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Under review as a conference paper at ICLR 2027

Information Present, Pathway Shut: A Conditional Flow Model That Never Used Its Diffraction Pattern

Abstract

When conditioning fails to improve a conditional generative model, the null is usually read as a limit of the data or the task. We show that it can instead mean the model never used its condition, and we give inexpensive diagnostics that tell the two apart. Our case study is rigid-body flow matching for molecular crystal structure determination from powder X-ray diffraction (PXRD). The pattern enters through zero-initialised, tanh-gated cross-attention. In every trained checkpoint the gate stayed near 5e-5. The pattern changed the predicted velocity by about one part in a million, classifier-free guidance was an identity, and our earlier guided-versus-unguided comparisons had been measuring prior-sampling noise. The gate's gradient was not vanishing. Forcing the gate fully open changed the loss identically for a crystal's own pattern and for another crystal's, because the attention weights behind the closed gate had never learned. An ideal-observer information-ceiling test shows that the pattern resolves 0.05 Å molecular displacements in all 200 held-out crystals tested, even at the lowest training count level. The flat conditioning is therefore a learning failure, not an information limit. We then test, under a pre-registered protocol with a deranged-pattern control, whether fine-tuning with the pathway forced open learns crystal-specific use of the pattern. It does not: even with the pathway open and the information present, the own-pattern advantage is confidently below a small effect (rank-biserial r < 0.15 on every head) and indistinguishable from the deranged-pattern control. That confident null is the full-corpus analysis; on the subset our representation defect provably cannot reach (Sohncke groups, n = 1,116) the pre-registered outcome is instead inconclusive, with the orientation bound at 0.152. We also identify an orientation target that is unlearnable in principle and a rigid-body representation defect that rebuilds improper symmetry copies with the wrong hand and, through a rigidity filter, leaves a corpus in which the two most common organic space groups are under-represented by close to an order of magnitude. We distil the diagnostics into a checklist for conditional generative models in the sciences.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
conditional flow matching, gated cross-attention, classifier-free guidance, conditioning collapse, powder X-ray diffraction, molecular crystal structure prediction, pre-registration, negative results

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 3 reviews, above 27% of the others.
Reviewer_cm4WOpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
2
Soundness
1
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Paper summary

The authors present an overview of their attempt to train a flow matching model to predict crystal structures from PXRD profiles. They show that the model performs poorly and fails to learn meaningful use of the PXRD conditioning. The manuscript continues with reporting a series of diagnostics to find out why the model doesn't train. Despite this the model never approaches anything comparable to a state-of-the-art. Based on this, the authors then try to make generalizable conclusions about training conditional generative models on scientific data.

Critical strengths

The authors present several diagnostic approaches that may be useful for finding out why a model doesn't learn in general.

Critical weaknesses

The authors never compare to a SOTA model, but checking the literature myself they don't seem to even approach SOTA results. There are several issues in the dataset, acknowledged by the authors themselves. Moreover there can be unaddressed issues in the implementation of the model or training protocol. Any patterns observed in this setup so far away from a valid training regime and cannot readily be assumed to generalize to other applications of conditional generative modelling. Despite this the central thesis of the manuscript is generalizability to other applications.

Questions for authors
  1. Can the authors compare to SOTA?
  2. Can the authors fix the issue in the dataset and report performance?
  3. How are the authors certain their implementation is working?
  4. Can the authors please roll back generalizability claims or substantiate them with a better model?
Reviewer_fcKLOpenReview ↗
Rating
2
Confidence
2
Informativeness
3
Presentation
3
Soundness
2
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Paper summary

This paper looks at why a diffraction-conditioned generative model for molecular crystals fails to use its conditioning input. The model does rigid-body flow matching over lattice parameters, molecular centroids, and orientations, and receives simulated PXRD patterns through a zero-initialized, gated cross-attention branch. The authors aren’t trying to build a competitive structure-determination method. The goal is to understand the failure.

The learned gates stay near zero, and the predicted velocity field barely changes with the diffraction input. An ideal-observer test shows the signal is there in principle: with the lattice, orientations, and profile parameters known, small centroid shifts produce distinguishable patterns. In a pre-registered experiment, the authors fine-tune with the gates open on either correctly matched or deranged (shuffled) patterns. Neither model does meaningfully better on its own pattern under the teacher-forced metric. Extra seeds, open-gate training from scratch, and an ungated architecture all give the same negative result. Along the way, the authors also find an orientation-gauge issue and a handedness bug that corrupts part of the structural representation and skews which structures make it into the dataset.

The paper is mainly a diagnostic case study plus an evaluation checklist. The failure itself is well documented. It’s harder to say much about why it happens, since the structural supervision is partly inconsistent and the centroid head doesn’t learn much even before conditioning comes into play.

Critical strengths
  1. The paper directly checks whether the model uses its condition. The authors don’t take the cross-attention module or aggregate metrics as evidence that conditioning works. They look at the gate, measure how much the conditioning branch contributes, test how sensitive the velocity field is to the input, and compare correct, missing, and mismatched patterns. Using common random numbers was a good call. It shows that different guidance settings can give identical per-crystal metrics, which independent prior samples would have hidden. Together, these experiments make a convincing case that the original checkpoints ignore the diffraction input.

  2. The open-gate experiment has a deranged-pattern control, a teacher-forced endpoint fixed in advance, multiple-comparison correction, an effect-size threshold, and confidence bounds. The confirmatory experiment is kept separate from the exploratory follow-ups, which cover three more seeds, open-gate training from scratch, and an ungated additive-conditioning model. So this is more than one failed run or one bad conditioning design.

  3. The synthetic experiments show that zero-initialized gates can open during training. On the real task, conditioning still fails when the gate starts open or is removed entirely. This rules out the easy story that zero initialization is the whole problem. The paper is careful to separate what it observed from what it can’t yet explain, though a few of the broader claims still need to be toned down.

Critical weaknesses
  1. The conditioning failure can’t be cleanly separated from bad supervision. This is the biggest issue. Some of the conditioning patterns and structural targets don’t describe the same crystal. Section 8 says the handedness defect contaminates the training corpus, and fixing it would mean rebuilding the data and retraining. So the central experiments run on a pipeline with a known source of input–target mismatch. That doesn’t invalidate the observation that the models ignore their conditions, but it makes it much harder to say why. The Sohncke-only reanalysis helps, but it’s not the same as training on clean data. Restricting evaluation doesn’t undo whatever corrupted examples did to the shared encoder and backbone during training. To tell apart “conditioning is hard to learn” from “the supervision is inconsistent,” the authors need a training run on a verified-clean subset—either after fixing the representation or using only Sohncke structures from the start.

  2. The centroid head doesn’t learn much even unconditionally, which weakens the null result on conditioning. Table 1 shows the centroid head performing slightly worse than the best constant predictor. The discussion says this doesn’t improve after the gauge fix or increased centroid-loss weighting. So the main question the paper asks is whether PXRD helps a component that can’t do its job from the other inputs alone. A bad unconditional model doesn’t prove conditioning can’t help. But without a working baseline, you can’t tell apart several explanations: the structural modeling is inadequate, the optimizer isn’t finding a good solution, the pattern encoder isn’t extracting useful features, or the model can’t integrate the condition. The synthetic positive control shows the gate mechanism and endpoint work in a toy setting, but that doesn’t tell us the real PXRD encoder and molecular representation can support a learnable inverse problem. A useful middle ground would keep the real encoder and representation but simplify the task—say, predict small centroid perturbations with the cell and orientations given.

  3. The “unlearnable in principle” claim about the original orientation target needs more work. Equation (2) computes the squared geodesic residual of a zero predictor under a uniform-rotation assumption. That gives you a reference number, but it doesn’t establish the minimum achievable loss for a network that sees the intermediate state, time, molecular features, and conditioning. A best-constant baseline is diagnostically useful; it’s not automatically an irreducible floor. The real question is whether the supposedly unpredictable component stays unpredictable after conditioning on everything the model has access to. A nearly uniform marginal over orientations isn’t enough to settle that on its own. The gauge fix does reduce orientation loss in practice, which supports the intervention. But that doesn’t independently prove the theoretical impossibility claim about the original parameterization. The paper should spell out the gauge symmetry and argue why the corresponding component can’t be inferred from the available inputs.

Questions for authors

Q1. Can the real pipeline pass a task-level positive control? Keep the same PXRD encoder, molecular representation, and conditioning interface, but give the model an easier job—recover centroid perturbations with the lattice and orientations provided, or solve a small, clean subset. That would help tell apart pattern encoding failure, structural prediction failure, and an integration problem, rather than just showing the statistical endpoint works on synthetic data.

Q2. What does the ideal-observer experiment actually tell us? How does distinguishability change when the orientations, lattice, and profile parameters aren’t fixed to their true values? Have you looked at weakly informative directions, not just random perturbations? If not, the result should be scoped as local sensitivity with known nuisance parameters. Also, the n=164n=164 label in Figure 1(b) doesn’t match the 200-crystal experiment described in Section 6—can you reconcile those?

Q3. Where does the r=0.15r = 0.15 threshold come from? What’s the scientific motivation, and how does it map to a meaningful improvement in structural prediction? It would help to see own-vs-wrong loss differences and field sensitivities broken out by evaluation time, along with normalized loss improvements. That way you can tell whether the benefit is absent everywhere or just gets washed out by time-averaging.

Q4. What’s the takeaway once the gate is ruled out? The open-gate and ungated models fail too, so which piece of evidence currently distinguishes inconsistent supervision, a backbone that hasn’t learned enough, an ineffective pattern encoder, and the target-variance explanation? What single experiment would most directly test the explanation you favor? Answering this would clarify whether the paper’s main contribution is a reusable diagnostic checklist or an identified mechanism.

Reviewer_MkLxOpenReview ↗
Rating
3
Confidence
3
Informativeness
3
Presentation
3
Soundness
2
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Paper summary

This paper investigates a conditional rigid-body flow model for molecular crystal structure determination from powder X-ray diffraction. It shows that a nearly closed cross-attention gate makes the original model essentially insensitive to its diffraction input, and that unpaired guidance comparisons can mistake sampling variation for conditioning effects. An ideal-observer experiment establishes sensitivity of simulated diffraction patterns to small centroid perturbations when other structural and profile parameters are known. A reported pre-registered own-pattern/deranged-pattern fine-tuning experiment finds no meaningful crystal-specific conditioning advantage even after opening the gate. Exploratory seeds, open-gate training from scratch, an ungated additive architecture, and synthetic positive controls probe this result further. The paper also identifies orientation-target and improper-symmetry representation defects.

Critical strengths

-- The main negative result is supported by direct and complementary measurements. Gate values, conditional velocity changes, forced-open tests, shared-randomness comparisons, and deranged-condition controls all indicate that the original checkpoints do not use their patterns meaningfully (Section 5; Tables 2–3). The analysis identifies why the earlier guidance comparisons were misleading. This is useful methodological evidence even without competitive crystal generation.

-- The authors test their proposed remedy and report its failure transparently. Section 7 specifies an effect-size threshold, multiple-testing correction, and a deranged-training control over 1,600 held-out crystals. Section 7.1 adds repeated seeds, from-scratch open-gate training, an ungated alternative, and a synthetic positive control. Crucially, the manuscript preserves the inconclusive Sohncke-only pre-registered outcome rather than reclassifying it using later exploratory results. This makes the paper more informative than an anecdotal account of a failed training run.

Critical weaknesses
  1. The information ceiling establishes local sensitivity under oracle assumptions, rather than identifiability of the full inference problem.

Section 6 fixes the true cell, orientations, and profile and perturbs centroids along sampled symmetry-consistent directions. Large discrimination statistics show that these perturbations affect the pattern above counting noise. They do not exclude distant ambiguous packings, poorly observed directions, or confounding when nuisance variables are also inferred. In particular, a perturbation lying within a joint confidence region does not by itself prove that no search can resolve that displacement; that interpretation requires assumptions about the test, likelihood geometry, and parameterization. The broad statement that the failure is “not an information limit” should be restricted to the tested local, oracle-conditioned problem.

  1. The failure mechanism remains confounded by a representation/data problem and an unsuccessful centroid head.

The authors explicitly acknowledge that the centroid head does not beat its no-information floor and that improper symmetry operations produce inconsistent pattern/target pairs (Sections 8–9). Evaluating on Sohncke crystals does not remove the influence of corrupted examples during training. The toy establishes that the diagnostic can detect signal in a simpler problem, but there is still no successful positive control using the actual crystal representation and condition pathway. The paper therefore convincingly diagnoses non-use, but does not isolate why the actual scientific model fails or establish how broadly the proposed causal account transfers.

Questions for authors
  1. Can you state precisely which local hypothesis is tested by the profiled statistic, and revise the “not resolvable by any search” interpretation? How would allowing profile, cell, or orientation nuisance variables to vary affect the claimed 0.05 Å sensitivity?

  2. Can you train the existing model on an exclusively Sohncke, representation-verified subset, and demonstrate that the centroid head learns a simpler supervised or low-noise version before testing conditional flow matching? The distinction between a head that cannot learn its target and a condition that is ignored matters directly to the claimed mechanism.

  3. Can the ACs verify the timestamped pre-registration and its exact endpoint/code version? Were bootstrap intervals and tests resampled/grouped by CSD refcode family when multiple validation structures belong to the same family, and how was the threshold r = 0.15 chosen as a practically meaningful effect?

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

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