the benefit of retaining information according to the proposed interventions, improving forecasts and point selection while holding the approximation method fixed (Appendix T.1). We also added a local neural response analysis and controlled feature-learning study: accounting for evolving representations improves forecasts in all twelve evaluated families, and four-trajectory screening recovers every development optimum (Appendix U).

These additions make the connection between the characterisation, its algorithmic decisions and their practical consequences substantially more explicit.

As the author-reviewer discussion phase is nearing its end, we would be grateful if the reviewers could take some time to go through our responses, confirm if they address their initial concerns, and raise any additional concerns that they might have, so that we have the opportunity to address them in time.

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

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