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Paper summary
This paper asks if we can predict how good an LLM will be at discovering just by counting how many facts only appear once in the training data (monofacts). The authors borrow the missing-mass framework (Kalai and Vempala, 2024) and propose that training dataset with more monofacts provide LLMs with much more room to generate unseen possibilities, hallucinations and discoveries. The authors show that discovery and hallucinations are related, and also show an upper and lower bound on discovery capacities using monofact rates. These were tested on GPT-OSS 20B and Gemma 3 12B with monofact rates from 0 to 100% on materials science and regulatory genomics. The authors find that higher monofact rates consistently improve recovery of held-out targets across model families, trainingstages, and sampling settings.
Critical strengths
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Potentially important theoretical perspective. Extending the missing-mass account of hallucination to correct, previously unseen statements offers an interesting connection between training-data and scientific discovery. The frontier formulation and associated bounds also provide a framework for reasoning about the relationship between discovery and hallucination.
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The authors directly manipulate monofact presence across two scientific domains and two model families, observing consistent improvements across training stages and sampling settings. The additional reasoning-budget, repeated-exposure, and cross-domain experiments provide useful evidence about the robustness and limitations of this relationship.
Critical weaknesses
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The theoretical results do not establish the claimed dependence of discovery on monofact prevalence. Theorem 6 provides an upper bound on discovery probability, but increasing an upper bound does not imply increasing realized discovery. Theorem 7 additionally depends on frontier leakage, calibration error, and parameters that may change across training conditions. The theoretical results do not guarantee the monotonic relationship observed experimentally. The discovery-frontier assumptions and quantities are also not directly validated in the experiments. This leaves a substantial gap between the mathematical results and the paper's central claim that monofacts govern discovery capacity.
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The causal interpretation of discovery remains insufficiently supported. Monofact prevalence and training-set diversity are confounded in the main experiments. In section 5.2, repeating examples changes optimization and memorization without changing the underlying distribution's missing mass. Diversity, training exposure, etc. are all possible confounds that were not removed.
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Connection between improvements in monofacts and scientific-discovery capacity is unclear. Discovery is evaluated through exact recovery of held-out targets rather than independently validated scientific findings. For example if a model that predicts another chemically valid material satisfying the requested properties could be a “real discovery,” but is counted as a failure here. While predicting the exact answer based on structural clues without scientific reasoning will be counted as a discovery here.
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In materials discovery, the model also receives structural information derived from the target material itself. The authors remove direct answer-related hints but the remaining information still includes geometry, parameters and positions hinting at the answer.
Questions for authors
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Theorems 6 and 7 provide bounds on discovery probability, but do not establish that realized discovery increases monotonically with monofact prevalence. Can the authors demonstrate that theoretical bounds meaningfully predict the results?
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In Section 5.2, repetition does not change the missing mass distribution, but changes optimization and memorization. How could this be interpreted as isolating monofact prevalence rather than training exposure? Could the authors distinguish these explanations?
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How much of the reported improvement remains when a target’s structural information is removed? Could the authors provide simple nearest-neighbor baselines, etc. to show that the gains reflect science rather than target-specific cues?
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How are alternative materials/DNA modifications that satisfy the constraints but differ from target treated? What is the true utility of exact matching in science?
5 comments
Thank you again for your careful review. We have added several new analyses addressing your concerns, including controls for diversity and structural cues. We would greatly appreciate your thoughts on these results and welcome any further questions.
I appreciate the authors' efforts to resolve the concerns above. I find the empirical findings of the paper to be more solid now. My remaining concern, however, is that there are still some overclaims in the paper.
Specifically, as in W1, the theoretical bounds do not imply a monotonic increase in actual scientific discovery. Furthermore, only counting the exact matches in W4 may still not fully capture scientific discovery.
With that said, I believe the empirical findings are interesting enough and the remaining problems are largely an issue of interpretation and framing. The responses from the authors have positively influenced my assessment of the paper.
Thank you for the careful review and for finding the theoretical perspective potentially important and our experiments robust.
W1/Q1: Do the bounds predict the results?
TL;DR: Thm. 7 adds a floor, and with every other term fixed or flat, both bounds rise with μ^.
We agree that an upper bound alone does not imply that realized discovery increases, which is why we pair Thm. 6 with the floor in Thm. 7. Sec. 4.1 (From theory to experiments) now states this argument in the paper.
Both bounds are linear in μ^, so whenever the remaining terms are stable, realized discovery is bracketed between two quantities that increase with the monofact rate. α, β, m are properties of the world prior and the domain (Def. 4 requires the band to hold for all D; m is the sparsity of true statements, assumption (iii)), and we fix N and δ, so the concentration terms do not move. The model-dependent terms, CE and ρf, could vary across SFT runs, so we measure both. ECE is nearly constant across monofact rates (5.6–6.2%; General Response A3 and App. B.1). Good–Turing estimates of ρf (Sec. 3) are also flat (0.772–0.789, no significant trend; General Response A4, App. B.5). Every term other than μ^ is thus fixed or empirically stable, and discovery indeed rises monotonically across two domains, two model families, and both pass@1 and pass@16.
The theory makes two further directional predictions that our results confirm. Discovery and hallucination rise together in-distribution (Fig. 2, App. C). Memorization also lowers the floor even at fixed μ^ (General Response A3 and revised Sec. 5.2).
W2/Q2: Confounds and repetition.
TL;DR: Exposure is fixed, discovery rises at fixed diversity, and repetition now tests calibration rather than diversity.
Training exposure is fixed across monofact rates: every run within an epoch condition uses the same N and number of steps (now stated in Sec. 4.1). For diversity, we ran the direct control (General Response A5, App. B.3). At fixed N, the same 5K chemical systems, and an identical one-epoch training, discovery still rises at every step from r = 0 to 0.4 (pass@16 17.7→20.8%). Two results in the paper align with this finding. The multi-epoch runs (revised Sec. 5.2, Fig. 4) also hold diversity fixed, yet the trend disappears at 3 and 5 epochs, and discovery falls at high r instead of strengthening, ruling out undertraining. A coverage account also predicts more discovery with fewer hallucinations, whereas both rise together in-distribution (Fig. 2, App. C).
We agree that repetition changes f while leaving the data statistics untouched. In this context, repeated passes push f toward the empirical distribution over O, shrinking f(U) and raising CE, which lowers the floor via f(U)≥q(U)−CE. We now confirm this: under repetition, ECE rises with r (Spearman p<10−4 at 3 and 5 epochs), reversing its slight decrease at one epoch (General Response A3, App. B.1, Fig. 6b).
Repetition is an established way to inject miscalibration at a fixed monofact rate [6]. The revised Sec. 5.2 states that repetition leaves μ^ unchanged, and it now presents the multi-epoch experiment as a direct test of the calibration rather than a diversity control.
W3/Q3: Structural cues and baselines.
TL;DR: The input contains no composition, a nearest-neighbor baseline scores 0%, and removing the CIF leaves the monofact gain unchanged.
The structural input contains no element identities, formula, labels or occupancies (App. D). Within a chemical system, many compounds remain possible (e.g., H$_2$O vs. H$_2$O$_2$ for H-O), so the model must still infer the stoichiometry. A nearest-neighbor baseline scores 0%, and 72% of test materials come from chemical systems absent from training (General Response A1, App. B.4).
We test this directly in App. B.6 (Table 3). Removing the CIF lowers pass@16 at each monofact rate tested, but the gain from r=0 to r=1 is unchanged (+6.5 vs. +6.7 points), so the CIF cannot explain the trend over r. Cumulatively removing the remaining properties at r=1 lowers discovery at every step, from 27.8% to 13.9% (App. B.6, Fig. 10), so the model uses the requested properties rather than geometry alone.
W4/Q4: Alternative valid answers.
Exact match is the only criterion with confirmed ground truth, since the test materials were later recorded in Materials Project, a curated database, and each MPRA variant’s activity was experimentally measured (see Protocol in General Response). Unlike prior monofact work on synthetic facts [6], we use real post-cutoff scientific targets.
We hope the revision addresses your concerns. If so, we would be grateful if this could be reflected in your assessment, and we are happy to clarify anything further.
References are listed in the comment following the general response.