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Under review as a conference paper at ICLR 2027

When Physical Views Should Not Be Positive Pairs: Cross-Frequency Collapse in Self-Supervised Learning for Eddy Current Testing

Abstract

Many scientific instruments acquire co-registered channels through distinct measurement operators, making cross-channel positive pairing tempting in self-supervised learning. Correspondence, however, is not exchangeability: pairing declares the operator difference nuisance for the task. When that difference carries target signal, pairing can suppress information the task needs. We test this failure mode in multi-frequency eddy current testing (ECT), where frequency controls penetration and the operator difference is known from physics. Holding backbone, objective, augmentation policy, split, and evaluation fixed, we change only the second-view channel. Same-frequency pretraining reaches 0.69–0.71 macro-AUPRC against a 0.047 random-ranking reference; all nine cross-frequency comparisons degrade transfer, with penalties approximately 5%–20% of their matched same-frequency macro-AUPRC, grouped physical-unit support after multiplicity correction, and adverse directions in all three pretraining seeds. The effect spans VICRegL, DenseCL, and SimCLR: mechanisms that avoid trivial collapse do not guarantee preservation of task-relevant operator variation when the view distribution encourages invariance to it. LP-FT shrinks the mean gap from 0.0688 to 0.0222 under full labels, bounding cross-frequency collapse to a supervision-dependent transfer penalty. PhysAug provides the constructive counterpart by deriving views from known sensing nuisances. Thus, when operator and target dependence are sufficiently known, candidate positive pairs can be audited at design time. Our controlled ECT study therefore motivates a broader principle for multi-channel scientific sensing: positive-pair validity depends on whether operator-dependent variation is nuisance or downstream signal, not merely on physical correspondence.

Primary area:
unsupervised, self-supervised, semi-supervised, and supervised representation learning
Keywords:
self-supervised learning, contrastive learning, positive-pair design, invariance learning, multi-channel scientific sensing, measurement operators, physics-informed augmentation, eddy current testing

Reviews

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1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 2 reviews, above 27% of the others.
Reviewer_v9fyOpenReview ↗
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2
Confidence
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Informativeness
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Paper summary

This paper investigates positive-pair construction in self-supervised learning (SSL) for multi-frequency eddy current testing (ECT). The authors argue that aligning signals from different frequency channels may suppress task-relevant information due to their different physical measurement operators. The paper compares same-frequency (AF2, AF2) and cross-frequency (AF2, AFx) positive pairs using SimCLR, DenseCL, and VICRegL, while the downstream defect detection task uses only AF2. Experiments on an ECT dataset show that same-frequency pretraining consistently outperforms cross-frequency pretraining. The authors also introduce PhysAug, a physics-informed data augmentation strategy, and evaluate its robustness to measurement perturbations.

Critical strengths

The paper provides a controlled comparison of same-frequency and cross-frequency positive pairs across three SSL methods.

Critical weaknesses
  1. The core hypothesis needs stronger validation. The downstream task uses only AF2, while other frequencies are introduced during SSL pretraining. Thus, the observed performance degradation may also be explained by domain mismatch rather than the suppression of task-relevant information. Moreover, most cross-frequency SSL configurations still outperform the supervised baseline.

  2. The novelty and generalizability could be strengthened. The paper mainly evaluates existing SSL methods on a single ECT dataset without proposing a new learning algorithm. Moreover, cross-view learning has already been extensively studied. The current evidence is insufficient to support the authors' claim of motivating "a directly testable criterion for auditing view design in other multi-channel scientific sensors."

Questions for authors

No additional questions.

2 comments

We thank the reviewer for highlighting partner-frequency exposure as a possible alternative explanation for the observed AF2 transfer penalty.

The original comparison changed both the positive partner and partner-frequency exposure, making domain mismatch a plausible alternative explanation. An aggregate-exposure-matched control does not reproduce the penalty, while DenseCL still shows a penalty despite its transferred encoder receiving AF2 only, as detailed below. Our conclusion is target-conditional: co-registration and shared labels alone do not establish positive-pair validity for AF2 transfer.

  1. Cross-frequency positives consistently hurt. Replacing AF2+AF2 with AF2+AF1/AF3/AF4 positives lowers AF2 macro-AUPRC at f = 10% in all nine objective-by-partner comparisons, by 0.032–0.138 (5–20% relative). All nine are BH-supported (grouped physical-unit bootstrap), and all 27 pretraining-seed contrasts show a penalty (Sec. 4.1, Table 2).
  2. Matching aggregate AF4 exposure does not reproduce the penalty. The control keeps the aggregate AF2/AF4 view counts of AF2+AF4 training but forms positives only within a channel. It improves AF2 macro-AUPRC over AF2+AF4 by +0.0382 for SimCLR (95% CI [+0.0130, +0.0594], BH q = 0.0090) and +0.0789 for VICRegL ([+0.0311, +0.1228], q = 0.0020), and all six seed contrasts favor it; both tests are exploratory and form their own BH family. If aggregate exposure alone caused the penalty, the control should trail AF2+AF2 by about the AF2+AF4 penalties (0.0323 and 0.0702). Its differences from AF2+AF2 are instead +0.0059 [−0.0115, +0.0264] and +0.0087 [−0.0084, +0.0238], which include zero and exclude deficits of that size; this comparison is descriptive (Sec. 4.2; App. D.1, Table 10).
  3. The penalty does not require mixed-frequency input to the transferred encoder. In DenseCL, the transferred encoder and its BatchNorm see only AF2 in both arms, as in the downstream task; the partner frequency enters only through momentum keys and queued negatives. DenseCL still has the two largest penalties: 0.1048 with AF3 and 0.1381 with AF4 (Sec. 4.2; App. A).

W1. Domain mismatch and the supervised baseline. The balanced-exposure control and DenseCL routing result implicate the tested cross-frequency pairing policy, without isolating a unique mechanism: the control also changes BatchNorm populations and objective-specific batch terms (App. A), and DenseCL's keys and queue still carry the partner frequency. The representation diagnostics are consistent with stronger cross-view alignment: in all 27 cross-frequency encoders, unrelated cross-view pairs are more similar and the positive-versus-unrelated margin is smaller than in matched AF2+AF2 encoders (Sec. 4.3). On the supervised baseline, we agree: six of nine cross-frequency SSL means exceed CNN-PhysAug in point estimate (Tables 2–3). The primary penalty is relative to matched same-frequency SSL: all nine cross-frequency settings trail their AF2+AF2 references (Sec. 4.1, 4.6).

W2. Novelty. Existing cross-view SSL establishes the value of pairing related observations, but does not settle whether exactly co-registered, identically labeled frequency channels should be equivalent positives for a specified target (Sec. 5). For AF2 transfer, the tested cross-frequency pairing policies consistently incur a relative penalty (Sec. 4.1; Table 2). Our contribution is the controlled pairing comparison and a validation rule for other candidate pairings, not a new SSL objective. We deliberately use three established objectives: a new algorithm would be confounded with the pairing policy under test, and the result does not depend on a single objective.

W2. Generalizability. The penalty recurs across three SSL objectives and three partner frequencies, so it is not confined to one tested loss or pairing. We do not claim cross-sensor replication. The broader contribution is an evaluation strategy for co-registered sensors: use measurement physics to flag operator differences that may matter for a target, then test the positive-pair policy against an exposure-matched within-channel reference (Secs. 3, 6).

The criterion. We agree with this point, and the revised paper replaces the "directly testable criterion" claim with a decision rule (Sec. 3, 6): (i) flag operator differences that may alter target-relevant responses, using the measurement model or labeled calibration standards; (ii) compare a flagged pairing on labeled validation data with an exposure-matched within-channel policy, using a pre-specified metric and its uncertainty, and keep it only if the evidence shows any loss is below a pre-specified tolerance. The rule does not predict outcomes for untested sensors; it identifies which pairings need testing. The balanced-exposure control instead uses the held-out test set to examine the exposure explanation, not to select a policy.

We hope the new control and the narrower claims address both concerns.

Thank you for the detailed response and additional experiments, which have addressed my concerns to some extent. However, I remain concerned about the limited novelty and generalizability of the findings, particularly given the evaluation on a single dataset.

Reviewer_sEvGOpenReview ↗
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Paper summary

This paper investigates a design issue in self-supervised learning: whether two observations from the same physical object are necessarily suitable as a positive pair. Using eddy current testing as an example, the authors found that even when two sensor channels are precisely aligned, observe the same physical defect, and have identical labels, treating them as positive samples for self-supervised pretraining may still degrade subsequent defect classification performance. The authors found that, under fixed model architecture, training objectives, data splitting, and downstream evaluation conditions, replacing same-frequency positive samples with cross-frequency positive samples consistently reduced the downstream classification performance of all three SSL methods. However, the core scientific insights of this paper align closely with existing self-supervised learning theory, and the conclusions demonstrated by the experiments are more limited than the general principles the authors attempt to propose.

Critical strengths
  1. The paper addresses the issue of validity in positive sample views in real scientific instruments, and the specific research scenario is well-founded.
  2. In-frequency and cross-frequency comparisons controlled for model, SSL objective, augmentation, data splitting, and downstream tasks. Adverse effects were observed under all three SSL objectives, demonstrating that this phenomenon is not limited to any specific loss function.
  3. The authors account for the correlation among overlapping patches by employing physical-group-level bootstrapping, paired comparisons, and multiple-test correction.
Critical weaknesses
  1. The authors argue that if the measurement operators (frequencies) differ, and these differences cause changes in the target information (classification results), then this is sufficient grounds to conclude that the selected positive pair is invalid. I think this conclusion is too absolute. Even if a measurement operator changes, a neural network can still learn to map different observations back to the same underlying physical state. This is common in the field of multimodal data; for example, images and text can still jointly express semantic information that is useful for downstream tasks.
  2. The authors claim that cross-frequency pairing suppresses response information related to defect depth; however, the designed experiments focused primarily on classification metrics and did not include a direct analysis of depth information.
  3. The paper reports only the average metric results for three defect types; however, if the authors could provide results for each individual type, it would be easier to determine whether depth-related information is being suppressed.
  4. The “design-time audit” proposed by the authors is not yet a practical method; the authors do not provide a clear algorithm or decision criterion, but rather rely primarily on practitioners’ own interpretations of physical processes. The paper needs to clarify what the actual contribution is relative to existing view selection research.
  5. Relevant work in the field of self-supervised learning has discussed why enforcing invariance between views may compromise task-relevant features [1,2]. This paper appears to be a concrete application of existing “Task-relevant View Invariance” principles to physical scenarios. We hope the authors will clarify the contributions of this paper relative to related works.

[1] Tian Y, Sun C, Poole B, et al. What makes for good views for contrastive learning?[J]. Advances in neural information processing systems, 2020, 33: 6827-6839. [2] Liang P P, Deng Z, Ma M Q, et al. Factorized contrastive learning: Going beyond multi-view redundancy[J]. Advances in Neural Information Processing Systems, 2023, 36: 32971-32998.

Questions for authors
  1. What exactly makes two measurement operators non-exchangeable for the downstream task?
  2. Can the author provide separate forecast results for ID, OD, and TW?
2 comments

We thank the reviewer for recognizing the importance of positive-pair validity and our controlled comparisons with physical-group-level inference. W1–W5 and Q1–Q2 refer to your weaknesses and questions in order.

We agree that different operators are not inherently invalid positives and that the cost of harmful invariance is known (InfoMin, FactorCL). The revised paper makes a narrower claim that the experiments support: exact co-registration and shared labels do not by themselves make two channels good positives for a given target, so a pairing should be tested. For AF2 transfer, the tested cross-frequency pairings fail that test:

  1. Cross-frequency positives consistently hurt. Replacing AF2+AF2 with AF2+AF1/AF3/AF4 positives lowers AF2 macro-AUPRC at f = 10% in all nine objective-by-partner comparisons, by 0.032–0.138 (5–20% relative). All nine are BH-supported (grouped physical-unit bootstrap), and all 27 pretraining-seed contrasts show a penalty (Sec. 4.1, Table 2).
  2. ID and OD favor same-frequency positives in every comparison. The requested classwise results (W3, Q2) are now in App. D.2 (Table 11): ΔID is +0.0658 to +0.1419 (positive in 27/27 seed contrasts) and ΔOD +0.0086 to +0.1555 (25/27). TW is near ceiling (same-frequency AP 0.994–1.000) and mixed (5 positive, 1 tie, 3 negative), and its 12 positive patches come from two physical flaws. These class effects are descriptive.
  3. Matching aggregate AF4 exposure does not reproduce the penalty. A new control keeps the aggregate AF2/AF4 view counts of AF2+AF4 training but forms positives only within a channel. It improves AF2 macro-AUPRC over AF2+AF4 by +0.0382 for SimCLR (95% CI [+0.0130, +0.0594], BH q = 0.0090) and +0.0789 for VICRegL ([+0.0311, +0.1228], q = 0.0020); both tests are exploratory and form their own BH family. Its differences from AF2+AF2 are small (+0.0059, +0.0087), with intervals that include zero; this comparison is descriptive (Sec. 4.2; App. D.1, Table 10).

W1 and Q1. Operators and exchangeability. A network can align different observations, as in image–text SSL; this helps when the target depends on shared content and can hurt when it also depends on how the views differ (Sec. 5). Across all 27 objective-matched encoder contrasts, unrelated-pair similarity rises and positive-versus-unrelated separation falls, consistent with reduced sample-specific cross-view structure (Sec. 4.3). On Q1, physics indicates when to suspect non-exchangeability, and the experiment shows whether it matters. AF4 (100 kHz) has about √3 times the skin depth of AF2 (300 kHz) (Sec. 2), so the channels weight the wall differently, while ID, OD and TW flaws differ in through-wall position. This flags the pairing for testing but does not by itself make the channels invalid positives; for AF2 transfer, the test shows a penalty (result 1).

W2–W3. Depth, classwise AP, and confounds. The ID/OD pattern fits the physical motivation, but class AP does not measure encoded depth; Section 4.2 makes that distinction explicit. In DenseCL, the transferred encoder and its BatchNorm see only AF2 in both arms, yet its AF3 and AF4 penalties are the two largest (0.1048, 0.1381); the partner frequency still enters through momentum keys and the negative queue (Sec. 4.2; App. A). Batch composition and optimization dynamics are not fully isolated. What we establish is a transfer penalty under the tested pairing policies, not direct depth-feature suppression.

W4. A practical decision rule. (i) Flag operator differences that may alter target-relevant responses, using the measurement model or labeled calibration standards, even if labels agree; registration, gain and noise are candidate nuisances, which PhysAug models. (ii) Compare a flagged pairing on labeled validation data with an exposure-matched within-channel policy, using a pre-specified metric and its uncertainty, and keep it only if the evidence shows any loss is below a pre-specified tolerance (Sec. 3, 6). Physics selects what to test; validation, not a practitioner's reading of the physics, decides. The exposure control (result 3) uses the held-out test set to check the exposure explanation, not to select a policy.

W5. InfoMin and FactorCL. InfoMin and FactorCL (Sec. 5) show why task-relevant view differences matter, but do not settle whether two co-registered, identically labeled channels are redundant for a given target. Co-registration and shared labels alone do not establish redundancy: the tested cross-frequency positives incur an AF2 transfer penalty. Our contribution is a controlled AF2-transfer test (result 1), descriptive classwise evidence (result 2), an exploratory matched-exposure control (result 3) and a test-before-pairing procedure (W4). It is not a new SSL objective or a claim that all cross-operator positives fail.

We hope these results and clarifications address your concerns.

Thank you for the detailed response, which have addressed my concerns to some extent. But I remain unconvinced that the proposed test-before-pairing procedure provides a sufficiently distinct conceptual or methodological contribution beyond standard validation-based selection of positive-pair policies. I will maintain my rating.

Comments on the paper

3 comments

We thank the reviewer for recognizing the PhysAug and fine-tuning results and for probing the novelty and scope of our findings.

What is new. We agree that frequencies penetrate to different depths and that ignoring useful information can hurt SSL. Those principles leave a specific experimental question open: should exactly co-registered, identically labeled channels of one instrument be positive pairs for a given target? For AF2 transfer, the answer is no:

  1. Cross-frequency positives consistently hurt. Replacing AF2+AF2 with AF2+AF1/AF3/AF4 positives lowers AF2 macro-AUPRC at f = 10% in all nine objective-by-partner comparisons, by 0.032–0.138 (5–20% relative). All nine are BH-supported (grouped physical-unit bootstrap), all 27 pretraining-seed contrasts show a penalty, and all nine remain BH-supported after LP-FT at the same budget (Sec. 4.1, 4.4; Tables 2, 15).
  2. Matching aggregate AF4 exposure does not reproduce the penalty. A new control keeps the aggregate AF2/AF4 view counts of AF2+AF4 training but forms positives only within a channel. It improves AF2 macro-AUPRC over AF2+AF4 by +0.0382 for SimCLR (95% CI [+0.0130, +0.0594], BH q = 0.0090) and +0.0789 for VICRegL ([+0.0311, +0.1228], q = 0.0020); both tests are exploratory and form their own BH family. Its differences from AF2+AF2 are +0.0059 and +0.0087, with intervals that include zero and exclude deficits as large as the AF2+AF4 penalties (0.0323, 0.0702); this comparison is descriptive (Sec. 4.2; App. D.1, Table 10).
  3. The penalty is not explained solely by mixed-frequency input to the transferred encoder. In DenseCL, the transferred encoder and its BatchNorm see only AF2 in both arms; the partner frequency enters only through momentum keys and queued negatives. DenseCL still has the two largest penalties: 0.1048 with AF3 and 0.1381 with AF4 (Sec. 4.2; App. A).

Q1. Decision rule and prediction. Beyond the established requirement to preserve task-relevant information, the rule adds two concrete steps. (i) Flag a pair when the measurement model, or labeled calibration standards, indicate that the operator difference may alter target-relevant responses, even if labels agree. Here, frequency changes through-wall weighting, and ID, OD and TW flaws differ in through-wall position, so cross-frequency pairs are flagged; registration, gain and noise are candidate nuisances. (ii) Compare a flagged pairing on labeled validation data with an exposure-matched within-channel policy, using a pre-specified metric and its uncertainty, and keep it only if the evidence shows any loss is below a pre-specified tolerance (Sec. 3, 6). The rule does not predict the outcome of an untested pairing; it identifies which pairings need testing. PhysAug applies the same logic constructively: its standard transformations are parameterized by those nuisances and produce the gains you note (Sec. 4.5). Result 2 uses the same comparison on the held-out test set to check the exposure explanation, not to select a policy.

Q2. Alternative explanations. Result 2 shows that aggregate exposure to AF4 data, including its signal quality, does not by itself reproduce the penalty, although the control also changes BatchNorm populations (App. A). Result 3 shows that partner-frequency input and mixed-frequency BatchNorm statistics in the transferred encoder are not necessary for the penalty; momentum keys, queue and optimization dynamics still differ. Hyperparameters are fixed within each objective, and the penalty recurs across three objectives and 27 seed contrasts. Across all 27 objective-matched contrasts, unrelated-pair similarity increases and positive-versus-unrelated separation decreases, consistent with reduced sample-specific cross-view structure (Sec. 4.3). In the new classwise breakdown, mean ID and OD AP favor AF2+AF2 in all nine comparisons; TW, with two physical flaws and near-ceiling AP, is mixed (App. D.2, Table 11). This pattern fits the physical motivation, but encoded depth is not directly measured or decoded.

Q3. Another tube, anchor, or frequency-aware model. These are not part of the present study; we agree they would test how far the result extends. The study uses calibration-standard tube scans with one held-out test tube and AF2 as the anchor, chosen because it is the balanced analysis channel for this tubing (Sec. 2). This design enables matched comparisons across objectives and partner frequencies. ECT is an informative testbed because its frequency-dependent operators are physically characterized. The compact backbone is held fixed within each objective, so model capacity does not vary across pairing arms; larger encoders remain untested. Our conclusion concerns equivalence-based cross-frequency pairing; frequency-aware conditioning or fusion could preserve channel identity and is the natural next step (Sec. 6).

We hope this clarifies what the study adds beyond the two principles you cite.

Reviewer_TbyMOpenReview ↗

thanks for the rebutal

the reviewer thanks the authors for the rebutal which helps me understand their contribution. specifically, their contribution is to show a very specific empirical study verifying that aligned measurements with identical labels (at different frequencies) can still make harmful positive pairs - which i took obvious; see for ecxample [1]. i am raising my score to 2, but my major concern is still whether this provides enough additional insight for ICLR.

References: [1]Xiao et al. (2020) What Should Not Be Contrastive in Contrastive Learning, arXiv.

Thank you for reconsidering our contribution and for raising your score.

As you note, Xiao et al. [1] provides an important foundation for our work (Secs. 1, 5). The distinction we hope to emphasize is between recognizing that invariance can be harmful and deciding which physically acquired measurements should be treated as equivalent positive views. In multi-channel scientific sensing, measurements can be exactly co-registered and share identical labels while their measurement operators preserve different task-relevant information. Our controlled ECT study shows what pairing them costs: at f = 10%, cross-frequency positives consistently lower AF2 transfer, and an exploratory SimCLR/VICRegL control, which matches aggregate AF2/AF4 view counts while pairing within each channel, does not reproduce the penalty (Sec. 4).

We therefore see the study as motivating a broader principle for multi-channel scientific sensing, where spectral bands, imaging contrasts, and excitation frequencies can provide naturally corresponding channels: positive-pair validity depends on whether operator-dependent variation is nuisance or downstream signal, not merely on physical correspondence. The measurement model makes this principle actionable. It flags pairings whose operator differences may matter for the target, which can then be tested against an exposure-matched within-channel policy (Secs. 3, 6), and it guides constructive view design: PhysAug, which you noted, builds views from modeled acquisition nuisances.

We appreciate your engagement and understand your remaining concern, and we hope this distinction helps clarify the contribution and its broader relevance to positive-pair design in scientific sensing.

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

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