Pathway-Constrained Prediction of Oncolytic Virus Response from Tiny Multi-Omics Cohorts

Oncolytic viruses — viruses engineered or selected to replicate inside cancer cells and kill them while sparing healthy tissue — are usually studied in cohorts of tens of animals or cell lines, yet each experiment now yields tens of thousands of molecular measurements: bulk RNA-seq, single-cell RNA sequencing, and metabolomics. This is exactly the regime where modern machine learning fails worst. The clearest documented example in the literature is the "Clinical Supremacy" paradox: ModalSurv showed that a multimodal deep survival model reached a discovery C-index of 0.891 on a 95-patient prostate cohort, only to collapse to 0.6446 on validation, where it was beaten by a handful of tabular clinical variables. At the same time, the oncolytic-virus field has started publishing rich small-cohort datasets without any predictive modeling: the OH2 study (A Multi-Omics Dataset of Prostate Cancer Response to Oncolytic Virus OH2 Treatment) archived bulk RNA-seq, metabolomics, and 61,713 single cells from OH2-treated (an engineered HSV-2 with ICP34.5 and ICP47 deletions) versus control prostate tumors, but performed only descriptive analysis — PCA separation and differential expression — and left open how to turn such data into predictors that do not memorize the cohort.

This proposal argues that the right way to close that gap is to build the small-sample regularization directly into the biology, not to bolt it on afterwards. The core deliverable is a sparse, biologically wired predictive network — a "white-box" architecture in the spirit of DeepSignalingSynergy (Zhang et al.), which restricted its connections to 46 KEGG signaling pathways and matched unconstrained deep models on drug-synergy prediction with a fraction of the parameters — extended with viral modules that KEGG drug-synergy priors do not contain: viral entry receptors, interferon-stimulated gene cascades, and the immune-checkpoint compensation loop that Xu et al. directly observed (OH2 recruits T cells and NK cells but concurrently upregulates PD-L1). The model predicts, from a small multi-omics snapshot, whether a tumor will mount a productive antiviral response or a compensatory escape program, and whether pairing the virus with a checkpoint inhibitor or a chemotherapy such as paclitaxel (synergy demonstrated for CVB3/2035A in cervical squamous cell carcinoma by Lin et al.) will help.

Core Claim

A network whose wiring encodes viral life-cycle biology — entry, intracellular innate defense, replication, immunogenic cell death, and checkpoint compensation — can predict oncolytic virus response and rational combination partners from cohorts of tens of samples without the discovery-to-validation collapse that unconstrained architectures suffer. The claim has a falsifiable core: on the same data, an unconstrained deep model of matched raw capacity should overfit and fail to externalize, while the biologically wired model should not; and ablating the viral modules (keeping only the standard KEGG drug-response pathways used by DeepSignalingSynergy) should specifically degrade prediction of the compensatory PD-L1 program, because that program is invisible to a small-molecule synergy prior.

The motivation comes from three documented facts. First, structural biological priors demonstrably control small-sample overfitting: DeepSignalingSynergy achieved a Pearson correlation of 0.67 on NCI ALMANAC drug combinations — competitive with the unconstrained DeepSynergy (0.73) and AuDNNsynergy (0.74) baselines — while eliminating thousands of free parameters and remaining interpretable via layer-wise relevance propagation. Second, capacity itself is the enemy in this regime: Alfasly et al. showed a 6-layer CNN reaching validation F1 of 0.75 on oesophageal adenocarcinoma histopathology while a widened Vision Transformer collapsed from 0.96 training F1 to 0.58 validation F1. Third, the target signal exists but is confounded: the STAT3 contradiction — Shao et al. showed STAT3 is required for Newcastle Disease Virus-induced immunogenic cell death in melanoma, while work in prostate cancer cited in the same literature showed inhibiting STAT3 enhances it — means a pan-cancer black box trained on pooled cohorts would treat one of the most informative signals as noise. A wiring that admits tissue-specific edge signs is the minimal architecture that can represent this.

Research Program

Three components, in increasing order of risk.

The first is constructing the viral-augmented prior graph. Starting from the 46 KEGG signaling pathways and 1,648 genes used by Zhang et al., we add four curated modules: a viral entry module (receptor exploitation as documented for coxsackievirus B3 in CSCC, Lin et al., and chimeric influenza A in hepatocellular carcinoma, Yang et al.); an interferon-response module (the intact antiviral program that healthy cells run and malignant cells frequently cannot, the selectivity mechanism documented by Yang et al.); an immunogenic-cell-death module (DAMP release and STAT3-dependent signaling per Shao et al.); and a checkpoint-compensation module (PD-L1 upregulation per Xu et al.). The STAT3 node is explicitly modeled with tissue-conditional edge signs, so the melanoma and prostate contradictions become data to estimate rather than noise to average away.

The second is the training scheme, which reuses the two regularization strategies with the strongest small-sample evidence in the file. Features enter through frozen, pre-derived representations rather than learned encoders — the pattern that beat end-to-end fine-tuning in FEDD (81% malignancy accuracy from 10% of DDI using frozen diffusion features plus linear probes) and in Alhuzali et al. (frozen SpanEmo embeddings into Random Forests beat the competition winner on 72 training subjects). Where multiple omic layers must be fused, we stack per-layer predictors and combine them in log-probability space with the calibrated meta-imputation of cUPMI rather than training a joint fusion network, directly because joint multimodal training is what collapsed in ModalSurv. Single-cell data is aggregated to per-sample cell-type-composition and per-module activity scores before entering the graph, keeping the effective sample count (animals and cell-line conditions, not 61,713 cells) honest.

The third, higher-risk component couples this predictor to mechanism. Parameter Estimation and Model Selection for the Quantitative Analysis of Oncolytic Virus Therapy in Zebrafish showed that in 20 zebrafish treated with a double-deleted vaccinia virus, an age-of-infection ODE structure is mandatory to capture the delay before lysis, yet the viral burst size $\beta$ and clearance rate $\delta$ are practically non-identifiable from tumor-volume curves alone. We will test whether module activity scores from our predictor, used as cheap per-animal observations of the intracellular state, tighten the profile likelihoods of $\beta$ and $\delta$ — i.e., whether molecular readouts make the non-identifiable kinetics identifiable. This is the one place the proposal could genuinely fail: if the omic snapshots carry no information about viral kinetics, the likelihoods will not shrink, and we will report that as a negative result.

Baselines

The "do nothing" reference point is the descriptive analysis actually published with the data: PCA and differential expression on the OH2 stack (Xu et al.). No reported result found on Lacuna for any predictive ML score on that dataset — that absence is precisely the gap — so the reference point is qualitative: PCA separates control from OH2 groups, and the analysis stops there. Our first, minimal claim is to move beyond this reference by producing any cross-validated predictive number where none exists.

The strongest existing competitor on the methodological question is the unconstrained deep synergy model, instantiated as DeepSynergy, which reports a Pearson correlation of 0.73 on NCI ALMANAC, with AuDNNsynergy at 0.74 (Zhang et al. reports both as baselines against its own 0.67). These models are the right competitor because they hold the record on synergy prediction precisely by using dense, high-capacity layers over 10,000-plus chemical and genomic features — the design our claim says must fail when samples number in the tens. We will run a DeepSynergy-style dense network (same depth, same total parameter count as our wired model, plus a matched-capacity variant with twice the parameters) on identical train/validation splits, identical feature inputs, and an identical tuning budget measured in random-search trials. On NCI ALMANAC we reproduce the comparison as a sanity check; on the OH2 and combination data the decisive criterion is the discovery-to-validation gap: our model counts as winning if it retains at least 90% of its discovery performance on held-out validation while the dense baseline loses more than it keeps, in the pattern ModalSurv documented (0.891 to 0.6446).

The second competitor is the simple tabular model: penalized logistic regression or a gradient-boosted tree on top-variance genes and cell-type proportions. This is the strongest competitor on the "should you even use deep models" question, since simple clinical variables beat ModalSurv's deep network on validation. It gets the same features, splits, and tuning budget. Beating it on the mechanism tasks — predicting the PD-L1 compensation program and tissue-conditional STAT3 behavior, where the signal is an interaction effect, not a main effect — is the substantive claim; if the trees match us on those tasks too, the wiring was unnecessary and we will say so.

The key ablation swaps the viral-augmented prior graph for the original 46-pathway KEGG graph of DeepSignalingSynergy, holding architecture size, training, and data fixed. This isolates the one ingredient the proposal is actually about: viral biology in the wiring. The predicted signature of the ablation is selective — near-equal performance on proliferation and general drug-response readouts, but a large drop on entry-receptor, interferon-escape, and PD-L1-compensation predictions.

Why not just…?

Why not just use simple clinical variables or penalized regression? This is a real threat and the experiments are built to answer it rather than argue around it. The evidence for the threat is strong: simple clinical baselines out-validated deep multimodal networks in Wahab et al.. But the tasks where simple models have won are prognostic tasks where clinicians have already abstracted the key features, and no such abstraction exists for a novel virus. The relevant counter-evidence in the file is that when the target is a latent molecular interaction, shallow models plateau: simple models reached 45.6% accuracy on liver fibrosis staging while indicator-guided multi-stream networks reached 65.6% (Liu et al.), and linear baselines were outperformed by the nonlinear stacked ensemble in Nelson et al.. Our decisive experiment is the head-to-head on the PD-L1-compensation and STAT3-inversion prediction tasks; the tabular baseline is included precisely so that if it wins, the negative result is publishable.

Why not just fine-tune a large pre-trained model end-to-end? The file contains three independent demonstrations that this fails at these sample sizes: full fine-tuning was beaten by frozen backbones with linear probes in FEDD, frozen representations into Random Forests beat end-to-end fine-tuning on 72 subjects in Alhuzali et al., and capacity scaling caused a 0.96-to-0.58 train-to-validation collapse in Alfasly et al.. We will still run end-to-end fine-tuning of a pre-trained encoder as a third baseline, with the same tuning budget, because the honest test is whether our architecture choice wins against it on this data rather than by citation.

Why not just use standard input-space augmentation? Alfasly et al. applied heavy image augmentation and early stopping and still saw high-capacity models overfit, which rules augmentation out as a fix for capacity-driven overfitting; and Nelson et al. showed input-space manipulation cannot model inter-model disagreement, which is what their log-probability-space augmentation (+0.022 QWK across seeds) was needed for. We nevertheless include a Gaussian-noise input augmentation arm in every experiment, since it costs one run and would settle the question empirically if anyone doubted the citations.

Why not just apply DeepSignalingSynergy unchanged? Because its prior graph has no viral nodes: it was built for 21 small-molecule drugs with KEGG-annotated targets, and its inputs (DrugBank target statuses) do not exist for a virus. Running it unchanged on this data would force viral entry and interferon biology through chemotherapy-pathway wiring, which is exactly the selective-ablation arm we run — so the question is answered by the ablation itself rather than by argument. This is also where the proposal differs most sharply from the closest existing work.

Proposed Experiments

Experiment 1 uses the OH2 multi-omics stack (GEO: GSE298912–GSE298915; NGDC OMIX: OMIX010418), following Xu et al.. Task 1a: predict treatment-versus-control state and the magnitude of immune infiltration shift under leave-one-animal-out and leave-one-cell-line-out cross-validation, reporting AUROC and, for the ordinal immune-infiltration target, quadratic weighted kappa (the metric convention used by Nelson et al. for ordinal risk). Task 1b, the mechanistic one: predict the PD-L1-compensation program from pre-treatment and early post-treatment features, where the ablation against the KEGG-only graph should bite hardest. Because no reported result found on Lacuna for any predictive model on this dataset, our numbers establish the first baseline for others to beat.

Experiment 2 builds a synthetic synergy benchmark with ground truth we control: we simulate combination-response data using the known mechanistic interactions (CVB3/paclitaxel synergy from Lin et al.; OV-plus-anti-CTLA4 from Yang et al.; OV-plus-anti-PD-1 motivated by the PD-L1 compensation in Xu et al.), under the NCI ALMANAC evaluation protocol so results are comparable in kind to the DeepSignalingSynergy literature (Pearson r = 0.67 wired versus 0.73/0.74 dense, per Zhang et al.). The decisive check is sample-size scaling: sweep training-set size from 20 to 200 and show the wired model's advantage grows as N shrinks, while the dense model's Pearson r degrades toward the collapse regime. If the dense model stays ahead even at N = 20, the core claim is wrong.

Experiment 3 tests the identifiability coupling on the zebrafish vvDD cohort from Parameter Estimation and Model Selection, where the individual-based age-of-infection model won model selection with AIC = 1437.0 but left $\beta$ and $\delta$ non-identifiable. We re-fit that model per animal with and without module-activity scores as auxiliary observations, and measure the profile-likelihood (or Bayesian posterior) width of $\beta$ and $\delta$. Identifiability gain of a factor of two or more in both parameters, replicated across the 20 animals, would be the decisive positive; no change would be a clean negative result on the physics-coupling component while leaving Experiments 1–2 intact.

The single most important number to watch across all three experiments is the discovery-to-validation gap, the quantity that Wahab et al. turned into the field's cautionary tale (0.891 to 0.6446). A method that keeps that gap small on real oncolytic-virus cohorts — while remaining interpretable enough to name the modules driving each prediction, in the way DeepSignalingSynergy's wiring allowed LRP to name PRKCG, KIT, and FLT3 — would give the oncolysis field its first predictive tool that matches the size of the cohorts it can actually afford to run.