acceptodds
Under review as a conference paper at ICLR 2027

Representable but Unlearned: Encoding Rank and the Interaction-Prediction Floor

Abstract

Input encodings can restrict which measured contrasts a predictor can jointly reproduce, even when no single contrast is forced to vanish. We compute the attainable contrast space from an encoder's equivalence classes and a fixed contrast design, without labels, loss, or a fitted model; projecting the recorded contrasts onto that space gives an empirical error floor for any unrestricted decoder on those classes. On a 140-rectangle siRNA interaction panel, a graph neural network's training-only feature mask merges 165 endpoint states into 90 classes and cuts the rank of the 140 interaction contrasts to 72. The resulting floor is 0.009980, which is 14.6% of the fitted model's interaction squared error; the fitted model reaches 0.068335, slightly worse than a control predicting no interaction at all. A minimum of three restored chemistry columns recovers full rank. Refitting without the mask removes the floor entirely, yet interaction MSE improves by only 0.000017 under the reported protocol, and the restored columns remain absent from every training input. On a released RNA-splicing predictor, whose encoding is injective on the measured states, the same computation returns the full design rank of 1,986 and a floor of exactly zero. These results separate what an encoding permits from what a fitted model achieves; they do not identify what limits the remaining error. The rank check needs no fits and bounds what any amount of training under a fixed encoding can recover.

Primary area:
interpretability and explainable AI
Keywords:
encoding rank, identifiability, interaction effects, graph neural networks, model diagnostics, faithfulness, scientific machine learning, siRNA

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_ceKsOpenReview ↗
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2
Confidence
3
Informativeness
2
Presentation
2
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3
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Paper summary

The paper proposes a label-free diagnostic for how an input encoding restricts which measured contrasts a predictor can jointly produce, and applies it to an audit of a modified-siRNA graph neural network (GNN).

The diagnostic (Sec. 2, App. A10.1/A10.6). Given distinct raw endpoint states, a signed contrast design C ∈ R^{q×m}, and an encoder that partitions states into k equal-input classes via H ∈ {0,1}^{m×k}, the contrast vectors attainable by an unrestricted deterministic decoder are exactly col(CH) (Prop. 2.1). Forced-zero functionals form the left null space, of dimension q − rank(CH). Projecting the recorded contrast vector onto col(CH) gives an empirical squared-error floor for any such decoder. The rank is label-free; the floor is empirical. Corollary 2.2 gives interaction rank (a−1)(b−1) for a full anchored product panel.

The audited instance (Sec. 2, 7, 8). On a 15×11 antisense-by-sense sub-rectangle the authors extract from the Bramsen et al. (2009) screen (165 states, 140 rectangles), the GNN’s training-only node-feature mask zeroes 44 of 93 columns and merges 165 states into 90 classes, cutting rank(CH) from 140 to 72. No row of CH is zero, so no single rectangle is forced to cancel; the restriction is joint. The floor is 0.009980, which is 14.60% of the fitted interaction error 0.068335 and 14.63% of recorded contrast energy. A minimum of three restored chemistry columns recovers full rank (six distinct minimal triples; marginal gains 27+27+8 = 62 against 68 jointly, so non-additive).

Interventions. Refitting without the mask restores rank 140 and removes the floor entirely, but interaction MSE moves only 0.068335 → 0.068318, i.e. +0.000017, or 0.17% of the removed floor, with paired-seed changes in [−0.000176, +0.000262]. The restored columns remain zero on every training node. A pre-registered synthetic sweep (App. A10.11.2) tested the same question on constructed designs: the registered prediction that removing the class-equality restriction would lower out-of-subspace error below the floor failed (8/42 below, 34/42 above, median ratio 1.33), and total MSE was higher in 28/42 fits.

Negative control and breadth. A released MAVE-NN splicing predictor has an injective one-hot encoding, so rank(CH) = rank(C) = 1,986 and the floor is exactly zero; its 97 forced-zero functionals are design dependencies the measurements satisfy. A frozen breadth audit (App. A10.22) adds an expanded Bramsen panel (730 of 1,845 directions lost, floor 0.007565) and a GB1 binding panel under the same one-hot rule (floor zero).

Supporting audit material. Sections 3–8 add an activity-prediction evaluation on three cohorts, weighting and identity-hash conventions, provenance adjudication (299 unresolved primary/released label discrepancies), a proof that relation blocks absent from every training graph cannot change any training prediction (8,192 scalars), a bounded perturbation test, and preflight failures for two published modified-siRNA predictors, neither of which could be run.

Critical strengths
  1. A sound, discriminating diagnostic with a working negative control.

The paper separates what an encoding permits from what a fitted model achieves, and computes the first exactly: ranks by rational elimination on integer matrices, verified left-null witnesses, fitted contrast vectors checked to lie in col(CH) to 10⁻¹⁶, and the encoding partition verified on all 27,225 state pairs. Critically, it distinguishes encoding-induced restrictions, which the recorded contrasts violate and therefore pay for, from design-induced dependencies, which the measurements satisfy and which cost nothing. The MAVE-NN splicing instance returns rank(CH) = rank(C) = 1,986 and a floor of exactly zero, so the check does not fire automatically on a new panel.

Why it is consequential: This is the only part of the paper that could stand on its own, and it is correct. Without the negative control I would treat the positive floor as an artifact of the method; with it, the diagnostic is at least measuring something real about the declared encoders.

  1. Negative results are reported, including a failed pre-registered prediction.

The authors retract their own protocol’s claim that improvement is bounded by the removed floor, explain why refitting can also change in-span error, report that the pre-registered synthetic sweep’s registered prediction failed (34 of 42 nonzero-deficit fits above the floor), and state plainly that 85.40% of the GNN’s squared error lies inside the permitted contrast space.

Why it is consequential: It makes the reported numbers credible, so I read the nulls as evidence rather than as missing work. This is what keeps the paper near the threshold rather than well below it.

Critical weaknesses
  1. On the only panel where the floor is positive, the contribution reduces to a triviality, and the headline percentage is near-vacuous.

App. A10.11.1 proves the 68-dimensional left null space is spanned by duplicate-row differences: every restriction says that two rectangles the encoder cannot distinguish get equal predictions. No instance is shown where the forced-zero structure is anything else, which is the regime where Prop. 2.1 would earn its generality. Separately, the audited model’s 140 contrasts have SD 0.0016 against a measured 0.22, and its interaction MSE is 0.19% worse than a zero-interaction control. With the fitted contrast vector ≈ 0, the floor’s share of fitted error necessarily approaches its share of recorded contrast energy — and it does: 14.6038% against 14.63%. The abstract leads with the fitted-error figure, which therefore carries almost no information about the fitted model.

Why it is consequential: This is my main reason for a below-threshold score. It removes both the theoretical novelty and the empirical headline. What remains is that 85.4% of the error lies inside the permitted subspace with no identified cause.

  1. Every test of practical consequence returned null, and breadth is one lossy encoder.

Removing the mask eliminated the entire floor and changed MSE by +0.000017, with paired-seed changes straddling zero. The pre-registered synthetic sweep found total MSE higher for the unrestricted arm in 28 of 42 fits. The diagnostic-utility analysis reports a primary interval including zero. Meanwhile the positive-floor rows of Table 24 are one encoder on one study, the zero-floor rows are one released one-hot encoder, and both published modified-siRNA predictors failed their readiness gate, so no independent lossy encoder was ever tested.

Why it is consequential: A diagnostic is worth publishing if it either predicts something or is shown to matter somewhere. On these panels it does neither, and the authors say so. An independent lossy encoder with a positive floor, or a restoration experiment that decouples representability from training support and shows realizable gain, would change my assessment.

Questions for authors
  1. Is there a measured panel and encoder for which the forced-zero functionals are not spanned by duplicate-contrast equalities? If not, what does Prop. 2.1 buy over directly checking which rows of CH coincide?
  2. Given that the fitted contrast vector is near zero (SD 0.0016 against measured 0.22), what does the floor’s 14.6% share of fitted error tell a reader that its 14.63% share of recorded contrast energy does not? Would you consider leading with the data-only quantity?
  3. In the mask-restoration refit, the restored columns were zero on every training node. Can you run an arm in which restored chemistry also appears in training — e.g. by admitting duplexes that exercise those columns, or by the fixed-size replacement design used for MAVE-NN — so that representability and training support are actually decoupled?
  4. Given the failed pre-registered prediction in App. A10.11.2 and the near-zero refit gain, is there any setting in which the floor predicts post-restoration improvement? If not, how should a practitioner use it?
  5. Can the diagnostic be applied to at least one independent encoder with a lossy encoding, other than the audited mask? For instance, do standard tokenizations in published chemistry or sequence models merge measured states on a public panel?
  6. The antisense-marginal floor share is 38.1% against 14.6% for interactions, and the error decomposition places the deficit in main effects. Why does the title and abstract foreground the interaction floor?
  7. The AI use statement says AI tools were used throughout. Could you state more specifically which components (text, code, proofs, number checking) were AI-assisted, and what verification each received? This bears on how a reader should weigh the self-reported checks.
1 comment

We wanted to thank you again for your review and to briefly highlight the new evidence addressing one of the forms of evidence you identified as potentially changing your assessment: an independent lossy encoder with a positive empirical floor.

Section 9, Appendix A10.23 and Table 24 report this example. Its 800 encoded contrast rows are nonzero and pairwise nonproportional, yet have rank 740, revealing 60 restrictions that duplicate-row checks miss. The empirical floor is 0.3150033, or 2.54% of recorded contrast energy.

We also completed the siRNA training-support experiment requested in Q3. Section 8 and Appendix A10.25 report its near-zero outcome and limitations.

Our point-by-point responses provide the details and supporting records. If you have an opportunity to revisit them before the discussion closes, we would appreciate your assessment of whether this evidence addresses your concerns. Thank you for your time.

Reviewer_Z1GvOpenReview ↗
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3(+1)
Confidence
2
Informativeness
2
Presentation
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2
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Paper summary

The authors focus on predicting biological interactions, e.g., whether chemical modifications to both strands of an siRNA produce an effect that differs from the sum of their individual effects. In particular, they present a methodology for assessing to which extent errors are unavoidable because of the chosen encoding. The methodology is tested on several tasks, including siRNA panels and RNA splicing.

Critical strengths

The presented methology seems logical and robust. In particular, the authors make an interesting distinction between representability, i.e., whether the encoding permits a predictor to express the relevant effects, and training support, whether the training examples provide evidence about the relevant features.

Critical weaknesses

My main concern is that the manuscript lack clarity. The language is convoluted, abstractions precede practical examples, to the point that the meaning of some terms is hard to appreciate from the immediated context and requires reading the text back and forth. Finally, the structure itself of the paper can be improved. A second concern is the actual innovativeness of the proposed methodology. The issue addressed by this work is quite general, and naturally goes beyond predicting interaction within biological contexts. The authors do discuss related work in section 10, however to my understanding they do not explainn clearly enough the innovativeness of their approach.

Questions for authors

I would strongly suggest to streamline the structure and language of the paper. My suggestion would be to start with a practical example, where terms like "contrasts" gain a physical, appreciable mearning, and then to generalize the proposed methodology with a robust mathematical formulation.

I would also appreciate if the authors could better describe how their methodology advances the state-of-the-art in the "related work" session.

I would be glad to increase my evaluation if the authors can improve their manuscript as described above.

Reviewer_iRnZOpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
1
Soundness
2
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Paper summary

This paper analyzes how input feature encodings restrict the joint contrasts a model can represent on a finite measured panel. It characterizes the attainable contrast space through encoding equivalence classes and matrix rank, and derives an empirical squared-error floor by orthogonal projection. Experiments on siRNA and an RNA-splicing predictor distinguish representability from learned accuracy. In the siRNA case, removing a feature mask eliminates the floor but yields negligible predictive improvement, with the restored features still absent from the training inputs.

Critical strengths

(1) The finite-panel formulation explicitly separates restrictions imposed by the encoding from dependencies in the contrast design. (2) The siRNA audit connects the rank deficit to specific masked chemistry columns and identifies a minimal restoration that recovers full rank. (3) The paper distinguishes an empirical error floor from a population-risk guarantee and avoids treating full representability as sufficient for accurate learning. (4) The reported negative results, including negligible gains after mask restoration and sensitivity of predictor rankings, make important limitations visible.

Critical weaknesses

(1) The use of campaigns v3/v4 (lines 92-93), readiness gates (lines 40-44), and logs of free disk space and missing container software (lines 2454-2455) gives the manuscript the style of an AI-generated project report and obscures the scientific argument. (2) Positive-floor results share one preprocessing mask, including the expanded Bramsen panel. Injective splicing and GB1 cases mainly check algebraic consistency, leaving usefulness across independent encodings insufficiently established. (3) The decision value beyond collision counts or individual-contrast cancellation remains unclear. Please show how rank, error floor, or minimal-column restoration changes an existing analysis. (4) The manuscript does not establish a substantive methodological advance beyond combining encoding equivalence classes, matrix rank, and orthogonal projection. (5) The MAVE-NN intervention replaces 2,000 training samples while also changing sequence backgrounds, and worsens the MSE on unaffected interaction contrasts by 0.01441. Effective validation on the primary siRNA task is also lacking, so the causal conclusion that training support improves interaction prediction accuracy is not established.

Questions for authors

(1) What is the substantive advance of the joint-rank and projection diagnostic over standard finite-panel estimability and individual-contrast cancellation checks? Identify a concrete decision in the reported experiments that cannot be reached using the simpler checks. (2) What completed evaluation on an independent published modified-siRNA predictor supports the motivating application? If none is available, which application claims remain justified by the current evidence? (3) What evidence demonstrates usefulness across independent encoders beyond the shared siRNA preprocessing mask and injective one-hot cases? Explain what the latter establish beyond the expected zero-floor identity. (4) In the mask-restoration experiment, separate changing the evaluation encoding at fixed parameters from changing the validation-selected checkpoint. How much of the reported 0.000017 improvement is attributable to each change? (5) How can the MAVE-NN comparison isolate feature support when replacing 2,000 examples also changes sequence backgrounds? Account for both the 0.04415 improvement on affected interactions and the 0.01441 degradation on unaffected interactions, and state precisely which conclusions remain descriptive. (6) Provide a concise map of the current contribution, historical campaigns v3/v4, and the experiments supporting each claim. Identify the exact configurations, commands, checkpoints, and result files for Figures 4 and 8, and consolidate version history and failed-run accounting separately.

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