No Foundations without Foundations -- Why semi-mechanistic models are essential for regulatory biology

Caroline Uhler; Hagen Triendl; Jake P. Taylor-King; James Opzoomer; John Whittaker; Lindsay Edwards; Luka Kova\v{c}evi\'c; Thomas Gaudelet

REVIEW 4 major objections 7 minor 1 cited by

No Foundations without Foundations -- Why semi-mechanistic models are essential for regulatory biology

T0 review · 4 major / 7 minor · reviewed 2026-08-09 · deepseek-v4-flash

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Pith's one-line read Foundation models of regulatory biology will stay out of reach unless they encode the order of perturbation, media, and time; this paper builds a semi-mechanistic framework to do so.

desk verdict The compositional framework is a genuinely useful new synthesis for perturb-seq modelling; the empirical pilot is too under-specified and potentially leaky to carry the weight of the central claim, so treat the paper as a principled proposal, not a validated method. read the letter →

arxiv 2501.19178 v1 pith:ODH7AK5I submitted 2025-01-31 cs.LG

Luka Kovačević , Thomas Gaudelet , James Opzoomer , Hagen Triendl , John Whittaker , Caroline Uhler , Lindsay Edwards , Jake P. Taylor-King This is my paper · ORCID

classification cs.LG

keywords regulatorybiologyfoundationmodelsCRISPRscreensperturb-seqsemi-mechanisticgeneexpressionpredictionneuralODEsbatcheffects

verification ladder T0 review T1 audit T2 compute T3 formal

The pith

A machine-rendered reading of the paper's core claim, the machinery that carries it, and where it could break.

The reading

This paper argues that the stalled progress in predicting gene-expression responses to perturbations is not mainly a data problem: it is a modelling problem. The authors propose that any reliable “foundation model” of regulatory biology must first encode how a CRISPR experiment actually works, as a sequence of non-commuting operations — edit the gene, change the media, wait. From that sequence they derive loss functions and expose an assumption, often unstated, that unedited cells do not respond to baseline media; when it fails, standard supervised training becomes counterfactual prediction. On an iPSC time-course they show that adding a steady-state term to the loss improves a neural-ODE model’s predictions of unseen perturbations and stabilises training. If the argument is correct, future perturbation models should be evaluated by whether they respect experimental structure, not just by architecture or data volume.

What carries the argument

The load-bearing object is the experiment-as-function $F=W\circ M\circ P$, with each operation defined as a map on cell-state random variables: $P(X,p_\gamma)=X_{p_\gamma}$ applies the CRISPR edit, $M(X,m)=X_m$ applies a media condition, and $W(X,t)=X_t$ waits. The argument advances by asking which paths in the four-branch experimental diagram can be treated as identity, deriving the loss in Eq. (6) from the necessary assumption $F(X,\cdot,\cdot,t)=X$ and the additional regularizer in Eq. (10) from the assumption that some perturbed populations are dynamical attractors. The proof of principle instantiates $F$ as a neural ODE, $F(x,p_\gamma,t)=x_0+\int_0^t G(x,p_\gamma,s)\,ds$, and the error analysis models batch effects as zero-mean additive noise on top of the measurement function $V$, leading to the recommendation to replicate baseline controls across batches.

What would settle it

Take any perturb-seq dataset used to train a perturbation predictor and compare the transcriptomes of unedited cells harvested at day 0 with those of unedited cells in baseline media at the end time $t$, using the same within-day-split baseline the paper uses for its iPSC analysis. If the end-time distribution separates from the day-0 distribution by more than technical noise, the necessary assumption $F(X,\cdot,\cdot,t)=X$ fails and the paper's recommended loss is not applicable to that experiment; conversely, a dataset that passes this check and contains known steady states should reproduce the reported MSE gap between Eq. (6) and Eq. (10).

Watch

Extended reading notes

Core claim

The central claim is that the genotype-to-phenotype mapping measured in a perturb-seq screen is the composed function $F(X,p_\gamma,m,t)=W(M(P(X,p_\gamma),m),t)$, where $P$ applies a CRISPR perturbation, $M$ switches media conditions, and $W$ waits $t$ units of time, in that order. Writing the experiment this way makes the non-commutativity of biological operations explicit and brings hidden assumptions to the surface: the standard supervised loss (Eq. 6) is only valid if unedited cells do not respond to baseline media, $F(X,\cdot,\cdot,t)=X$; otherwise paired measurements are counterfactual and require an inverse $F^{-1}$. The paper then derives a “steady-state” regularizer (Eq. 10): wherever biology dictates that a perturbed population is an attractor, the loss demands $F(X^{p_\gamma}_{m,t},\cdot,\cdot,s)=X^{p_\gamma}_{m,t}$, and the proof of principle shows that this term lowers test MSE and reduces seed-to-seed variance for a neural ODE on an iPSC dataset. Variational autoencoders and structural causal models are shown to be special cases of the same composition, and the batch-error analysis yields a concrete experimental prescription: include unperturbed baseline cells in every sequencing batch.

Load-bearing premise

The framework's loss functions collapse if unedited cells in baseline media are not statistically stationary over the experiment's time window, because the paper's central pathway $F(X,\cdot,\cdot,t)=X$ is then false and every paired prediction becomes a counterfactual requiring an invertible map.

Editorial extensions

If this is right

Established architectures—VAE-style perturbation autoencoders and structural causal models of perturbation screens—are recovered as special cases of the unified $F$-composition, so their design choices can be compared by the assumptions they make about $P$, $M$, and $W$.
Datasets must be checked for the necessary assumption before being used to train or benchmark perturbation models; if unedited cells drift in baseline media, Eq. (6) is a counterfactual loss, not a supervised one.
Enforcing biologically known steady states acts as a regularizer that improves prediction for other, non-steady-state perturbations, which is a concrete, testable benefit of injecting mechanism.
Batch design can be optimised from the error analysis: placing unperturbed baseline cells in every batch reduces total prediction error because the $\eta_b$ and $\eta_{b'}$ terms enter with opposite signs.

Reading between the lines

Editorial extensions of the paper, not claims the author makes directly.

Editorial inference: if the necessary-assumption check becomes standard practice, several published perturb-seq benchmarks may need re-scoring, because models trained on drifting baseline cells could be fitting counterfactual structure rather than biology.
Editorial inference: the steady-state regularizer should transfer to RNA-velocity and cell-differentiation models—any dataset with time series and known terminal states is a candidate for the same term, not just CRISPR screens.
Editorial inference: a direct quantitative prediction is that the performance gap between Eq. (6) and Eq. (10) should grow with the number of perturbed populations that are at steady state and with the duration of the experiment relative to relaxation time; both are testable by re-running the NODE experiment on datasets with longer time courses.
Editorial inference: the framework suggests a natural benchmark protocol—per-dataset verification of $F(X,\cdot,\cdot,t)=X$ and known attractors—before comparing foundation models; without it, leaderboard positions conflate architecture quality with baseline drift.

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Editorial analysis

A structured set of objections, weighed in public.

Desk editor's note, referee report, and a circularity audit.

Desk Editor's Note

read the letter

Short version: the formalism is the contribution, and it is a real one. The paper gives the regulatory-biology ML community a clean compositional language for what happens in a perturb-seq experiment — edit, change media, wait — with the non-commutativity and the hidden assumptions made explicit. The derivation from equation (4) through the loss functions is coherent, and the observation that VAE-style models and structural causal models fall out as special cases is genuinely instructive. I learned something from how they trace the paired-data assumption back to equation (5). The paper is also honest about its necessary and optional assumptions and translates them into concrete experimental recommendations, which is rarer than it should be.

The soft spots are all on the empirical side. The proof-of-principle in Section 6 is a pilot, not evidence. One pseudobulk dataset, no architecture details, no code, no hyperparameter reporting, and no ablation that rules out the explanation that any extra regularization term would produce the same faster convergence and lower test MSE. The stress-test concern about the steady-state subset lands: S is selected from the same days 2–5 time course that supplies the test labels, and the paper does not state that the steady/non-steady classification was done using training days only. That makes the reported gap in Figure 5 consistent with target leakage rather than with the value of the mechanistic prior. The authors explicitly flag their assumptions as needing validation, but the pilot does not show that validation being done out-of-sample.

The math and the citation pattern look solid. The compositional abstraction is a new synthesis, not a repackaging of existing results; the derivation of VAEs and causal models as special cases is their own argument and it checks out. The paper engages fairly with the recent benchmarks showing simple linear methods often beat deep models. I do not see a circularity problem in the formal core.

Who should read this: anyone building or benchmarking ML models for perturbation screens, and anyone designing perturb-seq experiments. They will get a useful conceptual frame, a checklist of assumptions to verify, and a batching error analysis that suggests practical experimental design. It is not a validated method paper. It deserves a serious referee, not a desk reject, because the framework is likely to be built on even if the pilot is reworked or removed. For peer review: request code, architecture details, a pre-registered or training-only steady-state selection, and an ablation with a generic regularizer of comparable strength.

Referee Report

4 major / 7 minor

Summary. The paper argues that foundation models for regulatory biology need to be grounded in mechanistic models of how perturbation experiments are conducted. The authors formalize an in vitro perturb-seq experiment as a composition of operators P (genetic perturbation), M (media change), and W (waiting), yielding the function F in Eq. (4). Under a 'necessary assumption' that unedited cells in baseline media do not change over time (Eq. 5), they derive a supervised loss (Eq. 6); under an optional steady-state assumption they add a loss term (Eq. 10). They then connect this framework to variational autoencoders (Section 5.1) and causal models (Section 5.2), and analyze batch effects in Appendix B, recommending that unperturbed controls be included in every batch. The empirical proof-of-principle in Section 6 trains a neural ODE on pseudobulked iPSC data from Ishikawa et al. (2023), reporting that enforcing steady states improves test MSE for 11 held-out non-steady perturbations.

Significance. If the framework's utility is borne out by further validation, it would provide a principled way to design loss functions and experimental batches for perturbation modeling, and would clarify the hidden assumptions in existing methods. The formal derivation of the loss structure from the experimental protocol is a conceptual contribution, and the demonstration of links between the framework and VAEs/causal models is interesting. However, the paper's central empirical claim — that the steady-state loss improves predictive performance over standard training — is currently supported only by a single dataset with a post hoc selected steady-state set and no non-mechanistic regularizer control. The strength of the claim in the abstract therefore exceeds what the evidence establishes.

major comments (4)

[Section 6 / Appendix D] The steady-state subset S is selected from the same days-2–5 time course that is later used for training and testing. Appendix D shows that the classification of the 14 steady-state perturbations is based on absolute LFC between sequential days, including the day-4-to-day-5 comparison; Section 6 then evaluates on the 11 'non-steady state' perturbations at t=5. If day-5 measurements contribute to deciding which perturbations are steady (and therefore which are non-steady and held out), the improved test MSE in Fig. 5 could reflect target leakage rather than a benefit of the mechanistic prior. The paper does not state whether the steady-state labeling uses only training days or an independent replicate. Please clarify the exact selection procedure and, if leakage is possible, re-run the experiment with S fixed a priori from a separate experiment or from a random split that does not use test-day information.
[Section 6 / Figure 5] The comparison between the 'original loss' and the 'modified loss' does not control for the presence of an additional loss term. Adding the steady-state loss (Eq. 10) introduces extra supervision on the training set; a generic regularizer of comparable strength — e.g., L2 weight decay, dropout, or an output-smoothing term — could plausibly produce the same faster convergence and lower test MSE on a 100-point pseudobulk dataset. Without ablations that match the number, type, and strength of extra loss terms, the improvement cannot be attributed specifically to the mechanistic steady-state prior. Please include such controls.
[Section 2.3.1 / Eq. (5)] The 'necessary assumption' that unedited cells do not respond to baseline media is explicit, but it is not validated on the Ishikawa et al. (2023) dataset used in Section 6. If this assumption fails, the paired supervised loss in Eq. (6) is not a proper objective for the observed data, and the counterfactual alternative in Eq. (7) requires an inverse F^{-1} whose existence is itself assumed. The paper's experimental recommendations (Section 2.3.1) call for verifying this assumption, yet the proof-of-principle does not report the stability of non-targeting controls across days. Please report this stability check or otherwise justify the assumption for the dataset analyzed.
[Section 6] The neural ODE model and training protocol are not described in sufficient detail. The paper does not specify the network architecture, the number of parameters, the optimizer, the learning rate schedule, the weight of the steady-state loss, or the hyperparameter selection procedure. Without these details and without code, the proof-of-principle is not reproducible, and it is unclear how sensitive the improvement in Fig. 5 is to the chosen regularization strength. Please provide full experimental details or release code.

minor comments (7)

[Section 2.2 / Eq. (4)] The notation X^{pγ}_{m,t} is used before the sub/superscript convention is explained; define it immediately before Eq. (4).
[Section 3.1 / Eq. (11)] The sentence ending 'respectfully' should be 'respectively,' and the spaces N0^{n_W n_G} and N0^{n_G} should be introduced before use.
[Section 3.1 / after Eq. (13)] The phrase 'to the extent that V has an inverse' is vague for a count-valued measurement function; clarify what is meant by V^{-1} in this setting.
[Section 5.1 / Eq. (18)] The latent function L in the VAE derivation conflicts with the loss L used elsewhere; use a different symbol (e.g., h).
[Section 6] The statement 'pseudobulk single-cell data over (pγ, t) pairs giving 100 unique data points' should state the number of perturbations and time points explicitly so the reader can verify the count.
[Appendix B / Eq. (23)] The symbol V is used both for the measurement function (Eq. 11) and for the valid set; rename one of them.
[Throughout] The phrase 'non-differentiating cellular models' is potentially confusing; consider using 'cells that do not differentiate over the experimental window.'

Circularity Check

1 steps flagged · score 4.0 of 10

Formal derivation is self-contained, but the proof-of-principle evaluation shows target leakage: the steady-state set S is selected from the same days-2–5 time course that defines the held-out t=5 test labels.

fitted input called prediction [Section 6, Proof of principle; Appendix D, Analysis of iPSC time series dataset]
"In Appendix D, we confirm this from transcriptomic signatures and identify 14 perturbations (including the non-targeting control) that appear to converge on a steady state. ... We train the model using the remaining data via the original loss function given by equation (6), or a loss function with steady states enforced using a modification analogous to equation (10)."

The steady-state subset S used in the modified loss (Eq. 10) is identified in Appendix D by comparing mean LFC between days 2–3, 3–4, and 4–5 against a within-day baseline. The day 4–5 comparison uses precisely the t=5 measurements that are later held out as the test targets for the 11 non-steady-state perturbations. Thus the choice of which perturbations receive the Eq. (10) autoencoding regularizer is informed by the evaluation outcome, and the reported test MSE improvement in Figure 5 may restate the day-5 information used to select S rather than independently demonstrate the value of the mechanistic prior. No ablation is reported to control for the amount or type of extra regularization, so the pilot is confounded as evidence for the central empirical claim.

full rationale

The core derivation is a formal abstraction and is not equivalent to its inputs: F is defined by composition of perturbation, media, and waiting operators (Eq. 4); the necessary assumption (Eq. 5) is stated explicitly and flagged for validation; the supervised loss (Eq. 6) and steady-state loss (Eq. 10) are constructed from stated assumptions rather than fitted to any specific dataset. The VAE and causal-model connections are presented as demonstrations that popular architectures become special cases under explicit assumptions, not as predictions derived from the framework. Self-citations (Gaudelet et al. 2024, Peidli et al. 2024, Kovačević et al. 2024, Taylor-King et al. 2024) are used for background, benchmarks, and terminology, but no load-bearing argument reduces to a self-cited uniqueness theorem or ansatz. The only concerning step is the pilot evaluation: Appendix D selects the steady-state set S from the same days-2–5 time course that supplies the held-out t=5 test labels, and the paper does not state that this classification used only training days or an independent replicate. This is an evaluative circularity/leakage that weakens the proof-of-principle, but it does not make the mathematical framework circular by construction, so the score is 4 rather than 6 or higher.

Assumptions & free parameters 4 free parameters · 5 assumptions · 0 invented entities

The framework rests on a small set of modeling assumptions, several of which the authors explicitly flag. No new physical or biological entities are postulated. The main load-bearing choices are the composition structure, the no-drift baseline assumption, the invertibility of the measurement process, and the data-dependent selection of steady states.

free parameters (4)

NODE neural network parameters = unknown (not reported)
The proof-of-principle model in Section 6 is trained on the Ishikawa dataset; no architecture or parameter count is given.
Steady-state subset S = 14 perturbations including non-targeting control
Selected in Appendix D based on observed decrease in absolute log2 fold change across days; this data-dependent selection defines the extra loss term in Eq (10).
Genes retained after filtering = 120 genes
Only genes that significantly varied over the time course are kept; the threshold and statistical test are not fully specified.
Regularization strength for steady-state loss = unknown
Equation (10) is added to the loss, but the weighting relative to Eq (6) is not reported.

assumptions (5)

domain assumption Cell state is representable by a random variable X in an abstract space, and the experiment is a well-defined function F = W∘M∘P.
Introduced in Section 2.2, Eq (4); this is the foundation of all subsequent losses.
domain assumption Unedited cells in baseline media do not respond over time, X_t = X.
Eq (5), Section 2.3.1, labeled the necessary assumption; the main loss in Eq (6) depends on it.
domain assumption The measurement map V has an inverse on the support of the data, X = supp(V(X)).
Eq (13), Section 3.1; the learned function F = V∘F∘V^{-1} is only exact if V can be inverted, despite dropout and batch effects.
ad hoc to paper Selected perturbations are at steady state within the observation window.
Section 6 and Appendix D; the subset S is defined by this assumption and directly changes the loss.
standard math Batch errors are small enough for a first-order Taylor expansion.
Eq (28) in Appendix B; the error analysis and batching recommendation depend on this approximation.

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Cite this review

Pith. "Pith review of No Foundations without Foundations -- Why semi-mechanistic models are essential for regulatory biology." pith.science (2026). https://pith.science/paper/ODH7AK5I

@misc{pith2026250119178,
  author       = {Pith},
  title        = {Pith review of: No Foundations without Foundations -- Why semi-mechanistic models are essential for regulatory biology},
  year         = {2026},
  howpublished = {\url{https://pith.science/paper/ODH7AK5I}},
  note         = {Machine review of arXiv:2501.19178}
}

read the original abstract

Despite substantial efforts, deep learning has not yet delivered a transformative impact on elucidating regulatory biology, particularly in the realm of predicting gene expression profiles. Here, we argue that genuine "foundation models" of regulatory biology will remain out of reach unless guided by frameworks that integrate mechanistic insight with principled experimental design. We present one such ground-up, semi-mechanistic framework that unifies perturbation-based experimental designs across both in vitro and in vivo CRISPR screens, accounting for differentiating and non-differentiating cellular systems. By revealing previously unrecognised assumptions in published machine learning methods, our approach clarifies links with popular techniques such as variational autoencoders and structural causal models. In practice, this framework suggests a modified loss function that we demonstrate can improve predictive performance, and further suggests an error analysis that informs batching strategies. Ultimately, since cellular regulation emerges from innumerable interactions amongst largely uncharted molecular components, we contend that systems-level understanding cannot be achieved through structural biology alone. Instead, we argue that real progress will require a first-principles perspective on how experiments capture biological phenomena, how data are generated, and how these processes can be reflected in more faithful modelling architectures.

Figures

Figures reproduced from arXiv: 2501.19178 by the authors.

**Figure 3.** Illustration of haematopoetic stem cells differen [PITH_FULL_IMAGE:figures/full_fig_p008_3.png] view at source ↗

**Figure 4.** (A.) High level causal graph where each con [PITH_FULL_IMAGE:figures/full_fig_p010_4.png] view at source ↗

Figures from the paper (1 more)

**Figure 8.** Figure 8: Absolute LFC between sequential days in the [PITH_FULL_IMAGE:figures/full_fig_p019_8.png]

Discussion (0). Continue with ORCID to comment.

Forward citations

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Reference graph

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Pith tools

Reviewed August 9, 2026 · model on record in the stance chip above.

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