1. Insufficient motivation for the pretraining objective and unclear significance of the scaling law
My overall impression is that the authors pursued scaling before finding a suitable pretraining objective.
Motivation and Figure 1. Figure 1 presents a scaling law primarily measured by masked-intensity reconstruction loss, which is not particularly interesting on its own. Why should we care that a much larger model can reduce reconstruction loss unless this is shown to correlate with performance on meaningful downstream tasks? De novo peptide sequencing is an obvious example: it has seen a surge of ML research in recent years and is increasingly being used in experimental studies, with important applications in metaproteomics, immunopeptidomics, and identifying sequence variants that are difficult to account for in sequence databases. This is a major direction in the field of ML for peptide MS/MS, yet the authors do not evaluate it at all. Spectrum retrieval is another relevant task, with applications in spectral-library searching, but their results here are particularly unconvincing, as discussed below. While the authors evaluate other useful downstream tasks, they do not convincingly establish that scaling their pretraining objective translates into improved downstream performance.
I can concede that masked m/z reconstruction is problematic, even if that was not brought up by the authors. For example, multiple plausible fragments may be missing between observed peaks. How should a model be penalized for predicting a plausible fragment that is absent from the target spectrum? I presume this is why the authors resort to masked-intensity prediction, although the choice is poorly motivated. Intensities carry substantially less chemically identifying information than m/z coordinates, and avoiding the ambiguity of m/z imputation does not automatically make intensity reconstruction a good pretraining objective.
Nevertheless, the authors push ahead with scaling this objective, spending substantial compute without first establishing that it produces useful representations. I find the motivation and validation of the pretraining objective insufficient.
The abstract asks whether larger models can "genuinely understand mass spectra". What does it mean to "understand" spectra? This is very vague language. A stronger motivation would define this in terms of learning representations useful for concrete downstream tasks.
Similarly, Section 3 states the objective but provides little justification for this choice or why intensity reconstruction should be an effective representation-learning objective.
The introduction frames two main questions: "Does scale help?" and "Is absolute mass necessary?" Why these two questions? A more fundamental question seems to be: What is a suitable self-supervised pretraining task for MS/MS spectra in the first place?
Relative-mass-only encoding. The second major research question concerns whether absolute m/z information is necessary. The authors note that previous models use absolute m/z, sometimes supplemented with pairwise mass differences, and propose removing absolute m/z entirely.
However, there is no ablation comparing otherwise identical models with and without absolute m/z information.
The framing also seems somewhat backward. A reasonable question would be whether explicitly providing higher-order features such as mass differences improves performance. This was already investigated in the cited prior work (Lapin et al., 2025; Bushuiev et al., 2025), with Lapin et al. reporting that the benefit narrows on larger training corpora.
Removing absolute m/z could be a somewhat interesting architectural choice, but its benefit is not demonstrated. The authors later argue that their encoder is invariant to global shifts in m/z and must therefore learn relationships rather than memorize absolute positions. This could motivate the design, but it remains unclear whether this inductive bias improves performance or generalization without an ablation study.
2. Unconvincing downstream scaling and substantial evaluation limitations
Figure 2(a,b): Denoising. As I understand it, this is a per-peak classification task distinguishing genuine fragment peaks from noise.
Performance saturates relatively early and shows no improvement beyond the 200M model, despite continued reductions in pretraining reconstruction loss. This is particularly concerning because denoising is closely related to the pretraining objective, limiting what these results demonstrate about general-purpose representations. If scaling provides little additional benefit on this task, it is unclear whether it should be expected to help on more challenging tasks such as de novo sequencing, which is not evaluated, or retrieval.
There are also serious evaluation issues:
- Appendix J states that the denoising recipe was selected using test AUROC from a grid of 216 hyperparameter configurations at 50M. The test set was therefore used for model selection rather than reserved for independent evaluation.
- The authors report that reloaded checkpoints produce AUROC values approximately 0.014 lower than their logged evaluations, an unresolved discrepancy that further undermines confidence in the results.
Figure 2(c): Retrieval. The figure presents retrieval scaling without baseline references, making the absolute performance difficult to interpret. The 50M through 200M models achieve almost identical MAP@R, with only the 400M model showing a noticeable improvement. This could indicate some scaling benefit, but without the GLEAMS or cosine baselines, introduced only in Figure 3, the results are difficult to assess.
Figure 2(d,e): Synthetic chimera decomposition. These panels evaluate chimera detection and peak assignment on purely synthetic mixtures generated from the same MSConsensus corpus used for pretraining. Synthetic mixtures may be useful for training or controlled evaluation, but this alone establishes little about performance on real chimeric spectra.
The detection task is also nearly saturated, with even the random-backbone baseline achieving approximately 0.95 AUROC, while peak-assignment F1 saturates at 200M. Furthermore, the training procedure includes 20k "half-real" examples, without clearly explaining what these are or how they were constructed. The task itself is also poorly introduced in the main text; the detection and two-slot peak-assignment heads are only described in Appendix E.
Figure 2(f): Real HCT116 decomposition. This is potentially more interesting, but the evaluation is quite limited. It uses only 1,376 search-corroborated peptide pairs. The ground-truth peak assignments are search-derived pseudo-labels rather than independently verified annotations, and Appendix R acknowledges that pair-level FDR is not controlled. The construction of these labels and the acquisition setup are insufficiently explained.
Furthermore, the reported advantage over the random-backbone control disappears on an external HEK dataset at 200M (Appendix R), raising additional concerns about generalization.
Overall, Figure 2 provides limited evidence for consistent downstream scaling. Several tasks saturate early, the retrieval trend is unclear, and the decomposition results have important generalization limitations.
Figure 3(a): Retrieval. The results here are particularly concerning. Iona performs very well on the in-distribution benchmark but suffers severe performance degradation on several external datasets.
Their supervised contrastively fine-tuned model falls substantially behind the older GLEAMS model and even simple binned cosine similarity. On low-resolution HEK293, the final fine-tuned Iona model achieves only 0.170 MAP@R, compared with 0.530 for GLEAMS and 0.554 for binned cosine. The first-stage Iona model performs even worse, at 0.017.
On the nine-species yeast benchmark, a common evaluation dataset, the fine-tuned Iona model is again substantially behind both baselines. On the 20k yeast subset, it achieves 0.600 MAP@R versus 0.770 for GLEAMS and 0.916 for binned cosine.
In Section 4.4: Comparison with specialized models, the authors write:
"Contrastive specialisation of Iona-400M reaches MAP@R 0.868 on its own distribution, far above GLEAMS [...] (0.646) and cosine [...] (0.729)."
The authors emphasize their strong in-distribution retrieval performance despite substantial failures on several external benchmarks. This is a fundamental issue in evaluating machine learning models, particularly for MS/MS data, where multiple highly similar spectra from the same peptides and charge states are common. Good performance on a held-out test set drawn from the supervised fine-tuning distribution does not establish generalization across acquisition conditions, especially when performance degrades so severely under distribution shift. The fact that Iona falls well behind GLEAMS and binned cosine on multiple external datasets should be a central finding, rather than a secondary qualification to the in-distribution results.
At the very least, the authors should investigate why their supervised contrastive fine-tuning performs so poorly compared with a model from 2022 and even non-learned similarity measures.
One possible explanation is that masked-intensity reconstruction is poorly suited to learning transferable spectrum-level representations. The pretraining objective operates at the peak level and does not directly optimize spectrum-level embeddings. However, the experiments do not distinguish this possibility from shortcomings of the contrastive fine-tuning procedure.
These results substantially weaken the evidence that the proposed pretraining approach learns transferable weights.
Figure 3(b): PSM rescoring. The rescoring pipeline is considerably more complicated than simply applying the pretrained spectrum encoder. It first uses supervised contrastive learning based on peptide identities, then trains an additional peptide Transformer to reproduce the spectrum encoder's embeddings from annotated peptide sequences and charges. Similarities between the two embeddings are subsequently used as features for PSM rescoring.
This second model is barely described. Appendix E essentially states only that it is a Transformer trained by MSE against the spectrum embeddings, without specifying its architecture, parameter count, or training hyperparameters. This is a serious reproducibility issue for a model that is essential to one of the paper's headline results.
Lack of a baseline: the final system relies on supervised contrastive training using peptide identities, followed by training an additional peptide encoder to reproduce the spectrum embeddings. A natural baseline would be to train the spectrum encoder from scratch using the same supervised contrastive objective, then train the peptide student and evaluate the complete rescoring pipeline identically. Without this comparison, it is unclear how much of the final performance comes from the proposed self-supervised pretraining rather than the subsequent supervised training. The shuffled-embedding control does not answer this question.
The headline PSM rescoring result is obtained on 18 HCT116 mass spectrometry runs, where adding Iona embedding features to MSFragger-based rescoring yields 20,763 additional PSMs at 1% FDR over a shuffled-embedding control. However, when adding Iona to the stronger MS2Rescore pipeline, including MS2PIP and DeepLC, the net improvement is only 251 PSMs on a separate eight-run dataset (Appendix M). The authors do not evaluate the full MS2Rescore pipeline on the original 18-run dataset. Consequently, it remains unclear whether the headline gains would persist against a stronger established baseline, or how much of the difference is explained by the datasets.
Fragment-intensity prediction and Prosit. Repurposing a pretrained spectrum encoder for peptide-to-spectrum intensity prediction is a potentially novel aspect of this work. However, the adaptation is rather convoluted. The authors convert peptide sequences into theoretical b/y-ion masses, assign peptide-agnostic prior intensities, and pass these through Iona with a newly trained prediction head (Appendix E).
This is a creative way to reuse the spectrum encoder, but why take this detour instead of directly encoding the peptide sequence, as existing methods do? The authors do not establish any advantage to this approach.
The results approximately match the older Prosit RNN but fall behind Prosit Transformer. More importantly, without a scratch-initialized Iona baseline, it is impossible to tell whether the pretrained representations contribute meaningfully to the final performance. Task-specific adaptation is perfectly reasonable for a foundation model, but the authors need to demonstrate that the pretraining is actually useful for this task.
Overall assessment. The paper's central weakness is that the authors attempt to establish compute-optimal scaling without first convincingly establishing the suitability of their pretraining objective. Additionally, it is lacking in novelty and clarity.
The scaling law concerns masked-intensity reconstruction loss, while the downstream experiments show inconsistent scaling and substantial generalization problems. Several evaluations also have methodological limitations, including test-set-based hyperparameter selection, unresolved reproducibility discrepancies, incomplete controls, and limited independent validation.
There are some promising application results, but the paper does not convincingly establish that continued scaling of this particular pretraining objective leads to meaningful, generalizable downstream improvements, or that its scaling law provides useful guidance for compute-optimal foundation-model development.
We thank the reviewer for the positive assessment and constructive suggestions.
“The authors don’t compare their method of including only mass differences and not absolute masses [...]”
We have added a matched 25M ablation using absolute m/z only (Section 4.3, Appendix S). The absolute variant fits pretraining slightly better (0.0658 vs. 0.0688, single seed), but this gap is small, less than half the improvement from doubling model size (0.0073 from 25M to 50M). We therefore do not claim superiority on clean, well-calibrated data. On whether invariance helps transfer, we evaluated both encoders on denoising under test-time drift (Table 25). The relative-only encoder is unaffected by constant offsets, where the absolute variant loses up to 15% AUROC. Under ppm drift, it degrades 5–9× less.
For tasks where absolute positions are diagnostic, we keep the encoder shift-invariant and provide absolute information downstream when a task needs it. In our new de novo experiment, for example, only the decoder receives the precursor mass, and the relative-only encoder still exceeds Casanovo v5 in mean peptide recall (Section 4.4, Appendix T). We leave a combined absolute + relative encoder to future work.
“[...] removing the pretraining from the model and performing the task in a supervised manner to compare it against IONA and Casanovo.”
We thank the reviewer for this suggestion. We ran this control on a new, larger chimericity benchmark with 101 PRIDE projects split by project. We also added a head with no encoder to separate the encoder’s contribution (Section 4.4, Table 28).
Trained purely supervised, the Iona architecture is no better than the encoder-free head (mean project AUROC 0.727 vs. 0.733; Table 28). Pretrained Iona-25M reaches 0.832, and Iona-400M reaches 0.872, against 0.834 for fine-tuned CasanovoTL. The same pattern holds for DIA precursor prediction, with bin AP of 0.533 from random initialization vs. 0.698 for pretrained Iona-25M (Table 29).