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Under review as a conference paper at ICLR 2027

Decay Signatures: Measuring Domain-Dependent Degradation and the Boundaries of Anchor Prediction

Abstract

Training on degraded inputs is a standard route to robust representations, yet choosing the degradation intensity remains empirical: existing approaches scan, search, or offer qualitative principles — none compute a schedule from measurable properties of its operators. Working in cross-modal molecule image–graph retrieval, where structure is discrete and verifiable, we introduce decay signatures: per-operator decay rates measured on task, structure, and frequency channels. Signatures overturn conventional operator labels — operator class is a measured, domain-dependent fact, not a priori intuition — and reveal a non-monotone, U-shaped response of fixed-anchor training to intensity, which decomposes into a mild-anchor penalty and a deployment-conditional optimum. Stress-testing a first-order transition-landmark predictor (product of per-operator survival curves, threshold calibrated once) on ten held-out schedules under pre-registration yields a boundary map: the primary criterion is not met (2/4 under the plateau reading, 1/4 under strict argmax scoring); prediction is exact at bracket resolution on a restricted subset, with the caveat that one exact hit rests on a near-cancellation of two measured error terms; and failures decompose into three observed structural sources — saturation, interaction error, and compensability. Degradation intensity is measurable — but only to first order; we report this boundary with the same fidelity as the hits.

Primary area:
unsupervised, self-supervised, semi-supervised, and supervised representation learning
Keywords:
data augmentation, corruption robustness, degradation intensity, representation learning, cross-modal retrieval, measurement methodology, pre-registration

Reviews

Among:
Shape:
1234this paper, Bottom 2%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_sddEOpenReview ↗
Rating
1
Confidence
2
Informativeness
1
Presentation
1
Soundness
1
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Paper summary

The paper is difficult to read due to convoluted prose and poorly defined words, which prevents me to reliably assess the proposed idea.

As far as I understand, the paper is working on finding the optimal intensity of degradation operations (e.g., downscaling, blur) used to learn a robust neural representations of images (and music audio). This is seemingly done by training a neural network architecture on varying degradation operators and intensity levels, and measuring some robustness metrics. It appears that different operators have different effects on the network's robustness. For example, the curve for downscaling operator shows a threshold-like behavior, with sudden drop in task performance at some intensity level, whereas gaussian noise degrades task performance gradually. Additionally, it seems that "transition landmarks" can be estimated from each operator's curve, but this landmark is poorly defined in the manuscript.

Critical strengths

There might be some strengths that I have missed, but unfortunately I could not properly understand what the manuscript is proposing.

Critical weaknesses

The manuscript in its current form has poor clarity. At the most granular level, the words and the grammars make sense. But when read at sentence-level, the combination of words often don't make sense. At paragraph-level, it is hard to identify what is being argued, and the logic of the arguments. The readers often have to infer the meaning of a sentence.

Below I put a small set of examples just from the introduction, but this issue persists throughout the manuscript.


  • (L038) "... and all three must be redone for every new operator set, every new task, and every new coupling; none computes a schedule from measurable properties of its operators."

This is the first paragraph of the introduction. Operator, task, coupling, and schedule are not defined. Each word can easily have multiple interpretations depending on the fields.

  • (L046) "... but with landmarks no existing account locates --- with a reproducible valley and recovery peak across five seeds."

Landmark, valley, recovery peak are not defined. One might infer that this is a performance-intensity curve's valley and peak only after reading Section 3 and 4.

  • (L047) "The decision-relevant layer is larger... self-matched nearly-optimal anchors lose 4-31 R@1 points.... shifts harsher as deployment hardens"

What do decision-relevant layer, self-matched, R@1, and deployment mean? What attribute is being measured by "larger", "harsher", and "hardens"?

  • (L053) "Measurement already delivers one surprise before any prediction is attempted: operator classes turn out to be measured, domain-dependent facts, not a priori labels..."

What kind of prediction is this?


The lack of clarity prevents me from fully understanding the manuscript, and therefore I cannot reliably assess the informativeness and soundness. My recommendation to reject is primarily based on the clarity.

Questions for authors

A major rewriting is needed to make sure the readers can understand what the paper is proposing.

Reviewer_RHCiOpenReview ↗
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Confidence
2
Informativeness
1
Presentation
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Soundness
1
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Paper summary

I will preface this by saying that the paper was largely incomprehensible. The paper summary is what I understood this paper is trying to do. The paper asks whether the right training degradation intensity (which the authors call the “anchor”) can be computed from measurements of the degradation operators. In contrast, the current literature tries to either learn them or find them empirically for each use case. The domain the authors use is cross-modal molecule image-to-graph retrieval, although they also mention audio settings and CIFAR-10 a couple of times, but don't explain how they use them. In particular, An "image tower" sees degraded molecule drawings, and a GIN graph tower always sees clean graphs. Degradation is a composite of blur, JPEG, downscale and coarse dropout, controlled by one intensity coordinate L.

The authors then introduce their so-called “decay signatures,” per-operator decay rates on three channels: task, structure and frequency. They found that blur, known to be a "purifier" in the literature, actually destroys molecular line-art, which is in high-frequency in its foreground. On CIFAR-10, instead, the classification flips as predicted.

The authors conclude that whether a damage type is harmful depends on what the images look like and that their own formula misses its target. They had aimed to get 3 out of 4 predictions right and got 2, or 1 with stricter scoring. To my understanding, their method didn't work as they hoped it to.

Critical strengths
  1. The problem that the authors set out to solve is interesting and well-motivated.
Critical weaknesses
  1. Again, the paper text is so dense that reading it is extremely hard, and even moreso understanding it or reviewing it. From the abstract alone, several terms are used without being defined (operators, signatures, anchor, intensity, deployment-conditional optimum, schedules, pre-registration). This problem spans the entire paper, including the figures, where most of the labels and text inside overlaps, which makes them incomprehensible (Figure 1B is a good example of this). The paper is unclear in multiple, important points (or as the authors would call them, "load-bearing" points): I don't understand how CIFAR-10 or the audio setting was used, I don't understand how the results were measured (in line 201, the authors claim that the dedicated controls are "an earlier vintage", which I could not translate. Basically, I could not verify the integrity of the experimental settings, also due to the fact that there is no dedicated experimental setting section. Sometimes, the authors just say that something is written in the "appendix", without referencing exactly what part of the lengthy appendix they are referring to.

  2. The authors only use one dataset, in one setting, and although they claim 5 seeds, standard deviations are never reported in the figures of the main text. In Appendix D, they actually say that 5 seeds aren't consistent: many of the results were repeated only two or three times, and one setup (N3) only twice (Appendix D, Table 6).

On top of that, the paper describes several mistakes that had to be corrected: One of the controls in their training setup secretly did nothing in early runs (Appendix A, “Implementation-defect note”). Some training runs were corrupted and had to be redone (Appendix F). A reference accuracy number in Figure 1b changed from 58.3 to 13.7 after a fix (Appendix F, item iv). I am not sure why the authors chose to keep this in the appendix test, as it only generates confusion and makes it hard to trust the other results.

Finally, to my understanding, the authors' own method failed in the test they set it up: get at least 3 out of 4 key predictions right, within a small margin of error. They get 2 out of 4, and 1 with more stringent limits. So their final practical advice, to train on images as blurry as the one you will get in the test set, does not use the formula.

Upon further inspection, some references seem to be hallucinated. The authors report "A simple way to make neural networks robust against diverse image corruptions." as ICLR 2022, but it should be ECCV 2020, and the author list is wrong. There are possibly more.

Questions for authors
  1. Is your method actually working, or did it fail 2 out of 4 times, and 3 out of 4 under stricter scoring (as written Appendix A)?
Reviewer_6LoDOpenReview ↗
Rating
2
Confidence
2
Informativeness
1
Presentation
2
Soundness
2
Read review
Paper summary

This paper asks how strong training-time degradation should be, working in cross-modal molecule image to graph retrieval where structure is discrete and checkable. The starting observation is that fixed-anchor training responds non-monotonically to intensity: there is a reproducible valley around L=0.14 and a recovery peak at 0.152 across five seeds. The decision-relevant version is the deployment view, where anchors that look near-optimal under self-matched testing lose 4 to 31 R@1 points at test L=0.150, and the best anchor shifts harsher as deployment hardens.

To get at this they build an instrument called decay signatures, which records for each of nine operators how fast three channels decay with intensity: retrieval R@1, ring-match structure preservation, and high-frequency energy. All measurements run on one fixed clean-trained reference model. The main measurement result is that operator class is domain-dependent rather than given a priori. Blur, conventionally a texture purifier, destroys molecular line drawings because the foreground strokes are themselves high frequency, and its task decay rate falls 28 times on CIFAR-10 while JPEG goes the other way. The same measurements also rule out smooth rate models, since exponential fits underfit at R² below 0.28.

They then pre-register the simplest estimator the measurements allow, taking composite survival as the product of per-operator ring-match curves with a single threshold calibrated once, and predicting the cliff point on ten held-out schedules. The pre-registered criterion is not met, at 2 of 4 under the plateau reading and 1 of 4 under strict argmax. The failures sort into three named structural causes: saturation, interaction error, and compensability.

Critical strengths
  1. The measurement layer is a reusable contribution that stands on its own.

Decay signatures turn operator class from an inherited label into something measured, and the cross-domain check makes the point stick. Blur has a ring-match decay rate of 2.22 on molecular line drawings, squarely in destructor territory, and its task decay rate falls 28 times on CIFAR-10 while JPEG moves the opposite way. That flip is predicted in advance by the frequency argument rather than fitted after the fact, and the same instrument transfers to a third domain. Table 1 and Table 2 would be worth having even if everything downstream of them were wrong, which is the test I apply to a measurement paper.

  1. The paper is pre-registered and reports its own failure at full volume.

The primary criterion is stated in advance, missed, and reported as missed in the abstract. The authors also flag that one of their two hits rests on a near cancellation of two error terms, reclassify N2 from hit to false positive after finding a defect in their own knob mapping, and report that exponential decay families underfit at R² below 0.28. The controls in 3.3 are the right ones, and the MixTrain baseline showing a monotone response is what makes the phenomenon specific rather than generic corruption exposure.

This matters to my overall assessment because it determines how much weight I can put on everything else in the paper. Work this willing to publish against itself is unlikely to be quietly selective elsewhere, so the boundary map in Section 5 is informative as a negative result rather than merely unconvincing as a positive one.

Critical weaknesses
  1. The U-shaped response that motivates the whole paper is not in the view the paper calls its primary evidence.

In the self-matched view the plateau maximum is 93.88 at L=0.124, the valley is 93.06 ± 0.53, and the so-called recovery peak is 93.20 ± 0.72, which never gets back to the plateau. The whole excursion is under one R@1 point against seed standard deviations of 0.5 to 0.7, the paired test has four degrees of freedom, and the Wilcoxon sits at its attainable floor of 0.0625. The authors themselves describe this view as a training dynamics diagnostic that conflates anchor quality with test difficulty. In the deployment view, which they designate as primary, test 0.150 gives a broad plateau spanning [0.13, 0.20] and test 0.200 is monotone increasing. Neither is a U.

This is consequential because it leaves the paper's one robust finding, that mild anchors lose 4 to 31 points under hard deployment and the optimum shifts harsher, disconnected from the apparatus built on top of it. That finding needs no valley and no landmark. If the optimum really is a plateau that wide, then locating it precisely is not the problem worth solving, and the motivation for a transition-landmark estimator largely evaporates.

  1. The estimator fails its own criterion, and the evidence base is too small to support the failure taxonomy offered in its place.

The pre-registered criterion is missed at 2 of 4 or 1 of 4, and the paper reframes this as a boundary map. But the map is drawn from ten schedules, of which two are hits, and one of those two is acknowledged to rest on a near cancellation of two measured error terms. That leaves roughly one clean positive. The seven failures are then sorted into three named structural causes, which is close to one explanation per two schedules, and I cannot distinguish that from post hoc labelling. The reference check is also circular: θ is calibrated on the reference schedule at L=0.152, so the rule returning 0.1521 there is the calibration point rather than evidence.

This determines my recommendation because the boundary map is what the paper offers in place of a working method. A boundary needs enough observations on both sides to be a boundary rather than a list, and ten schedules with one clean hit does not reach that. Saturation is at least stated as a rule that would have flagged N2 and V3 out of scope in advance, which is the right form of claim, but it is tested on the same handful of runs that generated it.

Questions for authors

1.Has the second pre-registered cohort been trained? You say it was registered with protocol and predictions but not yet run at submission. If those results exist by rebuttal, they would roughly double the evidence base and, unlike the first ten, they test the applicability rules out of sample rather than on the runs that generated them. This is the answer most likely to move me.

2.Does the valley appear in the deployment view at all? Right now it lives in the self-matched view that you yourself call a diagnostic, while test 0.150 gives a plateau over [0.13, 0.20] and test 0.200 is monotone. If the landmark is only visible under the protocol you disclaim, what is the estimator predicting that matters at deployment?

3.Was the plateau reading pre-registered, or chosen after seeing the results? The score moves from 1 of 4 to 2 of 4 depending on which reading applies, so I need to know when that rule was fixed.

4.The valley is under one R@1 point with seed standard deviations of 0.5 to 0.7 and n=5. Can you add seeds in the L ∈ [0.13, 0.16] window? Related, L=0.160 has std 4.2 and is attributed to run variance while a smaller dip at 0.138 is treated as the phenomenon. What rule separates the two?

5.After correcting the knob mapping that reclassified N2, were all ten verdicts re-scored under the corrected semantics, or only N2?

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

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