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Under review as a conference paper at ICLR 2027

Calibrate Before You Measure: Conditioning Interfaces Decide What a Generative Probe Reports

Abstract

Frozen diffusion models serve neural decoding as renderers and, through conditional likelihood, as instruments that measure how much a brain recording reveals about a stimulus. Both uses route the signal through a conditioning interface that is treated as a neutral pipe. We show that it is not. We construct a chain of stimulus channels ordered by the data-processing inequality, so that any valid instrument must report a non-increasing curve, and use this ground truth to audit four conditioning interfaces of one diffusion backbone. The single-token image-embedding interface adopted by most EEG and fMRI pipelines scores the true stimulus below a deliberately mismatched condition on spatial layout, whereas a 257-token readout of the same encoder pass reads layout correctly. The gap persists across a second backbone and two disjoint stimulus sets, and a far more bottlenecked caption interface reads layout correctly, so the failure cannot be anticipated from an interface's description and must be measured. A dose–response identifies conditioning strength as the mechanism: raising it improves the axes an interface can express while pushing the axes it cannot express below chance. Deployed decoders exhibit the same over-pushing: their decoded vector is a worse estimate of the true embedding than a constant in all ten subjects and is optimal at one third of its deployed strength, and two independent decoders are overconfident by a conformally guaranteed margin that rendering at the optimal strength narrows but does not close. We release the phantom as a pre-flight check for any conditioned generative probe.

Primary area:
generative models
Keywords:
diffusion models, conditioning interfaces, measurement validity, generative evaluation, data-processing inequality, neural decoding, EEG, calibration, conformal prediction

Reviews

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1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_7v2JOpenReview ↗
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2
Confidence
2
Informativeness
2
Presentation
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2
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Paper summary

In this work, the authors ask whether a frozen diffusion model's conditionable interface is a valid tool for estimating how much information a given signal carries about its stimulus, using the difference in conditional likelihood as a proxy. To this end, they construct a phantom that mimics a stimulus representation without requiring a brain: they define a chain of progressively coarser image averages, exploiting the ordering imposed by the data-processing inequality on the degraded stimuli, but not necessarily on their encoded representations or probe scores. In each trial, they perform a pairwise discrimination task in which the foils differ by one stimulus attribute – category, color, flip, blur, or layout – and assess the performance in a permutation-normalized manner.

When comparing four different interfaces on SDXL, they find that the 1-token interface underperforms relative to the null in the low-seam layout foils, while the 257-token readout of the same encoder pass, as well as the caption-based arms, do not. This directionality also replicates for SD1.5 and two independent stimulus samples from THINGS, with magnitudes attenuated by about 3x on the additional stimulus sets, showing that the effect depends on adapter scale. In the second part of this paper, they audit EEG-to-image decoding performance on the THINGS-EEG dataset.

Critical strengths
  • A cheap, brain-free audit. The nested-averaging phantom needs no brain data and can be reused. The paper documents two pitfalls: the noise-pairing bug (§2.1), and foil-dependent image-side bias (Table 3). Together they show that a raw two-way Δ ELBO comparison across images can’t be interpreted without a null. This is useful to anyone who uses diffusion likelihoods as a readout.

  • A controlled comparison with replication. The 1-token and 257-token readouts share one ViT-H forward pass, and the gap between them holds across two backbones and three stimulus sets.

Critical weaknesses

Critical Weaknesses

  1. The proposed explanation of the probe failure needs stronger support. The negative layout efficiency and the gap between pooled and patch-grid conditioning are interesting findings. However, it remains unclear how much of the negative score reflects an interaction between conditioning and the different denoising difficulties of true images and layout foils. Table 3 shows substantial differences in baseline difficulty, and the supplementary implementation uses different empty conditions across interfaces. A control that holds the candidate image fixed while comparing conditions derived from the true image and its layout foil would help clarify the mechanism. The adapter-scale experiment supports a dependence on conditioning strength, but the claim that the inversion “deepens monotonically” is stronger than Table 4 supports: roll2d becomes less negative between scales 0.8 and 1.0. These issues matter because the paper makes causal claims about why the observed failure occurs.

  2. The broader claims about brain-decoding systems and calibration exceed the demonstrated scope. The related-work discussion does not adequately support the claim that the tested pooled-embedding interface represents most EEG and fMRI reconstruction pipelines. The description of the cited fMRI systems is inaccurate: MindEye and Brain-Diffuser use patch-level image representations. The discussion also omits published EEG methods with alternative conditioning pathways, including DreamDiffusion (ECCV 2024), BrainVis (ICASSP 2025), and GWIT (ICASSP 2025). These works matter because the paper attributes the failure to the conditioning interface; the authors should explain how these methods fit their taxonomy and which conclusions extend beyond the tested architectures. The evaluated NICE and DCTD reconstruction pipelines also need clearer identification and references to establish what the “deployed decoders” claim covers. Furthermore, the proposed connection between adapter scaling in §4 and vector shrinkage in §5 remains insufficiently demonstrated: these are different interventions, and the authors acknowledge that shrinkage does not fully calibrate the renderer. Finally, “overconfident by a conformally guaranteed margin” overstates the guarantee. Split conformal prediction guarantees marginal coverage under its assumptions; the observed set sizes do not establish a guaranteed minimum set size or overconfidence margin. Together, these issues limit the generality and strength of the paper’s conclusions.

Questions for authors
  1. Diagnostic control: Could you hold the candidate image fixed and compare its denoising error under conditions derived from the true image and its layout foil? Does the pooled interface still show a systematic preference for the incorrect layout condition?

  2. Clarification: The supplementary code uses different empty conditions across interfaces. How do these choices affect Table 3 and the comparison of efficiencies? Is the main interface gap stable across repeated mismatched-condition assignments?

  3. Scope: Please identify and reference NICE and DCTD, explain whether the evaluated decoding heads reproduce published reconstruction pipelines, and correct the description of the cited fMRI conditioning interfaces. Which conclusions do you expect to extend to other conditioning architectures?

  4. Interpretation: What evidence establishes a shared mechanism between adapter scaling and vector shrinkage? Please also specify what quantity the conformal guarantee covers and distinguish that guarantee from the empirical set-size results.

Reviewer_sXDfOpenReview ↗
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1
Confidence
3
Informativeness
2
Presentation
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Soundness
1
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Paper summary

The author is trying to answer a question can we trust the measurements from the generative models or it's biased by their conditioning interfaces. The authors construct a chain of stimulus channels ordered by the data-processing inequality to audit conditioning interfaces. They compare 4 conditioning interfaces, and find that the single-token interface can produce misleading measurements of spatial information, while a multi-token interface performs better. The paper has additional analysis around the conditioning strength and uncertainties.

Critical strengths

Strengths:

S1. The research question raised is valid and valuable. Whether things obtained from the pretrained generative model reflect the input signal or conditioning interfaces.

S2 The design of using degradation chain to make the tests controllable with a known ordering of information is natural.

Critical weaknesses

Weaknesses:

W1. Multiple confounding factors in the main comparison between the 1-token and 257-token interfaces, dimensionality and pretrained adaptor parameters. It's difficult to attribute the different solely to the conditioning.

W2. Writing needs to be improved. The problem raised is clear and logic is fluent yes, but the introduction and related work section doesn't give me a comprehensive view of what is being done and where to adequately position the paper, In particular, should include more related work discussion on conditional likelihood reliability and the design and interpretation of probing methods. In the introduction, the notation of the degradation chain x0x_0, x64x_{64}, etc., is not defined before usage.

Questions for authors

Q1. How will the choice of degradation mechanism affect the testing results,e.g., masking? Will things look different and how sensitive is it to the degradation level and methods? Testing with different approaches will strengthen the justification of using DPI-ordered degradation chain.

Q2. How are the conditioning-strength effects related to the embedding shrinkage results with varying ss and α\alpha?

Q3. With conformal prediction, the authors link the larger conformal set size to the overconfidence issue in LLMs, which I don't fully agree. It indicates high uncertainty but not strictly overconfident. Could you elaborate on this argument?

Reviewer_QptwOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
1
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Paper summary

The paper studies how conditioning interfaces affect diffusion-based scoring and EEG-to-image reconstruction. Using degraded images and factor-specific foils, it finds that pooled CLIP conditioning performs worse than patch-based conditioning on spatial discrimination, sometimes falling below a mismatched-condition baseline. Additional EEG experiments show that shrinking predicted embeddings improves their MSE, while generated reconstructions yield large conformal prediction sets and limited sample diversity relative to error. Shrinkage produces mixed improvements in these output measures. The authors attribute these findings to excessive conditioning strength and recommend interface calibration and uncertainty reporting.

Critical strengths
  1. The spatial discrimination gap between pooled and patch-based conditioning is a useful finding. Correct pooled conditioning can impair discrimination relative to mismatched conditioning, while patch-based conditioning performs significantly better. Controls and replication across backbones and stimulus sets strengthen this result, and suggest this could be a true general property of conditioned visual diffusion models. Moreover, the paper appropriately distinguishes this consistent gap from the less stable degradation correlations.
  2. The EEG experiments usefully distinguish embedding accuracy from reconstruction performance. Embeddings shrinkage improves embedding MSE across ten subjects, but produces mixed results on the reconstruction uncertainty measures in Table 7. Reporting this discrepancy is valuable evidence that better embedding estimates do not automatically improve image reconstruction quality.
Critical weaknesses
  1. The proposed common mechanism is not established. The paper attributes three findings to excessive conditioning strength: poor spatial discrimination by the diffusion scorer (Section 4), excessive magnitude of EEG-derived embeddings under MSE (Section 5.1), and reconstruction overconfidence (Sections 5.2–5.3). However, it does not show that the scoring failure predicts corresponding errors in generated images, or that correcting it improves reconstruction. Moreover, scaling an adapter’s contribution and shrinking its input embedding toward the mean are different interventions. Table 7 provides a useful output-level experiment, but its mixed results do not establish their equivalence: embedding shrinkage reduces CLIP error/spread while increasing the conformal set size. Lower embedding MSE therefore does not establish an optimal generative conditioning strength, and residual error after shrinkage cannot be attributed specifically to the renderer.
  2. The scope of the claims is overstated through an incorrect characterization of major fMRI methods. The abstract and Section 2.2 claim that most EEG/fMRI reconstruction pipelines use the tested single-token interface, while Section 1 explicitly groups MindEye and MindEye2 among pooled-embedding methods. However, MindEye predicts a 257 × 768 CLIP representation, and MindEye 2 conditions generation on all 256 image-patch tokens. Furthermore, contemporary strong reconstruction methods such as Brain-IT (Beliy et al. , ICLR 2026) also condition the diffusion model on full grid tokens. This is significant because the paper’s strongest finding regarding conditioning failures centers aroung single token conditioning. With no fMRI experiments, the findings do not establish the claimed applicability to fMRI methods. Relevance to several EEG pipelines remains plausible, but does not substantiate the broader prevalence claim.
  3. The information-theoretic and conformal guarantees do not support the stated conclusions. The data-processing inequality orders information in the degraded images, but does not establish monotonicity of the reported efficiency of the probe. There are two gaps related to this issue. First, separately encoding each degraded image does not need to preserve that ordering: with encoder (E) and degradation (D), (E(D(X))) need not be obtainable from (E(X)). Second, even ordered representation information would not guarantee ordered performance for a fixed diffusion score, as preprocessing can make existing information easier for a restricted model to use. Below-null discrimination remains meaningful, but does not prove that the representation lacks layout information. Similarly, split conformal prediction guarantees marginal coverage under appropriate assumptions, not minimum set size or irreducible uncertainty in EEG. Large sets may reflect decoder or scoring limitations, and the oracle comparison does not distinguish these from information absent from EEG. Displaying one sharp sample also does not constitute a 90%-coverage singleton claim. These limitations directly affect the abstract’s claim of overconfidence by a guaranteed margin.
Questions for authors
  1. Connection of probe score to generated images. What evidence links the spatial scoring failure in Section 4 to spatial errors in generated reconstructions? Do interventions that improve the probe also improve reconstruction fidelity? Table 7 and Appendix E examine generated outputs but do not directly establish this connection. If the claim concerns scoring alone, which reconstruction claims should be narrowed? Is there any common mechanism that links the two claims (probe and reconstructions)?

  2. Common mechanism. What establishes that scaling the adapter’s contribution and shrinking its input embedding address the same mechanism? Can their effects be distinguished by varying them independently within one reconstruction pipeline? In particular, what supports treating the embedding-MSE-optimal shrinkage coefficient as an appropriate generative conditioning strength?

  3. Scope and evaluated systems. How do the pooled-interface claims accommodate the full-token conditioning used by MindEye and MindEye 2? What supports “most” EEG/fMRI pipelines, and the extension to fMRI without experiments?

  4. Information-theoretic justification. What does efficiency estimate, and why should it inherit the data-processing ordering? Please address both the lack of guaranteed information ordering between separately encoded degraded images and the distinction between available information and a fixed scorer’s performance. What distinguishes missing layout information from failure of this particular readout?

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